Author Response:

Evaluation Summary

Challa and Ryu et al. systematically evaluated various combinations of ADP-ribose-binding modules to make sensors detecting poly(ADP-ribose). They developed and tested two indicator designs optimized for analyses in cell culture (dimerization-dependent GFP-based) or intact tissues (split Nano luciferase-based). Overall, with further experimental controls and quantification, this timely set of cell biology probes will be useful to study the biological functions of ADP-ribosylation in cultured cells and whole organisms.

We appreciate the positive and encouraging words from the reviewer. We also appreciate the helpful comments, criticisms, and suggestions, which we have endeavored to address fully.

Reviewer 1 (Public Review):

While these tools are more sensitive than existing tools, it is unclear whether a dynamic range of 6-fold (GFP) and 3-fold (luciferase) provide sufficient sensitivity for properly understanding the PAR dynamics (which was thought to increase as much as 100-fold in DNA damage settings). In addition, it is unclear whether the fold increases in both fluorescence and luminescence linearly correlate with the traditional measures by western blot.

We are pleased that the reviewer found our sensors to potentially useful. The reviewer provided a number of excellent comments and suggestions that have served as a useful guide for improving our paper. We have carefully considered all of the comments, insights, and suggestions from the reviewer and revised the manuscript accordingly. We think this has strengthened our conclusions and improved the paper considerably. We thank the reviewer for the careful and thorough review of our paper.

Figure 1F indicates on the western blot that there was a precipitous drop of PARylation after 5 min, but the GFP signal indicated a linear drop. It will be important to quantify the signals on western blots and test how correlate their data with the GFP/luciferase data in scatter plots for their various sets of data. Would this system under-estimate the changes and be not sensitive enough to subtle changes that may be 1-2 fold measured by traditional means

We agree with the reviewer that a comparison with existing PAR detection technologies will improve the manuscript. We now performed a comparative analysis of ELISA, Western blot, and immunofluorescence assays with live cell imaging using PAR-T GFP (Figures 6A, 6C, 6D). The results indicate that the detection range of PAR-T ddGFP is comparable to the established PAR detection assays. In addition, we also compared the live cell luciferase assays using PAR-T NanoLuc to Western blotting (Figure 6B) and found that these two assays are able to detect PAR changes at comparable levels. We would also like to emphasize that these sensors were developed to improve our ability to detect PAR changes in living cells and animals, which the existing techniques are not capable of doing.

Similarly, how is their quantitation in Figure 2 compared with traditional immunofluorescence?

We performed this comparison and observed that the changes in PAR levels as detected by live cell imaging using PAR-T ddGFP are comparable to the changes detected in immunofluorescence assays using the WWE-Fc reagent (Figure 6D and 6E).

Lastly, for the luciferase signal in Figure 3B and C, the corresponding signal in western blots are missing. Therefore, it is difficult to estimate the background signal. If Niraparib, as in other figures, eliminates PAR signals on western blot, these data would indicate half of the basal signal are background, which is rather high. Having said that, tool development is an evolution process. These tools will provide a good foundation for future development. Therefore, understanding these limitations (dynamic range, quantitative sensitivity correlation, and background) will provide a better assessment of the utility of these new tools for investigating PAR biology.

We appreciate the reviewer’s concern about the high background signal in Niraparibtreated samples. To answer this concern, we compared the dynamic range of PAR-T NanoLuc to Western blotting (Figure 6B) and found that the results from live cell luciferase assays using PAR-T NanoLuc are comparable to Western blotting using WWE-Fc. Of note, we were able to detect decreases in PAR levels with Niraparib using live cell luciferase assays using PAR-T NanoLuc, but not Western blotting. Based on these analyses, we can conclude that the changes in PAR levels at the basal level are very minimal, leading to only 50% decrease in PAR-T NanoLuc signal with Niraparib treatment (Figure 6B, Figure 5A-5C). Note that the decrease in PAR-T NanoLuc signal is greater when UV-treated cells were pre-treated with Niraparib, which is consistent with the results from Western blot analysis (Figure 5A).

Reviewer 2 (Public Review):

In this study, the authors attempted to extend their own work and that of others in the field in developing probes to detect the signaling molecule, poly-ADPribose (PAR) that can be used in the test tube, in cells and in tumor models. Major strengths include the development of a set of probes with data demonstrating utility and efficacy. Further, the authors show the assay to be useful in cell models and tumor models. Some weaknesses include what appears to be a high level of background in the assay. Further, regarding methods, the exact probes (sequences) being evaluated are not defined. This is one of several new PAR probes being developed over the last few years but may have widespread utility due to the quantitative nature of the bioluminescent assay.

We thank the reviewer for these thoughtful and encouraging comments, as well as the interesting, thought-provoking, and constructive criticisms that have prompted us to dig deeper and provide more evidence to support our claims

Reviewer 3 (Public review):

The major drawback is that, while the authors demonstrated some applications of these PAR trackers (PAR-T) in both culture cells and in animals, the data of PAR-T ddGFP on cancer cells and the data of PAR-T Nano luciferase may not be sufficient to support the authors' claim that the new tool can detect spatial and temporal dynamics of PAR in cells and in animals. That said, the new tools can potentially expand the capability of cell biologists to visualize and study the PAR production process in both normal and disease states with improved sensitivity and tissue compatibility.

We thank the reviewer for appreciating the potential utility of the PAR-T sensors, as well as the detailed and constructive criticisms that have prompted us to provide more evidence to support our claims. Addressing these comments has helped us to improve the paper.

One of the major issues of this manuscript is the lack of time-course data for PAR-T luminescent sensors to demonstrate temporal monitoring of PAR levels in animals. If the binding of two split Nano Luciferase parts is irreversible, the application might be limited. However, according to the literature (Scientific Reports volume 11, Article number: 12535 (2021)), the split Nanoluc technology should be able to detect dynamic changes. Either way, a set of time-course data would be necessary. The authors need to provide evidence to support their statement "The high sensitivity and low signal to noise ratios of the PAR-Trackers described here enable spatial and temporal monitoring of PAR levels in cells and in animals.

We agree with the reviewer’s comment that the original manuscript did not demonstrate that the PAR-T sensors can be used to detect spatio-temporal changes in PAR. To demonstrate that PAR-T NanoLuc can be used to detect time-dependent changes in PAR levels, we performed a time course of UV-mediated PARP-1 activation (Figure 5D). The results from this assay demonstrated that the dynamic changes in PAR in live cells, in response to DNA damage, can be recaptured using the PAR-T NanoLuc sensors. In addition, we also measured PARGi-mediated PAR accumulation in vivo in xenograft tumors (Figure 8 - figure supplement 1B-1D). We found that PAR can be detected readily in breast cancer cells when injected into mice. Upon treatment with PARGi, the luminescence from PAR-T NanoLuc increased significantly by 6 hours and then diminished by 24 hours. These data demonstrate that PAR-T NanoLuc can be used to track dynamic changes in PAR levels both in cells and in animals. While not in vivo, our work with spheroids also addresses this concern. See our response to the next comment below.

Figure 2- figure supplement 2. For the detection of spatial dynamics of PAR signals in cancer spheroids, the authors did not provide sufficient evidence as only static images of different spheroids in different conditions were provided. And 2 out of 3 fields of view only include one spheroid. In addition, there is no time-course image data showing the spatial patterns of PAR in cancer cells are dynamic.

We have now performed a quantitative analysis of multiple spheroids. As indicated in Figure 3B, we observed a significantly higher GFP fluorescence signal in spheroids derived Challa et al. (Kraus) – Rebuttal February 2, 2022 10 from PAR-T ddGFP expressing cells compared to those expressing ddGFP or those treated with Niraparib. To address the reviewer’s concern about using PAR-T ddGFP for spatio-temporal changes in cells, we included a video for live cell imaging of H2O2-mediated increase in PAR-T ddGFP (Figure 2 - figure supplement 2, video). We also developed an analysis approach that allows us to quantify the signals from the core of the spheroids separately from the periphery of the spheroids. We also performed a time course in 3D cancer spheroids to visualize the spatio-temporal changes in PAR levels (Figure 3C and 3D). The results from this experiment demonstrate that the PAR levels in cells at the core of the spheroids are relatively resistant to Niraparib treatment, as the PAR levels in cells at the core of the spheroid decrease at a lower rate when compared to PAR in the cells at the outer layer of the spheroid.

In the caption of Figure 2 -figure supplement 1 (B and C), it states "Immunofluorescence assay to track PAR formation in response to H2O2.", but there is no evidence showing any antibodies were used there.

We thank the reviewer for pointing out this error. It should have been written as live cell imaging, not immunofluorescence assay. We made this correction.

It seems that Figure 3 B and C does not support the statement "we observed specific detection of firefly luciferase with D-Luciferin and NanoLuc with furimazine with no cross-reactivity" And it is unclear why the authors refer Fig. 3B and C after that statement as those data seems not supporting this claim. Similarly, the statement "Moreover, the luminescence of PAR-T Luc is only 30-fold lower than intact firefly luciferase." Was not supported by Fig. 3B. In fact, the differences between PAR-T Luc and intact firefly luciferase were ~1000 fold in vivo, judging from Fig 5B. It is also unclear which data of the construct was used to plot Fig. 3C.

We thank the reviewer for this comment. We changed the scale bar to represent the true scale for the luminescence from Nano luciferase and Firefly luciferase. This indicates that the brightness of PAR-T NanoLuc is 30-fold lower than intact firefly luciferase. In Figure 3C, we plotted the ratio of PAR-T NanoLuc to firefly luciferase.

Fig. 4C, it seems that Firefly luciferase was consistently brighter with PARGi, and I wonder if such difference is statistically significant. The authors did not perform a twoway ANOVA test for the firefly luciferase dataset.

We included the statistics to indicate that these changes were not significant.

The statement "Moreover, none of these sensors can detect PAR accumulation in vivo." seems to lack support. Have the authors proved that with evidence? I would recommend using the following statement instead: "Moreover, none of these sensors has yet demonstrated detection of PAR accumulation in vivo

We made this change.

For the in vivo experiment, it is unclear about the benefits of normalizing the PAR-T radiance to the Firefly luciferase since the signals from Firefly luciferase did not overlap well with that from the PAR-T nano luciferase, which may cause bigger variations.

We thank the reviewer for raising this point. We normalize the luminescence from PAR-T NanoLuc to that from firefly luciferase to account for the variability in tumor size between the mice. We think this is an important control in the analysis. The luminescence from firefly luciferase represents the differences in tumor size between the mice. Hence, that signal is greater than the signal from PAR-T NanoLuc and is spread over a larger area.

Judging from the data of Fig 3 supplement 1E, the signal intensity from the split firefly luciferase-based PAR-T sensors was ~10000 fold less than intact firefly luciferase, not ~1000 fold. It makes more sense to give up the split firefly luciferase for ~10000 fold differences since the signal intensity from the split nano luciferase was ~1000 fold less than intact firefly luciferase (Fig 5B).

We noted the reviewers concern about the split firefly luciferase PAR-T. We agree with the reviewer that the split nano luciferase is brighter than the split firefly luciferase (Figure 4C and Figure 4 - figure supplement 1E). Although split nano luciferase is 1000-fold dimmer than the intact firefly luciferase in vivo (Figure 8B and Figure 8 - figure supplement 1A), this difference is only 30-fold in in vitro assays (Figure 4C). Hence, the comparison of sensors based on split firefly luciferase to split nano luciferase highlights our efforts to make a brighter sensor. Moreover, we included the split firefly luciferase data to compare the performance of WWE vs macrodomain in the development of the PAR-T NanoLuc sensor. Since firefly luciferase is frequently used for sensor development, we believe that it is important to include the results obtained from this sensor.

Therefore, developing tools to measure ADPR dynamics in cells and in vivo is critical for better understating the various biological processes mediated by ADPR". "understating" should be "understanding".

We corrected this error.

Author Response:

Reviewer #1:

A number of metabolic traits show differences between reciprocal crosses of inbred mouse strains. These can be conceptualized as parent-of-origin effects. Differential expression (DE) at an unimprinted locus can be a pleiotropic side-effect of allele-specific expression (ASE) at an imprinted locus. There is no parent-of-origin effect at the unimprinted locus, in the sense that there would be no change in expression at this locus if the parental origin of the two alleles were reversed while keeping parental origin of alleles at the imprinted locus unchanged. Sexual recombination will have the effect of randomizing alleles at the unimprinted locus relative to alleles at the imprinted locus.

Expression of the imprinted gene Nnat and unimprinted gene F2r were correlated in the author's analyses of reproductive fat pads from their mice and their interaction was predictive of basal glucose levels. In a single-celled analysis, using an existing database, expression of the paternally-expressed imprinted gene Nnat increases and expression of the unimprinted gene F2r decreases along an adipogenic trajectory in preadipocytes.

One reason why small mammals, such as mice, socialize is to keep warm. Within a huddle or nest, heat generation consumes individual substrates for a communal benefit and this can create selection for imprinted expression when members of groups are asymmetric kin. This conflict has been discussed in the context of the effects of imprinted genes on brown adipocytes that use UCP1 to 'uncouple' oxidative phosphorylation in mitochondria (see Current Biology 18: R172). A UCP1-independent mechanism of non-shivering thermogenesis in skeletal muscle, and beige adipocytes (see Frontiers in Endocrinology 11: 498, involves 'uncoupling' of the SERCA channel that is regulated by Nnat. The role of Nnat is SERCA-dependent thermogenesis is yet to be established.

This is an interesting hypothesis, and one that extends our hypothesis by suggesting that Nnat alters beige thermogenesis, which would alter basal glucose levels. The primary effect would be adipogenic and the secondary effect could be thermogenic, both resulting in altered glucose levels. This would be very interesting to follow-up on in subcutaneous adipose which has been shown to beige in mice. We have added to the text in the discussion.

Reviewer #2:

The authors conducted experiments to examine whether non-imprinted genes interacted with imprinted genes, explored gene pairs that may affect phenotype, and identified two genes, Nnat and Cdkn1c that may initiate parent-of-origin effects. A major strength is the testing of these predictions in a new cohort by manipulating phenotype by diet.

I focus my review on the design. My major concern is the nature of the group assignment to diet, which would require different statistical analysis.

"At three weeks of age, animals were weaned into same-sex cages and randomly placed on high fat (42% kcal from fat; Teklad TD88137) or low-fat (15% kcal from fat; Research Diets D12284) isocaloric diets" - To be sure I and readers can understand, were the animals first placed into same-sex cages, then the cage was randomly assigned to a diet? If so, the unit of analysis is the cage, and results need to be analyzed as though the animals are not independent within cages. This does not currently seem to be the case, and the analyses not valid.

We thank the reviewer for the comment and we have added detail to the methods for clarity. The animals in each cage for each generation represent animals from different litters. The experimental unit of analysis is the individual animal: for the RNAseq studies one animal from each cage was randomly selected for sequencing in the F1 population. For the F2 animals, animals that were randomly placed into a cage and diet were not genetically identical. Specific details are described in the methods.

• Please describe how many animals were housed per cage and how many cages there were for each diet.

These details have been added to the methods.

• Please describe the method of randomization.

We used a random number generator in R, and have included this detail in the text.

To fully assess the methods and facilitate reproducibility, additional information is needed to describe items as recommended by the ARRIVE guidelines (https://arriveguidelines.org/sites/arrive/files/documents/ARRIVE%20guidelines%202.0%20-%20English.pdf). This includes: the number of animals represented in each experiment/figure (this is not clear throughout the text); the sex of animals used in each experiment; whether order of measurements or animal/cage positioning were randomized (or if not); whether any blinding was performed; housing conditions if available (e.g., room temperature and humidity, light/dark cycle), additional details about diet (whether ad lib, water quality), whether any animals were excluded from analysis after being assigned to a diet; cage type and bedding.

We have added these details to conform to the ARRIVE guidelines as suggested.

Reviewer #3:

Macias-Velasco et al. aimed to demonstrate that non-imprinted genes could generate parent-of-origin effects on metabolic traits, such as glucose concentrations, through interactions with imprinted genes. They used four populations at different levels of intercrossing of inbred mice, and by doing so were able to demonstrate that non-imprinted genes interact with imprinted genes and by doing so impact the animal's phenotype. They focused on two genes in particular, Nnat, and F2r, in high fat-fed female mice as the covariation of these two genes associated with basal glucose concentrations and the relationship. They provided a biological validation of this relationship by demonstrating it consistently across multiple generations. Interactions between imprinted and non-imprinted genes have been previously demonstrated, but the present study took it one step further to identify one possibly reason as to why there is such a prevalence of parent-of-origin effects by detailing the interactions of ASE and DE genes and how that interaction leads to a specific phenotype. The genes the authors identified appear to play a role in adipogenesis. The results may allow for better prediction of an individual's phenotype based on their genome.

The authors conducted a lot of work, and provided a lot of data for the reader, but the paper can be strengthened by the following:

In the results the authors refer to females on a high-fat diet. It would be useful for the reader to put this in a bigger context and explain the implication of diet. It was unclear whether the figures represented sexes combined, and if so, it would have been useful to show the results in males, even if they were null. The authors demonstrated that Nnat expression covaries with F2r in high fat-fed females, yet used available scRNAseq data collected from C57BL/6J epididymal adipose tissue to examine which cell types express these two genes and whether the negative correlation persisted across an adipogenic trajectory (which it did). In mice, the visceral fat pads in the perigonadal region are known as epididymal in males and periovarian in females. Although it was not implicitly stated that these cells were from males, it is presumed by the name of the fat pad. The authors should address possible limitations and considerations related to sex differences, and possibly even strain differences in these comparisons.

The clarity of the methods and materials needs to be improved. Specifically, to allow for others to reproduce the data and to provide greater transparency, in addition to following the eLife guidelines. The authors should follow the ARRIVE guidelines and cite this in the manuscript. With the multiple populations of mice used, it would make it easier on the reader if the sample size and sex were more clearly outlined. Although the authors state that the mice were randomly placed on high-fat or low-fat diet, how the animals were randomized was not outlined. Another possible consideration would be to include a figure outlining the study design, including sample size/sex for the various populations and components of the study. Also, please identify why the sample size was decided, and whether there were any inclusion/exclusion criteria.

We thank the reviewer for the comments and have modified the text for clarity.

Author Response:

Reviewer #1:

While the implications are compelling, a few other controls and analyses would better establish the link between arousal level and the TRR.

First, it is difficult to link changes in task difficulty to arousal level without demonstrating that the subjects did not change their strategy between easy and difficult task conditions by, for example, looking directly at the more difficult targets instead of maintaining central fixation as the task required. Without this control, the changes reported in TRRs could be attributed to changes in eye movements and the concomitant changes in the the visual field, especially given measurements were made in visual cortex.

We have analyzed observers’ eye movements to rule out this possibility. Please see the new section of the results: “An eye-movement-evoked artifact could not account for task-related fMRI responses."

In the same vein, a more detailed or explicit differentiation between the stimulus or attention-evoked hemodynamic response and the TRR is necessary to help the reader evaluate the TRR without simultaneous eye tracking to remove trials where the visual field may have changed.

Please see the new section of the supplement titled “Stimulus-evoked activity during the localizer” and the new supplementary figures S4 and S5.

Given arousal is a loosely defined cognitive phenomenon, physiologic arousal markers (ex. pupil, heart rate, respiration) are commonly used to track changes in arousal level, as is the case in this work. The evidence in this work that arousal level changed between task conditions (ex. difficult and easy trials) requires a more detailed analysis to control for the large number of variables and determine the effects that survive. While an accompanying data set showed changes in pupil diameter in a manner consistent with arousal changes during the task, this data was recorded in a separate experiment. This does provide a source of eye movement data for potential control analysis.

We have eye data from the pupillometry recordings outside the scanner. We have reanalyzed these data, comparing the variance in eye position between conditions. We did not find any statistically significant differences in this measure of fixation stability between conditions.

If the widespread BOLD responses were luminance-evoked, i.e., caused by eye movements changing the pattern of retinal stimulation, we would have expected to observe the strongest responses in V1 at eccentricities close to the representation of the screen edge. To test this hypothesis, we analyzed the BOLD signal amplitude across the representation of the visual field, but did not observe larger response amplitudes in the cortical locations corresponding to the edge of the screen.

Lastly, the authors speculate about the origin of the TRR by comparing its magnitude and modulation in different task conditions across different levels of the visual cortical hierarchy (V1 vs. V2 vs V3). A direct statistical comparison of these effects would be necessary to convincingly demonstrate differences in the TRR across visual regions.

We have performed this comparison and reported the results.

Reviewer #2:

The discussion suggests that this relates to a LC-NE arousal process. The connection is suggested by the data, but further work would be needed to cement this idea. The data are interesting, and a good window into further understanding of this effect.

In the discussion line 330, they suggest that the TRR should be separately modeled and removed from fMRI data in preprocessing. While the authors have convinced this reader that the TRR is likely related to arousal, it is far from clear that this means that this effect should be removed from fMRI data in preprocessing. Many arousal effects exist naturally in fMRI data, and in brain activity in general. Many arousal effects are observable in spiking and LFPs. Since no spiking or LFPs were measured here, we don't know whether this signal is or is not related to spiking or LFPs (though some data from monkeys suggests a similar signal is hemodynamic only, it would take more convincing that the current TRRs arise from the same process as the previously reported primate literature).

Agreed. We do not suggest that the TRR should be removed from fMRI data in all or even most scenarios. It can be removed if one has a specific reason to do so, e.g. separating a mixture of stimulus-evoked and task-related responses. We have revised our statement on this to clarify.

Reviewer #3:

However, a weakness of the paper is that the authors do not pursue the computational/functional significance, nor the biological drivers, of TRRs. For instance, linking TRRs to an explicit model of decision-making (beyond showing they covary with RTs and lapses), or further discussing their potential link to widespread arousal and movement variables in rodent calcium imaging and ephys data, would strongly increase the interest from those beyond the visual fMRI community.

We have now discussed how our findings relate to a relevant computational model that links arousal and decision-making. And we have discussed how merging linear modeling of the TRR with computational models of decision-making may be a fruitful future direction for research. We have also discussed the possible links to widespread arousal-related cortical responses observed in rodent calcium imaging and ephys data.

Author Response:

JMML is a rare pediatric leukemia, emanating from mutations in the RAS pathway. One of the most frequent genetic causes are loss of function mutations in PTPN11. Using genetically-engineered zebrafish, the investigators show that a chronic inflammatory state is present.

Comments:

1. A mouse model for Noonan Syndrome with overlap with JMML, PTPN11 D61G , displays myeloproliferative, cardiac, and craniofacial disease. Here, the zebrafish ptpn11 D61G displayed a wide penetrance depending on allelic burden.

2. The hematopoietic effects in the affected fish involve the myeloid compartment. There appears to be no zebrafish ortholog for GM-CSF, and instead the author look at effects of Gcsf. They note enhanced GM colony formation -- but Gcsf should not promote macrophage development. In addition, the effect in human is that of spontaneous growth of CFU-GM. The authors would need to address the differences with human JMML malignant hematopoiesis.

3. The use of MEK or PI3K inhibitors do not themselves implicate proinflammatory response (line 273). These agents are not anti-inflammatory but have a wide range of effects. They are as much anti-proliferative. To demonstrate inhibition of proinflammatory response would require true anti-inflammatory agents. Dexamethasone targets lymphocytes, and may also reduced cytokine release by macrophages in fish. Controls should include genes that are biomarkers for inflammation (i.e., not l-plastin or c-myb).

We have rephrased the text to make sure we did not unintentionally suggest that MEK or PI3K inhibitors are anti-inflammatory agents. We used MEK and PI3K inhibitors, because these are known to inhibit signaling downstream of SHP2. As anti-inflammatory agent, we used dexamethasone, which rescued many of the observed blood defects in Shp2-D61G mutant zebrafish embryos. We observed a rescue of the number of c-myb and l-plastin expressing cells (read-out for HSPCs). We have done additional experiments and assessed that the increase in the number of neutrophils and macrophages was largely rescued by dexamethasone, showing that dexamethasone targets the myeloid lineage. Moreover, dexamethasone rescued the inflammatory response in Shp2- D61G expressing embryos as assessed by expression of the inflammatory response genes, tnfa, gcsfb and il1b (new Fig. 6D-G). Based on these data, we conclude that the inflammatory response in Shp2- D61G mutant zebrafish embryos may have a causal role in the pathogenesis of the NS/JMML-like MPN blood phenotype.

Reviewer #3:

The authors of this paper model the D61G mutation in zebrafish, creating a model consistent with the human Noonan syndrome, which is predisposed to a JMML and MPN like syndrome. They use RNA-seq to identify the potential cellular abnormalities in either the HSPC or monocyte/macrophage clusters, which nominates an inflammatory signature as being pathogenic. They complement this with analysis of human JMML patients, showing a similar inflammatory signature.

The study nicely provides a new model that can be used as the basis of future studies in the field. Because the mutant variably displays phenotypes along a spectrum from NS to MPN, different researchers can choose to focus on this as they see fit. Where the manuscript falls short is in more clearly delineating the defect in HSPC vs. monocyte/macrophages (especially in comparing fish to human) and at least a hint of the involved mechanisms.

In fish and human, we are analyzing RNA expression in HSPCs, consisting of HSC- like cells and early progenitors, but not fully differentiated monocytes and/or macrophages. We have used the single cell sequencing dataset of zebrafish HSPCs to determine when pro-inflammatory gene expression was evoked. We used Monocle trajectory inference analysis and found that differentiation started in HSC-like cells and progressed in two directions in pseudotime, towards monocyte/macrophage progenitors in one direction and towards thrombocyte and erythrocyte progenitors in the other direction. The analysis showed that proinflammatory genes are evoked during early differentiation of monocyte/macrophage progenitor cells specifically in the Shp2D61G mutants. We have included this analysis in the new panels C-E in Fig. 4 and Fig.4 – figure supplement 1 of the revised version of the manuscript and accompanying textual changes in the Results section.

Author Response:

Reviewer #1:

In this study, Barrasso et. al., investigate the previously reported positive association between the commensal P. aminovorans and V. cholerae in the human gut during infection. The authors find that P. aminovorans and V. cholerae interact in vitro to form a dual-biofilm. Using a suckling mouse model of infection, the authors also demonstrate that V. cholerae gut colonization is enhanced in the presence of P. aminovorans, and that this colonization enhancement depends on the ability of V. cholerae to produce biofilm exopolysaccharide and biofilm proteins. Overall, the experiments are well-performed and the findings are interesting. My major comment is that the authors should perform some further analysis to demonstrate a definitive causal relationship between the abundance of P. aminovorans and V. cholerae colonization, which would help to strengthen their conclusions.

1) The authors find a positive correlation between the abundance of P. aminovorans and V. cholerae infection by the observation that 6 of 22 infected individuals harbored detectable levels of P. aminovorans in rectal swabs, compared to only 2 of the 36 uninfected individuals (Figure 1). The authors then go on to demonstrate that there is an increase in the colonization of V. cholerae (CFU) in the presence of P. aminovorans in the suckling mouse model on infection (Figure 2B and Figure 2C). The author's conclusions would be strengthened by demonstrating a positive association between the presence of P. aminovorans and the abundance of V. cholerae in the human samples (from Figure 1). The authors demonstrate that the presence of P. aminovorans is associated with the number of people infected with V. cholerae, but not that the presence of P. aminovorans also leads to higher levels of V. cholerae in the 6 of infected individuals harboring detectable levels of P. aminovorans, compared to the infected individuals that did not. This additional analysis would help to solidify the authors conclusions that the presence of P. aminovorans enhances the colonization of V. cholerae during infection.

In the prior study in which the association between P. aminovorans and V. cholerae infection was first noted (Midani F et al, JID,, July13;218[4] :645-653), among the 4,181 different operational taxonomic units ([OTU], a taxonomic grouping based roughly on species-level identification) identified in the stool of persons infected with V. cholerae, Pa was among the top 5 OTUs found to be most abundant during infection in a machine learning analysis. This analytic method provided additional resolution about the correlative relationships between gut microbes and clinical outcomes beyond that of community structure-based analyses (Midani 2018). We have added new Supplementary File 1 which contains the full data (raw and normalized abundance) with counts in persons with and without Pa found in the stool from the Midani 2018 study. Total bacterial counts in the stool of each group did not differ, and the average Vc OTUs were higher in the group with Pa in the stool; however, this difference was not statistically significant (Supplemental File 1), which may have been due to an underpowered comparison. The wide range of Vc abundance in the human samples reflects the cross-sectional nature of this human data in that study participants are likely to be at different stages of colonization or infection at the time of sampling (compared to mice who are sampled at the same time since infection). The limitations of V. cholerae stool culture for diagnosis of infection are evident in Supplemental File 1, in which 16S detection of Vc and culture positivity were discordant in some samples (see column 3, Vc infection determination, in Supplemental File 1, all previously published data). Notably, stool culture is the gold standard for diagnosing V. cholerae infection. Rationale and additional information about these classifications and the machine learning analysis methods are included in the prior manuscript (Midani 2018). In summary, we feel that our human data from the prior study are not of sufficient in sample size to fully resolve the question asked by the reviewer, and we have added the statistical testing of Vc counts in Pa- infected and Pa-uninfected humans in our results section and to Supplemental File 1. We have also included these results in the revised manuscript. We have also included the raw and normalized abundances data in Supplementary File 1.

2) It's surprising that the relative abundance Proteobacteria does not change much after the introduction of >10^6 CFU of P. aminovorans, which would be expected to represent a significant proportion of the abundance of the total bacteria in the small intestine (Supplemental Figure 1). It would be important for the authors to determine whether the addition of P. aminovorans and not the displacement of other members of the Proteobacteria Phylum leads to the increased V. cholerae CFU in Figure 2B and Figure 2C.

To show with more resolution the impact of Pa on the gut microbiota of the mouse we have added a Panel C to Figure 2-figure supplement 1 Panel C (original Supplemental Figure 1) showing order-level abundance data within the Proteobacteria phylum (to which Pa belongs). Differences in the two groups were not found to be significant with FDR-adjusted significance testing at multiple taxonomic levels. As in humans, it may be the case that a small amount of Pa is sufficient to impact Vc colonization, and it could be that only small amounts of Pa remain after inoculation.

3) Expression analysis should be performed to determine whether there is an increase in virulence factor expression in V. cholerae in the presence of P. aminovorans. This important given that previous studies have demonstrated that biofilm growth leads to the upregulation of V. cholerae virulence factors, which may enhance colonization.

We have added new Figure 7-figure supplement 1 showing the qRT-PCR results for measuring the relative transcript levels of ctxA and tcpA in Vc monoculture and Vc-Pa co-culture under two different culture conditions. First, we compared virulence gene expression under the AKI growth conditions (Iwanaga et al, Microbiology and immunology, 30(11), 1075–1083) because El Tor biotype Vc does not express virulence genes optimally under standard lab growth conditions (DiRita et al, PNAS, 93(15):7991-5). Under the AKI conditions, we observed a slight increase of the transcript levels of tcpA, but not ctxA, in Vc cocultured with Pa. It should be noted that, in addition to the use of a special medium, a biphasic growth (static growth followed by shaking for extended period) is needed for inducing virulence gene expression in AKI. We reasoned that such growth conditions did not allow Vc to interact sufficiently with Pa to form a robust biofilm, likely preventing a strong induction of virulence gene expression in the AKI coculture.

We also measured virulence gene expression in regular LB medium under static growth conditions (similar to the conditions used to grow the coculture biofilms). As discussed above, we noted that under these growth conditions the relative transcript levels of these virulence genes are low (e.g., compared to the relative transcript levels of vpsL), suggesting this is not an ideal condition for virulence gene expression comparison in mono- and co-culture. Nonetheless, we found that ctxA and tcpA transcript levels are slightly higher in the static LB coculture (although only ctxA comparison is statistically significant).

Reviewer #3:

The presence of the organism Paracoccus aminovorans in stool was previously shown to correlate with susceptibility of humans to infection with V. cholerae and to enhance agglutination and growth of V. cholerae. In this manuscript, the authors use a neonatal mouse model as well as in vitro models to demonstrate that the association between Paracoccus aminovorans and V. cholerae occurs in a VPS-dependent biofilm and enhances colonization of the neonatal mouse intestine.

The strengths of this manuscript:

1) Examination of P. aminovorans-V. cholerae interaction in the small intestine of the neonatal mouse model. V. cholerae colonizes the terminal ileum yet most of the human microbiota studies examine stool, which is unlikely to be representative of the terminal ileum. In addition, adult models of infection such as the gnotobiotic or antibiotic-treated mouse display colonic but not true ileal colonization. Furthermore, this colonization is not dependent on the V. cholerae toxin co-regulated pilus, which is necessary for human infection. In fact, flow in the colon is slow enough to allow growth without true attachment to the surface. This may explain why, as the authors note, the diarrhea of cholera clears most of the microbiota from wtool samples. Therefore, stool exiting the colon and the adult mouse are not ideal for studying the interaction between the microbiota and V. cholerae during infection. By using the neonatal mouse, the authors choose a host compartment that is relevant to human disease. The findings of the authors that P. aminovorans improves V. cholerae colonization of the small intestine are very convincing.

2) Use of microscopy to detail the distribution of the two organisms in culture. Imaging clearly demonstrates subdomains of the biofilm that contain mixtures of P. aminovorans and V. cholerae.

The weaknesses of this manuscript:

1) Specific markers for VPS exopolysaccharide and P. aminovorans are not used: The authors conclude that V. cholerae increases VPS synthesis in response to P. aminovorans based on increased WGA staining in regions of biofilms where P. aminovorans is concentrated. One concern is that WGA is not a specific marker for VPS. It adheres to GlcNAC residues, which could also be present in an extracellular polysaccharide synthesized by P. aminovorans.

In response to the reviewer’s question, we added negative controls (new Figure 4-figure supplement 1) showing that Pa cells along or Vc ΔvpsL mutant does not show WGA staining. While it is true that WGA stains GlcNAC residues, for Gram-negative bacterial cells including Vc and Pa, the WGA lectin molecules do not pass through the outer membrane. Only when the outer membrane is significantly impaired will one see strong WGA signal. Indeed, we always observe dead cells with strong WGA signal but those are easily distinguished from the VPS signal. We have updated Figure 6A-B accordingly to better show the local distribution of VPS.

Furthermore, the authors image biofilms that include neon-green-expressing V. cholerae and unlabeled P. aminovorans by staining with FM4-64. Regions of the biofilm with predominantly FM4-64 staining are presumed to have greater numbers of P. aminovorans. This is more convincing because the shape of these cells is coccoid as might be expected for P. aminovorans. However, this is not a feature that provides specificity. Because the authors also indicate that these clusters of Pa are surrounded by V. cholerae¬-synthesized VPS, it is important to definitively identify these cells as Pa.

We thank the reviewer for raising this point. In the new Figure 6A-B, we have provided clearer zoomed-in images in which Pa cells can be clearly distinguished from Vc cells by BOTH the absence of SCFP3A signal AND the characteristic cocci shape.

2) There is no examination of activation of VPS synthesis or other virulence factors at the transcriptional level. The authors conclude that VPS synthesis is activated by WGA staining but do not provide additional data to show whether this activation occurs at the transcriptional or post-transcriptional level. If transcription activation of vps genes were observed, this would bolster the WGA staining result.

In response to the reviewer’s request, we have obtained a strain harboring Pvpsl-mNeonGreen and we have repeated the pellicle imaging in the updated Figure 6C-D. Interestingly, subpopulations of Vc cells have elevated vpsL expression when co-cultured with Pa. In addition, we have performed qRT-PCR experiments to show that indeed the relative transcript levels of vpsL is higher in the co-culture (Figure 5).

Author Response:

Reviewer #1:

The paper uses a microfluidic-based method of cell volume measurement to examine single cell volume dynamics during cell spreading and osmotic shocks. The paper successfully shows that the cell volume is largely maintained during cell spreading, but small volume changes depend on the rate of cell deformation during spreading, and cell ionic homeostasis. Specifically, the major conclusion that there is a mechano-osmotic coupling between cell shape and cell osmotic regulation, I think, is correct. Moreover, the observation that fast deforming cell has a larger volume change is informative.

The authors examined a large number of conditions and variables. It's a paper rich in data and general insights. The detailed mathematical model, and specific conclusions regarding the roles of ion channels and cytoskeleton, I believe, could be improved with further considerations.

We thank the referee for the nice comment on our work and for the detailed suggestions for improving it.

Major points of consideration are below.

1) It would be very helpful if there is a discussion or validation of the FXm method accuracy. During spreading, the cell volume change is at most 10%. Is the method sufficiently accurate to consider 5-10% change? Some discussion about this would be useful for the reader.

This is an important point and we are sorry if it was not made clear in our initial manuscript. We have now made it more clear in the text (p. 4 and Figure S1E and S1F).

The important point is that the absolute accuracy of the volume measure is indeed in the 5 to 10% range, but the relative precision (repeated measures on the same cell) is much higher, rather in the 1% range, as detailed below based on experimental measures.

1) Accuracy of absolute volume measurements. The accuracy of the absolute measure of the volume depends on several parameters which can vary from one experiment to the other: the exact height of the chamber, and the biological variability form one batch of cell to another (we found that the distribution of volumes in a population of cultured cells depends strongly on the details of the culture – seeding density, substrate, etc... - which we normalized as much as possible to reduce this variability, as described in previous articles, e.g. see2). To estimate this variability overall, the simplest is to compare the average volume of the cell population in different experiments, carried out in different chambers and on different days.

Graph showing the initial average volume of cells +/- STD for 7 spreading experiments and 27 osmotic shock experiments, expressed as a % deviation from the average volume over all the experiments.

The average deviation is of 10.9 +/- 8%

2) Precision of relative volume measurements. When the same cell is imaged several times in a time-lapse experiment, as it is spreading on a substrate, or as it is swelling or shrinking during an osmotic shock, most of the variability occurring from one experiment to another does not apply. To experimentally assess the precision of the measure, we performed high time resolution (one image every 30 ms) volume measurements of 44 spread cells during 9 s. During this period of time, the volume of the cell should not change significantly, thus giving the precision of the measure.

Graph showing the coefficient of variation of the volume (STD/mean) for each individual cell (n=44) across the almost 300 frames of the movie. This shows that on average the precision of volume measurements for the same cell is 0.97±0.21%. In addition, if more precision was needed, averaging several consecutive measures can further reduce the noise, a method which is very commonly used but that we did not have to apply to our dataset.

We have included these results in the revised manuscript, since they might help the reader to estimate what can be obtained from this method of volume measurement. We also point the reviewer to previous research articles using this method and showing both population averages and time-lapse data2–8 . Another validation of our volume measurement method comes from the relative volume changes in response to osmotic shock (Ponder’s relation) measured with FXm, which gave results very similar to the numbers of previously published studies. We actually performed these experiments to validate our method, since the results are not novel.

2) The role of cell active contraction (myosin dynamics) is completely neglected. The membrane tether tension results, LatA and Y-compound results all indicate that there is a large influence of myosin contraction during cell spreading. I think most would not be surprised by this. But the model has no contribution from cortical/cytoskeletal active stress. The authors are correct that the osmotic pressure is much larger than hydraulic pressure, which is related to active contraction. But near steady state volume, the osmotic pressure difference must be equal to hydraulic pressure difference, as demanded by thermodynamics. Therefore, near equilibrium they must be close to each other in magnitude. During cell spreading, water dynamics is near equilibrium (given the magnitude of volume change), and therefore is it conceptually correct to neglect myosin active contraction? BTW, 1 solute model does not imply equal osmolarity between cytoplasm and external media. 1 solute model with active contraction was considered before, e.g., ref. 17 and Tao, et al, Biophys. J. 2015, and the steady state solution gives hydraulic pressure difference equal to osmotic pressure difference.

This is an excellent point raised by the referee. We have two types of answers for this. First an answer from an experimental point of view, which shows that acto-myosin contractility does not seem to play a direct role in the control of the cell volume, at least in the cells we used here. Based on these results we then propose a theoretical reason why this is the case. It contrasts with the view proposed in the articles mentioned by the referee for a reason which is not coming from the physical principles, with which we fully agree, but from the actual numbers, available in the literature, of the amount of the various types of osmolytes inside the cell. We give these points in more details below and we hope they will convince the referee. We also now mention them explicitly in the main text of the article (p. 6-7, Figure S3F) and in the Supplementary file with the model.

A. Experimental results

To test the effect of acto-myosin contraction on cell volume, we performed two experiments:

1) We measured the volume of same cell before and after treatment with the Rho kinase ROCK inhibitor Y-27632, which decreases cortical contractility. The experiment was performed on cells plated on poly-L-Lysin (PLL), like osmotic shock experiments, a substrate on which cells adhere, allowing the change of solution, but do not spread and remain rounded. This allowed us to evaluate the effect of the drug. Cells were plated on PLL-coated glass. The change of medium itself (with control medium) induced a change of volume of less than 2%, similar to control osmotic shock experiments (maybe due to shear stress). When the cells were treated with Y-27, the change of volume was similar to the change with the control medium (now commented in the text p. 6-7, Figure S3F). To make the analysis more complete, we distinguished the cells that remained round throughout the experiment from the cells which slightly spread, since spreading could have an effect on volume. Indeed we observed that treatment with Y-27 induced more cells to spread (Figure S3F), probably because the cortex was less tensed, allowing the adhesive forces on PLL to induce more spreading9. Nevertheless, the spreading remained rather slow and the volume change of cells treated or not with Y-27 was not significantly different. This shows that, in the absence of fast spreading induced by Y-27, the reduction of contractility per se does not have any effect on the cell volume.

Graphs showing proportion of cells that spread during the experiments (left); average relative volume of round (middle) and spread (right) control (N=3, n=77) and Y-27 treated cells (N=4, N=297).

2) To evaluate the impact of a reduction of contractility in the total absence of adhesion, we measured the average volume of control cells versus cells which have been pretreated with Y-27, plated on a non-adhesive substrate (PLL-PEG treatment). This experiment showed that the volume of the cells evolved similarly in time for both conditions, proving that contractility per se has no effect on the cell volume or cell growth, in the absence of spreading.

Graphs showing average relative volume of control (N=5, n=354) and Y-27 (N=3, n=292) treated cells plated on PLL-PEG (left); distributions of initial volume for control (middle) and Y-27 treated cells (right) represented on the left graph.

Taken together these results show that inhibition of contractility per se does not significantly affect cell volume. It thus confirms our interpretation of our results on cell spreading that reduction of contractility has an effect on cell volume, specifically in the context of cell spreading, primarily because it affects the spreading speed.

B. Theoretical interpretation

In accordance with our experiments, in our model, the effect of contractility is implicitly included in the model because it modulates the spreading dynamics, which is an input to the model, i.e. through the parameters tau_a and A_0.

We do not include the effect of contractility directly in the water transport equation because our quantitative estimates support that the contribution of the hydrostatic pressure to the volume (or the volume change) is negligible in comparison to the osmotic pressure, and this even for small variation near the steady-state volume. The main important point is that the concentration of ions inside the cell is actually much lower than outside of the cell10,11. The difference is about 100 mM and corresponds mostly to nonionic small trapped osmolytes, such as metabolites12. The osmotic pressure corresponding to this is about 10^5 Pa. Taking the cortical tension to be of order of 1 mN/m and cell size to be about ten microns we get a hydrostatic pressure difference of about 100 Pa due to cortical tension. A significant change in cell volume, of the order observed during cell spreading (let’s consider a ten percent decrease) will increase the osmotic pressure of the trapped nonionic osmolytes by 10^4 Pa (their number in the cell remaining identical). For this osmotic pressure to be balanced by an increase in the hydrostatic pressure, the cortical tension would need to increase by a factor of 100, which we consider to be unrealistic. Therefore, we find it reasonable to ignore the contribution of the hydrostatic pressure difference in the water flux equation. It is also consistent with the novel experiments presented above which show that inhibition of cortical contractility changes the cells volume below what can be detected by our measures (thus likely at maximum in the 1% range). This is now explained in the main text and Supplementary file.

Regarding our minimal model required to define cell volume, the reason why we believe one solute model is not sufficient is fundamentally the same as above: the concentration of trapped osmolytes is comparable to the total osmolarity, which means that their contribution to the total osmotic pressure cannot be discarded. Secondly, within the simplest one solute model, the pump and leak dynamics fixes in inner osmolytes concentration but does not involve the actual cell size. The most natural term that depends on the size is the Laplace pressure (inversely proportional to the cell size in a spherical cell model). But as discussed above, this term may only permit osmotic pressure differences of the order of 100 Pa, corresponding to an osmolytes concentration difference of the order of 0.1 mM. That is only a tiny fraction of the external medium osmolarity, which is about 300 mM. Such a model could thus only work for extremely fine tuning of the pump and leak rates to values with less than about 1% variation. Furthermore, such a model could not explain finite volume changes upon osmotic shocks without involving huge (100-fold) cell surface tension variations, as discussed above. For these reasons, we believe that the one-solute model is not appropriate to describe our experiments, and we feel that a trapped population of nonionic osmolytes is needed to balance the osmolarity difference created by the solute pump and leak.

In the revised version of the manuscript, we have now added a section in Supplementary file and in the main text, explaining in more detail this approximation.

3) The authors considered the role of Na, K, and Cl in the model, and used pharmacological inhibitors of NHE exchanger. I think this part of the experiments and model are somewhat weak. I am not sure the conclusions drawn are robust. First there are many ion channels/pumps in regulating Na, K and Cl. The most important of which is NaK exchanger. NHE also involves H, and this is not in the model. The ion flux expressions in the model are also problematic. The authors correctly includes voltage and concentration dependences, but used a constant active term S_i in SM eq. 3 for active pumping. I am not sure this is correct. Ion pump fluxes have been studied and proposed expressions based on experimental data exist. A study of Na, K, Cl dynamics, and membrane voltage on cell volume dynamics was published in Yellen et al, Biophys. J. 2018. In that paper, they used different expressions based on previously proposed flux expressions. It might be correct that in small concentration differences, their expressions can be linearized or approximated to achieve similar expressions as here. But this point should be considered more carefully.

