Reviewer #3 (Public Review):

Yin-wei Lin et al set out to visualize the inactive conformation of full-length Bruton's Tyrosine Kinase (BTK), a molecule that has evaded high-resolution structural studies in its full-length form to this date. An open question in the field is how the Pleckstrin Homology-Tec Homology (PHTH) domain inhibits BTK activity, with multiple competing models in the field. The authors used a complimentary set of biophysical techniques combined with well-thought-out stabilizing mutations to obtain structural insights into BTK regulation in its full-length form. They were able to crystallize the full-length construct of BTK but unfortunately, the PHTH was not resolved yielding a structure similar to that previously obtained in the field. The investigation of the same construct by SAXS yielded an elongated structural model, consistent with previous SAXS studies. Using cryo-EM the authors obtained a low-resolution model for the FL BTK with a loosely connected density assigned to the dynamic PHTH around the compact SH2-SH3-Kinase Domain (KD) core. To gain further molecular insights into PHTH-KD interactions the authors followed a previously reported strategy and generated a fusion of PHTH-KD with a longer linker, yielding a crystal structure with a novel PHTH-KD interface which they tested in biochemical assays. Lastly, Yin-wei Lin et al crystallized the BTK KD in a novel partially active state in a "face-to-face" dimer with kinases exchanging the activation loops, although partially disordered, being theoretically perfectly positioned for transphosphorylation. Overall this presents a valiant effort to gain molecular insights into what clearly is a dynamic regulatory motif on BTK and is a valuable addition to the field.

However, this work can be improved by considering these points:

1) The cryo-EM reconstructions are potentially over-interpreted. The reported resolution for all of the analyzed reconstructions is better than 8Å, at which point helices should be recognized as well-resolved structural elements. In the current view/depiction of the cryo-EM maps/models it is hard to see such structural features and it would be great if the authors could include a panel showing maps at higher thresholds to show correspondence between the helices in the kinase C lobe and the cryo-EM maps. Otherwise, the overall positioning of the models within the cryo-EM maps is hard to evaluate and may very well be wrong. (Fig 4, S2).

2) With the above in mind, if the maps are not at the point where helices are well resolved, it may be beneficial to low-pass filter the maps to a more conservative resolution for fitting, analysis, and representation. (Fig 4, S2).

3) It would be valuable to get a quantitative metric on the model/map fitting for the cryo-EM work. One good package for this is Situs which provides cross-correlation values for the top orthogonal fits, without user input for initial fitting. This would again increase the confidence in the correctness of model positioning on the map. (Fig 4, S2).

4) It would be great to see 2D class averages from the particles contributing to each of the 3D classes. Theoretically, a clear bright "blob" (hypothesized to be the PHTH domain) should be observable in the 2D class averages. In the current 2D class averages that region is unconvincingly weak. (Fig 4, S2).

5) It seems like there was quite a large circular mask applied during 2D classification. Are authors confident that the weak density attributed to the PHTH domain is not neighboring particles making their way into the extraction box? It would be great if the authors would trim their particle stack with a very stringent inter-particle distance cutoff (or report the cutoff in the manuscript if already done so) to minimize this possibility.

6) The cryo-EM processing may benefit from more stringent particle picking. The authors picked over 2M particles from 750 micrographs which likely represents very heavy overpicking. I would encourage the authors to re-pick the micrographs with 2D class averages and use more stringent metrics to reduce the overpicking. This may result in higher-resolution reconstructions. (Fig 4, S2).

7) The Dmax from SAXS for the Full Length BTK is at 190Å. It would be great if the authors could make a cartoon of what domain arrangement may satisfy this distance, as it is quite extended for such a small particle. Can the authors rule out dimerization at SAXS concentrations? (Fig 1).

8) In Figure S1 (C) it seems that the curves are just scattering curves with Guinier plots in the inserts, but are labeled as Guinier plots in the legend. The Guinier plots for some samples (FL 4P1F) show signs of aggregation, which may complicate the analysis, it could be beneficial to redo.

9) Have the authors verified that the activation loop mutations that they introduce do not disrupt the PHTH binding as they previously reported an activation loop on BTK to interact with PHTH, an interaction they do not see here? If so, a citation would be helpful in the text. If not, testing this would strengthen the paper.

10) Can the authors comment on the surfaces which are accessible and inaccessible to the PHTH in the crystal (Fig 3E)? The fact that PHTH doesn't adopt a stable conformation in the solvent channel to some degree indicates that the accessible interaction surfaces are not suitable for PHTH interactions, as the "effective concentration" of the PHTH would be quite high. Are these surfaces consistent with the cryo-EM analysis?

11) For the novel active state dimer of the Kinase Domain it would be great to see some functional validation of the dimerization interface. It is structurally certainly quite suggestive, but without such experiments the functional significance is unclear. If appropriate mutations have been published previously a citation would be helpful.

Reviewer #3 (Public Review):

Verdikt et al. focused on the influence of Δ9-THC, the most abundant phytocannabinoid, on early embryonic processes. The authors chose an in vitro differentiation system as a model and compared the proliferation rate, metabolic status, and transcriptional level in ESCs, exposure to Δ9-THC. They also evaluated the change of metabolism and transcriptome in PGCLCs derived from Δ9-THC-exposed cells. All the methods in this paper do not involve the differentiation of ESCs to lineage-specific cells. So the results cannot demonstrate the impact of Δ9-THC on preimplantation developmental stages. In brief, the authors want to explore the impact of Δ9-THC on preimplantation developmental stages, but they only detected the change in ESCs and PGCLCs derived from ESCs, exposure to Δ9-THC, which showed the molecular characterization of the impact of Δ9-THC exposure on ESCs and PGCLCs.

Reviewer #3 (Public Review):

This paper presents the cognitive implications of claims made in two accompanying papers (Berger et al. 2023a, 2023b) about the creation of rock engravings, the intentional disposal of the dead, and fire use by Homo naledi. The importance of the paper, therefore, relies on the validity of the claims for the presence of socio-culturally complex and cognitively demanding behaviors that are presented in the associated papers. Given the archaeological, hominin, and taphonomic analyses in the associated papers are not adequate to enable the exceptional claims for naledi-associated complex behaviors, the inferences made in this paper are currently inadequate and incomplete.

The claimed behaviors are widely recognized as complex and even quintessential to Homo sapiens. The implications of their unequivocal association with such a small-brained Middle Pleistocene hominin are thus far reaching. Accordingly, the main thrust of the paper is to highlight that greater cognition and complex socio-cultural behaviors were not necessarily associated with a positively encephalized brain. This argument begs the obvious question of whether absolute brain size and/or encephalization quotient (i.e., the actual brain volume of a given species relative the expected brain size for a species of the same average body size) can measure cognitive capacity and the complexity of socio-cultural behaviors among late Middle Pleistocene hominins.

Claims for a positive correlation between absolute and/or relative brain size and cognitive ability are not common in discussions surrounding the evolution of Middle- and Late Pleistocene hominin behavior. Currently, the bulk of the evidence for early complex technological and social behaviors derives from multiple sites across South Africa and postdates the emergence of H. sapiens by more than 100,000 years. Such lag in the expression of complex technologies and behaviors within our species renders the brain size-implies-cognitive capacity argument moot. Instead, a rich body of research over the past several decades has focused on aspects related to socio-cultural, environmental, and even the wiring of the brain in order to understand factors underlying the expression of the capacity for greater behavioral variability. In this regard, even if the claimed evidence for complex behaviors among the small-brained naledi populations proves valid, the exploration of the specific/potential socio-cultural, neuro-structural, ecological and other factors will be more informative than the emphasis on absolute/relative brain size.

The paper presents as supporting evidence previous claims for the appearance of similar complex behaviors predating the emergence of our species, H. sapiens, although it does acknowledge their controversial nature. It then uses the current claims for the association of such behaviors with H. naledi as decisive. Given the inadequate analyses in the accompanying papers and the lack of evidence for stone tools in the naledi sites, the present claims for the expression of culturally and symbolically mediated behaviors by this small-brained hominin must be adequately established. The importance of the paper thus rests on the validity of the claimed evidence--including contextual aspects--for rock engraving, mortuary practices, and the use of fire presented in the associated two papers. The claims in both associated papers are inadequate, incomplete, and largely assumption- (rather than evidence) based. As responsible and ethical researchers, the team must return to the sites, conduct the required standard chronomoetric and taphonomic studies and weigh the strength of the evidence before proceeding with the current claims.

Reviewer #3 (Public Review):

Lee Berger and colleagues argue here that markings they have found in a dark isolated space in the Rising Star Cave system are likely over a quarter of a million years old and were made intentionally by Homo naledi, whose remains nearby they have previously reported. As in a European and much later case they reference ('Neanderthal engraved 'art' from the Pyrenees'), the entangled issues of demonstrable intentionality, persuasive age and likely authorship will generate much debate among the academic community of rock art specialists. The title of the paper and the reference to 'intentional designs', however, leave no room for doubt as to where the authors stand, despite avoidance of the word art, entering a very disputed terrain. Iain Davidson's (2020) 'Marks, pictures and art: their contributions to revolutions in communication', also referenced here, forms a useful and clearly articulated evolutionary framework for this debate. The key questions are: 'are the markings artefactual or natural?', 'how old are they?' and 'who made them?, questions often intertwined and here, as in the Pyrenees, completely inseparable. I do not think that these questions are definitively answered in this paper and I guess from the language used by the authors (may, might, seem etc) that they do not think so either.

First, a few referencing issues: the key reference quoted for distinguishing natural from artefactual markings (Fernandez-Jalvo et al. 2014), whilst mentioned in the text, is not included in the references. In the acknowledgements, the claim that "permits to conduct research in the Rising Star Cave system are provided by the South African National Research Foundation" should perhaps refer rather to SAHRA? In the primary description of their own markings from Rising Star and their presumed significance, there are, oddly, several unacknowledged quotes from the abstract of one of the most significant European references (Rodriguez-Vidal et al. 2014). These need attention.

Before considering the specific arguments of the authors to justify the claims of the title, we should recognise the shift in the academic climate of those concerned with 'ancient markings' that has taken place over the past two or three decades. Before those changes, most specialists would probably have expected all early intentional markings to have been made by Homo sapiens after the African diaspora as part of the explosion of innovative behaviours thought to characterise the 'origins of modern humans'. Now, claims for earlier manifestations of such innovations from a wider geographic range are more favourably received, albeit often fiercely challenged as the case for Pyrenean Neanderthal 'art' shows (White et al. 2020). This change in intellectual thinking does not, however, alter the strict requirements for a successful assertion of earlier intentionality by non-sapiens species. We should also note that stone, despite its ubiquity in early human evolutionary contexts, is a recalcitrant material not easily directly dated whether in the form of walling, artefact manufacture or potentially meaningful markings. The stakes are high but the demands are no less so.

Why are the markings not natural? Berger and co-authors seem to find support for the artefactual nature of the markings in their location along a passage connecting chambers in the underground Rising Star Cave system. The presumption is that the hominins passed by the marked panel frequently. I recognise the thinking but the argument is weak. More confidently they note that "In previous work researchers have noted the limited depth of artificial lines, their manufacture from multiple parallel striations, and their association into clear arrangement or pattern as evidence of hominin manufacture (Fernandez-Jalvo et al. 2014)". The markings in the Rising Star Cave are said to be shallow, made by repeated grooving with a pointed stone tool that has left striations within the grooves and to form designs that are "geometric expressions" including crosshatching and cruciform shapes. "Composition and ordering" are said to be detectable in the set of grooved markings. Readers of this and their texts will no doubt have various opinions about these matters, mostly related to rather poorly defined or quantified terminology. I reserve judgement, but would draw little comfort from the similarities among equally unconvincing examples of early, especially very early, 'designs'. Two or even three half-convincing arguments do not add up to one convincing one.

The authors draw our attention to one very interesting issue: given the extensive grooving into the dolomite bedrock by sharp stone objects, where are these objects? Only one potential 'lithic artefact' is reported, a "tool-shaped rock [that] does resemble tools from other contexts of more recent age in southern Africa, such as a silcrete tool with abstract ochre designs on it that was recovered from Blombos Cave (Henshilwood et al. 2018)", also figured by Berger and colleagues. A number of problems derive from this comparison. First, 'tool-shaped rock' is surely a meaningless term: in a modern toolshed 'tool-shaped' would surely need to be refined into 'saw-shaped', 'hammer-shaped' or 'chisel-shaped' to convey meaning? The authors here seem to mean that the Rising Star Cave object is shaped like the Blombos painted stone fragment. But the latter is a painted fragment, not a tool and so any formal similarity is surely superficial and offers no support to the 'tool-ness' of the Rising Star Cave object. Does this mean that Homo naledi took (several?) pointed stone tools down the dark passageways, used them extensively and, whether worn out or still usable, took them all out again when they left? Not impossible, of course. And the lighting?

The authors rightly note that the circumstance of the markings "makes it challenging to assess whether the engravings are contemporary with the Homo naledi burial evidence from only a few metres away" and more pertinently, whether the hominins did the markings. Despite this honest admission, they are prepared to hypothesise that the hominin marked, without, it seems, any convincing evidence. If archaeologists took juxtaposition to demonstrate authorship, there would be any number of unlikely claims for the authorship of rock paintings or even stone tools. The idea that there were no entries into this Cave system between the Homo naledi individuals and the last two decades is an assertion, not an observation, and the relationship between hominins and designs no less so. In fact, the only 'evidence' for the age of the markings is given by the age of the Homo naledi remains, as no attempt at the, admittedly very difficult, perhaps impossible, task of geochronological assessment, has been made.

The claims relating to artificiality, age and authorship made here seem entangled, premature and speculative. Whilst there is no evidence to refute them, there isn't convincing evidence to confirm them.

References:

• Davidson, I. 2020. Marks, pictures and art: their contribution to revolutions in communication. Journal of Archaeological Method and Theory 27: 3 745-770.

• Henshilwood, C.S. et al. 2018. An abstract drawing from the 73,000-year-old levels at Blombos Cave, South Africa. Nature 562: 115-118.

• Rodriguez-Vidal, J. et al. 2014. A rock engraving made by Neanderthals in Gibralter. Proceedings of the National Academy of Sciences.

• White, Randall et al. 2020. Still no archaeological evidence that Neanderthals created Iberian cave art.

Reviewer #3 (Public Review):

This paper provides new information on the Dinaledi Chamber at the Rising Star Cave System. In short, a previously excavated area was expanded and resulted in the discovery of a cluster of bones appearing to be of one individual, a second similar cluster, and a third cluster with articulated elements (though with several individuals). Two of these clusters are argued to be intentionally buried individuals (the third one has not been investigated) and thus Homo naledi not only placed conspecifics in deep and hard to reach parts of caves but also buried them (apparently in shallow graves). This would be the oldest evidence of intentional burial. The main issue with the paper is that the purported burials were not fully excavated. Two are still in the ground, and one was removed in blocks but left unexcavated. As burials are mostly about sediments, it means the authors are lacking important lines of evidence. Instead, they bring other lines of argument as outlined below. While their preferred scenario is possible, there are important issues with the evidence as presented and they are severely hampered by the lack of detailed archaeological and geoarchaeological information both from the specific skeletal contexts and more generally from the chamber (because in fact the amount of excavation conducted here is still quite limited in scope). I also found that while the presentations of the various specialists in the team was quite good, the integration of these contributions into the main text was not. In particular, the geology of the cave system and the chamber need (especially what is known of the depositional and post-depositional processes) need to be better integrated into the presentation of the archaeology and the interpretation of the finds.

Often times the presence of articulated or mostly articulated skeletons is used to argue for intentional burial. This argument, however, is based on the premise that if not buried, these skeletons would have otherwise become disarticulated. Normally disarticulation would happen as a result of subsequent use of the site by hominins (e.g. purported burials in Neandertal cave sites) or by carnivores scavenging the body. Indeed this latter point is why bodies are buried so deeply in many Western societies (i.e. beyond the reach and smell of carnivores). Bodies can also be disarticulated by natural processes of deposit and erosion.

However, here in the case of the Dinaledi Chamber, we apparently don't have any of these other processes. The chamber was not used by carnivores and it was not a living area where H. naledi would have frequently returned and cleared out the space. As for depositional processes, it is more complex, but it is clear from Wiersma et al. that there is a steady, constant movement of these sediments towards drains. They also think that this process can account for the mix of articulated and non-articulated elements in the cave. Importantly, that same paper makes the argument that the formation of these sediments is not the result of water movement and that the cave has been dry since the formation of this deposit. So bodies lying on the surface and slowly covered by the formation of the deposit and slowly moving towards the drains could perhaps account for the pattern observed, meaning burial is not needed to account for articulations (note that more information on fabrics would be good in this context - orientation analysis of surface finds or of excavated finds is either completely lacking or minimal - see figure 13b and c report orientations on 79 bones of unknown context that appear to show perhaps elevated plunge angles and some slightly patterning in bearing but there is no associated statistics or text explaining the significance).

So, unless the team can provide some process that would have otherwise disarticulated these skeletons after the bodies arrived here and decomposed, their articulated state is not evidence of burial (no more than finding an articulated or mostly articulated bear skeleton deep in a European cave would suggest that it was buried).

As for the elemental analysis, what I understood from the paper is that the sediment associated with bones is different from the sediment not associated with bones. It is therefore unsurprising that the sediment associated with the reported skeletons clusters with sediments with bones. The linking argument for why this makes this sediment pit fill is unclear to me. Perhaps it is there, but as written I didn't follow it.

What the elemental analysis could suggest, I think, is that there has not been substantial reworking of the sediments (as opposed to the creep suggested by Wiersma et al.) since the bones leached these minerals into the sediment. What I don't know, and what is not reported, is how long after deposition we can expect the soil chemistry to change. If this elemental analysis were extended in a systematic way across the chamber (both vertically and horizontally) after more extensive excavations, I could see it perhaps being useful for better understanding the site formation processes and depositional context. As it is now, I did not see the argument in support of a burial pit.

The other line of evidence here is that some bones are sediment supported. The argument here is that when a body decomposes, bones that were previously held in place by soft tissues will be free to move and will shift their position. How the bones shift will differ depending on whether the body is surrounded by matrix (as they argue here in an excavated burial pit) or whether it is in the open (say, for instance, in a coffin) (and there are other possibilities as well - for instance wrapped in a shroud). Experiments have also shown the order in which the tendons, for instance, decompose and therefore which bones are likely to be free to move first or last.

I will note that this literature is poorly cited. I think the only two papers cited for how bodies decompose are Roksandic 2002 and Mickleburgh and Wescott 2019. The former is a review paper that summarizes a great many contexts that are clearly not appropriate here, and it generally makes the point that it is difficult to sort out, and it notes that progressively filled is an additional alternative to not buried/buried. The other looks at experimental data of bodies decomposing without being buried. In the paper here, this citation is used to argue that the body must have been buried. I don't see the linking argument at all. And the cited paper is mostly about how complicated it is to figure this all out and how many variables are still unaccounted for (including the initial positioning of the body and the consumption of the body by insects - something that is attested to at Naledi - plus snails - see not just Val but also Wiersma et al. and I think the initial Dirk et al. paper).

So the team here instead simply speaks of how the body decomposes in burials as if it is known. For the Feature 1 skeleton, the authors note that the ribs are "apparently" sediment supported and that a portion of the partial cranium is vertical or subvertical and sediment supported. For both of these, the figures show it very poorly. We really have to take their word for it. Second, I would have liked to have seen some reference and comparison to the literature for how the ribs should be in sediment burial cases. For the cranium, seems like a broken cranium resting on a surface will have vertical aspects regardless of sediment support. To the contrary, the orientation of the cranium will change depending on whether there is sediment holding it in place or not. But that argument is not made here. It is very hard from the figures to have a detailed idea of how these skeletons are oriented in the sediments, to know which elements are in articulation, which are missing, etc.

In the case of the Hill Antechamber Feature, an additional argument is made about the orientation of the finds in relation to the natural stratigraphy in this location. The team argues that the skeleton is lying more horizontally than the sediments and that in fact the foot is lying against the slope. First, there is no documentation of the slope of the layers here (e.g. a stratigraphic profile with the layers marked or a fabric analysis). There is a photo in the SI that says it shows sloping, but it needs some work. Second, this skeleton was removed in three blocks and then scanned. So the position of the skeleton is being worked out separate from its context. This is doable, but I would have liked to have seen some mention of how the blocks were georeferenced in the field and then subsequently in the lab and of how the items inside the block (i.e. the data coming from the CT scanner) were then georeferenced. I can think of ways I would try to do this, but without some discussion of this critical issue, the argument presented in Figure 10c is difficult to evaluate. Further, even if we accept this work, it is hard for me to see how the alignment of the foot is 15 degrees opposite the slope (the figure in the SI is better). It is also hard to understand the argument that the sediment separating the lower limb from the torso means burial. The team gives the explanation that if the body was in an open pit it would have been flat with no separation. Maybe. I mean I guess if the pit was flat. But there is no evidence here of a pit (at all). And what if the body was stuffed down the chute and was resting on a slope and covered with additional sediments from the chute (or additional bodies) as it decomposed? It seems that this should be the starting point here rather than imagining a pit.

One of the key pieces of evidence for demonstrating deliberate burial is the recognition of a pit. Pits can be identified because of the rupture they create in the stratigraphy when older sediments are brought to the surface, mixed, and then refilled into the pit with a different color, texture, compaction, etc. In some homogenous sediments a pit can be hard to detect and in some instances post-depositional processes (e.g. burrowing) can blur the distinction between the pit and the surrounding sediments. But the starting point of any discussion of deliberate burial has to be the demonstration of a pit. And I don't see it here. It might just be that the figures need to be improved. But I am skeptical because the team has taken the view that these finds can't be excavated. While I appreciate the scanning work done on the Antechamber find, it is not the same as excavating. Same comment for Features 1 and 2.

In short, my view is that they have an extremely interesting dataset. That H. naledi buried their dead here can't be excluded based on the data, but neither is it supported here. My view is that this paper is premature and that more excavation and the use of geoarchaeological techniques (especially micromorphology) are required to sort this out (or go a long way towards sorting it out).

Reviewer #3 (Public Review):

This study explores how condensin and telomere proteins cooperate to facilitate sister chromatid disjunction at chromosome ends during anaphase. Building upon previous results published by the same group (Reyes et al. 2015, Berthezene et al. 2020), the authors demonstrate that condensin is essential for sister telomere disjunction in anaphase in fission yeast. The primary role of condensin appears to be counteracting cohesin, which holds sister telomeres together. Furthermore, condensin is found to be enriched at telomeres, and this enrichment partially relies on Taz1, the principal telomere factor in S. pombe. The loss of Taz1 does not cause an obvious defect in sister telomere disjunction, which prevents drawing strong conclusions about its role in this process.

Reviewer #3 (Public Review):

In this study, Gadani et al. induced EAE in SJL/J mice and performed a comprehensive spatial transcriptomic analysis in areas of meningeal inflammation during the relapse phase of the disease. The authors found specific enrichment in spatial gene signatures (cluster 11) in the regions of increased contrast-enhancement by MRI (where meningeal extravasation of activated immune cells is observed) that overlap with signatures in the adjacent brain parenchyma, namely the thalamus. Several pathways were similarly upregulated in the meningeal-associated cluster 11 and adjacent parenchymal clusters (like adaptive mediated immunity, and antigen processing and presentation), suggestive of a "leakage" of inflammatory mediators from the meninges into the brain during the re-activation of disease. The tested hypothesis, as well as the data presented in this study, is quite interesting and novel.

Reviewer #3 (Public Review):

It is well known that as seasonal day length increases, molecular cascades in the brain are triggered to ready an individual for reproduction. Some of these changes, however, can begin to occur before the day length threshold is reached, suggesting that short days similarly have the capacity to alter aspects of phenotype. This study seeks to understand the mechanisms by which short days can accomplish this task, which is an interesting and important question in the field of organismal biology and endocrinology.

The set of studies that this manuscript presents is comprehensive and well-controlled. Many of the effects are also strong and thus offer tantalizing hints about the endo-molecular basis by which short days might stimulate major changes in body condition. Another strength is that the authors put together a compelling model for how different facets of an animal's reproductive state come "on line" as day length increases and spring approaches. In this way, I think the authors broadly fulfill their aims.

I do, however, also think that there are a few weaknesses that the authors should consider, or that readers should consider when evaluating this manuscript. First, some of the molecular genetic analyses should be interpreted with greater caution. By bioinformatically showing that certain DNA motifs exist within a gene promoter (e.g., FSHbeta), one is not generating robust evidence that corresponding transcription factors actually regulate the expression of the gene in question. In fact, some may argue that this line of evidence only offers weak support for such a conclusion. I appreciate that actually running the laboratory experiments necessary to generate strong support for these types of conclusions is not trivial, and doing so may even be impossible. I would therefore suggest a clear admission of these limitations in the paper.

Second, I have another issue with the interpretation of data presented in Figure 3. The data show that FSHbeta increases in expression in the 8Lext group, suggesting that endogenous drivers likely act to increase the expression of this gene despite no change in day length. However, more robust effects are reported for FSHbeta expression in the 10v and 12v groups, even compared to the 8Lext group. Doesn't this suggest that both endogenous mechanisms and changes in day length work together to ramp up FSHbeta? The rest of the paper seemed to emphasize endogenous mechanisms and gloss over the fact that such mechanisms likely work additively with other factors. I felt like there was more nuance to these findings than the authors were getting into.

Third, studies 1 - 3 are well controlled; however, I'm left wondering how much of an effect the transitions in day length might have on the underlying molecular processes that mediate changes in body condition. While the changes in day length are themselves ecologically relevant, the transitions between day length states are not. How do we know, for example, that more gradual changes in day length that occur over long timespans do not produce different effects at the levels of the brain and body? This seemed especially relevant for study 3, where animals experience a rather sudden change in day length. I recognize that these experimental methods are well described in the literature, and they have been used by endocrinologists for a long time; nonetheless, I think questions remain.

Reviewer #3 (Public Review):

In this manuscript, Touray et al investigate the mechanisms by which PIP5Pase and RAP1 control VSG expression in T. brucei and demonstrate an important role for this enzyme in a signalling pathway that likely plays a role in antigenic variation in T. brucei.

The methods used in the study are rigorous and well-controlled. The authors convincingly demonstrate that RAP1 binds to PI(3,4,5)P3 through its N-terminus and that this binding regulates RAP1 binding to VSG expression sites, which in turn regulates VSG silencing. Overall their results support the conclusions made in the manuscript.

There are a few small caveats that are worth noting. First, the analysis of VSG derepression and switching in Figure 1 relies on a genome that does not contain minichromosomal (MC) VSG sequences. This means that MC VSGs could theoretically be misassigned as coming from another genomic location in the absence of an MC reference. As the origin of the VSGs in these clones isn't a major point in the paper, I do not think this is a major concern, but I would not over-interpret the particular details of switching outcomes in these experiments.

The authors state that "our data imply that antigenic variation is not exclusively stochastic." I am not sure this is true. While I also favor the idea that switching is not exclusively stochastic, evidence for a signaling pathway does not necessarily imply that antigenic variation is not stochastic. This pathway could be important solely for lifecycle-related control of VSG expression, rather than antigenic variation during infection. Nevertheless, these data are critical for establishing a potential pathway that could control antigenic variation and thus represent a fundamental discovery.

Another aspect of this work that is perhaps important, but not discussed much by the authors, is the fact that signalling is extremely poorly understood in T. brucei. In Figure 1B, the RNA-seq data show many genes upregulated after expression of the Mut PIP5Pase (not just VSGs). The authors rightly avoid claiming that this pathway is exclusive to VSGs, but I wonder if these data could provide insight into the other biological processes that might be controlled by this signaling pathway in T. brucei.

Overall, this is an excellent study that represents an important step forward in understanding how antigenic variation is controlled in T. brucei. The possibility that this process could be controlled via a signalling pathway has been speculated for a long time, and this study provides the first mechanistic evidence for that possibility.

Reviewer #3 (Public Review):

Bierman et al. present a novel statistical framework for examining the subcellular localisation of RNA molecules. Subcellular Patterning Ranked Analysis With Labels, SPRAWL, uses the data available in multiplexed single-cell imaging datasets to assign four metrics of localisation patterns to RNA at a gene per cell level. These easy-to-understand scores, ranging from -1 to 1, can be averaged to detect cell-type specific spatial patterns or used in tandem with tools for RNA 3' UTR length or splicing state to determine the correlation between subcellular localisation and RNA isoforms. Such quantitive association between RNA isoforms and localisation provides a useful tool to determine candidate genes for future studies.

The peripheral and central scores indicate the proximity of RNA molecules to the cell boundary and centre of the cell respectively in relation to other RNA present in the cell. Whilst understanding whether a gene tends to be localised to the cellular membrane is important, it is unclear what biological benefits the central metric gives compared to high "anti-peripheral" scores considering that no single organelle (eg. the nucleus) is located specifically at the centre of the cell in all cell-types.

The punctate and radial patterning scores provide information on the spatial aggregation of RNA molecules of a given gene within a cell. Whilst the punctate score is easy to understand as simply the distance between RNA, the radial score, the angle between RNA, is harder to understand from the main text and would benefit from a schematic showing how this is in respect to the cell-boundary centroid.

Despite endeavouring to create a robust statistical measure of RNA subcellular localisation, this paper is full of inconsistencies. Values (eg. Pearson correlation coefficient values, number of significant genes, number of total genes) and names (eg. cell types, gene names) stated throughout the main text and figures/table do not match repeatedly and without fixing these disparities, the conclusions from this paper are hard to believe.

Reviewer #3 (Public Review):

The article by Ma et al pursues the previous work of the Schekman group, exploring the mechanisms of targeting of miRNAs into extracellular vesicles (EVs), or possibly exosomes, in HEK293 and U2OS cells. The authors had identified YBX1 as an RNA-binding protein required for the sorting of miR223 into CD63-expressing small EVs, probably mainly exosomes. Here they further observed that YBX1 directly binds miR223, which also binds to another protein, YBAP1, localized in mitochondria, where it sequesters miR223, thus preventing its targeting to MVBs' intraluminal vesicles. They observe the association of YBX1-containing P-bodies in the cytoplasm with mitochondria and with enlarged Rab5-endosomes and propose that this step is required for the exchange of miR223 for its loading into MVBs intraluminal vesicles and future exosomes.