We thank the reviewer for this comment. Indeed, we have not well justified our use of the NHE inhibitor EIPA. Our aim was not to directly affect the major ion pumps involved in volume regulation (which would indeed rather be the Na+/K+ exchanger), because that would likely strongly impact the initial volume of the cell and not only the volume response to spreading, making the interpretation more difficult. We based our choice on previous publication, e.g.13, showing that EIPA inhibited the main fast volume changes previously reported for cultured cells: it was shown to inhibit volume loss in spreading cells, as well as mitotic cell swelling14,15. Using EIPA, we also found that, while the initial volume was only slightly affected, the volume loss was completely abolished even in fast spreading cells (Y-27 and EIPA combined treatment, Figure S5H). This clearly proves that the volume loss behavior can be abolished, without changing the speed of spreading, which was our main aim with this experiment.

The most direct effect of inhibiting NHE exchangers is to change the cell pH16,17, which, given the low number of H protons in the cell (negligible contribution to cells osmotic pressure), cannot affect the cell volume directly. A well-studied mechanism through which proton transport can have indirect effect on cell volume is through the effect of pH on ion transporters or due to the coupling between NHE and HCO3/Cl exchanger. The latter case is well studied in the literature18. In brief, the flux of proton out of the cell through the NHE due to Na gradient leads to an outflux of HC03 and an influx of Cl. The change in Cl concentration will have an effect on the osmolarity and cell volume.

We thus performed hyperosmotic shocks with this drug and we found that, as expected, it had no effect on the immediate volume change (the Ponder’s relation), but affected the rate of volume recovery (combined with cell growth). Overall, the cells treated with EIPA showed a faster volume increase, which is what is expected if active pumping rate is reduced. This is in contrast with the above mentioned mechanism of volume regulation which will to lead to a reduced volume recovery of EIPA treated cells. This leads us to conclude that there is potentially another effect of NHE perturbation. Changing the pH will have a large impact on the functioning of many other processes, in particular, it can have an effect on ion transport16. Overall, the cells treated with EIPA showed a faster volume increase, which is what is expected if active pumping rate is reduced.

On the model side, the referee correctly points out that there are many ion transporters that are known to play a role in volume regulation which are not included in Eq. 3. In the revised manuscript we now start with a more general ion transport equation. We show that the main equation (Eq.1 - or Supplementary file Eq.13) relating volume change to tension is not affected by this generalization. This is because we consider only the linear relation between the small changes in volume and tension. We note that the generic description of the PML (Supplementary file Eqs.1-6) can be seen as general and does not require the pump and channel rates to be constant; both \Lambda_i and S_i can be a function of potential and ion concentration along with membrane tension. It is only later in the analysis that we do make the assumption that these parameters only depend on tension. This point is now made clear in the Supplementary file.

There is a huge body of work both theoretical and experimental in which the effect of different ion transporters on cell volume is analyzed. The aim of this work is not to provide an analysis of cell volume and the effect of various co-transporters but is rather limited to understanding the coupling between cell spreading, surface tension and cell volume.

To analytically estimate the sign of the mechano-osmotic coupling parameter alpha we use a minimal model. For this we indeed take the pumps and channels to be constant. As it is again a perturbative expansion around the steady state concentration, electric potential, and volume, the expression of alpha can be easily computed for a model with more general ion transporters. This generalization will come at the cost of additional parameters in the alpha expression. We decided to keep the simpler transport model, the goal of this estimate is merely to show that the sign of alpha is not a given and depends on relative values of parameters. Even for the simple model we present, the sign of alpha could be changed by varying parameters within reasonable ranges.

Given these points, and the clarification of the reasons to use EIPA in our experiments, a full mechanistic explanation of the effect of this drug is beyond the scope of this work. Because of this we are not analyzing the effect of EIPA on the model parameter alpha in detail. We now clarified our interpretation of these results in the main text of the article.

Reviewer #2:

The work by Venkova et al. addresses the role of plasma membrane tension in cell volume regulation. The authors study how different processes that exert mechanical stress on cells affect cell volume regulation, including cell spreading, cell confinement and osmotic shock experiments. They use live cell imaging, FXm (cell volume) and AFM measurements and perform a comparative approach using different cell lines. As a key result the authors find that volume regulation is associated with cell spreading rate rather than absolute spreading area. Pharmacological assays further identified Arp2/3 and NHE1 as molecular regulators of volume loss during cell spreading. The authors present a modified mechano-osmotic pump and leak model (PLM) based on the assumption of a mechanosensitive regulation of ion flux that controls cell volume.

This work presents interesting data and theoretical modelling that contribute new insight into the mechanisms of cell volume regulation.

We thank the referee for the nice comments on our work. We really appreciate the effort (s)he made to help us improve our article, including the careful inspection of the figures. We think our work is much improved thanks to his/her input.

Reviewer #3:

The study by Venkova and co-workers studies the coupling between cell volume and the osmotic balance of the cell. Of course, a lot of work as already been done on this subject, but the main specific contribution of this work is to study the fast dynamics of volume changes after several types of perturbations (osmotic shocks, cell spreading, and cell compression). The combination of volume dynamics at very high time resolution, and the robust fits obtained from an adapted Pump and Leak Model (PLM) makes the article a step-forward in our understanding of how cell volume is regulated during cell deformations. The authors clearly show that:

-The rate at which cell deforms directly impacts the volume change

-Below a certain deformation rate (either by cell spreading or external compression), the cells adapt fast enough not to change their volume. The plot dV/dt vs dA/dt shows a clear proportionality relation.

-The theoretical description of volume change dynamics with the extended PLM makes the overall conclusions very solid.

Overall the paper is very well written, contains an impressive amount of quantitative data, comparing several cell types and physiological and artificial conditions.

We thank the referee for the positive comment on our work.

My main concern about this study is related to the role of membrane tension. In the PLM model, the coupling of cell osmosis to cell deformation is made through the membrane-tension dependent activity of ion channels. While the role of ion channels is extensively tested, it brings some surprising results. Moreover, the tension is measured only at fixed time points, and the comparison to theoretical predictions is not always as convincing as expected: when comparing fig 6I and 6J, I see that predictions shows that EIPA (+ or - Y27), CK-666 (+ or - Y27) and Y27 alone should have lower tension than in the control conditions, and this is clearly not the case in fig 6J. But I would not like to emphasize too much on those discrepancies, as the drugs in the real case must have broad effects that may not be directly comparable to the theory.

We apologize for the mislabeling of the Figure 6I (now Figure 5I). This plot shows the theoretical estimate for the difference in tension (in the units of homeostatic tension) between the case when the cell loses its volume upon spreading (as observed in experiments) compared to the hypothetical situation when the cell does not lose volume upon spreading (alpha = 0). The positive value of the tension difference predicts that the cell tension would have been higher if the cell were not losing volume upon spreading, which is the case for the treatments with EIPA and CK-666 (+ Y27) and corresponds to what we found experimentally.

It thus matches our experimental observations for drug treatments which reduce or abolish the volume loss during spreading and correspond to higher tether force only at short time.

We have corrected the figure and figure legend and explained it better in the text.

But I wonder if the authors would have a better time showing that the dynamics of tension are as predicted by theory in the first place, as comparing theoretical predictions with experiments using drugs with pleiotropic effects may be hazardous.

Actually, a recent publication (https://doi.org/10.1101/2021.01.22.427801) shows that tension follows volume changes during osmotic shocks, and overall find the same dynamics of volume changes than in this manuscript. I am thus wondering if the authors could use the same technique than describe in this paper (FLIM of flipper probe) in order to study the dynamics of tension in their system, or at least refer to this paper in order to support their claim that tension is the coupling factor between volume and deformation.

As was suggested by the referee, we tried to use the FLIPPER probe. We first tried to reproduce osmotic shock experiments adding to the HeLa cells 4% of PEG400 (+~200 mOsm) or 50% of H20 (-~170 mOsm) and measuring the average probe lifetime before and after the shock. We found significantly lower probe lifetime for hyperosmotic condition compared with control, and non-significant, but slightly higher lifetime for hypoosmotic shock. The magnitude of lifetime changes was comparable with the study cited by the reviewer, but the quality of our measures did not allow us to have a better resolution. Next we measured average lifetime for control and CK-666+Y-27 treated cells 30 min and 3 h after plating, because we have highest tether force values for CK-666+Y-27 at 30 min. We did not see a change in lifetime in control cells between 30 min and 3 h (which also did not see with the tether pulling). Cells treated with CK-666+Y-27 showed a slightly lower lifetime values than control cells, but both 30 min and 3 h after plating, which means that it did not correspond to the transient effect of fast spreading but probably rather to the effect of the drugs on the measure.

Graph showing FLIPPER lifetime before and after osmotic shock for HeLa cells plated on PLL- coated substrate. Left: control (N=3, n=119) and hyperosmotic shock (N=3, n=115); Right: control (N=3, n=101) and hypoosmotic shock (N=3, n=80). p-value are obtained by t-test.

Graph showing FLIPPER lifetime for control just after the plating on PLL-coated glass (the same data for control shown at the previous graph), 30 min (control: N=3, n=88; Y-27+CK-666: N=3, n=130) and 3 h (control: N=3, n=78; Y-27+CK-666: N=3, n=142) after plating on fibronectin-coated glass. p-value are obtained by t-test.

Because the cell to cell variability might mask the trend of single cell changes in lifetime during spreading, we also tried to follow the lifetime of individual cells every 5 min along the spreading. Most illuminated cells did not spread, while cells in non-illuminated fields of view spread well, suggesting that even with an image every 5 minutes and the lowest possible illumination, the imaging was too toxic to follow cell spreading in time. We could obtain measures for a few cells, which did not show any particular trend, but their spreading was not normal. So we cannot really conclude much from these experiments.

Graph showing FLIPPER lifetime changes for 3 individual cells plated on fibronectin-coated glass (shown in blue, magenta and green) and average lifetime of cells from non-illuminated field (cyan, n=7)

Our conclusions are the following:

1) We are able to visualize some change in the lifetime of the probe for osmotic shock experiments, similar to the published results, but with a rather large cell to cell variability.

2) The spreading experiments comparing 30 minutes and 3 hours, in control or drug treated cells did not reproduce the results we observed with tether pulling, with a global effect of the drugs on the measures at both 30 min and 3 hours.

3) Following single cells in time led to too much toxicity and prevented normal spreading.

We think that this technology, which is still in its early developments, especially in terms of the microscope setting that has to be used (and we do not have it in our Institute, so we had to go on a platform in another institute with limited time to experiment), cannot be implemented in the frame of the revision of this article to provide reliable results. We thus consider that these experiments are for further development of the work and are out of the scope of this study. It would be very interesting to study in details the comparison between the oldest and more established method of tether pulling and the novel method of the FLIPPER probe, during cell spreading and in other contexts. To our knowledge this has never been done so far, so it is not in the frame of this study that we can do it. It is not clear from the literature that the two methods would measure the same thing in all conditions even if they might match in some.

Authors Response:

Reviewer #2 (Public Review):

The authors use representational similarity analysis on a combination of behavioral similarity ratings and EEG responses to investigate the representation of actions. They specifically explore the role of visual, action-related, and social-affective features in explaining the similarity ratings and brain responses. They find that social-affective features best explain the similarity ratings, and that visual, action-related, and social-affective features each explain some of the variance in the EEG responses in a temporal progression (from visual to action-related to social-affective).

The stimulus set is nicely constructed, broadly sampled from a large set of naturalistic stimuli to minimize correlations between features of interest. I'd like to acknowledge and appreciate the work that went into this in particular.

The analyses of the behavioral similarity judgments are well executed and interesting. The subject exclusion criteria and catch trials for online workers are smart choices, and the authors have tested a good range of models drawn from different categories. I find the case that the authors make for social features as determinants of behavioral similarity ratings to be compelling.

I have a few questions and requests for additional detail about the EEG analyses. I appreciate that the authors have provided the code they used for all the analyses, and I'm sure that the answers to many if not all of my questions are there, but I don't have access to a Matlab license to run the code. Also, since the code requires familiarity with not just Matlab but with specific libraries to understand, I think that more description of the analysis in the paper would be appropriate.

Some more detail is needed in the description of the multivariate classifier analysis. The authors write (line 597-599): "The two pseudotrials were used to train and test the classifier separately at each timepoint, and multivariate noise normalization was performed using the covariance matrix of the training data (Guggenmos et al., 2018). "

I suspect I'm missing something here, because as written this sounds as if there was only one trial on which to train the classifier, which does not seem compatible with SVM classification. If only one trial was used to train the classifier, that sounds more like nearest-neighbor classification (or something else). Alternatively, if all different pseudo-trial averages - each incorporating a different subset of trials - were used for training, then that would seem to mean that some of the training pseudo-trials contained information from trials that were also averaged into the pseudo-trials used for testing. I don't know if this was done (probably not) but if it was it would constitute contamination of the test set. I think this part of the methods needs more detail so we can evaluate it. How many trials were used to train and to test for each iteration?

Thank you for raising this issue; we agree that our Methods section was unclear on this point. We used split-half cross-validation. There was one pseudotrial for training per condition (which was obtained by averaging trials). There was no contamination between the training and test sets, because the data was first divided into separate training and test sets, and only afterwards averaged into pseudotrials for classification. This procedure was repeated 10 times with different data splits to obtain more reliable estimates of the classification performance. We rewrote the corresponding section to make this clearer:

“Split-half cross-validation was used to classify each pair of videos in each participant’s data. To do this, the single-trial data was divided into two halves for training and testing, whilst ensuring that each condition was represented equally. To improve SNR, we combined multiple trials corresponding to the same video into pseudotrials via averaging. The creation of pseudotrials was performed separately within the training and test sets. As each video was shown 10 times, this resulted in a maximum of 5 trials being averaged to create a pseudotrial. Multivariate noise normalization was performed using the covariance matrix of the training data (Guggenmos et al., 2018). Classification between all pairs of videos was performed separately for each time-point. […] The entire procedure, from dataset splitting to classification, was repeated 10 times with different data splits.”

We also performed the decoding procedure with a higher number of cross-validation folds and found very similar results.

I think a bit more detail is also necessary to clarify the features used for the classification. My understanding is that each timepoint was classified as one action vs each other action on the basis of all the electrodes in the EEG for a given temporal window. Is this correct? (I'm guessing / inferring more than a little here.)

This is correct, and we agree that further clarification was needed in text. We have added this:

“Classification between all pairs of videos was performed separately for each time-point. Data were sampled at 500 Hz and so each time point corresponded to non-overlapping 2 ms of data. Voltage values from all EEG channels were entered as features to the classification model.

The entire procedure, from dataset splitting to classification, was repeated 10 times with different data splits. The average decoding accuracies between all pairs of videos were then used to generate a neural RDM at each time point for each participant. To generate the RDM, the dissimilarity between each pair of videos was determined by their decoding accuracy (increased accuracy representing increased dissimilarity at that time point).”

It would be useful to know how many features constituted each feature space. For example, was motion energy reduced to one summary feature (total optic flow for whole sequence?) For "pixel value", is that luminance? (I suspect so, since hue is quantified separately, but I don't think this was specified).

For motion energy, we used the magnitude of the optic flow, and calculated Euclidean distances between the vectorized magnitude maps rather than reducing it to summary features. We have included the dimensionality of each feature in Supplementary File 1b and we now refer to it in text:

“These features were vectorized prior to computing Euclidean distances between them (see Supplementary File 1b for the dimensionality of each feature).”

Pixel value was indeed the luminance, and we have clarified this in text.

More broadly, I would appreciate a bit more discussion of the role of time in these analyses. Each clip unfolds over half a second, so what should we make of the temporal progression of RDM correlations? Are the social and affective features correlated with later responses because they take more time to compute (neurally speaking), or because they depend on longer temporal integration of information? These two are not even exactly mutually exclusive, and I realize that it may be difficult to say with certainty based on this data, but I think some discussion of this issue would be appropriate.

This is a great point, although it is difficult to speculate based on this data. One way to get at this would be to examine how much social-affective processing relies on previously extracted features. Future work could look at the causality between early and later-stage EEG features (unfortunately our post-hoc attempts to address this via Granger-causal analysis were unsuccessful, likely due to insufficient SNR with our specific experimental design). Alternatively, this could be investigated in a follow-up experiment that varies how social information unfolds over time (e.g., images vs. videos or varying video duration). We now discuss this possibility in the manuscript:

“Given the short duration of our videos and the relatively long timescale of neural feature processing, it is possible that social-affective features are the result of ongoing processing relying on temporal integration of the previously extracted features. However, more research is needed to understand how these temporal dynamics change with continuous visual input (e.g. a natural movie), and whether social-affective features rely on previously extracted information.”

Author Response:

Reviewer #1 (Public Review):

In this study, the authors present a detailed analysis of the T cell receptor repertoire in mice examining how the age, the cell differentiation status, the tissue compartment distinguishing between spleen and bone marrow, and antigen exposure influence its composition. Looking at amino acid motif distributions and sharing patterns of nucleotide sequences within the individual clones, and comparing them between the different cell compartments and groups, they aim at identifying the main axes of influence that shape the T cell receptor repertoire within these mice. They find some interesting differences, with e.g. repertoires from different functional compartments being more separated within young animals compared to older ones. However, given the complexity of the different aspects that are investigated and compared, it is sometimes difficult to follow the main conclusions from each of the presented analyses. In addition, the main conclusion shown in Figure 7 that repertoire evolution is influenced by cell migration, differentiation and age/infection seems to be partly well known, as also acknowledged by the authors. However, it would be really interesting if, based on their analyses, the authors could put a "weight" to each of these features, i.e. if aging has a larger effect on repertoire differences than tissue compartments. This is currently not easily seen from their analyses. If possible this would increase the value of this study going beyond a descriptive presentation of the results and support the mechanistic relationships hypothesized within the discussion.

We are grateful to the reviewer for these insightful comments. We have introduced a completely new analysis (new Figure 5 and two additional panels in Figure 6) which captures the quantitative shift in a two-dimensional space defined by two global statistical parameters of the repertoire (V and Triplet cosine similarity) as the repertoires move along the multidimensional trajectory illustrated in Figure 7 (old, now Figure 5A). This analysis framework is novel, at least to our knowledge. When combined with the existing analysis, this additional analysis reveals a clear hierarchy of impact of different immunological processes on repertoire diversification. Definition of this hierarchy is itself we believe novel. In addition, we observe a CD4+/CD8+ lineage dependent interaction between age and differentiation on the structure of the repertoire providing additional novelty. A completely new results and discussion session are attached to this figure.

Reviewer #2 (Public Review):

This is a careful observational study of a rich dataset, quantifying the relationships between naive, regulatory, effector and memory subsets. it is notable for its thorough approach to analysing TCR diversity by multiple levels of granularity, from V-beta usage to nucleotide level. However it is a little lacking in narrative and interpretation. As a result my impression is that it doesn't present any results that expand significantly on our existing understanding of T cell biology. As the authors note, shifts in diversity of T cell subsets with age are already well established and while multiple measures of diversity are explored, the results are broadly in agreement with each other. I wanted to be more enthusiastic about this study but it comes across as a tour de force in data exploration rather than something that sheds light on the forces shaping the structure and overlap of T cell repertoires.

We agree with this reviewer and the prior reviewer that the main impact of this study was not clearly explained. We provide a quantitative framework which can be used to track the movement of repertories along the multidimensional space illustrated in our Figure 7(old) and can define a hierarchy of impact of different immunological processes in driving diversification of the repertoire. As outlined in detail in the response to reviewer 1, we think this perspective on statistical features of TCR repertoires goes significantly beyond previous studies and provides a robust quantitative framework for analysing the relative influence of internal or external selective pressure on the T cell compartment.

Author Response:

Reviewer #2 (Public Review):

Zhang et al. describe a new method for inducing traumatic optic neuropathy in larger mammalian models that offers the additional advantage of allowing rapid administration of local therapies to the site of optic nerve injury. Furthermore, the authors build on their prior work which has demonstrated a neuroprotective effect of hypothermia provided that protease inhibitors are employed to protect against cold-induced microtubule damage. In the present manuscript, they show that an endonasal approach to accessing the optic nerve within the optic canal can be performed safely in goat without inducing optic nerve damage. They then demonstrate that experimental crush of the optic nerve within the optic canal results in progressive degeneration of retinal ganglion cell (RGC) neurons and of their axons which form the optic nerve; this occurs over a period of several months, a similar time course to traumatic optic neuropathy in humans. Transcriptional profiling of mRNA obtained from the optic nerve at its site of injury identified changes in gene expression related to molecular pathways involved in inflammation, ischemia, and cellular metabolism. The authors then proceed to apply local hypothermia or protease inhibitor administration (individually or in combination) to the site of optic nerve crush for two minutes and observed a decrease in axonal degeneration in the subsequent months, although without an improvement of conduction of visual information by the affected optic nerve. Finally, the authors describe a computer program which uses computed tomography scans to evaluate thousands of potential endonasal approaches to access the prechiasmal optic nerve in large and medium sized mammals, and they proceed to successfully perform optic nerve exposure and experimental crush in a macaque model.

The authors' interpretation of the data is generally accurate; however, their conclusions about the impact of the work are somewhat overstated.

We appreciate the reviewer’s insightful and precise comments, which definitely help improve our manuscript. We have scaled back the conclusions about the impact of our work, and revised our manuscript point by point according to the reviewer’s comments.

Strengths:

The prevailing use of rodent models of traumatic optic neuropathy in the field is problematic, and the authors' efforts to use larger mammalian models may be helpful in understanding the pathophysiology of and developing treatments for traumatic optic neuropathy in humans. The computer program that evaluates and recommends detailed surgical approaches and instrumentation is novel and would be quite useful to other investigators attempting to perform similar endonasal procedures. The authors make use of multimodal assessments of the goats and macaques [e.g. quantitative retina and optic nerve histology; optical coherence tomography measurements of retinal layers; pupillary light reflex assessment; and electrophysiology studies including visual evoked potential (VEP) and pattern electroretinography (PERG)] to convincingly demonstrate that the endonasal procedure itself can be performed without inducing progressive optic nerve damage and that experimental optic nerve crush using this procedure induces the expected profound decrease in optic nerve function, associated with progressive degeneration of RGC cell bodies and axons. The histological assessment of goat optic nerves following the local hypothermia/protease inhibitor treatment demonstrates a convincing reduction in the absolute number of RGC axons that are lost at 1 month after optic nerve crush.

Thank you very much.

Weaknesses:

The premise that optic nerve crush within the optic canal is much more physiologically relevant than other existing animal models is overstated: while the optic canal is believed to be the most common site of injury to the optic nerve, most human cases of traumatic optic neuropathy occur as a result of indirect mechanisms rather than compression/crush-namely, stretching and shearing forces are applied to the optic nerve where it is tethered to the periosteum of the optic canal by its dura. The authors' example of a bony fragment compressing the optic nerve within the optic canal (Figure 1B) is relatively rare and would actually represent one of the few cases where a surgical intervention (to relieve acute optic nerve compression) might be considered clinically justifiable.

We agree with the reviewer that “most human cases of traumatic optic neuropathy occur as a result of indirect mechanisms rather than compression/crush”. To address the reviewer’s concern, we updated our discussion as: “Recently, rodent models have been developed using indirect mechanisms (apply periorbital ultrasound or skull weight drop) to induce distal ON injury. Compared with direct optic nerve compression or crush, these models are likely more clinically relevant since most clinical TON cases are indirect and due to force transmission (39-41). However, due to force scattering, unwanted and uncontrolled collateral damage to the eyeball, contralateral optic nerve, orbit or skull often occur in these models (39,40). Additionally, the success rate of these modeling methods is not as high as direct optic nerve crush; for example, 10% mice died immediately after head weight drop (39). Moreover, extension of these modelling methods to large animal species has not been reported. Therefore, clinically translatable, local treatment of injured ONs via trans-nasal endoscopy cannot be performed in these small animal models.”

To further address the reviewer’s concern, we have added the following statement to the “Limitations of this study” section in the revised manuscript: “Our TON model is clinically relevant in terms of injury site, subsequent spatiotemporal pattern of retrograde axonal degeneration, and availability of trans-nasal local treatment. However, the mechanism of optic nerve injury in our model differs from that in most clinical TON cases, in which the intra-canalicular optic nerve is injured by an indirect mechanism (stretching and shearing forces), rather than by direct compressing forces.”.

We respectfully disagree that “a bony fragment compressing the optic nerve within the optic canal (Figure 1B) is relatively rare”, at least in China. According to our previous clinical study of 1275 patients with indirect traumatic optic neuropathy (PMID: 27267448), bony fracture of the optic canal is not rare: 50% of patients had a visible optic canal fracture on high-resolution CT scans, and an additional 20% had a visible optic canal fracture under trans-nasal endoscopy (because endoscopy provides excellent illumination and a magnified view of the optic canal).

The transcriptomic profiling at three locations along the visual pathway in post-trauma goats only showed differences in expression at the location of optic nerve injury, and not within the retina or proximal optic nerve on the affected side. The authors assert that the high rate of expression changes in pathways relevant to ischemia, inflammation and metabolism indicates "that targeting these pathways with local treatment could alleviate secondary damage." This is overstated. While such profiling may be useful for hypothesis generation, it was not followed up by any experiments to determine whether these expression changes are actually detrimental to the optic nerve. Some of them may very well be compensatory, such that inhibiting them may only exacerbate damage. Furthermore, given that these transcriptional changes are not seen in the retina (where RGC nuclei reside) or in the proximal optic nerve, this would suggest that the observed transcriptional changes at the site of injury are actually occurring in non-neuronal cells (e.g. astrocytes, oligodendrocytes, microglia). The authors should convey that the changes they observe are unlikely intrinsic to the optic nerve axons.

We appreciate the reviewer’s insightful explanation and agree that our original claim is premature. We deleted the statement " targeting these pathways with local treatment could alleviate secondary damage" in the Results section. Additionally, we have replaced the previous sentence in the Discussion, which stated: " Instead, we targeted hypothermia to the injured pre-chiasmatic ON to prevent early changes in ischemia, inflammation, and metabolism transcripts (as revealed by RNA-sequencing at 1 dpi)." with “Instead, we targeted hypothermia to the injured pre-chiasmatic ON according to early transcriptomic changes in ischemia, inflammation, and metabolism pathways.”.

We also agree with the reviewer’s comment that these transcriptomic changes at the injured optic nerve mainly occurred in the micro-environment of non-neuronal cells. The major advantage of our large animal model is the ability to modulate the micro-environment around the axons of the distal optic nerve, including glial cells, vasculature, connective tissues and the extracellular matrix. To incorporate the reviewer’s comment, we have added the following statement in the Results section: “These transcriptomic changes at the injury site were unlikely intrinsic to the distal optic nerve, and more likely occurred mostly in non-neuronal cells in the micro-environment.”

The lack of any rescue of the pupillary light reflex or of visual evoked potential responses after local hypothermia/protease inhibitor treatment suggests that the physiological significance of any anatomical rescue by this treatment is minimal. If a number of axons survive but cannot conduct sufficient visual signal to stimulate the pupil response or stimulate the visual cortex, then the local treatment (even when applied immediately after trauma in this model, unlike in human patients in which a delay of a number of hours would be required at the very least) cannot be considered a substantial success. The authors also characterize the goats at 1 month post-injury, so one cannot say whether the statistically significant improvement in axon loss with the combined treatment would be durable at the later 3-month time point.

We agree with the reviewer that the local treatment with hypothermia/protease inhibitor did not achieve functional recovery of the visual pathway, and thus it could not be considered a substantial success. Our work provides a safe and clinically translatable approach to modulate the inhibitory extrinsic environment at the injury site. Although in our current study, application of local treatment with hypothermia/protease inhibitor does not achieve eye-to-brain functional recovery, and its long-term therapeutic effect is unclear, these results are encouraging because they show some benefit of local treatment. Another important feature of our large animal model is that local treatment of the extrinsic environment at the distal optic nerve can be combined with currently available intravitreal treatments, such as gene therapy to boost intrinsic axon regrowth capacity, to target both extrinsic and intrinsic factors. To address the reviewer’s comment, we have added the following to the discussion in the “Limitations of this study” section: “Additionally, the current local treatment did not achieve functional recovery of the eye-to-brain pathway, and its long-term therapeutic effect is unclear.”

As the authors acknowledge, the use of larger mammals prevented them from conducting studies with a large n. As a result, their analyses are underpowered.

We agree with the reviewer that, in an ideal scenario, increasing the sample size would improve the power of the analysis. In this study, however, ethical issues and limitations of housing space and other resources, constrain the sample size of large mammals. We include this point in our “Limitations of this study” section.

Because of the dissimilarities between their model and the most common mechanism of human traumatic optic neuropathy and because of the lack of a clinically significant rescue of the optic neuropathy when the local hypothermia/protease inhibitor treatment was applied, the authors' assertion that their model may "trigger a paradigm shift " for traumatic optic neuropathy research should be scaled back.

We agree with the reviewer that it is too early to state that our model may “trigger a paradigm shift”. We need more effective local treatments to prove the value of this model and the novel therapeutic approach. Therefore, we have deleted “trigger a paradigm shift” in the Introduction and Discussion.

Author Response:

Reviewer #1 (Public Review):

Phillips and Rubin investigated the biophysical mechanisms that underly the generation of respiratory related burstlets and bursts in the rhythmogenic pre-Botzinger circuit. They show, suing a computational modelling approach, that synaptically mediated intracellular calcium concentrations and Ca2+ release and uptake via the endoplasmic reticulum are a unifying mechanism of the generation of the respiratory rhythm and its recruitment at the motoneuronal level. This explanatory model is able to unify contradictory experimental findings and is further evaluated by modelling the effect of opioids on the generation of burstlets and bursts in pre-Botzinger complex.

The conclusions of this paper are mostly well supported by a sound computational modelling approach, however the current computational modelling data are largely based on experimental data of very few workgroups, while previous modelling approaches and experimental data that support anatomical network connectivity as a key feature for respiratory rhythm generation and transmission of burstlet/bursts to motorneuron pool were neglected.

To our knowledge, the work supporting anatomical network connectivity as a key feature that the reviewer mentions (Ashhad & Feldman, Neuron, 2020; Slepukhin et al., arXiv: 2012.12486) makes the claim that in a general setting involving spread of activity by percolation without any additional biophysical mechanisms (such as synaptic plasticity, cf. Guerrier et al., PNAS, 2015), a specific distribution of synaptic weights is needed to produce burstlet generation that agrees with experimental findings. Our work shows that random connectivity without specially distributed weights is sufficient in a setting in which a fraction of neurons are endogenous bursters and the calcium-related recruitment mechanisms that we model are also present. Our approach of studying this biophysical framework independently from the alternative, based entirely on anatomical network connectivity, is important in order to characterize what properties can follow from the biophysical framework on its own. Once our paper is published, the two complementary frameworks and their corresponding predictions will be represented in the literature and can be tested in future experiments. We contend that this is more useful than if we had tried to combine both biophysical and connection-based frameworks in the present model, before considering the former on its own.

The current model is exclusively focused on biophysical properties and in particular calcium dynamics to generate a unifying computational model for respiratory rhythm generation. However, a previous model and experimental data suggest the emergence of rhythmogenic activity in pre-Botzinger complex may be largely determined by the local network connectivity as well as by the connectivity of the pre-Botzinger complex with the extended medullary and caudal pontine respiratory circuit. It would be interesting if this crucial component of a truly unifying model could be added or at least needs to be discussed appropriately.

We fully acknowledge that our work focuses on rhythm-generation and pattern-generation mechanisms in the preBotC. It is quite possible that these mechanisms can only function at full capacity when the neurons involved receive inputs from other parts of the extended respiratory circuit (e.g., Jones and Dutschmann, J. Neurophysiol., 2016). These inputs, for example, might help set the level of excitability of preBotC neurons (cf. Smith et al., J. Neurophysiol., 2007). Although adding any sort of detailed representation of this extended circuit is beyond the scope of this work, we agree that it is important to mention, to help put our work in a bigger picture context, and we have added text about this point in our revised Discussion and in our responses below to Reviewer #1’s Recommendations for the authors.

Reviewer #2 (Public Review):

Since its isolation in the transverse slice in 1991 (1), researchers have studied the preBotC with a focus on 2 related questions: how respiratory rhythm is generated, and how this rhythm is transformed into the pattern of inspiratory bursts, which are recorded at hypoglossal rootlets (XIIn), and in more intact preparations, from cervical ventral roots. The discovery of burstlets has provided support for the conjecture that the preBotC can be functionally parcellated into rhythm-generating and pattern-forming networks (2).

Others have proposed that burstlets are rhythmogenic (2-4), via a stochastic percolation mechanism that synchronizes tonic spiking into burstlets, which in turn give rise to inspiratory drive. Phillips and Rubin challenge this account for its lack of detail and argue that it is weakly supported by features of burstlets that can be otherwise accounted for (burstlet onset and slope; percolation of activation following photostimulation of network subsets). Their points are well-taken, but two points need to be made. First, the percolation conjecture has gained traction because other more conventional mechanisms for rhythmogenesis have been shown not to apply, as nicely summarized in (4, 5). In particular, rhythmogenesis arising out of the activity of endogenous bursters (as is the case in their model) has failed to find empirical support: optical recordings of respiratory networks under conditions of synaptic blockade have not revealed appreciable numbers of endogenous bursters (this despite the fact that groups are recording from slices expressing genetically-encoded Ca2+ indicators in glutamatergic neurons in preBotC, using two-photon microscopy), older studies using conventional patch clamp methods identified negligible numbers of endogenous bursters (6, 7), and pharmacological disruption of specific endogenous bursting mechanisms has not silenced respiratory rhythm in the slice (8). Second, and more importantly, the processes that they model mediate the amplification of burstlets to bursts, and thus don't have obvious bearing on whether or not burstlets are generated by stochastic percolation or endogenous burster activity. As they state (lines 605-607) "the findings about burstlets and bursts presented in this work would have been obtained if the burstlet rhythm was imposed (Fig. 1) or if burstlets were generated by some other means". Thus a discussion of the inadequacies of current percolation models of respiratory rhythmogenesis seems to be irrelevant to their main points, and fails to acknowledge that other more plausible mechanisms have been set aside because they were undermined by experimental findings. They should either explain why a percolation-based mechanism for the emergence of burstlets is incompatible with their model for CIRC-mediated amplification of burstlets to network bursts, or they should remove these arguments, which distract from their main findings.

We acknowledge that different experiments, done using different approaches and in various settings, have yielded heterogeneous results about the prevalence and importance of endogenous bursters in respiratory rhythm generation. Importantly, the emphasis in our work is on the biophysical mechanisms associated with neural recruitment in the burstlet-to-burst transition. We do not make the claim that a percolation-based mechanism for the emergence of burstlets is incompatible with our ideas about this transition. We have added a critical phrase to this text to clarify this point. Importantly, in the revision process, we have also performed additional simulations, now included in the paper, which show that our model gives similar recruitment and amplification of activity when INaP-based bursting is replaced by imposing rhythmic activity on the burstlet population; see Figure 4-Figure Supplement 1.

It would be useful if the authors could elaborate on the applicability of their findings to less reduced preparations. The emergence of burstlets as well as the transition from predominantly burstlets to predominantly bursts is strongly dependent on network excitability, which is controlled by varying [K+]bath. Importantly, in their simulations burstlet activity falls silent at [K+]bath < 4 mM, and robust motor output only emerges for [K+]bath > 8 mM. While these modeling results jibe well with experimental results in the slice preparation, in more intact preparations, robust and stable respiratory rhythm is maintained at physiological levels ([K+]bath = 3 mM); in intact animals, 9 mM [K+]o is lethal. This raises the question of whether their model has explanatory power for respiratory rhythmogenesis in more intact preparations, or whether it is limited to describing fictive respiration in the slice.

We thank the reviewer for highlighting this important point. The relevance of the current simulations to more intact preparations is now discussed in the revised manuscript. In in vitro slice preparations the preBotC generally lacks sufficient intrinsic excitability to generate an inspiratory rhythm presumably due to the loss of excitatory drive from higher brainstem centers such as the KF, PB, RTN, RO; see Smith et al., J. Neurophysiol 2007. As such, elevating extracellular potassium in in vitro slice preparations is a standard procedure in the field as it is required for generating rhythmic output under these conditions. However, elevating the preBotC excitability by other means such as manipulations of extracellular Ca2+ does not appear to significantly impact preBotC rhythmicity (Ruangkittisakul et al., Respir Physiol Neurobiol. 2011) or the generation of bursts and burstlets (Kam et al., J. Neurosci. 2013). Moreover, burstlets can be seen in vivo via manipulations of preBotC and BotC excitability (Kam et al., J. Neurosci. 2013). Therefore, understanding burstlet and burst generation in the reduced preBotC slice preparation is highly relevant in more intact preparations. Investigation of how these higher brainstem centers impact preBotC inspiratory rhythm and pattern generation are beyond the scope of this study.

Another aspect to this problem is that the rhythmogenic mechanism they have incorporated in their model has strong dependence on [K+]bath; this straight-forwardly accounts for the transition from quiescence to burstlets, since within their models, endogenous bursters are quiescent at lower excitability levels. Of greater interest is the extent to which the [K+]bath dependence of the transition from burstlets to inspiratory bursting is again due to their choice of endogenous burster implementation. This is important, because it might enable CIRCA-mediated transitions from burstlets to network bursting that show less steep voltage dependence, and which are robust at more physiological [K+]o, thus enhancing the generalizability of their model. This was certainly a feature of an early study, in which I(CAN) was proposed as a mechanism for endogenous bursting, with weaker voltage dependence than the I(NaP)-based endogenous bursters implemented here (7).

Our response to this comment has several aspects, which we present sequentially below.

1) Qualitatively, the Kbath dependence of our model matches well with the Kbath dependence shown in Kallurkar et al., eNeuro 2019. That is, the burstlet frequency and bustlet amplitude increase with Kbath. We are unaware of any data that shows a different Kbath vs burstlet frequency relationship. Moreover, if PSynCa is increased with Kbath our model produces changes in the burstlet fraction that closely match those seen experimentally.

2) It is not clear why we would want to show a less steep Kbath-dependence (we are assuming that was what the reviewer was commenting about, rather than voltage dependence) with the burstlet to burst transition (burstlet fraction). First, our model actually has a very shallow slope in the Kbath vs burstlet fraction curve if Kbath is the only parameter varied (PSynCa=fixed). This can be seen by considering a horizontal slice through Fig. 4 D-F. In order to match the slope of the Kbath vs burstlet fraction curve in experimental data we actually needed to make the slope between Kbath and the burstlet fraction steeper. This was achieved by increasing PsynCa with Kbath, Fig. 4I. The justification of increasing PSynCa is presented on lines 422-442 of the discussion.

3) Indeed, some earlier work has identified Cd2+ sensitive and presumably Ca2+/ICAN dependent endogenous bursters and these bursters showed weaker voltage-dependence (Thoby-Brisson Journal of neurophysiology 2001). However, more recent studies have shown that ICAN is not involved in rhythm generation (Koizumi et al. 2018, Picardo et al., 2019). Similarly, application of Cd2+ which should eliminate Ca2+/ICAN dependent bursters does not affect rhythm generation, and instead blocks preBotC motor output (Kam et al., 2013, Sun et al., 2019). That is, Cd2+ application eliminates preBotC network bursts but does not affect the ongoing burstlet rhythm.

4) The Kbath value of approximately 5mM where endogenous bursting first emerges in our model is also in agreement with existing experimental data (Del Negro et al., 2001, Mellen et al., 2010).

5) In our model, a burstlet transitions into a burst when postsynaptic calcium transients in the pattern generating subpopulation are of a sufficient magnitude to trigger CICR, which leads to ICAN activation, depolarization, and ultimately recruitment of these neurons into a network burst. The rhythm in the burstlet population is driving the postsynaptic Ca2+ transient in the pattern generating subpopulation. The mechanism that is driving the burstlet rhythm has no impact on the dynamics of the postsynaptic Ca2+ transients, CICR, ICAN activation or recruitment of the pattern generating population. Therefore, the mechanism of rhythm generation does not impact the proposed mechanism underlying the burstlet to burst transition. However, to illustrate this point we imposed a rhythm in the neurons comprising the rhythmogenic subpopulation. This was achieved by imposing a Poisson spike train in each neuron where the frequency was zero during the interburst interval. At the start of the burstlet the frequency linearly ramps up over 250ms to an imposed maximum firing rate and then linearly ramps back down to zero over an additional 250mS, see Figure 4-figure supplement 1A. The burstlet frequency was set by changing the interburst interval and the amplitude was set by changing the maximum firing rate at the peak of the burstlet, Figure 4-figure supplement 1 panels A and B. These simulations show that this network produces qualitatively similar bursts and burstlets which depend on a CICR-mediated burstlet-to-burst recruitment process. Moreover, as in Fig. 4, the burstlet fraction primarily depends on Psynca, whereas the burst frequency depends on Psynca and the burstlet frequency.

1. Smith JC, Ellenberger HH, Ballanyi K, Richter DW, Feldman JL. Pre-Botzinger complex: a brainstem region that may generate respiratory rhythm in mammals. Science. 1991;254(5032):726-9.
2. Kam K, Worrell JW, Janczewski WA, Cui Y, Feldman JL. Distinct inspiratory rhythm and pattern generating mechanisms in the preBotzinger complex. J Neurosci. 2013;33(22):9235-45.
3. Ashhad S, Feldman JL. Emergent Elements of Inspiratory Rhythmogenesis: Network Synchronization and Synchrony Propagation. Neuron. 2020;106(3):482-97 e4.
4. Kallurkar PS, Grover C, Picardo MCD, Del Negro CA. Evaluating the Burstlet Theory of Inspiratory Rhythm and Pattern Generation. eNeuro. 2020;7(1).
5. Del Negro CA, Funk GD, Feldman JL. Breathing matters. Nat Rev Neurosci. 2018;19(6):351-67.
6. Del Negro CA, Koshiya N, Butera RJ, Jr., Smith JC. Persistent sodium current, membrane properties and bursting behavior of pre-botzinger complex inspiratory neurons in vitro. J Neurophysiol. 2002;88(5):2242-50.
7. Thoby-Brisson M, Ramirez JM. Identification of two types of inspiratory pacemaker neurons in the isolated respiratory neural network of mice. J Neurophysiol. 2001;86(1):104-12.
8. Del Negro CA, Morgado-Valle C, Feldman JL. Respiratory rhythm: an emergent network property? Neuron. 2002;34(5):821-30.
9. Del Negro CA, Johnson SM, Butera RJ, Smith JC. Models of respiratory rhythm generation in the pre-Botzinger complex. III. Experimental tests of model predictions. J Neurophysiol. 2001;86(1):59-74.

Reviewer #3 (Public Review):

A key contribution of this study includes a demonstration that two sets of neurons coupled via excitation can drive network activity similar to that observed in mXII nerve during breathing. In particular, the authors formulate a link between synaptic excitation and intracellular calcium induced Ca2+ release mechanisms via positive feedback from ICaN. This forms the basis for recruitment of non-rhythmogenic neurons by rhythm generating neurons. Such a formulation seems to help explain the burstlet theory and support a percolation theory of network bursts put forward in the field.

The manuscript is well written. Figures and figure legends are clear, and justify the results stated. Methodology is well laid out; however, missed references in many places where it is not clear where the equations came from (e.g., equations 19 through 24 and elsewhere). The authors state that the model code "will" be available on ModelDB. This should instead be submitted with the manuscript for review. Later, the code must be made available on a GitHub repository for wide dissemination and future updates by others. ModelDB has models which can only be downloaded but not extended for wider use. Oftentimes this leads to lack of technical help for future users and limits model use and enhancement.

We thank the reviewer for the positive comments about readability and clarity. The reviewer makes an excellent point about ensuring that code sharing occurs in a way that allows for future use. We have made our model code available on GitHub at the following link:

https://github.com/RyanSeanPhillips/Putting-the-theory-into-burstlet-theory

The authors put forward a plausible mechanistic explanation for Ca2+ dependent recruitment of non-rhythmogenic neurons by linking synaptic excitation from the rhythm generating neurons to CICR in the former. Although attractive, there are numerous factors which control intracellular Ca2+ signaling and buffering. It would be important to clarify whether the assumption that dendritic depolarization due to synaptic inputs directly contributes to CICR as postulated in this model (the term PsynCa*Isyn in equation 19), has any (direct/indirect) empirical support either in preBotz neurons or elsewhere to ensure that this is not purely conjectural.

The link between postsynaptic Ca2+ transients and CICR in the pattern generating preBotC subpopulation and equation (19) has empirical support from multiple studies, which are discussed on lines 422-444. Specifically, Mironov et al., 2008 showed that synaptically triggered Ca2+ transients in the distal dendrites of preBotC inspiratory neurons travel in a wave to the soma, where they activate TRPM4 currents (𝐼𝐶𝐴𝑁). This idea is further supported by Del Negro et al., 2011, which showed that dendritic Ca2+ transients precede inspiratory bursts, and Phillips et al., 2018, which showed that Cd2+ sensitive voltage-gated Ca2+ channels are primarily located in distal dendritic compartments. Taken together, these studies suggest that excitatory synaptic inputs to distal dendrites of preBotC inspiratory neurons trigger postsynaptic Ca2+ transients. In the model, we capture the synaptically triggered postsynaptic Ca2+ transient with equation (19), which specifies that a percentage (PSynCa) of the total postsynaptic current (ISyn) is carried by Ca2+ ions.