The biochemical parts of the article, with quantitative experiments to decipher the molecular interactions of YBX1 and YBAP1 with miR223, are nicely performed and convincing. By contrast, the parts on the involvement of YBX1 and of YBAP1 in the release of miR223 in EVs or exosomes are more correlative than demonstrative and lack some controls. In particular, it is far-fetched to conclude from the observed movement (which may be serendipitous) of 2 P-bodies between mitochondria and enlarged endosomes (without any visualization of the miR) that this movement may be instrumental in the transfer of miR223 between mitochondria and putative exosomes (figures 6 and model in figure 7).

The experiments designed to evidence the mechanisms of miR223 release in EVs are also not sufficiently controlled and analysed to really support the interpretations. And the EV isolation steps are not performed in a way that supports the actual exosomal nature (i.e. exclusive origin from multivesicular endosome) of the EV analysed.

Another experimental weakness is that the authors make strong conclusions on MVBs and exosomes when they only analyse artificially-enlarged endosomes induced by overexpression of mutant Rab5. Although this approach has been used previously and shown CD63 in these induced enlarged compartments, it is an artificial blocking of normal endosomal trafficking, and may not reflect the situation of intracellular trafficking of miR223 in normal cells.

Reviewer #3 (Public Review):

Sarkari et al. describe the effects of TTFields on inter-cellular communication structures called tunneling nanotubes in malignant pleural mesothelioma cells. Recent studies have implicated these F-actin-based nanotubes in promoting malignant transformation and biology by allowing long-range communications between malignant cells. The authors suggest that TTFields disrupt these structures by impacting the expression of genes involved in nanotube formation and cell proliferation. Although TTFields are thought to affect tubulin-based structures, recent studies suggest that TTFields also impact actin-based structures. Therefore, the authors' findings are in keeping with this new understanding. They also found that TTFields upregulated marker genes in immunity. This is one of the first studies that implicate TTFields in these tunneling nanotube structures. Overall, the study adds to our understanding of TTFields on various cellular structures. However, conclusions are only partially supported by the data presented. The study is largely descriptive and there are many areas that need to be addressed to substantively improve the premise and rigors and strengthen the conclusions.

Reviewer #3 (Public Review):

The authors investigate the potential effect of OGlcNacylation on the activity of the DNA methyltransferase DNMT1.

Some results that are convincingly obtained include:<br /> - There is more overall OGlcNacylation when Glucose concentration in the culture medium or the feed is high;<br /> - DNMT1 is OGlcNacylated, and more so in high glucose or on rich chow;<br /> - The position S878 can be OGlcNacylated;<br /> - The activity of transfected DNMT1 is decreased in high glucose conditions. This effect is lessened when S878 is mutated to A or D.

Some results that are suggested but not fully backed by experimental data include:<br /> - This process happens to the endogenous protein under physiologically relevant conditions;<br /> - This process is responsible for changes in DNA methylation, leading to changes in gene expression, leading to increased ROS and increased apoptosis.

Studying the connection between cellular metabolism and epigenetic phenomena is interesting. However, I feel that the article falls short of its aims because of the limits of the experimental system, some missing controls, and some data overinterpretation.

Reviewer #3 (Public Review):

This US study presents findings from an online survey and in-person interviews of healthcare providers regarding themes associated with cervical screening in federally qualified health centres (FQHCs). The study provides insights during the post-acute phase of the pandemic into a range of areas, including perceived changes in the provision of cervical cancer screening services and the impact of the pandemic, staffing and systems barriers to cervical cancer screening, strategies for tracking missed screens and catch-ups, follow-up of abnormal screening results, as well as attitudes towards HPV self-sampling. Results indicate persisting pandemic-related impacts on patient engagement and staffing, as well as system barriers to effective screening, catch-up of missed screens and follow-ups. Taken together, these issues may lead to increases in cervical cancer in the long-term in populations serviced by these centres, if measures are not taken to adequately support them. Participants were recruited from various regions in the US, however, the study was not conducted using a nationally-representative sample. Although highlighted issues are informative, findings cannot be generalised and larger studies are warranted in the future to monitor cervical screening provision and outcomes in FQHCs.

Reviewer #3 (Public Review):

This study presents a new pipeline for mapping the auditory-language pathway in children with profound congenital sensorineural hearing loss (SNHL), focusing on those with inner ear malformations and/or cochlear nerve deficiency (IEM&CND). Using structural and diffusional MRI, the researchers investigated the structural fiber properties of the auditory-language networks in affected children under six years old. Findings suggest that the language pathway is more sensitive to peripheral auditory than the central auditory pathway, emphasizing the need for early intervention to provide speech inputs. The study also proposes a comprehensive pre-surgical evaluation from the cochlea to the auditory-language network.

Strengths:

1. Investigating fiber properties across various brain network levels (from peripheral structures to central auditory and higher-level language pathways) using high-resolution diffusion imaging and an innovative pipeline.

2. Evaluating presurgical fiber properties in two subgroups of SNHL children (cochlear implant and auditory brainstem implant candidates) to demonstrate the relationship between peripheral auditory structure damage and the development of auditory-language structural pathways.

Weaknesses:

1. Limited sample size: The study analyzed data from 13 SNHL children and 10 normal-hearing children, potentially restricting the validity and reproducibility of the findings, particularly in correlation results based on individual differences.

2. Lack of speech and language behavioral measures: Although the researchers collected behavioral data post-CI/ABI surgery for most participants, no such data was reported. Consequently, the association between presurgical fiber measures and postsurgical outcomes remains unclear.

3. Unclear practical implications: The relevance of the presurgical evaluation of the auditory-language network for surgical decision-making and prognosis estimation is not evident, as fiber measures may not correlate with behavioral outcomes.

Reviewer #3 (Public Review):

Summary:

A useful and potentially powerful analysis of gene expression correlations across major organ and tissue systems that exploits a subset of 310 humans from the GTEx collection (subjects for whom there are uniformly processed postmortem RNA-seq data for 18 tissues or organs). The analysis is complemented by a Shiny R application web service.

The need for more multisystems analysis of transcript correlation is very well motivated by the authors. Their work should be contrasted with more simple comparisons of correlation structure within different organs and tissues, rather than actual correlations across organs and tissues.

Strengths and Weaknesses:

The strengths and limitations of this work trace back to the nature of the GTEx data set itself. The authors refer to the correlations of transcripts as "gene" and "genetic" correlations throughout. In fact, they name their web service "Genetically-Derived Correlations Across Tissues". But all GTEx subjects had strong exposure to unique environments and all correlations will be driven by developmental and environmental factors, age, sex differences, and shared and unshared pre- and postmortem technical artifacts. In fact we know that the heritability of transcript levels is generally low, often well under 25%, even studies of animals with tight environmental control.

This criticism does not comment materially detract for the importance and utility of the correlations-whether genetic, GXE, or purely environmental-but it does mean that the authors should ideally restructure and reword text so as to NOT claim so much for "genetics". It may be possible to incorporate estimates of chip heritability of transcripts into this work if the genetic component of correlations is regarded as critical (all GTEx cases have genotypes).

Appraisal of Work on the Field:

There are two parts to this paper: 1. "case studies" of cross-tissue/organ correlations and 2. the creation of an R/Shiny application to make this type of analysis much more practical for any biologist. Both parts of the work are of high potential value, but neither is fully developed. My own opinion is that the R/Shiny component is the more important immediate contribution and that the "case studies" could be placed in the context of a more complete primer. Or Alternatively, the case studies could be their own independent contributions with more validation.

Reviewer #3 (Public Review):

In this paper, the authors analyze a large previously published deep mutational scanning data set using a reference-free regression approach. They extract the contributions of single locus and epistatic effects to the functionality of the sequence (no, weak or strong transcription activation of two response elements). They find that pairwise epistasis plays a crucial and dominant role at creating functional sequences and at connecting the functional sequence space.

I enjoyed reading the paper and the topic (role of epistasis at creating and connecting functional sequences; development of measures of epistasis) is very exciting to me. However, I found it difficult to judge the strength of the paper both because it is written in a rather dense and yet potentially redundant fashion (see comment 1) and because I was left with a number of questions upon reading. I will focus on conceptual questions in the following comments, since I am not able to judge the statistical approach in detail.

1/ Regarding the biological result (importance of pairwise epistasis) I was wondering how potentially redundant the consecutive sections of the paper are. In which situation would the authors expect that pairwise epistasis does *not* play a crucial role for mutational steps, trajectories, or space connectedness, if it is dominant in the genotype-phenotype landscape? I would also appreciate an explanation of how much new biological results this paper delivers as compared with the paper in which the data were published (which I, unfortunately, cannot access at the moment of writing this report).

2a/ Regarding the regression approach: I very much appreciate a reference-free approach to the estimation of epistasis. However, I would enjoy an explanation of how the results would have been (potentially) different if a reference-based approach was used, and how it compares with other reference-free approaches to estimating epistasis (e.g., linear regression or the gamma statistics of Ferretti et al. 2015).

2b/ When comparing the outcomes with and without epistasis, I understood that the authors compare the estimated "full model" with the outcome if epistatic effects were ignored - but without a new estimation of main effects if epistasis is ignored. Wouldn't that be a more fair comparison?

2c/ Where do the authors see the applicability of their approach to data beyond those analyzed in the present study? What are the requirements to use it? Does it only work for combinatorially complete landscapes? I did not have a chance to look at the code - how easily could other researchers apply the approach to their data?

Reviewer #3 (Public Review):

This work provides a novel design of implantable and high-density EMG electrodes to study muscle physiology and neuromotor control at the level of individual motor units. Current methods of recording EMG using intramuscular fine-wire electrodes do not allow for isolation of motor units and are limited by the muscle size and the type of behavior used in the study. The authors of myomatrix arrays had set out to overcome these challenges in EMG recording and provided compelling evidence to support the usefulness of the new technology.

Strengths:

• They presented convincing examples of EMG recordings with high signal quality using this new technology from a wide array of animal species, muscles, and behavior.<br /> • The design included suture holes and pull-on tabs that facilitate implantation and ensure stable recordings over months.<br /> • Clear presentation of specifics of the fabrication and implantation, recording methods used, and data analysis

Weaknesses:

• The justification for the need to study the activity of isolated motor units is underdeveloped. The study could be strengthened by providing example recordings from studies that try to answer questions where isolation of motor unit activity is most critical. For example, there is immense value for understanding muscles with smaller innervation ratio which tend to have many motor neurons for fine control of eyes and hand muscles.

Reviewer #3 (Public Review):

The manuscript describes new ligand-bound structures within the larger bile acid sodium symporter family (BASS). This is the primary advance in the manuscript, together with molecular simulations describing how sodium and the bile acids sit in the structure when thermalized. What I think is fairly clear is that the ligands are more stable when the sodiums are present, with a marked reduction in RMSD over the course of repeated trajectories. This would be consistent with a transport model where sodium ions bind first, and then the bile acid binds, followed by a conformational change to another state where the ligands unbind.

While the authors mention that BASS transporters are thought to undergo an elevator transport mechanisms, this is not tested here. In my reading, all the crystal structures describe the same conformational state, and the simulations do not make an attempt to induce a transition on accessible simulation timescales. Instead, there is a morph between two states where different substrates are bound, which induces a conformational change that looks unrelated to the transport cycle.

Instead, the focus is on what kinds of substrates bind to this transporter, interrogating this with isothermal calorimetry together with mutations. With a Kd in the micromolar range, even the best binder, pantoate, actually isn't a particularly tight binder in the pharmaceutical sense. For a transporter, tight binding is not actually desirable, since the substrate needs to be able to leave after conformational change places it in a position accessible to the other side.

There is one really important point that readers and authors should be aware of. In Figure 2A, the names are not consistent with the chemical structure. "-ate" denotes when a carboxylic acid is in the deprotonated form, creating a charged carboxylate. What is drawn is pantoic acid, ketopantoic acid, and pantoethenic acid. Less importantly, the wedges and hashes for the methyl group are arguably not appropriate, since the carbon they are attached to is not a chiral center. For the crystallization, this makes no difference, since under near-neutral pKas the carboxylic acid will spontaneously deprotonate, and the carboxylate form will be the most common. However, if the structures in Figure 2A were used for classical molecular simulation, that would be a big problem, since now that would be modeling the much rarer neutral form rather than the charged state. I am reasonably sure based on Figure 5 that the MD correctly modeled the deprotonated form with a carboxylate, but that is inconsistent with Figure 2A. Otherwise, the structure and simulation analysis falls into the mainstream of modern structural biology work.

Reviewer #3 (Public Review):

The authors investigate the mechanisms by which ISG65 and C3 recognize and interact with each other. The major strength is the identification of eco-site by determining the cryoEM structure of the complex, which suggests new intervention strategies. This is a solid body of work that has an important impact on parasitology, immunology, and structural biology.

Reviewer #3 (Public Review):

The manuscript describes a combination of in vitro and in vivo results implicating Dyrk1a in the regulation of mTORC. Particular strengths of the data are this combination of cell and whole animal (drosophila) based studies. However, most of the experiments seem to lack a key additional experimental condition that could increase confidence in the authors' conclusions. Overall some tantalizing data is presented. However, there are several issues that should be clarified or otherwise addressed with additional data.

1. In Figure 1G, why not test overexpression levels of Dyrk1a via western rather than only looking at the RNA levels?

2. In Figure 2, while there is clearly TSC1 protein in the Dyrk1a and FLAG-Dyrk1a IPs that supports an interaction between the proteins, it would be good to see the reciprocal IP experiment wherein TSC1 or TSC2 are pulled down and then the blot probed for Dyrk1a.

3. Figures 3 A and D tested the effects of Dyrk1a knockdown using different methods in different cell lines. This is a reasonable approach to ascertain the generalizability of findings. However, each experiment is performed differently. For example, in 3A, the authors found no difference in baseline pS6, so they did a time course of treatment to induce phosphorylation and found differences depending on Dyrk1a expression. In 3D, they only show baseline effects from the CRISPr knockdown. Why not do the time course as well for consistency? Also, why the inconsistency in approaches wherein one shows baseline effects and the other does not? The authors could also consider the pharmacologic inhibition of Dyrk1a activity as well.

4. In Figure 4, RHEB overexpression increases cell size in both Dyrk1a wt and Dyrk1a shRNA treated cells, although the magnitude of the effect appears reduced in Dyrk1a shRNA cells. However, there is the possibility here that RHEB acts independently of Dyrk1a. Why not also do the experiment of Figure 1 wherein Dyrk1a is overexpressed and then knockdown RHEB in that context? If the hypothesis is supported, then RHEB knockdown should eliminate the cell size effect of Dyrk1a overexpression.

5. The discussion should incorporate relevant findings from other models, such as Arabidopsis. Barrada et al., Development (2019), 146 (3).

Reviewer #3 (Public Review):

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

Reviewer #3 (Public Review):

The authors set out to demonstrate the utility of functional ultrasound for evaluating changes in brain hemodynamics elicited acutely and subacutely by the middle cerebral artery occlusion model of ischemic stroke in awake rats.

Functional ultrasound affords a distinct set of tradeoffs relative to competing imaging modalities. Acclimatization of rats for awake imaging has proven difficult with most, and the high quality of presented data in awake rats is a major achievement. The major weakness of the approach is in its being restricted to single-slice acquisitions, which also complicates the registration of acquisition across multiple imaging sessions within the same animal. Establishing that awake imaging represents an advancement in relation to studies under anesthesia hinges upon the establishment of the level of stress experienced by the animals in the course of imaging, i.e., requires providing data on the assessment of stress over the course of these long imaging sessions. This is particularly significant given how significant a stressor physical restraint has been established to be in rodent models of stress. Furthermore, assessment of the robustness of these measurements is of particular significance for supporting the wide applicability of this approach to preclinical studies of brain injury: the individual animal data (effect sizes, activation areas, kinetics) should thus be displayed and the statistical analysis expanded. Both within-subject, within/across sessions, and across-subjects variability should be evaluated. Thoughtful comments on the relationship between power doppler signal and cerebral blood volume are important to include and facilitate comparisons to studies recording other blood volume-weighted signals. Finally, the contextualization of the observations with respect to other studies examining acute and subacute changes in brain hemodynamics post focal ischemic stroke in rats is needed. It is also quite helpful, for establishing the robustness of the approach, when the statistical parametric maps are shown in full (i.e. unmasked).

Reviewer #3 (Public Review):

In this manuscript, Rossato and colleagues present a method for real-time decoding of EMG into putative single motor units. Their manuscript details a variety of decision points in their code and data collection pipeline that lead to a final result of recording on the order of ~10 putative motor units per muscle in human males. Overall the manuscript is highly restricted in its potential utility but may be of interest to aficionados. For those outside the field of human or nonhuman primate EMG, these methods will be of limited interest.

Notes<br /> 1. Artificial data should be used with this method to provide ground truth performance evaluations. Without it, the study assumptions are unchallenged and could be seriously flawed.

2. From the point of view of a motor control neuroscientist studying movement in animals other than humans or non-human primates, the title was misleadingly hopeful. The use case presented in this study requires human participants to perform isometric contractions, facilitating spatially redundant recordings across the muscle for the algorithm to work. It is unclear whether these methods will be of utility to use cases under more physiological conditions (ie. dynamic movement).

3. The text states that "EMG signals recorded with an array of electrodes can be considered and instantaneous mixture of the original motor unit spike trains and their delayed versions." While this may be a true statement, it is not a complete statement, since motor units at distal sites may be shared, not shared, or novel. It was not clear to me whether the diversity of these scenarios would affect the performance of the software or introduce artifacts. In other words, if at site 1 you can pick up the bulk signal of units 1,2,3,4; at site two you pick up the signals of units 2,3,4,5 and site three you pick up the signal of units 3,4,5,6, what does the algorithm assume is happening and what does it report and why?

4. I could not fully appreciate the performance gap solved by the current methods. What was not achievable before that is now achievable? The 125 ms speed of deconvolution? What was achievable before? Intro text around ln 85 states that 'most of the current implementations of this approach rely on offline processing, which restricts its ability to be used..." but no reference is provided here about what the non 'most' of can achieve.

5. Relatedly, it would have been nice to see a proof of concept using real-time feedback for some kind of biofeedback signal. If that is the objective here, why not show us this? I found the actual readout metrics of performance rather esoteric. They may be of interest to very close experts so I will defer to them for input.

6. I was disappointed to see that only male participants are used because of some vague statement that 'it is widely known in the field' that more motor units can be resolved in males, without thorough referencing. It seems that the objective of the algorithm is the speed of analysis, not the number of units, which makes the elimination of female participants not justified.

7. Human curation is often used in spike sorting, but the description of criteria used in this step or how the human curation choices are documented is missing.

8. The authors might try to add text to be more circumspect about the contributions of this method. I would recommend emphasizing the conceptual advances over the specifics of the performance of the algorithm since processor speed and implementation of the ideas in a faster environment (Matlab can be slow) will change those outcomes in a trivial way. Yet, much of the results section is very focused on these metrics.<br /> Minor<br /> Ln 115, "inversing" is not a word. "inverse" is not a verb<br /> Ln 186, typo, bioadhesive<br /> MVC should be defined on first use. It is currently defined on 3rd use or so.<br /> The term rate is used in a variety of places without units. Eg line 465 but not limited to that

Reviewer #3 (Public Review):

This paper analyses self-citation rates in the field of Neuroscience, comprising in this case, Neurology, Neuroscience and Psychiatry. Based on data from Scopus, the authors identify self-citations, that is, whether references from a paper by some authors cite work that is written by one of the same authors. They separately analyse this in terms of first-author self-citations and last-author self-citations. The analysis is well-executed and the analysis and results are written down clearly. There are some minor methodological clarifications needed, but more importantly, the interpretation of some of the results might prove more challenging. That is, it is not always clear what is being estimated, and more importantly, the extent to which self-citations are "problematic" remains unclear.

When are self-citations problematic? As the authors themselves also clarify, "self-citations may often be appropriate". Researchers cite their own previous work for perfectly good reasons, similar to reasons of why they would cite work by others. The "problem", in a sense, is that researchers cite their own work, just to increase the citation count, or to promote their own work and make it more visible. This self-promotional behaviour might be incentivised by certain research evaluation procedures (e.g. hiring, promoting) that overly emphasise citation performance. However, the true problem then might not be (self-)citation practices, but instead, the flawed research evaluation procedures that emphasis citation performance too much. So instead of problematising self-citation behaviour, and trying to address it, we might do better to address flawed research evaluation procedures. Of course, we should expect references to be relevant, and we should avoid self-promotional references, but addressing self-citations may just have minimal effects, and would not solve the more fundamental issue.

Some other challenges arise when taking a statistical perspective. For any given paper, we could browse through the references, and determine whether a particular reference would be warranted or not. For instance, we could note that there might be a reference included that is not at all relevant to the paper. Taking a broader perspective, the irrelevant reference might point to work by others, included just for reasons of prestige, so-called perfunctory citations. But it could of course also include self-citations. When we simply start counting all self-citations, we do not see what fraction of those self-citations would be warranted as references. The question then emerges, what level of self-citations should be counted as "high"? How should we determine that? If we observe differences in self-citation rates, what does it tell us?

For example, the authors find that the (any author) self-citation rate in Neuroscience is 10.7% versus 15.9% in Psychiatry. What does this difference mean? Are psychiatrists citing themselves more often than neuroscientists? First author men showed a self-citation rate of 5.12% versus a self-citation rate of 3.34% of women first authors. Do men engage in more problematic citation behaviour? Junior researchers (10-year career) show a self-citation rate of about 5% compared to a self-citation rate of about 10% for senior researchers (30-year career). Are senior researchers therefore engaging in more problematic citation behaviour? The answer is (most likely) "no", because senior authors have simply published more, and will therefore have more opportunities to refer to their own work. To be clear: the authors are aware of this, and also take this into account. In fact, these "raw" various self-citation rates may, as the authors themselves say, "give the illusion" of self-citation rates, but these are somehow "hidden" by, for instance, career seniority.

Again, the authors do consider this, and "control" for career length and number of publications, et cetera, in their regression model. Some of the previous observations then change in the regression model. Neuroscience doesn't seem to be self-citing more, there just seem to be junior researchers in that field compared to Psychiatry. Similarly, men and women don't seem to show an overall different self-citation behaviour (although the authors find an early-career difference), the men included in the study simply have longer careers and more publications.

But here's the key issue: what does it then mean to "control" for some variables? This doesn't make any sense, except in the light of causality. That is, we should control for some variable, such as seniority, because we are interested in some causal effect. The field may not "cause" the observed differences in self-citation behaviour, this is mediated by seniority. Or is it confounded by seniority? Are the overall gender differences also mediated by seniority? How would the selection of high-impact journals "bias" estimates of causal effects on self-citation? Can we interpret the coefficients as causal effects of that variable on self-citations? If so, would we try to interpret this as total causal effects, or direct causal effects? If they do not represent causal effects, how should they be interpreted then? In particular, how should it "inform author, editors, funding agencies and institutions", as the authors say? What should they be informed about?

The authors also "encourage authors to explore their trends in self-citation rates". It is laudable to be self-critical and review ones own practices. But how should authors interpret their self-citation rate? How useful is it to know whether it is 5%, 10% or 15%? What would be the "reasonable" self-citation rate? How should we go about constructing such a benchmark rate? Again, this would necessitate some causal answer. Instead of looking at the self-citation rate, it would presumably be much more informative to simply ask authors to check whether references are appropriate and relevant to the topic at hand.

In conclusion, the study shows some interesting and relevant differences in self-citation rates. As such, it is a welcome contribution to ongoing discussions of (self) citations. However, without a clear causal framework, it is challenging to interpret the observed differences.

Reviewer #3 (Public Review):

The present study aims to investigate whether pain influences cortical excitability. To this end, heat pain stimuli are applied to healthy human participants. Simultaneously, TMS pulses are applied to M1 and TMS-evoked potentials (TEPs) and pain ratings are assessed after each TMS pulse. TEPs are used as measures of cortical excitability. The results show that TEP amplitudes at 45 msec (N45) after TMS pulses are higher during painful stimulation than during non-painful warm stimulation. Control experiments indicate that auditory, somatosensory, or proprioceptive effects cannot explain this effect. Considering that the N45 might reflect GABAergic activity, the results suggest that pain changes GABAergic activity. The authors conclude that TEP indices of GABAergic transmission might be useful as biomarkers of pain sensitivity.

Pain-induced cortical excitability changes is an interesting, timely, and potentially clinically relevant topic. The paradigm and the analysis are sound, the results are mostly convincing, and the interpretation is adequate. The following clarifications and revisions might help to improve the manuscript further.

1. Non-painful control condition. In this condition, stimuli are applied at warmth detection threshold. At this intensity, by definition, some stimuli are not perceived as different from the baseline. Thus, this condition might not be perfectly suited to control for the effects of painful vs. non-painful stimulation. This potential confound should be critically discussed.<br /> 2. MEP differences between conditions. The results do not show differences in MEP amplitudes between conditions (BF 1.015). The analysis nevertheless relates MEP differences between conditions to pain ratings. It would be more appropriate to state that in this study, pain did not affect MEP and to remove the correlation analysis and its interpretation from the manuscript.<br /> 3. Confounds by pain ratings. The ISI between TMS pulses is 4 sec and includes verbal pain ratings. Considering this relatively short ISI, would it be possible that verbal pain ratings confound the TEP? Moreover, could the pain ratings confound TEP differences between conditions, e.g., by providing earlier ratings when the stimulus is painful? This should be carefully considered, and the authors might perform control analyses.<br /> 4. Confounds by time effects. Non-painful and painful conditions were performed in a fixed order. Potential confounds by time effects should be carefully considered.<br /> 5. Data availability. The authors should state how they make the data openly available.

Reviewer #3 (Public Review):

In this manuscript, Magnuson and colleagues investigate the meiotic functions of ARID1A, a putative DNA binding subunit of the SWI/SNF chromatin remodeler BAF. The authors develop a germ cell specific knockout mouse model using Stra8-cre and observe that ARID1A-deficient cells undergo pachytene arrest, although due to inefficiency of the Stra8-cre system the mice retain ARID1A-expressing cells that yield sperm and allow fertility. Because ARID1A was found to accumulate at the XY body late in Prophase I, the authors suspected a potential role in meiotic silencing and by RNAseq observe significant misexpression of sex-linked genes that typically are silenced at pachytene. They go on to show that ARID1A is required for exclusion of RNA PolII from the sex body, consistent with a meiotic sex chromosome inactivation (MSCI) defect. The authors proceed to investigate the impacts of ARID1A on chromatin accessibility and H3.3 deposition genome-wide. H3.3 is known be regulated by ARID1A and is linked to silencing, and here the authors find that upon loss of ARID1A, overall H3.3 enrichment at the sex body as measured by IF failed to occur, but H3.3 was enriched specifically at transcriptional start sites of sex-linked genes that are normally regulated by ARID1A. The results suggest that ARID1A normally prevents H3.3 accumulation at target promoters on sex chromosomes and based on additional data, restricts H3.3 to intergenic sites. Finally, the authors present data implicating ARID1A and H3.3 occupancy in DSB repair, finding that ARID1A KO leads to a reduction in focus formation by DMC1, a key repair protein. Overall the paper covers a lot of ground, provides important new insights into the process of MSCI from the perspective of chromatin composition and structure, and raises many interesting questions. In general the paper is well written and the data are clear. Specific points to address are as follows:

1. A challenge with the author's CKO model is the incomplete efficiency of ARID1A loss, due to incomplete CRE-mediated deletion. The authors effectively work around this issue, but they don't state specifically what percentage of CKO cells lack ARID1A staining. This information should be added. They refer to cells that retain ARID1A staining in CKO testes as 'internal controls' but this reviewer finds that label inappropriate. Although some cells that retain ARID1A won't have undergone CRE-mediated excision, others may have excised but possibly have delayed kinetics of deletion or ARID1A RNA/protein turnover and loss. Such cells likely have partial ARID1A depletion to different extents and therefore in some cases are no longer wild-type. In subsequent figures in which co-staining for ARID1A is done, it would be appropriate for the authors to specify if they are quantifying all cells from CKO testes, or only those that lack ARID1A staining.

2. The authors don't see defects in a few DDR markers in ARID1A CKO cells and conclude that the role of ARID1A in silencing is 'mutually exclusive to DDR pathways' (p 12) and 'occurs independently of DDR signaling' (p30). The data suggest that ARID1A may not be required for DDR signaling, but do not rule out the possibility that ARID1A is downstream of DDR signaling (and the authors even hypothesize this on p30). The data provided do not justify the conclusion that ARID1A acts independently of DDR signaling.

3. After observing no changes in levels or localization of H3.3 chaperones, the authors conclude that 'ARID1A impacts H3.3 accumulation on the sex chromosomes without affecting its expression or incorporation during pachynema.' It's not clear to this reviewer what the authors mean by this. Aside from the issue of not having tested DAXX or HIRA activity, are they suggesting that some other process besides altered incorporation leads to H3.3 accumulation and if so what process would that be?

4. The authors find an interesting connection between certain regions that gained chromatin accessibility after ARID1A loss (clusters G1 and G3) and presence of the PRDM9 sequence motif. The G1 and G3 clusters also show DMC1 occupancy and H3K4me3 enrichment. However, an additional cluster with gained accessibility (G4) also shows DMC1 occupancy and H3K4me3 enrichment but unlike clusters G1 and G3 has modest H3.3 accumulation. The paper would benefit for additional discussion about the G4 cluster (which encompasses 960 peak calls). Is there any enrichment of PRDM9 sites in G4? If H3.3 exclusion governs meiotic DSBs, how does cluster G4 fit into the model?

5. The impacts of ARID1A loss on DMC1 focus formation (reduced sex chromosome association) are very interesting and also raise additional questions. Are DMC1 foci on autosomes also affected during pachynema? The corresponding lack of apparent effect on RAD51 implies that breaks are still made and resected, enabling RAD51 filament formation. A more thorough quantitative assessment of RAD51 focus formation will be interesting in the long run, enabling determination of the number of break sites and the kinetics of repair, which the authors suggest is perturbed by ARID1A loss but don't directly test. It isn't clear how a nucleosomal factor (H3.3) would influence loading of recombinases onto ssDNA, especially if the alteration is not at the level of resection and ssDNA formation. Additional discussion of this point is warranted. Lastly, there currently are various notions for the interplay between RAD51 and DMC1 in filament formation and break repair, and brief discussion of this area and the implications of the new findings from the ARID1A CKO would strengthen the paper further.

Reviewer #3 (Public Review):

Neuronal migration is one of the key processes for appropriate neuronal development. Defects in neuronal migration are associated with different brain disorders often accompanied by intellectual disabilities. Therefore, the study of the mechanisms involved in neuronal migration helps to understand the pathogenesis of some brain malformations and psychiatric disorders.

FMRP is an RNA-binding protein implicated in RNA metabolism regulation and mRNA local translation. FMRP loss of function causes fragile X syndrome (FXS), the most common form of inherited intellectual disability. Previous studies have shown the role of FMRP in the multipolar to bipolar transition during the radial migration in the cortex and its possible relation with periventricular heterotopia and altered synaptic communication in humans with FXS. However, the role of FMRP in neuronal tangential migration is largely unknown. In this manuscript, the authors aim to decipher the role of FMRP in the tangential migration of neuroblasts along the rostral migratory stream (RMS) in the postnatal brain. By extensive live-imaging analysis of migrating neuroblasts along the RMS, they demonstrate the requirement of FMRP for neuroblast migration and centrosomal movement. These migratory defects are cell-autonomous and mediated by the microtubule-associated protein Map1b.

Overall, the manuscript highlights the importance of FMRP in neuronal tangential migration. They performed an analysis of different aspects of migration such as nucleokinesis and cytokinesis in migrating neuroblasts from live-imaging videos.<br /> However, the work is quite incomplete. The role of FMRP and Map1b in neuronal migration is not well introduced and discussed. In the cortex, FMRP is mainly implicated in the multipolar to bipolar transition of immature neurons, but not in the migration itself (la Fata et al., 2014). In fact, Fmr1 KO mice do not show impairment in cortical lamination. On the other hand, very less is mentioned about the role of Map1b in neuronal migration. It is not shown whether overexpression of Map1b alters neuroblast migration and recapitulates the Fmr1 KO phenotype.

Moreover, it is unclear to me which are the anatomical consequences of aberrant migration of neuroblasts in the Fmr1 KO mice. Authors mention that neuroblasts properly arrive at the OB and they refer to a previous publication (Scotto-Lomassese et al., 2011). However, this study does not show the distribution of neuroblasts in the SVZ, along the RMS or in the olfactory bulb (OB) in mutant mice. On the contrary, they said that there is no delay in the migration or maturation of granular cells arriving at the OB (Scotto-Lomassese et al., 2011). In summary, the authors do not show the functional consequences of aberrant neuroblast migration in the Fmr1 KO mice, making weaker the assumption that the study is important for the understanding of FXS pathophysiology.

Reviewer #3 (Public Review):

This important manuscript investigates the role of basal forebrain cholinergic interneurons in conditioned responding by measuring the licking behaviour of head-fixed mice during photostimulation of the aforementioned neurons. Licking is found to increase only during windows when licking is rewarded, and similar behaviour is observed when terminals are stimulated in basolateral amygdala, then several more experiments are conducted to determine the behavioural and anatomical specificity of the effect. The findings are solid, particularly those relating to the recordings, although the interpretation of the behavioural findings is still somewhat unclear.

Strengths<br /> • The manuscript is beautifully written and structured. I found it really easy to follow and felt that the authors did an exceptional job of walking me through each experiment that they completed, the rationale for it, and what they found.<br /> • The question of the function of basal forebrain cholinergics is an interesting one and a somewhat understudied question, so the study is timely and on an interesting topic.<br /> • The experiments are well-designed and the findings are novel. There are a number of important control experiments performed to determine that the observed effects were not due to locomotor activity and that stimulating basal forebrain ACh neurons is not inherently reinforcing.<br /> • The discussion is really nice - covering important topics such as potential interactions with dopamine, the potential anatomical specificity of the effects observed, and the possibility that projections other than those studied here might mediate effects, among other things.

Weaknesses<br /> • Although very clearly written and set out, I found myself confused by the behavioural findings and their interpretation. Mainly this was because photostimulation only increased licking during the window of opportunity, which is not signalled by any discrete stimulus, which means that the only signal that the animal receives to determine that they are within the reward window is them receiving the reward. Therefore, the only time within this window that licking could be increased is post-reward (otherwise the reward window is identical to a non-rewarded window) and it is not clear to me what this increase in post-award licking might mean? In fact, this time post-award is actually the time the animal is most certain to not receive another reward for a few seconds, meaning that licking at this time is not a useful behaviour and therefore it is difficult to interpret what it means to artificially increase licking at this time. I think it would probably have been less confusing for the authors to study a paradigm in which animals develop a conditioned response that is unsignaled by discrete stimuli and then to inhibit basal forebrain ACh prior to that response.<br /> • I should also note that the authors state (Lines 249-251) that stimulation increases responding prior to reinforcer delivery, but I couldn't find evidence for this, and it seems counterintuitive to me that it would do so because then how would the animals discriminate the window of opportunity from a non-rewarded window? Perhaps I misunderstood something, but I found this confusing.<br /> • I do not think the behaviour in this task can be classed as operant - it is still a good task and still fine for detecting conditioned responding, but it cannot determine whether the responding is governed by a response-outcome association in the absence of a stimulus-outcome association (with stimuli being the licking spout, other facets of the behavioural context etc) through bidirectionality or omission, as would be required to demonstrate its operant nature.<br /> • I was confused by the pupil dilation data in Figure S4 as the authors seem to want to argue that this effect, although specific to the rewarded window as licking is, is independent of the licking behaviour as it develops more slowly than the behaviour (Lines 201-202). I was curious as to how the authors interpret these data then? Does it indicate that stimulating basal forebrain ACh interneurons does both things (i.e. increases arousal AND conditioned responding in the absence of discrete stimuli) but that the two things are independent of each other?<br /> • The authors refer to the dorsal medial prefrontal cortex in mice, which from the methods appears to be the prelimbic region. My understanding is that dmPFC has fallen out of favour for use in mice as it is not homologous to the same region in primates and can be confusing for this reason.

Reviewer #3 (Public Review):

Summary:<br /> The present article attempts to answer both the ultimate question of why different stinging behaviours have evolved in Cnidiarians with different ecological niches and shed light on the proximate question of which electro-physiological mechanisms underlie these distinct behaviours.

Account of major methods and results:<br /> In the first part of the paper, the authors try to answer the ultimate question of why distinct dependencies of the sting response on internal starvation levels have evolved. The premise of the article that Exaiptasia's nematocyte discharge is independent of the presence of prey (Artemia nauplii) as compared to Nematostella's significant dependence of the discharge on the presence of actual prey, is shown be a robust phenomenon justified by the data in Figure 1.

The hypothesis that defensive vs. predatory stinging leads to different nematocyte discharge behaviours is analysed in mathematical models based on the suitable framework of optimal control/decision theory. By assuming functional relations between the:<br /> 1) cost of a full nematocyte discharge and the starvation level.<br /> 2) probability of successful predation/avoidance on the discharge level.<br /> 3) desirability/reward of the reached nutritional state.

Based on these assumptions of environmental and internal influences, the optimal choice of attack intensity is calculated using Bellman's equation for this problem. The model predictions are validated using counted nematocytes on a coverslip. The scaling of normalised nematocyte discharge numbers with scaled starvation time is qualitatively comparable to what is predicted from the models. The abundance of nematocytes in the tentacles was, on the other hand, independent of the starvation state of the animals.

Next, the authors turn to investigate the proximate cause of the differential stinging behaviour. The authors have previously reported convincing evidence that a strongly inactivating Cav2.1 channel ortholog (nCav) is used by Nematostella to prevent stinging in the absence of prey (Weir et al. 2020). This inactivation is released by hyperpolarising sensory inputs signalling the presence of prey. In this article, it is clearly shown by blocking respective currents that Exaiptasia, too, relies on extracellular Ca2+ influx to initiate stinging. Patch clamp data of the involved currents is provided in support. However, the authors find that in addition to the nCav with a low-inactivation threshold, Exaiptasia has a splice variant with a higher inactivation threshold expressed (Figure 3D).

The authors hypothesise that it is this high-threshold nCav channel population that amplifies any voltage depolarisation to release a sting irrespective of the presence of prey signals. They found that the β subunit that is responsible for Nematostella's unusually low inactivation threshold exists in Exaiptasia as two alternative splice isoforms. These N-terminus variants also showed the greatest variation in a phylogenetic comparison (Figure 5), rendering it a candidate target for mutations causing variation in stinging responses.

Appraisal of methodology in support of the conclusions:<br /> The authors base their inference on a normative model that yields quantitative predictions which is an exciting and challenging approach. The authors take care in stating the model assumptions as well as showing that the data indeed does not contradict their model predictions. The interesting comparative nature of the modelling part of the study is complicated by slightly different cost assumptions for the two scenarios. Hence, Figure 2 needs to be carefully digested by readers.

It would be even more prudent to analyse the same set of cost-of-discharge vs. starvation scenarios for both species. Specifically, for Nematostella the complete cost-of-discharge vs starvation-state curves as for Exaiptasia (Figure 2E, example 2-4) could be used. It is likely that the differential effect size of Nematostella and Exaiptasia behaviour is the strongest if only the flat cost-of-discharge vs starvation is used (Figure 2A) for Nematostella. But as a worst-case comparison the other curves, where the cost to the animal scales with starvation would be a good comparison. This could help the reader to understand when the different prediction of Nematostella's behaviour breaks down. In addition, this minor change could shed light on broader topics like common trade-offs in pursuit predation.

The qualitatively similar scaling of the model-derived relation between starvation and sting intensity with the counted nematocytes for different feeding pauses is evidence that feeding has indeed been optimised for the two distinct ecological niches.<br /> To prove that Exaiptasia uses a similar Ca2+ channel ortholog as well as a different splice variant, the authors employed both clean electrophysiological characterisaiton (Figure 3) as well as transcriptomics data (Figure 4S1).

To strengthen the authors' hypothesis that variation in the N-termini leads to changes in Ca2+ channel inactivation and hence altered stinging, the response sequence variability of 6 Cnidaria was analysed.

Additional context:<br /> Although, the present article focuses on nematocytes alone, currently, there has been a refocus in neurobiology on the nervous systems of more basal metazoans, which received much attention already in the works of Romanes (1885). In part, this is driven by the goal to understand the early evolution of nervous systems. Cnidarians and Ctenophors are exciting model organisms in this venture. This will hopefully be accompanied by more comparative studies like the present one. Some of the recent literature also uses computational models to understand mechanisms of motor behaviour using full-body simulations (Pallasdies et al. 2019; Wang et al. 2023), which can be thought of as complementary to the normative modelling provided by the authors.

Comparative studies of recent Cnidarians, such as the present article, can shed light on speculative ideas on the origin of nervous systems (Jékely, Keijzer, and Godfrey-Smith 2015). During a time (the Ediacarium/Cambrium transition) that has seen the genesis of complex trophic foodwebs with preditor-prey interaction, symbioses, but also an increase of body sizes and shapes, multiple ultimate causes can be envisioned that drove the increase in behavioural complexity. The authors show that not all of it needs to be implemented in dedicated nerve cells.

References:

Jékely, Gáspár, Fred Keijzer, and Peter Godfrey-Smith. 2015. "An Option Space for Early Neural Evolution." Philosophical Transactions of the Royal Society B: Biological Sciences 370 (December): 20150181. https://doi.org/10.1098/rstb.2015.0181.

Pallasdies, Fabian, Sven Goedeke, Wilhelm Braun, and Raoul-Martin Memmesheimer. 2019. "From Single Neurons to Behavior in the Jellyfish Aurelia Aurita." eLife 8 (December). https://doi.org/10.7554/elife.50084.

Romanes, G. J. 1885. Jelly-Fish, Star-Fish and Sea-Urchins: Being a Research on Primitive Nervous Systems. Appleton.

Wang, Hengji, Joshua Swore, Shashank Sharma, John R. Szymanski, Rafael Yuste, Thomas L. Daniel, Michael Regnier, Martha M. Bosma, and Adrienne L. Fairhall. 2023. "A Complete Biomechanical Model of hydra Contractile Behaviors, from Neural Drive to Muscle to Movement." Proceedings of the National Academy of Sciences 120 (March). https://doi.org/10.1073/pnas.2210439120.

Weir, Keiko, Christophe Dupre, Lena van Giesen, Amy S-Y Lee, and Nicholas W Bellono. 2020. "A Molecular Filter for the Cnidarian Stinging Response." eLife 9 (May). https://doi.org/10.7554/elife.57578.

Reviewer #3 (Public Review):

In this study, Hwangbo and co-workers investigate the extent to which the well-established life extending effects of DR rely on the molecular circadian clock and how the landscape of clock-controlled gene expression changes in the face of DR within the fat body of the fly, a tissue that performs the functions associate with both the liver and adipose tissue of mammals. The authors evidence that DR extends lifespan in a manner that depends on only one of the two major limbs of the fly's molecular circadian clock, namely the positive limb, that DR produces major changes in the identities of cycling clock output genes, and that genes related to the proteosome represent a major component of DR-induced transcript cycling. Though interesting, these conclusions are not strongly supported by the data and there are two major reasons for this. First, the authors rely on only one loss of function genotype each for the loss of positive and negative limb clock gene function. Second, though they wish to address the "circadian transcriptome" under normal and DR conditions, the authors conduct all their work under strong Light/Dark cycles, making it impossible to address circadian phenomena. These shortcomings are problematic in the extreme, as they leave open obvious alternative explanations for the results and fail to directly determine if the rhythmic expression, they observe are clock controlled or merely driven by the light/dark cycles, which themselves produce major effects on activity, feeding, etc., that may be responsible for differentially driving rhythmic transcripts under normal and DR conditions in the fat bodies.

Major Weakness One: The use of only genotype each for the loss of positive (Clk^JRK) and negative (Per^01) limb of the circadian represents a major challenge for a central conclusion of the study. Phenotypes caused by the loss of a single clock gene may be due to the loss of circadian timekeeping, or they may represent a pleiotropic effect of the loss of function mutant being used. There are multiple precedents for pleiotropic (non-circadian) effects of clock gene mutants. It is, therefore, possible that the differences in the extent of DR mediated life extension between Clk^JRK and Per^01 may not represent a difference between breaking the positive and negative limbs of the clock but may simply reflect a pleiotropic effect of the dominant negative Clk^JRK. This possibility is acknowledged by the authors (lines 343-344). This could be addressed quite easily by extending the analysis to other loss of function mutants, for example, tim01 for the negative limb and cyc01 for the positive. Given the central focus here on the "circadian transcriptome," leaving open this alternative explanation for Clk's role in DR induced life extension represents a major weakness of the study. Furthermore, given the fact that Clk^JRK appears to be short lived on most of the media tested in the study, is it really surprising or informative that they would display lower life extension under DR?

Major Weakness Two: The authors have not established that any of cycling transcripts they have detected in the fat body under normal and DR conditions are driven by the circadian clock. This is because: 1.) they have conducted their transcriptomic analysis on cells taken from flies entrained to light dark cycles, which can themselves drive daily changes in expression levels and 2.) they have not shown that the cycling measured on normal diet or DR conditions depends on a functional circadian clock. The "significant reorganization of the circadian transcriptome" is presented as a major conclusion of this study, but the authors have not addressed circadian control of transcription at all here, either by an examination of transcription under free-running conditions and/or in loss of function clock mutants.

In addition, there is a logical gap in this study. The authors have shown that DR produces less life extension in Clk^JRK mutants than Per^01 or wild-type controls. They then show that DR produces changes in the rhythmic transcriptome when flies are place on DR. The central model presented in Fig. 6 shows/concludes that CLK drives increases in proteome-related transcript rhythms under DR. This conclusion could have been directly tested by asking if the changes in rhythmic gene expression induced by DR are gone the loss of function Clk mutants, or if the transcriptomic landscapes fail to differ between feeding conditions in these mutants.

In conclusion, the study falls far short of directly testing the ideas it puts forth, greatly limiting its impact and interest.

Reviewer #3 (Public Review):

In this study, Ciampa and colleagues demonstrate that HIF-1α activity is increased with gestation in humans and mice placentas and use several in vitro models to indicate that HIF activation in trophoblasts may release factors (yet to be identified) which promote myometrial contraction. Previous studies have linked placental factors to the preparation of the myometrium for labour (e.g. prostaglandins), but HIF-1α has not been implicated.

Weaknesses and concerns:

1) The author's rebuttal state that placentas undergo subclinical cellular aging as they reach term. Although several future studies are described to test functional deficits at the cellular level, the current manuscript does not provide convincing evidence of cellular aging. The only evidence of cellular senescence provided in both human and mouse data is the mRNA expression of a single gene associated with senescence.

2) The authors have not responded to the concern regarding CoCl2 mediating differentiation. The paragraph from a ref states that JAR cells do not respond as well as BeWOs to forskolin. However, this does not mean that JAR cells do not differentiate. This point is particularly pertinent as a quick search of their RNA-seq data shows upregulation of STB genes following CoCl2 treatment including ERVs (ERVFRD1, ERVV-1, ERVV-2, ERV3-1), CYP19A1 and OVOL1 just to name a few. If the authors' conclusion is that CoCl2 treatment did not alter trophoblast differentiation, the authors should provide additional data showing this. For example, cell fusion assays showing E-cadherin/desmoplakin staining and nuclear localization within stained boundaries.

3) The authors acknowledge the possibility of extraplacental effects of DMOG in the initiation of labour in their model, no additional evidence has been provided to support placental effects of their model. The authors also argue that although PMID 30808919 (which specifically overexpressed HIF-1a in the placenta) did not show changes in birth length, they propose that this may be due to constitutive HIF1a expression at the beginning of pregnancy. This argument is invalid since placental maldevelopment is consistently linked with several pregnancy complications including spontaneous preterm birth. If anything, perturbations in the beginning of pregnancy are more likely to lead to worse outcomes than those at the end of pregnancy.

4) Regarding induction of syncytialisation, please provide additional evidence that the cells have/have not syncytialised.

5) Lack of cohesion between experimental models. Please provide evidence that DMOG mediates similar effects on SA-β gal activity as CoCl2 in JARs.

6) Evidence of senescence and mitochondrial abundance could be strengthened by providing additional markers. E.g. only GLB1 mRNA expression is provided as evidence of senescence, and COX IV protein for mitochondrial abundance in mouse and human placentas. This point has not been addressed. Please provide at least one additional marker of senescence and mitochondrial abundance.

Reviewer #3 (Public Review):

The computational study reported in the manuscript "Free energy landscapes of KcsA inactivation" by Pérez-Conesa and Delemotte is quite interesting and insightful.

The computations provide the first complete analysis of how the opening of the activation gate and the constriction of the selectivity filter are coupled in the KcsA channel.

The analysis is careful and is state-of-the-art. The results reveal remarkable differences between the CHARMM and AMBER force fields.

Unfortunately, the "elephant in the room" with regards to K+ channel inactivation is the significance of the dilated structures more recently obtained by Xray and EM. While it is worthwhile doing our best to really understand the constriction mechanism of KcsA, and the present manuscript does an excellent job at that, the ground has shifted and understanding finer points about KcsA constriction has become, unfortunately, not the most prominent issue in the field at the present time.

Let's discuss the current situation about the inactivation of K+ channels. The situation is fairly unsettled. The KcsA channel was the first for which some atomic structure and mechanism, centered on a constriction of the selectivity filter, were proposed. The constricted conformation really does not conduct because the filter is too narrow. More recently a few structures (Xray and EM) for channel mutants known to have more propensity to inactivate have revealed a different conformation of the filter which appears to be dilated toward the extracellular side. This is a conformation that had never been seen previously. Different "camps" co-exist in the K+ channel community about inactivation. Those who were very skeptical about the constricted conformation claim that the new dilated structures is the final truth. While the dilated structures are certainly part of the body of information that we have now, but their significance remains somewhat unclear if anything because of the fact that they are not perfectly occluded and they allow ion conduction! While it is worthwhile doing our best to really understand the constriction mechanism of KcsA, and the present manuscript does an excellent job at that, the ground has shifted and understanding finer points about KcsA constriction has become, unfortunately, not the most prominent issue in the field at the present time.

Reviewer #3 (Public Review):

How chromatin state is defined is an important question in the epigenetics field. Here, Jamge et al. proposed that the dynamics of histone variant exchange control the organization of histone modifications into chromatin states. They found 1) there is a tight association between H2A variants and histone modifications; 2) H2A variants are major factors that differentiate euchromatin, facultative heterochromatin, and constitutive heterochromatin; 3) the mutation in DDM1, a remodeler of H2A variants, causes the mis-assembly of chromatin states in TE region. The topic of this paper is of general interest and the results are novel.

Overall, the paper is well-written and the results are clearly presented. The biochemical analysis part is solid.

Reviewer #3 (Public Review):

In this work, Urbanska et al. link the mechanical phenotypes of human glioblastoma cell lines and murine iPSCs to their transcriptome, and using machine learning-based network analysis identify genes with putative roles in cell mechanics regulation. The authors identify 5 target genes whose transcription creates a combinatorial marker which can predict cell stiffness in human carcinoma and breast epithelium cell lines as well as in developing mouse neurons. For one of the target genes, caveolin1 (CAV1), the authors perform knockout, knockdown, overexpression and rescue experiments in human carcinoma and breast epithelium cell lines. They determine the cell stiffness via RT-DC, AFM indentation and AFM rheology and confirm that high CAV1 expression levels correlate with increased stiffness in those model systems. This work brings forward an interesting approach to identify novel genes in an unbiased manner, but surprisingly the authors validate caveolin 1, a target gene with known roles in cell mechanics regulation.

I have two main concerns with the current version of this work:<br /> 1) The authors identify a network of 5 genes that can predict mechanics. What is the relationship between the 5 genes? If the authors aim to highlight the power of their approach by knockdown, knockout or over-expression of a single gene why choose CAV1 (which has an individual p-value of 0.16 in Fig S4)? To justify their choice, the authors claim that there is limited data supporting the direct impact of CAV1 on mechanical properties of cells but several studies have previously shown its role in for example zebrafish heart stiffness, where a knockout leads to higher stiffness (Grivas et al., Scientific Reports 2020), in cancer cells, where a knockdown leads to cell softening (Lin et al., Oncotarget 2015), or in endothelial cell, where a knockout leads to cell softening (Le Master et al., Scientific Reports 2022).<br /> 2) The authors do not show how much does PC-Corr outperforms classical co-expression network analysis or an alternative gold standard. It is worth noting that PC-Corr was previously published by the same authors to infer phenotype-associated functional network modules from omics datasets (Ciucci et al., Scientific Reports 2017).

Altogether, the authors provide an interesting approach to identify novel genes associated with cell mechanics changes, but the current version does not fulfill such potential by focusing on a single gene with known roles in cell mechanics.

Reviewer #3 (Public Review):

The goal of this study was to use a combination of fluorescent dyes and genetically encoded reporters to estimate the temperature of mitochondria. The authors provide additional evidence that they claim to support "hot" mitochondria.

Strengths:<br /> 1. The authors use several methods, including a mitochondrial fluorescent reporter dye, as well as a genetically encoded gTEMP temperature probe, to estimate mitochondrial temperature.<br /> 2. The authors couple these measurements with other perturbation of mitochondria, such as OXPHOS inhibitors, to show consistency

Weaknesses:<br /> 1. The methodology for inferring mitochondrial temperature is not well-established to begin with and requires additional controls for interpretation.<br /> a. Very little benchmarking is done of the "basal" fluorescence ratio, and whether that fluorescence ratio actually reflects true organelle temperature. For instance, the authors should in parallel compare between different organelles to see if only mitochondria appear "hot" or whether this is some calibration error. Another control is to use different incubator temperatures and see how mitochondrial (vs other organelle) temperature varies as a function of external temperature.<br /> b. The authors do not rigorously control for other factors that may also be changing fluorescence and may be confounders to the delta fluorescence (eg, delta calcium in response to mito inhibitors, membrane potential, redox status, ROS, etc.). There should be additional calibration for all potential confounders.<br /> c. It was unclear where the mito-targeted dyes/probes localized in terms of mitochondrial compartment. Regardless, one important control would be to target these dyes to each of the different compartments eg. Matrix vs IMS vs outer membrane to determine if a gradient of temperatures can be observed.<br /> d. Can these probes be used in isolated mitochondria and other isolated organelles. Such data would also help to clarify whether the high temperature is a specific to mitochondria.<br /> 2. The authors should try to calibrate their fluorescence inference of temperature with an alternative method and benchmark to others in the field. For instance, Okabe et al Nat Comm 2012 used a polymeric thermometer to measure temperature and reported 33degC cytoplasm and 35degC nucleus. Can the authors also show a ~2degC difference in their hands between those two compartments, and under those conditions are mitochondria still 10degC hotter?<br /> 3. There are some theoretical considerations and critiques about temperature imaging in cells (eg Baffou et al Nat Methods 2014; Lane et al Plos Biology 2018), and the possible magnitude of theoretical variation between compartments. The authors should address some of those theoretical concerns, either experimentally or in the discussion.

Based on the aforementioned weaknesses, in my opinion, the authors did not achieve their Aims to accurately determine the temperature of mitochondria. The results, while interesting, are preliminary and require additional controls before conclusions can be drawn. Previous studies have indicated intra-organelle temperature variations within cells; typically, previous reports have estimated that the variation is within a few degrees (Okabe et al Nat Comm 2012). Only one report has previously suggested that mitochondria are at 50degC (Cretien, Plos biology 2018). The study does not substantially clarify the true temperature of mitochondria or resolve potential discrepancies in previous estimates of mitochondrial temperature.

Reviewer #3 (Public Review):

To assess the degree to which highly social primates like marmosets share a human-like Theory of Mind (ToM), the authors used eye tracking and functional magnetic resonance brain imaging on marmosets and humans who were viewing two of the three categories from classic Frith-Happé animations. Humans viewing the ToM animations showed, relative to the random movement animations, longer fixation times, more viewing of the large shape, and more viewing of the small shape. In contrast, the marmosets did not differ in their viewing of the ToM videos as a category and did not show differential viewing of the small shape. The marmosets did show differential viewing of the large shape, but this difference was blunted relative to that seen in humans. Neurally, both species showed widespread brain activation in many areas that discriminated between ToM videos and random movement videos. This pattern of activation partially overlapped and partially was different in humans and marmosets. It was also partially overlapping and partially different when comparing humans in this study to humans in another study. Overall, the authors conclude that their evidence cannot address whether marmosets have a Theory of Mind, but that marmosets show a "clear preference for interacting shapes" that may be an ancestral form of human Theory of Mind.

There are several laudable strengths to this report. It reports a direct human/monkey comparison. It uses a robust population of subjects, especially for the monkey experiment. It uses strong imaging methods that use modern parcellation maps, compares human data from this study to comparable data from another study, and accounts for lateralization differences convincingly using maps of signal-to-noise ratio. It uses eye-tracking methods and stimuli that are solidly grounded in the human literature and that has recently been used in a different monkey species.

Unfortunately, the weaknesses of this report limit its interpretability. First, it omits one of the three major categories of the Frith-Happé animations: Goal-Directed actions. Data from this category are critical because they provide a case where the shapes are engaging in biological motion but are not behaving as if they attribute minds to each other. Without including it, readers cannot interpret whether any given finding is due to biological motion or mentalizing. Second, the study did not gather explicit reports of mental state attribution from humans. This does not allow for a manipulation check about whether humans were even engaging in mentalizing and does not allow the researchers to separate out what brain activation patterns are due to mentalizing and which are due to eye movements or stimulus movement. Third, in interpreting the data, the researchers gloss over the major species differences and primarily focus on one small species similarity. Both this study and a previous human study (Klein et al., 2009, Quart. J. Exp. Psychol.) have shown longer fixations for the ToM videos relative to the random motion videos and that these fixations correlate with explicit ratings of the intentionality of the shapes (Klein et al., 2009). That the marmosets don't show this difference should be a major piece of evidence against the hypothesis that they are engaging in anything like mentalizing. The marmosets also failed to show a viewing difference for the small shape. In short, the small viewing difference in the large shape, itself blunted relative to that seen in humans, is not sufficient evidence to justify the conclusion that marmosets engage in anything like ToM or even that they show a "clear preference for interacting shapes". Fourth, alternative explanations for the small differences that do exist were not sufficiently explored. The videos that make up the categories in the Frith-Happé animations differ in many ways, such as in the amount of visual motion, smoothness/jerkiness of motion, amount of the screen taken up by shapes vs white space, etc. Indeed, in the prior study to use these stimuli with monkeys, the authors also found that the categories differed in viewing parameters but that this difference disappeared once low-level visual motion was accounted for (Schafroth et al., 2021, Sci. Rep.). Without a similar analysis here or a second experiment that assesses generalization to stimuli that don't differ on low-level perceptual features, readers cannot know whether the small viewing difference that exists is due to something like mentalizing or something about low-level visual motion. Indeed, other studies have found overlapping brain activity patterns in monkeys that are driven primarily by low-level visual motion (e.g., Russ et al., 2015, Neuroimage). Fifth, the prior monkey study to use these stimuli raised the point that these stimuli may not even be appropriate to test ToM in nonhumans. Human-like displays of "mocking", "coaxing", or "seducing" are likely meaningless to monkeys. This weakness has not been addressed in the current study.

Considering the weaknesses in the behavioral methods, the well-collected neural activity patterns cannot be interpreted in a meaningful way. As such, the authors' conclusions are not justified at the current time. Nevertheless, this report may be useful to others who attempt similar experiments of their own.

Reviewer #3 (Public Review):

Aso et al. provide insight into how learned valences are transformed into concrete memory-driven actions, using a diverse set of proven techniques.