Author Response:

We thank the reviewers for their positive, constructive feedback. However, we would like to take the opportunity now to briefly address one comment from Reviewer #1:

In addition, only pyramidal cells were considered here but long-range projecting GABA neurons have been recently reported in the prelimbic cortex (preprint from Malik et al., 2021) which suggests that this could be a possibility in the anterior cingulate cortex as well. So even if the starter cells identified in the present study were sufficient to detect other inputs to the hippocampus, I am not sure it is sufficient to completely rule out the existence of a scarce and potentially inhibitory projection to the hippocampus.

We are quantifying the number of starter cells in our rabies experiment and will report these in the revised manuscript. However, the preprint from Malik et al. reported that optogenetic stimulation of the inhibitory projection from PFC did not evoke IPSCs in CA1 pyramidal cells (0/38 neurons tested). As such, if a similar inhibitory projection from ACC does indeed exist (it appears that it does, based on informal conversations with other researchers on social media) then we would not detect it in our monosynaptic rabies experiment, as we used the Emx1-cre mouse line to specifically map presynaptic inputs onto hippocampal glutamatergic neurons. Indeed, the preprint from Malik and colleagues provides evidence of a direct route by which prefrontal cortex can drive feedforward inhibition in CA1 while avoiding pyramidal cells. How the function of this projection differs from the indirect route via nucleus reuniens which, as we recently reported in another preprint (Andrianova et al., 2021, bioRxiv 2021.09.30.462517), also appears selective for interneurons over pyramidal cells, provides an exciting avenue for future research.

Author Response:

We thank the reviewers for their thoughtful evaluation of the manuscript and insightful comments. One reviewer commented on the lack of biological replicates for our scRNAseq. To mitigate batch effects, we sequenced a single technical replicate for each condition, but each consisted of several biological specimens (11-13 animals each) from multiple litters, totaling 49 animals. Pooling this large number of retinas was necessary for obtaining enough cells for analysis, and consequently, we have many biological samples represented. In addition, the proportions of microglia expressing specific markers in our scRNAseq match our published quantification by in situ hybridization (Anderson et al. Cell Reports 2019), giving us confidence that the proportions determined here are representative. The reviewer also asked whether the clusters with remodeling signatures are actually remodeling. We agree with the reviewer that we cannot infer function using transcriptomic data alone. However, our scRNAseq of microglia illustrates several clusters with high expression of lysosomal and lipid metabolism genes which are diminished or absent in retinas lacking developmental apoptosis (Bax KO), consistent with remodeling activity. A complete in vivo functional analysis of each remodeling cluster is beyond the scope of this manuscript, but we are currently probing this further for another publication.

Author Response:

Reviewer #2:

Major comments:

1. Despite the strong ERG phenotype, some 50% of the TADR mutant flies still show behavioral responses in the phototaxis axis, strongly arguing for a pathway acting in parallel to TADR. Comparison to a known blind mutant, such as HDC could clarify this issue.

As an essential amino acid, each cell can only use extracellular histidine. Although TADR is a specific histidine transporter, its expression pattern suggests that it is not the only histidine transporter. Supporting this, null tadr mutants are viable and have no growth phenotype. As photoreceptor cells may uptake histidine from other histidine transporters, they have a small histidine pool and synthesize some histamine via Hdc. Supporting this, histamine levels in tadr mutants are higher than in Hdc mutants, although histamine levels are greatly reduced in both mutants (Figure 5D). Consistent with reduced histamine levels, tadr^2 mutants exhibit weak phototactic behavior, indicating the presence of another histidine transporter in Drosophila photoreceptor cells. However, given that tadr^2 mutants displayed a complete loss of ON and OFF transients, greatly reduced histamine levels, and much less phototactic behavior, we speculate that TADR is the major histidine transporter, responsible for maintaining the histidine pool and keeping visual transmission at high frequencies. We added this part to the discussion section.

1. Such a second pathway is also consistent with the level of histamine still present in TADR flies. Although curiously this issue is not specifically addressed by the authors, the level appears to be significantly higher than in HDC mutants (Figure 5D). This should be addressed.

We thank the reviewer for this concern. Indeed, we found that levels of histamine in compound eyes of tadr^2 mutant flies were slightly higher than in eyes from Hdc^P217 mutants. As you mentioned, we cannot not rule out the possibility that another pathway acts in parallel to TADR. We briefly explain this in the results section (highlighted). Moreover, histamine levels in tadr^2 mutant flies were higher than in Hdc^P217 mutants, suggesting that a small fraction of histidine could be supplied by other transporter systems.

1. Beyond referring to a "complete disruption of the tadr locus", the molecular details of the mutant should be better explained: Does the mutant result in an in-frame or an out-of-frame fusion of exon3 and 5? What parts of the protein are deleted?

We thank the reviewer for this suggestion. We verified the genomic details of the tadr^2 mutant, and indeed the tadr^2 mutation generates a truncated tadr mRNA with a frame-shift (deletion of 244 nt) at the truncated site. We added the molecular details of the mutant to the manuscript: “PCR amplification and sequencing of the tadr locus from genomic DNA isolated from wild-type and tadr^2 flies revealed a truncated tadr locus in mutant animals, resulting in an out-of-frame fusion of exon 3 and 5 (Figure 2-figure supplement 2B and 2C).”. We also modified Figure 2-figure supplement 2C showing the cDNA sequence and corresponding amino acids around the truncated stie.

Author Response:

Reviewer #1:

NPM1-mutated acute myeloid leukemia (AML) is a frequent AML subtype for which new therapeutic approaches are needed. Immunotherapy may represent a promising strategy, to be combined with or alternative to chemotherapy. Particularly, vaccination strategies may be successful in NPM1-mutated AML, as mutant NPM1 is known to be immunogenic and specific T-cells may control disease relapse. In this study, Tripodo et al. performed a handful of experiments to demonstrate the feasibility and the antileukemic efficacy of a dendritic cell (DC) vaccine armed with neutrophil extracellular traps (NETs) derived from NPM1-mutated myeloid cells.

While this work has the major strength of being novel and performed in vivo, the models used in the study, the number of replicates and the quality of some of the data presented seem insufficient.

One of the major issues is the lack of a formal demonstration of clear antileukemic activity of this approach in leukemic mice. The authors first used a non-leukemic model, then, in their second set of experiments, a subcutaneously injected AML model. In this regard, I am worried that no effect may be seen in AML models where leukemia is engrafted in the bone marrow or in leukemic genetically modified mouse models.

As for Reviewer suggestion we challenged the possibility of detecting vaccine effect against the leukemia model engrafted into the bone marrow. To this end C1498-NPMc+ also GFP+ cells were injected directly into the tibia of C57BL/6 mice, to better mirror leukemia development and the cross-talk with bone marrow microenvironment. Treating injected mice with NPMc+ NET DCs, we confirmed the efficacy of the vaccination schedule showing a reduced engraftment of C1498 within the BM of treated mice compared with animals left untreated. In the same experiment we compared mice vaccinated with DC+NPMc+NET with those vaccinated with DC+NPMc+peptides. Tumor take was evaluated by FACS as number of GFP+ leukemia cells in flushed BM. We show a reduction in GFP+ cells in the BM of mice that have been vaccinated with both NPMc+ NET/DC and the control DC/peptide vaccine in comparison to non-vaccinated mice (new Figure 4G). However only the reduction obtained through the NPMc+ NET/DC vaccine reached statistical significance (New Figure 4G). Also, the NPMc+ NET/DC vaccine was superior in inducing the proliferation of CD8 T-cells (evaluated as frequency of CD8+Ki-67+, Fig. 4I) and their production of TNF (new Figure 4I). Both vaccines sustained OX40 expression on CD8 T-cells (new Figure 4J) and reduced the frequency of exhausted PD1+TIM3+LAG3+ CD8-T cells (new Figure 4K). -cells (new Figure 4L-M). The production of TNF by CD8 T-cells was higher in NPMc+ NET/DC vaccinated mice compared to controls. In this mice we also observed a trend in the induction of Tem (CD44+CD62L+) (new Figure 4O).

Finally, both vaccines were able to induce Auto-Ab against mutant NPMc (new Figure 4P), however only NPMc+ NET/DC vaccinated mice developed Ab to MPO (new Figure 4Q). The last might concur to the anti-leukemia response we have particularly observed in the sc setting, indeed C1498 cells do express MPO (Mopin, A 2016).

Overall, the data support reason and advantage of the newly proposed NET-based vaccines in AML. The use of leukemic blasts as source of NETs provides the cell antigen repertoire displayed onto the DNA threads, also endowed of adjuvant functions. Differently, peptide-based vaccines require prior knowledge of the immunogenic peptides to be loaded into in vitro-activated DCs.

Furthermore, it is unclear what would be the place of NET-DC among other DC vaccines, as there is no direct comparison in this study.

We understand the point raised by the reviewer. The requested comparison between NPMc/NET and DC peptides vaccines was already present in the original manuscript (Figure 4C-E and supplementary Figure 2 in the present resubmission) and indicated a more efficient reduction in tumor growth in presence of NET/DC vaccines compared to NPMc+ peptides-based vaccines. Following the Reviewer’s request, we performed additional in vivo experiments comparing the efficacy of the two vaccines in the orthotopic injection setting (intra-bone). Similarities and differences in the two vaccines in terms of leukemia take and CD8 T cell activation status are discussed above and in the manuscript were data are shown as new Figure 4 (panel G-Q).

Other issues include replicate numbers that need to be increased in some experiments, data representation which is not always appropriate and one panel which has been duplicated from a previously published work.

To overcome the limitation of the number of observations, we now applied non-parametric approaches in order to have more robust results, according to the new statistical analysis performed.

In addition for the new experiments we increased the number of observations and results obtained from the new analysis adjusted for the different experiments (block variable) have been reported in the manuscript.

For all the experiments, we represented individual data as dot plots with the average and appropriate error bars for each group or boxplots. Statistical methods section has been accordingly modified.

We also thank the Reviewer for pointing out the issue regarding the IF panel, which has been replaced with the correct one.

Author Response:

Reviewer #1 (Public Review):

1. Figure 1A discusses Horvath et al. multi-tissue and skin and blood clocks but more clocks could be applied. It is recommended to add Hannum et al., Levine et al. PhenoAge, Lu et al. GrimAge, and Teschendorff epitoc2 clocks.

We have applied other epigenetic clocks to our dataset and commented on their results in the first results section (see Supplementary Figure 1A). These clocks appeared to rejuvenate later in the reprogramming process, suggesting that the epigenome may be rejuvenated in stages.

1. The study reports substantial differences in DNA methylation and chronological ages, which might be due to passage number. The passage number of these cells should be listed, if possible. Additionally, there seems to be a deviation when applying EPIC chip data to the Horvath et al. clock compared to its original platform. The authors may address in the Methods section whether this inconsistency has been addressed.

We tried to use the lowest passage number available to reduce the effect of in vitro culture on epigenetic age. As such, cells were used at passage four after purchasing. The exact passage number at purchase is unfortunately not available from Thermo Fisher. These details have been added to the methods section. As for applying EPIC data to the Horvath clock, work by McEwen et al (2018) shows that DNA methylation age is highly correlated between 450K and EPIC array platforms. Nevertheless, we have applied multiple epigenetic clocks to our dataset including those trained for EPIC array data and stated this point in the methods section.

1. It is discussed that fibroblast morphology is reversed. It would be good to quantify this morphological dynamics. For instance, whether cell size undergoes transition from mesenchymal to epithelial lineages and if any reversal is observed.

This is an interesting point and we have quantified the morphological changes using confocal microscopy and measuring a ratio of roundness (the maximum length divided by the perpendicular width) of individual cells before, during and after maturation phase transient reprogramming (MPTR). Cells became temporarily rounder during MPTR (lower ratio) and then returned to an elongated state (higher ratio) which matched that of the starting fibroblasts (Figure 1D).

1. The findings relate to cells >39 years old. Would the same significant effect be observed in younger cells?

The effect of MPTR on cells of other ages (younger or older) is an interesting question (also raised by reviewer 3), but we feel it is beyond the scope of the current study. We have examined this idea in more detail in the discussion section.

1. Citation 32 should be updated. Also, are there any common genes responsible for both rejuvenation and transient reprogramming?

Citation 32 has been updated to the published article. We are not here able to distinguish between genes responsible for cellular rejuvenation relative to genes responsible for iPSC reprogramming. Indeed, the required genes for each process may be (partially) overlapping or unique. A number of transcriptional programs are activated by the Yamanaka factors, and it may be possible to disentangle these in the future to determine which genes are required for rejuvenation and which are required for reprogramming.

1. Figure 1F (the PCA figure) has a disproportional percentage of PC1 and PC2. As PC1 represents the reprogramming trajectory, does PC2 have any obvious biological meaning?

PC2 is composed of CpG sites that are temporarily hypermethylated or hypomethylated during reprogramming. These CpG sites are near genes that are involved in asymmetric protein localisation (according to gene ontology enrichment). We have included these observations in the results section.

1. Of the cells that failed to reprogram, do they undergo cellular senescence? What are their predicted ages?

Cells that fail to reprogram appear to remain fibroblast like (transcriptionally and epigenetically) and their epigenetic ages are unchanged (Figures 1A, 1D, 1F and 4B). The cell cultures continued to replicate for several weeks following the MPTR process with no obvious cellular senescence beyond what is usually observed in cultures of growing primary fibroblasts.

1. It would be interesting to investigate multiple rounds of transient reprogramming, and the maximum number rounds that could be achieved.

The effect of multiple rounds of MPTR is an interesting question as this may enhance the magnitude of rejuvenation. It is our view that this is beyond the scope of this manuscript, however, we have discussed this idea in the discussion section.

1. Ohnishi et al. 2014 could be cited as a key article, which should not be missed when discussing the oncogenicity of these genes.

The Ohnishi et al 2014 article has been cited in the discussion section.

1. There are only 6 rejuvenation genes overlapping in figure 4f. Would DNAm age be reversed if all 6 genes are overexpressed? Would it erase cell identity?

The genes in figure 4F have both rejuvenated levels of expression and DNA methylation, however, these genes are likely to be downstream of rejuvenation pathways as they are not known to possess transcription factor activity. As a result, upregulating and downregulating these genes as appropriate may not recapitulate the effects of reprogramming induced rejuvenation. In addition, there may be further overlaps that are not captured due to the limited CpGs covered by the DNA methylation array.

Reviewer #3 (Public Review):

In this manuscript, the authors investigate the potential of cellular reprogramming for the rejuvenation of age-associated phenotypes in human fibroblasts. Importantly, compared to previous studies in this field, the authors go one step further in the degree of induction of cellular reprogramming by expressing the reprogramming factors for a longer time until the maturation phase (MPTRs). Using this approach, they demonstrate not only the rejuvenation of fibroblasts at the transcriptional and epigenetic level but also the restoration of cellular identity following partial dedifferentiation. First, the authors showed that DNA methylation age is progressively decreased following the expression of the Yamanaka factors using a doxycycline inducible lentiviral system. In addition, they demonstrate that although fibroblasts transiently lose their identity during reprogramming to the maturation phase (transient reprogramming intermediate), this identity is recovered after the expression of the factors has been terminated following doxycycline withdrawal. Subsequently, analysis of DNA methylation at promoters and enhancers associated with fibroblast identity, reveals what they authors refer to as epigenetic memory, which might be responsible for the restoration of fibroblast identity following termination of transient reprogramming. Lastly, the authors elegantly demonstrate the rejuvenation of human fibroblasts following reprogramming at the transcriptional and epigenetic level using clocks based on these analyses, as well as the restoration of epigenetic marks and expression of dysregulated genes associated with fibroblast function.

This is very interesting manuscript that follows up on previous studies demonstrating the amelioration of age-associated phenotypes by cellular reprogramming. Although the concept presented in the manuscript is not completely novel, the authors try to go one step further by investigating the rejuvenation of aging phenotypes and recovery of cellular identity following a more extensive and longer reprogramming protocol. This manuscript elegantly reinforces the potential of cellular reprogramming for the rejuvenation of aging and proposes a hypothesis for the restoration of cellular identity after cellular reprogramming based on the existence of a certain degree of epigenetic memory in the cells. This manuscript will be of interest to scientist working in cellular reprogramming, aging and epigenetics. Nevertheless, before publication the authors would need to address the points stated below:

Major points:

• The timeline of induction and termination of cellular reprogramming by addition and withdrawal of doxycycline is not very clear across the manuscript. This is a critical aspect of the manuscript that should be better explained at the beginning of the results as well as in the methods section. Specifically, the authors only refer to the time of analysis following withdrawal of doxycycline in the legend of Figure 1B. Even there, the authors mentioned that "Sorted cells were also further cultured and grown in the absence of doxycycline for at least four weeks". The precise timeline of induction and termination of reprogramming by addition and withdrawal of doxycycline is critical for the whole message of the manuscript and therefore should be explained in much more detail. How long after doxycycline withdrawal were the transient reprogrammed fibroblasts analyzed?

The amount of time that doxycycline was withdrawn has been further clarified in results and methods sections. This was 4 weeks in the first experiment and 5 weeks in the second experiment. Cells had returned to fibroblast morphology by four weeks in the second experiment, however, they needed to be further expanded to generate enough material for downstream analyses.

• In the same line, the authors described in the methods section that transient reprogrammed sorted cells were replated on irradiated mouse embryonic fibroblasts (iMEFs) in fibroblast medium without doxycycline. Were the negative control cells processed in the same way and plated on top of iMEFs? Was there any effect observed due to the growth of fibroblasts on top of iMEFs? How long were the cells cultured on top of iMEFs before culturing under normal conditions? Could the authors explain the rationale for the use of iMEFs during this protocol?

All cells (including the negative controls) were initially replated onto iMEFs after flow sorting to replicate the culture conditions before the flow sort and aid in the reattachment of cells to the culture surface. At subsequent passages, cells were replated without iMEFs. Culturing on iMEFs had no obvious effect on negative control cells, which were similar (based on transcriptome and morphology) to cells that had never been grown with iMEFs. These points have been added to the methods section.

• There is a certain degree of contradiction between the results shown in some sections of the manuscript as well as the discussion of the results. In one hand, the authors claim that reprogramming can rejuvenate fibroblasts not only at the transcriptional but also at the epigenetic level, more specifically at the level of DNA methylation, and that this rejuvenation is maintained even weeks after the induction of reprogramming has stopped. On the other hand, the authors propose that epigenetic memory based on the absence of changes in DNA methylation in promoters and enhancer of fibroblasts-related genes allow the restoration of cellular identity following reprogramming. Why epigenetic age does not display this memory? Why some regions will maintain DNA methylation memory but the site used for the analysis of epigenetic age by DNA methylation show changes in methylation status and therefore rejuvenation? The authors should discuss in more detail this important aspect of their data.

This is a very interesting point. Cell identity CpG sites (at fibroblast specific enhancers) and age-associated CpG sites (used to calculate epigenetic age) are distinct. In addition, DNA methylation has different dynamics at different times during reprogramming, with cell identity CpG sites changing methylation during the stabilisation phase, and age-associated CpG sites changing methylation during the maturation phase. This suggests these sites may be regulated by different mechanisms. In addition, methylation changes at age-associated CpG sites include both gain and loss of methylation, implying these are targeted methylation changes rather than global changes. These points have been highlighted in the discussion section.

• In Figure 3A the changes induced by reprogramming in the PC2 direction look orthogonal to the aging changes observed in PC1. Could the authors maybe use a more stringent criteria for the selection of age-related genes. How do they explain the direction of these changes? In the same line, have the authors tested the effect of MPTRs in young fibroblasts? Could young fibroblasts be included in Figure 3C?

Our method for identifying age-associated genes is already quite stringent as we have applied Bonferroni multiple testing correction to the p values generated by the Pearson correlation analysis.

We have not yet attempted MPTR on young fibroblasts, this is certainly an interesting future direction but we feel it is beyond the scope of the current study. Instead, we have discussed this idea in the discussion section.

Unfortunately, we cannot include young fibroblasts in figure 3C as they have been included in the training dataset for the transcription clock.

• Based on the standard protocols used for the culture of fibroblasts using culture medium containing fetal bovine serum (FBS), I hypothesis that the recovery of cellular identity following reprogramming is mainly due to differentiation signals coming from factors present in the medium. For these reasons, knockout serum (KSR) is used at later stages (day 8) of reprogramming to allow generation of iPSCs. The authors should rule out the possibility that recovery of fibroblast identity is due to the culture of reprogramed fibroblasts in FBS containing medium. For this purpose, the authors should test whether the fibroblast identity can be recovered following doxycycline withdrawal by culturing the cell in KSR or 1% FBS containing medium instead of 10% FBS. This is a very important concept for the message that the manuscript tries to communicate regarding an epigenetic memory responsible for the recovery of fibroblast identity.

The effect of FBS in promoting the return to fibroblast identity is an interesting possibility. As mentioned above in response to the essential revisions, we attempted to investigate this by growing cells in fibroblast medium containing 10% KSR instead of 10% FBS after withdrawal of doxycycline, however, KSR containing medium was unable to support long term culture of fibroblasts. In addition, we examined the effect of 1% FBS on fibroblasts and found that their growth rate was substantially impeded, which would be major confounder.

Minor points: - The authors claim that their maturation phase transient reprogramming protocol (MPTRs) induces further rejuvenation compared to previous studies because of the use of a longer induction timeline. Nevertheless, the authors mentioned that cells took around 50 days to reach a fully pluripotent state. This is a very long timeline to reach pluripotency compared to previous studies inducing reprogramming in mouse or human fibroblasts where typically iPSCs can be generated after 2 or 3 weeks following expression of the reprogramming factors. In the same line, secondary systems based on the use of cells isolated from transgenic mice carrying a cassette for the expression of Yamanaka factors have been shown to be very rapid and efficient in the generation of iPSCs. For these reasons, the authors should not use during their discussion a direct comparison with previous studies based just on time of induction since it is possible than systems with a more efficient or higher expression of the reprogramming factors and therefore a much more rapid alteration of cell fate have been used in previous studies.

We could isolate iPSCs that could be cultured without doxycycline earlier than this at 30 days of reprogramming. However, we analysed iPSCs after 50 days of reprogramming to ensure the stabilisation phase had been completed and donor memory was erased. We agree that other reprogramming systems can achieve pluripotency faster than lentiviral based systems so we have acknowledged this in the discussion section.

• In Figure 1D, principal component analysis shows "Not reprogramming" fibroblasts represented by a cross that cluster between young, old, and rejuvenated fibroblasts. What cells are the authors referring to? Are these cells represented in the diagram included in Figure 1B? Why do they cluster differently compared to the other fibroblasts?

The ‘not reprogramming cells’ in figure 1E are reference data samples from our Sendai virus reprogramming experiment that were annotated as ‘failing to reprogram’ based on surface markers. Therefore, these samples are not in figure 1B. Like the ‘failing to reprogram intermediates’, they may be expressing the Yamanaka factors, and have therefore moved along PC1 relative to fibroblasts, but they have failed to upregulate SSEA4. We have clarified this in the figure legend and methods section.

• The authors propose in the discussion that the use of transient reprogramming protocols like the one presented in the manuscript could be used in vivo to safely induce the rejuvenation of tissues and organs. Although previous studies have shown that this in fact the case, the authors should be aware that the recovery of cellular identity might be easier to achieve in vitro where differentiation signals like the ones in FBS are present during in vitro culture but not present anymore in an adult fully differentiated animal. For these reasons, the authors should be cautious when discussing the potential of in vivo application of these approaches and their safety.

This is an interesting point and we have clarified that our method may be suitable for ex vivo approaches where our method is performed on cells in vitro.

• The figure legend of Supplementary Figure 2B shows iPSC but this population is not present in the figure.

The figure legend for supplementary figure 2B has been corrected to remove the iPSC group, which the reviewer correctly noticed is not present in the heatmap.

Author Response:

Reviewer #3 (Public Review):

The authors aim to understand the functional roles of Atm transporters, a family of ABC transporters with cellular localization of mitochondria and play important roles in transition metal homeostasis. To understand their functions, the author captured the structures of Atm3 from plant Arabidopsis in several functional states by cryo-EM--inward-facing, inward-facing with substrate GSSH bound, nucleotide bound closed state and nucleotide bound outward-facing states. Although many of those functional states have been reported for Atm orthologues in other species, the authors did elegant analyses on how the rareness of cysteine residues in the transport pathways could be very important for efficient glutathione transport. Moreover, the authors systematically show the unlikelihood of capturing an ABC transporter with both substrate and nucleotides bound. Although conceptually, a functional state with substrate and nucleotides bound should be very transient to avoid backflow of the substrate, it is wonderful that the authors put in the effort to capture such state and present a systematic principal component analysis (PCA) to show it may not be possible to attain such state structurally. The usage of PCA on analyzing a plethora of ABC transporters with different functional states could be applicable to other systems. The conclusions of this paper are mostly well supported by data, with some aspects of analysis and discrepancy that need to be addressed.

1) In Figure 1, the authors report the ATPase activities of AtAtm3 are quite different in detergent and membrane environments, with a more than 10-fold decrease in basal activity from detergent to POPC containing nanodiscs. Is this composition a good representation of Arabidopsis mitochondria membrane? The nanodisc belts in Figure S4 looks quite tight. Could that contribute to the decrease in ATPase activity? In one of the papers you cited, Schaedler et. al, 2014, ATM3's activity is not stimulated by GSH versus in your data, 10mM GSH strongly stimulated AtAtm3. How would you explain the discrepancy? In terms of data analysis, the fit for 10mM GSH and 2.5mM GSSG ATPase activity in nanodiscs is poor visually, the addition of goodness of the fit in the figure could help the reader to assess the real quality of the data.

In our experience, the ATPase rates of ABC transporters are highly dependent on the precise solubilization conditions, particularly for detergents as some detergents/detergent combinations are stimulatory, while others are inhibitory. In addition, the POPC used in the nanodiscs might not be the best substitute of the natural lipids that are found in the mitochondrial membrane. Given the variability that has been observed in ATPase activities for different solubilization conditions, we do not know which condition more likely reflects the true physiological activity. (As an aside, we would have thought that basal ATPase rate should be zero in the absence of transported substrate to avoid uncoupled (and presumably wasteful) ATPase activity, but this has been rarely reported).

The Schaedler paper used GSH at two concentrations, 1.7 and 3.3 mM, to test the stimulation of ATPase activity. In our study, we used 10 mM GSSG for the ATPase activity assay to be consistent with our previous studies on NaAtm1. This discrepancy presumably reflects concentration differences utilized in these studies, and other experimental conditions including the nature of the protein construct. Different expression systems were used in the two studies, Schaedler et al employed L. lactis, while we used E. coli; it is possible that different lipids co-purified with the proteins that could influence the ATPase activity. In addition, we used a truncation with an 80-residue deletion, while Schaedler et al utilized a 60-residue truncation; our initial characterization of various constructs showed that the 80-residue deletion had a higher ATPase activity, although we did not characterize these differences in detail – certainly not for publication. While both studies used AtAtm3 solubilized in DDM, it is possible that there are still differences in the solubilization conditions reflecting the precise way in which detergents are introduced. We have added a sentence noting this discrepancy in the GSH stimulation results, without ascribing a particular mechanism.

We have added the goodness of fit to the figure.

2) There are a couple of structural studies on Atm transporters available to date, and the authors did a couple of overall structural comparisons in Figure S3 and S5. However, it is still not clear what exactly those systems are similar or dissimilar, and what are new structural insights gained with these structures. It could be helpful to compare the substrate-binding sites side by side or have a cartoon representation of different functional states in different systems. The authors brought this reader's attention to "a ~20 amino acid loop between TM1 and Tm2 of AtAtm3 that would be positioned in the intermembrane space and is absent from the structures of ScAtm1 and NaAtm1" without further explanation. Does this loop have any proposed functional roles? Is it present in other Atm or ABC transporters?

We included a new figure, Figure S4, comparing different homologs, AtAtm3, human ABCB7 (an Alphafold model), human ABCB6, yeast Atm1 and prokaryotic Atm1. Among these five structures, only AtAtm3 presents a loop between TM1 and TM2. A quick protein sequence blast in PubMed showed the presence of this loop in many other plant atm transporters. This long loop has not been observed in other structure we know so far, but an external helix was observed for PglK, a lipid-linked oligosaccharide flippase, and this loop has been implicated in substrate interaction (Perez et al. Nature 524, 433 (2015); doi: 10.1038/nature14953).

Author Response:

Reviewer #1 (Public Review):

In this manuscript, the authors challenge the long-standing conclusion that Orco and IR-dependent olfactory receptor neurons are segregated into subtypes such that Orco and IR expression do not overlap. First, the authors generate new knock-in lines to tag the endogenous loci with an expression reporter system, QF/QUAS. They then compare the observed expression of these knock-ins with the widely used system of enhancer transgenes of the same receptors, namely Orco, IR8a, IR25a, and IR76b. Surprisingly, they observe an expansion of the expression of the individual knock-in reporters as compared to the transgenic reporters in more chemosensory neurons targeting more glomeruli per receptor type than previously reported. They verify the expression of the knock-in reporters with antibody staining, in situ hybridization and by mining RNA sequencing data.

Finally, they address the question of physiological relevance of such co-expression of receptor systems by combining optogenetic activation with single sensillum recordings and mutant analysis. Their data suggests that IR25a activation can modulate Orco-dependent signaling and activation of olfactory sensory neurons.

The paper is well written and easy to follow. The data are well presented and very convincing due in part to the combination of complementary methods used to test the same point. Thus, the finding that co-receptors are more broadly and overlappingly expressed than previously thought is very convincing and invites speculation of how this might be relevant for the animal and chemosensory processing in general. In addition, the new method to make knock-ins and the generated knock-ins themselves will be of interest to the fly community.

We thank the reviewer for their enthusiasm and support of our work!

The last part of the manuscript, although perhaps the most interesting, is the least developed compared to the other parts. In particular, the following points could be addressed:

• It would be good to see a few more traces and not just the quantifications. For instance, the trace of ethyl acetate in Fig. 6C, and penthyl acetate for 6G.

Thank you for the suggestion. We have added a new figure supplement (Figure 6-Figure Supplement 3) with additional example traces for all odorants from Figure 6 for which we found a statistically significant difference between the two genotypes (Ir25a versus wildtype).

• In Fig. 4D, the authors show the non-retinal fed control, which is great. An additional genetic control fed with retinal would have been nice.

For these experiments, we followed a standard practice in Drosophila optogenetics to test the same experimental genotype in the presence or absence of the essential cofactor all-trans-retinal. This controls for potential effects from the genetic background. It is possible our description of these experiments was unclear (as also suggested by comments from Reviewer 2). As such, we have clarified our experimental design for the optogenetic experiments in the revised manuscript:

Modified text: “No light-induced responses were found in control flies, which had the same genotype as experimental flies but were not fed all-trans retinal (-ATR), a necessary co-factor for channelrhodopsin function (see Methods).” and “Bottom trace is control animal, which has the same genotype as the experimental animal but was not fed the required all-trans retinal cofactor (-ATR).”

Figure 4-Figure Supplement 1 legend: “In all optogenetic experiments, control animals have the same genotypes as the corresponding experimental animals but have not been fed all-trans retinal.”

Methods: “For all optogenetic experiments, the control flies were of the same genotype as experimental flies but had not been fed all-trans retinal.”

• It appears that mostly IR25a is strongly co-expressed with other co-receptors. The provided experiments suggest a possible modulation between IR25a and Orco-dependent neuronal activity. However, what does this mean? How could this be relevant? And moreover, is this a feature of Drosophila melanogaster after many generations in laboratories?

We share this reviewer’s excitement regarding the numerous questions our work now raises. While testing additional functional ramifications of chemosensory co-receptor expression is beyond the scope of this work (but will undoubtedly be the focus of future studies), we did expand on what this might mean in the revised Discussion section of the revised manuscript. Previously, we had raised the hypothesis that chemoreceptor co-expression could be an evolutionary relic of Ir25a expression in all chemoreceptor neurons , or a biological mechanism to broaden the response profile of an olfactory neuron without sacrificing its ability to respond to specific odors. We now extend our discussion to raise additional possible ramifications. For example, we suggest that modulating Ir25a coexpression could alter the electrical properties of a neuron, making it more (or possibly less) sensitive to Orco-dependent responses. We also suggest that Ir25a coexpression might be an evolutionary mechanism to allow olfactory neurons to adjust their response activities. That is, that most Orco-positive olfactory neurons are already primed to be able to express a functional Ir receptor if one were to be expressed. Such co-expression in some olfactory neurons might present an evolutionary advantage by ensuring olfactory responses to a complex but crucial biologically relevant odor, like human odors to some mosquitoes.

Reviewer #2 (Public Review):

In the present study, the authors: 1) generated knock-in lines for Orco, Ir8a, Ir25a, and IR7ba, and examined their expression, with a main focus on the adult olfactory organs. 2) confirmed the expression of these receptors using antibody staining. 3) examined the innervation patterns of these knock-in lines in the nervous system. 4) identified a glomerulus, VM6, that is divided into three subdivisions. 5) examined olfactory responses of neurons co-expressing Orco and Ir25a

The results of the first four sets of experiments are well presented and support the conclusions, but the results of the last set of experiments (the electrophysiology part) need some details. Please find my detailed comments below.

We thank the reviewer for their support of our work and appreciating the importance of our findings. In the revised manuscript, we now provide the additional experimental details for the electrophysiology work as requested.

Major points

Line 167-171: I wonder if the authors also compared the Orco-T2A-QF2 knock-in with antibody staining of the antenna.

We did perform whole-mount anti-Orco antibody staining on Orco-T2A-QF2 > GFP antennae (example image below). We saw broad overlap between Orco+ and GFP+ cells, similar to the palps. However, we did not include these results since quantification of these tissues is challenging for the following reasons:

1. There are ~1,200 olfactory neurons in each antenna, many of which are Orco+.
2. The thickness of the tissue makes determinations of co-localization difficult in wholemount staining.
3. Co-localization is further complicated by the sub-cellular localization of the signals: Orco antibodies preferentially label dendrites and weakly label cell bodies, while our GFP reporter is cytoplasmic and preferentially labels cell bodies. For these reasons, we focused on the numerically simpler palps for quantification. For the Ir8aT2A-QF2 and Ir76b-T2A-QF2 lines, palp quantification was not an option as neither knock-in drove expression in the palps (and the available antibodies did not work with the whole-mount staining protocol). This is why we performed antennal cryosections to validate these lines. Below is an example image of the antennal whole-mount staining in the Orco-T2A-QF2 knock-in line, illustrating the quantification challenges enumerated above.

*Co-staining of anti-Orco and GFP in Orco-T2A-QF2 > 10xQUAS-6xGFP antenna *

Lines 316-319 (Figure 4D): It would be better if the authors compare the responses of Ir25a>CsChrimson to those of Orco>CsChrimson.

The goal of the optogenetic experiments was to provide experimental support for Ir25a expression in Orco+ neurons in an approach independent to previous methods. Our main question was whether we could activate what was previously considered Orco-only olfactory neurons using the Ir25a knock-in. These experiments were not designed to determine if this optogenetic activation recapitulated the normal activity of these neurons. For these reasons, we did not attempt the optogenetic experiments with Orco>CsChrimson flies.

Line 324-326: Why the authors tested control flies not fed all-trans retinal? They should test Ir25a-T2A-QF2>QUAS-CsChrimson not fed all-trans retinal as a control.

We apologize for the confusion. The “control” flies we used were indeed Ir25a-T2AQF2>QUAS-CsChrimson flies not fed all-trans retinal as suggested by the reviewer. This detail was in the methods, yet likely was not clear. We have amended the main text in multiple locations to state the full genotype of the control fly more clearly:

Modified text: “No light-induced responses were found in control flies, which had the same genotype as experimental flies but were not fed all-trans retinal (-ATR), a necessary co-factor for channelrhodopsin function (see Methods).” and “Bottom trace is control animal, which has the same genotype as the experimental animal but was not fed the required all-trans retinal cofactor (-ATR).”

Figure 4-Figure Supplement 1 legend: “In all optogenetic experiments, control animals have the same genotypes as the corresponding experimental animals but have not been fed all-trans retinal.”

Methods: “For all optogenetic experiments, the control flies were of the same genotype as experimental flies but had not been fed all-trans retinal.”

Line 478-500: I wonder if the observed differences between the wildtype and Ir25a2 mutant lines are due to differences in the genetic background between both lines. Did the authors backcross Ir25a2 mutant line with the used wildtype for at least five generations?

Yes, the mutants are outcrossed into the same genetic background as the wildtypes for at least five generations. Please see Methods, revised manuscript: “Ir25a2 and Orco2 mutant fly lines were outcrossed into the w1118 wildtype genetic background for at least 5 generations.”

Line 1602-1603: Does the identification of ab3 sensilla using fluorescent-guided SSR apply for ab3 sensilla in Orco mutant flies. How does this ab3 fluorescent-guided SSR work?

In fluorescence guided SSR (fgSSR; Lin and Potter, PloS One, 2015), the ab3 sensilla is GFPlabelled (genotype: Or22a-Gal4>UAS-mCD8:GFP), which allows this sensilla to be specifically identified under a microscope and targeted for SSR recordings. We generated fly stocks for fgSSR identification of ab3 in all three genetic backgrounds (wildtype, Orco mutant, Ir25a mutant).

These three genotypes are described in the methods:

“Full genotypes for ab3 fgSSR were:

Pin/CyO; Or22a-Gal4,15XUAS-IVS-mcd8GFP/TM6B (wildtype),

Ir25a2; Or22a-Gal4,15XUAS-IVS-mcd8GFP/TM6B (Ir25a2 mutant),

Or22a-Gal4/10XUAS-IVS-mcd8GFP (attp40); Orco2 (Orco2 mutant).”

Line 1602-1604: There is no mention of how the authors identified ab9 sensilla.

Information on the identification of ab9 sensilla is under the optogenetics section of the methods: “Identification of ab9 sensilla was assisted by fluorescence-guided Single Sensillum Recording (fgSSR) (Lin and Potter, 2015) using Or67b-Gal4 (BDSC #9995) recombined with 15XUAS-IVS-mCD8::GFP (BDSC #32193).”

Line 1648: what are the set of odorants that were used to identify the different coeloconic sensilla?

We have added the specific odorants used for sensillar identification for coeloconic SSR in the Methods. The protocol and odorants used were:

*2,3-butanedione (BUT), 1,4-diaminobutane (DIA), Ammonia (AM), hexanol (HEX), phenethylamine (PHEN), and propanal (PROP) to distinguish coeloconic sensilla:

o Wildtype flies: Strong DIA and BUT responses identify ac2 and rule out ac4. Absence of strong AM response rules out ac1, absence of HEX response rules out ac3, absence of PHEN response further rules out ac4.

o Ir25a mutant flies (amine responses lost, so cannot use PHEN and DIA as diagnostics): Strong BUT response and moderate PROP response identify ac2 and rule out ac4. Absence of strong AM response rules out ac1, absence of HEX response rules out ac3. Ac4 is further ruled out anatomically based on sensillar location compared to ac2.

Revised text: “Different classes of coeloconic sensilla were identified by their known location on the antenna and confirmed with their responses to a small panel of diagnostic odorants: in wildtype flies, ac2 sensilla were identified by their strong responses to 1,4-diaminobutane and 2,3-butanedione. The absence of a strong response to ammonia was used to rule out ac1 sensilla, the absence of a hexanol response was used to rule out ac3 sensilla, and the absence of a phenethylamine response was used to rule out ac4 sensilla. In Ir25a mutant flies in which amine responses were largely abolished, ac2 and ac4 sensilla were distinguished based on anatomical location, as well as the strong response of ac2 to 2,3-butanedione and the moderate response to propanal (both absent in ac4). Ac1 and ac3 sensilla were excluded similarly in the mutant and wildtype flies. No more than 4 sensilla per fly were recorded. Each sensillum was tested with multiple odorants, with a rest time of at least 10s between applications.

Reviewer #1 (Public Review):

In this manuscript, Yang et al. trained monkeys to play the classic video game Pac-Man and fit their behavior with a hierarchical decision making model. Adapting a complex behavior paradigm, like Pac-Man, in the testing of NHP is novel. The task was well-designed to help the monkeys understand the task elements step-by-step, which was confirmed by the monkeys' behavior. The authors reported that the monkeys adopted different strategies in different situations, and their decisions can be described by the model. The model predicted their behavior with over 90% accuracy for both monkeys. Hence, the conclusions are mostly supported by the data. As the authors claimed, the model can help quantify the complex behavior paradigm, providing a new approach to understanding advanced cognition in non-human primates. However, several aspects deserve clarification or modification.

1. The results showed that the monkeys adopted different strategies in different situations, which is also well described by the model. However, the authors haven't tested whether the strategy was optimal in a given situation.

Our approach to analyze monkeys’ behavior is not based on optimality. Instead, we centered around the strategies and showed that they described the monkeys’ behavior well. The model and its fitting process does not assume the monkeys were optimizing for something. Nevertheless, the fitting results suggested that the strategies that the monkeys chose were rational, which suggests validity of our model. As we have pointed out above, optimality is hard to define in such a complex game. In particular, most of the game is about collecting pellets, strategies that are only used in a small portion of the game can be ignored when searching for optimal solutions. We feel that further analyses on the issue of optimality would dilute the center message of the paper and choose not to include them here.

According to the results, the monkeys didn't always perform the task in an optimal way, as well. Most of the time, the monkeys didn't actively adopt strategies in a long-term view. They were "passively" foraging in the task: chasing benefit and avoiding harm when they were approached. This "benefit-tending, harm-avoiding" instinct belongs to most of the creatures in the world, even in single-cell organisms. When a Paramecium is placed in a complex environment with multiple attractants and repellents, it may also behave dynamically by adopting a linear combination of basic tending/avoiding strategies, although in a simpler way. In other words, the monkeys were responding to the change of environment but not actively optimizing their strategy to achieve larger benefits with fewer efforts. The only exception is the suicides. Monkeys were proactively taking short-term harms to achieve large benefits in the future.

One possible reason is that the monkeys didn't have enough pressure to optimize their choices since they will eventually get all the rewards no matter how many attempts they make. The only variable is the ghosts. Most of the time, the monkeys didn't really choose between different targets/ strategies. They were making choices between the chasing order of the options, but not the options themselves. It is similar to asking a monkey to choose either to eat a piece of grape or cucumber first, but not to choose one and give up the other one. A possible way to avoid this is to stop the game once the ghost catches the Pac-Man or limit each game's time.

The game is designed to force the players to make decisions quickly to clear the pellets, otherwise the ghosts would catch Pac-Man. Even in the monkey version of the game where the monkeys always get another chance, Pac-Man deaths lead to long delays with no rewards. They will not be able to complete the game if they do not actively plan their route, especially in the late stage when they must reach the scarcely placed dots while escaping from the ghosts. In addition, we provided additional rewards when a maze is cleared in fewer rounds (20 drops if in 1 to 3 rounds; 10 drops if in 4 to 5 rounds; and 5 drops if in more than 5 rounds), which added motivation for the monkeys to complete a game quickly.

The monkeys’ behavior also suggested that they did not just adopt a passive strategy. Our analyses of the planned attack and suicide behavior clearly demonstrated that the monkeys actively made plans to change the game into more desirable states. Such behavior cannot be explained with a passive foraging strategy.

2. It is well known that the value of an element is discounted by time and distance. However, in the model, the authors didn't consider it. A relevant problem will be the utility of the bonus elements, including the fruits and scared ghosts. Their utilities were affected not only by their value defined by the authors but also by effects, including their novelty and sense of achievement when they were captured, as the ghosts attracted relatively much more attention than the other elements (considering the number is 2 for them, see in figure 3E).

These are good points, and our strategies could be built with more complexity to account for other potential factors. However, we focused our investigation on how to account for monkeys’ behavior with a set of strategies. A set of simple strategies with a small number of parameters would make a strong argument.

Using a complex game such as Pac-Man allows us to investigate all of these interesting cognitive processes. We can certainly look at them in the future.

3. The strategies are not independent. They are somehow correlated to each other. It may result in, in some conditions, false alarming of more strategies than the real, as shown in figure 2A.

We have computed the Pearson correlations between the action sequences chosen with each basis strategy within each coarse-grained segment determined by the two-pass fitting procedure. As a control, we computed the correlation between each basis strategy and a random strategy, which generates action randomly, as a baseline. Most strategy pairs' correlations were lower than the random baseline. The results were now included in Supplementary (Appendix Figure 3).

Sometimes two strategies may give exactly the same action sequence in a game segment. To deal with this problem, now we include an extra step when we fit the model to the behavior, which was described in Methods:

“To ensure that the fitted weights are unique (Buja et al., 1989) in each time window, we combine utilities of any strategies that give exactly the same action sequence and reduce multiple strategy terms (e.g., local and energizer) to one hybrid strategy (e.g., local+energizer). After MLE fitting, we divide the fitted weight for this hybrid strategy equally among the strategies that give the same actions in the time segments.“

Moreover, as the reviewer correctly reasoned, correlations between the strategies would yield possibly more strategies. However, our finding is that the monkeys were using a single strategy most of the time. This possible false alarm would go against our claim. Our conclusions stand despite the strategy correlations.

It is hard to believe that a monkey can maintain several strategies simultaneously since it is out of our working memory/attention capacity.

Exactly, and we are among the first to quantitatively demonstrate that the monkeys’ mostly relied on single strategies to play the game.

Reviewer #2 (Public Review):

In this intriguing paper, Yang et al. examine the behaviors of two rhesus monkeys playing a modified version of the well-known Pac-Man video game. The game poses an interesting challenge, since it requires flexible, context-dependent decisions in an environment with adversaries that change in real time. Using a modeling framework in which simple "basic" strategies are ensembled in a time-dependent fashion, the authors show that the animals' choices follow some sensible rules, including some counterintuitive strategies (running into ghosts for a teleport when most remaining pellets are far away).

I like the motivation and findings of this study, which are likely to be interesting to many researchers in decision neuroscience and animal behavior. Many of the conclusions seem reasonable, and the results are detailed clearly. The key weakness of the paper is that it is primarily descriptive: it's hard to tell what new generalizable knowledge we take away from this model or these particular findings. In some ways, the paper reads as a promissory note for future studies (neural or behavioral or both) that might make use of this paradigm.