Here the authors use a four-armed arena to evaluate flies' preference for a reward-predicting odor and measure upwind locomotion. This behavioral paradigm was combined with the photoactivation of different memory-eliciting neurons, revealing that appetitive memories stored in different compartments of the mushroom bodies (center of olfactory memory) induce different levels of upwind locomotion. The authors then proceed to a non-exhaustive optogenetic screen of the neurons located downstream of the output neurons of the mushroom bodies (MBONs) and identify a group of 8-11 Cholinergic neurons promoting significant changes in upwind locomotion, the UpWins. By combining confocal immunolabelling of these neurons with electron microscope images, they manage to establish the UpWins' connectome within themselves and with the MBONs. Then, using two in vivo cell recording techniques, electrophysiology, and calcium imaging, they define that UpWins integrate both inhibitory and excitatory synaptic inputs from the MBONs encoding appetitive and aversive memory, respectively. In addition, they show that the UpWins' response to a reward-predicting odor is increased after appetitive training. On a behavioral level, the authors establish that the UpWins respond to wind direction only and are not involved in lower-level motor parameters, such as turning direction and acceleration. Finally, they demonstrate that the UpWins' activity is necessary for long-term appetitive memory retrieval, and even suggest a broader role for the UpWins in olfactory navigation, as their photoactivation increases the probability of revisiting behavior. In the end, the authors state that they provide new insights into how memory is translated into concrete behavior, which is fully supported by their data. Altogether, the authors present a pretty complete study that provides very interesting and reliable data, and that opens a new field of investigation into memory-driven behaviors.

Strengths of the study:

- To support their conclusions, the authors provide detailed data from different levels of analysis (behavioral, cellular, and molecular), using multiple sophisticated techniques.

- The measurement of multiple parameters in the behavioral analysis supports the strong changes in upwind locomotion. In addition, taken individually these parameters provide precise insights into how upwind locomotion changes, and allow the authors to more precisely define the role of the UpWins.

- The authors use split-Gal4 drivers instead of Gal4, allowing them to better refine neuron labelling.

The authors discussed and investigated all possible biases, making their data very reliable. For example, they demonstrated that the phenotypes observed in the behavioral assay were wind-directed behaviors and could not be explained by bias avoidance of the arena's center area.

Limitations of the study:

- In the absence of more precise drivers, the UpWins' labelling lacks precision. For example, there is no way to know exactly which UpWin is responding in the electrophysiological experiment presented in Figure 4.

- The screening of neurons located downstream of the MBONs is not exhaustive, meaning that other groups of neurons might be involved in memory-driven upwind locomotion. Although, it does not diminish the authors' conclusions.

- All data were obtained with walking flies. So far, there have been no experiments on flying flies.

Reviewer #3 (Public Review):

The authors are presenting a new simulation for artificial vision that incorporates many recent advances in our understanding of the neural response to electrical stimulation, specifically within the field of visual prosthetics. The authors succeed in integrating multiple results from other researchers on aspects of V1 response to electrical stimulation to create a system that more accurately models V1 activation in a visual prosthesis than other simulators. The authors then attempt to demonstrate the value of such a system by adding a decoding stage and using machine-learning techniques to optimize the system to various configurations. While there is merit to being able to apply various constraints (such as maximum current levels) and have the system attempt to find a solution that maximizes recoverable information, the interpretability of such encodings to a hypothetical recipient of such a system is not addressed. The authors demonstrate that they are able to recapitulate various standard encodings through this automated mechanism, but the advantages to using it as opposed to mechanisms that directly detect and encode, e.g., edges, are insufficiently justified. The authors make a few mistakes in their interpretation of biological mechanisms, and the introduction lacks appropriate depth of review of existing literature, giving the reader the mistaken impression that this is simulator is the only attempt ever made at biologically plausible simulation, rather than merely the most recent refinement that builds on decades of work across the field. The authors have importantly not included gaze position compensation which adds more complexity than the authors suggest it would, and also means the simulator lacks a basic, fundamental feature that strongly limits it utility. Finally, the computational capacity required to run the described system is substantial and is not one that would plausibly be used as part of an actual device, suggesting that there may be difficulties with converting results from this simulator to an implantable system. With all of that said, the results do represent an advance, and one that could have wider impact if the authors were to reduce the computational requirements, and add gaze correction.

Reviewer #3 (Public Review):

In this study, titled "Epigenetic signature of human immune aging: the GESTALT study," the authors reanalysed data from five highly purified human immune cell types from 55 healthy volunteers across a wide age range to characterize age-related changes in DNA methylation status. Additionally, they performed some integrative analyses with chromatin state and transcriptional data. Findings support that age-related DNA methylation changes are predominantly cell type-specific. Out of thousands of age-associated sites, only 350 sites were differentially methylated in the same direction in all cell types and validated in an independent longitudinal cohort. Some conserved changes exist, which appear to be underpinned by alterations in the hypoxia response, with linked enrichment of transcription factor binding motifs related to ARNT and REST. The authors conclude that DNA methylation changes in healthy aging may represent adaptive responses to fluctuations in oxygen availability.

Strengths:

- The study utilised data from a large cohort of individuals (n=55), with participants ranging in age from their 20s to 80s, providing a comprehensive age-related analysis.

- The data set reanalysed was based on highly purified cells rather than unfractionated PBMCs. This revealed the largely cell-type-specific nature of these changes and demonstrated that conflicting directional changes can cancel each other out, going undetected at the PBMC level.

- The authors were able to verify the DNA methylation changes that were conserved across cell types longitudinally in PBMCs by reanalyzing published datasets from the InCHIANTI study, adding robustness to their findings.

Weaknesses:

- The authors make statements in the abstract and manuscript that overreach the study's findings. Specifically, they claim that "DNA methylation changes in healthy aging may represent adaptive responses to fluctuations in oxygen availability." In reality, the study shows that a small minority of conserved DNA methylation changes across hematopoietic cell types appear to be driven by hypoxia response processes. The study does not demonstrate that hypoxia response processes account for a large proportion of DNA methylation changes or that these processes apply to non-hematopoietic cell types. These statements should be put into context relative to the study findings.

- The authors should make it clear in the introduction and methods section that this current study is merely reanalysing a data set they published before. Also, the authors should describe in the introduction the key findings of the initial analysis as presented in their 2021 Immunity publication.

- In some instances, the manuscript lacks citations to support claims.

Reviewer #3 (Public Review):

In this manuscript, the authors are aiming to demonstrate that a fatty-acyl synthase gene (fas5) is involved in the composition of the blend of surface hydrocarbons of a parasitoid wasp and that it affects the sexual attractiveness of females for males. Overall, the manuscript reads very well, it is very streamlined, and the authors' claims are mostly supported by their experiments and observations. However, I find that some experiments, information and/or discussion are absent to assess how the effects they observe are, at least in part, not due to other factors than fas5 and the methyl-branched (MB) alkanes. I'm also wondering if what the authors observe is only a change in the sexual attractiveness of females and not related to species recognition as well.

The authors explore the function of cuticular hydrocarbons (CHCs) and a fatty-acyl synthase in Nasonia vitripennis, a parasitic wasp. Using RNAi, they successfully knockdown the expression of the fas5 gene in wasps. The authors do not justify their choice of fatty-acyl synthase candidate gene. It would have been interesting to know if that is one of many genes they studied or if there was some evidence that drove them to focus their interest in fas5. The authors observe large changes in the cuticular hydrocarbons (CHC) profile of male and females. These changes are mostly a reduction of some MB alkanes and an increase in others as well as an increase of n-alkene in fas5 knockdown females. For males fas5 knockdowns, the overall quantity of CHC is increased and consequently, multiple types of compounds are increased compared to wild-type, with only one compound appearing to decrease compared to wild-type. Insects are known to rely on ratios of compounds in blends to recognize odors. Authors address this by showing a plot of the relative ratios, but it seems to me that they do show statistical tests of those changes in the proportions of the different types of compounds. In the results section, the authors give percentages while referring to figures showing the absolute amount of CHCs. They should also test if the ratios are significantly different or not between experimental conditions. Similar data should be displayed for the males as well. Furthermore, the authors didn't use an internal standard to measure the quantity of CHCs in the extracts, which, to me, is the gold standard in the field. If I understood correctly, the authors check the abundance measured for known quantities of n-alkanes. I'm sure this method is fine, but I would have liked to be reassured that the quantities measured through this method are good by either testing some samples with an internal standard, or referring to work that demonstrates that this method is always accurate to assess the quantities of CHC in extracts of known volumes.

The authors provide a sensible control for their RNAi experiments: targeting an unrelated gene, absent in N. vitripennis (the GFP). This allows us to see if the injection of RNAi might affect CHC profiles, which it appears to do in some cases in males, but not in females. The authors also show to the reader that their RNAi experiments do reduce the expression of the target gene. However, one of the caveats of their experiments, is that the authors don't provide evidence or information to allow the (non-expert) reader to assess whether the fas5 RNAi experiments did affect the expression of other fatty-acyl synthase genes. I'm not an expert in RNAi, so maybe this suggestion is not relevant, but it should, at least, be addressed somewhere in the manuscript that such off-target effects are very unlikely or impossible, in that case, or more generally.

The authors observe that the modified CHCs profiles of RNAi females reduce courtship and copulation attempts, but not antennation, by males toward live and (dead) dummy females. They show that the MB alkanes of the CHC profile are sufficient to elicit sexual behaviors from males towards dummy females and that the same fraction from extracts of fas5 knockdown females does so significantly less. From the previous data, it seems that dummy females with fas5 female's MB alkanes profile elicit more antennation than CHC-cleared dummy females, but the authors do not display data for this type of target on the figure for MB alkane behavioral experiments. Unfortunately, the authors don't present experiments testing the effect of the non-MB alkanes fractions of the CHC extracts on male behavior toward females. As such, they are not able to (and didn't) conclude that the MB-alkane is necessary to trigger the sexual behaviors of males. I believe testing this would have significantly enhanced the significance of this work. I would also have found it interesting for the authors to comment on whether they observe aggressive behavior of males towards females (live or dead) and/or whether such behavior is expected or not in inter-individual interactions in parasitoids wasps.

CHCs are used by insects to signal and/or recognize various traits of targets of interest, including species or groups of origin, fertility, etc. The authors claim that their experiments show the sexual attractiveness of females can be encoded in the specific ratio of MB alkanes. While I understand how they come to this conclusion, I am somewhat concerned. The authors very quickly discuss their results in light of the literature about the role of CHCs (and notably MB alkanes) in various recognition behaviors in Hymenoptera, including conspecific recognition. Previous work (cited by the authors) has shown that males recognize males from females using an alkene (Z9C31). As such, it remains possible that the "sexual attractiveness" of N. vitripennis females for males relies on them not being males and being from the right species as well. The authors do not address the question of whether the CHCs (and the MB alkanes in particular) of females signal their sex or their species. While I acknowledge that responding to this question is beyond the scope of this work, I also strongly believe that it should be discussed in the manuscript. Otherwise, non-specialist readers would not be able to understand what I believe is one of the points that could temper the conclusions from this work.

Reviewer #3 (Public Review):

The manuscript by Rossini et al suggests an interesting novel mechanism for the regulation of tyrosine kinase Src by spermidine. The idea is interesting and some of the data suggest that spermidine may regulate Src activity. However, the manuscript suffers from multiple major shortcomings. The mechanism proposed by the authors is not supported by their studies. Authors tend to overinterpret data and overlook critical information that is missing. Some of the data is insufficient to support the statements that the authors make. Authors tend to use confusing nomenclature without clarifications making it difficult to interpret the data. The extent of Src activation by spermidine should be carefully evaluated by comparing it to the maximum activity of constitutively active Src. Furthermore, the biological significance of this regulation is not demonstrated. Only a few overexpression data are shown.

Reviewer #3 (Public Review):

Alternative splicing as a result of mutations in different components of the splicing machinery has been associated with a variety of cancer types, including hematological malignancies where this has been most extensively studied but also for solid tumors such as breast and pancreatic ductal adenocarcinoma (PDAC). Here the authors analyze genome sequencing data in human PDAC samples and identify a recurring mutation in the SF3B1 subunit that substitutes lysine for glutamate at residue 700 (SF3B1K700E) in PDACs. This mutation has been identified and its' molecular role in disease progression in other diseases has been studied, but the mechanism for promoting disease progression in pancreatic cancer has not been as well characterized.

To study how SF3B1K700E contributes to PDAC pathology, the authors generate a novel genetically modified mouse model of a pancreas specific SF3B1K700E mutation and explore its oncogenicity and tumor promoting potential. The authors find that SF3B1K700E is not oncogenic, but potentiates the oncogenic potential of Kras and p53 (KP) driver mutations commonly found in PDAC tumors. The authors then proceed to characterize the molecular mechanisms that might drive this phenotype. By transcriptomic analysis, the authors find KP-SF3B1K700E tumors have downregulation of epithelial-to-mesenchymal transition (EMT) genes compared to KP tumors. The cytokine TGFβ has previously been found to limit PDAC initiation and progression by causing lethal EMT in PDAC and PDAC precursor cells. Thus, the authors propose SF3B1K700E inhibition of EMT blocks the tumor suppressive activity of TGFβ and this underpins the tumor promoting role of SF3B1K700E mutation in PDAC. Consistent with this finding, SF3B1K700E mutation blocks TGFβ-induced toxicity in a variety of cell culture models of PDAC and PDAC precursor models.

Lastly, the authors seek to identify how altered splicing reduces EMT activity in PDAC cells. The authors identify misspliced genes consistent in both KP and human SF3B1K700E mutant cancer samples and find Map3k7 as one of 11 consistently misspliced genes. MAP3K7 has previously been identified as a positive regulator of EMT. Thus the authors speculated Map3k7 missplicing would lead to reduced MAP3K7 activity and a reduction EMT and that this underpins the TGFβ in SF3B1K700E mutant PDAC cells. Consistent with this, the authors find inhibition of MAP3K7 reduces TGFβ toxicity in SF3B1K700E WT cells and overexpression of MAP3K7 in SF3B1K700E mutant PDAC cells induces TGFβ toxicity. Altogether, this suggests activity of Map3k7 is responsible for altered EMT activity and TGFβ sensitivity in SF3B1K700E mutant PDAC.

Altogether, the authors generate a valuable model to study the role of a recurring splicing mutation in PDAC and provide compelling evidence that this mutation is accelerates disease. The authors then perform both: (1) an open-ended investigation of how this mutation alters PDAC cell biology where they identify altered EMT activity and (2) rigorous mechanistic studies showing suppressed EMT provides PDAC cells with resistance to TGFβ, which has previously been shown to be tumor suppressive in PDAC, suggesting a possible mechanism by which SF3B1K700E mutation is oncogenic in PDAC that future animal studies can confirm. This work generates valuable models and datasets to advance the understanding of how mutations in the splicing machinery can promote PDAC progression and suggests alternative splicing of MAP3K7 is one such possible mechanism that altered splicing promotes PDAC progression in vivo.

- One major concern about the manuscript is that the proposed mechanism by which SF3B1K700E mutation accelerates PDAC progression (MAP3K7 inhibition -> EMT inhibition -> reduced TGFb toxicity) is only tested in ex vivo culture models and there is very limited and correlative data to suggest that this is the operative mechanism by which SF3B1K700E mutant tumors are accelerated. This is especially important because of recent findings that IFNa signaling, which the authors also found to be high in SF3B1K700E mutant tumors, also promotes PDAC progression (https://www.biorxiv.org/content/10.1101/2022.06.29.497540v1). Thus, while thoroughly convinced by the rigorous ex vivo work that SF3B1K700E does lead to MAP3K7 inhibition -> EMT inhibition -> reduced TGFb toxicity, further experiments to confirm this mechanism is critical in vivo would be needed to convince me that this mechanism is critical to tumor progression in vivo. For example, would forced expression of MAP3K7 slow orthotopic KP-SF3B1K700E tumor growth while leaving IFNa signaling unperturbed?

Reviewer #3 (Public Review):

This manuscript aims to define the importance of long-range resection for homologous recombination, a relevant and yet unanswered question in the field of genome maintenance. The data shows that long-range resection is required for interchromosomal, but not intrachromosomal, recombination is well-developed and convincing. The claim that the DNA damage checkpoint is crucial for promoting distal recombination is interesting and founded on logical rationale. However, some key points about the proposed role of checkpoint signaling and the presented results need further clarification, mainly regarding the issue of checkpoint activation status in exo1Δ sgs1Δ cells and the attempts of using forced Rad53 activation to rescue interchromosomal recombination defects. Additional experiments would help solidify the proposed model. Nonetheless, the paper establishes the importance of long-range resection for distal recombination and should be considered a significant contribution to the field.

Reviewer #3 (Public Review):

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

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

Reviewer #3 (Public Review):

Mirror neurons are a big deal in the neuroscience literature and have been for thirty years. I (and many others) remain skeptical of whether they serve the functions often attributed to them - specifically, whether they are motor planning neurons that contribute to understanding the actions of others. Testing their functions, therefore, is of great interest and importance. The present study, however, is not a cogent or convincing test. I do not think this study helps to answer the questions surrounding mirror neurons. It purports to provide a crucial test, that comes out mostly against the mirror neuron hypothesis, but the test has too many weaknesses to be convincing.

First, consider that the motor tuning and the visual tuning match "poorly." How poor or good must the match be before the mirror neuron hypothesis is rejected? I do not know, and the study does not help here. Even a "poor" match could contribute significantly to a social perception function.

Second, the results remind me in some ways of other multi-modal responses in the brain. For example, in the visual area MST, neurons are tuned to optic flow fields that imply specific directions of self-motion. Many of the same neurons are tuned to vestibular signals that also imply specific directions of self-motion. But the optic flow tuning and the vestibular tuning are not perfectly matched. There is considerable slop and complexity in how the two tunings compare within individual neurons. That complexity is not evidenced against multi-modal tuning. Instead, it suggests a hidden-layer complexity that is simply not fully understood yet. Just so here, the fact that the apparent motor tuning and apparent visual tuning match "poorly" is not evidence against both a motor planning and a visual encoding function.

Third, the animals are massively over-trained in three actions. They perform these actions and see them performed thousands of times toward the same object. Surely, if I were in the place of the monkey, every time I saw the object, I'd mentally imagine all three actions. As I saw a person act on the object, I'd mentally imagine the alternative two actions at the same time. Even if the mirror neuron hypothesis is strictly correct, this experiment might still find a confusion of signals, in which neurons that normally might respond mainly to one action begin to respond in a less predictable way during all three trial types.

Fourth, the experiment relies on a colored LED that acts as an instructional cue, telling the monkey which action to perform. What is to stop the neurons from developing a cue-sensitive response, as in classic studies from Steve Wise and others in the premotor cortex? Perhaps the neuronal signal that the experimenters are trying to measure is partly obscured by other, complex responses influenced in some manner by the instructional cue?

Fifth, finally, and most importantly, the fundamental problem with this study is that it is correlational. Studies that purport to test the function of a set of neurons, and do so by use of correlational measurements, cannot provide strong answers. There are always half a dozen different interpretations and caveats, such as the ones I raised here. Both sides of a debate can always spin the results, and the arguments are never resolved. To test the mirror neuron hypothesis properly would require a causal study. For example, lesion area F5 and test if the monkey is less able to discriminate the actions of others. Or, electrically microstimulate in area F5 and test if the stimulation interferes (either constructively or destructively) with the task of discriminating the actions of others. Only in this way will it be possible to answer the question: do mirror neurons functionally participate in understanding the actions of others? The present study does not answer that question.

Reviewer #3 (Public Review):

Khalil et al. investigated the role of medial geniculate nuclei -> basolateral amygdala pathway in the processing of innate and learned threats. Using looming stimuli and cued fear conditioning the authors show that both the BLA and MGN projections to the BLA respond to learned and innately threatening stimuli and that their activation is necessary to generate adequate fear responses. Lastly, Khalil et al. highlight a possible role of adrenergic signaling in modulating threat-induced BLA (but not MGN) activity. The manuscript is well conceived, the statistical analysis is solid, and the methodology is appropriate. The strength of this paper is that the hypothesis is tested using multiple experimental strategies that all nicely converge to demonstrate the involvement of the MGN-BLA pathway in threat processing. However, a more detailed analysis of fiber photometry data in relation to the presented stimuli and to behavioral responses would help to clarify whether this MGN-BLA pathway is involved in processing sensory stimuli per se or directly generates behavioral responses.

Reviewer #3 (Public Review):

This study reports data collected across time and treatment modalities (internet CBT (iCBT), pharmacological intervention, and control), with a particularly large sample in the iCBT group. This study addresses the question of whether metacognitive confidence is related to mental health symptoms in a trait-like manner, or whether it shows state-dependency. The authors report an increase in metacognitive confidence as anxious-depression symptoms improve with iCBT (and the extent to which confidence increases is related to the magnitude of symptom improvement), a finding that is largely mirrored in those who receive antidepressants (without the correlation between symptom change and confidence change). I think these findings are exciting because they directly relate to one of the big assumptions when relating cognition to mental health - are we measuring something that changes with treatment (is malleable), so might be mechanistically relevant, or even useful as a biomarker?

This work is also useful in that it replicates a finding of heightened confidence in those with compulsivity, and lowered confidence in those with elevated anxious-depression.

One caveat to the interest of this work is that it doesn't allow any causal conclusions to be drawn, and only measures two timepoints, so it's hard to tell if changes in confidence might drive treatment effects (but this would be another study). The authors do mention this in the limitations section of the paper.

Another caveat is the small sample in the antidepressant group.

Some thoughts I had whilst reading this paper: to what extent should we be confident that the changes are not purely due to practice? I appreciate there is a relationship between improvement in symptoms and confidence in the iCBT group, but this doesn't completely rule out a practice effect (for instance, you can imagine a scenario in which those whose symptoms have improved are more likely to benefit from previously having practiced the task).

Relatedly, to what extent is there a role for general task engagement in these findings? The paper might be strengthened by some kind of control analysis, perhaps using (as a proxy for engagement) the data collected about those who missed catch questions in the questionnaires.

I was also unclear what the findings about task difficulty might mean. Are confidence changes purely secondary to improvements in task performance generally - so confidence might not actually be 'interesting' as a construct in itself? The authors could have commented more on this issue in the discussion.

To make code more reproducible, the authors could have produced an R notebook that could be opened in the browser without someone downloading the data, so they could get a sense of the analyses without fully reproducing them.

Rather than reporting full study details in another publication I would have found it useful if all relevant information was included in a supplement (though it seems much of it is). This avoids situations where the other publication is inaccessible (due to different access regimes) and minimises barriers for people to fully understand the reported data.

Reviewer #3 (Public Review):

The authors successfully explain the sharp rise and subsequent saturation of the viscosity in dependence of cell packing fraction in zebrafish blastoderm with the help of a 2d model of soft deformable, polydisperse and self-propelled (active) disks. The main experimental observations can be reproduced and the unusual dependence of the viscosity on packing fraction can be explained by the available free area and the emergent motility of small sized cells facilitating multi-cell rearrangement in a highly jammed environment.

The paper is very well written, the results (experimental as well theoretical) are original and scientifically valid. This is an important contribution to understand rheological properties of non-confluent tissues linking equilibrium and transport properties.

Reviewer #3 (Public Review):

The study presented in this paper explores the role of gut microbiota in the therapeutic effect of metformin on HIRI, as supported by fecal microbiota transplantation (FMT) experiments. Through high throughput sequencing and HPLC-MS/MS, the authors have successfully demonstrated that metformin administration leads to an increase in GABA-producing bacteria. Moreover, the study provides compelling evidence for the beneficial impact of GABA on HIRI.

Reviewer #3 (Public Review):

In this manuscript, Berger et al. study how internal energy storage influence learning and memory. Since in Drosophila melanogaster, octopamine (OA) is involved in the regulation of energy homeostasis they focus on the roles of OA. To do so they use the tyramine-β-hydroxylase (Tbh) mutant that is lacking the neurotransmitter OA and study short term memory (STM), long-term memory (LTM) and anesthesia-resistant memory (ARM). They show that the duration of starvation affects the magnitude of both short- and long-term memory. In addition, they show that OA has a suppressive effect on learning and memory. In terms of energy storage, they show that internal glycogen storage influences how long sucrose is remembered and high glycogen suppresses memory. Finally, they show that insulin-like signaling in octopaminergic neurons, which is also related to internal energy storage, suppresses learning and memory.

This is an important study that extends our knowledge on OA activity in learning and memory and the effects the metabolic state has on learning and memory. The authors nicely use the genetic tools available in flies to try and unravel the complex circuitry of metabolic state level, OA activity and learning and memory.<br /> Nevertheless, I do have some comments that I think require attention:

1. The authors use RNAi to reduce the level of glycogen synthase or glycogen phosphorylase. These manipulations are expected to affect the level of glycogen. Using specific drivers the authors attempt to manipulate glycogen level at the muscles and fat bodies and examine how this affects learning and memory. The conclusions of the authors arise solely from the manipulation intended (i.e. the genetics). However, the authors also directly measured glycogen levels at these organs and those do not follow the manipulation intended, i.e. the RNAi had very limited effect on the glycogen level. Nevertheless, these results are ignored.

2. The authors claim in the summary that OA is not required for STM. However, according to one experiment OA is required for STM as Tbh mutants cannot form STM. In another experiment OA is suppressive to STM as wt flies fed with OA cannot form STM. Therefore, it is very difficult to appreciate the actual role of OA on STM.

3. The authors use t-test and ANOVA for most of the statistics, however, they did not perform normality tests. While I am quite sure that most datasets will pass normality test, nevertheless, this is required.

4. While it is logical to assume that OA neurons are upstream to R15A04 DA neurons, I am not sure this really arises from the experiment that is presented here. It is well established that without activity in R15A04 DA neurons there is no LTM. Since OA acts to decrease LTM, can one really conclude anything about the location of OA effect when there is no learning?

5. It is unclear how expression of a dominant negative form of insulin receptor (InR) in OA neurons can rescue the lack of OA due to the Tbh mutation. If OA neurons cannot release anything to the presumably downstream DA neurons, how can changing their internal signaling has any effect?

While I stressed some comments that need to be addressed, the overall take-home message of the manuscript is supported and the authors do show that the metabolic state of the animal affects learning and memory. I do think though, that some more caution is required for some of the conclusions.

Reviewer #3 (Public Review):

The present study used novel data logging devices to record the foraging behavior of wandering albatrosses. Specifically, the authors showed how localized winds and wave heights influence their ability to take off from the sea surface, which is the most expensive behavior they engage in while foraging. There is no better platform for this initial work because these birds are so large, the equipment they can carry without creating significant impact is tremendous.

The results were impressive, presented well, and the paper generally written in an accessible way to readers with less knowledge. The authors provide a convincing set of results that support the aims and conclusions. The theory and application could be used to inform our understanding of flight behavior in other seabirds.

Although the idea of taking off from the sea surface may sound trivial, it is essential to understand that albatrosses and other soaring seabirds have wings that are adapted for soaring (i.e. long and narrow). The trade off however, is that powered flight through wing flapping is energetically expensive because the wings have a shallow amplitude and generate less power compared to a shorter, wider wing. Thus, wind is everything and this study shows how wind facilitates the ability of the birds to gain flight using wind and waves. Awesome!

Reviewer #3 (Public Review):

The manuscript by Boyd and co-authors "A Vibrio cholerae viral satellite maximizes its spread and inhibits phage by remodelling hijacked phage coat proteins into small capsids" reports important results related to self-defending mechanisms that bacteria are used against phages that infect them. It has been shown previously that bacteria produce phage-inducible chromosomal island-like elements (PLE) that encode proteins that are integrated into bacterial genome. These proteins are used by bacteria to amend the phage capsids and to create phage-like particles (satellites) that move between cells and transfer the genetic material of PLE to another bacteria. That study highlights the interactions between a PLE-encoded protein, TcaP, and capsid proteins of the phage ICP1.

The manuscript is well written, provides a lot of new information and the results are supported by biochemical analysis.

Reviewer #3 (Public Review):

Hung et al provide a well-written manuscript focused on understanding how Eklf mutation confers anticancer and longevity advantages in vivo. The work is fundamental and the data is convincing although several details remain incompletely elucidated. The major strengths of the manuscript include the clarity of the effect and the appropriate controls. For instance, the authors query whether Eklf (K74R) imparts these advantages in a background, age, and gender dependent manner, demonstrating that the findings are independent. In addition, the authors demonstrate that the effect is not the consequence of the specific amino acid substitution, with a similar effect on anticancer activity. Furthermore, the authors provide some evidence that PD-1 and PDL-1 are altered in Eklf (K74R) mice.

Finally, they demonstrate that the effects are transferrable with BMT. Several weaknesses are also evidence. For instance, only melanoma is tested as a model of cancer such that a broad claim of "anti-cancer activity" may be somewhat of an overreach. It is also unclear why a homozygous mutation is needed when only a small fraction of cells during BMT can confer benefit. It is also difficult to explain how transplanted donor Eklf (K74R) HSCs confer anti-melanoma effect 7 and 14 days after BMT. Furthermore, it would be useful to see whether there are virulence marker alterations in the melanoma loci in WT vs Eklf (K74R) mice. Finally, the data in Fig 4c is difficult to interpret as decreased PD-1 and PDL-1 after knockdown of EKLF in vitro is not a useful experiment to corroborate how mutation without changing EKLF expression impacts immune cells. The work is impactful as it provides evidence that healthspan and lifespan may be modulated by specific hematological mutation but the mechanism by which this occurs is not completely elucidated by this work.

Reviewer #3 (Public Review):

This work investigates the use of extracellular vesicles (EVs) in blood as a noninvasive 'liquid biopsy' to aid in the differentiation of patients with pancreatic cancer (PDAC) from those with benign pancreatic disease and healthy controls, an important clinical question where biopsies are frequently non-diagnostic. The use of extracellular vesicles as biomarkers of disease has been gaining interest in recent history, with a variety of published methods and techniques, looking at a variety of different compositions ('the molecular cargo') of EVs particularly in cancer diagnosis (Shah R, et al, N Engl J Med 2018; 379:958-966).

This study adds to the growing body of evidence in using EVs for earlier detection of pancreatic cancer, identifying both new and known proteins of interest. Limitations in studying EVs, in general, include dealing with low concentrations in circulation and identifying the most relevant molecular cargo. This study provides validation of assaying EVs using the novel EVtrap method (Extracellular Vesicles Total Recovery And Purification), which the authors show to be more efficient than current standard techniques and potentially more scalable for larger clinical studies.

The strength of this study is in its numbers - the authors worked with a cohort of 124 cases, 93 of them which were PDAC samples, which are considered large for an EV study (Jia, E et al. BMC Cancer 22, 573 (2022)). The benign disease group (n=20, between chronic pancreatitis and IPMNs) and healthy control groups (n=11) were relatively small, but the authors were not only able to identify candidate biomarkers for diagnosis that clearly stood out in the PDAC cohort, but also validate it in an independent cohort of 36 new subjects.

Proteins they have identified as associated with pancreatic cancer over benign disease included PDCD6IP, SERPINA12, and RUVBL2. They were even able to identify a set of EV proteins associated with metastasis and poorer prognosis, which include the proteins PSMB4, RUVBL2 and ANKAR and CRP, RALB and CD55. Their 7-EV protein signature yielded an 89% prediction accuracy for the diagnosis of PDAC against a background of benign pancreatic diseases that is compelling and comparable to other studies in the literature (Jia, E. et al. BMC Cancer 22, 573 (2022)).

The limitations of this study are its containment within a single institution - further studies are warranted to apply the authors' 7-EV protein PRAC panel to multiple other cases at other institutions in a larger cohort.

Reviewer #3 (Public Review):

Cancer is a disease of many faces and in particular, the ability of cancers cells to change their phenotypes and cell behaviors - cancer cell plasticity - is a major contributor to cancer lethality and therapeutic challenge of treating this disease. In this study, Nasir, Pearson et al., investigate tumor cell plasticity through the lens of invasive heterogeneity, and in particular in models of triple-negative breast cancer (TNBC), a subtype of breast cancer with particularly poor clinical prognosis and more limited treatment modalities. Using organoid models in a variety of matrix systems, microscopy, and signaling pathway inhibitors, they find that invading TNBC breast tumors, primarily in the C31-Tag genetically engineered mouse model of TNBC, are composed of heterogeneous invasive/"trailblazer" type tumor cells that in many cases express vimentin, a classical intermediate filament marker of epithelial-mesenchymal transition, and reduced keratin-14, another filament marker of basal epithelial cells associated with collective invasion in different breast cancer models. Supportive genetic and pharmacologic evidence is provided that generation of these cells is TGF-beta signaling pathway driven, likely in vivo from the surrounding tumor microenvironment, in accord with published studies in this space. Another important aspect of this study is the good transcriptional evidence for multiple migratory states showing differing degrees of partial overlap with canonical EMT programs, dependent on TGF-beta, and suggestive but at present incomplete understanding of a parallel program involving Egfr/Fra-1 mediated effects on invasion. When taken in context with other recent studies (Grasset et al. Science Translational Medicine 2022), these data are broadly supportive of concept of targeting vimentin-dependent invasion programs in TNBC tumors.

The core conclusions of this paper are generally supported by the data, but there are some conceptual and technical considerations that should be taken into account when interpreting this study. Specific comments:

1) The contribution of the different vimentin-positive trailblazer cells to distant metastasis was not directly confirmed in vivo in this study. Given the limited proliferative potential of many fully EMT'd cells and in light of recent studies indicating that invasion can be uncoupled from metastatic potential, it seems important to directly test whether the different C31-tag isolates, varying in invasive potential in this study, produce metastases and if so do metastases abundance correlate with the invasive potential in 3D culture. The collection of lungs at 34 days post injection described in methods is too short to evaluate metastatic frequency.

2) The invasion of cancer cells is dependent on 3D matrix composition. In other studies, collective cancer invasion is performed in exclusively collagen type 1 gels or in other instances entirely in 3D reconstituted basement membrane gel, e.g. lung cancer invasion studies. In this study, the authors use a mixture composed of both matrices. Given the invasion suppressive effects of matrigel, particularly for epithelial type cells, further studies would be important to determine whether the invasion phenotypes seen in this study are generalizable across matrix environments.

3) TGF-beta is well known to induce EMT. Although this study identifies potential transcriptional mediators of the invasion/trailblazer program, is this program reversible?

Reviewer #3 (Public Review):

Wu et al. present cryo-EM structures of the potassium channel Kv1.2 in open, C-type inactivated, toxin-blocked and presumably sodium-bound states at 3.2 Å, 2.5 Å, 2.8 Å, and 2.9 Å. The work builds on a large body of structural work on Kv1.2 and related voltage-gated potassium channels. The manuscript presents a large quantity of structural work on the Kv1.2 channel, and the authors should be commended on the breadth of the studies. The structural studies seem well-executed (this is hard to fully evaluate because the current manuscript is missing a data collection and refinement statistics table). The findings are mostly confirmatory, but they do add to the body of work on this and related channels. Notably, the authors present structures of DTX-bound Kv1.2 and of Kv1.2 in a low concentration of potassium (with presumably sodium ions bound within the selectivity filter). These two structures add new information, but the studies seem somewhat underdeveloped - they would be strengthened by accompanying functional studies and further structural analyses. Overall, the manuscript is well-written and a nice addition to the field.

Reviewer #3 (Public Review):

In this study, the authors investigate the effects of Notch pathway inactivation on the termination of Drosophila neuroblasts at the end of development. They find that termination is delayed, while temporal patterning progression is slowed down. Forcing temporal patterning progression in a Notch pathway mutant restores the correct timing of neuroblast elimination. Finally, they show that Imp, an early temporal patterning factor promotes Delta expression in neuroblast lineages. This indicates that feedback loops between temporal patterning and lineage-intrinsic Notch activity fine tunes timing of early to late temporal transitions and is important to schedule NB termination at the end of development.<br /> The study adds another layer of regulation that finetunes temporal progression in Drosophila neural stem cells. This mechanism appears to be mainly lineage intrinsic - Delta being expressed from NBs and their progeny, but also partly niche-mediated - Delta being also expressed in glia but with a minor influence. Together with a recent study (PMID: 36040415), this work suggests that Notch signaling is a key player in promoting temporal progression in various temporal patterning system. As such it is of broad interest for the neuro-developmental community.

Strengths<br /> The data are based on genetic experiments which are clearly described and mostly convincing. The study is interesting, adding another layer of regulation that finetunes temporal progression in Drosophila neural stem cells. This mechanism appears to be mainly lineage intrinsic - Delta being expressed from NBs and their progeny, but also partly niche-mediated - Delta being also expressed in glia but with a minor influence. A similar mechanism has been recently described, although in a different temporal patterning system (medulla neuroblasts of the optic lobe - PMID: 36040415). It is overall of broad interest for the neuro-developmental community.

Weaknesses<br /> The mechanisms by which Notch signaling regulates temporal patterning progression are not investigated in details. For example, it is not clear whether Notch signaling directly regulates temporal patterning genes, or whether the phenotypes observed are indirect (for example through the regulation of the cell-cycle speed). The authors could have investigated whether temporal patterning genes are directly regulated by the Notch pathway via ChIP-seq of Su(H) or the identification of potential binding sites for Su(H) in enhancers. A similar approach has been recently undertaken by the lab of Dr Xin Li, to show that Notch signaling regulates sequential expression of temporal patterning factors in optic lobes neuroblasts (PMID: 36040415), which exhibit a different temporal patterning system than central brain neuroblasts in the present study. As such, the mechanistic insights of the study are limited.

Reviewer #3 (Public Review):

In this study, Gray and coworkers use a transposon mutant library in order to define: (i) essential genes for K. pneumoniae growth in LB medium, (ii) genes required for growth in urine, (iii) genes required for resistance to serum, and complement-mediated killing. Although there are previous studies, using a similar strategy, to describe essential genes for K. pneumoniae growth and genes required for serum resistance, this is the first work to perform such a study in urine. This is important because these types of pathogens can cause urinary tract infections. Moreover, the authors performed the work using a highly saturated library of mutants, which makes the results more robust, and use a clinically relevant strain from a pathotype for which similar studies have not been performed yet. Besides applying the transposon mutant library coupled with high-throughput sequencing, the authors validate some of the most relevant genes required for each condition using targeted mutagenesis. This is clearly an important step to confirm that the results obtained from the library are reliable. Moreover, in vitro experiments involving complementation of urine with iron provide additional support to the results obtained with the mutants suggesting the importance of genes required for iron acquisition in a limiting-iron environment such as urine. Overall, the study is well-designed and written, and the methodology and analysis performed are adequate. The study would have benefited from in vivo experiments, including a mouse model of bacterial sepsis or urinary tract infections which could have demonstrated the role of the identified genes in the infection process. Nevertheless, the results obtained are informative for the scientific community in order to understand which genes are potentially more relevant in infections caused by K. pneumoniae. The identified genes could represent future targets for developing new therapies against a type of pathogen that is acquiring resistance to all available antibiotics. Below I include several comments regarding potential weaknesses in the methodology used:

- The study was done with biological duplicates. In vitro studies usually require 3 samples for performing statistical robust analysis. Thus, are two duplicates enough to reach reproducible results? This is important because many genes are analyzed which could lead to false positives. That said, I acknowledge that genes that were confirmed through targeted mutagenesis led to similar phenotypic results. However, what about all those genes with higher p and q values that were not confirmed? Will those differences be real or represent false positives? Could this explain the differences obtained between this and other studies?

- Two approaches are performed to investigate genes required for K.pneumoniae resistance to serum. In the first approach, the resistance to complement in serum is investigated. And here a total of 356 genes were identified to be relevant. In contrast, when genes required for overall resistance to serum are studied, only 52 genes seem to be involved. In principle, one would expect to see more genes required for overall resistance to serum and within them identify the genes required for resistance to complement. So this result is unexpected. In addition, it seems unlikely that 356 genes are involved in resistance to complement. Thus, is it possible false positives account for some of the results obtained?

Reviewer #3 (Public Review):

Eyraud and colleagues examine how fibrocytes and CD8 cells can interact with each other to promote COPD. The key findings include that CD8 cells and fibrocytes are found to exist in close proximity to each other in COPD lungs using histopathological analysis of patient samples. The authors leverage pre-existing transcriptomic data on CD8 cells to focus on chemokine release by CD8 cells as a potential pathogenic mechanism by which they could affect fibrocyte migration. In vitro studies using peripheral blood-derived CD8 cells and fibrocytes confirm increased fibrocyte migration in the presence of CD8 cells. as drivers of COPD progression. Conversely, in vitro studies show that fibrocytes exert a pro-proliferative effect on CD8 cells. The authors also use a computational model to assess how these interactions could promote the development of fibrocyte-CD8 clusters as COPD progresses over the course of 20 years.

The strengths of the study include:

1. The multi-faceted research approach that integrates histopathology from clinical COPD lung sections, in vitro co-culture studies, and computational modeling.

2. Applying computational modeling to determine how cell-cell interactions of migration and proliferation can result in distribution patterns within the lung that approximate what is found in actual clinical samples

3. Propose a feedback loop of CD8 cells and fibrocytes that could become a potential therapeutic target to interrupt a vicious cycle that promotes COPD

However, there are also some weaknesses:

1. Specificity of the role of CD8 cells: While much of the focus is on the proximity of and interactions between CD8 cells and fibrocytes, it is not clear whether other cells similarly interact with fibrocytes. For example, CD4 cells, dendritic cells, or interstitial macrophages may similarly interact with fibrocytes as several of these also release chemokines. In the absence of a more comprehensive assessment, it becomes difficult to parse out how specific and relevant the fibrocyte-CD8 cell interactions are for COPD progression when compared to other putative interactions.

2. The transcriptomic analysis which in many ways sets the stage for the chemokine studies uses a pre-existing dataset of COPD and non-COPD samples with only n=2. The robustness of such a sample size is limited and the narrow focus on chemokines or adhesion receptors of CD8 cells in this limited sample size does not provide a more comprehensive analysis that would require larger samples sizes, studying the transcriptomes of other cell types and a broader analysis of which pathways are the most likely to be dysregulated in the cells that surround fibrocytes.

3. Specificity of the findings for COPD: The in vitro studies use circulating cells which are different from lung cells and this is appropriately acknowledged by the authors. However, it appears from the description that the cells are all from COPD patients. It is therefore not clear whether these interactions between fibrocytes and CD8 cells are unique to COPD, whether they also occur between control CD8 and fibrocytes, or only in cells obtained from patients with inflammatory/pulmonary diseases. This limitation is appropriately acknowledged in the manuscript.

Reviewer #3 (Public Review):

The authors provide a detailed analysis of the sulcal and sutural imprints preserved on the natural endocast and associated cranial vault fragments of the KNM-ER3732 early Homo specimen. The analyses indicate a primitive ape-like organization of this specimen's frontal cortex. Given the geological age of around 1.9 million years, this is the earliest well-documented evidence of a primitive brain organization in African Homo.

In the discussion, the authors re-assess one of the central questions regarding the evolution of early Homo: was there species diversity, and if yes, how can we ascertain it? The specimen KNM-ER1470 has assumed a central role in this debate because it purportedly shows a more advanced organization of the frontal cortex compared to other largely coeval specimens (Falk, 1983). However, as outlined in Ponce de León et al. 2021 (Supplementary Materials), the imprints on the ER1470 endocranium are unlikely to represent sulcal structures and are more likely to reflect taphonomic fracturing and distortion. Dean Falk, the author of the 1983 study, basically shares this view (personal communication). Overall, I agree with the authors that the hypothesis to be tested is the following: did early Homo populations with primitive versus derived frontal lobe organizations coexist in Africa, and did they represent distinct species?

I greatly appreciate that the authors make available the 3D surface data of this interesting endocast.

Reviewer #3 (Public Review):

By popular single-cell RNA-seq, the authors identified FOXC2 as an undifferentiated spermatogonia-specific expressed gene. The FOXC2+-SSCs can sufficiently initiate and sustain spermatogenesis, the ablation of this subgroup results in the depletion of the uSPG pool. The authors provide further evidence to show that this gene is essential for SSCs maintenance by negatively regulating the cell cycle in adult mice, thus well-established FOXC2 as a key regulator of SSCs quiescent state.

The experiments are well-designed and conducted, the overall conclusions are convincing. This work will be of interest to stem cell and reproductive biologists.

Reviewer #3 (Public Review):

The researchers aim add to the literature on faculty career pathways with particular attention to how gender disparities persist in the career and funding opportunities of researchers. The researchers also examine aspects of institutional prestige that can further amplify funding and career disparities. While some factors about individuals' pathways to faculty lines are known, including the prospects of certain K award recipients, the current study provides the only known examination of the K99/R00 awardees and their pathways.

Strengths:

The authors establish a clear overview of the institutional locations of K99 and R00 awardees and the pathways for K99-to-R00 researchers and the gendered and institutional patterns of such pathways. For example, there's a clear institutional hierarchy of hiring for K99/R00 researchers that echo previous research on the rigid faculty hiring networks across fields, and a pivotal difference in the time between awards that can impact faculty careers. Moreover, there's regional clusters of hiring in certain parts of the US where multiple research universities are located. Moreover, documenting the pathways of HBCU faculty is an important extension of the Wapman et al. study (among others from that research group), and provides a more nuanced look at the pathways of faculty beyond the oft-discussed high status institutions. (However, there is a need for more refinement in this segment of the analyses as discussed further below.). Also, the authors provide important caveats throughout the manuscript about the study's findings that show careful attention to the complexity of these patterns and attempting to limit misinterpretations of readers.

Weaknesses:

The authors reference institutional prestige in relation to some of the findings, but there's no specific measure of institutional prestige included in the analyses. If being identified as a top 25 NIH-funded institution is the proximate measure for prestige in the study, then more justification of how that relates to previous studies' measures of institutional prestige and status are needed to further clarify the interpretations offered in the manuscript.

The identification of institutional funding disparities impacting HBCUs is an important finding and highlights another aspect of how faculty at these institutions are under resourced and arguably undervalued in their research contributions. However, a lingering question exists: why compare HBCUs with Harvard? What are the theoretical and/or methodological justifications for such comparisons? This comparison lends itself to reifying the status hierarchy of institutions that perpetuate funding and career inequalities at the heart of the current manuscript. If aggregating all HBCU faculty together, then a comparable grouping for comparison is needed, not just one institution. Perhaps looking at the top 25 NIH funded institutions could be one way of providing a clearer comparison. Related to this point is the confusing inclusion of Gallaudet in Figure 6 as it is not an officially identified HBCU. Was this institution also included in the HBCU-related calculations?

There is a clear connection that is missed in the current iteration of the manuscript derived from the work of Robert Merton and others about cumulative advantages in science and the "Matthew effect." While aspects of this connection are noted in the manuscript such as well-resourced institutions (those with the most NIH funding in this circumstance) hire each others' K99/R00 awardees, elaborating on these connections are important for readers to understand the central processes of how a rigid hierarchy of funding and career opportunities exist around these pathways. The work the authors build on from Daniel Larremore, Aaron Clauset, and their colleagues have also incorporated these important theoretical connections from the sociology of knowledge and science, and it would provide a more interdisciplinary lens and further depth to understanding the faculty career inequalities documented in the current study.

Reviewer #3 (Public Review):

Dekraker and colleagues previously developed a new computational tool that creates a "surface representation" of the hippocampal subfields. This surface representation was previously constructed using histology from a single case. However, it was previously unclear how to best register and compare these surface-based representations to other cases with different morphology.

In the current manuscript, Dekraker and colleagues have demonstrated the ability to align hippocampal subfield parcellations across disparate 3D histology samples that differ in contrast, resolution, and processing/staining methods. In doing so, they validated the previously generated Big-Brain atlas by comparing seven different ground-truth subfield definitions. This is an impressive and valuable effort that provides important groundwork for future in vivo multi-atlas methods.

Reviewer #3 (Public Review):

Scheer and Bargmann use a combination of computational and experimental approaches in C. elegans to investigate the neuronal mechanisms underlying the regulation of foraging decisions by the state of arousal. They showed that, in C. elegans, the decision to leave food substrates is linked to a high arousal state, roaming, and that an increase in speed at different timescale preceded the food leaving decisions. They found that mutants that exhibit increased roaming also leave food substrates more frequently and that both behaviors can be triggered if food intake is inhibited. They further identify a set of chemosensory neurons that express the transduction channel tax-4 that couple the roaming state and the food-leaving decisions. The authors postulate that these neurons integrate foraging decisions with behavioral states and internal feeding cues.

The strength of the paper relies on using quantitative and detailed behavioral analysis over multiple time scales in combination with the manipulation of genes and neurons to tackle the state-dependent control of behavioral decisions in C. elegans. The evidence is convincing, the analysis rigorous, and the writing is clear and to the point.

Reviewer #3 (Public Review):

In this manuscript, a cytosolic extract of porcine oocytes is prepared. To this end, the authors have aspirated follicles from ovaries obtained by first maturing oocytes to meiose 2 metaphase stage (one polar body) from the slaughterhouse. Cumulus cells (hyaluronidase treatment) and the zona pellucida (pronase treatment) were removed and the resulting naked mature oocytes (1000 per portion) were extracted in a buffer containing divalent cation chelator, beta-mercaptoethanol, protease inhibitors, and a creatine kinase phosphocreatine cocktail for energy regeneration which was subsequently triple frozen/thawed in liquid nitrogen and crushed by 16 kG centrifugation. The supernatant (1.5 mL) was harvested and 10 microliters of it were used for interaction with 10,000 permeabilized boar sperm per 10 microliter extract (which thus represents the cytosol fraction of 6.67 oocytes).

The sperm were in this assay treated with DTT and lysoPC to prime the sperm's mitochondrial sheath.

After incubation and washing these preps were used for Western blot for Fluorescence microscopy and for proteomic identification of proteins. I am very positive about the porcine cell-free assay approach and the results presented here.

Reviewer #3 (Public Review):

In the present study by Boyle et al., the function of NPY expressing spinal neurons in pain and itch perception is studied. While the function of these neurons has been addressed previously, the difference to previous studies is the combinatorial use of AAV encoded effectors and cre transgenic mice whereas previous studies relied on cre transgenic mice and reporter mice encoding the effector or only viruses. Boyle at al. demonstrate that their strategy enabled them to restrict the analysis to only those neurons expressing NPY in the adult mouse compared to a more heterogenous population that had been studied before. By using a combination of morphology, electrophysiology and behavioral paradigms they convincingly show that NPY neurons impact pruritoception via inhibiting GRPR neurons. Furthermore, they indicate a role of NPY neurons also in nociception as activation attenuates not only responses to acute nociceptive stimuli but also blocks inflammation or nerve injury induced mechanical and heat hypersensitivity. Selectively activating NPY neurons in vivo may therefore be a promising strategy to treat neuropathic pain.

The result of this study extends and partially contrast previous studies. The authors argue that contrasting results may be due to the different experimental strategies (e.g. only neurons expressing NPY adult in the present study versus a more heterogeneous population before).

Overall, the experiments are convincing, and the quality of the data/figures is exceptionally high.

Reviewer #3 (Public Review):

This study investigated the role of Zn2+ on the maintenance of Ca2+ oscillation upon fertilization. TPEN was used to reduce the level of available Zn2+ in fertilized oocytes and different inhibitors were used to pinpoint the mechanistic involvement of intracellular Zn2+ on the maintenance of Ca2+ oscillation. As also stated in the manuscript, previous studies have demonstrated the role of Zn2+ for the successful completion of meiosis/fertilization. However, the mechanistic actions of Zn2+ on the hallmark of fertilization processes such as Ca2+ oscillation has not been elucidated. A previous publication used TPEN to cease Ca2+ oscillation, but the study was not focused on the involvement of Zn2+ signal. The manuscript expands our understanding of fertilization process by describing how the level of Zn2+ regulates Ca2+ channels and stores. The manuscript is well-organized and the topic is important in early embryo development fields.

Reviewer #3 (Public Review):

In this manuscript, Haubrich and Nader investigated the difference between mild and strong fear memory mechanisms at the circuit levels. Previous studies have shown the difference in mechanisms and functions of mild and strong fear memory. Interestingly, memory retrieval induces reconsolidation of mild fear memory, but not always strong fear memory; retrieved mild fear memory is disrupted by protein synthesis inhibition, whereas retrieved fear memory is more immune to this inhibition compared to mild memory. The authors measured c-fos expression following retrieval of mild and strong fear memories and compared functional connectivity of brain regions associated with retrieval of them using computation analyses. The authors suggested that mind and strong fear memories differ in neural networks at the circuit levels.<br /> These are interesting findings.

Major concerns:

1) Previous studies including Karim's lab have shown that protein synthesis in the hippocampus is required for the reconsolidation of contextual fear memory and that the retrieval of contextual fear memory activates gene expression such as c-fos in the hippocampus. However, the authors failed to confirm this observation. This may be due to the small number of rats or some technical problems.

2) The author's computation analyses suggested differences in neural networks activated by the retrieval of mild and strong fear memories. The results of computer analysis are interesting. However, it is not clear whether such results are actually occurring in vivo. At this moment, the author's findings are not a conclusion, but rather a suggestion or hypothesis. Therefore, it is also important to conduct interventional experiments to evaluate the validity of the authors' findings. Specifically, the authors' results could be validated by analyzing the effects of inhibition of specific brain regions on mild and strong fear memories retrieval using such as DREADD and other methods. These experiments seem hard, but would greatly improve the quality of the manuscript.

Reviewer #3 (Public Review):

This is an interesting manuscript that addresses a longstanding debate in evolutionary biology - whether social or ecological factors are primarily responsible for the evolution of the large human brain. To address this, the authors examine the relationship between the size of two prefrontal regions involved in metacognition and working memory (DLPFC and FP) and socioecological variables across 16 primate species. I recommend major revisions to this manuscript due to: 1) a lack of clarity surrounding model construction; and 2) an inappropriate treatment of the relative importance of different predictors (due to a lack of scaling/normalization of predictor variables prior to analysis). My comments are organized by section below:

Introduction:<br /> • Well written and thorough, but the questions presented could use restructuring.

Methods:<br /> • It is unclear which combinations of models were compared or why only population density and distance travelled tested appear to have been included.<br /> • Brain size (vs. body size) should be used as a predictor in the models.<br /> • It is not appropriate to compare the impact of different predictors using their coefficients if the variables were not scaled prior to analysis.

Reviewer #3 (Public Review):

Schnell and colleagues trained rats on a visual categorization task. They found that rats could discriminate objects across various image transformations. Rat performance correlated best with late convolutional layers of an artificial neural network. In contrast, human performance showed the strongest correlation with higher, fully connected layers, indicating that rats employed simpler strategies to accomplish this task as compared to humans. This is a methodologically rigorous study. The authors tested a substantial number of rats across a large variety of stimuli. One notable strength is the use of neural networks to generate stimuli with varying levels of complexity. This approach shows significant potential as a principled model for conducting studies on object recognition and other related visual behavioral phenomena. The data strongly support the conclusion that rats and humans rely on different visual features for discrimination tasks. Overall, this is a valuable study that provides novel, important insights into the visual capabilities of rats. However, some aspects of the study need further clarification. The study does not provide clear insights into the visual features that enable rats to perform these discriminations. The relationship between neural network layers and specific aspects of visual behavior is not well-defined, representing a key limitation of the current work. Further, the current analyses do not adequately address the consistency of visual behaviors across different rats or whether different rats rely on the same visual features to accomplish the task. Lastly, rodent performance was substantially lower compared to humans and generally worse than neural network classification. The factors contributing to this disparity are unclear.

Reviewer #3 (Public Review):

Nitta et al. establish a fly model of autosomal dominant optic atrophy, of which hundreds of different OPA1 mutations are the cause with wide phenotypic variance. It has long been hypothesized that missense OPA1 mutations affecting the GTPase domain, which are associated with more severe optic atrophy and extra-ophthalmic neurologic conditions such as sensorineural hearing loss (DOA plus), impart their effects through a dominant negative mechanism, but no clear direct evidence for this exists particularly in an animal model. The authors execute a well-designed study to establish their model, demonstrating a clear mitochondrial phenotype with multiple clinical analogs including optic atrophy measured as axonal degeneration. They then show that hOPA1 mitigates optic atrophy with the same efficacy as dOPA1, setting up the utility of their model to test disease-causing hOPA1 variants. Finally, they leverage this model to provide the first direct evidence for a dominant negative mechanism for 2 mutations causing DOA plus by expressing these variants in the background of a full hOPA1 complement.

Strengths of the paper include well-motivated objectives and hypotheses, overall solid design and execution, and a generally clear and thorough interpretation of their results. The results technically support their primary conclusions with caveats. The first is that both dOPA1 and hOPA1 fail to fully restore optic axonal integrity, yet the authors fail to acknowledge that this only constitutes a partial rescue nor do they discuss how this fact might influence our interpretation of their subsequent results. The second caveat is that their effect sizes are small. Statistically, the results indeed support a dominant negative effect of DOA plus-associated variants, yet the data show a marginal impact on axonal degeneration for these variants. The authors might have considered exploring the impact of these variants on other mitochondrial outcome measures they established earlier on. They might also consider providing some functional context for this marginal difference in axonal optic nerve degeneration.

Despite these caveats, the authors provide the first animal model of DOA that also allows for rapid assessment and mechanistic testing of suspected OPA1 variants. The impact of this work in providing the first direct evidence of a dominant negative mechanism is under-stated considering how important this question is in development of genetic treatments for DOA. The authors discuss important points regarding the potential utility of this model in clinical science. Comments on the potential use of this model to investigate variants of unknown significance in clinical diagnosis requires further discussion of whether there is indeed precedent for this in other genetic conditions (since the model is nevertheless so evolutionarily removed from humans).

Reviewer #3 (Public Review):

This study of CFTR, its mutants, dynamics, and effects of ATP binding, and drug binding is well written and highly informative. They have employed coarse-grained dynamics that help to interpret the dynamics in useful and highly informative ways. Overall the paper is highly informative and a pleasure to read.

The investigation of the effects of drugs is particularly interesting, but perhaps not fully formed.

Reviewer #3 (Public Review):

This paper presents several eyetracking experiments measuring task-directed reading behavior where subjects read texts and answered questions.<br /> It then models the measured reading times using attention patterns derived from deep-neural network models from the natural language processing literature.<br /> Results are taken to support the theoretical claim that human reading reflects task-optimized attention allocation.

Strengths:

1) The paper leverages modern machine learning to model a high-level behavioral task (reading comprehension). While the claim that human attention reflects optimal behavior is not new, the paper considers a substantially more high-level task in comparison to prior work. The paper leverages recent models from the NLP literature which are known to provide strong performance on such question-answering tasks, and is methodologically well grounded in the NLP literature.

2) The modeling uses text- and question-based features in addition to DNNs, specifically evaluates relevant effects, and compares vanilla pretrained and task-finetuned models. This makes the results more transparent and helps assess the contributions of task optimization. In particular, besides fine-tuned DNNs, the role of the task is further established by directly modeling the question relevance of each word. Specifically, the claim that human reading is predicted better by task-optimized attention distributions rests on (i) a role of question relevance in influencing reading in Expts 1-2 but not 4, and (ii) the fact that fine-tuned DNNs improve prediction of gaze in Expts 1-2 but not 4.

3) The paper conducts experiments on both L2 and L1 speakers.

Weaknesses:

1) The paper aims to show that human gaze is predicted the the DNN-derived task-optimal attention distribution, but the paper does not actually derive a task-optimal attention distribution. Rather, the DNNs are used to extract 144 different attention distributions, which are then put into a regression with coefficients fitted to predict human attention. As a consequence, the model has 144 free parameters without apparent a-priori constraint or theoretical interpretation. In this sense, there is a slight mismatch between what the modeling aims to establish and what it actually does.

2) While Experiment 1 tests questions from different types in blocks, and the paper mentions that this might encourage the development of question-type-specific reading strategies -- indeed, this specifically motivates Experiment 2, and is confirmed indirectly in the comparison of the effects found in the two experiments ("all these results indicated that the readers developed question-type-specific strategies in Experiment 1") -- the paper seems to miss the opportunity to also test whether DNNs fine-tuned for each of the question-types predict specifically the reading times on the respective question types in Experiment 1. Testing not only whether DNN-derived features can differentially predict normal reading vs targeted reading, but also different targeted reading tasks, would be a strong test of the approach.