I have two broad concerns, one mostly technical, one conceptual:

First, the modeling framework, while adequate, is a bit ad hoc and seems to rely on many decisions that are specific to exactly this task. While I like the idea of modeling monkeys' choices using ensembling, the particular approach taken to segment time and the two-pass strategy for smoothing ensemble weights is only one of many possible approaches, and these decisions aren't particularly well-motivated. They appear to be reasonable and successful, but there is not much in the paper to connect them with better-known approaches in reinforcement learning (or, perhaps surprisingly, hierarchical reinforcement learning) that could link this work to other modeling approaches. In some ways, however, this is a question of taste, and nothing here is unreasonable.

Thanks for the suggestion. In the new revision, we include a linear approximate reinforcement learning model (LARL) (Sutton, 1988; Tsitsiklis & Van Roy, 1997). The LARL model shared the same structure with a standard Q-learning algorithm but used the monkeys’ actual joystick movements as the fitting target. The model, although computationally more complex than the hierarchical mode, achieves a worse fitting performance.

Second, there is an elision here of the distinction between how one models monkeys' behavior and what monkeys can be said to be "doing." That is, a model may be successful at making predictions while not being in any way a good description of the underlying cognitive or neuroscientific operations. More concretely: when we claim that a particular model of behavior is what agents "actually do," what we are usually saying is that (a) novel predictions from this model are born out by the data in ways that predictions from competing models are not (b) this model gives a better quantitative account of existing data than competitors. Since the present study is not designed as a test of the ensembling model (a), then it needs to demonstrate better quantitative predictions (b).

We concede to the point that our model, while fitting to the behavior well, does not directly prove that the monkeys actually solved the task in this way. The eye movement and pupil dilation analyses partly addressed this issue, as their results were consistent with what one would expect from the model. We also hope future recording experiments will provide neural evidence to support the model.

But the baselines used in this study are both limited and weak. A model crafted by the authors to use only a single, fixed ensemble strategy correctly predicts 80% of choices, while the model with time-varying ensembling predicts roughly 90%. This is a clear improvement and some evidence that *if* the animals are ensembling strategies, they are changing the ensemble weights in time. But there is little here in the way of non-ensemble competitors. What about a standard Q-learning model with an inferred reward function (that is, trained to replicate monkeys' data, not optimal performance). The perceptron baseline as detailed seems very poor as a control given how shallow it is. That is, I'm not convinced that the authors have successfully ruled out "flat" models as explanations of this behavior, only found that an ensembled model offers a reasonable explanation.

We hope the new LARL model provides a better baseline control as a flat model. It performs better than the perceptron, yet much worse than our hierarchical model. Yet, we must point out that any hierarchical models can be matched in performance with a flat model in theory (Ribas-Fernandes et al., 2011). The advantage of hierarchical models mainly lies in their smaller computational cost for efficient planning. Even in a much simpler task such as a four-room navigation task, a hierarchical model can plan much faster than a flat model, especially under conditions with limited working memory (M. Botvinick & Weinstein, 2014). Our Pac-Man task contains an extensive feature space while requiring real-time decision-making. The result is that a reasonably performing flat model would go beyond the limits of the cognitive resources available in the brain. Even for a complex flat model such as Deep Q-Network (it can be considered to be similar a flat model since it does not explicitly plan with temporal extended strategies (Mnih et al., 2015)), the game performance is much worse than a hierarchical model (Van Seijen et al., 2017). The performance of the monkeys was unlikely to be achieved with a flat model. In addition, we trained the monkeys by introducing the game concepts gradually, with each training stage focusing on certain game aspects. The training procedure may have encouraged the monkeys to generalize the skills acquired in the early stages and use them as the basis strategies in the later training stages when the monkeys faced the complete version of the Pac-Man task.

Reviewer #3 (Public Review):

Yang and colleagues present a tour de force paper demonstrating non-human primates playing a full on pac-man video game. The authors reason that using a highly complex, yet semi controlled video game allows for the analysis of heuristic strategies in an animal model. The authors perform a set of well motivated computational modeling approaches to demonstrate the utility of the experimental model.

First, I would like to congratulate the authors on training non-human primates to perform such a complex and demanding task and demonstrating that NHP perform this task well. From previous papers we know that even complex AI systems have difficulty with this task and extrapolating from my own failings in playing pac-man it is a difficult game to play.

Overall the analysis approach used in the paper is extremely well reasoned and executed but what I am missing (and I must add is not needed for the paper to be impactful on its own) is a more exhaustive model search. The deduction the authors follow is logically sound but builds very much on assumptions of the basic strategy stratification performed first. This means that part of the hierarchical aspect of the behavioral strategies used can be attributed to the heuristic stratification nature of the approach. I am not trying to imply that I do not think that the behavior is hierarchically organized but I am implying that there is a missed opportunity to characterize that hierchical'ness (maybe in a graph theoretical way, think Dasgupta scores) further.

All in all this paper is wonderful. Congratulations to the authors.

We thank the reviewer for the encouraging comments. We have included a new flat model in the new revision for comparison against our hierarchical model and discussed other experimental evidence to support our claim.

Author Response:

Reviewer #1:

The authors have developed a method (scQuint) for analyzing alternative splicing using scRNA-Seq. The method performs both visualization and clustering and also differential analysis, although the differential analysis modeling is not novel and has been adopted from a bulk RNAseq method (Leafcutter) and applied to pseudobulked data by grouping reads from cells within a cell type. Therefore, the method is not able to capture the true splicing variation at the single-cell level. Also, authors have only applied the method to Smart-Seq2 data and therefore it is not clear if their method is applicable to 10x data which has much higher throughout compared to Smart-Seq2 and is able to capture rare cell types but is more challenging for splicing analysis due to its 3' bias and lower coverage.

Authors have applied their method to two mouse scRNA-Seq datasets: Tabula muris (from multiple tissues) and BICCN (from brain) and provided a comprehensive analysis of alternative splicing in mouse cell types. They have found that cell-type-specific splicing is ubiquitous in mouse cell types and splicing variation augments the total gene expression variation as there is little overlap between top differentially spliced and differentially expressed genes. They also found that a considerable fraction of cell-type-splicing events involve novel transcripts. They applied predictive machine learning models to show that cell types can be well distinguished by the splicing information and identifies relationships between the splicing changes in known splicing factors and the splicing changes in their target genes.

The authors provide several biological findings regarding alternative splicing at cell-type-level and have shown how scRNA-Seq (despite being underutilized for splicing analysis so far) can expand our understanding of splicing mechanisms in single cells. Additionally, authors have made their data publicly available through interactive data browsers that can serve as a resource tool for future studies.

We thank reviewer 1 for their thoughtful consideration of our manuscript and for their comments and recommendations. We wish to briefly address three remarks made in the reviewer’s summary. First, although our differential splicing model is based on that of LeafCutter, we make several substantive changes for the setting of single-cell experiments which affect its scalability and statistical performance. Furthermore, we do not use pseudobulked data with the exception of our splicing factor regression analysis at the end of the results section. These facts have been made more clear in the manuscript. Finally, we discuss the challenges of working with 10x data in comment 5 response.

Author Response:

Reviewer #2:

This study examined the effect of land-use change on soil animal food webs in Sumatra, Indonesia using datasets of stable isotopes and metabolisms of 23 animal groups. They found that the calibrated 13C values of soil animals are generally higher in the rainforests compared to those in the plantations, and multidimensional metrics of the soil animal community (e.g., isotopic dispersion) differed across the land-use types. They also showed that the community food web metrics are influenced by environmental variables (e.g., soil pH and tree density and species richness. These results demonstrate that the conversion of rainforest to plantations could affect not only the above- but also the below-ground components of the ecosystems and likely the ecosystem functions.

Strength:

This is the first attempt to investigate the effect of land-use changes in soil food web structure with stable isotope and metabolism datasets. This study is based on a great amount of data of high quality (biomass and metabolism rates, high taxonomic resolution for some taxa) and collected from four land-uses, which were achieved through a well-organized project. It is also noteworthy that the measurement of stable isotopes of tiny soil invertebrates required the improvement of the continuous flow isotope ratio mass spectrometer. The collaborations among international groups and across different disciplines shows a direction to be followed in studies on global environmental issues.

Weakness:

The only weakness of this study is that the isotopic measurements were conducted on the high-rank taxonomic group level (order or family) based on an assumption that "the high-rank animal taxa in soil are generally consistent in their isotopic niches and reflect the trophic niches of species in most taxa" (L164-165). Although I am not sure if I understand this assumption correctly, the authors consider that different species in some taxa should have similar isotopic (trophic) niches. If so, it is difficult to accept this assumption because previous studies have already reported large variations in C and N isotope ratios (~ 6 permil) within the order or family (e.g., oribatids, collembola, ants, and earthworms). The isotopic variation exceeds those observed across the land-use types. Because of the considerable variation within the high-rank taxa, which species were included in the mixed samples (only 3 to 15 individuals for each taxonomic group, Line 176) should have affected the present results and thus the key claims in this paper. Therefore, it would be necessary to scrutinize whether the samples used for the isotopic analyses could represent the high-rank taxa and whether the isotopic values presented in this study are understandable in light of the previous knowledge of their biology. I suppose that this could be a main focus of this study. Based on the compiled isotopic datasets, previous work (Potapov et al. 2019, Funct. Ecol.) successfully shows that the high-rank taxa can be treated as trophic nodes in food web studies. However, the work does not demonstrate that the isotopic values of relatively few individuals of a high-rank taxon could be used as the representative values of the taxon.

For the justification of using stable isotopes of high-ranks taxonomic groups please see our response to this point in ‘Essential Revisions’ above. For Oribatids and Collembola we had 15 individuals, and we include 829 samples to represent Oribatida, and 202 samples to represent Collembola. Soil ants and earthworms were typically represented by a single (few) dominant species per site in our study, which were represented with our measurements (see https://link.springer.com/10.1007/s10530-021-02539-y for earthworms and https://iopscience.iop.org/article/10.1088/1755-1315/771/1/012031 for ants).

Author Response:

Reviewer #1:

In this work Warneford-Thomson et al. developed an approach for surveillance screening for SARS-CoV-2, which involves the isothermic amplification of a region of the SARS-CoV-2 nucleocapsid gene using RT-LAMP, followed by detection with deep sequencing. High-throughput and cost effectiveness is achieved by two sets of barcodes that allow up to about 37,000 samples to be combined into one deep sequencing run. Moreover, the authors demonstrate they can do the detection from saliva collected on paper, which should make sample collection easier.

The main strength of the work lies in the technical aspects, including setting up multiple controls such as a detection of a human gene, and multiplexing with detection of the influenza virus.

The main weakness is that there are multiple other papers either published or archived that use RT-LAMP for SARS-CoV-2 detection, deep sequencing for SARS-CoV-2 detection, or both. These are cited in the current work, which is very well written and presented. Whether this method is better than the others which have the same aim of developing cost-effective and high-throughput detection is not conclusively demonstrated as only 8 clinical saliva samples are examined.

We do not wish to claim that our method is better than the others. We think it has advantages and disadvantages and certainly it should be further optimized before scaling it up to population level. We have added these considerations to the text (lines 376–80).

Furthermore, the requirement for deep sequencing and batching many samples for cost-effectiveness will, in most situations, greatly increase turn-around time. This will make surveillance much less effective, since by the time results are fed back, the asymptomatically infected individual would have had more opportunity to transmit the infection to others.

We argue that time from sample to result is a mostly a function of logistics and not of the method. With proper set ups the time from sample collection to results could be < 16 hours, which would be compatible with population-level surveillance. We added these considerations to the text.

However, the deep sequencing step may be very useful for surveillance of circulating SARS-CoV-2 spike sequences to detect emerging variants within a population, provided this method can be modified to do it.

We agree and we mention this possibility in the discussion.

Reviewer #2:

In 'COV-ID: A LAMP sequencing approach for high-throughput co-detection of SARS-CoV-2 and influenza virus in human saliva', Warneford-Thomson et al. present a novel methodology to perform large numbers of COVID-19 tests in parallel. Their approach takes unprocessed saliva and requires only a small number of experimental steps before the results are sequenced overnight to generate many thousands of results. This straightforward experimental design should allow the protocol to be expanded to a number of settings where population-level monitoring is required in order to contain outbreaks and reduce transmission. In this paper, the authors demonstrate the efficacy of their approach and perform a large number of benchmarking experiments to quantify its sensitivity, specificity and limitations of detection. They are able to detect artificially created infections (spike-ins) with as low as 5 virions per µL and all clinically available samples agreed with the standard RT-qPCR test. This method can detect both SARS-CoV-2 and Influenza infection and can also be applied to saliva samples which have been collected on filter paper, a strategy which will further simplify the testing regime.

The authors have spent much time testing this approach but these have largely been limited to analysing artificially created infections. The only results which were obtained were from eight clinically derived samples which are presented in Figure 2E. Although all results from this approach agreed with the standard clinical test this is a small number of tests compared to the total number of tests which are reported in this paper. It is also only a small proof-of-principle experiment to justify a quick rollout of this technology.

We have now performed COV-ID on 120 additional patient samples (new Figure 2-figure supplement 2). These new results are described in the text.

The potential for this technology to perform rapid, high-throughput SARS-CoV-2 testing alongside the potential for very low sequencing costs (Figure 4G) is impressive. It is noted in the manuscript that this will require 96 unique barcodes but only 32 are tested here. All but three of these 32 work for the SARS-CoV-2 N2 primers and required STATH control but how will the remaining 67 primers be derived (i.e. is it realistic that this can be made to work to deliver the promise of this approach)?

The current COV-ID patient barcodes are 5 base pairs long. This allows for 4^5 = 1,024 combinations. Out of an abundance of caution, we excluded barcodes with homology to the reverse complement of the RT-LAMP primers used in any of the experiments (i.e. primers for SARS-CoV-2 N2, STATHERIN, ACTIN, and influenza virus) and then selected a set of 32 with Hamming distances of at least 2 from each other. This is now described more in detail in the methods.

Regarding the numbers, out of 1,024 5-bp barcodes, 404 were removed due to homology, leaving 620. Of these, we could find at least 163 with Hamming distance ≥ 2 from each other. Even with a substantial failure rate, this should allow for 96 working barcodes. If we had only considered clashes with N2 and STATHERIN primers, the number of available barcodes would be substantially higher.

Overall, this is an interesting paper which has very clear real-world application to helping to defeat the ongoing COVID-19 pandemic, but some extra validations are needed to fully demonstrate its performance in clinical and/or public health settings.

Author Response:

Reviewer #1:

The experiments are well designed, generally well controlled, and carefully conducted, and are thoughtfully and appropriately discussed. The authors make conclusions that are well supported by their results.

When describing the aptamer knockdown of the PPS, the authors explain that the western blot was too noisy for monitoring the knockdown, which is frustrating for the reader and must have been frustrating for the authors. The authors instead counter-intuitively use qRT-PCR to monitor the transcript abundance of the PPS transcript in the aptamer system - this aptamer system is thought to be a modifier of protein, not transcription or transcript abundance. The authors describe that this has been seen once before (using aptamer knockdown of PfFis1), and the authors of that study speculate that the TetR-DOZI aptamer might be degrading the target mRNA. This is a plausible explanation, but it isn't quite clear from the description how this experiment was performed. The authors explain that the knockdown parasites grew normally for three days, but the parasites may be becoming sicker over this period. It's therefore possible that the decrease in PPS mRNA abundance is a product, rather than a cause of the growth defect. Sick or dying parasites could plausibly impact the PPS differently to the two chosen controls, particularly since both control genes chosen have substantially longer half-lives than the PPS mRNA (according to the Shock and DeRisi datasets). I therefore I suggest that this experiment be performed in an IPP rescue scenario (where the parasites aren't dying) with biological replicates. There is no explanation of the replicates here, but the error bars in 6C are implausibly small for real biological replicates.

To address these concerns, we have added western blot data showing down-regulation of PPS expression in -aTc +IPP conditions, relative to a loading control. We have also repeated the growth assay and RT-qPCR experiment (in biological triplicate) under IPP-rescue conditions. Parasites samples harvested on day 3 of the IPP-rescue assay were analyzed by RT-qPCR and show reduced PPS mRNA abundance that is similar to (and slightly lower than) that observed without IPP supplementation. This similarity is not surprising to us, since the day 3 harvest in the original growth assay (without IPP) was 3 days before observing a parasite growth defect in -aTc conditions. With respect to the mechanism of transcript loss in the aptamer/TetR-DOZI system, the fate of transcripts in this system has not been investigated in depth. However, DOZI is believed to target bound mRNA to P-bodies, which are a known site of mRNA degradation in cells. We have unpublished data with multiple parasite proteins tagged with the aptamer/TetR-DOZI system. In all cases, we see strong reductions in mRNA abundance in -aTc conditions, suggesting that such decreases are a general property of this knockdown system.

Line 342 "These results directly suggest that apicoplast biogenesis specifically requires synthesis of linear polyprenols containing three or more prenyl groups." - I think that this might be overinterpreting those results - there could be a number of different reasons why polyprenols of different sizes do or don't rescue, including different solubility, diffusion, availability of transporters, predisposition to break down to useable subunits. Perhaps this needs a caveat.

We have modified the text here to remove “directly” and to acknowledge uncertainty in beta-carotene uptake: “Although it is possible that β-carotene is not taken up efficiently into the apicoplast, rescue by decaprenol, which is similar in size and hydrophobicity to β-carotene, suggests that apicoplast biogenesis specifically requires synthesis of linear polyprenols containing three or more prenyl groups.” We have also added the statement that “this hypothesis is further supported by additional results described in the next two sections”, referring to our identification of an apicoplast-targeted polyprenyl synthase.

Line 361 " the cytosolic enzyme, PF3D7_1128400" - I don't think we know the localisation of this protein based on the published data. The Gabriel et al study makes it clear the protein isn't apicoplast or mitochondrial, but it is punctate at stages in a pattern that doesn't look to me to be a straightforward cytosolic localisation (and the original authors don't describe it as cytosolic).

We agree that the localization of PF3D7_1128400 requires further investigation. The Gabriel study, which (surprisingly) is the only study we found that has examined localization of this protein by microscopy, observed diffuse signal in trophozoites consistent with cytoplasmic localization, in additional to focal, punctate signals in schizonts that were distinct from the apicoplast or mitochondrion. The authors described their results as, “Analysis by fluorescence microscopy of live parasites confirms expression along the intra-erythrocytic cycle and shows FPPS/GGPPS localization throughout the cytoplasm and also forming spots, which increase in number as parasites mature from trophozoite to schizont stages.” For simplicity we referred to FPPS/GGPPS localization as cytoplasmic but agree that available data suggest more a complex localization that requires further studies to understand. We have modified the text to indicate that available data suggests a complex cellular distribution that includes both the cytoplasm and additional sub-cellular foci outside the apicoplast and mitochondrion.

Line 423 "with strong prediction of an apicoplast-targeting transit peptide but uncertainty in the presence of a signal peptide". I don't think this describes well the bioinformatic analysis of the N-terminus. Although the experimental data are convincing that this is an apicoplast-targeted protein, bioinformatically this would not be predicted as an apicoplast protein. There is no obvious signal peptide, and "uncertainty" is too vague a descriptor. None of the versions of signalP, nor psort, predict this as possessing a signal peptide (which by definition means that PlasmoAP absolutely rejects it), and there is no obvious hydrophobic segment at the N-terminus that we would normally expect of a signal peptide. The toxoplasma hyperlopit doesn't suggest that the Toxoplasma orthologue is apicoplast, and the protein isn't found in the Boucher et al apicoplast proteome. This is somewhat of a mystery. It doesn't diminish the solid localisation data, with the excellent complementary data from IFA as well as the doxycycline+IPP experiment, but it should be pointed out clearly that this localisation isn't to be expected from the sequence analysis.

We thank the reviewer for this perspective and agree that SignalP is unable to identify a signal peptide at the N-terminus of PPS. We have modified the text to remove our description of “uncertainty” and explicitly state that SignalP is unable to identify a canonical signal peptide at the N-terminus of PPS.

We note that multiple proteins detected in the Boucher et al. apicoplast proteome also lack an identifiable signal peptide by SignalP yet are clearly imported into the apicoplast. These proteins include the key MEP pathway enzymes DXR (PF3D7_1467300) and IspD (PF3D7_0106900), holo ACP synthase (PF3D7_0420200), FabB/F (PF3D7_0626300), and the E1 subunit of pyruvate dehydrogenase (PF3D7_1446400). Thus, apicoplast import despite lack of identifiable signal peptide by SignalP is not unique to PPS but general to multiple (if not numerous) apicoplast-targeted proteins. These observations suggest to us that protein N-termini in Plasmodium can have sequence properties compatible with ER targeting that are broader and more heterogenous than other eukaryotic organisms that comprise the training sets upon which SignalP is currently based. It remains a future challenge to fully understand these properties.

With respect to the lack of PPS detection in the Boucher et al. apicoplast proteome, PPS appears to have a very low expression level and unusual solubility properties that require overnight extraction of parasite pellets in 2% SDS (or LDS) for detection. In our experience, the RIPA extraction conditions (which contained 0.1% SDS) used in the Boucher et al. study are insufficient to solubilize PPS, which may explain lack of PPS detection in their study.

To explicitly address these questions regarding PPS targeting to the apicoplast, we have added a new section to the Discussion to explore PPS targeting in the absence of a recognizable signal peptide, its unusual solubility properties and lack of detection in the Boucher et al. proteome, and planned future studies to further test, refine, and understand targeting determinants.

With respect to Toxoplasma, T. gondii appears to also express two polyprenyl synthase homologs, TGME49_224490 and TGME49_269430, that are ~30% identical (in homologous regions) to PF3D7_1128400 (FPPS/GGPPS) and PF3D7_0202700 (PPS), respectively. TGME49_224490 appears to be targeted to the mitochondrion in T. gondii (based on MitoProt and HyperLOPIT analysis), in contrast to its P. falciparum homolog, PF3D7_1128400, which localizes to the cytoplasm and other cellular foci outside the mitochondrion. TGME49_269430 does not appear to target the apicoplast in T. gondii (based on HyperLOPIT data), which contrasts with our determination of apicoplast targeting for the P. falciparum homolog, PF3D7_0202700. These differing localizations may suggest distinct cellular roles for these homologs in T. gondii compared to P. falciparum. We are also aware of a recent study (Pubmed 34896149) showing that loss of MEP pathway activity in T. gondii (due to loss of apicoplast ferredoxin) does not impact apicoplast biogenesis, in contrast to our observations in P. falciparum based on FOS treatment, DXS deletion, and PPS knockdown. These distinct phenotypes further suggest differences in isoprenoid utilization and metabolism between T. gondii and P. falciparum that remain to be understood. We have added a new section to the Discussion to address these considerations.

The section after line 344 "Iterative condensation of DMAPP with IP…", up until line 377 doesn't sit well within the section that has the heading "Apicoplast biogenesis requires polyprenyl isoprenoid synthesis". I suggest either creating a separate subheading for this material, or moving it into the start of the subsequent section "Localization of an annotated polyprenyl synthase to the apicoplast.".

We thank the reviewer for this suggestion, which we have followed. We have moved the referenced text to the beginning of the subsequent section to better align the text with that section heading.

Reviewer #2:

Minor comments:

The authors emphasize that this study reveals a previously unnoted interconnection between apicoplast maintenance and pathways that produce an output from the apicoplast to serve the cell. But is the prevailing view really that these two are separate? Isn't the interconnection already clear from many other studies and observations? E.g., the fatty acids produced inside the apicoplast provide membrane- and lipid- precursors for the rest of the cell as well as for the apicoplast itself (Botte et al., PNAS, 2013) (although not essential in Plasmodium blood stages). Other pathways that function inside the apicoplast such as the Fe-S cluster synthesis are critical to support enzymes that provide exported metabolites (e.g., IPP synthesis, IspG/H) and function in maintenance (e.g., MiaB) (Gisselberg et al., PLoSPath, 2013). Perhaps the authors could tone this conclusion down and acknowledge that maintenance and output are interconnected in other cases, which have been acknowledged in the literature.

We thank the reviewer for this perspective and agree that in Toxoplasma as well as in mosquito- and liver-stage Plasmodium there are multiple apicoplast outputs (i.e., metabolic products exported from the apicoplast) that contribute to parasite fitness, including IPP, fatty acids, and coproporphyrinogen III. To clarify, we are specifically referring to blood-stage Plasmodium in our manuscript, when heme and fatty acid synthesis are dispensable and where the prior literature has intensely focused on IPP as the key essential output of the blood-stage apicoplast and consistently stated that IPP is not required for organelle maintenance.

We agree that prior work has firmly established that apicoplast housekeeping functions (e.g., synthesis of proteins and Fe-S clusters) are required for organelle maintenance and to support IPP synthesis. However, our work is the first to demonstrate in blood-stage Plasmodium that the reverse is also true- that IPP as an essential apicoplast output is also required for organelle maintenance and that apicoplast maintenance and IPP synthesis are thus reciprocally dependent. We have modified the Discussion section to clarify these points and to explicitly acknowledge that apicoplast maintenance and other metabolic outputs may also be interdependent in Toxoplasma and other Plasmodium stages.

Could the authors elaborate more on the leader sequence predicting apicoplast localization for the PPS characterized here and discuss why it might have been missed in previous detailed study of apicoplast localised proteins (Boucher et al., PlosBiol, 2018)?

Please see our response above to Reviewer #1.

Could the authors discuss conservation of the PPS gene(s) in other Apicomplexa with (e.g., T. gondii) and without (e.g., Cryptosporidium spp.) an apicoplast? This could be relevant for other people in the field and could give further insights into the enzyme's role in apicoplast maintenance.

Please see our response above to Reviewer #1. Polyprenyl synthases are diverse enzymes that perform a variety of cellular functions, whose specific roles can differ between organisms. Although the two Plasmodium prenyl synthases show preferential homology with each of two different prenyl synthase homologs in Toxoplasma and Cryptosporidium (CPATCC_003578 and CPATCC_001801), the differing localizations of these homologs in each parasite suggest differing cellular roles. The differing dependence of apicoplast biogenesis on MEP pathway activity in T. gondii and P. falciparum and the absence of an apicoplast in Cryptosporidium further support differences in isoprenoid utilization and metabolism in these organisms. We have added a new section to the Discussion to address these considerations.

Reviewer #3:

The paper is very nicely written and was a true pleasure to read. The introduction is concise yet dense with all relevant background of our current understanding of functioning of the apicoplast in relation to IPP production and utilization. The rational of the experiments and the interpretation of the results are presented clearly and everything is discussed well in the context of the current understanding of the field. The main conclusion of the paper that isoprenoid is not solely essential for critical functions elsewhere in the cell, such as prenylation-dependent vesicular trafficking but also for apicoplast biogenesis via its processing by an essential polyprenyl synthase conserved with plants and bacteria is well substantiated and very exciting. The authors demonstrate an equally beautiful and clever use of available and newly generated genetic mutants in combination with complementary pharmacological interventions and metabolic supplementation. There are no true major weaknesses that could jeopardize the conclusions or change the interpretation of the results. However, the authors do consistently perform statistical analyses on data obtained from individual cells obtained in no more than two independent experiments, which in my humble opinion does not qualify for statistical analysis. That said, the results are so clear-cut that no statistics are required to convince me, or to quote Ernest Rutherford: '"If your experiment needs statistics, you ought to have done a better experiment."

We thank the reviewer for these positive comments and suggestions. For growth assays, we have performed a third biological replicate and updated those figures and the indicated statistical analyses. For microscopy experiments, we have removed p values.

Author Response:

Reviewer #1:

Significance: A central puzzle in evolutionary biology (and philosophy of biology) is the evolution of new (collective) entities that can evolve on their own right (e.g. the evolution of multicellular organisms from single cells). These evolutionary transitions are often conceptualized in terms of fitness decoupling (a fitness increase of the collective even as the fitness of the component particles decreases). Using a life-history model, the authors show that fitness decoupling is not possible when the conditions for fitness are the same. Thus, this paper has the potential to change how we think about the evolution of new collective entities.

Strengths: This paper is conceptually rich and the overall argument is clear. Re-analyzing previous data/models using their new framework highlights new patterns of fitness change in these transitions of individuality, and as such, it provides novel and exciting avenues of research.

Weaknesses: While the overall argument is clear, some of the details can be hard to follow (even as someone familiar with the literature). The initial description of their model is fairly clear, but given its conceptual novelty, the paper does not spend enough time developing the different concepts of fitness at the particle level.

Moreover, it is not entirely clear what is at stake: what is the role of fitness decoupling in our understanding of fitness transitions? And how does the proposed mechanistic ("trade-off breaking") model serve as a replacement? It seems to me like trade-off breaking is a characteristic of many evolutionary innovations, not only of major transitions. It seems even possible to envision groups that allow for an escape in a trade-off without leading to the evolution of a new "Darwinian" individual.

For example, one could conceive of a trade-off in zebras between time spent foraging and protection against predators. Coming together temporarily as a group is likely to allow for values outside this trade-off space (similar to those in Fig. 6). One could even imagine a new mutation that makes zebras switch activities (foraging/watching) depending on their position within the group. This mutation is only available to zebras that form groups (the phenotype does not exist in the absence of a group). But I would still want to argue that there is more to the evolution of new levels of individuality. Trade-off breaking seems (potentially) a necessary, but not sufficient step in these transitions.

And while the language of the authors is careful to not suggest sufficiency, it is not entirely clear how this approach helps us understand the particularity of these transitions.

Reviewer #1 asks first to clarify the stakes: what is the role of fitness decoupling in the explanation and how does tradeoff-breaking replace or supplement it? Second, they requested us to make a statement about the necessary or sufficient nature of tradeoff-breaking.

With respect to the second point, we argue that tradeoff breaking is not sufficient, but is probably necessary for an ETI to occur.

Let us now clarify the role of fitness decoupling and tradeoff breaking in the explanation of ETIs. It must be stressed that tradeoff breaking does not “replace” fitness decoupling; rather, tradeoff breaking is an event that cannot be understood readily in the framework of fitness decoupling. Thus, we claim that ETIs are better understood when seen through the lenses of traits and the evolutionary constraints that link them (i.e., tradeoffs) than via the export-of-fitness model (i.e., fitness decoupling). To illustrate this, we use the zebra herd example proposed by the reviewer. Coming together temporarily as a collective does not, in itself, constitute a tradeoff-breaking event, but rather simply a collective-formation event (similar to the first ace2 mutation in snowflake yeast or the first WS mutation in the Pseudomonas system). From this starting point, a number of mutations (i.e., change in traits values) can be fixed in the population that improve the performance of zebras within this environment. This is the “fast” part of the evolutionary trajectory that occurs on the ancestral tradeoff, which we called “low hanging fruit mutations” in the manuscript. As a consequence, “optimal herds within the ancestral tradeoff” evolve. As stated in the manuscript, if we assume that the tradeoff on traits is identical for lone zebra and zebra herd and also assume that the ancestral lone zebra exhibit trait values that are optimal (within these constraints) for lone zebras, it follows that the low-hanging fruit mutations that improve the zebra herd will probably reduce counterfactual fitness. This lowering of counterfactual fitness is not due to a “transfer” between real and counterfactual fitness (because there is nothing to transfer between real and counterfactual worlds), but is a consequence of the differential contribution of the traits involved in the tradeoff to the two fitness quantities. However, this specificity of the tradeoff might be significant because it could lead to stabilisation of the new collectives through ratchetting.

There is, indeed, “more to the evolution of new levels of individuality,” as pointed out by Reviewer #1. We claim that it involves rare mutations that would overcome the ancestral constraint and call them “tradeoff breaking mutations”. Tradeoff-breaking mutations are not bound by ancestral tradeoff; therefore, there is no a priori theoretical or biological reason to think they would have any positive or negative effect on counterfactual fitness. Here, we must stop using the zebra herd example because no tradeoff-breaking mutation occurred. However, the tradeoff-breaking lineages in the Pseudomonas example exhibit an improvement of both counterfactual and within-collective fitness. This observation does not fit within an export-of-fitness framework, but makes perfect sense in a traits-based view of ETIs—as a tradeoff-breaking mutation.

Reviewer #2:

This work reviews the influential "fitness decoupling" heuristic for understanding evolutionary transitions in individuality (ETIs), describes some of its limitations, and clarifies its interpretation. The review of the fitness decoupling account capably describes an interpretation of this framework that has frequently occurred in the literature, for example in Okasha 2006, Godfrey-Smith 2011, Hammerschmidt et al. 2014, Black et al. 2019, and Rose et al. 2020. However, it does not address the interpretation advanced by its authors, Richard Michod and colleagues, which they have clarified in several papers cited in the present work. Michod and colleagues have argued that the fitness decoupling account describes a changing relationship between the fitness of groups and the "counterfactual" fitness of their component cells, that is, the fitness the cells would have if they were removed from the group. This point is made explicitly in Shelton & Michod 2104 and Shelton & Michod 2020 and was present (though perhaps not as obvious) in Michod 2005 and later works, in contrast to the claim in the Glossary that this is a "relatively recent development of the fitness decoupling literature." The interpretation that Michod embraces is similar to what is here described as f2, the fitness of a "theoretical mono-particle collective", but that interpretation is not mentioned in the present work until Section 2.3. It is possible that an argument could be made that Michod and colleagues have not consistently interpreted fitness decoupling this way, or have made statements inconsistent with this interpretation, but no such argument is present in this work. Thus the impression conveyed is that Michod and colleagues consider decoupling of "commensurably computed fitnesses" possible, which is counter to their explicit statements on the topic.

The description of the limitations of the fitness decoupling heuristic (Section 2) is useful and goes a considerable distance toward clarifying the ways in which fitness decoupling can rigorously be interpreted. However, the final assessment (Section 2.3) does not make a compelling case for its central argument, the lack of utility of the fitness decoupling concept. Elsewhere in the work, the ratcheting model of Libby and colleagues is referenced in comparison to the tradeoff-breaking approach, but Section 2.3 does not acknowledge the relationship between Libby and colleagues' model and the counterfactual interpretation of the fitness decoupling heuristic. For example, the argument in Libby and Ratcliff 2014 that "If any of the yeast that evolved high rates of apoptosis within clusters were to leave the group and revert to a unicellular lifestyle, they would find themselves at a competitive disadvantage relative to other, low-apoptosis unicellular strains." and in Libby et al. 2016 that "…if G cells were to revert to unicellular I cells, they would be quickly outcompeted" are counterfactual fitness arguments essentially similar to that of Shelton and Michod 2020 that "the fitness a cell would have on its own declines as the transition progresses." Section 2 makes a convincing case that commensurable fitnesses cannot be decoupled, but by fixating on commensurability, which is not relevant to the counterfactual interpretation of fitness decoupling, Section 2.4 fails to make a convincing case that "fitness-decoupling observations do little to clarify the process of an ETI." That is, "because they are not commensurable" does little to explain why the counterfactual interpretation of fitness decoupling "does little on its own to clarify the process of an ETI," since commensurability is not a claim that the the counterfactual interpretation of fitness decoupling makes.

We agree with the reviewer on two essential points: (1) the decoupling of commensurably computed fitness is impossible when collectives have a finite size and (2) counterfactual fitness is not commensurable to particle or collective fitness.

While we recognise that Michod and collaborators did clarify that fitness decoupling referred to counterfactual fitness (although, to us, this becomes clear from 2015 onward), we argue that the fitness transfer (or export-of-fitness) metaphor implies (by its wording) a commensurability of fitnesses that undermine this welcome clarification.

Indeed, for a quantity to be transferred from one place—or component—to another, the source and destination must be commensurable. It is incorrect to talk about a transfer between counterfactual and actual quantities. A better choice of words to discuss the relative change of counterfactual and actual quantities would avoid the physical transfer metaphor and focus instead on the correlation of the two quantities. It must be noted that, despite the clarification of counterfactual fitness, the word “transfer” continues to be used in recent work (Davison & Michod, 2021).

This may seem like nitpicking; however, there is a real advantage in being careful about this. We do agree that, under some assumptions, counterfactual fitness would decrease while whole–life cycle particle fitness (or collective fitness) increases. From there, one might ask: what needs explaining? If one assumes an export-of-fitness framework, the transfer of fitness explains why it cannot be otherwise. If fitness decreases on one side, it must increase on the other. In other words, the existence of a tradeoff is taken for granted based on the improper physical metaphor. While there are strong reasons to think that such tradeoffs exist, they should be assessed in their own right and on a case-by-case basis rather than being assumed to hold. Otherwise, there is no way to make sense of the tradeoff-breaking scenario described in Section 4.

By the same token, the metaphor of “decoupling” often associated with the export-of-fitness model is misleading because it is used to describe a part of the evolutionary dynamics where counterfactual particle fitness and whole–life cycle particle fitness are strongly dependant on one another (even if their changes are anticorrelated), through the existence of the tradeoff.

Nevertheless, we welcome the reviewer’s urge to clarify our position and how this relates to Michod and colleagues’ counterfactual fitness proposal.

The model based on trade-offs and trade-off breaking is useful and likely to be of interest to theorists interested in ETIs. The observation that this model can reproduce the (counterfactual) fitness-decoupling observation is a useful in showing the how the two models relate. The result that counterfactual fitness decoupling is a consequence rather than a cause of the evolutionary dynamics is an important point (though perhaps obvious in retrospect, since counterfactuals, things to do not happen, can't be the causes of anything).

The caution in Section 3.3 that "the same [counterfactual fitness decoupling] observation will be made in any situation in which short-term costs are compensated by long-term benefits, not solely during ETIs" is a good point, and it sets up the argument that trade-off breaking is a "genuine marker for an ETI". However, no convincing case is made that the same criticism, that the observed phenomenon is not unique to ETIs, is not equally true of trade-off breaking. Some nice examples of trade-off breaking in the context of ETIs are given, but these do not amount to an argument that trade-off breaking is only observed during ETIs. The life history literature includes examples of trade-off breaking that are not related to ETIs, so it is not clear that trade-off breaking is either a reliable indicator of ETIs or superior in this respect to counterfactual fitness decoupling.

This point is in line with one of the points made by Reviewer #1. We have now clarified our position with respect to the generality of the tradeoff-breaking approach.

In the Discussion, the "inconveniences" associated with the fitness decoupling are cogent limitations of this heuristic. The "impossibility of decoupling between commensurable measures of fitness" is an important result, but it is not new and should thus probably not be presented as "[o]ur first main finding". Shelton and Michod 2014 includes a mathematical proof in the appendix that, given the model assumptions, "consideration of the births and deaths of colonies gives us exactly the same bottom line (fitness) as consideration of the births and deaths of lone cells." The second main finding, that "fitness decoupling observations cannot be reliably used as a marker for ETIs," is valid, but as described above, a convincing case is not made that trade-off breaking can be reliably used in this manner, either. Trade-off breaking may, however, be a useful way to think about ETIs in the other ways that are suggested, for example as key events and as stepping stones to new hypotheses.

We have now clarified our position.

Author Response:

Reviewer #1 (Public Review):

In this paper, Qin et al. investigated the molecular mechanism of phospholamban (PLN) linked dilated cardiomyopathy (DCM), using structural approaches combined with biophysical measurements. Structures of the catalytic domain of protein kinase A (PKAc) in complex with PLN peptides (both wild-type and the R9C and A11E DCM mutants) provide insights into the mechanism of substrate recruitment and how it is perturbed in the disease state. Qin et al. show convincingly that the mutant peptides all have lower affinity for PKA than the wild-type peptide, suggesting models in which heterozygous DCM mutations act via sequestering PKA and thereby preventing phosphorylation of the wild-type peptide may be incorrect.

The authors highlight significant differences between their structure of the WT-PLN:PKAc complex, which has a 1:1 stoichiometry, and a previous structure of the complex (PDB 3O7L), which has 1 PLN bound between two PKAc monomers (a 1:2 complex). The authors posit that the stoichiometry observed in 3O7L is an artifact of the crystal lattice, and does not occur in solution, supporting this with analysis of the elution volumes of the peptide complexes on size exclusion chromatography compared to PKAc alone. They further suggest that the AMP-PNP ligand included in the 3O7L structure is not bound, based on analysis of Fo-Fc maps calculated from the deposited coordinates. Inspecting 3O7L I am not convinced of this last point - it seems more likely that a technical error was made in assigning or refining the B-factor of the ligand in 3O7L, because there is clearly density present in SA-omit maps for the nucleotide.

Taking these results together, the authors suggest a mechanism for DCM, whereby mutations in PLN result in lower affinity for PKA, and consequently reduced phosphorylation. This seems plausible and well supported by the data, although in the ADP-Glo assay used here, the reductions in phosphorylation observed for some of the mutant peptides are rather modest. However, as the authors state, it is plausible that even relatively subtle changes in PLN phosphorylation could have substantial effects on Ca2+ homeostasis via increasing SERCA inhibition.

We thank the reviewer for the appreciation of our work.

Reviewer #2 (Public Review):

Strengths:

The authors presented new high-resolution 3D crystal structures of the PKA catalytic domain (PKAc) in complex with PLN WT or mutant peptides (residues 8-22) containing the DCM-associated PLN mutations (R9C or A11E). These are novel and important data given that the present structures are dramatically different from those reported previously. The authors made convincing argument that the 3D model reported previously may result from a crystallization artifact.

By characterizing the interactions between the PKAc domain and PLN WT or DCM-associated mutant peptides using surface plasmon resonance (SPR) analysis, the authors convincingly showed that the DCM-associated PLN mutations at positions 9, 14, and 18 alter the conformation of the PLN peptide and reduce the binding affinity of the PLN peptide with PKAc. These data provide an explanation how some DCM-associated PLN mutations at these positions reduce the level of PKA-dependent phosphorylation of PLN.

The authors also performed nuclear magnetic resonance (NMR) to determine the structural dynamics of PLN WT, R9C, P-Ser16, and P-Thr-17 peptides. These NMR structures combined with the SPR analysis also support their conclusion that PLN phosphorylation and DCM-associated PLN mutations have an impact on its conformation.

We thank the reviewer for the comments.

Weakness:

The present study used PLN-derived peptides (aa 8-22). Although technically challenging, it is important to consider if the full-length WT or mutant PLN will behave the same as those observed with the peptides. This is especially crucial in light of the prior work showing substantially different structures using a different segment of PLN.

We are fully aware of the potential risk to draw conclusion from an isolated peptide instead of the full-length PLN as a transmembrane protein. In the previous study, people showed that the PLN peptide could be used as a good model substrate that gets phosphorylated as efficiently as the full-length PLN protein (L. R. Masterson et al., Dynamics connect substrate recognition to catalysis in protein kinase A. Nat Chem Biol 6, 821-828 (2010); D. K. Ceholski, C. A. Trieber, C. F. Holmes, H. S. Young, Lethal, hereditary mutants of phospholamban elude phosphorylation by protein kinase A. The Journal of biological chemistry 287, 26596-26605 (2012)). These results together with our biochemistry results suggest the tail peptides are indeed active substrates of PKA. Due to the technical difficulty, we were not able to crystallize PKAc in complex with the full-length PLN. To explain the potential difference between the peptides and the full-length PLNs, we added more text in the discussion section “Additionally, the trend of the reduced phosphorylation by DCM mutations can be significantly affected by the oligomerization state of PLN. Ceholski et al. showed that R9C severely inhibits PKA phosphorylation in the context of full-length pentameric PLN, but has a much milder effect in the context of full-length monomeric PLN or an isolated tail peptide [41].”

Although it is convincing that DCM-associated PLN mutations likely reduce the interaction between PKAc and PLN (assuming that the peptides behave the same as the full-length PLN with respect to interaction with PKA) and, as a result, the PKA dependent phosphorylation of the mutant PLN, it is unclear how this impaired interaction between PKA and PLN mutant could explain the effects of the DCM-associated PLN mutations on SERCA function (either reduced or enhanced PLN-dependent inhibition of SERCA, as proposed previously). In this regard, can the authors predict if the DCM-associated PLN R9C mutation reduces or increases SERCA inhibition based on the results of their present study?

It is indeed controversial how PLN mutations cause DCM. Previous studies have shown that the DCM mutations in PLN might change this regulation in either a phosphorylation-dependent or phosphorylation-independent manner. Our results show that the mutations may act through both manners: 1) the mutations reduce the phosphorylation level of PLN, which has been shown to enhance the inhibition of SERCA and inhibit the uptake of Ca2+; 2) the mutations change the conformation of PLN before binding to PKA or SERCA, which could have additional consequences, such as altered assembly state of PLN, phosphorylation of PLN by CaMKII, or changes in interactions of PLN with the lipid membrane. This could impact in either directions, reducing or increasing SERCA inhibition, which is difficult to predict based on our data. We added the explanation in the discussion “While decreased PLN phosphorylation is likely an important contributor to the physiological dysfunction associated with familial DCM, disease-causing mutations in PLN may have additional consequences, such as altered assembly state of PLN, phosphorylation of PLN by CaMKII, or changes in interactions of PLN with the lipid membrane. The influence of such factors on SERCA inhibition are unclear. In principle, they might further increase inhibition of SERCA and act in conjunction with lower PKA-mediated phosphorylation to manifest the disease symptoms. Conversely, it is possible that these factors could decrease the inhibition of SERCA, partially compensating for the decreased phosphorylation level, and mitigating the symptoms.”

It is also unclear how reduced PKA phosphorylation of mutant PLN could lead to DCM. PLN is unlikely to be significantly phosphorylated by PKA at rest (in other words, PLN is likely to be phosphorylated by PKA during stress, i.e. during the adrenergic fight-or-flight response). Therefore, it is puzzling how such reduced PKA-dependent phosphorylation of PLN would significantly affect the PLN function during the absence of flight-or-flight response.

As explained above, we think that this regulation could be through both phosphorylation-dependent and phosphorylation-independent manner. Even only considering the phosphorylation-dependent manner, the DCM phenotype could be due to an accumulation of the Ca2+ imbalance in the cell over repeated cycles of cardiac muscle contraction upon chronic accumulation of the sporadic phosphorylation events. It is also possible that the mutations affect the CaMKII-dependent regulation of PLN, which leads to DCM.

Given that the DCM-associated PLN mutations have significant effects on the conformation of PLN itself, at least in the form of short-peptides, it is possible that these mutations could affect the folding, oligomerization, trafficking, degradation, etc., in addition to PKA-dependent phosphorylation. The relevance and contribution of reduced PKA-dependent PLN phosphorylation to DCM remain unresolved.

We agree with the reviewers that both phosphorylation-dependent and phosphorylation-independent manners could contribute to the DCM disease phenotype. It remains unresolved which factor is the major contributor. We have added a statement in the discussion (see point above).

Reviewer #3 (Public Review):

This manuscript describes an elegant study utilizing the crystal structures for the elucidation of the disease mechanism of familial dilated cardiomyopathy. It has been known for decades that the mutations in PLN are associated with DCM, but the underlying mechanism remains controversial. In my opinion, Prof Yuchi and co-authors did excellent job on revealing the high-resolution crystal structures of PKA-phospholamban complexes, representing both the native and diseased states. Combined with various of biophysical and biochemical methods, including SPR, ADP-glo, thermal melts, NMR, etc, the authors systematically investigated the correlations between the PLN conformation, the binding affinity, and the phosphorylation level. The mechanism of PKA phosphorylation on another related substrate, ALN, was also convincingly revealed. The results are very helpful for understanding the pathological mechanism of PLN-related DCM. More importantly, the atomic structures of PKA-phospholamban complexes lay a solid foundation for the structure-based rational design of therapeutic molecules that can reverse the effects of the DCM-causing mutations in the future, e.g. by stabilizing the interactions between PLN and PKA.

We thank the reviewer for the appreciation of our work.

Author response:

Reviewer #2 (Public Review):

This work by Castledine et al. addresses the important question of whether results from in vitro (laboratory-based) evolution studies may be useful for predicting evolution during phage therapy in a clinical setting. In order to explore this question, the authors cultured a set of bacterial isolates from a patient pre- and during phage therapy, as well as phages from several time points during therapy. They then experimentally evolved (in vitro) a mixture of the bacterial isolates from the patient in the absence of phage, or in the presence of phage using two different treatments (phage added once or added repeatedly). Overall, they observed similarities between the evolutionary outcomes (genomic and phenotypic) in vitro and in the patient. Resistance evolved rapidly in the patient and in vitro under phage selection, and similar genomic changes were observed in both environments. The approach of using bacterial isolates directly from the patient (as well as the phages used for therapy) in vitro is clever, and the observed similarities are compelling.

We thank the reviewer for appreciating the novelty in our results and methodology.

However, I think there are some limitations with the study that should be addressed in the text.

In particular, (1) While the similarities in vitro and in the patient are quite interesting, there are some differences that were dismissed as being minor without justification. Calling the results "highly parallel" is a bit subjective - in vitro in the repeated phage treatment (which is suggested to be most similar to the clinical context), there did appear to be phage coevolution that was not observed in vivo. The tradeoffs/relationships between traits (as shown in Fig. 3) also differed to some extent.

We agree this could have been more objectively phrased at the start of the discussion – this has been edited to reflect this. We have highlighted the differences between in vivo and in vitro treatments with respect to phage evolution. Moreover, we have also highlighted that the observed trade-offs had different underlying mechanisms which may not always result in parallel evolutionary changes between in vivo and in vitro environments.

Additionally, for the genomic results only a subset of variants were plotted (those in genes of known function), but there were far more significant variants in genes of unknown function that were not included. It is difficult to assess whether the genomic findings are truly similar across environments if only a fraction of those results were presented in the manuscript.

We chose to concentrate on genes of only known function so that we could better understand their potential significance, and also because the figures and analyses (Figures 4 and 5) would become extremely complex and large and uninterpretable with genes of unknown function included. This is especially true for Figure 5, which would have required us to show 284 rows if all genes would have been included. Ultimately, whichever way we do this exploratory analysis, it is going to be difficult to see if findings are truly similar across environments because we only have a single patient who had phage therapy.

However, we have redone the analysis with all of the significant genetic changes (SNPs and indels from both known and unknown genes) included.

Figure 5 has been recreated and is now included as "Figure 5 - Figure supplement 1". All of the statistical analysis on (a) the number of SNP/indels seen (b) genetic distance from ancestor and (c) alpha diversity give quantitatively similar results. That is, although all the estimates are generally much higher after including many more genetic variants, all of the significant results from both the overall model fit and post-hoc multiple comparisons remain the same. One interesting result that came out of looking at all the genetic changes was that for genetic variants occurring in a gene of known function, 56% (28 out of 50) were de novo mutations, whereas this value was only 42% (98 out of 234) for variants in genes of unknown function.

We then looked at the proportion of genetic variants (both in known and unknown genes) found in vitro that were also found in vivo. For genes of known function, 62% of genetic variants were found in vivo (31 of 50) and this was comparable to the 65% of genetic variants in genes of unknown function (153 of 234). Of the 26 genes of known function with differences identified in the in vitro analysis, 16 (61%) were also found to have genetic changes in vivo. The equivalent metric for genes of unknown function was 86% (85 of 99). Similar to in vitro, variants occurring in a gene of known function were more likely to be de novo mutations (77%) compared to variants occurring in a gene of unknown function (46%).

While these patterns and exploratory analyses are interesting, they have extremely limited statistical power and therefore do not alter the conclusions or results of the work presented. For these reasons, we have chosen not to include these results in the already long manuscript. We have added a line to say we have done it both way:

“We performed all downstream statistical analyses on (a) only genetic variants in genes of known function and (b) all genetic variants.”

And we also added a line at the beginning of the genomic analysis results section:

“Results were not affected whether we included only genetic variants occurring in genes of known function or all genetic variants (Figure 5-Figure supplement 1). As we were interested in attributing potential functions to the variants identified, we only present the results for genetic variants occurring in genes of known function.”

(2) Much of the text is framed around whether in vitro outcomes are predictive of those in vivo, but this study only included results from a single patient. Thus, it is impossible to know whether these findings are by chance or representative of a more general relationship between in vitro and in vivo evolution.

We agree that having a single patient for our in vivo comparison limits the generalisability of our results. We have highlighted this in the revised manuscript. However, that our replicated in vitro experiments agreed broadly with our in vivo results and that of other studies (finding resistance-virulence trade-offs) suggests that at least in some circumstance in vitro dynamics are predictive of in vivo dynamics. Further studies are clearly needed (and hopefully will arise as a consequence of this work) to determine the generalisability of this finding and the circumstances where this parallelism might break down.

(3) Although the evolutionary outcomes appear to be similar, the pathogen was successfully cleared from the patient but persisted throughout experimental evolution. Whether the pathogen is successfully eliminated or not is presumably the most important clinical outcome, and while this difference is not surprising, it is an important one to point out to the reader. Essentially, evolution was similar to some extent but the consequences of evolution for bacterial persistence in each environment were quite different.

We have now highlighted this difference to the reader in the revised manuscript.

Author Response:

Reviewer #2 (Public Review):

The paper by Meyer and collaborators first describes the in silico identification of a putative beta 1-4-N-acetylglucosaminyltransferase in the model Crenarchaeon Sulfolobus acidocaldarius. Beta 1-4-N-acetylglucosaminyltransferases are involved in the N-glycosylation pathway for the synthesis of glycoproteins. To detect this enzyme, the authors have used as baits the bacterial enzyme MurG and the eukaryotic enzymes Alg13 and Alg14. These enzymes have no detectable similarities and it was not possible to detect their Sulfolobus homologs by simple BLAST search. However, they detected several putative candidates with very low sequence identity (10-17%) using Delta-BLAST. They selected one of them which was retrieved using the Alg14 protein of Saccharomyces cerevisiae as bait.

We thank the reviewer for this comment. We tested all identified candidates by deletion approaches. However, Saci1262 was the most promising one, whose function could not be determined by the deletion approach. To confirm the function we developed the described in vitro assay. We restructured the text to make this point more clear.

They report that the overall topology of this candidate protein is identical to those of MurG and that the N and C terminal part of the protein could correspond to the eukaryotic proteins Alg14 and Alg13, respectively. They give the name Agl24 to this protein (why 24?) and then describe the enzyme as if its identification was already demonstrated. Closely related homologues of this protein are present in most Crenarchaeota, except in Thermoproteales, but absent in other archaea (Fig. S7).

We agree that this was confusing; we have changed the naming of Saci1262 to Agl24 after the confirmation of its function in the text. Based on the proposal for the naming of N-glycosylation pathway components in Archaea (Eichler et al. ”A proposal for the naming of N-glycosylation pathway components in Archaea”. Glycobiology 23:620–621) the enzyme was named archaeal glycosylation enzyme 24 (Agl24).

At this stage of the manuscript (lane 153), the identification of Agl24 is only based on the detection of several patches of conserved amino-acids between the different enzymes (Fig.1, B and D) and on a structural model that fits the structure of the homologous enzymes. I suggest that the authors slightly change this part of the manuscript by first describing how they modelled the structure of their candidate enzyme (this is not indicated in the M&M) and how they identified these conserved amino-acids.

We have added the process used to obtain the structural model to the Methods section.

They can conclude that the structural and sequence similarities (although low) suggest that they have selected the right candidate and name it (then follow up with their detailed comparison of the different enzymes). An interesting result is the identification of a motif (GGxGGH) conserved between Alg24, MurgG and Alg14. If it's really the first time that this motif is detected, thanks to the identification of Alg24, this is worth to be much more emphasized, especially since the authors demonstrate later on that the histidine is essential.

We report in this manuscript for the first time the sequence conservation of this motive in bacterial, eukaryotic and archaeal homologs. However, the motif has been described as an extended motif G13GTGGHX2PXLAXAX2LX9G39 in MurG sequences (Crouvoisier et al., 2007). This is now mentioned in the text.

Lane 37 of the abstract, this sentence is ambiguous, there is no strong similarity between Alg24 and eukaryotic Alg13/14. There is possibly strong structural similarity but it is not obvious that it is higher than with MurG from Figure 2A. Is it possible to quantify these similarities? It could be also wise to compare with the structure of a bacterial EpsF, since, from the phylogenetic analysis of the authors (see below) Alg24 could also exhibit more sequence similarities with EpsF than with MurG.

We agree that this sentence in the abstract was very ambiguous and it has now been modified. The structural similarity can be quantified and it is represented by the Root Mean Square Deviation (RMSD) values of the C-alpha backbone atoms of our model compared to the published structures (now added to the Table S2) or the Global Model Quality Estimation (GMQE) score. The resulting GMQE score is expressed as a number between 0 and 1, reflecting the expected accuracy of a model built with that alignment and template. GMQE is coverage dependent, and models covering only half of the target sequence is unlikely to get a score above 0.5. The obtained values obtained for Agl24 was given in Table S2, and vary between 0.46-0.56. We also performed the structural prediction with AlphaFold which resulted in a very similar prediction as obtained by Swissmodel (RMSD: 3.80). These findings are now reported in the manuscript.

No EpsE or EpsF GT structures are published, therefore we could not compare those to Saci1262.

In my opinion, the next section should not be "Agl24 is essential" but the biochemical characterization of the enzyme which confirms the in silico prediction. The authors have produced and purified a recombinant Alg24 enzyme. They show that the enzyme is membrane bond and has an inverting beta-1,4-N-acetylglucosamine-transferase activity. The section "Alg24 is essential…" could be possibly removed and the result mentioned in the discussion since they are not conclusive concerning the biological role of Alg24 but confirm the previous observation of Zhang and colleagues made by transposon mutagenesis on the Alg24 homologue in Sulfolobus islandicus.

We thank the reviewer for this important comment. We have added a short text to highlight, that the essential properties indicated that we might had candidate proteins to identify the N-glycosylation enzyme, as our previous studies have indicated that the N-glycosylation is essential in Sulfolobus.

In comparison with the first part of this paper, the last part, dealing with evolutionary aspects raises many problems. The authors do not seem familiar with evolutionary concepts as indicated by the use of the term "lower eukaryotes" lanes 163, 175 that is not used by evolutionists since it is highly biased (a bit racist!), animals, including ourselves, being " higher" eukaryotes. This weakness is also apparent from the use of the expression "conserved from yeast to human" lane 57. Yeast and Human belong to the same eukaryotic subdivision (Opistokonts) so this conservation does not testify for the presence of an enzyme in the Last Eukaryotic Common Ancestor (LECA). Similarly, the authors often limit their description of "lower eukaryotes" to Leishmania/Trypanosoma or Dictyostelium/Entamoeba. A more extensive survey of the Alg13/14 topology in all eukaryotic major groups would be necessary to conclude for instance that the protein was a monomer or a dimer in LECA.

While we agree that the term “lower” is not technically correct (and probably slightly speciesist), it’s (even historically) a common colloquialism in the literature. Nonetheless, all the term has been removed or changed to “deep-branching” or more appropriate terminology. The mentions of non-Opisthokont Eukaryotes were limited to these particular Kinetoplastids and Ameobozoa, mainly due to the tidbit of their genes being fused, unlike other Eukaryotes. However, it is evident from both earlier work (Lombard, 2016) and our updated analyses that the distribution of these genes among Eukaryotes is much wider. Specifically, line 57 was referring to (Lehle et al., 2006) and is not linked to our inference of an early presence of these genes in Eykaryotes in general.

In the revised manuscript, we have searched for homologs in 1611 eukaryotic genomes, and demonstrated a very wide presence of the Alg14-13 proteins among them (Supplementary Data 1). Of these, we used a subset covering the known eukaryotic diversity and from these data there seem to be specific fusion events within the Eukaryotes. Similarly, any fused sequences in Archaea and Bacteria are sparse independent events and we can conclude that at the original acquisition (in LECA or otherwise), the genes were split.

The authors have performed two single gene phylogenetic analyses of several groups of Agl24 homologues, including either the eukaryotic Alg13 or Alg14, which correspond to the N and C-terminal domains of Alg24. These phylogenies are valid to identify different subgroups of enzymes, but they are not reliable to provide real information about the evolutionary relationships between these different groups and within these groups (for instance, they did not recover the strong clade formed by Thaumarchaeota, Bathyarchaeota and Aigarchaeota which is present in all robust archaeal phylogenies, see for instance Adam et al., PMID: 28777382). This is not surprising considering the small size of the genes and the very low similarities between the different subgroups. Since the two phylogenies are rather congruent, in particular for the identification of the different subgroups, it could be interesting to perform a concatenation (removing Methanopyrus kandleri which is a fast evolving species and disturb the phylogeny with Alg14).

We agree with the reviewer that the internal topology of the TACK for Alg14-13 does not reflect the reference tree. As pointed out, these sequences are rather short and not very well conserved, which is reflected in our revised phylogenies where almost none of the relationships among TACK clades are strongly supported. Furthermore, as is evident from the various Asgard and the Thermofilales clades, ancient lateral transfer events are not out of the question. However, recovering a strongly supported TACK clade points towards an ancestral presence of that particular Agl24/Alg14-13 homolog in the lineage.

Concerning a concatenation, we have followed the reviewer’s suggestion and removed the M. kandleri sequence from Alg14. We disagree on the subject of congruence between the two phylogenies; especially for the relationship between Asgards and Eukaryotes, the two trees are incongruent with the respective topologies being strongly supported. Although it is not good practice to proceed with a concatenation in such cases, we did it, if for no other reason to test the effect of mashing the two phylogenetic signals together. The concatenated dataset phylogeny is shown in Supplementary Figures S13 and S14 (collapsed and uncollapsed, respectively). Putting the concatenated dataset together required some planning, since we had to match the subsampled taxa for Eukaryotes and Bacteria in Alg13 and Alg14 and fuse the sequences semi-manually, and in some cases invert the gene order in fused eukaryotic sequences (see Methods section).

I personally identify 4 subgroups in the two phylogenies that I will discuss in some detail below.

Group 1: A first group includes a wide variety of archaea belonging to different phyla. Importantly, Euryarchaeota and other archaea (including one sequence of Odinarchaeota) are well separated. This group possibly correspond to descendants of an ancestral enzyme that was present in the Last Archaeal Common Ancestor (LACA). If correct, this indicates the position of LACA in the two trees. Some Crenarchaeota are present in this part. Did they correspond to Thermoproteales or did some Crenarchaeota have both Alg24 and this form?

We are now able to address this point with our new analysis (mainly using the revised phylogenies), since our updated local database for Archaea contains far more genomes, including all Asgards from (Liu et al., 2021). Moreover, we searched for Alg14-13 homologs against local databases of Eukaryotes and Bacteria (1611 and 25118 genomes respectively), instead of simply relying on the sequences from (Lombard, 2016). Finally, we added the MurG sequences from the respective datasets of (Lombard, 2016) for outgroup rooting of the Alg14 and Alg13 trees, plus we performed outgroup-free rooting with the Minimal Ancestor Deviation method (Tria et al., 2017). The two approaches yield the same root as noted in Figure 7 (that would be without the MurG clade for the MAD root).

“Group 1”: In the revised rooted phylogenies, this group is sister to the clade containing all other homologs (excluding MurG). It can be divided into two subclades. One consists of mainly methanogenic Euryarchaeota interspersed with other Archaea, mainly DPANN. At least for Methanosarcinales and Methanococcales (and perhaps Methanomicrobiales), the distribution is wide enough and the clades strongly supported, so we can trace the Alg14-13 homolog to the base of each of these lineages but not necessarily to all Euryarchaeota. That is due to the homologs missing from other lineages and disagreements with archaeal reference phylogenies (e.g., Methanomicrobiales and Methanosarcinales should have been together and monophyletic, without the Methanococcales). Any further inferences are problematic, since we have made clear that we mainly stuck with the clades from (Lombard, 2016) and very divergent Alg14-13-like homologs exist throughout Archaea including, for example, in Bathyarchaeota, two in Methanobacteriales.

The second subclade corresponds to the TACK superphylum with the addition of several Asgard branches therein. The latter correspond to multiple independent ancient lateral transfers from the TACK to different Asgard lineages. There exists a second divergent Thaumarchaeota clade, whose position is inconsistent between the Alg13/EpsF and Alg14/EpsE trees.

We understand the reviewer’s inclination to label this clade as having emerged at the LACA, however, we believe that our rooted phylogenies suggests that the node corresponding to the LACA is deeper.

Group 2: A second group corresponds to orthologues of Alg24 include Crenarchaeota (Sulfolobales, Desulfurococcales) and Bathyarchaeota,. Questions: How many Bathyarchaeota? Are they widespread in Bathyarchaeota? Since Bathyarchaeota are also present in group 1 (same questions), these group 2 Bathyarchaeota could correspond to MAG contamination with Crenarchaeota? Or LGT between Crenarchaeota and Bathyarchaeota?

“Group 2”: The reviewer’s description of this clade is fairly accurate. In the updated phylogenies, it is still composed primarily of Crenarchaeota with one Baldrarchaeota and a strongly supported cluster of Bathyarchaeota sequences (14 in total, mainly from o__B26-1) that indicates a single transfer event (Supplementary Figures 11, 12, 14) from Crenarchaeota to Bahtyarchaeota. A number of the Bathyarchaeota genomes in “Group 2” also contain homologs in “Group 1”. The Thermofilales member B67-G16 also possesses one homolog in each of these groups.

It is noteworthy that there was another very divergent clade composed of Bathyarchaeota (mainly members of g__PALSA-986 but other as well) in the preliminary phylogenies that were used for dataset cleanup/curation that was omitted from the final datasets. Some of sequences in that clade are also additional homologs to the ones included in our phylogenies. However, further examining the Agl24-like homologs in Bathyarchaeota is beyond the aims of this study.

The enzymes of group 2 were probably not present in LACA, except of they have evolved more rapidly than the other bona fide archaeal enzymes of group 1 (drastic modification of their function?). More likely, they have been introduced at the base of the Sulfo/Desulfo clade from an unknown source (extinct lineage?)

We mostly agree with that deduction. However, since most Crenarchaeota only contain a single Agl24-like homolog (unlike some Bathyarchaeota) and we know nothing about the function of “Group 1” enzymes, we would like to avoid further conjecture.

Group 3: A third group corresponds to EpsF in Archaea and Bacteria Question: How widespread in Bacteria? Were they present in the Last Bacterial Common ancestor? They are sister group to the eukaryotic enzymes. Are they their orthologues? Could it be that the eukaryotic enzymes originated from bacterial EpsF via mitochondria?

Group 4: A fourth group includes all Eukaryotes (monophyletic) and very few sequences of archaeal MAGs belonging to different phylums, a few Thorarchaeota and one Odinarchaeota, but also several Verstraetearchaeota, one Geothemarchaeota, and one Micrarchaeota (DPANN). The lane 39 in the abstract is thus misleading since the phylogenetic analysis revealed similar sequences not only in two phylums of Asgard but also in Verstraetearchaeota, Geothemarchaeota, and Micrarchaeota! Moreover, these similarities remain very low. This does not fit with the classical situation observed in universal tree of life in which archaeal and eukaryotic proteins always exhibit a high level of similarity.

“Groups 3 & 4”: We would like to address these two groups together.

Firstly, bacterial sequences in the revised phylogenies are no longer confined to the EpsE/F-like clade (“Group 3”) but a few sequences are found among the Archaea of “Group 4”. When subsampling the non-MurG clades of our preliminary bacterial trees (Supplementary Data 1) we saw that the EpsE/F-like and Alg14-13-like homologs are quite ancient in some lineages (e.g., Actinobacteria, Cyanobacteria, some Firmicutes subgroups) but when we put sequences from all three domains together, there seem to have been multiple interdomain transfers between Bacteria and Archaea. The archaeal “Group 3” sequences, with the exception of some methanogens and Thermococcales are mainly from DPANN; there even exists a distinct Diapherotrites branch (Supplementary Figures S11, S12). Even though we cannot pinpoint its exact origin, as it is found among archaeal clades from “Groups 2 and 4”, “Group 3” didn’t emerge at the LBCA and is of archaeal origin.

Other than the addition of a few bacterial sequences, the reviewer’s description of “Group 4” seems accurate. Nevertheless, we are not particularly surprised by the extremely low sequence conservation between Eukaryotes and the various archaeal lineages, seeing how many divergent homologs we have found throughout this analysis. The abstract has been altered to remove the mention to “similar” sequences and all mentions to eukaryogenesis in both the abstract and manuscript have been emended based on the revised phylogenies.

At the moment we have no way of testing whether Eukaryotes acquired Alg14-13 through mitochondria, in spite of the few bacterial sequences in “Group 4”. All our data point toward an archaeal origin (see below).

The authors suggest a split (red arrow) at the origin of the Group 3 and 4. However, since the tree is unrooted, one cannot exclude a fusion at the origin of groups 1 and 2?

More importantly, it is profoundly misleading to conclude from this analysis that eukaryotes emerge from Asgardarchaeota!!!! The position of the lonely archaeal sequences in group 4 suggests either problems of MAG reconstruction (contamination, recombination, mis annotation) or, more interestingly, independent LGT of proto Alg13/14 from proto-eukaryotes to these archaeal lineages. Moreover, the few sequences of Asgard present in group 4 only correspond to two Asgard phylums, while the number of Asgard phylums has skyrocketed in recent years. I did a rapid BLAST search and homologues of the Thorarchaeal sequences of group 4 are absent not only in Heimdall and Loki but also in Hela and Gerda. The authors could contact two Chinese groups who published recently preprint describing several additional Asgard phyla (Liu, Y et al. BioRxiv 2020, Xie R et al., BioRxiv 2021).

We have to thank the reviewer for this comment and sharing their thoughts with us, that ultimately spurred us to update our local databases and increase the number of Asgard genomes, without which the additional Asgard sequences in “Groups 1 and 2” wouldn’t have been found. On the issue of Archaea in “Group 4”, the monophyletic eukaryotic clade is found within a primarily archaeal clade, surrounded by several other archaeal homologs throughout the phylogeny, and not at root-level. While we did not go in-depth to check all the included Asgard MAGs for problems, the Alg14-13-like homologs are extremely widespread in the various archaeal lineages, covering essentially all Thorarchaeota, Odinarchaeota, and Verstraetearchaeota, which in our opinion would be a far-fetched series of MAG problems. Despite the incongruence on what the sister clade of Eukaryotes is (Odinarchaeota or Thorarchaeota), on the basis of the data we cannot infer that a transfer from Eukaryotes (proto- or otherwise) to Archaea occurred.

Obviously, the authors have chosen to fit their paper into the mold of the now popular two domains (2D) scenario in which Eukaryotes emerged from Asgardarchaeota. There is presently a debate between proponents of the 2D and 3D (classical Woese) universal tree of life. The authors are obviously strong proponents of the 2D since they don't mention any of the papers that have recently supported the 3D scenario (Da Cunha et al., 2017, 2018). From lane 457 to the end of the paper, all the discussion turned around the 2D model and the Asgard origin of eukaryotes! They possibly consider that the debate has been closed by the paper of Williams and colleagues (Nat Ecol Evol, 2020) who criticized the work of Da Cunha and colleagues. They should notice that Williams et al still obtained a 3D tree with RNA polymerase (supplementary figure 1) except when they use amino-acid recoding a method that reduce the phylogenetic signal (Hernandez and Ryan, BioRxiv, 2020). A 3D tree was again obtained with the RNA polymerase (including those of giant viruses and the three eukaryotic RNA polymerases) by Guglielmini et al., PNAS, 2019. The debate should thus be considered as still open.

In any case, the phylogenies presented by the authors are not universal tree of life and cannot be used in the 2D versus 3D debate. A proponent of the 3D scenario would said that the Odin sequence present in group 1 corresponds to the real position of Asgardarchaeota, in agreement with the results of Da Cunha et al (2017) who found that Asgardarchaeota are not sister group to eukaryotes but branch deep within archaea.

We would like to abstain from criticizing any previously published phylogenies on 2D or 3D trees of life. The main point of our paper was to highlight the similarities in N-glycosylation between our crenarchaeal Agl24 and Eukaryotes.

While we did point out a probable acquisition during eukaryogenesis, as would be implied by a 2D scenario, at no point in the original submission did we try to specifically address the 2D/3D debate, or go out of our way to discredit a 3D tree. That said, we are pointing out in the revised manuscript that the new phylogenies cannot directly support a 3D model. The Eukaryote branch covers their known diversity (barring taxa where we didn’t find any Alg14-13 homologs; Supplementary Data 1). With the exception of a Perkinsela sequence in Alg13, Eukaryotes are monophyletic and seem to emerge from within Archaea in all phylogenies. Moreover, in the rooted trees, they’re nowhere near forming a sister clade to archaeal homologs (all clades or even a subset of them). We hope to make clear in this version of the manuscript that the Asgard group forming the sister clade to Eukaryotes is inconsistent and not Heimdallarchaeota, as would be expected from most published 2D trees. We did not even find any Alg14-13 homologs in Heimdallarchaeota. Furthermore, the internal branching of Eukaryotes (Supplementary Figures S11, S12) does not even recover their major branches. It is unknown whether this is due to transfers or just poor signal, since sequence conservation in eykaryotic Alg14-13 is very low. Thus, even though we retain that acquisition through eukaryogenesis in a 2D tree is a possibility, our results are also compatible with a lateral transfer from Archaea very early in the history of Eukaryotes which is 2D/3D-agnostic.

Since the enzymes studied here are apparently absent in most Asgards, it is profoundly misleading to label Asgard the group close to eukaryote in the Cover art and to have a highlight claiming that eukaryotic Alg13/14 are closely related to the Asgard homologs, suggesting their acquisition during eukaryogenesis, since the number of these Asgard homologues are very limited.

Indeed, the cover art could have been misleading; as such, we have removed it. See other parts of this response concerning how we handled the sampling of Asgard genomes and the new results.

It is also profoundly misleading to conclude in the title that their result "strengthens the hypothesis of an archaeal origin of the eukaryal N-glycosylation". One can only said that archaeal and eukaryotic N-glycosylation pathways are evolutionarily related.

We disagree with this comment, even if they did not originate during eukaryogenesis, the eukaryotic homologs are clearly archaeal in origin.

However, in the case of Alg13/Alg14, it seems that these eukaryotic proteins are more closely related to bacterial enzymes (EpsF) than to their archaeal homologues (group 1 and 2)! We would like to know more about the phylogeny and distribution of EpsF in Bacteria and Archaea. According to the authors, they are only present in Euryarchaeota but widespread in Bacteria, suggesting a LGT from Bacteria to Archaea. Was this enzyme present in the Last bacterial common ancestor? In summary, the authors conclusions and formulations on the evolutionary part of their paper, especially in the title, the summary, the discussion and the Cover Art are misleading and should be corrected.

We have now address the issue of EpsEF and their relationship with Alg14-13. To recap the contents of the manuscript and this response, EpsEF and Alg14/13-related sequences are very widespread in Bacteria but do not date to the LBCA. The clade EpsEF+Alg14-13 (“Groups 3& 4”) clade is sister to Agl24 and archaeal in origin although there exist multiple interdomain transfers between Archaea and Bacteria. EpsEF sequences are found in Euryarchaeota but also in DPANN. There exists a single gene split event at the base of the EpsEF-Alg14/13 clade followed by multiple independent gene fusion events in all three domains.

Reviewer #3 (Public Review):

Meyer, Benjamin et al. identified the enzyme involved in the transfer of the second GlcNAC residue on the nascent oligosaccharide in protein N-glycosylation of the thermophilic Crenarchaeon Sulfolobus acidocaldarius. Although N-glycosylation is well-known in Euryarchaeota, the enzymes involved in this process, their substrates, and the mechanisms followed to produce the mature glycan are still elusive in Crenarchaeota, a phylum belonging to TACK archaeal superphylum, which contains also Thaumarchaeota, Aigarchaeota, and Korarchaeota. The authors, by screening the data banks with the sequences of the bacterial MurG and yeast ALg13/Alg14, which catalyze the transfer of GlcNAC in N-glycosylation, identified a gene, named saci1262 and alg24 showing very low identity. The authors characterized in deep the product of this gene with a very complete approach. Firstly, the authors could demonstrate by molecular modelling that Alg24 enzyme shows a 3D structure similar to those of MurG and Alg13/Alg14, and catalytic residues similar to the latter enzyme. The functional characterization was very complete, showing that alg24 is essential in vivo, and that the recombinant Alg24 specifically uses UDP-GlcNAC and lipid-GlcNAc as donor and acceptors substrates, respectively. In addition, the enzyme was thermophilic, did not require metals for catalysis, and followed an 'inverting' reaction mechanism in which the anomeric configuration of the product is the opposite to that of the substrate. Experiments of site-directed mutagenesis demonstrated that His14 is essential for catalysis as predicted by sequence multialignments and inspection of the 3D models, while the role of Glu114, also invariant, remained obscure. Then, the phylogenetic analysis of Alg13/Alg14 on TACK archaeal superphylum, showed that Alg24 are widespread among Archaea, suggesting that N-glycosylation in Eukaryotes was inherited by an archaeal ancient ancestor. This observation fostered the hypothesis that the first eukaryotic cell originated from Asgard superphylum.

Strengths:

The main question of the work, which is the enzyme involved in the first crucial step of protein glycosylation in Archaea? is of general interest in glycobiology. Although this process, in the past believed a peculiarity of Eukaryotes, has been well studied in Euryarchaeota, it is almost unknown in TACK superphylum that, being considered the closest to the Last Eukaryotic Common Ancestor, is a very interesting matter of study. The work shows several strengths:

1) The authors unequivocally demonstrated that Alg24 is the enzyme catalyzing the transfer of the second GlcNAc unit on the nascent oligosaccharide, thereby completing the puzzle of the first step of N-glycosylation, for which only AlgH enzyme was known so far.

2) The approach used to identify Alg24, the choice of the model system, the characterization of the enzyme are absolutely excellent and set a new standard to study N-glycosylation in Archaea.

3) The identification and characterization of a novel Glycosyl Transferase is of great importance in glycobiology. GTs are elusive enzyme, difficult to purify, due to their instability and association to membranes, and to characterize because of their extreme specificity for donor and acceptor substrates. In addition, GT enzymatic assays use very expensive substrates and very laborious procedures. For this reason, characterized GT are by far less common than, for instance, glycoside hydrolases. This study is a milestone for glycobiology. GTs from thermophilic microorganisms could be interesting subject studies in general. Thermostable GT could be more easy to purify and characterize if compared to their mesophilic counterparts.

4) The knock-out in vivo of alg24 gene, was possible because S. acidocaldarius model system is one of the few Crenarchaea for which reliable molecular genetics tools can be used. These experiments, confirmed that N-glycosylation is essential in Crenarchaeota as previously shown for AlgH and AlgB.

Weaknesses:

There are not many weaknesses in this work.

1) How the characterization of Alg24 is directly connected to the evidence that N-glycosylation in Eukaryotes was inherited from an ancestral archaeal cell should be better explained.

We thank the reviewer for this suggestion. We believe that in the revised manuscript and phylogenies we clarify how the Alg14-13 eukaryotic homologs are of archaeal origin (due to being nested within an otherwise archaeal clade) and the possible scenarios for their origin (eukaryogenesis or transfer).

2) The novelty of the presence of Alg13/14 and Alg24 homologues in TACK superphylum shown in this paper should be commented in comparison with the available literature.

We have added a new paragraph and references in the discussion part to highlight the novelty of Agl24, adding also the information that Agl24 will be assigned to a new GT family (see below).

3) The Cover Art should be revised. The 'take home message' is not clear and the phylogenetic interdependencies of the different superphyla are a bit confusing.

We have removed the cover art, as it might create more confusion than being helpful.

Author Response:

Reviewer #1 (Public Review):

• Line 141: It would be beneficial to better understand how the sequenced sample of the population corresponds to the PCR confirmed sample of the population, in order to understand possible selection biases in the sequence data. Could you elaborate on how the composition of sequence PCR confirmed cases matches the composition of PCR confirmed cases, by the demographic characteristics listed in Table 1.

Early in the pandemic (March-April), we tried to sequence every SARS-CoV-2 positive case diagnosed in our KWTRP laboratory from Coastal Kenya. However, with the sharp increase in the number of identified cases from the month of May 2020 onwards, and a limited in-house sequencing capacity, we changed strategy to sequence only a sub-sample of the identified positives. The criteria for sub-sampling included having a cycle threshold of < 30.0, spatial representation (at county level) and temporal representation (at month level). The consequent number and proportion of samples sequenced across the study period months and across the counties is summarized in Fig. 2C-E with the sample flow provided in Figure 2-figure supplement 1.

In the revised manuscript we have provided a comparison of the demographic characteristics of the sequenced cases versus non-sequenced cases (shown as Table 2). The participants providing the sequenced and non-sequenced positive samples had a similar gender distribution and similar probabilities of being from either from Wave one or Wave two. However, the distribution of sequenced vs non-sequenced cases differed significantly in age distribution, nationality and travel history. Specifically in the sequenced sample, there were more participants in 30–39 years age bracket compared to the non-sequenced samples, a disproportionately representation of non-Kenyan nationals and persons with a recent international travel history in the sequenced sample.

• Line 283: I am particularly interested in the observed inter county flows, but it is hard to interpret the numbers. Considering population sizes in each county, what are the phylogenetically observed import rates per 100,000? What are the rate ratios? Based on the observed data, is there any evidence that imports into coastal Kenya occurred statistically significantly through Mombasa?

We thank the reviewer for these comments.

In the revised manuscript we have added two new tables (1 & 4) which detail the population size in each of the six Coastal Kenya counties, population density and estimated import/export rates (per 100,000) for the counties.

The alluvial plots are descriptive regarding genome flows. The underlying data on the pattern of virus movement is inferred using the ancestral state reconstruction which an established phylogenetic approach that has been applied elsewhere to infer SARS-CoV-2 local and global movement (Wilkinson et al, Science 2021, Tegally et al, Nature, 2021).

The results we obtained from ancestral state reconstruction of Mombasa being a major gateway for variants entering the coastal region of Kenya is consistent with (a) the county showing the highest number circulating of lineages (n=28) compared to the other five remaining counties of Coastal Kenya, (b) approximately half (n=21, 49%) of the detected lineages in coastal Kenya had their first case identified in Mombasa and (c) Mombasa had an early wave of infections compared to the other Coastal counties.

We are not aware of an approach to consider statistical significance on these plots. The graphical display is based on the observed number events, and we would argue this is more appropriate than presenting absolute rates which would be susceptible to sampling bias.

Is it possible to account for potential bias in sequence sampling in these calculations, perhaps as done in Bezemer et al AIDS 2021? It should be possible to adjust for the proportion of sequenced individuals in PCR confirmed individuals, and it might also be possible to back calculate infected cases from cumulative reported deaths and to adjust for the proportion of sequenced individuals in infected individuals?

The reviewer suggests helpful methods to examine sampling bias, but we found this beyond scope here. Our method was based on ancestral location state reconstruction of the dated phylogeny. The approach has been used elsewhere to answer similar questions (Wilkinson et al, Science 2021, Tegally et al, Nature, 2021). The Bezemer paper uses maximum parsimony ancestral state reconstruction algorithm implemented in phyloscanner, and the Bayesian method applied to impute incomplete sampling is applicable to chains of transmission which we have not tried to reconstruct in our analysis.

Considering my earlier recommendation to document sequence sampling representativeness in Table 1, if Mombasa is found to be oversampled relative to infections, then it might also be helpful to perform sensitivity analyses in which sequences from over-represented locations are down-sampled. Another option might be to consider the approaches considered in de Maio PLOS Comp Bio 2015, or Lemey Nat Comms 2020. Thank you for investigating potential caveats and substantiating your findings in more detail.

In the revised manuscript we have clarified that our sequenced sample was proportional the number of positive cases reported in the respective Coastal Kenya counties (see-Fig.2E and Table 1).

The De Maio method uses BASTA (BAyesian STructured coalescent Approximation) into BEAST for purposes of phylogeographic analysis to compare ability to discriminate a zoonotic reservoir vs the implausible alternative cryptic human transmission. Analyses developed from these methods would be valid and interesting to apply to our dataset but would be a major new analysis and beyond the scope of the present paper. We have therefore taken the approach of: a) more clearly acknowledging sampling bias (see below) and b) undertaking sensitivity analyses (Supplementary File 5, see below). Using the larger global background sequence sets selected in a different way (more geographically balanced relative to the first round that was random), we still find that most of the virus introductions into coastal Kenya occurred via Mombasa consistent with our previous analysis.

The results are consistent with the case numbers in that (i) Mombasa experienced an earlier peak during wave one relative to other counties and (ii) had in total more cases than all the other five counties, and (iii) was commonly the first county of detection for many of the identified lineages in the region. However relative to its population, the border county of Taita Taveta had a higher import rate (13.5. per 100,000 people) compared to that of Mombasa (11.6 per 100,000 people), Table 4

Observations from our sensitivity analyses (Supplementary File 5) are included in the revised manuscript. We found that the absolute number of estimated viral imports/exports and intercounty transmission events fluctuated depending on the number of Coastal Kenya sequences and size of global comparison dataset but with a clear pattern of (a) counted events increasing with sample size (b) with Mombasa County consistently leading in the number of events; imports or exports.

• Line 292: The results are of course subject to differences in sequencing rates in each of the countries listed, and differences in reporting of these data.

This is a valid concern; to mitigate the bias that arises with these differences, unlike in the previous comparison dataset where we randomly selected a specified number of samples per month for each continent, in the revised analysis we have done the selection at country level. We limited the comparison data to maximum of 30 genomes per country per month per year. In this way, countries with high sequencing rates do not become overrepresented in our comparison dataset.

Some of these biases could be elicited through comparison to international travel data. For example, are the US and England also the top two countries from which most travellers arrive into Kenya? If such additional analyses are out of scope, it seems warranted to either strongly point to the substantial limitations of this analysis, or remove it altogether.

We concur with the reviewer on the potential bias that could exist in conclusions that arise from inferring sources of importations based on genomic data alone, available from only a few countries. However, vital quality and curated international travel data into Kenya during the study period was not available to us at the time of this analysis. We have therefore agreed to remove the previous analysis on potential origins and destinations of observed Kenya lineages from the revised manuscript.

What is perhaps striking is that Tanzania is entirely missing from this list, given extensive spread there. Another analysis that could be useful is a comparison of country specific lineage compositions, which might bypass some of the difficulties associated with substantial differences in sequence sampling/reporting rates.

SARS-CoV-2 genomic data from Tanzania has not been publicly shared to date, and hence is not included. And as indicated above, we have removed the analysis that was trying to infer sources of SARS-CoV-2 importations into Kenya.

To hypothesize on the potential lineages circulating in Tanzania, we have added a sentence detailing that 5 Pango lineages were identified among the 34 Tanzanian nationals who provided samples that were sequenced: B.1 (n=10), B.1.1 (n=10), B.1.351 (n=8), A (n=5) and A.23.1 (n=1)

• Line 536: it seems problematic that the data used in the import/export analysis did not contain all available African sequences. Can these be included in the corresponding analysis please.

In the revised manuscript we have included all accessible, good quality and contemporaneous Africa genomes in the revised manuscript (n=21,150). However due to the huge computational processing power need to process the phylogenetics for such large sequence data sets, we split the analysis into two parts, each with approximately 10,000 genomes (see Figure 3-figure supplement 1).

Notably with the increased sample size (including the analysis of 390 more genomes from coastal Kenya), we detected far more imports of SARS-CoV-2 into Coastal Kenya compared to our previous analysis (n=280 vs n=69) but only a modest change in exports (n=95 vs n=105) and inter-county virus movement events (239 vs 190).

Reviewer #2 (Public Review):

Agoti et al. analyzed SARS-CoV-2 samples collected from infected patients in coastal Kenya, collected between March 2020 and February 2021. This period spans the first two waves of COVID-19 in Kenya, and the authors aimed to understand the lineages circulating throughout the region, in comparison to the virus circulating elsewhere in Kenya and in the world. The manuscript is clearly written, and the figures and results are thorough and well described throughout. These data add to our understanding of COVID-19 in Kenya and in East Africa, and the discussion of how different lineages spread in Kenya (single clusters versus dispersed over several regions) is both interesting and potentially useful for informing public health measures.

The analyses are well done and excellently presented, but this paper is significantly lacking in a discussion of how sampling bias may affect the stated conclusions. Additionally, the paper focuses almost exclusively on genomic data and fails to closely examine epidemiological factors that may better contextualize the results presented.

We thank the reviewer for bringing this to our attention, we have added the paragraph below to the revised manuscript.

“Sampling bias is a potential limitation of this study arising from the fact that (a) demographic characteristics (age distribution, travel history and nationality) of the sequenced versus non-sequenced sub-sample differed significantly, (b) <10% of confirmed SARS-CoV-2 infections in Coastal Kenya were sequenced, prioritizing samples with a Ct value of <30.0 (Table 1); (c) the Ministry of Health case identification protocols were repeatedly altered as the pandemic progressed (Githinji et al., 2021) and (d) sampling intensity across the six Coastal counties differed, probably in part due to varied accessibility of our testing center that is located in Kilifi County (Figure 1A and Table 1). This may have skewed the observed lineage and phylogenetic patterns. To better contextualize the genomic analysis results, close examination of the case metadata is important, but unfortunately there was a lot of the metadata was missing (e.g., travel history, nationality, Table 2) which made it hard to integrate genomic and epidemiological data in an analysis. Although all analyzed genomes had > 80% coverage, very few were complete or near complete (>97.5%, n=344) due to amplicon drop-off or low sample quality and this may have reduced the overall phylogenetic signal.”

Specifically:

1) The authors do not discuss the potential effects of sampling on their import/export analyses. For example, they find that the USA and England are in the top six country sources of SARS-CoV-2 importation into coastal Kenya, as well as in the top six country destinations of viral export from the region. These two countries have generated huge numbers of sequences compared to the rest of the world, which may clearly bias these findings. While the authors do evaluate the sensitivity of their analyses by repeating them with different global subsamples, it is unclear if these subsamples corrected for large discrepancies in available data from different parts of the world.

We concur and appreciate that sampling bias is indeed a common limitation in the type of analysis we have undertaken given the variation in data collection across geographies. Some of the approaches we took to correct for this have been highlighted in our responses to reviewer #1.

In the revised manuscript, we have undertaken a reanalysis with a larger and more representative dataset at all scales of observation (Figure 3-figure supplement 1). Specifically, for the global dataset, we have revised our sub-sampling script to pick up the comparison dataset uniformly across months and countries for non-African countries. All the available African genomes have been included in our analysis including 605 collected in Kenya outside the coastal regional.

Similarly, the authors find that new variant introductions were mainly through Mombasa city, but most of the Kenyan sequences were from this region, so it is perhaps unsurprising that more lineages were found there. The authors should repeat their analyses with a more representative global subsample, or at the very least discuss these caveats in the discussion and discuss what other evidence there may be to support their findings.

Our sequencing rate by county is approximately proportional to the total number of cases seen in the county (Table 1 and Figure 2E). For Coastal Kenya, the revised manuscript included 389 additional genomes from coastal Kenya that became available while the manuscript was under review.