3) The paper compares the DNN-derived features to word-related features such as frequency and surprisal and reports that the DNN features are predictive even when the others are regressed out (Figure S3). However, these features are operationalized in a way that puts them at an unfair disadvantage when compared to the DNNs: word frequency is estimated from the BNC corpus; surprisal is derived from the same corpus and derived using a trigram model. The BNC corpus contains 100 Million words, whereas BERT was trained on several Billions of words. Relatedly, trigram models are now far surpassed by DNN-based language models. Specifically, it is known that such models do not fit human eyetracking reading times as well as modern DNN-based models (e.g., Figure 2 Dundee in: Wilcox et al, On the Predictive Power of Neural Language Models for Human Real-Time Comprehension Behavior, CogSci 2020). This means that the predictive power of the word-related features is likely to be underestimated and that some residual predictive power is contained in the DNNs, which may implicitly compute quantities related to frequency and surprisal, but were trained on more data. In order to establish that the DNN models are predictive over and above word-related features, and to reliably quantify the predictive power gained by this, the authors could draw on (1) frequency estimated from the corpora used for BERT (BookCorpus + Wikipedia), (2) either train a strong DNN language model, or simply estimate surprisal from a strong off-the-shelf model such as GPT-2.

This concern does not fundamentally cast doubt on the conclusions, since the authors found a clear effect of the task relevance of individual words, which by definition is not contained in those baseline models. However, Figure S3 -- specifically Figure S3C -- is likely to inflate the contribution of the DNN model over and above the text-based features.

The results broadly support the conclusions; however, with the qualification that the paper provides a somewhat indirect test, by testing DNN-derived features without deriving a single task-optimized attention distribution for each task.

The data are likely to be useful as a benchmark in further modeling of eye-movements, an area of interest to computational research on psycholinguistics.<br /> The modeling results contribute to theoretical understanding of human reading behavior, and strengthens a line of research arguing that it reflects task-adaptive behavior.

The theoretical claim, and some basic features of the research, are quite similar to other recent work (Hahn and Keller, Modeling task effects in human reading with neural network-based attention, Cognition, 2023; cited with very little discussion as ref 44), which also considered task-directed reading in a question-answering task and derived task-optimized attention distributions. There are various differences, and the paper under consideration has both weaknesses and strengths when compared to that existing work -- e.g., that paper derived a single attention distribution from task optimization, but the paper under consideration provides more detailed qualitative analysis of the task effects, uses questions requiring more high-level reasoning, and uses more state-of-the-art DNNs.

Reviewer #3 (Public Review):

Artificial neural networks have developed into a new research tool across various disciplines of neuroscience. However, specifically for studying neural control of movement it was extremely difficult to train those models, as they require not only simulating the neural network, but also the body parts one is interested in studying. The authors provide a solution to this problem which is built upon one of the main software packages used for deep learning (Tensorflow). This allows them to make use of state-of-the-art tools for training neural networks.

They show that their toolbox is able to (re-)produce several commonly studied experiments e.g., planar reaching with and without loads. The toolbox is described in sufficient detail to get an overview of the functionality and the current state of what can be done with it. Although the authors state that only a few lines of code can reproduce such an experiment, they unfortunately don't provide any source code to reproduce their results (nor is it given in the respective repository).

The modularity of the presented toolbox makes it easy to exchange or modify single parts of an experiment e.g., the task or the neural network used as a controller. Together with the open-source nature of the toolbox, this will facilitate sharing and reproducibility across research labs.

I can see how this paper can enable a whole set of new studies on neural control of movement and accelerate the turnover time for new ideas or hypotheses, as stated in the first paragraph of the Discussion section. Having such a low effort to run computational experiments will be definitely beneficial for the field of neural control of movement.

Reviewer #3 (Public Review):

The authors have devised a clever experimental design involving the provision of cues to participants, indicating the finger that is more likely to be stimulated in each trial (e.g., ring finger or thumb). Employing fMRI analyses, the authors have leveraged the distinct and well-defined finger representations in the somatosensory cortex to investigate how prior knowledge influences the processing of haptic stimuli in a probability cueing paradigm. The authors successfully replicate key neural phenomena associated with predictive processing, encompassing expectation suppression, the sharpening of expected information representation, and the pre-activation of sensory templates associated with the anticipated stimulus. The methodology employed in this study is straightforward, and the obtained results are convincing.

However, it is worth noting that the cue-finger and finger associations were explicitly conveyed to the participants in this study. Additionally, the inter-stimulus interval (ISI) between the finger-cue and the cue varied randomly across trials, rendering the onset of the cue unpredictable (in time) for the participants. These experimental manipulations lead me to consider that the observed results may not be solely explained by predictive mechanisms but could also involve top-down controlled attention. It would be valuable for the authors to include a task similar to Experiment 2 in Kok et al. (2012), where participants' attention was diverted away from the gratings contrast, yet decoding sharpening for expected but task-irrelevant stimulus orientations was still evident. By incorporating such a task, it would help elucidate whether the authors would replicate similar results when predictive information remains intact but the predicted stimulus feature becomes task-irrelevant.

Furthermore, I have concerns regarding potential issues related to the training of the multivariate decoder. If I understand correctly, instead of using the functional localiser to train the SVM classifier, the authors directly employed the experimental data from the congruent, incongruent, and non-informative conditions together. It is noted that the number of trials used in each training fold was downsampled to achieve an equal number of trials from each condition, controlling for the asymmetry in number of trials between the incongruent and congruent conditions. However, I am concerned that if there are univariate differences between the activity patterns in the training datasets (e.g., congruent < incongruent), the decoder might exhibit a bias towards relying more on the activity of one specific condition, thereby potentially performing better in decoding that particular condition. To address this, I suggest presenting Representational Similarity Analysis (RSA) results using the activity patterns evoked by congruent, incongruent, and non-informative stimuli. This analysis would offer a simpler, more interpretable representation of changes in the representational geometry of the stimuli based on previous predictions (see Blank & Davis, 2016), and might shed some light on whether your results correspond on sharpening or dampening of the expected information.

Reviewer #3 (Public Review):

Goetz, Akl and Dixit investigated the heterogeneity in the fidelity of sensing the environment by individual cells in a population using computational modeling and analysis of experimental data for two important and well-studied mammalian signaling pathways: (insulin-like growth factor) IGF/FoxO and (epidermal growth factor) EFG/EFGR mammalian pathways. They quantified this heterogeneity using the conditional mutual information between the input (eg. level of IGF) and output (eg. level of FoxO in the nucleus), conditioned on the "state" variables which characterize the signaling pathway (such as abundances of key proteins, reaction rates, etc.) First, using a toy stochastic model of a receptor-ligand system - which constitutes the first step of both signaling pathways - they constructed the population average of the mutual information conditioned on the number of receptors and maximized over the input distribution and showed that it is always greater than or equal to the usual or "cell state agnostic" channel capacity. They constructed the probability distribution of cell state dependent mutual information for the two pathways, demonstrating agreement with experimental data in the case of the IGF/FoxO pathway using previously published data. Finally, for the IGF/FoxO pathway, they found the joint distribution of the cell state dependent mutual information and two experimentally accessible state variables: the response range of FoxO and total nuclear FoxO level prior to IGF stimulation. In both cases, the data approximately follow the contour lines of the joint distribution. Interestingly, high nuclear FoxO levels, and therefore lower associated noise in the number of output readout molecules, is not correlated with higher cell state dependent mutual information, as one might expect. This paper contributes to the vibrant body of work on information theoretic characterization of biochemical signaling pathways, using the distribution of cell state dependent mutual information as a metric to highlight the importance of heterogeneity in cell populations. The authors suggest that this metric can be used to infer "bottlenecks" in information transfer in signaling networks, where certain cell state variables have a lower joint distribution with the cell state dependent mutual information.

The utility of a metric based on the conditional mutual information to quantify fidelity of sensing and its heterogeneity (distribution) in a cell population is supported in the comparison with data. Some aspects of the analysis and claims in the main body of the paper and SI need to be clarified and extended.

1) The authors use their previously published (Ref. 32) maximum-entropy based method to extract the probability distribution of cell state variables, which is needed to construct their main result, namely p_CeeMI (I). The salient features of their method, and how it compares with other similar methods of parameter inference should be summarized in the section with this title. In SI 3.3, the Lagrangian, L, and Rm should be defined.<br /> 2) Throughout the text, the authors refer to "low" and "high" values of the channel capacity. For example, a value of 1-1.5 bits is claimed to be "low". The authors need to clarify the context in which this value is low: In some physically realistic cases, the signaling network may need to simply distinguish between the present or absence of a ligand, in which case this value would not be low.<br /> 3) Related to (2), the authors should comment on why in Fig. 3A, I_Cee=3. Importantly, where does the fact that the network is able to distinguish between 23 ligand levels come from? Is this related to the choice (and binning) of the input ligand distribution (described in the SI)?<br /> 4) The authors should justify the choice of the gamma distribution in a number of cases (eg. distribution of ligand, distribution cell state parameters, such as number of receptors, receptor degradation rate, etc.).<br /> 5) Referring to SI Section 2, it is stated that the probability of the response (receptor binding occupancy) conditioned on the input ligand concentration and number of receptors is a Poisson distribution. Indeed this is nicely demonstrated in Fig. S2. Therefore it is the coefficient of variation (std/mean) that decreases with increasing R0, not the noise (which is strictly the standard deviation) as stated in the paper.<br /> 6) In addition to explicitly stating what the input (IGF level) and the output (nuclear GFP-tagged FoxO level) are, it would be helpful if it is also stated what is the vector of state variables, theta, corresponding to the schematic diagram in Fig. 2C.<br /> 7) Related to Fig. 2C, the statement in the caption: "Phosphorylated Akt leads to phosphorylation of FoxO which effectively shuttles it out of the nucleus." needs clarification: From the figure, it appears that pFoxO does not cross the nuclear membrane, in which case it would be less confusing to say that phosphorylation prevents reentry of FoxO into the nucleus.<br /> 8) The explanations for Fig. 2D, E and insets are sparse and therefore not clear. The authors should expand on what is meant by model and experimental I(theta). What is CC input dose? Also in Fig. 2E, the overlap between the blue and pink histograms means that the value of the blue histogram for the final bin - and therefore agreement or lack thereof with the experimental result - is not visible. Also, the significance of the values 3.25 bits and 3 bits in these plots should be discussed in connection with the input distributions.<br /> 9) While the joint distribution of the cell state dependent mutual information and various biochemical parameters is given in Fig. S7, there is no explanation of what these results mean, either in the SI or main text. Related to this, while a central claim of the work is that establishing this joint distribution will allow determination of cell state variables that differentiate between high and low fidelity sensing, this claim would be stronger with more discussion of Figs. 3 and S7.<br /> 10) The related central claim that cell state dependent mutual information leads to higher fidelity sensing at the population level would be made stronger if it can be demonstrated that in the limit of rapidly varying cell state variables, the I_CSA is retrieved.

Reviewer #3 (Public Review):

This manuscript presents a novel fluorescence toolkit designed for investigating the folding states of RNA-binding proteins (RBPs) and their association with molecular chaperones during liquid-liquid phase separation (LLPS) in the formation of nuclear bodies under stress. The strategy is to use SNAP-tag technology including cell lines stably expressing three model proteins fused with SNAP tag and a series of environmentally sensitive fluorophores that can selectively label on the SNAP proteins. The changes in the microenvironment such as microviscosity and micropolarity can be well characterized by these fluorophores to reflect the conformational states of the RBPs.

The strength of this method is that the SNAP protein is smaller than classic fluorescent proteins like GFP and thus its impact on the conformation and behavior of the targeted proteins is much smaller. The experiment is carefully designed and well thought-out. Overall, this work is of very high quality.

This method can thus be adapted by other protein systems to study the LLPS process and thus I believe it will be of great interest to cell biologists and biophysicists.

Reviewer #3 (Public Review):

This paper concerns whether scaling (or homeostatic synaptic plasticity; HSP) occurs similarly at GABA and Glu synapses and comes to the surprising conclusion that these are regulated separately. This is surprising because these were thought to be co-regulated during HSP and in fact, the major mechanisms thought to underlie downscaling (TTX or CNQX driven), retinoic acid and TNF, have been shown to regulate both GABARs and AMPARs directly. (As a side note, it is unclear that the manipulations used in Josesph and Turrigiano represent HSP, and so might not be relevant). Thus the main result, that GABA HSP is dissociable from Glu HSP, is novel and exciting. This suggests either different mechanisms underlie the two processes, or that under certain conditions, another mechanism is engaged that scales one type of synapse and not the other.

However, strong claims require strong evidence, and the results presented here only address GABA HSP, relying on previous work from this lab on Glu HSP (Fong, et al., 2015). But the previous experiments were done in rat cultures, while these experiments are done in mice and at somewhat different ages (DIV). Even identical culture systems can drift over time (possibly due to changes in the components of B27 or other media and supplements). Therefore it is necessary to demonstrate in the same system the dissociation. To be convincing, they need to show the mEPSCs for Fig 4, clearly showing the dissociation. Doing the same for Fig 5 would be great, but I think Fig 4 is the key.

The paper also suggests that only receptor function or spiking could control HSP, and therefore if it is not receptor function then it must be spiking. This seems like a false dichotomy; there are of course other options. Details in the data may suggest that spiking is not the (or the only) homeostat, as TTX and CNQX causes identical changes in mIPSC amplitude but have different effects on spiking. Further, in Fig 5, CTZ had a minimal effect on spiking but a large effect on mIPSCs. Similar issues appear in Fig 6, where the induction of increased spiking is highly variable, with many cells showing control levels or lower spiking rates. Yet the synaptic changes are robust, across all cells. Overall, this is not persuasive that spiking is necessarily the homeostat for GABA synapses.

The paper also suggests that the timing of the GABA changes coincides with the spiking changes, but while they have the time course of the spiking changes and recovery, they only have the 24h time point for synaptic changes. It is impossible to conclude how the time courses align without more data.

Reviewer #3 (Public Review):

This work shows how, in the formation of the immune synapse, the B cell controls the contraction phase, the formation and retraction of actin structures concentrating the antigen (actin foci), and, ultimately, global signal attenuation. The authors use a combination of TIRF microscopy and original image quantification to show that Arp2/3 activated by N-WASP controls a pool of actin concentrated in foci (situated in the synapse), formed and transported centripetally towards the center of the synapse through myosin II mediated contractions. These contractions concentrate the B cell receptors (BCRs) in the center, promote disassembly of the stimulatory kinase Syk as well as the the disassociation from the BCR of the inhibitory phosphatase SHIP, process which entails the attenuation of the BCR signal.

The author prove their claims by mean of thorough image analysis, mainly observing and quantifying the fluorescence and the dynamics of single clusters of antigen and actin foci and analyzing two-colors dynamical images. They perform their observation in control cells, on pharmacologically perturbed cells where the action of Arp2/3 or N-WASP is inhibited, and on modified primary cells (primary derived from genetically engineered mice) to silence N-WASP or WASP. The work is sound and complete, the experiments technically excellent and well explained. Some experiments and discussions are objectively harder to describe, and given the length of the work, the reader might find itself lost some times. A graphical abstract/summary of the main way NWASP ultimately control signal attenuation would solve this minor point.

This work adds an important information to the current view of B cell activation, in particular it links the contraction phase to the actin foci that have been recently characterized. Moreover, the late phase of the immune synapse formation is, in general, poorly investigated, but it is crucial for the fate of the cell: this work provides an explanation for the attenuation of the signal that might lead to the termination of the synapse.

Reviewer #3 (Public Review):

This study investigates the roles of astrocytes in the regulation of synapse development and astrocyte morphology using conditional KO mice carrying mutations of three neuroligins1-3 in astrocytes with the deletion starting at two different time points (P1 and P10/11). The authors use morphological, electrophysiological, and cell-biological approaches and find that there are no differences in synapse formation and astrocyte cytoarchitecture in the mutant hippocampus and visual cortex. These results differ from the previous results (Stogsdill et al., 2017), although the authors make several discussion points on how the differences could have been induced. This study provides important information on how astrocytes and neurons interact with each other to coordinate neural development and function. The experiments were well-designed, and the data are of high quality.

Reviewer #3 (Public Review):

My biggest concern is that I am not convinced that the HIER task is indeed hierarchical. Based on Figure 1B, it seems that the rules of the task can be listed as "Green and same = 2", "Green and different = 4", "Red and same = 1", "Red and different = 3". If so, the hierarchical organisation intended by the authors can be trumped by simply memorising these 4 options. The rote memory explanation is even more likely given that the other, ITER task, clearly required rote memory. Hence the two tasks may vary simply in the amount of difficulty/WM involvement.

Reviewer #3 (Public Review):

The authors first explore structural differences of unbound TCR-CD3 complexes and pMHC-bound TCR-CD3 complexes with coarse-grained simulations. In the simulations with pMHC-bound complexes, the transmembrane (TM) domains of the TCR-CD3 complex and of pMHC are embedded in two opposing membrane patches. In the pMHC membrane patch, a pore is created and stabilised in the simulation setup with the aim to allow water transport in and out of the compartment between the membranes. The authors report a more upright conformation of the TCR extracellular (EC) domain in the simulations in which this EC domain is bound to pMHC, compared to simulations with unbound TCR, and postulate an allosteric signalling model based on these apparent conformational changes and associated changes in TCR-CD3 quaternary arrangements. Subsequently, the authors identify a GxxG motif in the TCRbeta connecting peptide between EC domain and TM domain as putative hinge in allosteric signalling, and explore the effect of double proline and double alanine substitutions in atomistic simulations and experiments.

While these simulation and experimental setups and the addressed questions are of interest in the field, the following weaknesses prevail in my overall assessment of the work:

(1) I am not convinced that the reported coarse-grained simulation results are sound or allow to draw the conclusions stated in the work. In the simulations with a pMHC-bound TCR-CD3 complex, the intermembrane distance in the setup shown in Figure S1 appears excessively large and likely leads to a rather strong force in the membrane-vertical direction and to the reported upright conformation of the TCR EC domain. This upright confirmation thus appears to be a consequence of force from the simulation setup, rather than a consequence of pMHC binding alone as suggested by the authors. While the membrane pore in principle allows water exchange, the relaxation of the intermembrane distance resulting from this water exchange in the 10 microsecond long simulation trajectories is not (but needs to be) addressed. This relaxation eventually would lead to an equilibrated membrane separation, in which essentially no force is exerted on the TCR-pMHC EC complex. However, I suspect that this computationally demanding equilibration is not achieved in the simulations, with the consequence that forces on the TCR-pMHC EC complex in the membrane-vertical direction remain.

In addition, I am not convinced that the Martini force field of the coarse-grained simulations allows a reliable assessment of the quaternary interactions between the TCR and CD3 EC domains. Getting protein structures and interactions right in coarse-grained simulations is notoriously difficult. In simulations with the coarse-grained Martini force field, secondary protein structures are constrained as a standard procedure, and the authors also use a recommended Go-potential procedure, likely to stabilise tertiary protein structures. The quaternary interactions between the TCR EC domain and the pMHC EC domain are modelled by rather strong harmonic constraints to prevent dissociation. While the treatment of the quaternary interactions between the TCR EC domain and the CD3 EC domains in the simulations is not (but needs to be) addressed in detail, I suspect that there are no additional, or only weak constraints to stabilise these interactions. In any case, I think that a faithful representation of these quaternary interactions is beyond the reach of the Martini force field, as is the reported diffusion of the CD3 EC domains around the TCR EC domain, which plays a central role in the allosteric mechanism proposed by the authors (see Fig 2 and 5).

(2) The allosteric model suggested by the authors is motivated in an introduction that appears to omit central controversial aspects in the field, as well as experimental evidence that is not compatible with allosteric conformational changes in the TCR. These aspects are:

- The mechanosensor model is controversial. In original versions of this model, a transversal force has been postulated to be required for T cell activation. However, more recent single-molecule force-sensor experiments reported in J Goehring et al., Nat Commun 12, 1 (2021) provide no evidence for a scenario in which transversal forces beyond 2 pN are associated with T cell activation.

- The role of catch bonds is controversial. Evidence for TCR catch bonds has been mainly obtained in experimental setups using the biomembrane force probe, in which force is applied to TCRs on the surface of T cells, but is not reproduced in experimental setups using isolated TCRs, see e.g. L Limozin et al., PNAS 116, 16943 (2019)

- Ref. 1 of the manuscript prominently discusses the kinetic segregation model of T cell activation, which is not (but needs to be) addressed in the introduction. In this model, exclusion of CD45 from close-contact zones around pMHC-bound TCRs triggers T cell activation. The model is supported by evidence from diverse experiments, see for example M Aramesh et al., PNAS 118, e2107535118 (2021) and Ref. 1. At least part of this evidence is not compatible with mechanosensing or allosteric models of T cell activation.

Reviewer #3 (Public Review):

The Liu, et al. manuscript focuses on the interesting topic of evaluating in an almost genome-wide-scale, the number of transcriptional isoforms and fusion gene are present in single cells across the annotated protein coding genome. They also seek to determine the occurrences of single nucleotide variations/mutations (SNV) in the same isoform molecule emanating from the same gene expressed in normal and normal and hepatocellular carcinoma (HCC) cells. This study has been accomplished using modified LoopSeq long‐read technology (developed by several of the authors) and single cell isolation (10X) technologies. While this effort addresses a timely and important biological question, the reader encounters several issues in their report that are problematic.:

1) Much of the analysis of the evolution of mutations results and the biological effects of the fusion genes is conjecture and is not supported by empirical data. While their conclusions leave the reader with a sense that the results obtained from the LoopSeq has substantive biological implications. However, they are extended interpretations of the data. For example: The fusion protein likely functions as a decoy interference protein that negatively impacts the microtubule organization activity of EML4.(pg 9)... and other statements presented in a similar fashion.

2) LoopSeq has the advantage of using short read sequencing analyses to characterize the exome capture results and thus benefits from low error rate compared to standard long-read sequencing techniques. However, there is no evidence obtained from standard long read sequencing that the isoforms observed with LoopSeq are obtained with parallel technologies such as long read technologies. It is not made clear how much discordance there is in comparing the LoopSeq results are with either PacBio or ONT long read technologies.

3) There is no proteome evidence (empirically derived or present in proteome databases) from the HCC and normal samples that confirms the presence or importance of the identified novel isoforms, nor is there support that indicate that changes in levels HLA genes translate to effects observed at the protein level. Since the stability and transport differences of isoforms from the same gene are often regulated at the post-transcriptional level, the biological importance of the isoform variations is unclear.

4) It is unclear why certain thresholds were chosen for standard deviation (SD) <0.4 (page 5), SD >1.0 (pg 11).

5) HLA is known to accumulate considerable somatic variation. Of the many non-immunological genes determined to have multiple isoforms what are the isoform specific mutation rates in the same isoform molecule? Are the HLA genes unique in the number of mutations occurring in the same isoform?

Reviewer #3 (Public Review):

In this paper by Keramidioti et al, the authors have characterized a polyclonal antibody from rabbit, which was raised against a peptide of the intracellular domain of the Hydra Cadherin. This antibody unexpectedly recognizes presumably all neurons in the Hydra polyp and indeed the specificity of the antibody is not fully convincing. Regardless, the antibody can be used to visualize and study the nerve net under a variety of conditions. The authors find that the endodermal and ectodermal nerve net do not make any contacts through the mesoglea, in contrast to earlier assumptions and data. They show that ectodermal neurons make close contacts to the myoepithelial muscles, in contrast to the endodermal muscles. Furthermore, they show that tentacle endoderm surprisingly does not have any neurons. Finally, a very nice tool to visualize the connections between the neurons is the staining of mosaic nGreen transgenic lines. This showed that the neurites align in parallel forming bundles of neurites over longer stretches, in particular in the ectoderm, which offers a mechanism how new neurons are added laterally to the existing nerve net. This has important implications about the way the neurons might communicate with each other.

Taken together, this paper adds to our knowledge of the Hydra nerve net and provides a new experimental tool. Although most of the study is rather descriptive the pictures are of spectacular quality, providing fascinating new insights into the arrangement and topology of the nerve net.

Reviewer #3 (Public Review):

In this study, a minimalistic setup was used to investigate the selectivity of the nuclear pore complex as a function of its diameter. For this an array of solid-state pores was designed in a free-standing palladium membrane and attached to a PDMS-based fluidic cell, which could be mounted on a confocal microscope. In this way, the frequency of translocation events could be measured in an unbiased manner, i.e., no voltage was applied in this setup to facilitate them as it was done previously (Kowalczyk et al., 2011; Ananth et al, 2018; Fragasso et al., 2021, 2022), and therefore they can be considered as spontaneous. Moreover, the pores exhibited the key properties of the nuclear pore complex: (i) the size of the pore, (ii) disordered FG Nups specifically attached in the central channel; (ii) transport receptors that can shuttle through the central channel by binding to the FG Nups. Additionally, the properties of such minimalistic system could be well controlled. This gave the authors an advantage to monitor the translocation of multiple fluorescently labeled molecules (e.g. Kap95 and BSA) simultaneously, in real time and under well controlled conditions.

Strength:<br /> By being able to adjust each system parameter independently, the authors were able to monitor a reciprocal influence of active transporters, such as Kap95, and passive diffusion (using BSA as passive cargo) at different pore sizes and protein concentrations. It was discovered that up to a certain pore size (ca. 50-60 nm, which is close to the diameter of the physiological nuclear pore complex) and the Nsp1 density, Kap95 binding in the pore significantly increases selectivity as it was previously predicted by 'Kap-centric control' model (Kapinos, et al, 2014, Wagner et al, 2015). However, in pores larger than 60 nm, this effect was fading and becoming negligible in very large pores (> 60 nm), showing that the pores could become leaky and less selective due to stretching, as has been previously suggested (Andreu et al., 2022). It was also shown that passive molecules, such as BSA, had no effect on the Kap95 translocation frequency through the pore.

The experimental data were also supported by coarse-grained modelling of Nsp1-coated pores, and the theoretical prediction correlates qualitatively with the experimentally obtained data. These simulations show that there is a relationship between pore diameter and Nsp1 conformation. Based on these simulations, the authors suggest that in small pores (<60 nm) Kap95 increases selectivity by interacting with the Nsp1-FG domains across the pore, whereas this is less likely for larger pore diameters and Kap95 may collapse the Nsp1-FG domains along the pore walls, making them more permeable.

Weaknesses:<br /> However, the simulations did not consider an effect of Kap95 on the conformation of the Nsp1 layer within the pore, which weakens the conclusion of Kap95-induced collapse, even though it seems very plausible.<br /> In addition, there is a discrepancy in the frequency of translocation events in different experimental setups reported in different studies. The authors suggest that this may be due to differences in the sensitivity of detection methods.

Strength of evidence:<br /> However, this does not detract from the results obtained in this work, as the conclusions are based on the relative changes compared to the numerous controls within the same experimental setup and a careful evaluation of all possible sources of error.

Reviewer #3 (Public Review):

Wang et al. investigated the role of acetate production, a byproduct of fatty acid oxidation, in the context of metabolic stressors, including diabetes mellitus and prolonged fasting. Mechanistically, they show the importance of the liver enzymes ACOT8 (peroxisome) and ACOT12 (cytoplasm) in converting FFA-derived acetyl-CA into acetate and CoA. The regeneration of CoA allows for subsequent fatty acid oxidation. Inhibiting the generation of acetate has negative motor and behavioral consequences in streptozocin-treated mice, which are mitigated with acetate injection.

This paper's strengths include using multiple mouse models, metabolic stressors (db/db-/-, streptozocin, and prolonged starvation), numerous cell lines, precise knockout and rescue experiments, and complimentary use of mass spectrometry and nuclear magnetic resonance analytical platforms. The presented data support the conclusions of this paper, but some aspects need to be clarified.

For example, for all animal studies, please list the age and sex of the animals at the time of the experiments. Sex and age are important biological variables that can affect metabolism, and such characteristics are needed when comparing results from different research groups.

In clinical medicine, common ketones that are measured are acetoacetate, beta-hydroxybutyrate, and acetone. However, the data presented here suggest the importance of measuring acetate when patients present with ketoacidosis in uncontrolled diabetes or starvation.

Reviewer #3 (Public Review):

One challenge with this study doing descriptive mosquito and virus work in a remote location is the uncertainly with species identification for both mosquitoes and viruses. It appears that nearly half of the mosquitoes in three of the study sites could not be identified to species. This appears problematic for the estimation of host (mosquito) richness and diversity along the anthropogenic gradient. Viral taxonomy is also complicated and this study is presenting many new viruses which, based on partial or whole sequencing, are putative novel viruses. It is not clear how many of these novel viruses would be accepted by current practices endorsed by the International Committee on Taxonomy of Viruses. The viral taxa uncertainty add complexity for the current analysis. How many of these viral lineages that cluster together are variants of the same virus? How many are unique taxonomic units? This has important consequences on the application of these data to the analyses conducted in this study.

On a related front, many of these viruses the authors are documented are mostly Insect-specific viruses (ISVs). But it also appears that several could be amplified by vertebrate hosts with poorly understood natural history and for the purposes of this study, all of the viral taxa appear to be grouped together. The inclusion of all viruses is therefore somewhat confounding given the very different natural history associated with these viruses. You frequently refer to 'hosts' throughout the MS and for ISVs, the host would likely only be mosquitoes but for arboviruses involving vertebrate amplification hosts, the hosts would be both the mosquitoes and the vertebrates. This study did not quantify any aspect of vertebrate host abundance, diversity, or richness across the gradient. Since most of this study focuses just on the ISVs as a unique system to test the hypotheses, it would be interesting if the authors restricted the analysis to just those viruses with higher probability of being restricted to mosquitoes (e.g. based on phylogenetic placement) to see if the results remain the same.

You report an anthropogenic disturbance gradient from primary forest to village habitat but how was this quantified? How is a village more disturbed than an agricultural field (rice plantation?)? The method to rank these study sites, which becomes important for the analysis, was not described in the methods. Also, along this topic of study sites, it appears you really only had one replicate of each of the study site type. To test these hypotheses on how host communities influence viral communities it would seem prudent to have had multiple replicates of each study area.