Thus, in the revised manuscript, we have addressed the valid sampling bias concerns of the reviewers and editor by: (i) increasing the number of analyzed genomes in our dataset for previously under-represented periods and regions, (ii) including contemporaneous Kenyan genomes from outside the coastal counties in our import/export analysis, (iii) including all available Africa genomes into the analysis and selecting a balanced global sub-sample for inclusion into the analysis. In addition, were have also provided a paragraph in the discussion section highlighting sampling bias as a caveat to interpretation of the findings of the current study:

“The accuracy of the inferred patterns of virus importations to and exportations from coastal Kenya are in part dependent on both the representativeness of our sequenced samples for Coastal Kenya and the comprehensiveness of the comparison data from outside Coastal Kenya. Our sequenced sample was proportional the number of positive cases reported in the respective Coastal Kenya counties (Figure 2E and Table 1). Also, we carefully selected comparison data to optimize chances of observing introductions occurring into the coastal region (e.g. by using all Africa data). But still there remained some important gaps e.g. non-coastal Kenya genomic data was limited (n=605). Despite this, we think the results from ancestral state reconstruction indicating that Mombasa is a major gateway for variants entering coastal Kenya is consistent with (a) the county showing the highest number lineages circulating (n=28) during the study period compared to the other five remaining Coastal counties Kenya, (b) approximately half (n=21, 49%) of the detected lineages in coastal Kenya had their first case identified in Mombasa and (c) Mombasa had an early wave of infections compared to the other Coastal counties and (d) is the most well connected county in the region to the rest of the world (large international seaport and airport and major railway terminus and several bus terminus).”

2) Restriction measures enforced by the Kenyan government are briefly introduced at the very beginning of the manuscript and then mentioned at the very end as a possible explanation for observed transmission patterns. However, there is very limited discussion of the potential effect of restriction measures throughout, and no formal analyses are presented using this kind of epidemiological information. Adding formal analyses to back up the hypothesis that relaxation of interventions may have driven the second wave of infections would make this paper much stronger and potentially more interesting.

In the revised manuscript, we have detailed the restriction measures the government of Kenya put in place in the introduction, methods, and results sections and discussed where appropriate on how we think they impacted the observed transmission patterns. We have added Supplementary Table 1 that provides the dates the various measures took effect or were relaxed.

In a separate piece of work (Brand et al, 2021 published in Science journal, 10.1126/science.abk0414), we investigated the potential drivers of the first three waves of infection observed in Kenya and we have appropriately referenced this in the revised manuscript.

We feel that additional analyses on the impact of the restriction measures on SARS-CoV-2 epidemiology and the lineage patterns observed are beyond the scope of this work whose focus was primarily genomic epidemiology.

3) Generally, the text of the manuscript focused on waves of SARS-CoV-2 transmission, while the analyses presented data aggregated by month. A clearer connection between month and wave (particularly visually, on the figures themselves) would aid in interpretation of the data presented.

This is a valid concern and a good suggestion. In the revised manuscript, for all temporal plots, we have added a line to demarcate when we switched from wave one to wave two period. Similarly, for several analyses, we have provided aggregations by wave period rather than by month.

4) One of the strengths of this manuscript is the depth to which the authors discuss the detection of specific lineages in coastal Kenya. However, there is limited discussion of these results in the context of when various lineages appeared or disappeared globally, though these details are presented in a table. Discussing the appearance of the various lineages (was it surprising to see a particular lineage at a certain time or in a certain place?) would also improve this manuscript.

In the revised manuscript, we have compared the patterns of lineage detection locally compared to all Kenya and to all continents in the newly added Figure 3. We have also discussed this aspect for the most frequent 4 lineages in both Wave one and Wave two.

Author Response:

Reviewer #1:

Hauser et al, analyze two large datasets of GPCR-G protein interactions/couplings ("Inoue" and "Bouvier"), comparing and combining them with the widely-used literature-based Guide to Pharmacology (GtP) database. As the Inoue and Bouvier datasets were based on different experimental setups, this enables the identification of which couplings are supported by more than one method. The authors also establish a normalization protocol that enables to move from qualitative to quantitative comparisons and identify couplings that might be either below are above a rigid threshold. Overall, the paper describes a new resource and the methodologies used to build this resource. The resulting coupling map is available through the GPCRdb website, a widely used resource in the field.

The authors have thus improved the ability of researchers to assess prior results and compare them to their own new data. This resource clearly and significantly upgrades options currently available and will likely be of interest and prove quite useful to scientists both in academia and in industry.

We thank the reviewer for so nicely describing the study and its prospective application.

Weaknesses include:

• The data is described mostly by broad numbers, such as the number of receptors or coupling in a subset, or percentages. While this is helpful to understand the data, this reviewer found it hard to follow the mountain of numbers. A suggestion would be to add a section where the authors pick selected examples of particular experimental data and show how their combine database can resolve previously unanswered (or wrongly answered) questions of GPCR/G protein coupling.

We have removed numbers in several places throughout Results where we had included multiple measures e.g., absolute numbers and percentages. Furthermore, where an overall number has been broken down into distributions, e.g., across different G proteins of families thereof, we moved other numbers to parentheses.

The different sections of Results that answer questions of GPCR-G protein coupling have now been presented more clearly by updating their headings and grouping them all in a subsection of part of Results called “Research Advances – Insights on GPCR-G protein selectivity”. These sections are all based on our “combined database”/coupling map. In each such section, we start at the overall level – covering all GPCRs and/or G proteins – but then give selected examples thereof that are weaved into and exemplifies the text. This approach has also been used in the new Results section “Differential tissue expression gives G proteins in the same family large spatial selectivity”, which gives selected examples of G proteins with specific tissue expression profiles.

Given that the paper has already exceeded the maximum of 5,000 words by quite a bit, we think that this approach of weaving selected examples into each selectivity insight section is the most appropriate, and that it brings most clarity. Furthermore, we hope that readers will be inspired to use our coupling map to generate additional questions for future experiments.

• The paper does not reveal new biological findings. For example, while some emphasis is placed on new data on G15, it would be helpful to take the extra step and use this to suggest new biological insights.

eLife’s author guidelines (https://reviewer.elifesciences.org/author-guide/types) state that “Tools and Resources articles do not have to report major new biological insights or mechanisms, but it must be clear that they will enable such advances to take place, for example, through exploratory or proof-of-concept experiments.” In case this manuscript is published as a Tools and Resources paper, it may therefore be sufficient to provide the foundation for future studies to reveal new biological findings.

Nevertheless, the coupling map led to biological findings relating to patterns and mechanisms of GPCR-G protein selectivity that were not described in the original studies. I.e., while this study did not generate new data, it arrived at new insights based on published data. This seems to be in line with eLife’s publication format “Research Advances” (https://reviewer.elifesciences.org/author-guide/types), and the Analysis format of several other journals. Some insights described herein have not been presented before while others have been updated in scope and precision. Furthermore, we have added a new section of Results with insights on G protein expression profiles and co-expression.

We have clarified this by updating the headings of the sections that present these insights, and grouped them under a common subheading of Results termed “Research Advances – Insights on GPCR-G protein selectivity”. However, in case we have overlooked very recent studies describing some of the same biological insights, we would please like to ask for their references and would be more than willing to revise the manuscript again to incorporate them. Furthermore, if the Reviewer is missing a particular analysis that is critical to understand GPCR-G protein coupling, please let us know.

• The authors cautiously label couplings supported by only one dataset as "unsupported". It would seem more helpful to grade couplings by a reliability scale, providing users with a wider set of data. Perhaps only couplings that are directly conflicted by negative data should be labeled as unsupported?

We understand that the term “unsupported” has been used in a confusing way. We have now replaced this term with “unique” and explained all terms in Table 1 of the revised manuscript.

To address the need for a means to grade or filter couplings by reliability, we have added the following paragraph to the manuscript:

“To enable any researcher to use the coupling map, we have availed a “G protein couplings” browser (https://gproteindb.org/signprot/couplings) in GproteinDb (2). By default, this browser only shows “supported” couplings with evidence from two datasets, but there is an option (first blue button) to changes the level of support to only one (for most complete coverage of GPCRs) or to three (for the highest confidence) sources. We propose a standardized terminology to describe couplings based on their level of experimental support from independent groups (Table 1). The criterion of supporting independent data, and the terms “proposed” and “supported”, are already used by the Nomenclature Committee of the International Union of Basic and Clinical Pharmacology (NC-IUPHAR) for GPCR deorphanization. Furthermore, the online coupling browser allows any researcher to use only a subset of datasets, or to apply filters to the Log(Emax/EC50), Emax, and EC50 values. Finally, users can filter datapoints based on a statistical reliability score in the form of the number of SDs from basal response."

Furthermore, we have added references to the online G protein coupling browser in the:

(1) Introduction ending: “On this basis, we develop a unified map of GPCR-G protein couplings that can be filtered or intersected in GproteinDb …”, (2) Fig. 2 legend ending: “Note: Researchers wishing to use this coupling map, optionally after applying own reliability criteria or cut-offs, can do so for any set of couplings in GproteinDb (1).” (3) Fig. S2 ending: “Unique couplings are hidden by default in the online G protein couplings browser in GproteinDb, as they await the independent support by a second group.”

To many scientists the most reliable option is to involve NC-IUPHAR. Gloriam is a corresponding member of NC-IUPHAR, which has mentioned the possibility of involving its many worldwide pharmacological experts to update GtP on a case-by-case basis for receptors. For example, many of the “novel” couplings jointly supported by Bouvier and Inoue may be added. This option is advantageous as it involves experts in each receptor system (often with knowledge of other relevant studies) and is backed by the authoritative organization.

• Given that this manuscript includes authors from both the Inoue and Bouvier studies, I can understand why they are not directly assessing which of the two datasets (in relation to the GtP) might be more accurate. Nevertheless, I believe this assessment should be done and that the advantages and disadvantages of the two experimental systems discussed clearly.

We believe that the three-way intersection of couplings is the most informative and therefore preferred over individual comparison of each of the Inoue and Bouvier datasets to GtP. GtP is unfortunately not suitable as a stand-alone resource – neither to contradict nor support couplings (on the G protein subtype level). This is because GtP is incomplete (especially for G12/13) and does not provide any information on the level of G protein subtypes, only families. The three-way interactions will always use GtP but adds a second dataset on top of this when validating a third dataset. Our manuscript already included a three-way intersection of datasets, allowing readers to conclude which dataset might be more accurate (then Fig. 3 and Spreadsheet 3) on a per-G protein basis.

In the revised manuscript, we have rewritten this section, which now has the heading “Bouvier’s and Inoue’s biosensors appear more sensitive for G15 and, Gs and G12, respectively. We have also made a completely new figure, Fig. 7, which more clearly illustrates for which G proteins that Bouvier and Inoue may have overrepresented or underrepresented couplings. This section specifically investigates the question of whether differential sensitivity can explain “unique” couplings. However, such unique couplings can either be due to overrepresentation or instead be true positives that are missing in GtP because of incompleteness and in the other biosensor due to lower sensitivity. Unfortunately, we will not be able to distinguish these possibilities until the research community has gained additional datasets from independent biosensors with as high sensitivity.

Whereas our study compares datasets rather than experimental systems, we have added a paragraph in the Discussion describing which aspects should be considered when choosing a biosensor. There, we reference a review from last year dedicated to biosensors and describing their pros and cons (3), and the accompanying paper by Bouvier et al. (4), comparing several aspects of the experimental system used by Inoue et al. It is also important to note that the most advantageous biosensor may be one of the two for which data is analyzed in our paper. For many studies, researchers may instead be better off with another biosensor, for example those from Lambert/Mamyrbekov (5), Roth (2) (Gαβγ sensors first described in (6-11)) or Inoue (unpublished dissociation assays using wt G proteins fused with LgBit and HiBit). These are all referenced in the Discussion.

References:

1. Pandy-Szekeres G, Esguerra M, Hauser AS, Caroli J, Munk C, Pilger S, et al. The G protein database, GproteinDb. Nucleic Acids Res. 2022;50(D1):D518-D25. 10.1093/nar/gkab852
2. Olsen RHJ, DiBerto JF, English JG, Glaudin AM, Krumm BE, Slocum ST, et al. TRUPATH, an open-source biosensor platform for interrogating the GPCR transducerome. Nat Chem Biol. 2020;16(8):841-9. 10.1038/s41589-020-0535-8
3. Wright SC, Bouvier M. Illuminating the complexity of GPCR pathway selectivity – advances in biosensor development. Curr Opin Struct Biol. 2021;69:142-9. https://doi.org/10.1016/j.sbi.2021.04.006
4. Avet C, Mancini A, Breton B, Gouill CL, Hauser AS, Normand C, et al. Effector membrane translocation biosensors reveal G protein and B-arrestin profiles of 100 therapeutically relevant GPCRs. bioRxiv. 2021:2020.04.20.052027. 10.1101/2020.04.20.052027
5. Masuho I, Martemyanov KA, Lambert NA. Monitoring G Protein Activation in Cells with BRET. Methods Mol Biol. 2015;1335:107-13. 10.1007/978-1-4939-2914-6_8
6. Gales C, Rebois RV, Hogue M, Trieu P, Breit A, Hebert TE, et al. Real-time monitoring of receptor and G-protein interactions in living cells. Nat Methods. 2005;2(3):177-84. 10.1038/nmeth743
7. Gales C, Van Durm JJ, Schaak S, Pontier S, Percherancier Y, Audet M, et al. Probing the activation-promoted structural rearrangements in preassembled receptor-G protein complexes. Nat Struct Mol Biol. 2006;13(9):778-86. 10.1038/nsmb1134
8. Schrage R, Schmitz AL, Gaffal E, Annala S, Kehraus S, Wenzel D, et al. The experimental power of FR900359 to study Gq-regulated biological processes. Nat Commun. 2015;6:10156. 10.1038/ncomms10156
9. Breton B, Sauvageau E, Zhou J, Bonin H, Le Gouill C, Bouvier M. Multiplexing of multicolor bioluminescence resonance energy transfer. Biophys J. 2010;99(12):4037-46. 10.1016/j.bpj.2010.10.025
10. Bunemann M, Frank M, Lohse MJ. Gi protein activation in intact cells involves subunit rearrangement rather than dissociation. Proceedings of the National Academy of Sciences of the United States of America. 2003;100(26):16077-82. 10.1073/pnas.2536719100
11. Janetopoulos C, Jin T, Devreotes P. Receptor-mediated activation of heterotrimeric G-proteins in living cells. Science. 2001;291(5512):2408-11. 10.1126/science.1055835

Reviewer #2:

This study is a meta-analysis of previously reported studies on G protein-coupled receptor (GPCR) coupling to G proteins. The data sets are from three distinct sources: a compendium compiled by the International Union of Basic & Clinical Pharmacology (IUPHAR), and two data sets compiled by two separate laboratories. Each of these data sets describes the coupling of members of the superfamily of non-sensory GPCRs (~200 genes) to the large family of G protein alpha subunits (~20 genes). The authors try to arrive at a consensus for receptor-G protein coupling from the three data sets, as well as identify and highlight differences or incongruencies. Compiling these vast data sets into a unified format will be extremely useful for investigators to understand receptor and effector relationships. The meta-analysis will help to deconvolute the complex physiology and pharmacology underlying hormone or drug actions acting on receptor superfamilies. A better understanding of receptor-G protein selectivity and/or promiscuity will ultimately help in identifying safer therapeutics.

We appreciate the summary and the explanation of the usefulness of our meta-analysis and its potential impact.

Author Response:

Reviewer #3 (Public Review):

In both neurons and glia (astrocytes, microglia, and oligodendrocytes) of patients with amyotrophic lateral sclerosis (ALS) and/or frontotemporal dementia (FTD), the DNA/RNA-binding protein TDP-43 is mislocalized from the nucleus to the cytoplasm where it forms pathological inclusions. Because this subcellular redistribution leads to TDP-43 depletion from the nucleus, the pathogenic mechanism may involve (1) the loss of nuclear function, (2) a gain of cytoplasmic function, or (3) a contribution from both. Heo, Dongeun et al., teases apart this first possibility by investigating the depletion of TDP-43 within specific stages of the oligodendrocyte lineage in vivo and raising the possibility of glial damage in disease progression. The authors found that the consequences of TDP-43 deletion in oligodendrocytes was dependent on the stage of oligodendrocyte maturation. First, they find that deletion of TDP-43 from oligodendrocyte precursor cells (OPCs) resulted in their rapid death, however OPCs that retained TDP-43 expression repopulated to their normal density. Secondly, they find that constitutive deletion of TDP-43 from early premyelinating oligodendrocytes exhibited seizures and early lethality. Similar conditional deletion of TDP-43 from early premyelinating oligodendrocytes in the adult CNS induces abnormal morphological changes, motor discoordination (but no seizures), and premature lethality. Meanwhile, constitutive deletion of TDP-43 from myelinating oligodendrocytes did not lead to any gross phenotypes or shortened lifespan. However, early deletion led to oligodendrocyte degeneration and astrogliosis followed by oligodendrocyte regeneration. Interestingly, in both early and mature oligodendrocytes loss of TDP-43 lead to morphological changes, thinner myelin, less myelinated axons, and aberrant myelination. These results are very interesting and opens the door for further questions, such as why are the oligodendrocytes mislocalizing their myelination targets? Why does early deletion of TDP-43 cause such drastic phenotypes? Lastly, to understand the molecular consequences of TDP-43 deletion in both early and late myelinating oligodendrocytes the authors perform RNAseq on FACS isolated KO cells and controls. The authors uncover that loss of TDP-43 from oligodendrocytes in the adult CNS leads to altered splicing of key regulators of oligodendrocyte growth and morphogenesis.

These findings complement those of Wang, J et al 2018 that shows depletion of TDP-43 in mature oligodendrocytes in the spinal cord is indispensable for the proper functioning of mature oligodendrocytes, including myelination and cell survival. Although Wang, J et al 2018 saw no apparent harm to motor neurons of mice with TDP-43 deleted in mature oligodendrocytes, the mice did have progressive motor deficits and early lethality - similar to Heo, Dongeun et al.

Strengths:

To investigate the role of TDP-43 within distinct stages of oligodendrocyte maturation, the authors used four different Cre and CreER mouse lines: 1) Pdgfra-CreERT2, 2) Mobp-iCre, 3) Mog-iCre, and 4) Mobp-iCreERT2, thus allowing them to inactive Tardbp in both the developing and mature CNS. By performing thorough analysis at each discrete stage within the oligodendrocyte lineage, the authors uncovered differential requirement for TDP-43 in cell survival and structural maintenance as OPCs transform into early and late myelinating oligodendrocytes. These results are important because they elucidate the contribution of a DNA/RNA-binding protein to oligodendrocyte development. Additionally, the results of the conditional deletion of TDP-43 from early premyelinating oligodendrocytes in the adult CNS is critical for understanding how nuclear depletion of TDP-43 from oligodendrocyte might contribute to disease pathogenesis.

The authors also performed bulk RNAseq on early and late myelinating oligodendrocyte controls and TDP-43 KO cells. In doing so, not only did they uncover hundreds of differentially expressed (DE) genes between each control and KO, but thousands of DE genes between the two controls. This experiment also confirmed that Mobp-iCre and Mog-iCre mouse lines were able to target different stages of oligodendrocyte development. This dataset is very exciting to both the developmental glial biology community and to those trying to understand the molecular mechanisms within glia that contribute to neurodegenerative disorders.

Minor weaknesses:

In Figure 1, the authors observe that in the cKO mice, the OPCs are dying because they observe a lack of NG2 staining. Is it possible the OPCs have changed to another cell identity that is NG2- in the absence of TDP-43? Tunnel staining would clarify that indeed the cKO OPCs are dying. Furthermore, the authors note that despite the extensive death of OPCs, they do not see signs of GFAP+ astrogliosis. Is there instead an increase in microglia activation? Throughout the paper, the authors use only GFAP+ astrogliosis to measure widespread inflammation. It would be more compelling to also look at the contribution of microglia or other inflammatory markers to measure inflammation.

To perform fate-mapping of TDP-43 deficient OPCs, we crossed the Cre-dependent EGFP reporter (RCE) to Pdgfra-CreER x Tardbp floxed mice (PDGFRα-TDP43). By assessing EGFP expression, we determined that disrupting Tardbp expression in OPCs results in rapid degeneration of OPCs within one month. The dramatic reduction in EGFP^+ OPCs indicates that knockout of Tardbp results in cell loss rather than downregulation of NG2 and/or a shift in cell identity.

We agree that it would also be informative to extend these studies to examine other markers of neuroinflammation. We settled on GFAP immunostaining for visualization purposes, as cortical GFAP immunoreactivity is limited in control mice, providing the greatest sensitivity and has been established as a robust biomarker of neuroinflammation. As the external consequences are not the primary focus of this study and are likely to be both complex and time dependent, we feel that these studies are outside the scope of the present study.

As shown in Figure 3, loss of TDP-43 in oligodendrocytes at early and mature stages leads to similar profound phenotypes within both the Mobp-TDP43KO and Mogp-TDP43KO mouse lines. However, only early when TDP-43 is deleted using the Mobp-TDP43KO, are there severe physical phenotypes in the mice and early lethality. However, the authors show that there is no change in the density of ASPA+ mature oligodendrocytes in Mobp-TDP43KO and Mogp-TDP43KO at any stage. If there is an increase in the turnover of oligodendrocytes and oligodendrocyte number stays the same, can the authors speculate in their discussion what they believe is causing the severe seizure and lethality phenotypes in the Mobp-TDP43 KO mice? The authors mention that there is an increase in astrogliosis. Are they suggesting this change in astrocyte activity could promote the severe phenotypes and early lethality? Because motor neuron number is not affected by TDP-43 deletion, but no direct measurements of motor neuron activity were taken, it is hard to make sense of the phenotypes observed.

In the Discussion, we speculated that early deletion of TDP-43 in oligodendrocytes (Mobp-TDP43 KO) compromises their long-term survival. This gradual degeneration of oligodendrocytes, which is masked at the population level by OPC mediated regeneration, nevertheless induces widespread astrogliosis, indicative of progressive neuroinflammation. Oligodendrocyte loss has previously been shown to induce neuroinflammation, seizures and neurodegeneration (Traka et al. 2016). We agree that there are many interesting features that remain to be understood about the phenotypic consequences of TDP-43 loss within oligodendrocytes, such as possible reorganization of myelin patterns (see Orthmann-Murphy, Call, et al. 2020) and mechanistic links between oligodendrocyte degeneration, gliosis and inflammation. We are pursuing some of this analysis now, but they necessitate extensive interrogation of the transgenic mice using new assays. Thus we feel that these experiments are outside the scope of the current study.

Author Respoinse

Reviewer #2 (Public Review):

In the results of Fig. 2, the proteins are emitted at distance epsilon from the cortical boundary. From there, they locally perform 1D diffusion to the boundary, so most of them would readsorb once they diffuse a distance epsilon. Only a small fraction would extend past epsilon, which I assume is why the concentration drops by orders of magnitude beyond epsilon. Is such a concentration drop realistic given typical numbers of proteins in cells?

This is a good point. In [29], McInally et al. investigate kinesin-13 concentrations in Giardia and find that it drops sharply near the pole (about three to four orders of magnitude), as surmised by the referee. The drop off we see in our model is like what McInally et al see in terms of orders of magnitude decrease in the concentration gradient close to the pole.

It should be clarified if the proposed size scaling is independent of the specific choice of the distance epsilon of the point of protein release from the anterior pole. I don't see any reason why this distance should increase with cell size as epsilon = 0.05 R (on page with equation 5). It's unclear if the size scaling of the concentration gradient might be dependent on the assumption epsilon ~ R.

Figure R1 shows the dependence of the gradient on epsilon and see that the concentration gradient from the pole is unaffected everywhere beyond the source.

Figure R1. Concentration gradient for cells with the source at different distances from the pole (ϵ) Concentration profiles with differing source points. We start very close to the pole and move further away. The radius of the sphere is 10 μm, the diffusion constant D=1 μm^2/s and the transport speed along the cortex is v=1μm/s.

Author Response

Reviewer #1 (Public Review):

Canonical miRNA-targeting involves pairing between the miRNA seed region (nucleotides 2-7, counting from the miRNA 5' end) and a target mRNA. Pairing downstream of the seed can also influence target recognition, and in some cases 3' pairing can compensate for imperfect seed complementarity. In this study, McGeary et al. investigated the features of such miRNA 3' compensatory sites in a high-throughput manner by adapting the RNA bind-n-seq (RBNS) method used previously to characterize binding of purified Argonaute2-miRNA complexes to a random pool of target RNAs.

Strengths To focus on 3'-compensatory sites, which are rare in random libraries, the authors designed libraries of RNAs containing imperfect seed complementarity followed by 25 nucleotides of random sequence. This approach allowed investigation of a range of 3' pairing possibilities far more extensive than any previous work. Results provide several unexpected findings. Contrary to the prevailing model that miRNA nucleotides 13-16 are most efficacious for 3' pairing, the authors found the optimal position varies between miRNA sequences and is often shifted to include G nucleotides in the miRNA. The number of unpaired nucleotides bridging seed and 3'-paired regions is also a factor-certain let-7 sites preferring an offset of +4 target nucleotides, indicating a high affinity target-binding mode previously unknown. Additionally, the contribution of miRNA 3' pairing correlates poorly with predictions from nearest-neighbor parameters. Overall findings greatly expand insights into miRNA 3' pairing and provide metrics for improving target prediction.

Weaknesses Conclusions are drawn entirely from RBNS data sets, leading to a few limitations. Affinity measurements are limited to relative KD values, making comparison to other work in the field indirect and potentially problematic. For example, let-7 target sites in lin-41 have 11-19 3' compensatory pairing, +1nt offset, which (based on Fig. 2B and 2C) has a greater relative KD than the let-7 8mer canonical site. However, a recent result showed an in vivo lin-41 reporter with two 8mer sites is less repressed than same reporter bearing the wild type 3'-compensatory sites (1). In the absence of KD values and/or cellular repression data for these specific sites the noted differences are difficult to reconcile. Additionally, analyses assume miRNA-target complementarity directly correlates with physical pairing between miRNA and target. However, because physical pairing occurs within the Argonaute2-miRNA complex, this may not always be the case

1. Duan, Ye, Isana Veksler-Lublinsky, and Victor Ambros. "Critical contribution of 3'non-seed base pairing to the in vivo function of the evolutionarily conserved let-7a microRNA." bioRxiv (2021).

Although conclusions from our affinity measurements agree with those of the Duan et al. (2021) bioRxiv submission with respect to the relative importance of pairing to let-7a nucleotides 11 and 12 compared to that of pairing to nucleotides 18 and 19 (Figure 7—figure supplement 1D), some of the more detailed conclusions do indeed differ. These differences might be due to our measurement of site affinity rather than repression (as mentioned by the referee). Alternatively, they might be due to either differences between flanking sequences of the sites or differences between human and C. elegans systems. With respect to whether two 8mer sites without 3′ pairing are as effective as the endogenous lin-41 sites, the results of Duan et al. (2021) are another step removed from ours because they measure mutant phenotypes rather than lin-41 repression. Nonetheless, as the reviewer suggests, the strain in which lin-41 seed pairing is restored and 3′ pairing is disrupted has phenotypes consistent with insufficient repression by let-7, which would not be expected if relative affinity of 8mer sites matched the affinities of the endogenous lin-41 sites.

To investigate the relationship between 3′-pairing affinity in vitro and repression in cells, we performed a massively parallel reporter assay and have included these new results in our revision (Figure 3). Overall, we found that affinity in vitro corresponded well to repression in cells (r2 = 0.71). With respect to the example mentioned by the referee, we observed that dual 8mer sites imparted repression similar to that of the lin-41 sites (Figure 3B, bottom). We also observed some benefit of the endogenous flanking-sequence context of the lin-41 sites, but this benefit extended to the other sites as well, including to the 8mer sites (Figure 3—figure supplement 2). Thus, differences between our results an those of Duan et al. (2021) appear to be primarily attributable to differences between our two systems—perhaps a difference between human and C. elegans.

With respect to the referee’s last point, we use “pairs” and “pairing” as synonymous with “Watson–Crick matches” and “complementarity.” In our revision, we have clarified that our use of “pairing” refers to potential pairing, not physical pairing.

Reviewer #3 (Public Review):

The Bartel Lab tackles the elusive role of the 3' part of miRNAs to contribute to the binding of target RNAs. In short, the presented data lead to the following conclusions:

1- The positions most important for 3′ pairing differed between different miRNAs;

2- Compared to Grimson et al. 2007, the authors show that preferred pairing often does not correspond precisely to positions 13-16, but it does always at least partially overlap such stretch of nucleotides;

3- Two distinct 3′-binding modes seem to exist. Yet, arriving to that conclusion (that is at the core of the title) is not easy for the reader (see below);

4- Increasing miRNA length can sometimes improve 3′ binding affinity, but it cannot substitute for other features required for high affinity to the miRNA 3′ region.

5- Central to the paper and underlying several analyses, the authors show that parameters derived from interactions of purified RNAs in solution are not directly relevant to miRNAs associated with AGO2;

6- GG/GC/CG dinucleotides in positions 13-16 most likely participate in productive 3' pairing, and extra Gs beyond this stretch also favor.

7- Importantly, there is a functional difference between 3′-supplementary and 3′- compensatory pairing in regard to the presence of mismatches in the seed.

8- By using chimeric miRNAs, the authors separate effects of seed-mismatches, to those effects derived from the length, position, offset, and nucleotide-identity preferences of the 3′ region;

9- Finally, the two different 3' binding modes presented in this manuscript help rationalizing some aspects of target-dependent miRNA degradation (TDMD).

The title: Should the term "seed mismatch" be included to highlight one of the most important aspects of the paper?

We have changed the title to “MicroRNA 3′-compensatory pairing occurs through two binding modes, with affinity shaped by nucleotide identity and position,” to indicate that the conclusions of the title were derived using seed-mismatch sites.

The Introduction: Well-written and informative, but perhaps too long. The authors should explain why they have chosen Ago2 for all their experiments, when they continuously refer to "AGOs" in the Introduction.

The Introduction has been shortened to enhance readability. We have also added justification for using AGO2, pointing out that this paralog is typically the most highly expressed and is the one most frequently used by others for biochemical and structural studies of AGO–miRNA complexes.

The results: Specific comments: The authors jump from Fig. 1A to Fig. 1C. Fig. 1B is mentioned at the Introduction. Should Fig. 1B be moved to the supplement?

Although we jump from Figure 1A to Figure 1C in the Results section, Figure 1A and Figure 1B are both cited in the Introduction section. Because of the importance of Figure 1B for the Introduction, we have opted to keep this panel in the main text.

The authors mainly focus on let-7a and two well-known miRNAs: miR-1 and miR-155. The RNA bind-n-seq analysis reveals different binding behaviors. Are those miRNAs representatives? In how much the analysis provided by the authors get close to a (nearly) full picture of 3' miRNA binding modes?

We initially observed evidence for the positive-offset binding mode in our analysis of let-7a (Figures 2 and 3) but not in our analyses of miR-1 and miR-155 (Figure 4). Nonetheless, we also observed evidence of this second binding mode in our analyses of miR-124, lsy-6, and miR-7, the three other miRNAs with AGO2-RBNS datasets (Figure 5—figure supplement 4). With respect to the question of whether there are more than two binding modes, we have no evidence for additional binding modes but of course cannot rule out this possibility.

The (many) figures displaying color-gradient squares to calculate Kds are elegant but I would argue that replacing some of them by tables and numbers would be more informative and less demanding for the eye of the reader.

Although replacing each of the color-gradient squares with a number might be more informative when comparing values for just a few sites, we wonder if digesting the entire table of numbers would be less demanding for the reader. Because replacing the heat maps with tables of numbers would also take much more space, we have opted to keep the heat maps.

I would also suggest to bring back TargetScan at the Discussion (as in the previous paper by Mc Geary et al. 2019), to highlight the benefits of the biochemical approach on top of the powerful and universally used TargetScan.

Ideally, the insights gained in this type of study could be used to improve the ability of TargetScan to predict the efficacy of sites with 3′ pairing. However, even with machine learning, we will need binding information for 3′ pairing of more miRNAs before we can build a model that generalizes to miRNAs of any sequence and thereby improve TargetScan.

A general comment goes towards the presentation of the data. In contrast to other manuscripts, the authors rely on a unique type of data, that emerges from binding assays on nitrocellulose membranes, and their quantification. For a better visualization, I would encourage the authors to include examples of such bindings and quantifications.

As the reviewer points out, most data of this paper come from AGO-RBNS experiments, which include a filter-binding step to separate library molecules that are bound from those that are unbound. However, because these data are derived from sequencing of amplicons prepared from RNA extracted from the nitrocellulose membranes, they cannot be visualized in the same manner as data from classical filter-binding experiments.

Author Response

Reviewer #2 (Public Review):

In this manuscript Shore et al determine that Nucleoporin 107 (Nup107) is required in developing female somatic cells [intermingled cells (ICs)] for proper ovarian development. The authors propose that Nup107 is required for proper orientation of ICs during development to ensure proper function of escort cells during adulthood. They show that loss of Nup107 results in ectopic germline stem cells (GSCs) away from the GSC niche (primarily cap cells and terminal filament cells) and that these ectopic GSCs display hypermorphic Bone Morphogenic Protein (BMP) signaling. The authors also find that Nup107 regulates expression of the transcription factor doublesex (dsx) and share a common transcriptional target of AdamTS-A. Through knockdown/rescue experiments, the authors show that expression of Dsx-F can rescue phenotypes observed with ovarian somatic knockdown of Nup107 and that ovarian somatic knockdown of AdamTS-A mimics loss of Nup107 and dsx (including loss of escort cell membrane protrusions and enhanced BMP signaling). These data provide an interesting non-cytoplasmic to nuclear transport mechanism for Nup107 in regulating oogenesis.

This is a well written manuscript with proper experimental analysis (sufficient n's, proper statistics). However, it is unclear how the authors came to some of their conclusions and how their results significantly enhance findings from prior studies exploring how disruption of organization of somatic cells of the developing female gonad influences adult escort cell protrusions and preventing expansion of BMP signaling to ensure proper germline stem cell cyst differentiation.

Points to consider:

1. It was unclear reading the first part of the paper how the adult phenotypes were connecting to defects during larval development. It would further strengthen the rationale for describing the adult phenotypes first if the authors perhaps show the larval gonad defects (abnormal IC stacking/arrangement) prior to showing adult phenotypes. This would also help with citing previous studies that have also found the correlation with incorrect IC placement and ectopic GSC-like cells in adulthood (e.g., Tseng et al., 2018, Stem Cell Reports).

We appreciate this insight and have changed the manuscript as advised, beginning with the larval gonads (line number 116) and then progressing to the adult ovaries (line number 156).

1. It would also help the reader to know that nuclear pore complex proteins have roles outside of nuclear-cytoplasmic transport early in the manuscript as opposed to only in the discussion.

As suggested, we have included this in the introduction (line number 63).

1. It is unclear the model the authors are proposing for the Nup107-Dsx-AdamTs relationship. Are the authors proposing that Nup107 can regulate the import of Dsx or is directly regulating dsx transcription (based on the RNA-sequencing results)? A little more explanation would be helpful.

We have elaborated on this in the discussion (lines numbers 482-512).

Reviewer #3 (Public Review):

This is an interesting story, providing molecular explanation for XX-OD, caused by mutations in Nup107 gene. Overall, the experiments are thoroughly conducted, and the results are important in understanding XX-OD. However, there are some issues that need to be addressed, as the data presented in this study still leaves some gaps that need attention. Whereas I do not think that all the gaps need to be filled for a paper to be published, the gaps that remain in this paper leaves confusions and inconsistencies, they need to be addressed.

1. Dsx is the major target of Nup107. Although it is clear that Dsx is downregulated in Nup107 mutant, how exactly Nup107 regulates Dsx expression remains entirely unclear. Does Nup107 functions as transcriptional regulator of Nup107?

As previously mentioned, this is an important question that we hope to answer in future. However, we think that the answer to this question is beyond the scope of this work as our data have clearly demonstrated that Dsx-F acts downstream of Nup107 to regulate activities of unique cell types in the larval as well as adult ovaries to modulate germline soma interactions underlying ovarian morphology and GSC development.

1. Nup107  Dsx axis is required for escort cells to encapsulate germ cells to allow the downregulation of BMP signaling in germ cells, which in turn allows differentiation of germ cells. Whereas this axis appears to operate, the relationship between germ cell encapsulation and BMP signaling is quite unclear. Is encapsulation upstream or downstream of BMP modulation? Authors provide the evidence that adamTS-A, which modulates the amount of extracellular BMP ligands, is the downstream target of Dsx, and adamTS-A appears to regulate encapsulation. This makes it unclear whether encapsulation is required to down regulate BMP, or BMP regulates encapsulation (and if the latter, what is achieved by encapsulation that leads to germ cell differentiation?)

This is an excellent point and we followed reviewer’s suggestion to resolve this issue. To answer this question, we knocked down coracle activity specifically just in the ECs (new Figure 4-Figure supplement 2 & 3). This turned out to be highly informative and we thank the reviewer for encouraging us to do this experiment.

This manipulation revealed that encapsulation is likely upstream of BMP, as disruption of the cellular processes responsible for the encapsulation of germ cells, leads to dysregulation of BMP signaling. Our data thus argue that Nup107, Dsx and AdamTS-A likely function in ECs and are necessary for the formation and maintenance of the cellular protrusions which are required for restricting the BMP signal emanating from the GSC niche. These observations also suggest that Adam-TS-A, which typically resides in the extracellular matrix, is essential for the proper formation and/or maintenance of these cellular protrusions. Altogether these observations indicate that AdamTS-A modulates BMP signal distribution indirectly by regulating the density/length/ activity of the cellular protrusions that restrict the propagation of BMP signal. We have included a short discussion of this possibility at a relevant juncture in the revised discussion. See new addition to discussion, “AdamTS-A modulates BMP signaling via regulation of EC extensions (line number 556).

1. Dsx regulates germ cell differentiation in a female specific manner. I am somewhat puzzled by distinct phenotypes of Dsx depletion described in this paper (germ cell differentiation defect in female only) compared to other previous reports on Dsx function in male and female germline. Is there any sex-transformation phenotype? The part of this manuscript that describes Dsx appears to be detached from the context (published literature on Dsx), and it's somewhat difficult for me to interpret the results.

As mentioned previously (and also in the manuscript), we have not addressed the effect of compromising dsx in males since the effect of Nup107 is largely female specific and males are not obviously affected by Nup107 mutation. Whether this is unique to the specific point mutation in nup107 remains to be determined, however.

We have addressed the question regarding previous reports in great detail above, in point number two of the editor and in the manuscript as well (See new addition to discussion, “Dsx is essential for proper ovarian development” line number 535).

Author Response

Reviewer #1 (Public Review):

The genetic destruction of the prothoracic gland by the cell death gene Grim is an accepted method. They need to indicate in this case, how long the prothoracic gland is detectable in the third instar after exposure to the elevated temperature to inactivate the GAL80. For instance, are any gland cells still functional at the time of critical weight? How does this affect the onset of Achaete progression which normally occurs beginning at 5 hr after ecdysis which they show is dependent on low levels of ecdysone? Do you get the same result if you place them at the elevated temperature 12 hr after ecdysis to the 2nd instar, a time when the ecdysteroid titer has already risen to cause the molt to the third instar?

These are all valid points, and future experiments should explore manipulating larvae at earlier developmental times. We have not tried transferring L2 larvae to higher temperatures, but would be keen to explore this option. We would need to work out the timing of the ecdysteroid pulse in L2 larvae reared at 17oC first to make this work.

Our previous publication shows that some PG cells are still visible at 42 h after L3 ecdysis in PGX animals, although the whole ring gland is dramatically reduced in size (Herboso et al 2015 Supp Fig 3E,F). However, given the growth and patterning defects are similar to those found in previous studies where ecdysone signalling was inhibited in the wing disc (Mirth et al, 2009; Herboso et al 2015), and because these animals cannot pupariate, it is clear that the residual cells do not produce sufficient ecdysone to promote proper development. We believe the gland cannot produce normal ecdysone titres even early in the third instar because:

• Delays in patterning for Achaete and Senseless in the wing discs are similar to those we found when over expressing a dominant negative form of the ecdysone receptor specifically in the wing (Mirth et al 2009)

• The growth defects in the wing discs are similar to other manipulations that reduce ecdysone synthesis in the prothoracic gland, like expressing RNAi against smt3 (Herboso et al 2015)

• In response to Reviewer 3’s recommendation, we have analysed the ecdysone titres in fed PGX and control larvae and found that PGX produce significantly lower, albeit variable, 20E titres than controls (Figure 2 Supplement 1).

One concern with the paper is why the authors begin contrasting the effects of temperature on embryonic development and wing disc patterning in the Discussion on p25. This discussion seems irrelevant to the experimental manipulations done in this paper concerned with nutrition and hormone levels. Nothing was done relative to environmental temperature effects except to genetically kill the prothoracic gland, the source of ecdysone. I recommend omission of this section of the Discussion.

We were attempting to make a point about rates of patterning across developmental contexts, but obviously missed the mark. We have deleted this paragraph.

Author Response

Reviewer #1 (Public Review):

Identifying private peptides for generating personalised cancer vaccines is a promising approach to launch robust anti-tumor response; however, the challenges remain in developing an effective process to achieve that. In this manuscript, the authors present an interesting and powerful pipeline (PeptiCRAD) to achieve this goal by examining CT26 model. Overall, this manuscript is well written and presented. Despite that this work presents interesting findings and pipeline, I have the following concerns. I do feel that this manuscript will improve if these concerns can be addressed.

We thank the reviewer very much for having appreciated the quality and the originality of our work.

1. It will be critical to confirm TILs and T cells in draining lymph nodes indeed recognise the peptide used in Figure 7-8 by ELISPOT of IFNg.

We agree with the reviewer´s comment as regard to confirming that TILS and T cells in draining lymph nodes recognise the peptide used in Figure 7-8 by functional characterization in an ELISPOT IFN-γ assay. In our experience, the ELISPOT assay works at the best when fresh samples are employed; additionally, the splenocytes are source of enough cells to test individual mouse reactivity to single peptide. To this end, as the samples from figures 7 and 8 were frozen, we decided to repeat the animal experiment according to figure 7 schedule treatment to perform then the ELISPOT on splenocytes freshly harvested from mice. Following the previous results, we selected the best group (PeptiCRAd1) to further investigate the peptide response; untreated mice (Mock) and Virus alone (VALO-mD901) were used as control as well. Interestingly, the peptide deconvolution showed T cell reactivity to one peptide (RYLPAPTAL, peptide 2) (Figure 1A) in the PeptiCRAd1 group, in contrast no T-cell reactivity was observed for SYLPPGTSL (peptide 1) (Figure 1B). These data highlighted the role of an individual antigen in eliciting specific anti-tumor T cell response, appearing an interested candidate for further proof of concept in animal experimental setting.

Figure 1 Interferon-γ Elispot results Harvested splenocytes from the treatment groups (as indicated in the figure) were functional characterized in an IFN-γ ELISPOT assay; individual response to SYLPPGTSL A) and RYLPAPTAL B) for each mouse is reported as IFN-γ spot forming cells (SFC)/106 splenocytes. The data are depicted as single dots plot and mean + SEM is shown. (Virus=VALO-mD901, PC=PeptiCRAd).

1. It would be interesting to see if this pipeline can be used to identify human peptides in human melanomas.

We thank the reviewer for pointing out that this pipeline can be used to identify human peptide in human melanomas. Indeed, the work here described is a proof concept meant to be translated in human setting. To this end, in the lab we have two projects on-going that are exploiting the same pipeline to investigate the human epithelioid and human mesothelioma ligandome landscape. Regarding this latter, we are investigating four different human cell lines (H2B, MSTO211H, H2452 and JL1). As shown in the picture below (Figure 2), the peptide length distribution showed an enrichment in 9mres in both replicates (Rep1 and Rep2), in line with a ligandome profile. The analysis of the binders revealed that most of them were good binders (according to EL-Rank score) for at least one of alleles for each cell line. Following the pipeline reported in this manuscript, to select candidate peptides we applied two different approaches; the first approach relied on RNA seq analysis to check which source proteins of the peptides isolated in the ligandome analysis were reported as upregulated or downregulated in resected tumor compared to normal tissues.

(Fromhttps://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE51024 GSE51024). The second approach (analysis still on-going) will be the use of HEX software.

Regarding the epithelioid project, we have analysed the ligandome profile of two human cell lines: NEPS and VA-ES-BJ. Please find below the example of the ligandome analysis for VAES- BJ cell line (Figure 3). Overall, the analysis outcome was similar to published dataset (aminoacidic length distribution, Gibbs clustering profile, amount of binders) confirming the good quality of the ligandome landscape identified. Next, we applied HEX analysis to narrow down the list of peptide candidates for further test. We are currently in the stage of collecting more different epithelioid cell lines to expand our cohort of samples.

Figure 2 Mesothelioma project (data not published)

Figure 3 Epithelioid project (data not published)

Author Response

Reviewer #2 (Public Review):

The authors model drug uptake with a lag time (t0), after which there is a constant rate of drug uptake. But why is there such a lag time at all? This would suggest a positive feedback loop in drug binding. However, then one would not necessarily expect a constant drug uptake rate afterwards. The rationale for this model should be better explained. Correlating the fluorescence measurements (as in Fig. 1) with the single-cell elongation rates (as in Fig. 5) could help to identify if the lag in drug uptake coincides with the lag in cell growth.

We agree with the reviewer that the lag in drug uptake coincides with the lag in cell growth, our data in Figure 2 clearly support the correlation between lag in roxithromycin-NBD uptake and lag in cell growth during treatment. We also agree with the reviewer that other intracellular mechanisms could contribute to lag in drug uptake including a positive feedback loop in drug binding or a positive feedback loop between efflux and drug accumulation (Le et al. mBio 12, e00676, 2021).

We have added this new information on lines 330-333 of our revised manuscript.

We have also rephrased the text on lines 103-104 and 216-217 to clarify that the drug uptake rate is not constant and that we have taken this into account by modelling the drug uptake rate as a dynamical variable (described by the second differential equation of the model).

Finally, we have now explicitly stated that the primary focus of our model is to capture the phenomenology of drug accumulation in our experiments, for example in terms of the measured lag in drug uptake and the time-varying uptake rate. For this reason we have not made assumptions regarding the underlying biological mechanisms (e.g. positive feedback). However, more detailed models will be necessary in the future as we begin to dissect the mechanisms underlying antibiotic accumulation dynamics in individual cells.

We have now discussed this information on lines 209-212 of our revised manuscript.

The fact that t0 and k1 are always strongly anti-correlated suggests that these two fit parameters are not independent and simply reflect the same underlying process. It would be critical to clarify this point for the entire analysis of correlations between fit parameters. To this end, the confidence intervals for the fit parameters and their correlations should be estimated using a suitable numerical optimization algorithm. It only makes sense to interpret correlations between fit parameters obtained from different cells if such an analysis shows that the fit parameters are independent (uncorrelated or only weakly correlated) for each individual cell.

Following the reviewer's input we have measured the correlation between the different kinetic parameters for each individual cell. We found that for 86% and 79% of cells across all antibiotic treatments there was a positive correlation between t0 and k1 and between t0 and Fmax in the posterior Bayesian distribution (i.e. the distribution of parameter values for which the model behaviour matches the data). In contrast, at the population level (using the maximum likelihood estimate for each cell) we found a significantly negative correlation between t0 and k1 for the accumulation of polymyxin B, octapeptin and roxithromycin probes and between t0 and Fmax for the accumulation of polymyxin B, octapeptin, linezolid and trimethoprim probes (Table 2). Finally, we found a significantly positive correlation between k1 and Fmax for the accumulation of polymyxin B, ciprofloxacin and roxithromycin probes (Table 2). The latter correlation was partially imposed by the definition of Fmax in the model (as already acknowledged in the submitted manuscript) and in fact we found that 78% of the cells displayed a positive correlation between these two parameters at the single-cell level. Taken together these data demonstrate that the measured negative correlation between t0 and k1 for the accumulation of polymyxin B, octapeptin and roxithromycin is not due to the fact that t0 and k1 reflect the same underlying process.

This new information is discussed on lines 267-270 and 275-277 of our revised manuscript.

The results in Figure 4 are confusing: It seems unlikely that cells are a large enough 'antibiotic sink' to protect neighbouring cells, especially given that cells do not seem to be affected by the nutrient uptake of their neighbours. Furthermore, the opposite correlation (where drug accumulation increases with more 'screening' cells) is very hard to rationalize. A plausible explanation for this effect would be needed. Here, it would be helpful to estimate the molecule numbers (concentrations), uptake rates, and diffusion coefficients of the different antibiotics, compare them to those of nutrient molecules in the growth medium, and explain based on this why the 'screening' cells can have different effects for these molecules on the relevant time and length scales. Without more support there is a concern that these observations may be due to technical artefacts.

Following the reviewer input we have now explicitly advanced the hypothesis that delayed accumulation of membrane targeting drugs in bacteria screened by other cells could be explained by a transient reduction in the extracellular drug concentration around these bacteria (compared to the concentration in the main microfluidic chamber) due to rapid drug binding to the membranes of screening cells. In accordance with this hypothesis, when we run 2-dimensional numerical simulations of drug diffusion in channels hosting bacteria with a high drug absorption rate (g=0.2 mol m-2 s-1, see Methods), we found a gradient in extracellular drug concentration along the channel length: for the first 90min post drug addition, the concentration was highest around the bacterium without screens and lowest around the bacterium with four screens (new Figure 3-figure supplement 1A). On the contrary, in the presence of bacteria with a low absorption rate (g=0.002 mol m-2 s-1), the extracellular drug concentration equilibrated along the channel length within 2min post drug addition to the device (Figure 3-figure supplement 1C). Accordingly, in the presence of bacteria with high absorption rate, the intracellular drug concentration (that we simply modelled as concentration at the bacterial surface) reached saturation levels in the bacterium without screens within minutes post drug addition, whereas the bacterium with 4 screens reached saturation levels 90min post drug addition (Figure 3-figure supplement 1B). Conversely, bacteria with low absorption rate slowly accumulated the drug independently on the number of screens (Figure 3-figure supplement 1D). Therefore, according to these simplified 2-dimensional transport simulations (i.e. we do not take into account neither efflux nor transport across the gram-negative double barrier), delayed accumulation of membrane targeting drugs in bacteria screened by other cells is due to a transient reduction in the extracellular drug concentration around these bacteria, whereas other mechanisms must underpin increased roxithromycin accumulation in screened bacteria and this phenomenon should be investigated further in future studies. Finally, we would also like to reiterate that mechanisms other than the microcolony architecture must underlie phenotypic variants with reduced antibiotic accumulation. In fact, we registered significant cell-cell differences in antibiotic accumulation even within the same subpopulation of bacteria with the same number of screening cells (Fig. 3).

These new data are discussed in the revised manuscript on lines 386-406 and 796-815 (where we have now reported details about the COMSOL simulations) and in the new Figure 3-figure supplement 1.

Author Response

Reviewer #1 (Public Review):

Zaffagni et al. investigated the host cell response in a transcriptome level upon expression of viral proteins of SARS-CoV-2. They found that expression of Nsp14, highly conserved non-structural protein induces a dramatic remodeling of transcriptome that mimics SARS-CoV-2 infection. They revealed functional impacts of Nsp14 in various transcriptomic aspects such as transcript abundance, alternative splicing, and transcriptomic remodeling in a time course manner. They found IMPDH2, the rate-limiting enzyme in GTP biosynthesis as a key mediator of Nsp14 effects on host transcriptome, posing IMPDH2 and Nsp14 as a therapeutic target against SARS-CoV-2.

The paper revealed various transcriptomic effects upon Nsp14 expression. But biological relevance of infected cells should be verified on these effects. It would be better to explain the mechanistic link among these observations and some data need to be further validated to support their conclusions.

1. Are the alternative splicing pattern and increased circRNAs upon Nsp14 expression also observed in SARS-CoV-2 infection?

We thank the reviewers for the insightful question, helping us to contextualize our data to the physiological events of SARS-Cov-2 infection.

Regarding alternative splicing, previous publication showed that upon infection -90% of the genes show altered splicing events, mainly intron retention events (Banerjee et al. 2020). Previous studies attributed this to another viral protein, Nsp16, as expression of Nsp16 causes mRNA splicing suppression of a minigene by binding U1 and U2(Banerjee et al. 2020). However, those studies are mainly based on experiments in which Nsp16 is expressed as exogenous protein. Interestingly, we see a similar trend when we express Nsp14, with retention of more than 2,000 introns. This suggests that the massive intron retention observed during SARS-CoV-2 infection might be due to both Nsp16 and Nsp14. We have added some sentences contemplating this possibility although making clear that, while there is a known mechanisms by which Nsp16 expression provokes intron retention, this is not the case for Nsp14 and could be indirect (i.e., by activation of IMPDH2 since pharmacological inhibition of this protein partially rescues some intron retention effects, or other unknown pathway). Besides, we re-analyzed a published dataset of HEK293T-hACE2 infected with SARS-CoV-2(Sun et al. 2021) and we showed that there is a 10% overlap between the alternative splicing events in this dataset and in our dataset (in the HEK293T dataset a much smaller number of genes showed altered splicing upon infection). This is way over what is expected by chance (p-value <10-15), indicating that Nsp14 expression partially recapitulates the effects on alternative splicing that happen during the infection. Notably, this might be an underestimation because the sequencing depth of this published dataset was lower than our dataset. In any case, these effects in splicing strengthen the idea of parallel and comparable changes in gene expression during infection with those we observed upon Nsp14 overexpression.

Regarding circRNAs, previous studies showed that circRNAs are generally degraded in the context of viral infection (T.-C. Chen et al. 2020 and Liu et al. 2019), so it is no possible to perform this comparison as it will be masked by this general phenomenon. Nevertheless, we think that the Nsp14 effect on circRNAs expression is very interesting. Indeed, it could be related to the observed anti-innate immunity activity of Nsp14. One proposed model is that circRNAs can trap PKR into the cytoplasm, to repress its activity (Liu et al. 2019). Upon viral infection, they are degraded, and PKR can shuffle into the nucleus to trigger immune surveillance. Indeed, upon SARS-CoV-2 infection, circRNAs are mostly downregulated (our own unpublished data, manuscript in preparation), suggesting that maybe Nsp14 could antagonize innate immunity by upregulating some circRNAs. We agree we didn’t address this in the present study. In any case, we have now included all this explanation and discussion in the new version of the manuscript. We thank the reviewers for bringing this up, as it has significantly improved the manuscript.

1. The authors showed that IMPDH2 contributes to Nsp14-mediated transcriptome changes. I wonder whether catalytic activity of IMPDH2 also affects the alternative splicing events mediated by Nsp14 expression. Given that the GC content is associated with the sensitivity to Nsp14-mediated alternative splicing, I am curious whether increased GTP level upon Nsp14 expression could be related to the alternative splicing events. How are the alternative splicing events when IMPDH2 inhibitor (MPA) was treated to Nsp14-expressed cells (comparing Nsp14+MPA to Nsp14+DMSO as Figure 6E)?

This is indeed an interesting point which we have now addressed experimentally. Unfortunately, we could not perform alternative splicing analysis on the original dataset generated for comparing Nsp14+MPA or Nsp14+DMSO because it is a 3’RNA seq experiment. To overcome this problem and address this point, we performed RT-qPCR for detecting some of the intron retention events observed upon Nsp14 expression. First, we confirmed that Nsp14 expression induces an increase in these intron retention events (Figure 6G and Figure 6 - figure supplement 6G, red bars). Second, we showed that both MPA and MZR treatment partially rescue the splicing of these introns (see Figure 6G and Figure 6 - figure supplement 6G). Taken together, these data demonstrates that IMPDH2 mediates also the alternative splicing events induced about Nsp14 and the idea that this might be mediated by the increased GTP is indeed a compelling hypothesis. We thank the reviewer for bringing this point.

In addition, and as mentioned above, we see increased circRNAs levels upon Nsp14 expression, that might derive from increased back-splicing. In the original version of the manuscript, we showed that the expression of circRNAs is partially rescued upon MPA treatment, and we confirmed this result using another inhibitor (Mizoribine, abbreviated as MZR). Now we included these results in Figure 6 - figure supplement 2F. These data indicate that IMPDH2 is involved in modulating circRNAs expression, probably due to biosynthesis regulation, but we cannot exclude that IMPDH2, or other pathways might increase also circRNA stability.

1. It would be nice to provide information of a responsible domain of Nsp14 for its effect on the host transcriptome. Also, I wonder whether this domain is required for its interaction with IMPDH2, which would further validate the IMPDH2-mediated Nsp14 effect on host transcriptome.

We thank the reviewer for the insightful suggestion. In response to this comment, we generated a Nsp14 mutant for the N7-guanine–methyltransferase activity (Nsp14 D331A). Then, we compared how the expression of this construct affects some Nsp14 targets (mRNAs and circRNAs) by RT-qPCR (Figure 4G and 4H). Interestingly, we found that the N7-guanine-methyltransferase domain is required for mediating the gene expression changes induced by Nsp14 WT, as the level of the tested Nsp14-targets are not affected by expression of the N7-guanine-methyltransferase Nsp14 mutant. Importantly, we verified by Western Blot that the protein was expressed at levels comparable to WT Nsp14 (Figure 4 - figure supplement 2E). We thank the reviewer for suggesting checking more carefully which domain of Nsp14 is mediating the described effects. We believe that the information obtained with the N7-guanine-methyltransferase mutant provides a more comprehensive view of the mechanism. We agree with the reviewer that it would be nice in the future to check whether this domain is crucial for the interaction with IMPDH2 by performing CoIP or in vitro activity experiments.

1. To make their conclusion "IMPDH2 is a key mediator of the effects of Nsp14 on the transcriptome of the hosting cell." more compelling, a rescue experiment using wild-type or catalytic dead mutant of IMPDH2 is needed. Or at least, the authors should confirm whether MPA effect on Nsp14-mediated transcriptome change can be reproducible using another IMPDH2 inhibitor.

We understand the concern of the reviewer and hence we have performed the suggested experiment and showed that the effect on mRNAs, circRNAs, and alternative splicing can also be partially reverted by using a second IMPDH2 inhibitor (Mizoribine - MZR). Specifically, MPA binds targets the site of the cofactor, NAD+/ NADH, while Mizoribine binds targets the binding pocket of the natural substrate, inosine monophosphate (IMP)(Liao et al. 2017). We presented the new data in the Figure 6 - figure supplement 2. We thank the reviewer for the suggestion that we believe significantly improved the manuscript.

Author Response

Reviewer #1 (Public Review):

This is a very solid and exciting study.

We thank the reviewer for finding our study to be very solid and exciting.

I have several suggestions, comments and questions:

1. The authors focused on examining the role of C129 as a regulator of PTPN22 redox sensitivity based on a published crystal structure of the catalytic domain. It would be great if they could demonstrate the existence of the disulfide bond between C129 and C227 also experimentally (in T cells).

As we understand it, it is requested that the disulfide bond between C227 and C129, as previously suggested by Tsai et al. (2009) (1) with pure protein, should be documented to actually occur in the activated T cells. We fully agree that this would improve the study and we have therefore made several attempts to demonstrate this oxidation, or the oxidation state of the active site Cys residue in PTPN22 in situ. However, as we had also expected, it has proven to be technically very challenging. Nevertheless, as the functional consequence of the PTPN22 oxidation and the effect of the C129S mutation is clearly documented in the mouse, using in vivo experiments, we still think it is valid to conclude that the reversible oxidation state of PTPN22 as well as the involvement of the Cys129 residue regulates the function of PTPN22 in vivo, which is the main conclusion of our study.

1. To this end, there are other cysteine residues in the vicinity of C227 such as the C231 that might be involved in the redox regulation PTPN22. The authors should at least discuss the their possible involvement.

It is correct that Tsai et al. (2009) (1) found that mutating C231 to serine dramatically reduced phosphatase activity, thus suggesting its importance in catalysis. Reactivation assays showed higher reactivation rates for C231S mutants, and they suggested that C231 suppresses reactivation in a reducing environment by competing with C227 for reduction in the catalytic pocket. Therefore, C231 could also be a target for negative regulation of PTPN22. However, our project was from the start limited to the intention of studying whether PTPN22 could be shown to be redox regulated in vivo through modification of key cysteine residues, and the aim has not been to give the full picture of how the molecule is regulated. We have now extended this point in the discussion in the paper.

1. How is mutation of C227 affecting T cell function? Are the effects similar with those of C129S?

This would be interesting but to analyze if also the cysteine at 227 is regulating the T cell activation by creating another transgenic C227S mouse is outside the scope of the study. As said above and clearly described in the study, we have focused on the redox-mediated effects through C129 and hope that the reviewer can agree with us that this rather focused study is solid and fully sufficient for publication on its own merits.

1. Although the in vitro evaluation of the PTPN22 activity is of highest quality, it would be good to demonstrate that C227 redox status is modified under physiological conditions. 25-100 µM H2O2 is a high concentration that might not be reached within a cell and might be lethal for T cells.

See response to point 1.

1. C129 seems not to be mutated in patients with autoimmunity but is an excellent tool to test the importance of C227 redox regulation and the findings of this study suggest that its over-oxidation will support autoimmune responses. When considering the clinical relevance of the study, a drug that will protect the oxidation of the catalytic cysteine and/or stabilize the disulfide bond would have beneficial effects. The authors could test such pharmacological modulators in isolated T cells.

Indeed, such modulators would be very interesting to test; however, developing such drugs can hardly be demanded to be within the scope of this study. We have however included a statement on this topic in the Discussion of the manuscript.

1. The authors discuss that NOX2-derived ROS most likely originate from antigen presenting cells. I fully agree with this discussion. However, some studies have proposed that NOX2 plays an important role also in T cells, a finding which was not confirmed by other following studies. It would be great if the authors could address this controversial issue in regards to their findings.

The finding that the ROS that modify PTPN22 in fact come from the interacting APC rather than from the T cell itself we believe is very important. However, we have not made a major point of this as we have shown that aspect before in other studies, and we wanted in the current paper to focus on the take home message that PTPN22 could hereby be shown to be redox regulated in vivo. However, the last word about the source of ROS has not been said. The controversy whether the Ncf1 containing NOX2 complex is functionally expressed in T cells stems from the paper by Jackson et al. in Nat Immunol 2004 (2). We have not been able to reproduce those findings and in addition we have never detected a NOX2 dependent response in pure T cells, which has also been shown in several of our papers. There are certainly many pitfalls, contaminating NOX2 expressing cells, NOX2 containing exosomes and peroxides, and even NOX2 complexes picked up by interactions with antigen presenting cells. However, it is dangerous to completely exclude that Ncf1 could be expressed at minimal levels or to exclude that functional NOX2 complex can indeed be formed in T cells, and we all know that minute levels of any peroxide as produced by cells could have an impact on cellular functions. But, based on the present knowledge we conclude that T cells do not functionally express Ncf1-containing NOX2 complexes. We have now added two references to enlighten this point, (3, 4; refs. 38 & 39 in the manuscript).

1. Fig. 1: Is the addition of bicarbonate affecting the pH and thus the activity of PTPN22?

No, we believe that addition of bicarbonate is not acting by an altered pH but is instead required for formation of peroxymonocarbonate when reacting with H2O2, which is subsequently the molecular species that bypasses the cellular antioxidant systems in order to oxidize the active site Cys residues of target PTPs. This was shown by us in an earlier publication (Dagnell et al, ref. 11 in the manuscript) (5) and a sentence has now been added in the Discussion to further emphasize this point.

1. The H2O2 concentration dependence of PTPN22_C129S should also be shown as for WT (see Fig. 1B)

We agree with the reviewer that titration of the mutant with additional H2O2 concentrations could potentially have been done, but we thought that the comparison of WT and C129S enzyme side-by-side using either 0 µM, 25 µM or 50 µM as in Fig. 1D was a sufficient comparison in H2O2 sensitivity. Unfortunately, we do not have the possibility to analyze more purified C129S mutant protein at the moment and it would require a major effort to run those additional experiments. We thereby hope that the reviewer would agree with having the data presented as they currently are to be sufficient.

1. Quantification of the slope based on only 3 measuring points is not accurate (Fig. 1D).

Each data point in those curves represents the mean ± S.D. derived from duplicate samples ran three different times, with clearly very low standard deviations. Thus, we believe that the data are reliable and that the statistically significant difference when comparing the slopes between WT and the C129S mutant as shown in the figure, should be trustworthy.

1. The pinna thickness measurements shown in Fig. 3B and C suggest that in NCF1 mice C129S has no effect. However, the thickness in NCF1 mice is already much higher than in WT mice (compare B and C). Does this mean that NOX2-derived ROS are the only factor that affects C227 redox properties?

The effects of the decreased ROS due to the Ncf1 mutation is likely to have consequences for the functions of many proteins, in different pathways, and not only of PTPN22. The sum effect is that the Ncf1 mutated mice responds stronger than the wild type, which explains the difference. However, the main message here is that if there is no ROS from the NOX2 complex, the effect of the PTPN22 mutation is lost.

1. The results shown in Fig. 5D could be moved to a supplementary figure.

We prefer to keep it within Fig 5 as it is more logical in the context or the other parts of this figure. Of course, if there is a space layout problem, we can consider moving it.

1. The calcium measurements are not convincing and the differences are rather small. The y axis labels show 50K, 100K etc. Are this ratio values? If yes the imaging settings need to be optimized. Why is the mutant labeled as Pep? How is the C129S affecting calcium signaling? These observations need be examined in more detail or maybe calcium is not playing an important role.

We agree that the differences in calcium measurements are not very large but have nevertheless been repeated several times, and there is a significant difference as shown. The calculation is done on the slope of the curve, which is independent of the absolute values given on the y-axis. We agree that the figure was not properly labeled and have now changed this.

1. I would suggest a more extensive evaluation of the proteomic data presented in Fig. 6D. The results might be very exciting and can further increase the impact of this study.

We fully agree with this. We have chosen not to go into details of the results of the proteomic analysis. The data shown confirms our conclusion and we did not plan to identify the downstream targets of the PTPN22 oxidative regulation. Highlighting some of these targets will require biological confirmation, which can be done but must await future work. The full dataset has however been deposited in PRIDE for any reader interested to analyze the results further.

1. Is 24h BSO treatment not toxic for the T cells (ferroptosis)?

We have not seen any evidence for toxicity upon the BSO treatment of T cells in vitro, which however has been more thoroughly checked by others. Gringhuis et al (JI, 2000) (6) have shown immunofluorescence staining on T cells 72 hours post BSO treatment with intact cell membranes. Additionally, Carilho et al. (Chem. Cent. J., 2013, 7:150) (7) noted no changes in Jurkat T cell viability after 24 hours at a maximum dose of 100 µM BSO.

Reviewer #3 (Public Review):

The manuscript by James, Chen Hernandez et al. reveals a novel function for PTPN22 oxidation in T-Cell activation. The authors used a broad array of methods to demonstrate that PTPN22 is catalytically impaired in addition to being more sensitive to reversible oxidation in vitro. In the characterization process, the authors found that PTPN22 could be directly reduced by Thioredoxin Reductase and that oxidation of PTPN22 oxidation could be easily monitored by the appearance of a faster migrating band in non-reducing gels. Supporting the hypothesis that the catalytic Cysteine forms a disulfide with a backdoor Cysteine (Cys129), the authors found that this C129S mutant is prone to oxidation and cannot be reduced back to its active form by Thioredoxin Reductase. Using a new mouse model in which this key Cysteine of PTPN22 is mutated to a Serine residue (PTPN22C129S mutant) and can presumably not form a stabilizing redox intermediate between the catalytic Cys residue and this backdoor Cys (C227-C129), the authors study how the oxidation prone mutant affects T-Cell activation. The authors find that the C129S mutant mouse showed an increased T-Cell dependent inflammatory response that was dependent on activation of the reactive oxygen species-producing enzyme NOX2. This data adds an interesting redox twist to the function of PTPN22 in T-Cells that contributes to conversation on the protective effects of reactive oxygen species against inflammatory diseases in vivo.

Strengths:

The in vitro characterization of the WT and C129S mutant form of PTPN22 is very thorough. Determination of the Km and Kcat highlights the differences between the two enzymes that go beyond redox regulation of the phosphatase. The reduction studies are masterfully done and highlight a novel reduction mechanism that merits to be further studied in cells. Demonstrating that PTPN22C129S is prone to oxidation in vitro is a key and technically challenging result that may be applicable to other members of the PTP family that also form disulfides with a backdoor cysteine. Showing that PTPN22C129S mice (backcrossed to B6Q mice making them susceptible to autoimmune arthritis) displayed higher T cell activation in two models (DTH and GPI), in addition to studies in T cells stimulated with collagen, increased this reviewer's confidence that the PTPN22C129S mouse exhibited T-cell-dependent inflammatory response phenotype similar to the PTPN22 knockout phenotype. Validation of T-cell signaling events in PTPn22C129S T cells were in line with the in vitro characterization of the phosphatase.

We thank the reviewer very much for the detailed summary of our findings and the appreciative words.

Weaknesses: Although the paper has many strengths, some important weaknesses need to be addressed by the authors. In particular, the authors need to characterize better their mouse model and determine if PTPN22 is reversibly oxidized following TCR activation. If PTPN22 is oxidized, does it form an intramolecular disulfide between C227 and C129? The proposed model, that PTPN22C129S is more prone to oxidation, also has to be validated in vivo. Although this could be technically challenging in theory, the authors have shown that the migration pattern of the oxidized enzyme is different that of the reduced enzyme. Another major issue is that PTPN22 does not appear to be expressed in CD4+ T cells unless these cells are activated in vitro with anti-CD3/CD28 for 24 hours. This makes acute CD3-stimulation of CD4+ T cells studies - such as the measurement of acute calcium influx in Fig. 5E - very difficult to interpret. Perhaps the authors should explain why acute signal transduction studies in Figure 6 were performed in lymph node cells. If the reason is that PTPN22 (WT and C129S mutant) expression is higher, the authors should provide immunoblots for PTPN22 in these cells. Since the PTPN22C129S mouse model has not been sufficiently validated, the claims of the authors are unfortunately weakened and the underlying molecular mechanisms do not completely support their conclusions. However, given the clear in vitro work provided in figures 1 and 2, it is this Reviewer's opinion that the authors can address the issues related to the oxidation status of PTPN22 and of PTPN22C129S in vivo, support their claims, and make a significant contribution to the field.

We again thank the reviewer for the detailed summary of our findings and for the suggestions. With regards to the in vivo oxidation status of PTPN22, please see the discussion above.

1. Tsai SJ, Sen U, Zhao L, Greenleaf WB, Dasgupta J, Fiorillo E, et al. Crystal structure of the human lymphoid tyrosine phosphatase catalytic domain: insights into redox regulation. Biochemistry. 2009;48(22):4838-45.
2. Jackson SH, Devadas S, Kwon J, Pinto LA, Williams MS. T cells express a phagocyte-type NADPH oxidase that is activated after T cell receptor stimulation. Nat Immunol. 2004;5(8):818-27.
3. Gelderman KA, Hultqvist M, Holmberg J, Olofsson P, Holmdahl R. T cell surface redox levels determine T cell reactivity and arthritis susceptibility. Proc Natl Acad Sci U S A. 2006;103(34):12831-6.
4. Gelderman KA, Hultqvist M, Pizzolla A, Zhao M, Nandakumar KS, Mattsson R, et al. Macrophages suppress T cell responses and arthritis development in mice by producing reactive oxygen species. J Clin Invest. 2007;117(10):3020-8.
5. Dagnell M, Cheng Q, Rizvi SHM, Pace PE, Boivin B, Winterbourn CC, et al. Bicarbonate is essential for protein-tyrosine phosphatase 1B (PTP1B) oxidation and cellular signaling through EGF-triggered phosphorylation cascades. J Biol Chem. 2019;294(33):12330-8.
6. Gringhuis SI, Leow A, Papendrecht-Van Der Voort EA, Remans PH, Breedveld FC, Verweij CL. Displacement of linker for activation of T cells from the plasma membrane due to redox balance alterations results in hyporesponsiveness of synovial fluid T lymphocytes in rheumatoid arthritis. J Immunol. 2000;164(4):2170-9.
7. Carilho Torrao RB, Dias IH, Bennett SJ, Dunston CR, Griffiths HR. Healthy ageing and depletion of intracellular glutathione influences T cell membrane thioredoxin-1 levels and cytokine secretion. Chem Cent J. 2013;7(1):150.

Author Response:

Reviewer #1:

The paper by Liu et al investigates the question of whether the mitochondrial protein import component Tom70 might be involved in the coordination of biogenesis and localization of mitochondrial proteins. It follows a smart hypothesis that positions Tom70 in a coordinating role of nuclear-encoded mitochondrial gene expression and subsequent protein incorporation. The paper shows that Tom70 overexpression uniquely promotes the expression of numerous mitochondrial proteins and that Tom70's mitochondrial localization is required for this. The data then suggest that both mtDNA and a combination of transcription factors are involved in Tom70 controlled nuclear gene expression. The authors then find that Tom70 is also required to dampen nuclear mitochondrial gene expression during import stress. Importantly, Tom70 and numerous other import machinery components become depleted with age in yeast, and the same is true for mitochondrial membrane potential. This is a very strong part of the paper. Tom70 OE rescues this effect, and Tom70 OE extends survival. Finally, suggestive data show that the age-dependent Tom70 depletion is due to reduced expression and enhanced degradation.

This is an interesting study that uses cutting-edge methods. However, a clear focus of the paper is somewhat missing. The paper touches on many topics that remain unresolved. These include the role of CR and the role of LCD-containing TFs as an explanation for the age-dependent decline of Tom70. There is a role of mtDNA in the Tom70 OE but the link to transcription factors remains unaddressed. For example, degradation of Tom70 is investigated via MDCs, but is autophagy involved? There is a large amount of data in the manuscript that cover a lot of territory, but further mechanistic insights would significantly enhance the paper.

The authors appreciate the enthusiasm and comments from the reviewer. The focus of our manuscript is to report the discovery that Tom70 moonlights to regulate the biogenesis of mitochondrial protein and mtDNA (Figure 1-3). After identifying this new role of Tom70, we applied it to understand physiological processes including mitochondrial import-related stress response and aging-related mitochondrial dysfunctions (Figure 4-7). We did these application studies because we think it is necessary to understand the physiological significance of this Tom70’s role, which was strongly encouraged by senior colleagues in the aging field during the progress of our project.

Specifically, we removed the LCD/proteostasis part according to reviewers’ suggestions. We include caloric restriction (CR) because this Tom70’s role can explain the previously observed phenotypes in the aging field, and it is important to connect our discoveries to the previous works as encouraged by colleagues in the field during the progress of our project. We think this is a strength of our study that generated new knowledge which can be used to address previous questions. Regarding mtDNA, we focused on the biogenesis role of Tom70 on mtDNA as a necessary and immediate extension of our study on the biogenesis of mitochondrial proteins. Indeed, the detailed mechanism of how Tom70 signals through the secondary messengers and multiple TFs to achieve these biogenesis functions is still not clear, which will be our future goal. Similar to our manuscript, the seminal study that identified PGC-1 as a key mitochondrial biogenesis regulator also reported the increase of mitochondrial proteins and mtDNA through the induction of a few TFs by PGC-1 (Wu et al., 1999). Regarding MDCs, we simply applied previous knowledge from Hughes and Gottschling’s study that Fis1/Mdv1 regulate the sorting of Tom70 into MDCs in response to acute vacuole stress (Hughes et al., 2016). They have carefully dissected the role of autophagy downstream of MDC formation. However, our purpose is to see what regulates Tom70’s abundance but not how MDC is disposed during aging.

Reviewer #2:

The authors test the hypothesis that components of the TOM complex regulate efficient mitochondrial biogenesis by coordinating the synthesis of mitochondrial proteins with the rate of mitochondrial protein import. In general, the experiments are well developed and the findings and topic are likely of broad interest. The weaknesses are mainly related to the underdeveloped approaches and the vagaries related to the mechanism(s) by which Tom70 influences transcription of mitochondrial components.

The authors performed a survey of TOM components (proteins required for protein translocation from the cytosol into mitochondria) and found that overexpression of Tom70 was sufficient to increase accumulation of 4 GFP-tagged mitochondrial proteins that localize to each of the four mitochondrial sub-compartments suggesting that Tom70 has a unique role in mitochondrial biogenesis.

Interestingly, the authors demonstrate that Tom70 is required to limit transcription of mitochondrial components when Tim23 is impaired. In doing so, Tom70 prevents the aggregation of mitochondrial proteins that fail to be imported into mitochondria.

The authors demonstrate that mtDNA is required for the increase in mitochondrial component transcription upon Tom70 overexpression. This is an exciting observation. However, experiments to understand the phenomenon are not considered.

The authors appreciate the enthusiasm and comments from the reviewer. The focus of our manuscript is to report the discovery that Tom70 regulates the biogenesis of mitochondrial protein and mtDNA. According to reviewers’ suggestion, we tested several possibilities and the results have been discussed. The detailed mechanism of how Tom70 signals through the secondary messengers to achieve this function will be the next focus of our lab.

Interestingly, overexpression of Tom70 prevents the decline in mitochondrial function typically observed in aging cells, while Tom70-deletion accelerated the loss of mitochondrial function.

Author Response

Reviewer #1 (Public Review):

The manuscript by Catela is a very interesting study investigating terminal selection factors in spinal motor neurons. While the field has focused largely on the development and specification of motor neurons, much less attention has been garnered on gene expression programs that endow the mature motor neuron with adult stage terminal characteristics. This question has recently been tackled in the nematode roundworm C. elegans, but a terminal selector code in mammals is lacking. The work here showing sustained activity of Hoxc8 acting as a terminal selector is interesting and may point towards this kind of encoding being a general rule throughout nervous systems, from invertebrates to vertebrates. In addition to the strengths of this work

We are glad the reviewer finds our study interesting and comments on its evolutionary implications.

However, this work would benefit from added approaches beyond RNAseq and RNA in situ to strengthen the data. Additional neuroanatomical, physiology, and behavior data would certainly also strengthen this work - especially since one would expect to see more phenotypes in hoxc8 mutants beyond only misexpression of downstream genes. There are a wealth of motor behavior/motor acuity tasks that can be performed in the mouse and adding such experiments would certainly strengthen this paper.

We agree. Our new behavioral data (Fig. 6) nicely complement the molecular analysis of brachial motor neurons in Hoxc8 MNΔearly and Hoxc8 MNΔlate mice.

Reviewer #2 (Public Review):

Different motor neurons located in different parts of the spinal cord are known to perform distinct functions. It is known that these differences are specified during embryonic development by the expression of different transcription factors. But it is unknown how these differences are maintained in the adult spinal cord. In this manuscript, Kratsios and colleagues propose that the Hox transcription factor Hoxc8 acts as a terminal selector for brachial motor neurons in the developing mouse spinal cord. They perform a series of experiments in which Hoxc8 is deleted from embryonic (e12) and early postnatal (p8) motor neurons and show that this transcription factor is required for the establishment and/or maintenance of a set of terminal differentiation genes in this motor neuron population. Notably, a similar and larger body of work from this lab has previously focused on the role of terminal selector genes, including Hox factors, in the worm C elegans nervous system development. The main conclusions of this current study are 1) Hox factors also control mouse neuronal terminal differentiation, suggesting an evolutionarily conserved role; 2) Hox genes such as Hoxc8 act through multiple downstream effectors, including other transcription factors such as Irx family; and 3) single transcription factors such as Hoxc8 can have multiple distinct roles in terminal differentiation based on the timing of their expression/action. This latter point is perhaps the most interesting conclusion of this paper as it helps to uncover why Hox gene expression may be maintained in post-mitotic neurons beyond initial cell specification.

This is an exciting paper and will be of broad interest to the spinal cord field. Their demonstration of similar logic in mouse as to what they reported earlier for C. elegans demonstrates the evolutionarily conserved mechanism by which Hox genes function in terminal differentiation of spinal motor neurons. Strengths of this study include the detailed transcriptomics analyses at different time points in mouse and functional studies using conditional mouse knockouts.

Overall, the conclusions in this paper are well-supported and of high quality. However, one of the authors' main conclusions is that Hoxc8 expression helps control terminal differentiation of spinal motor neurons. But they identify relatively few potential terminal effector genes (8) that seem to require Hoxc8 at any stage. This is especially evident when examined in the context of the initial RNA seq analysis of wildtype e12 vs p8 motor neurons, in which there are >3000 differentially expressed genes between those time points. Therefore, while Hoxc8 may have some role in brachial motor neuron differentiation, it appears to not be a very significant role, or at least does not seem so based on the analyses presented here. The authors might wish to either clarify this point or try to put their findings in a broader context so the readers can appreciate the importance of Hoxc8 in motor neuron differentiation and the potential involvement of other collaborating factors.

We completely agree and have modified the text and figures (Fig. 4F, new Fig. 5 - figure supplement 1) accordingly to clarify the importance of Hoxc8 in motor neuron terminal differentiation and the involvement of Hoxc8 collaborators.

Of note, we found six other Hox genes to be expressed continuously in brachial MNs - these could act as Hoxc8 collaborators. Based on studies conducted in mice and chick embryos at early stages of MN development, the strongest candidate is Hoxc6 (Catela et al., 2016, PMID: 26904955; Jung et al., 2010, PMID: 20826310). Deletion of either Hoxc6 or Hoxc8 at the MN progenitor stage (with Olig2-Cre) results in similar axon guidance defects in brachial MNs, and these early defects can be molecularly explained by Hoxc6 and Hoxc8 collaborating to control the expression of Ret, an axon guidance molecule (Catela et al., 2016, PMID: 26904955). Interestingly, when we interrogated available ChIP-Seq datasets from mouse ESC-derived motor neurons in which Hoxc6 or Hoxc8 expression is induced with doxycycline (Bulajic et al., 2020, we found Hoxc6 and Hoxc8 bind on the same cis-regulatory regions of the terminal differentiation markers (e.g., Mcam, Pappa, Glra2) we identified with our in vivo genetic studies (new Fig. 5; new Fig. 5 – figure supplement 1).

We have modified the Results and Discussion to clarify this important point, as well as highlight the potential involvement of additional factors outside the Hox family, such Islet-1.

Author Response

Reviewer #1 (Public Review):

Dias et al proposed a new method for genotype imputation and evaluated its performance using a variety of metrics. Their method consistently produces better imputation accuracies across different allele frequency spectrums and ancestries. Surprisingly, this is achieved with superior computational speed, which is very impressive since competing imputation softwares had decades of experience in optimizing software performance.

The main weakness in my opinion is the lack of software/pipeline descriptions, as detailed in my main points 36 below.

We have made the source code and detailed instructions available publicly at Github. The computational pipeline for autoencoder training and validation is available at https://github.com/TorkamaniLab/Imputation_Autoencoder/tree/master/autoencoder_tuning_pipeline.

1. In the neural network training workflow, I am worried it will be difficult to compute the n by n correlation matrix if n is large. If n=10^5, the matrix would be ~80GB in double precision, and if n=10^6, the matrix is ~2TB. I wonder what is n for HRC chromosome 1? Would this change for TOPMed (Taliun 2021 Nature) panel which has ~10x more variants? I hope the authors can either state that typical n is manageable even for dense sequencing data, or discuss a strategy for dealing with large n. Also, Figure 1 is a bit confusing, since steps E1-E2 supposedly precede A-D.

We included more details in the methods section to address this question. It is true that computing the entirety of this matrix is computationally intensive, thus, in order to avoid this complexity, we calculated the correlations in a sliding box of 500 x 500 common variants (minor allele frequency (MAF) >=0.5%). In other words, no matter how dense the genomic data is, the n x n size will always be fixed to 500 x 500. Larger datasets will not influence this as the additional variants fall below the MAF>=0.5% threshold. Thus, memory utilization will be the same regardless of chromosome length or database size. Please note that this correlation calculation process is not necessary for the end-user to perform imputation, since we already provide the information on what genomic coordinates belong to the local minima or “cutting points” of the genome. This computational burden remains on the developer side. The reviewer is right to point out that Figure 1 is misleading in its ordering, we have corrected this in the revision.

1. I have a number of questions/comments regarding equations 2-4. (a) There seems to be no discussion on how the main autoencoder weight parameters were optimized? Intuitively, I would think optimizing the autoencoder weights are conceptually much more important than tuning hyper-parameters, for which there are plenty of discussions.

These parameters are optimized through the training process described in “Hyperparameter Initialization and Grid Search / Hyperparameter Tuning” - where both the hyperparameters and edge weights are determined for each autoencoder for each genomic segment. There are 256 genomic segments in chromosome 22, and each segment has a different number of input variables, sparsity, and correlation structure. Thus, there is a unique autoencoder model that best fits each genomic tile (e.g.: each autoencoder has different weights, architecture, loss function, regularizes, and optimization algorithms). Therefore, while there are some commonalities across genomic tiles, there is not a single answer for the number of dimensions of the weight matrix, or for how the weights were optimized. Instructions on how to access the unique information on the parameters and hyperparameters of each one of the 256 autoencoders is now shared through our source code repository at https://github.com/TorkamaniLab/imputator_inference.

We included an additional explanation clarifying this point in the Hyperparameter Tuning subsection of the Methods.

(b) I suppose t must index over each allele in a segment, but this was not explicit.

That is correct, t represents the index of each allele in a genomic segment. We included this statement in the description of equation 2.

(c) Please use standard notations for L1 and L2 norms (e.g. ||Z||_1 for L1 norm of Z). I also wonder if the authors meant ||Z||_1 or ||vec(Z)||_1 (vectorized Z)?

We included a clarification in the description of equation 3. ‖𝑾‖𝟏 and ‖𝑾‖𝟐 are the standard L1 and L2 norms of the autoencoder weight matrix (W).

(d) It would be great if the authors can more explicitly describe the auto-encoder matrices (e.g. their dimensions, sparsity patterns if any...etc).

As we answered in comment 2.a, each one of the 256 autoencoders for each genomic segment is unique, so it would be unfeasible to describe the architecture, parameters, optimizers, loss function, regularizes, of each one of them. We realized it would be more suitable to share this information in a software repository and have now done so.

1. It is not obvious if the authors intend to provide a downloadable software package that is user-friendly and scalable to large data (e.g. HRC). For the present paper to be useful to others, I imagine either (a) the authors provide software or example scripts so users can train their own neural network, or (b) the authors provide pretrained networks that are downloaded and can be easily combined with target genotype data for imputation. From the discussion, it seems like (b) would be the ultimate goal, but is only part dream and part reality. It would be helpful if the authors can clarify how current users can benefit from their work.

We have now shared the pre-trained autoencoders (including model weights and inference source code) and instructions on how to use them for imputation. These resources are publicly available at https://github.com/TorkamaniLab/imputator_inference. We have added this information to the Data Availability subsection of the Methods.

1. Along the same lines, I also found the description of the software/pipeline to be lacking (unless these information are available on the online GitHub page, which is currently inaccessible). For instance, I would like to know which of the major data imputation formats (VCF/BGEN..etc) are supported? Which operating systems (window/linux/mac) are supported? I also would like to know if it is possible to train the network or run imputation given pre-trained networks, if I don't have a GPU?

We have now made the github repository publicly available. The description of the requirements and steps performed in the hyperparameter tuning pipeline is available at https://github.com/TorkamaniLab/Imputation_Autoencoder/tree/master/autoencoder_tuning_pipeline.

1. Typically, imputation software supplies a per-SNP imputation quality score for use in downstream analysis. This is important for interpretability as it helps users decide which variants are confidently imputed and which ones are not. For example, such a quality score can be estimated from the posterior distribution of an HMM process (e.g. Browning 2009 AJHG). Would the proposed method be able to supply something similar? Alternatively, how would the users know which imputed variants to trust?

We included further clarification in the data availability session of methods: Imputation data format. The imputation results are exported in variant calling format (VCF) containing the imputed genotypes and imputation quality scores in the form of class probabilities for each one of the three possible genotypes (homozygous reference, heterozygous, and homozygous alternate allele). The probabilities can be used for quality control of the imputation results.

We included this clarification in the manuscript and in the readme file of the inference software repository https://github.com/TorkamaniLab/imputator_inference.

1. I think the authors should clarify whether input genotypes must be prephased. That is, given a trained neural network and a genotype data that one wishes to impute, does the genotype data have to be phased? The discussion reads "our current encoding approach lacks phasing information..." which can be understood both ways. On a related note, I hope the authors can also clarify if the validation and testing data (page 7 lines 1423) were phased data, or if they were originally unphased but computationally phased via softwares like Eagle 2 or Beagle 5.

The input genotypes are not phased, nor pre-phased, and no pre-phasing was performed before imputation. We included further clarification on the method section, stating “All input genotypes from all datasets utilized in this work are unphased, and no pre-phasing was performed.”. We also included further clarification in the Discussion session.

1. It is unclear if the reported run times (Figure 6) includes model training time, or if they are simply imputing the missing genotypes given a pre-trained autoencoder? For the later, I think the comparison may still be fair if users never have to train models themselves. However, if users currently have to train their own network, I feel it is imperative to also report the model training time, even if in another figure/table.

The end-users do not have to train the models, the computational burden of training the models remains on the developer side, so the runtimes refer to the task of imputing the missing genotypes given a pre-trained autoencoder set. This allows for distribution without reference datasets. We included further clarification on the Performance Testing and Comparisons subsection of Methods.

Reviewer #2 (Public Review):

In this manuscript the authors introduce a segment based autoencoder (AE) to perform genotype imputation. The authors compare performance of their AE to more traditional HMM-based methods (e.g. IMPUTE) and show that there is a slight but significant improvement on these methods using the AE strategy.

In general the paper is clearly presently and the work in timely, but I have some concerns with respect to the framing of the advances presented here along with the performance comparisons.

Specific Points:

1. The authors aren't doing a good enough job presenting the work of others in using deep neural networks for imputation or using autoencoders for closely related tasks in population genetics. For instance, the authors say that the RNN method of Kojima et al 2020. is not applicable to real world scenarios, however they seem to have missed that in that paper the authors are imputing based on omni 2.5 at 97% masking, right in line with what is presented here. It strikes me that the RNNIMP method is a crucial comparison here, and the authors should expand their scholarship in the paper to cover work that has already been done on autoencoders for popgen.

This is an important comparison that we erroneously misrepresented. We have now separated out this particular application of the RNN-IMP in the introduction of the manuscript. The major difference is that RNN-IMP needs to be retrained on different input genetic variants, much like a standard HMM-based method. The computational burden of RNN-IMP remains on the end-user side. It appears that computational complexity is tremendous in this model, given that the only example the authors provided with their software consists of 100 genomes from 1000 Genomes Project to perform the imputation on Omni by de novo training of the data. Given their approach does not achieve the benefits of distributing a generalizable pre-trained neural network, and the computational burden associated with training these models on the 60K+ genomes we use in our manuscript, we have opted for stating the benefits and downsides of their approach in the introduction.

1. With respect to additional comparisons-Kenneth Lange's group recently released a new method for imputation which is not based on HMM but is extremely fast. The authors would be well served to extend their comparisons to include this method (MendelImpute)-it should be favorable for the authors as ModelImpute is less accurate than HMMs but much faster.

We appreciate the reviewer pointing out this additional method, however their parent manuscript clearly shows substantially inferior imputation performance relative to BEAGLE/Minimac etc. which we already compare against. There is not much to gain by performing this comparison. Our autoencoder-based approach is already generating results that are competitive with the best and most cited imputation tools, which are all HMM-based and outperforming MendelImpute. The outcome of this comparison is forecasted based upon the parent manuscript.

1. The description of HMM based methods in lines 19-21 isn't quite correct. Moreover-what is an "HMM parameter function?"

Thank you for catching this. We were referring to parameter *estimation and have corrected this in the manuscript.