Reviewer #3 (Public Review):

This paper investigates the role of the p38g and p38d kinases in the immune response using genetically modified mice that are deficient in p38d and express a kinase-inactive form of p38g. This model avoids the possible confounding effect of the downregulation of the ERK1/2 activator Tpl2, which is observed in mice that are deficient for both p38g and p38d, making it more straightforward to determine the contribution of p38g/p38d to specific phenotypes. The mice that express kinase-inactive p38g and lack p38d show reduced susceptibility to both C. albicans infection and LPS-induced septic shock. Macrophages derived from these mice show dysregulated expression of a number of genes involved in innate immunity. Phospho-proteomics analysis identifies the transcription factor MEF2D as one of the targets of p38g/p38d in macrophages, and in vitro assays show that p38d can phosphorylate several residues of MEF2D including Ser444. Reporter assays provide evidence that a MEF2D-S444A mutant has enhanced transcriptional activity compared with the WT MEF2D, and this is also supported by analyzing the mRNA levels of MEF2D targets in fibroblasts overexpressing both proteins. Taken together, these results support that S444A phosphorylation negatively regulates MEF2D activity.

The manuscript contains a number of interesting observations supporting a role for p38g/p38d in the control of the innate immune response independently of the regulation of the Tpl2-ERK1/2 pathway. It also provides evidence that p38d but not p38g can phosphorylate MEF2D, which inhibits its transcriptional activity, and it is therefore a candidate target for some of the gene expression changes observed. Altogether, the manuscript adds new and exciting information on the functions performed by p38 MAPKs in macrophages and introduces a new mouse model that will be useful for further studies.

Reviewer #3 (Public Review):

This paper enhances our understanding of the evolution of cerebellar size and structure and is a potentially valuable addition to the recent literature on this. The examination of both the correlated evolution and divergent patterns of folding in the cerebellum and cortex may help us to understand what processes are involved and how these relate to the structural organisation at macro- and micro-levels. The study combines careful anatomical measurements based on a curated, publicly available mammalian brain collection, consideration of theoretical explanation of folding patterns, and for the most part a good comparative sample size. However, questions about the sample size arise in the authors' more complex statistical models (see below).

The main issues I have are with the statistical analyses. The authors use a standard phylogenetic approach - Phylogenetic Generalised Least Squares - which is adequate for these questions. I think the authors need to be a bit more cautious in interpreting their results in two respects.

1. The first problem relates to their use of the Ornstein-Uhlenbeck (OU) model: they try fitting three evolutionary models, and conclude that the Ornstein-Uhlenbeck model provides the best fit. However, it has been known for a while that OU models are prone to bias and that the apparent superiority of OU models over Brownian Motion is often an artefact, a problem that increases with smaller sample sizes. (Cooper et al (2016) Biological Journal of the Linnean Society, 2016, 118, 64-77,

2. Second, for the partial correlations (e.g. fig 7) and Principal Components (fig 8) there is a concern about over-fitting: there are 9 variables and only 56 data points (violating the minimal rule of thumb that there should be >10 0bservations per parameter). Added to this, the inclusion of variables lacks a clear theoretical rationale. The high correlations between most variables will be in part because they are to some extent measuring the same things, e.g. the five different measures of cerebellar anatomy which include two measures of folial size. This makes it difficult to separate their effects. I get that the authors are trying to tease apart different aspects of size, but in practice, I think these results (e.g. the presence of negative coefficients in Fig 7) are really hard or impossible to interpret. The partial correlation network looks like a "correlational salad" rather than a theoretically motivated hypothesis test. It isn't clear to me that the PC analyses solve this problem, but it partly depends on the aims of these analyses, which are not made very clear.

The claim of concerted evolution between cortical and cerebellar values (P 11-12) seems to be based on analyses that exclude body size and brain size. It, therefore, seems possible - or even likely - that all these analyses reveal overall size effects that similarly influence the cortex and cerebellum. When the authors state that they performed a second PC analysis with body and brain size removed "to better understand the patterns of neuroanatomical evolution" it isn't clear to me that is what this achieves. A test would be a model something like [cerebellar measure ~ cortical measure + rest of the brain measure], and this would deal with the problem of 'correlation salad' noted below.

It is not quite clear from fig 6a that the result does indeed support isometry between the data sets (predicted 2/3 slope), and no coefficient confidence intervals are provided.

Referencing/discussion/attribution of previous findings<br /> - With respect to the discussion of the relationship between cerebellar architecture and function, and given the emphasis here on correlated evolution with cortex, Ramnani's excellent review paper goes into the issues in considerable detail, which may also help the authors develop their own discussion: Ramnani (2006) The primate cortico-cerebellar system: anatomy and function. Nature Reviews Neuroscience 7, 511-522 (2006<br /> - The result that humans are outliers with a more folded cerebellum than expected is interesting and adds to recent findings highlighting evolutionary changes in the hominin human cerebellum, cerebellar genes, and epigenetics. Whilst Sereno et al (2020) are cited, it would be good to explain that they found that the human cerebellum has 80% of the surface area of the cortex. It would surely also be relevant to highlight some of the molecular work here, such as Harrison & Montgomery (2017). Genetics of Cerebellar and Neocortical Expansion in Anthropoid Primates: A Comparative Approach. Brain Behav Evol. 2017;89(4):274-285. doi: 10.1159/000477432. Epub 2017 (especially since this paper looks at both cerebellar and cortical genes); also Guevara et al (2021) Comparative analysis reveals distinctive epigenetic features of the human cerebellum. PLoS Genet 17(5): e1009506. https://doi.org/10.1371/journal. pgen.1009506. Also relevant here is the complex folding anatomy of the dentate nucleus, which is the largest structure linking cerebellum to cortex: see Sultan et al (2010) The human dentate nucleus: a complex shape untangled. Neuroscience. 2010 Jun 2;167(4):965-8. doi: 10.1016/j.neuroscience.2010.03.007.<br /> - The authors state that results confirm previous findings of a strong relationship between cerebellum and cortex (P 3 and p 16): the earliest reference given is Herculano-Houzel (2010), but this pattern was discovered ten years earlier (Barton & Harvey 2000 Nature 405, 1055-1058. https://doi.org/10.1038/35016580; Fig 1 in Barton 2002 Nature 415, 134-135 (2002). https://doi.org/10.1038/415134a) and elaborated by Whiting & Barton (2003) whose study explored in more detail the relationship between anatomical connections and correlated evolution within the cortico-cerebellar system (this paper is cited later, but only with reference to suggestions about the importance of functions of the cerebellum in the context of conservative structure, which is not its main point). In fact, Herculano-Houzel's analysis, whilst being the first to examine the question in terms of numbers of neurons, was inconclusive on that issue as it did not control for overall size or rest of the brain (A subsequent analysis using her data did, and confirmed the partially correlated evolution - Barton 2012, Philos Trans R Soc Lond B Biol Sci. 367:2097-107. doi: 10.1098/rstb.2012.0112.)

Reviewer #3 (Public Review):

This manuscript provides a high amount of data supporting the author's hypothesis. Serre et al aimed to address the root surface pH and the molecular factors regulating the establishment of the root surface pH pattern important for root growth and gravitropic response. The authors are able to provide solid data on the role of AUX1, AFB1, and CNGC14 in establishing an alkalic patch in the transition zone on the root surface. A weak point in the manuscript is the absence of cellular resolution. The authors mention the technical problems to assess apoplastic pH with previously published tools. They offer Fluorescein106 5-(and-6)-Sulfonic Acid, Trisodium Salt (FS) as an alternative. Even though they were able to generate valuable data with FS, bringing in cellular resolution would increase the quality of the paper even more. Overall, Serre et al provide a solid manuscript with novel data which is of high importance for the field of root and auxin biology.

Reviewer #3 (Public Review):

The comments below focus mainly on ways that the data and analysis as currently present do not to this reviewer compel the conclusions the authors wish to draw. It is possible that further analysis and/or clarification in the presentation would more persuasively bolster the authors' position. It also seems possible that a presentation with more limited conclusions but clarity on exactly what has been demonstrated and where additional future work is needed would make a strong contribution to the literature.

* Fig 3A. It might be worth emphasizing a bit more explicitly that the x-axis (delta S) is the result of a model fit to the data being shown, since this then means that if RNL model fit the data perfectly, all of the thresholds would fall at deltaS = 1. They don't, so I would like to see some evaluation from the authors' experience with this model as to whether they think the deviations (looks like the delta S range is ~0.4 to ~1.6 in Figure 4B) represent important deviations of the data from the model, the non-significant ANOVA notwithstanding. For example, Figure 4B suggests that the sign of the fit deviations is driven by the sign of the UV contrast and that this is systematic, something that would not be picked up by the ANOVA. Quite a bit is made of the deviations below, but that the model doesn't fully account for the data should be brought out here I think. As the authors note elsewhere, deviations of the data from the RNL model indicate that factors other than receptor noise are at play, and reminding the reader of this here at the first point it becomes clear would be helpful.

* Line 217 ff, Figure 4, Supplemental Figure 4). If I'm understanding what the ANOVA is telling us, it is that the deviations of the data across color directions and fish (I think these are the two factors based on line 649) is that the predictions deviate significantly from the data, relative to the inter-fish variability), for the trichromatic models but not the tetrachromatic model. If that's not correct, please interpret this comment to mean that more explanation of the logic of the test would be helpful.

Assuming that the above is right about the nature of the test, then I don't think the fact that the tetrachromatic model has an additional parameter (noise level for the added receptor type) is being taken into account in the model comparison. That is, the trichromatic models are all subsets of the tetrachromatic model, and must necessarily fit the data worse. What we want to know is whether the tetrachromatic model is fitting better because its extra parameter is allowing it to account for measurement noise (overfitting), or whether it is really doing a better job accounting for systematic features of the data. This comparison requires some method of taking the different number of parameters into account, and I don't think the ANOVA is doing that work. If the models being compared were nested linear models, than an F-ratio test could be deployed, but even this doesn't seem like what is being done. And the RNL model is not linear in its parameters, so I don't think that would be the right model comparison test in any case.

Typical model comparison approaches would include a likelihood ratio test, AIC/BIC sorts of comparisons, or a cross-validation approach.

If the authors feel their current method does persuasively handle the model comparison, how it does so needs to be brought out more carefully in the manuscript, since one of the central conclusions of the work hinges at least in part on the appropriateness of such a statistical comparison.

* Also on the general point on conclusions drawn from the model fits, it seems important to note that rejecting a trichromatic version of the RNL model is not the same as rejecting all trichromatic models. For example, a trichromatic model that postulates limiting noise added after a set of opponent transformations will make predictions that are not nested within those of RNL trichromatic models. This point seems particularly important given the systematic failures of even the tetrachromatic version of the RNL model.

* More generally, attempts to decide whether some human observers exhibit tetrachromacy have taught us how hard this is to do. Two issues, beyond the above, are the following. 1) If the properties of a trichromatic visual system vary across the retina, then by imaging stimuli on different parts of the visual field an observer can in principle make tetrachromatic discriminations even though visual system is locally trichromatic at each retinal location. 2) When trying to show that there is no direction in a tetrachromatic receptor space to which the observer is blind, a lot of color directions need to be sampled. Here, 9 directions are studied. Is that enough? How would we know? The following paper may be of interest in this regard: Horiguchi, Hiroshi, Jonathan Winawer, Robert F. Dougherty, and Brian A. Wandell. "Human trichromacy revisited." Proceedings of the National Academy of Sciences 110, no. 3 (2013): E260-E269. Although I'm not suggesting that the authors conduct additional experiments to try to address these points, I do think they need to be discussed.

* Line 277 ff. After reading through the paper several times, I remain unsure about what the authors regard as their compelling evidence that the UV cone has a higher sensitivity or makes an omnibus higher contribution to sensitivity than other cones (as stated in various forms in the title, Lines 37-41, 56-57, 125, 313, 352 and perhaps elsewhere).

At first, I thought they key point was that the receptor noise inferred via the RNL model as slightly lower (0.11) for the UV cone than for the double cones (0.14). And this is the argument made explicitly at line 326 of the discussion. But if this is the argument, what needs to be shown is that the data reject a tetrachromatic version of the RNL model where the noise value of all the cones is locked to be the same (or something similar), with the analysis taking into account the fewer parametric degrees of freedom where the noise parameters are so constrained. That is, a careful model comparison analysis would be needed. Such an analysis is not presented that I see, and I need more convincing that the difference between 0.11 and 0.14 is a real effect driven by the data. Also, I am not sanguine that the parameters of a model that in some systematic ways fails to fit the data should be taken as characterizing properties of the receptors themselves (as sometimes seems to be stated as the conclusion we should draw).

Then, I thought maybe the argument is not that the noise levels differ, but rather that the failures of the model are in the direction of thresholds being under predicted for discriminations that involve UV cone signals. That's what seems to be being argued here at lines 277 ff, and then again at lines 328 ff of the discussion. But then the argument as I read it more detail in both places switches from being about the UV cones per se to being about postive versus negative UV contrast. That's fine, but it's distinct from an argument that favors omnibus enhanced UV sensitivity, since both the UV increments and decrements are conveyed by the UV cone; it's an argument for differential sensitivity for increments versus decrements in UV mediated discriminations. The authors get to this on lines 334 of the discussion, but if the point is an increment/decrement asymmetry the title and many of the terser earlier assertions should be reworked to be consistent with what is shown.

Perhaps the argument with respect to model deviations and UV contrast independent of sign could be elaborated to show more systematically that the way the covariation with the contrasts of the other cone stimulations in the stimulus set goes, the data do favor deviations from the RNL in the direction of enhanced sensitivity to UV cone signals, but if this is the intent I think the authors need to think more about how to present the data in a manner that makes it more compelling than currently, and walk the reader carefully through the argument.

* On this point, if the authors decide to stick with the enhanced UV sensitivity argument in the revision, a bit more care about what is meant by "the UV cone has a comparatively high sensitivity (line 313 and throughout)" needs more unpacking. If it is that these cones have lower inferred noise (in the context of a model that doesn't account for at least some aspects of the data), is this because of properties of the UV cones, or the way that post-receptoral processing handles the signals from these cones mimicking a cone effect in the model. And if it is thought that it is because of properties of the cones, some discussion of what those properties might be would be helpful. As I understand the RNL model, relative numbers of cones of each type are taken into account, so it isn't that. But could it be something as simple as higher photopigment density or larger entrance aperture (thus more quantum catches and higher SNR)?

* Line 288 ff. The fact that the slopes of the psychometric functions differed across color directions is, I think, a failure of the RNL model to describe this aspect of the data, and tells us that a simple summary of what happens for thresholds at delta S = 1 does not generalize across color directions for other performance levels. Since one of the directions where the slope is shallower is the UV direction, this fact would seem to place serious limits on the claim that discrimination in the UV direction is enhanced relative to other directions, but it goes by here without comment along those lines. Some comment here, both about implications for fit of RNL model and about implications for generalizations about efficacy of UV receptor mediated discrimination and UV increment/decrement asymmetries, seems important.

* Line 357 ff. Up until this point, all of the discussion of differences in threshold across stimulus sets has been in terms of sensitivity. Here the authors (correctly) raise the possibility that a difference in "preference" across stimulus sets could drive the difference in thresholds as measured. Although the discussion is interesting and germaine, it does to some extent further undercut the security of conclusions about differential sensitivity across color directions relative to the RNL model predictions, and that should be brought out for the reader here. The authors might also discuss about how a future experiment might differentiate between a preference explanation and a sensitivity explanation of threshold differences.

* RNL model. The paper cites a lot of earlier work that used the RNL model, but I think many readers will not be familiar with it. A bit more descriptive prose would be helpful, and particularly noting that in the full dimensional receptor space, if the limiting noise at the photoreceptors is Gaussian, then the isothreshold contour will be a hyper-ellipsoid with its axes aligned with the receptor directions.

* Use of cone isolating stimuli? For showing that all four cone classes contribute to what the authors call color discrimination, a more direct approach would seem to be to use stimuli that target stimulation of only one class of cone at a time. This might require a modified design in which the distractors and target were shown against a uniform background and approximately matched in their estimated effect on a putative achromatic mechanism. Did the authors consider this approach, and more generally could they discuss what they see as its advantages and disadvantages for future work.

Reviewer #3 (Public Review):

In this manuscript, Mao et al. reported that the two proteases ECS1 and ECS2 participate in both polyspermy block and gamete fusion in Arabidopsis thaliana. The authors could observe polytubey phenotype which has been reported previously and obtain both triparental plants and haploids in ecs1 ecs2 mutants. Therefore they proposed that the triparental plants resulted from the polytubey block defect, whereas the haploids were caused by the gamete fusion defect. Together with two other previous reports, I think it is very interesting to see these two proteases participating in so many different but connected processes. Although they did not provide the molecular mechanism of how ECS participated in polyspermy block and gamete fusion, their findings provide more options for and thus promote plant breeding. The work may have a wide application in the future and will be of broad interest to cell biologists working on gamete fusion and plant breeders. Although most of the conclusions in this paper are well supported by the data, it could be improved with a minor revision including providing clearer data analysis and descriptions, images with higher resolution, and more discussions.

Reviewer #3 (Public Review):

Pentameric ligand-gated ion channels are a class of neurotransmitter receptors playing a key role in cellular communication. Besides their presence in mammalians, a multitude of receptors is found in lower organisms such as bacteria and invertebrates. They display a large diversity of molecular architectures and functions, as exemplified by atypical bacterial channels GLIC, ELIC, STELIC, or DeCLIC that have been characterized at the structural and functional levels. The study of unorthodox receptors, while challenging, is thus fascinating and is expected to give insights into the evolution, as well as the functional and structural divergence occurring in the superfamily.

In this work, authors solve the structure of the orphan receptor Alpo4 from an extreme thermophile worm Alvinella pompejana. Alpo4 is solved in two conformations, Apo and CHAPS-bound, both displaying a closed channel. The structures show several unusual features, in particular in the orthosteric site where, in the Apo, the tryptophan residues at the heart of the site lie in a place usually occupied by the neurotransmitter resembling a "self-liganded" conformation. In addition, the channel is bordered by unusual rings of hydrophobic residues in its upper part, and the protein shows substantial reorganization upon CHAPS binding. Alpo4 was previously investigated by electrophysiology but no agonist was found. Based on the structures, a number of gain-of-function mutants and chimeric constructs have been tested, but unfortunately, none are allowed to observe a ligand-gated ion channel function.

Overall, the paper is written in a very clear and fair manner, presenting the structural architecture and conformational reorganizations but also the limitation of the work concerning the lack of functional identification.

The paper constitutes a substantial amount of work (six cryo-EM structures in total). While it failed to identify an agonist and capture an open-channel conformation, the structure of a member of the family from an extreme thermophile species is novel and interesting for our fundamental knowledge of this important family of receptors.

Reviewer #3 (Public Review):

The paper by Xie et al is a modelling study of the mossy fiber-to-granule cell-to-Purkinje cell network, reporting that the optimal type of representations in the cerebellar granule cell layer depends on the type task. The paper stresses that the findings indicate a higher overall bias towards dense representations than stated in the literature, but it appears the authors have missed parts of the literature that already reported on this. While the modelling and analysis appear mathematically solid, the model is lacking many known constraints of the cerebellar circuitry, which makes the applicability of the findings to the biological counterpart somewhat limited.

I have some concerns with the novelty of the main conclusion, here from the abstract:<br /> 'Here, we generalize theories of cerebellar learning to determine the optimal granule cell representation for tasks beyond random stimulus discrimination, including continuous input-output transformations as required for smooth motor control. We show that for such tasks, the optimal granule cell representation is substantially denser than predicted by classic theories.'<br /> Stated like this, this has in principle already been shown, i.e. for example:<br /> Spanne and Jorntell (2013) Processing of multi-dimensional sensorimotor information in the spinal and cerebellar neuronal circuitry: a new hypothesis. PLoS Comput Biol. 9(3):e1002979.<br /> Indeed, even the 2 DoF arm movement control that is used in the present paper as an application, was used in this previous paper, with similar conclusions with respect to the advantage of continuous input-output transformations and dense coding. Thus, already from the beginning of this paper, the novelty aspect of this paper is questionable. Even the conclusion in the last paragraph of the Introduction: 'We show that, when learning input-output mappings for motor control tasks, the optimal granule cell representation is much denser than predicted by previous analyses.' was in principle already shown by this previous paper.

However, the present paper does add several more specific investigations/characterizations that were not previously explored. Many of the main figures report interesting new model results. However, the model is implemented in a highly generic fashion. Consequently, the model relates better to general neural network theory than to specific interpretations of the function of the cerebellar neuronal circuitry. One good example is the findings reported in Figure 2. These represent an interesting extension to the main conclusion, but they are also partly based on arbitrariness as the type of mossy fiber input described in the random categorization task has not been observed in the mammalian cerebellum under behavior in vivo, whereas in contrast, the type of input for the motor control task does resemble mossy fiber input recorded under behavior (van Kan et al 1993).

The overall conclusion states:<br /> 'Our results....suggest that optimal cerebellar representations are task-dependent.'<br /> This is not a particularly strong or specific conclusion. One could interpret this statement as simply saying: ' if I construct an arbitrary neural network, with arbitrary intrinsic properties in neurons and synapses, I can get outputs that depend on the intensity of the input that I provide to that network.'<br /> Further, the last sentence of the Introduction states: 'More broadly, we show that the sparsity of a neural code has a task-dependent influence on learning...' This is very general and unspecific, and would likely not come as a surprise to anyone interested in the analysis of neural networks. It doesn't pinpoint any specific biological problem but just says that if I change the density of the input to a [generic] network, then the learning will be impacted in one way or another.

The interpretation of the distribution of the mossy fiber inputs to the granule cells, which would have a crucial impact on the results of a study like this, is likely incorrect. First, unlike the papers that the authors cite, there are many studies indicating that there is a topographic organization in the mossy fiber termination, such that mossy fibers from the same inputs, representing similar types of information, are regionally co-localized in the granule cell layer. Hence, there is no support for the model assumption that there is a predominantly random termination of mossy fibers of different origins. This risks invalidating the comparisons that the authors are making, i.e. such as in Figure 3. This is a list of example papers, there are more:<br /> van Kan, Gibson and Houk (1993) Movement-related inputs to intermediate cerebellum of the monkey. Journal of Neurophysiology.<br /> Garwicz et al (1998) Cutaneous receptive fields and topography of mossy fibres and climbing fibres projecting to cat cerebellar C3 zone. The Journal of Physiology.<br /> Brown and Bower (2001) Congruence of mossy fiber and climbing fiber tactile projections in the lateral hemispheres of the rat cerebellum. The Journal of Comparative Neurology.<br /> Na, Sugihara, Shinoda (2019) The entire trajectories of single pontocerebellar axons and their lobular and longitudinal terminal distribution patterns in multiple aldolase C-positive compartments of the rat cerebellar cortex. The Journal of Comparative Neurology.

The nature of the mossy fiber-granule cell recording is also reviewed here:<br /> Gilbert and Miall (2022) How and Why the Cerebellum Recodes Input Signals: An Alternative to Machine Learning. The Neuroscientist<br /> Further, considering the recoding idea, the following paper shows that detailed information, as it is provided by mossy fibers, is transmitted through the granule cells without any evidence of recoding: Jorntell and Ekerot (2006) Journal of Neuroscience; and this paper shows that these granule inputs are powerfully transmitted to the molecular layer even in a decerebrated animal (i.e. where only the ascending sensory pathways remains) Jorntell and Ekerot 2002, Neuron.

I could not find any description of the neuron model used in this paper, so I assume that the neurons are just modelled as linear summators with a threshold (in fact, Figure 5 mentions inhibition, but this appears to be just one big lump inhibition, which basically is an incorrect implementation). In reality, granule cells of course do have specific properties that can impact the input-output transformation, PARTICULARLY with respect to the comparison of sparse versus dense coding, because the low-pass filtering of input that occurs in granule cells (and other neurons) as well as their spike firing stochasticity (Saarinen et al (2008). Stochastic differential equation model for cerebellar granule cell excitability. PLoS Comput. Biol. 4:e1000004) will profoundly complicate these comparisons and make them less straight forward than what is portrayed in this paper. There are also several other factors that would be present in the biological setting but are lacking here, which makes it doubtful how much information in relation to the biological performance that this modelling study provides:<br /> What are the types of activity patterns of the inputs? What are the learning rules? What is the topography? What is the impact of Purkinje cell outputs downstream, as the Purkinje cell output does not have any direct action, it acts on the deep cerebellar nuclear neurons, which in turn act on a complex sensorimotor circuitry to exert their effect, hence predictive coding could only become interpretable after the PC output has been added to the activity in those circuits. Where is the differentiated Golgi cell inhibition?

The problem of these, in my impression, generic, arbitrary settings of the neurons and the network in the model becomes obvious here: 'In contrast to the dense activity in cerebellar granule cells, odor responses in Kenyon cells, the analogs of granule cells in the Drosophila mushroom body, are sparse...' How can this system be interpreted as an analogy to granule cells in the mammalian cerebellum when the model does not address the specifics lined up above? I.e. the 'inductive bias' that the authors speak of, defined as 'the tendency of a network toward learning particular types of input-output mappings', would be highly dependent on the specifics of the network model.

More detailed comments:<br /> Abstract:<br /> 'In these models [Marr-Albus], granule cells form a sparse, combinatorial encoding of diverse sensorimotor inputs. Such sparse representations are optimal for learning to discriminate random stimuli.' Yes, I would agree with the first part, but I contest the second part of this statement. I think what is true for sparse coding is that the learning of random stimuli will be faster, as in a perceptron, but not necessarily better. As the sparsification essentially removes information, it could be argued that the quality of the learning is poorer. So from that perspective, it is not optimal. The authors need to specify from what perspective they consider sparse representations optimal for learning.

Introduction:<br /> 'Indeed, several recent studies have reported dense activity in cerebellar granule cells in response to sensory stimulation or during motor control tasks (Knogler et al., 2017; Wagner et al., 2017; Giovannucci et al., 2017; Badura and De Zeeuw, 2017; Wagner et al., 2019), at odds with classic theories (Marr, 1969; Albus, 1971).' In fact, this was precisely the issue that was addressed already by Jorntell and Ekerot (2006) Journal of Neuroscience. The conclusion was that these actual recordings of granule cells in vivo provided essentially no support for the assumptions in the Marr-Albus theories.

Results:<br /> 1st para: There is no information about how the granule cells are modelled.

2nd para: 'A typical assumption in computational theories of the cerebellar cortex is that inputs are randomly distributed in a high-dimensional space.' Yes, I agree, and this is in fact in conflict with the known topographical organization in the cerebellar cortex (see broader comment above). Mossy fiber inputs coding for closely related inputs are co-localized in the cerebellar cortex. I think for this model to be of interest from the point of view of the mammalian cerebellar cortex, it would need to pay more attention to this organizational feature.

Reviewer #3 (Public Review):

Combining slice physiology and simulation, Combe and colleagues discovered that TRPM4 channels activated by Ca2+ in nanodomains mediate ICAN currents in CA1 pyramidal neurons that drive the cholinergic modulation of firing rate. The finding is novel and interesting.

Strengths:<br /> 1) Identification of TRPM4 channels as the carrier of ICAN currents with independent pharmacological inhibitors and other supporting evidence.<br /> 2) Physiological and simulational verification of physically closely located Ca2+ source and TRPM4 channels required for ICAN activation.

Weaknesses:<br /> 1) The conclusion of the cholinergic role in down-ramp or backward firing shifts is not convincing.

Reviewer #3 (Public Review):

The authors, in their research manuscript, dissected the role of Metformin in bone healing under type-2 diabetics conditions. The authors used three classic bone fracture models to assess the impacts of Metformin in bone healing under hyperglycemic conditions. In all three models, Metformin treatment showed bone formation. At the cellular level, the authors showed the effect of Metformin on promoting bone healing using BMSCs in vitro. The authors in the paper demonstrated that Metformin promotes bone growth only in hyperglycemic conditions. The experiments were appropriately well-defined and carried out to support the role of Metformin in bone healing. The use of three different bone-defective rat models to study the role of Metformin in skeletal tissues is convincing.

Reviewer #3 (Public Review):

Dhekne et al. set out to identify novel activators of the LRRK2 kinase. They developed a flow cytometry assay to separate pools of unmodified and phosphorylated Rab10 (pRab10) from mouse NIH-3T3 cells. They then used this methodology to perform a CRISPR-based genome-wide screen to identify genes responsible for increased pRab10 levels. Candidates were validated with knock-out experiments. As far as we know, LRRK2 is the only kinase that phosphorylates the Switch II motif in Rab10. Therefore, the genes affecting pRab10 levels were classified into positive and negative LRRK2 regulators. Knocking out a positive LRRK2 regulator led to a decrease in pRab10 while knocking out a negative regulator led to an increase in pRab10. The authors found several interesting, previously unknown modulators of LRRK2 activity, including SPTLC2 and CERT1, which are involved in ceramide synthesis.

The major finding of this work is the unexpected effect of Rab12 on pRab10 levels in cells. Knocking out Rab12 resulted in a five-fold decrease in pRab10 levels. This observation was validated in an animal model. Conversely, overexpression of Rab12 led to a ten-fold increase in pRab10 levels. To exclude the possibility that other kinases were responsible for modifying Rab10, the authors overexpressed Rab12 in A549 cells lacking LRRK2; no increase in pRab10 was observed in these cells.

Dhenke et al. then used AlphaFold to model possible interaction between LRRK2 and Rab12 and identified a putative binding site for Rab12 in its Armadillo domain. This is the third Rab binding site in the domain of LRRK2. To validate this interaction, they mutated E240 and S244, both of which are involved in the interface; they observed no changes in pRab10 levels in cells expressing LRRK2 carrying the E240R and S244R mutations. The previously reported site #1 and site #2, both of which also bind Rabs and are involved in feed-forward LRRK2 activation, seem to be unrelated to the binding of Rab12 to site #3. The authors propose that site #3 might open the kinase of LRRK2 to increase its activity.

Finally, the authors point out the important role of Rab12 in lysosomal damage by showing that LLOME- or Nigericin-induced cellular stress increases LRRK2 activity in a Rab12-dependent manner.

Reviewer #3 (Public Review):

In this manuscript Fujino and colleagues used C9-ALS/FTD fly models to demonstrate that FUS modulates the structure of (G4C2) repeat RNA as an RNA chaperone, and regulates RAN translation, resulting in the suppression of neurodegeneration in C9-ALS/FTD. They also confirmed that FUS preferentially binds to and modulates the G-quadruplex structure of (G4C2) repeat RNA, followed by the suppression of RAN translation. The potential significance of these findings is high, since C9ORF72 repeat expansion is the most common genetic cause of ALS/FTD, especially in Caucasian populations and the DPR proteins have been considered the major cause of the neurodegenerations.

1) While the effect of RBP as an RNA chaperone on (G4C2) repeat expansion is supposed to be dose-dependent according to (G4C2)n RNA expression, the first experiment of the screening for RBPs in C9-ALS/FTD flies lacks this concept. It is uncertain if the RBPs of the groups "suppression (weak)" and "no effect" were less or no ability of RNA chaperone or if the expression of the RBP was not sufficient, and if the RBPs of the group "enhancement" exacerbated the toxicity derived from (G4C2)89 RNA or the expression of the RBP was excessive. The optimal dose of any RBPs that bind to (G4C2) repeats may be able to neutralize the toxicity without the reduction of (G4C2)n RNA.

2) In relation to issue 1, the rescue effect of FUS on the fly expressing (G4C2)89 (FUS-4) in Figure 4-figure supplement 1 seems weaker than the other flies expressing both FUS and (G4C2)89 in Figure 1 and Figure 1-figure supplement 2. The expression level of both FUS protein and (G4C2)89 RNA in each line is important from the viewpoint of therapeutic strategy for C9-ALS/FTD.

3) While hallmarks of C9ORF72 are the presence of DPRs and the repeat-containing RNA foci, the loss of function of C9ORF72 is also considered to somehow contribute to neurodegeneration. It is unclear if FUS reduces not only the DPRs but also the protein expression of C9ORF72 itself.

4) In Figure 5E-F, it cannot be distinguished whether FUS binds to GGGGCC repeats or 5' flanking region. Same experiment should be done by using FUS-RRMmut to elucidate whether FUS binding is the major mechanism for this translational control. Authors should show that FUS binding to long GGGGCC repeats is important for RAN translation.

5) It is not possible to conclude, as the authors have, that G-quadruplex-targeting RBPs are generally important for RAN translation (Figure 6), without showing whether RBPs which do not affect to (G4C2)89 RNA levels lead to decreased DPR protein level or RNA foci.

Reviewer #3 (Public Review):

This important work provides convincing evidence that artificial recurrent neural networks can be used to model neural activity during remapping events while an animal is moving along a one-dimensional circular track. This will be of interest to neuroscientists studying the neural dynamics of navigation and memory, as well as the community of researchers seeking to make links between artificial neural networks and the brain.

Low et al. trained artificial recurrent neural networks (RNNs) to keep track of their location during a navigation task and then compared the activity of these model neurons to the firing rates of real neurons recorded while mice performed a similar task. This study shows that a simple set of ingredients, namely, keeping track of spatial location along a one-dimensional circular track, along with storing the memory of a binary variable (representing which of the two spatial maps are currently being used), are enough to obtain model firing rates that reproduce features of real neural recordings during remapping events. This offers both a normative explanation for these neural activity patterns as well as a potential biological implementation.

One advantage of this modeling approach using RNNs is that this gives the authors a complete set of firing rates that can be used to solve the task. This makes analyzing these RNNs easier, and opens the door for analyses that are not always practical with limited neural data. The authors leverage this to study the stable and unstable fixed points of the model. However, in this paper there appear to be a few places where analyses that were performed on the RNNs were not performed on the neural data, missing out on an opportunity to appreciate the similarity, or identify differences and pose challenges for future modeling efforts. For example, in the neural data, what is the distribution of the differences between the true remapping vectors for all position bins and the average remapping vector? What is the dimensionality of the remapping vectors? Do the remapping vectors vary smoothly over position? Do the results based on neural data look similar to the results shown for the RNN models (Figures 2C-E)?

There are many choices that must be made when simulating RNNs and there is a growing awareness that these choices can influence the kinds of solutions RNNs develop. For example, how are the parameters of the RNN initialized? How long is the RNN trained on the task? Are the firing rates encouraged to be small or smoothly varying during training? For the most part these choices are not explored in this paper so I would interpret the authors' results as highlighting a single slice of the solution space while keeping in mind that other potential RNN solutions may exist. For example, the authors note that the RNN and biological data do not appear to solve the 1D navigation and remapping task with the simplest 3-dimensional solution. However, it seems likely that an RNN could also be trained such that it only encodes the task relevant dynamics of this 3-dimensional solution, by training longer or with some regularization on the firing rates. Similarly, a higher-dimensional RNN solution may also be possible and this would likely be necessary to explain the more variable manifold misalignment reported in the experimental data of Low et al. 2021 as opposed to the more tightly aligned distribution for the RNNs in this paper. However, thanks to the modeling work done in this paper, the door has now been opened to these and many other interesting research directions.

Reviewer #3 (Public Review):

Mahlandt et al. report the design and proof of concept of Opto-RhoGEF, a new set of molecular tools to control the activation by light of the three best known members of the Rho GTPase family, RhoA, Rac1 and Cdc42.

The study is based on the optogenetically-controlled activation of chimeric proteins that target to the plasma membrane guanine nucleotide exchange factors (GEFs) domains, which are natural activators specific for each of these three Rho GTPases. Membrane-targeted GEFs encounter and activate endogenous Rho proteins. Further investigation on the effect of these tools on RhoGTPase signaling would have strengthened the report.

These three Opto-RhoGEFs are reversible and enable the precise spatio-temporal control of Rho-regulated processes, such as endothelial barrier function, cell contraction and plasma membrane extension. Hence, these molecular tools will be of broad interest for cell biologists interested in this family of GTPases.

Mahlandt et al. design and characterize three new optogenetic tools to artificially control the activation of the RhoA, Rac1 and Cdc42 by light. These three Rho GTPases are master regulators of the actin cytoskeleton, thereby regulating cell-cell contact stability or actin-mediated contraction and membrane protrusions.

The main strength of this new experimental resource lies in the fact that, to date, few tools controlling Rho activation by reversibly targeting Rho GEFs to the plasma membrane are available. In addition, a comparative analysis of the three Opto-RhoGEFs adds value and further strengthens the results, given the fact that each Opto-GEF produces different (and somehow expected) effects, which suggest specific GTPase activation. The design of the tools is correct, although the membrane targeting could be improved, since the Lck N-terminus used to construct the recombinant proteins contains myristoylation and palmitoylation sites, which has the potential to target the chimeric protein to lipid rafts. As a consequence, this may not evenly translocate these Rho-activating domains.

An additional technical feature that must be highlighted is an elegant method to activate Opto-RhoGEFs in cultured cells, independent of laser and microscopes, by using led strips, which notably expands the possibilities of this resource, potentially allowing biochemical analyses in large numbers of cells.

The experimental evidence clearly indicates that authors have achieved their aim and designed very useful tools. However, they should have taken more advantage of this remarkable technical advance and investigate in further detail the spatiotemporal dynamics of Rho-mediated signaling. Although the manuscript is a "tool and resource", readers may have better grasped the potential benefits of tuning GTPase activity with this tool by learning about some original and quantitative insights of RhoA, Rac1 and Cdc42 function.

One of such insights may have come from the set of data regarding the contribution of adherens junctions. The effect of other endothelial cell-cell junctions, such as tight junctions, may also contribute to barrier function, as well as junctional independent, cell-substratum adhesion. These optogenetic tools will undoubtedly impact on these future studies and help decipher whether these other adhesion events that are important for endothelial barrier integrity are also under control of these three GTPases. Overall, the manuscript is sound and presents new and convincing experimental strategies to apply optogenetics to the field of Rho GTPases.

Reviewer #3 (Public Review):

This paper proposes a computational account for the phenomenon of pattern differentiation (i.e., items having distinct neural representations when they are similar). The computational model relies on a learning mechanism of the nonmonotonic plasticity hypothesis, fast learning rate and inhibitory oscillations. The relatively simple architecture of the model makes its dynamics accessible to the human mind. Furthermore, using similar model parameters, this model produces simulated data consistent with empirical data of pattern differentiation. The authors also provide insightful discussion on the factors contributing to differentiation as opposed to integration. The authors may consider the following to further strengthen this paper:

The model compares different levels of overlap at the hidden layer and reveals that partial overlap seems necessary to lead to differentiation. While I understand this approach from the perspective of modeling, I have concerns about whether this is how the human brain achieves differentiation. Specifically, if we view the hidden layer activation as a conjunctive representation of a pair that is the outcome of encoding, differentiation should precede the formation of the hidden layer activation pattern of the second pair. Instead, the model assumes such pattern already exists before differentiation. Maybe the authors indeed argue that mechanistically differentiation follows initial encoding that does not consider similarity with other memory traces?

Related to the point above, because the simulation setup is different from how differentiation actually occurs, I wonder how valid the prediction of asymmetric reconfiguration of hidden layer connectivity pattern is.

Although as the authors mentioned, there haven't been formal empirical tests of the relationship between learning speed and differentiation/integration, I am also wondering to what degree the prediction of fast learning being necessary for differentiation is consistent with current data. According to Figure 6, the learning rates lead to differentiation in the 2/6 condition achieved differentiation after just one-shot most of the time. On the other hand, For example, Guo et al (2021) showed that humans may need a few blocks of training and test to start showing differentiation.

Related to the point above, the high learning rate prediction also seems to be at odds with the finding that the cortex, which has slow learning (according to the theory of complementary learning systems), also shows differentiation in Wammes et al (2022).

More details about the learning dynamics would be helpful. For example, equation(s) showing how activation, learning rate and the NMPH function work together to change the weight of connections may be added. Without the information, it is unclear how each connection changes its value after each time point.

In the simulation, the NMPH function has two turning points. I wonder if that is necessary. On the right side of the function, strong activation leads to strengthening of the connectivity, which I assume will lead to stronger activation on the next time point. The model has an upper limit of connection strength to prevent connection from strengthening too much. The same idea can be applied to the left side of the function: instead of having two turning points, it can be a linear function such that low activation keeps weakening connection until the lower limit is reached. This way the NMPH function can take a simpler form (e.g., two line-segments if you think the weakening and strengthening take different rates) and may still simulate the data.

Reviewer #3 (Public Review):

Kandola et al. explore the important and difficult question regarding the initiating event that triggers (nucleates) amyloid fibril growth in glutamine-rich domains. The researchers use a fluorescence technique that they developed, dAMFRET, in a yeast system where they can manipulate the expression level over several orders of magnitude, and they can control the length of the polyglutamine domain as well as the insertion of interfering non-glutamine residues. Using flow cytometry, they can interrogate each of these yeast 'reactors' to test for self-assembly, as detected by FRET.

In the introduction, the authors provide a fairly thorough yet succinct review of the relevant literature into the mechanisms of polyglutamine-mediated aggregation over the last two decades. The presentation as well as the illustrations in Figure 1A and 1B are difficult to understand, and unfortunately, there is no clear description of the experimental technique that would allow the reader to connect the hypothetical illustrations to the measurement outcomes. The authors do not explain what the FRET signal specifically indicates or what its intensity is correlated to. FRET measures distance between donor and acceptor, but can it be reliably taken as an indicator of a specific beta-sheet conformation and of amyloid? Does the signal increase with both nucleation and with elongation, and is the signal intensity the same if, e.g., there were 5 aggregates of 10 monomers each versus 50 monomeric nuclei? Is there a reason why the AmFRET signal intensity decreases at longer Q even though the number of cells with positive signal increases? Does the number of positive cells increase with time? The authors state later that 'non-amyloid containing cells lacked AmFRET altogether', but this seems to be a tautology - isn't the lack of AmFRET taken as a proof of lack of amyloid? Overall, a clearer description of the experimental method and what is actually measured (and validation of the quantitative interpretation of the FRET signal) would greatly assist the reader in understanding and interpreting the data.

The authors demonstrate that their assay shows that the fraction of cells with AmFRET signal increases strongly with an increase in polyQ length, with a 'threshold around 50-60 glutamines. This roughly correlates with the Q-length dependence of disease. The experiments in which asparagine or other amino acids are inserted at variable positions in the glutamine repeat are creative and thorough, and the data along with the simulations provide compelling support for the proposed Q zipper model. The experiments shown in Figure 5 are strongly supportive of a model where formation of the beta-sheet nucleus is within a monomer. This is a potentially important result, as there are conflicting data in the literature as to whether the nucleus in polyQ is monomer.

I did not find the argument, that their data shows the Q zipper grows in two dimensions, compelling; there are more direct experimental methods to answer this question. I was also confused by the section that Q zippers poison themselves. It would be easier for the reader to follow if the authors first presented their results without interpretation. The data seem more consistent with an argument that, at high concentrations, non-structured polyQ oligomers form which interfere with elongation into structured amyloid assemblies - but such oligomers would not be zippers.

Although some speculation or hypothesizing is perfectly appropriate in the discussion, overall the authors stretch this beyond what can be supported by the results. A couple of examples: The conclusion that toxicity arises from 'self-poisoned polymer crystals' is not warranted, as there is no relevant data presented in this manuscript. The authors refer to findings 'that kinetically arrested aggregates emerge from the same nucleating event responsible for amyloid formation', but I cannot recall any evidence for this statement in the results section.

Reviewer #3 (Public Review):

The manuscript by Kairouani et al. investigates the function of a small family of plant RNA binding proteins with similarity to the well-studied Musashi protein in animals, and, therefore, called MUSASHI-LIKE1-4 (MSL1-4). Studies on the biological importance of post-transcriptional control of gene expression via RNA-binding proteins in plants are not numerous, and advances in this important field are much needed. The thorough work presented in this manuscript is such an advance.

The central observations of the paper are:

- Knockout of any MSL gene alone does not produce a phenotype.<br /> It is of note that basic characterization of knockout mutations is really well done - for example, the authors have taken care to raise specific antibodies to each of the MSL proteins and use them to demonstrate that each of the T-DNA insertion mutants used actually does knock out protein production from the corresponding gene.

- Knockout of MSL2/4 (but no other double mutant) produces a clear leaf phenotype, and a remarkable stem phenotype in which the mutants collapse as they are unable to support upright growth

- The phenotypes of knockout mutants persist in point mutants defective in RNA-binding, indicating that RNA-binding is required for biological activity. Consistent with this, and associate physically with other RNA-binding proteins and translation factors.

- MSL proteins are cytoplasmic

- The msl2/4 mutants present multiple defects in secondary cell wall composition and structure, probably explaining their inability to grow upright. I did not examine the cell wall analyses in detail as I am no specialist in this field.

- Msl2/4 mutants show transcriptomic changes with at large two big categories of differentially expressed genes compared to wild type.<br /> (1) Genes related to cell wall metabolism<br /> (2) Genes associated with defense against herbivores and pathogens

- Two of the mRNAs encoding cell wall factors with significant upregulation in msl2/4 mutants compared to wild type also associate physically with MSL4 as judged by RNA-immunoprecipitation-RT-PCR assays, and this physical association is abrogated in the RNA-binding deficient MSL4 mutant.

Altogether, the study shows clear biological relevance of the MSL family of RNA-binding proteins, and provides good arguments that the underlying mechanism is control of mRNAs encoding enzymes involved in secondary cell wall metabolism (although concluding on translational control in the abstract is perhaps saying too much - post-transcriptional control will do given the evidence presented). One observation reported in the study makes it vulnerable to alternative interpretation, however, and I think this should be explicitly treated in the discussion:

The fact that immune responses are switched on in msl2/4 mutants could also mean that MSL2/4 have biological functions unrelated to cell wall metabolism in wild type plants, and that cell wall defects arise solely as an indirect effect of immune activation (that is known to involve changes in expression of many cell wall-modifying enzymes and components such as pectin methylesterases, xyloglucan endotransglycosylases, arabinogalactan proteins etc. Indeed, the literature is rich in examples of gene functions that have been misinterpreted on the basis of knockout studies because constitutive defense activation mediated by immune receptors was not taken into account (see for example Lolle et al., 2017, Cell Host & Microbe 21, 518-529).

With the evidence presented here, I am actually close to being convinced that the primary defect of msl2/msl4 mutants is directly related to altered cell wall metabolism, and that defense responses arise as a consequence of that, not the other way round. But I do not think that the reverse scenario can be formally excluded with the evidence at hand, and a discussion listing arguments in favor of the direct effect proposed here would be appropriate. Elements that the authors could consider to include would be the isolation of a cellulose synthase mutant as a constitutive expressor of jasmonic acid responses (cev1) as a clear example that a primary defect in cell wall metabolism can produce defense activation as secondary effect. The interaction of MSL4 with GXM1/3 mRNAs is also helpful to argue for a direct effect, and it would strengthen the argument if more examples of this kind could be included.

Reviewer #3 (Public Review):

The manuscript by Daly et al examines endosomal signaling of the vasopressin type 2 receptors using engineered mini G protein (mG proteins) and a number of novel techniques to address if sustained G protein signaling in the endosomal compartment is enhanced by β arrestin. Employing these interesting techniques they have how V2R could activates Gαs and Gα in the endosomal compartments and how this modulation could occur in arrestin dependent and independent manner. Although the phenomenon of endosomal signaling is complex to address the authors have tried their best to examine these using a number of well controlled set of experiments.

Reviewer #3 (Public Review):

The spindle checkpoint ensures the accuracy of chromosome segregation by sensing unattached kinetochores during mitosis and meiosis and delays the onset of anaphase. Unattached kinetochores catalyze the conformational activation of the latent open MAD2 (O-MAD2) to the active closed MAD2 (C-MAD2). C-MAD2 is then incorporated into the mitotic checkpoint complex (MCC), which inhibits the anaphase-promoting complex or cyclosome (APC/C) to delay anaphase. When all kinetochores are properly unattached, the MAD2-binding protein p31comet and the ATPase TRIP13 extract C-MAD2 from the MCC, leading to MCC disassembly and the conversion of C-MAD2 back to O-MAD2. This action turns off the spindle checkpoint, resulting in APC/C activation and anaphase onset. Cells deficient in p31comet exhibit mitotic delays.

In the current study, Huang et al. have linked p31comet mutations to female infertility. Biallelic loss-of-function alleles of p31comet cause delays in the exiting metaphase of meiosis I and polar body extrusion. The p31comet mutant proteins contain C-terminal truncations and fail to bind to MAD2. Reintroducing full-length p31comet into patient oocytes can bypass the metaphase arrest. Together with a previous study that showed biallelic mutations of TRIP13 caused female infertility, this work established a critical role of the p31comet-TRIP13 module in regulating meiotic progression during oogenesis. As such, this is a significant study.

Reviewer #3 (Public Review):

In this work, Eccleston et. al. use a computational method involving the Rosetta (Flex ddG) suite to infer epistasis in binding free energy changes for combinatorial sets of mutations in the DHFR gene and the drug pyrimethamine. They use this to estimate the most likely path of stepwise mutation accumulation in the evolution of antimalarial drug resistance. The authors also infer likely pathways from different geographical regions from isolated data using a method based on mutation frequencies. They report that these results are broadly consistent with their computational predictions as well.

In contrast to machine learning approaches, the Rosetta Flex ddG method uses physical models at the atomic scale to compute various macromolecular properties. The present paper, therefore, uses atomic-scale molecular properties to make predictions at the population level. As acknowledged by the authors, their method has the limitation that chemical factors other than the free energy changes are largely ignored, as are complications arising from complex population dynamics. Nonetheless, there is reasonable agreement between their predictions and the experimental data, especially at high drug concentrations.

The authors also infer likely trajectories of mutation acquisition from isolate data from various parts of the world. The inference method is based on a simple ranking scheme of mutation frequencies. It is difficult to gauge the reliability of this method, given the complexity of infectious disease dynamics, including confounding factors introduced by varied drug treatment regimens. However, predictions from the computational method are still able to capture some of the general trends in the inferred pathways from isolates, inspiring some confidence in both approaches. The authors emphasize the importance of geographic variation in evolutionary pathways, but their computational method is limited in its ability to provide quantitative insights into the origins of such variation.

A few limitations of the work should be mentioned. It suffers from a lack of summary metrics that quantify the performance of its computational method, which is important for a clearer understanding of its accuracy. While the work is a useful indicator of the potential usefulness of the Rosetta Flex ddG method in enabling evolutionary predictions through macromolecular modeling, the method is applied to a well-studied system and the work remains limited in the novelty of the insights it generates into the dynamics of the evolution of antimalarial drug resistance.

Reviewer #3 (Public Review):

The authors of this study have examined which cation channels specifically confer to ventral tegmental area dopaminergic neurons their autonomic (spontaneous) firing properties. Having brought evidence for the key role played by NALCN and TRPC6 channels therein, the authors aimed at measuring whether these channels play some role in so-called depression-like (but see below) behaviors triggered by chronic exposure to different stressors. Following evidence for a down-regulation of TRPC6 protein expression in ventral tegmental area dopaminergic cells of stressed animals, the authors provide evidence through viral expression protocols for a causal link between such a down-regulation and so-called depression-like behaviors. The main strength of this study lies on a comprehensive bottom-up approach ranging from patch-clamp recordings to behavioral tasks. However, the interpretation of the results gathered from these behavioral tasks might also be considered one main weakness of the abovementioned approach. Thus, the authors make a confusion (widely observed in numerous publications) with regard to the use of paradigms (forced swim test, tail suspension test) initially aimed (and hence validated) at detecting the antidepressant effects of drugs and which by no means provide clues on "depression" in their subjects. Indeed, in their hands, the authors report that stress elicits changes in these tests which are opposed to those theoretically seen after antidepressant medication. However, these results do not imply that these changes reflect "depression" but rather that the individuals under scrutiny simply show different responses from those seen in nonstressed animals. These limits are even more valid in nonstressed animals injected with TRPC6 shRNAs (how can 5-min tests be compared to a complex and chronic pathological state such as depression?). With regard to anxiety, as investigated with the elevated plus-maze and the open field, the data, as reported, do not allow to check the author's interpretation as anxiety indices are either not correctly provided (e.g. absolute open arm data instead of percents of open arm visits without mention of closed arm behaviors) or subjected to possible biases (lack of distinction between central and peripheral components of the apparatus).

Reviewer #3 (Public Review):

In this study, authors used the Drosophila model to characterize molecular details underlying traumatic brain injury (TBI). The authors used the transcriptomic analysis of astrocytes collected by FACS sorting of cells derived from Drosophila heads following brain injury and identified upregulation of multiple genes, such as Pvr receptor, Jun, Fos, and MMP1. Additional studies identified that Pvr positively activates AP-1 transciption factor (TF) complex consisting of Jun and Fos, of which activation leads to the induction of MMP1. Finally, authors found that disruption of endocytosis and endocytotic trafficking facilitates Pvr signaling and subsequently leads to induction of AP-1 and MMP1.

Overall, this study provides important clues to understanding molecular mechanisms underlying TBI. The identified molecules linked to TBI in astrocytes could be potential targets for developing effective therapeutics. The obtained data from transcriptional profiling of astrocytes will be useful for future follow-up studies. The manuscript is well-organized and easy to read. However, I would like to request the authors to address the following issue to improve the quality of their study.

It is unclear why the authors did not explore the involvement of the JNK pathway in their study. While they described the potential involvement of the JNK pathway based on previous literature, they did not include any evidence on the JNK pathway in their own study.

It is important to note that the mechanism by which JNK activates AP-1 is primarily through phosphorylation, not the quantitative control of amounts, as much as I know. This raises questions about the authors' proposed hierarchical relationship between Pvr and AP-1 and the potential involvement of the JNK pathway in mediating this relationship.

Given the significance of the mechanistic link between Pvr and AP-1 in solidifying the authors' conclusion, it would have been beneficial for them to explore the involvement of the JNK pathway in their study, even if only minimally. The lack of such exploration may weaken the overall strength of their findings and the potential implications for understanding TBI.

Reviewer #3 (Public Review):

This work provides new insights into the regulation of the intracellular effector protein Calcineurin B homologous protein 3 (CHP3). The authors precisely delineate how intracellular calcium signals and myristoylation affect the binding of CHP3 to lipid membranes and the sodium/proton exchanger NHE1. Different mechanisms are known to trigger the exposure of the myristoyl-moiety in the calcium-binding protein family and CHP3 was proposed to use a "calcium-myristoyl switch", which leads to exposure of the myristoyl group due to conformational changes in the protein triggered by calcium-binding. Becker and Fuchs et al. now demonstrate that CHP3 uses a novel mechanism, in which not calcium-binding but binding to the target protein NHE1 triggers exposure of its myristoyl-group. This paper represents a detailed functional characterization of CHP3 and the maximum level of mechanistic interpretation that can be achieved without high-resolution structural information.

The conclusions of this paper are fully supported by the data.

Strengths<br /> The protein biochemistry is of an exceptionally high level, both with respect to the quality of the material and the stringency with which the authors assess and assure the protein quality. The authors purify CHP3 without any affinity tags, and thus in its most representative relevant state. Their validations indicate that complete myristoylation of CHP3 is achieved and that all protein is functional with respect to calcium binding.

The authors go to extensive lengths to convince themselves of the quality of their data and their interpretation. They use an extensive amount of replicates, including both biological and technical replicates. Assays and experimental procedures are verified using model proteins, such as Recoverin. In addition, the authors employ an extensive set of complementary approaches to assure their observations are universal.

Weaknesses<br /> A small weakness is the fact that the interpretation in terms of mechanistic insights contributed by some of the assays employed is rather limited, resulting in comparably unprecise descriptions of the state of the protein such as "affects the conformation and/or flexibility of CHP3" or the "open" and "closed" conformations. As indicated by the authors, structural studies are required to precisely detail the conformational states and delineate their mechanism of action.

The authors imply that the major form of CHP3 is the myristoylated state. However, it remains unclear whether the source of the biological material, which appears to be membrane-only, already implies a significant experimental bias that only allows (or highly favors) the identification of myristoylated CHP3. Without a calcium-signal, unmyristoylated CHP may not associate with membranes, or be less strong, resulting in its depletion upon isolation of the vesicles.

Reviewer #3 (Public Review):

The authors present a study of 13000, Salmonella Typhi genomes from across the globe. Here, they present an overview of the global genomic epidemiology of Salmonella Typhi, in the context of the evolution of antimicrobial resistance. The authors present the temporal trends in the prevalence of Salmonella Typhi genotypes in select regions/ countries as well as the prevalence and antimicrobial resistance. The authors cite travel isolates of Salmonella Typhi as a useful proxy for surveillance in high burden settings where there exists a paucity of genomic data. While the authors acknowledge the limitations of their study, there remain major concerns over sampling bias and representativeness that question the generalizability of their findings.

Based on the methods section, the authors did not make mention of adjusting their prevalence estimates for outbreak investigations. When conducting a population analysis, including outbreak samples can lead to an overestimation of the prevalence of the outbreak strain. First, outbreaks tend to be sampled more densely than isolates from routine surveillance of endemic disease, secondly in an outbreak, you are essentially sampling the same strain multiple times. This needs to be taken into consideration when estimating the prevalence of genotypes in the population. Treating outbreak investigations and routine surveillance equally in calculating prevalence can be misleading if the proportion of outbreak isolates sequenced is greater than the proportion of isolates in the surveillance area that are sequenced.

There are concerns regarding the validity of the results presented in Figures 1-3. These results require a nuanced assessment of the factors that are likely to influence genotypic diversity including type of study, duration of sampling and total number of genomes sequenced. In big Countries like Nigeria and India, where can be heterogeneity in different regions of the country and this needs to also be considered in inferring the prevalence of genotypes.

This heterogeneity in prevalence of genotypes was observed in countries with multiple laboratories. In India for example, the prevalence of lineage 4.3.1.2 ranged from 39% to 82%, in different cities/ regions. The authors have not provided sufficient context on the underlying source of this variation in prevalence. In order to understand the reason for observing these differences there needs to be a discussion around when the samples in each place/ region were conducted, how long the study was conducted, how many isolates were collected and whether this was a routine surveillance, outbreak investigation or other type of study. Similar variability is observed in Nigeria where most isolates were from Abuja (Zankli Medical Center, n=105, 2010-2013) and other sources included Ibadan (University of Ibadan, n=14, 2017-2018), and reference laboratories in England (n=15, 2015-2019) and the USA (n=10, 2016-2019). Given the small sample sizes and the fact that the time periods for sample collection varied, using this dataset to get a snapshot of the prevalence of genotypes in Nigeria can be potentially misleading.

Moreover, the authors cite that 70% of cases in Pakistan are caused by XDR. Is this based on the proportions of isolates that are XDR in this dataset? Klemm et al 2018 sequenced primarily XDR isolates, therefore that dataset is not representative of the wider population. Rasheed et al included on 27 genomes, which were isolated at hospitals. Hospitals isolates may give an overestimated XDR burden because susceptible isolates are likely to get treated successfully with antibiotics alleviating the need for hospitalization. Similarly, Yousafzai et al 2019 was an investigation into an outbreak of ceftriaxone-resistant Salmonella Typhi in Hyderabad, which is a densely sample dataset and not necessarily a representation of the wider population. Aggregating these data may lead to an accumulation of bias that gives a distorted snap shot of the diversity on genotypes. Also, it is unclear whether the number of isolates collected from each of these studies was consistent with time. Thus, changes in the prevalence may be representative of a change in the proportion of genomes that were sampled from individual studies.

One of the major recommendations from this study was that travel associated isolates can be a proxy for surveillance in high burden regions where there is paucity of data. The authors have not demonstrated a rigorous test for representativeness of the travel associated samples. The test conducted by the authors looked at how well the travel isolates correlated with the isolates from other studies conducted in the source population. However, they have not factored in potential biases associated with the studies conducted in the host countries. Also, travel is more likely to encompass a specific socio-economic demography of people who can afford to travel. This leads to underrepresentation of low income individuals and communities, especially in low-income countries. Moreover, the authors have not shown that the phylogenetic placement of the travel isolates supports the claim that they originated from that country. Conclusions drawn from travel associated isolates need to be tempered, while it can be a useful tool for early detection of potentially virulent lineages or lineages that have novel resistance mechanisms, using it to determine prevalence can be misleading.

Other minor observations include:

Introduction needs to trim significantly to be more concise. The authors can demonstrate that Salmonella typhi accumulates resistance genotypes over time and as new antibiotics are introduced resistance mutations become selected for and fixed in the population.

Figure 4 is very similar to Figure 1 of Klemm et al 2018, does not add any new insights.