1. Using tiled AEs across the genome makes sense given the limitations of AEs generally, but this means that tiling choices may affect downstream accuracy. In particular-how does the choice of the LD threshold determine accuracy of the method? e.g. if the snp correlation threshold were 0.3 rather than 0.45, how would performance be changed?

This choice is driven by the limitations of cutting-edge GPUs. 0.45 is the threshold that returns the minimum number of tiles spanning chromosome 22 with an average size per tile that fits into the video memory of GPUs. While developing the tiling algorithm, we tested lower thresholds, which made the tiles smaller and more abundant, and thus made the GPU memory workload less efficient (e.g. many tiles resulted in many autoencoders per GPU, which thus caused a CPU-GPU communication overhead). Due to the obstacles related to computational inefficiency, CPUGPU communication overhangs, and GPU memory limits, we did not proceed with model training on tiles generated with other correlation thresholds. We’ve added a paragraph explaining this choice in the manuscript.

1. How large is the set of trained AEs for chromosome 22? In particular, how much disk space does the complete description of all AEs (model + weights) take up? How does this compare to a reference panel for chr22? The authors claim that one advance is that this is a "reference-free" method - it's not - and that as such there are savings in that a reference panel doesn't have to be used along with the genome to be imputed. While the later claim is true, instead a reference panel is swapped out for a set of trained AEs, which might take up a lot of disk space themselves. This comparison should be given and perhaps extrapolated to the whole genome.

This is an interesting point. For comparison, the total combined uncompressed size of all pre-trained autoencoders together is 120GB, or 469MB per autoencoder. The size of the reference data, HRC chromosome 22 across ~27,000 samples is 1GB after compression – or nearly 10X the autoencoder size. Moreover, unlike in HMM-based imputation, the size of the pre-trained autoencoders does not increase as a function of the reference panel sample size. The size of the autoencoders remains fixed since the number of model weights and parameters remains the same regardless of sample size – though it will expand somewhat with the addition of new genetic variants. Another point to consider is that privacy concerns associated with distribution of reference data are mitigated with these pretrained autoencoders.

1. The results around runtime performance (Figure 6) are misleading. Specifically HMM training and decoding is being performed here, whereas for the AE only prediction (equivalent to decoding) is being done. To their credit, the authors do mention a bit of this in the discussion, however a real comparison should be done in Figure 6. There are two ways to proceed in my estimation - 1) separate training and decoding for the HMM methods (Beagle doesn't allow this, I'm not sure of the other software packages) 2) report the training times for the AE method. I would certainly like to see what the training times look like given that the results as present require 1) a separate AE for each genomic chunk, 2) a course grid search, 3) training XGBoost on the results from the course grid search, and 4) retraining of the individual AEs given the XGBoost predictions, and 5) finally prediction. This is a HUGE training effort. Showing prediction runtimes and comparing those to the HMMs is inappropriate.

We consider the prediction only during the runtime comparisons because only the prediction side is done by the enduser, whereas the computational burden remains on the developer side. For the HMMs, we included only the prediction time as well (excluded the time for data loading/writing, computing model parameters and HMM iterations). The pre-trained autoencoders, when distributed, can take as input any set of genetic variants to produce the output without any additional training or fine-tuning required.

1. One well known problem for DNN based methods including AEs is out-of-sample prediction. While Figure 5 (missing a label by the way) sort of gets to this, I would have the authors compare prediction in genotypes from populations which are absent from the training set and compare that performance to HMMs. Both methods should suffer, but I'm curious as to whether the AEs are more robust than the HMMs to this sort of pathology.

Our test datasets in Figures 4 and 5 are independent of the reference dataset. MESA, Wellderly, and HGDP are all independent datasets, never used for training, nor model selection. Only HRC was used as reference panel or for training, and ARIC was used for model selection during tuning. We included a statement in the methods clarifying this point.

Reviewer #3 (Public Review):

Over the last 15 years or so genotype imputation has been an important and widely-used tool in genetic studies, with methods based on Hidden Markov Models (HMMs) and reference panels emerging as the dominant approach. This paper suggests a new approach to genotype imputation based on denoising autoencoders (DAE), a type of neural network. This approach has two nice advantages over existing methods based on Hidden Markov Models (HMMs): i) once the DAE is trained on a reference panel the reference panel can be discarded, and users do not need access to the reference panel to use the DAE; ii) imputation using a DAE is very fast (training is slow, but this step is done upfront so users do not need to worry about it). The paper also presents data showing that the tuned DAE is competitive in accuracy with HMM methods.

I have two main concerns.

First, it is unclear to me whether the accuracy presented for the tuned DAE (eg Figure 3, Table 4) is a reliable reflection of expected future accuracy. This is because the tuning process was quite extensive and complex, and involved at least some of the datasets used in these assessments. While the paper correctly attempts to guard against overfitting and related issues by using separate Training, Validation and Testing data (p7), it seems that the Testing data were used in at least some of the development of the methods and tuning (eg p14, "A preliminary comparison of the best performing autoencoder..."; Figure 2 and Table 2, all involve the Testing data). Because of the complexity of the process by which the final DAE was arrived at it is unclear to me whether there is a genuine concern here, but it would seem safest and most convincing at this point to do an entirely independent test of the methods on genotype data sets that were not used at all up to this point.

MESA, Wellderly, and HGDP were not used for training, nor for tuning, they are completely independent. So all the results showing these datasets are completely independent. Only HRC and ARIC were used for training and validation/tuning, respectively. We included a statement in the methods session clarifying this point.

Moreover, HGDP in particular includes 828 samples from 54 different populations representing all continental populations and including remote populations like Siberia, Oceania, etc. This reference panel is described in more detail in the reference below and likely represents the most diverse human genome dataset available. Thus, we have externally validated generalizability on a dataset with much greater diversity than our training dataset:

Bergström A, et al. Insights into human genetic variation and population history from 929 diverse genomes. Science. 2020 Mar 20;367(6484):eaay5012.

Second, there is a potentially tricky issue of to what extent distributing a black box DAE trained on a reference sample is consistent with data sharing policies. Standards of data sharing have evolved over the last decade. Generally there currently seems to be little hesitation to publicly share "single-SNP summary data" such as allele frequency information from large reference panels, whereas sharing of individual-level genotype data is usually explicitly forbidden. It is not quite clear to me where sharing the fit of a DAE falls here, or how much information on individual genotypes the trained DAE contains. The current manuscript does not adequately address this issue.

Currently there are no official data sharing restrictions on deep learning data. We are aware that future policies may rise, and we have started a collaboration with Oak Ridge National Laboratory to explore differential privacy techniques and privacy concerns for these autoencoders. Another point to consider is that the autoencoders segment the genome, making reconstruction of an individual genome impossible even if reference data were somehow recoverable from the neural networks. Regardless, this is an interesting and important point that should be addressed in the manuscript and we have added a paragraph discussing this point.

Reviewer #4 (Public Review):

In this manuscript, Dias et al proposed a novel genotype imputation method using autoencoders (AE), which achieves comparable or superior accuracy relative to the state-of-the-art HMM-based imputation methods after tuning. The idea is innovative and provides an alternative solution to the important task of genotype imputation. The authors also conducted some experiments using three different datasets as targets to showcase the value of their approach. The overall framework of the method is clearly presented but more technical details are needed. The results presented showed slight advantage of AE imputation after tuning but more comprehensive evaluations are needed. In particular, the authors didn't consider post-imputation quality control. The reported overall performance (R2 in the range of 0.2-0.6) seems low and inconsistent with the imputation literature.

Overall, the method has potential but is not sufficiently compelling in its current form.

We show average accuracy of 0.2-0.6 in Table 4, but that is the average R2 per variant across all variants (no MAF filtering or binning applied). The reviewer points that the accuracy should be R2>0.8, but this R2>0.8 refers to common variants only (allele frequency >1%), and we have shown r2>0.8 for these variants (Figure 4). The aggregate accuracy displayed in Table 4 is lower because the vast majority of variants fall below 1% allele frequency threshold.

The references bellow demonstrate this issue and agree with our results:

References:

Rubinacci S, Delaneau O, Marchini J. Genotype imputation using the positional burrows wheeler transform. PLoS genetics. 2020 Nov 16;16(11):e1009049.

McCarthy S, Das S, Kretzschmar W, Delaneau O, Wood AR, Teumer A, Kang HM, Fuchsberger C, Danecek P, Sharp K, Luo Y. A reference panel of 64,976 haplotypes for genotype imputation. Nature genetics. 2016 Oct;48(10):1279.

Vergara C, Parker MM, Franco L, Cho MH, Valencia-Duarte AV, Beaty TH, Duggal P. Genotype imputation performance of three reference panels using African ancestry individuals. Human genetics. 2018 Apr;137(4):281-92.

Author Response

Reviewer #1 (Public Review):

The manuscript by Rekler and Kalcheim examines the role of neural tube-derived retinoic acid (RA) in neural crest development. They observe that the onset of expression of the RA-synthesizing enzyme RALDH2 in the dorsal neural tube coincides with the end of neural crest production. The authors propose that this local source of RA is essential to activate the transcription of Bambi other BMP inhibitors, leading to the disruption of BMP signaling. Loss of BMP activity at the dorsal neural tube would halt neural crest production, leading to the establishment of the definite roof plate. Thus, precise temporal regulation of RALDH2 in the dorsal neural tube would dictate the timing of neural crest production and the segregation of PNS and CNS progenitors.

Previous studies have already identified a role for RA in the control of the timing of neural crest production. MartinezMorales et al (JCB 2011) have shown that during early trunk development, mesoderm-derived RA works with FGF signaling to jumpstart the BMP/Wnt cascade that drives neural crest migration in the trunk. Rekler and Kalcheim choose to focused on a distinct function of RA at a later timepoint. The main contribution of the present study is the demonstration that - at later stages - RA produced by the neural tube has the opposite effect, acting to inhibit the BMP/Wnt cascade and halt neural crest production. Thus, RA would be a major regulator of the timing of neural crest production, acting to both trigger and repress neural crest migration.

The study's strengths lie in an experimental strategy that allows the authors to manipulate RA function in a stagespecific manner and therefore uncover a later role for the signaling system in neural crest production. The authors also show that RA inhibition results in an incomplete fate switch and results in the generation of cells that share regulatory features of neural crest and roof plate cells. A significant limitation of the study is that the molecular mechanisms that endow RA signaling with stage-specific functions remain unknown. This is of particularly important since the early vs. late RA seem to have opposing effects, acting to either promote or terminate neural crest production.

We thank this referee for her/his positive comments on our manuscript. We agree with the referee that a key question is understanding how RA signaling is differentially interpreted over time given its multistage activity in dorsal NT development.

This is based on the following findings: Years ago, we uncovered that the balance between activities of BMP/Wnt and noggin in the dorsal NT trigger the onset of NC EMT. Martinez-Morales et al. strengthened our findings by reporting that a balance between somitic RA and FGF works on the reported BMP/Wnt modules to initiate the process. This group found that at gastrulation stages, RA is required for NC specification, as revealed by analysis of VAD quail embryos. Next, during somite formation, somitic RA is necessary for the onset of emigration of specified NC progenitors but at advanced somite stages it is dispensable for the subsequent maintenance of cell emigration. Presently, we find that RP-derived RA ends NC production. Together, this highlights a dynamic behavior of RA at 4 sequential stages of NC ontogeny. Clearly enough, the two first effects are mediated by an influence of RA dorsoventral patterning of the early NT, as distribution of ventral NT markers was strongly affected. In our case, RA from the nascent RP has no such effects suggesting that RP-derived RA acts at a post-patterning phase to specifically affect the dorsal NT.

All things considered, we think that the problem is not simply a binary question of “opposing functions of RA signaling in starting or terminating NC production”. Instead, it is the understanding of a differential interpretation to the same morphogen by progenitor cells with changing states and at sequential stages.

To the referee’s request, we begun addressing the question of how does RA inhibit BMP signaling close to the RP stage. To this end, we decided first to examine the temporal regulation of Raldh2 expression that is restricted to the RP stage, and is therefore a prerequisite for the late activity of RA. Whereas repressing RA activity extends the NC phase including the continuous transcription of Foxd3, Sox9 and Snail2 (Fig.3), we now found that extending the activity of each of these transcription factors close to the RP stage represses the onset of Raldh2 transcription in the nascent RP (new Fig. 9). We interpret these results to mean that as long as NC genes are active in the dorsal NT (NC stage), local Raldh2 and consequent RA synthesis in the NT does not take place, so Raldh2 in RP is repressed by NC-specific traits. The significance of these data is twofold: first, they explain the late onset of Raldh2 production at the RP stage. Second, since we also report the reciprocal result, that RA represses NC genes (Fig.3), we conclude that a cross repressive interaction exists between NC and RP-specific genes downstream of RA, being an emerging temporal property of the network. These data further indicate that the changing roles of RA throughout development of the dorsal neural primordium, largely depend on a different interpretation of the signal mediated by changing and mutually repressive codes.

We have now presented these data in Fig.9. To clarify our thoughts further, we now provide a working model summarizing the effects of RA in NC to RP transition (Fig.10B).

Our article uncovers for the first time and thoroughly documents, a role of local RA activity on the end of NC production and ensuing RP architecture. We believe that a comprehensive elucidation of the molecular mechanism responsible for inhibition of BMP signaling by local RA is the next obligatory step. We show in this study the selective activation of BMP inhibitors by endogenous RA and previously found that one of them, Hes/hairy, indeed inhibits BMP signaling and NC EMT (Nitzan et al, 2016). Therefore we propose that upregulation of BMP inhibitors by RA is a possible mechanism. However, we also predict that this is not the only one, and a deeper understanding of this problem is beyond the scope of the present study.

Additional possibilities that fit with our data were now discussed: RA expression in somites vs. RP can be regulated by different enhancers and thus have distinct functions. For example, a specific enhancer driving expression of Raldh2 was found to be activated only at the definitive RP stage (Castillo et al., 2010). This enhancer contains Tcf binding sites and thus may be activated by Wnt signaling. In turn, as we show, RP-derived Raldh2 and resulting RA could negatively feed-back on Wnt signaling in the formed RP either directly or through BMP acting upstream of Wnt (now presented in Fig. 10B).

Another possible scenario is that RA represses BMP signaling by inactivating Smad proteins via ubiquitination, as shown to be the case in selected cell lines (Sheng et al., 2010). These possibilities were discussed and await to be systematically explored.

Comments:

Previous studies have demonstrated that early RA production (presumably from the mesoderm) is necessary for the expression of early dorsal neural tube / neural crest genes like Pax7, Msx, Wnt1, and even BMP ligands. This is in contrast to the local source of RA, which presumably would be silencing these genes. Thus, mesoderm-derived RA would have the opposite effect in these progenitors than the RA synthesized in the neural tube. The study does not provide a mechanism that explains these stage-specific effects of the morphogen.

As elaborated in our reply above to the general comment, we believe that RA whether emanating from somites or nascent RP, provides an initial signal that is later relayed upon target factors unique to each stage. It is possible that the precise source of factor plays a role; along this line we showed that somitic RA is dispensable for late events, reciprocally, there is no RA synthesis in the early NT that could affect NC cells. Having said that, there is RA activity in the NT at both stages and the output is still different. Hence, there should be more to this: In the revised version, we report that NC and RP-specific genes stand in a mutually repressive interaction downstream of RA, and this may contribute to the stage-specific effects of the morphogen.

The effects of RA manipulation are often examined with non-quantitative techniques, like in situ hybridization (Fig. 2, 3). The incorporation of quantitative approaches (e.g., qPCR) would allow for the precise characterization of phenotypes (and better estimation of penetrance, etc.). Furthermore, the study lacks molecular/biochemical strategies to define the regulatory linkages between genes and pathways. This is a considerable limitation of the study since it prevents the establishment of a regulatory axis that would directly connect RA signaling to the BMP pathway.

As the referee may notice, most genes examined are not restricted solely to the dorsal NT/RP domains. Since it is technically not accurate to isolate only the regions of interest for qPCR analysis, collecting entire NTs following unilateral or bilateral electroporations for qPCR would be highly inaccurate. In situ hybridization and immunohistochemistry provide a precise tool to assess the spatial localization of the transcripts/proteins of interest. To note is that in all cases examined, development of the color reactions was for the same length of time for control and experimental cases and photography was performed under identical conditions. Furthermore, in most cases, effects between treatments were dramatic, readily apparent at a qualitative level and easily quantifiable from ISH or fluorescent images.

As to regulatory linkages between genes and pathways, the referee is correct; we do not demonstrate direct molecular interactions between the different players at the biochemical level. The present study provides a wealth of novel data connecting morphogens such as RA with BMP and Wnt activities, and those with a variety of downstream genes specific for either NC or RP stages. The next step will be to ask about the precise nature of the linkages between specific molecules/pathways.

The function (and the regulation) of RALDH2 at the dorsal neural tube has been studied thoroughly, and RA is a known player in the dorsal-ventral patterning of the CNS. It is not clear to what extent the phenotypes observed by the authors are due to the disruption of a neural crest-intrinsic mechanism or if they are secondary to the overall changes in the cellular organization of the neural tube caused by loss of RA.

This is a good point as RA is known to have multiple effects on NT development whose nature changes with stage. Available data emanating from young caudal neural plate explants and from VAD embryos that lack RA, showed that early RA signaling from developing somites is required for ventral patterning of the neural tube (motoneurons and V1, V2 interneurons) and for neuronal differentiation (Diez del Corral et al, 2003, Sockanathan and Jessel, 1998, Liu et al, 2001, Maden et al, 1996). These effects were shown to depend, at least partly, on antagonistic activities of RA and FGF in mesoderm which affect ventral, but not dorsal NT patterning (Diez del Corral et al, 2003). Our study focuses on a later stage when D-V neural tube patterning is already established.

To address the referee’s comment, we now examined the effects of RA attenuation on expression of Pax7, a dorsal factor, and Hb9, a motoneuron-specific protein. We found that RARa403 does not affect the localization and/or extent of expression of Hb9, and causes only a mild 12% increase in the area of expression of Pax7. Consistent with these results, we also show in several figures that in the absence of RA signaling pSmad and Wnt activities, Foxd3, Snai2 and Sox9 expression patterns are prolonged in time but not in D-V extent.

These data corroborate that the effects documented are directed to the dorsal NT and do not result from overall changes in D-V patterning. The data were now added as Fig.7 Supplementary 1.

The authors rely solely upon overexpression constructs to manipulate the activity of the RA signaling pathway, which may be prone to artifacts. Furthermore, both overexpression constructs aim at inhibiting RA activity. This limits the impact of the work since there is no demonstration that RA is sufficient to activate BMP inhibitors and halt neural crest production.

The tools we used to repress RA signaling consist of RARa403 that acts as a pan-dominant negative construct to abrogate receptor activity, and Cyp26A1, an enzyme that degrades RA. To activate RA signaling in a ligand- independent manner, we now implemented VP16-RAR-alpha in the revised version of this manuscript. All these tools are extensively and routinely employed in the literature in a variety of animal species and were shown to act in vivo as expected both by others and further confirmed by us in the present study. Having said that, we are currently optimizing the CRISPR-Cas9 method for gene editing of RA-specific genes and hope to succeed in the near future.

We have now performed experiments to address the sufficiency of RA. Data were now added as Fig.5 Supplem 2 and 3 and Fig.6 Supp.2 .

As we expected, gain of RA function at NC stages is not sufficient to prematurely activate BMP inhibitors like BAMBI, to end prematurely BMP signaling (pSMAD) or NC EMT, to alter the dynamics of expression of NC-specific genes, or to cause an earlier appearance of RP-specific traits. This is fully consistent with RA being active at NC stages when BMP/Wnt signaling, NC EMT, etc are operational. The fact that RA is necessary but not sufficient for these processes further suggest that the key is how NC cells at various stages of their ontogeny and then RP cells, differentially interpret the signal given the profound changes in cellular and molecular landscapes apparent between these stages.

Reviewer #2 (Public Review):

The manuscript presents a novel role for RA signaling during development as the mediator of the switch that occurs in the dorsal neural tube after the neural crest cells have migrated and the roof plate forms. The finding is interesting and novel as the events that take place at the end of neural crest stage are poorly understood. The strengths of the manuscript are that the study is well planned and executed to show the interesting phenotype of delayed/disturbed roof plate formation accompanied with prolonged neural crest stage caused by inhibition of RA signaling in the dorsal neural tube. The results also show that RA signaling marks the RP territory and inhibits the DI1 interneurons from invading the region. The results bring novel information to the field. The original finding of the involvement of RA in the process was revealed in a RNAseq screen comparison between the neural crest and the roof plate (which was recently published by the same lab). However, the current study doesn't use any new technology such as high throughput screens or high resolution or live imaging etc., but rather relies mainly on "old fashioned" techniques: electroporation to induce transient inhibition of RA signaling in the dorsal neural tube followed by analysis of the phenotype by using chromogenic in situ hybridization. The chosen techniques are sufficient to convincingly show the point the authors want to make and the study serves as a reminder that fancy new techniques are not necessarily a requirement for creating a solid story. The manuscript is also well written and easy to follow.

We thank this referee for a very positive feedback on our study. Although we are always motivated by the implementation of new techniques, we agree that the primary goal is to answer a biologically meaningful question with suitable means.

Finally, the manuscript links the activation of RA signaling to the decline of BMP signaling and specifically the upregulation of BMP inhibitors in the dorsal neural tube at the end of the NC stage, but in its current form the proof of this proposed link remains weak.

Our article uncovers for the first time and thoroughly documents, a role of local RA activity on the end of NC production and ensuing RP architecture. We believe that a comprehensive elucidation of the molecular mechanism responsible for inhibition of BMP signaling by local RA is the next obligatory step. We show in this study the selective activation of BMP inhibitors by endogenous RA and previously found that one of them, Hes/hairy, indeed inhibits BMP signaling and NC EMT (Nitzan et al, 2016). Therefore we propose that upregulation of BMP inhibitors by RA is a possible mechanism. However, we also predict that this is not the only one, and a deeper understanding of this problem is beyond the scope of the present study.

Additional possibilities that fit with our data were now discussed: RA expression in somites vs. RP can be regulated by different enhancers and thus have distinct functions. For example, a specific enhancer driving expression of Raldh2 was found to be activated only at the definitive RP stage (Castillo et al., 2010). This enhancer contains Tcf binding sites and thus may be activated by Wnt signaling. In turn, as we show, RP-derived Raldh2 and resulting RA could negatively feed-back on Wnt signaling in the formed RP either directly or through BMP acting upstream of Wnt (this was now presented in a working model in Fig. 10B).

Another possible scenario is that RA represses BMP signaling by inactivating Smad proteins via ubiquitination, as shown to be the case in selected cell lines (Sheng et al., 2010). These possibilities were discussed and await to be explored systematically.

Similarly, the manuscript does not address the consequences of exposure of RA to the dorsal neural tube during NC stage and it thus remains unknown whether RA signaling is sufficient to end the NC stage and activate roof plate formation prematurely. Additional experiments of this kind would help clarify the role of RA in the dorsal neural tube and the reciprocal roles of the two signaling pathways (RA and BMP).

We have now performed experiments to address the sufficiency of RA. Data were now added as Fig.5 Supp.2 and Supp.3, and Fig.6 Supp.2, and discussed.

As we expected, gain of RA function at NC stages is not sufficient to prematurely activate BMP inhibitors, to end prematurely BMP signaling (pSMAD) or NC EMT, to alter the dynamics of expression of NC-specific genes, or to cause an earlier appearance of RP-specific traits.

This result is totally understandable in light of RA being anyway active (but not produced) in NT at NC stages (original Fig.1) when BMP/Wnt signaling, a NC-specific gene network, and NC EMT are operational.

The fact that RA is necessary but not sufficient for these processes further suggests that the key is in the following, perhaps complementary mechanisms: 1) a different interpretation of the same signal by NC progenitors at sequential stages of their ontogeny and then by RP cells, accounted for by the profound changes in cellular and molecular landscapes apparent between these stages. 2) the possibility that somite-derived versus RP-derived RA are differentially interpreted by the dorsal NT cells owing, for example, to a distinctive mode of ligand presentation (e.g; by CRABP1 expressed in RP but not NC, etc).

Author Response

Reviewer #1 (Public Review):

Weaknesses: 1. The paper lacks some clarification in some terms used in the paper such as "round chondrocytes". Additional histological data on the organ cultures would provide supporting evidence on the role of CNP in chondrocytes.

In bone research fields, growth plate chondrocytes are generally classified into three major cell types; round, columnar, and hypertrophic chondrocytes, and “round chondrocytes” is generally used for specifying growth plate chondrocytes. We have briefly explained cells assessed in the Materials and Methods section of the revised manuscript.

In response to the comment, we histologically analyzed cultured CNP-treated bones from the chondrocyte specific Trpm7-knockout (Trpm7fl/fl, 11Enh-Cre+/−) and control (Trpm7fl/fl, 11Enh-Cre−/−) mice. The new data obtained clearly indicate that CNP treatments extend the columnar chondrocytic zones in control bones but not in chondrocyte-specific Trpm7-knockout bones (Figure 7 in the revised manuscript). We further analyzed in detail CNP-treated metatarsal bones from wild-type mice. CNP treatments consistently expanded the columnar chondrocytic zones but did not affect the cell densities (Figure 7-figure supplement 1 in the revised manuscript). Moreover, CNP-promoted extracellular matrix production seemed to contribute largely to the extension of columnar chondrocyte zone toward bone outgrowth stimulation.

1. The authors also generated NPR2 chondrocytes-specific null mouse mode. It would be interesting to include some data on the phenotype of these mice by micro-CT, histology, etc. More specific details are provided below.

Overview of histological analysis in chondrocyte-specific Npr2-knockout (Npr2fl/fl, Col2a1-Cre+/−) mice has been previously reported (Nakao K., et al., Sci Rep., 5;10554, 2015). Since femoral bones from E17.5 mice were too fragile to analyze using micro-CT, we performed von Kossa-staining of femoral bones from the chondrocyte-specific Npr2-knockout (Npr2fl/fl, Col2a1-Cre+/−) and control (Npr2fl/fl, Col2a1-Cre−/−) mice instead. As reasonably expected, femoral bones from the knockout mice exhibited insufficient mineralization.

The reviewer believe the authors achieved their aims, while some additional supporting data and clarifications are needed.

The overall summary of the data provided is supportive, methods utilized are well justified, again, additional histological data would support the overall summary.

Data generated and presented in the report will enhance our understanding on the role of CNP and possible utilization of novel therapeutic targets for CNP for the treatment of bone growth diseases.

We thank the reviewer for his valuable and helpful comments.

Reviewer #2 (Public Review):

Strength: 1. Experiments are well designed, performed with proper control and conclusion drawn from data is highly convincing. 2. Valid animal model (floxed mice) using chondrocyte specific deletion of gene were used to show in vivo effect of gene deletion on bone formation. 3. Preclinical model of OA were used in vivo using mice as an experimental animal, OA progression were characterized using established grading system. 4. All the Western blots are shown along with densitometric quantification. 5. Ex vivo molecular mechanism is also provided which added strength in the manuscript.

Methods, results and data interpretation: 1. Methods section is adequate and describes enough details to replicate in independent study. 2. Relevant statistics are used to infer conclusion form data. 3. There is no objective error in presenting the data, conclusions drawn from experiments are convincing.

We thank the reviewer for the encouraging comments.

Author Response:

Reviewer #1 (Public Review):

This paper provides experimental and modeling analysis of the inter-brain coupling of socially interacting bats, and reports that coordinated brain activity evolves at a slower time scale than the activity describing the differences. Specifically, the paper finds that there is an attracting submanifold corresponding to the mean (or "common mode") of neural activity, and that the dynamics in the orthogonal eigenmode, corresponding to the difference in brain activity, decays rapidly. These rapid decays in the difference mode are referred to as "catch up" activity.

There are two main findings:

1) Neural activity (especially higher frequency LFP activity in the 30-150Hz range) is modulated by social context. Specifically, the ratio of the averaged, moment-to-moment MEAN:DIFF ratio is much higher when the bats are in a single chamber, clearly indicating that the animals are coordinating their neural activity. This change also seems to hold -- although not as striking -- in lower-frequency LFP and spiking activity.

2) The time scales of the mean vs. difference dynamics are segregated: the "difference dynamics" evolve at a faster time scale than "similarity dynamics", seems to be well supported.

The basic finding is presented in Figure 1. The rest of the paper is focused on a modeling study to garner further insight into the dynamics.

Weaknesses:

This is an entirely phenomenological paper, and while it claims to garner "mechanistic insight", it is unclear what that means.

We regret not clarifying sufficiently what we meant by “mechanistic insight.” The insight is the following: functional across-brain coupling acts as positive feedback to the mean component of neural activity, which amplifies it and slows it down; at the same time, it acts as negative feedback to the difference component, which suppresses it and speeds it up. Thus, findings (1) and (2) in the reviewer’s summary above can be explained by the same model mechanism. As the reviewer pointed out below, the details of the model are complex, which could have made the simple mechanism above opaque. Thus, we analyzed two simplified versions of the model to make the mechanistic insight clear. This is detailed below in our response to the reviewer’s comment on model complexity.

The basic idea of the model is simple and somewhat interesting, but the details are extremely complex. There are many examples of this, but the method used to "regress out" the behavior was very hard to interpret.

The method for regressing out behavior was described in Materials and Methods section 3.10, and we regret having neglected to reference it in the main text. We now reference it at the first instance in the main text where this is relevant.

On the face of it, the model is extremely simple: a two-state linear dynamical system. However, this simplistic description buries extreme complexity. The model is extremely complex as involves a large number of parameters (e.g., time switching 'b' values, the values of which are completely unclear), the switching over time of these parameters based on hand-scored animal behavioral state, and the complex mix of markovian and linear dynamical systems theoretic results.

As the reviewer pointed out, the core of the model is very simple: a linear dynamical system that models neural activity coupling. The model mechanism of positive and negative feedback, which is responsible for reproducing the two experimental results summarized by the reviewer above, is contained in this core (see Materials and Methods section 3.7 for details). On top of this, the model has a layer of complexity, involving a Markov chain model of behavior and a large number of behavioral parameters. This layer of complexity is independent from the feedback mechanism of the core of the model. Thus, while it makes the model more biologically realistic, it is not required to reproduce the two main experimental results. To explicitly show this, and to better understand the dependence of model behavior on its parameters, we analyzed two reduced versions of the model. The first reduced model replaces the behavioral inputs with white noise. The original model is , where a is neural activity, , is the coupling matrix, b is behavioral modulation, and τ is a time constant. b is where the complexity lies, as it is simulated using a Markov chain and involves many parameters. To strip away this layer of complexity, we replaced b with noise having a simple structure, namely, the mean and difference components of b having identical, flat power spectra. Importantly, this noise input does not induce correlation between bats, and it amounts to inputs of the same magnitude and same timescales to the mean and difference components of a. The resulting reduced model has only two parameters, the functional self-coupling C_S and functional across-brain coupling C_I (for simplicity, τ can be absorbed into the other parameters). We are interested in the two results the reviewer summarized above: (1) the mean component of neural activity having a larger variance than the difference component; (2) the mean component having a slow timescale than the difference component. In the manuscript, these are respectively quantified using the variance ratio and the power spectral centroid ratio of the mean and difference components. The reduced model allowed us to derive analytical expressions for these two quantities (see Materials and Methods section 3.8 for details). We found that they have very simple dependence on the functional coupling parameters: the variance ratio (mean variance divided by difference variance) is approximately , and the centroid ratio (mean centroid divided by difference centroid) is approximately .

This parameter dependence is visualized below (note that the color maps are in log scale, and the white spaces are regions where the model is unstable).

In the experimental data, the mean component had larger variance and lower power spectral centroid than the difference component. This corresponds to the parameter regime of (enclosed by dashed lines). Thus, a positive C_I acts as positive feedback to the mean component and negative feedback to the difference component, modulating their variance and timescales in opposite directions. This is consistent with the analysis of the original model in Materials and Methods section 3.7. In the revised manuscript, we’ve now added analysis of this reduced model to the Results section, and the above figure has been added as Figure 3I-J.

The reviewer has stated a concern regarding the large number of parameters that set the input level according to behavioral state (b_resting, b_(social grooming), b_fighting, etc.). These parameters are important for ensuring that the model outputs realistic levels of behaviorally modulated neural activity (discussed below in our reply regarding model fit), but they are not important for the main results on variance and timescales. To demonstrate this, we studied a second reduced model. This model is identical to our original model except that, for each simulation, each of the behavior parameters (b_fighting, etc.) was independently drawn from the uniform distribution from 0 to 1. Despite the completely random behavioral parameters, this reduced model reproduces the variance and timescales results just like the original model, as shown in the figure below (compare with Figure 3E-F).

To summarize, the reduced models allowed us to identify the simple parameter dependence of the modeling results, and showed that the simple linear dynamical system at the core of the original model is sufficient to reproduce the two main experimental observations.

Indeed, a fundamental weakness of the model is that the Markov chain is taken as an "input" to the 2-state linear systems model, as if somehow the neural state does not affect the state transitions.

Yes, this is a limitation of our model. We’ve added a discussion of this limitation, as well as future directions for overcoming it, in the Discussion section. The reason we did not model neural control of behavioral transitions is that it is under-constrained by existing data. While the brain obviously controls behaviors, not every part of the brain controls every behavior. Of the 11 behaviors observed in this study, we do not know which of them is controlled by the bat frontal cortex, and we do not know how they might be controlled (i.e., what specific spatiotemporal activity patterns affects behaviors in what ways). Without this knowledge, it’s unclear how to implement neural control of behavior in the model. This knowledge requires perturbation studies (lesion, inactivation, or activity manipulation) to establish casual relationships from neural activity to specific behaviors in the bat, which will be an important future direction.

On the other hand, as the reviewer stated, our model included behavioral modulation of neural activity. It is well known that in mammals, arousal and movement modulate neural activity globally across cortex (McGinley et al., 2015, Neuron). Thus, given that different behaviors in general involve different levels of arousal and movement, our model included behavior-dependent modulation of frontal cortical neural activity. Finally, for the reviewer’s convenience, we also quote below the paragraph addressing this issue in the revised Discussion. “Another limitation of our model is the “open-loop” nature of the relationship between behavior and neural activity. Specifically, we modeled neural activity as being modulated by behavior, but behavior was modeled using a Markov chain that is independent from the neural activity. In reality, neural activity and behavior form a closed-loop, with different social behaviors being controlled by the neural activity of specific neural populations in specific brain regions. Thus, an important future direction is to close the loop by incorporating neural control of social behaviors into models of the inter-brain relationship in bats. This will require future experimental studies to identify which frontal cortical regions and populations in bats are necessary or sufficient to control social behaviors, as well as the detailed causal relationship from neural activity to social behavior. Furthermore, as social interactions can occur at multiple timescales, it will be interesting to investigate how these are controlled by neural activity at different timescales, and how those timescales are shaped by functional across-brain coupling. In summary, such a closed-loop model will shed light on how inter-brain activity patterns and dynamic social interactions co-evolve and feedback onto each other.”

Further, the Markov assumption is not rigorously tested.

We have now tested the Markov assumption, using the following methods. We compared three models of bat behaviors: (1) the independent model, where the behavioral state at a given time point is independent from the state at other time points; (2) the 1st-order dependency model, where the behavioral state at a given time point depends on the state at the previous time point only; (3) the 2nd-order dependency model, where the behavioral state at a given time point depends on the states at the two previous time points. The Markov assumption corresponds to model (2), which is used as a part of the main model of the paper. Note that models with longer time-dependencies (≥3) were not tested because the number of parameters grows exponentially with model order and our dataset is not large enough to fit them.

To compare the three models, we split the behavioral data into a training set and a test set, fitted each model on the training set (Laplace smoothing was used to avoid assigning zero probability to unobserved events), and calculated the log-likelihood of the test set under each model. The figure below shows the cross-validated likelihoods for the behavioral data of one-chamber (A) and two-chambers (B) sessions, which were fitted separately; circles and error bars are means and standard deviations across 100 random splits of the data into training and test sets.

As the figure above shows, the 1st-order model had the highest likelihood on average. This does not necessarily prove that bat behavior obeys the Markov assumption (if we had a lot more data, we might be able to fit better 2nd-order and higher-order models). But this does mean that, given the amount of data we have, the best model that we can fit is the 1st-order Markov chain. Thus, this result supports our usage of the Markov chain in the main model of the paper. In the revised manuscript, the above figure is included as Figure 3—figure supplement 2A-B, and the analysis is described in Materials and Methods section 3.5.

No model selecting or other model validation appears to be done.

To evaluate model fit, we simulated our model using experimentally observed behaviors (rather than simulating behaviors using a Markov chain), and compared the simulated neural activity with the experimentally observed activity (see Materials and Methods section 3.6 for detailed procedures). The comparison for an example experimental session is shown below, where we’ve plotted the experimentally observed neural activity and behaviors for bat 1 (A) and bat 2 (B), along with the simulated neural activity. The correlation coefficient between data and model are indicated above each plot. These are representative examples, as the average correlation over all sessions and bats is 0.72 (standard deviation is 0.10). This figure was added to the revised manuscript as Figure 3—figure supplement 1.

In evaluating model fit, we realized that the model in the original manuscript produced outputs with a DC offset different from that of the data. Thus, in the revised manuscript (including the figure above), we added one more behavioral parameter (b_constant) that adjusts the DC offset, which is a parameter that reflects the effect of a baseline arousal level on neural activity (Materials and Methods section 3.4). Note that, since the only effect of this parameter is to adjust the DC offset of neural activity, it does not change any of the results in the paper.

In short, the model, while very interesting, is so complex that it is literally impossible to evaluate. The authors report literally no shortcomings of their model. They do not report parameter estimation methods. They do not report fitting errors or other model validation metrics. The only evaluation is whether it can produce certain outputs that are similar to biological data. While the latter is certainly important, all models are wrong, and it essential to have a model simple enough to understand, both in terms of how it works and how it fails.

The comments on the complexity of the model and on fitting errors have been addressed above. Regarding parameter estimation methods, they were described in Materials and Methods section 3.14, and we regret having neglected to directly reference it in the original manuscript. We now reference the section in the legend of Figure 3A which is the first place to introduce the parameters. Briefly, the behavioral parameters (b_resting, b_fighting, etc.) were simply chosen to be the average neural activity during the respective behaviors from the data; the other parameters were chosen by hand to roughly match the levels of activity from the data, keeping within the parameter regime of identified from the analyses. As we showed above, these parameters provide a reasonable fit to the data.

The reason we chose the parameters heuristically in this way, rather than by minimizing some error objective, is the following. Our goal was to build a model that could qualitatively reproduce the experimental findings in a robust manner, that is, without fine-tuning of parameters. Thus, we analyzed the model to understand how model behaviors depend on the parameters, and to identify the parameter regime that reproduces the qualitative trends seen in the data (Figure 3I-J; Materials and Methods sections 3.7 and 3.8). Guided by these analyses, we chose parameters heuristically without algorithmic fine-tuning.

Finally, following suggestions from reviewer 1 and reviewer 3, we have added discussions of shortcomings of the models (the last two paragraphs of the Discussion). With these discussions of model limitations, along with the presentation of simple insights into model mechanism from the reduced models above, we believe we have now presented a model that is “simple enough to understand, both in terms of how it works and how it fails.”

In general, while the basic finding is fairly interesting, and the experiments and their findings are highly relevant to the field, the modeling and its explication fall short.

It is not that it is wrong or bad; however, it is not clear that such a complex model increases our understanding beyond the experimental findings in Figure 1, and if it does, there has to be a major caveat that the model itself is not carefully vetted.

Based on the reviewer’s comments on the model’s complexity, we have analyzed reduced versions of the model to understand its simple underlying mechanisms, as described above. This goes beyond the experimental findings in Figure 1, as it provides a computational mechanism that could give rise to those experimental findings. Moreover, based on the reviewer’s comments, we have more carefully vetted the model, by evaluating model fit and testing different behavioral models that assume or doesn’t assume the Markov property. Finally, we now discuss caveats of the model in the Discussion section, including the open-loop nature of the model as pointed out by the reviewer.

Author Response

Reviewer #1 (Public Review):

Yang. et al. use computational modeling to explore how neurons can co-regulate different properties (firing rate, excitability thresholds, energy consumption) by adjusting ion channel expression. To do so, they rely on the activity-dependent channel expression model introduced in O'Leary et al. 2014 and assume that any regulation loop can be boiled down to such a model. They thus propose a parallel feedback loop regulation model, in which each loop regulates a property by chasing its target value and regulating ion channel expression according to an integral control law.

The authors start by proving experimentally and computationally ion channel pleiotropy. This preliminary analysis is clearly developed and confirms/rediscovers in CA1 neurons known facts originally observed in invertebrate systems like the STG. They subsequently use their regulation model to provide elegant geometric explanations for the emergence of ion channels correlations and for the success or failure of homeostatic regulation, as a function of the number of regulated properties and the number of ion channels.

The model they rely on exhibits two basic characteristics. Suppose the model possesses N different types of ion channels.

1.As in the model in O'Leary et al. 2014, when taken in isolation, the regulator of each neural property possesses an N-1 dimensional submanifold of steady-states in the N-dimensional maximal conductance space where the target for the regulated property is reached.

2.Regulation loops are independent of each other.

Given these two characteristics, in the presence of M regulated neural properties, the regulation target is reached simultaneously for each of them on an (N-M)-dimensional joint target submanifold of homeostatic steady states, i.e., the intersection of M (N-1)-dimensional target submanifolds. Depending on initial conditions, homeostatically regulated maximal conductances will spread out along this submanifold, thus creating N-M dimensional correlations. This (mathematically) elementary observation leads to the various general conclusions of the paper, the main of which are i) that increasing the number of regulated properties increase ion channel correlations (by reducing the dimension of the joint target submanifold) and ii) that increasing the number of regulated properties makes homeostatic regulation more likely to fail (when the intersection between the target submanifolds is empty). This simple geometric view on multi-property regulation is neat and, most importantly, experimentally verifiable/falsifiable.

The main drawback of this approach is that characteristics 1 and 2 (above) of the model used in the paper are non-generic and makes the model a useful but maybe oversimplified (and fragile) testbed. Let me develop.

Property 1 reflects one of the main limitations of the model in O'Leary et al. 2014, namely, that this model provides biologically meaningful results and predictions only when initial conditions are small and in the absence of any disturbance to its regulation dynamics (including the presence of multiple master regulators).This follows exactly from the fact that, in that model, the homeostatic regulator has zero effect once the state reaches the N-1 dimensional submanifold of target steady states. Thus, different initial conditions or exogenous disturbances will arbitrarily spread conductances on this submanifold, making it unrealistically unrobust to both types of perturbations.This limitation was overcome in a simple, biologically plausible way in Franci et al. 2020 by adding a molecular regulatory network between the homeostatic sensor and the regulated conductances. The revised model still exhibits the same correlated variability between maximal conductances as the original model. But only in the revised model the correlation ray exhibits biologically-meaningful levels of robustness both to disturbances and initial conditions. In dynamical systems terminology, the model in O'Leary et al. 2014 is structurally unstable (non generic) whereas its 2020 revision is structurally stable (generic). Crucially, in the 2020 model the homeostatic target is approximately reached at a unique steady state (i.e., the target submanifold is zero-dimensional) but the presence of a slow direction v_slow in the regulation space amplifies heterogeneities and disturbances, which leads to correlated variability (along v_slow).

We have identified several issues, and will address each in turn.

Initial conditions: Our results do not rely on initial conditions being small. This is first illustrated in Fig. 4 with the conditions immediately post-perturbation. Whereas O’Leary et al. (2014) presented results in the context of development (starting from nothing), we have focused on recovery from an acute perturbation (recovering from something). The statement that our model provides “biologically meaningful results and predictions only when initial conditions are small” is inaccurate – this depends on the question being asked. We use (a simplified version of) the O’Leary regulation mechanism to show that correlations arise in different ways depending on the dimensionality of solution space. This does not depend on initial conditions and, as explained in a new figure (Fig. 8), the dimensionality of solution space still has an important impact on the correlations that emerge under noisy conditions. We believe these to be meaningful results.

Unrobustness / structural instability: Noise is an important, ongoing perturbation that we did not consider in the original version of our paper. Franci et al. (2020) show that noise disrupts solutions found by the simple regulation mechanism used by O’Leary et al. (2013, 2014). The basis for this – that the simple regulation mechanism brings conductance densities to the solution manifold but does not control their spread across the manifold – is now highlighted in our revised text (lines 208-210). As now shown in a new figure (Fig. 8), ion channel correlations are disrupted by noise, depending on solution space dimensionality, but other correlations arise. Importantly, our regulation mechanism successfully maintains regulated properties near their target values despite noise; in that respect, regulation is robust.

Conductance densities do not remain / return to a restricted location on the solution manifold. In that sense, the solution set is not attractive, which, if we understand correctly, is equivalent to being unrobust, non-generic, and structurally unstable. Being unstable sounds bad, but from our perspective, so long as the system can regulate properties to their target values, the conductance density combinations used to do so are not a main concern (see Discussion, lines 310-314). Indeed, we highlight that conductance densities do not converge on the same restricted space if we control different ion channels (Fig 4) or if we control the same ion channels with different regulation rates (Fig 7). In fact, being too stable would reduce the hidden variability required to explain why neurons that appear similar respond differently to a perturbation, which is a concern. Furthermore, even if there is an attractive subspace, this could arise from regulation of other unaccounted for properties (which would reduce solution space dimensionality) rather than because of cooperative molecular interactions, which is to say that there are alternative explanations for attractive solution sets. Addressing such issues arguably extends beyond the scope of our study.

Unbounded spread: Noise-induced spread would be a problem if it caused conductance densities to spread infinitely, but there are biological mechanisms (apart from cooperative molecular interactions) that prevent this. (i) Conductance densities cannot become negative. One conductance density hitting zero prevents other conductance densities from continuing to rise when solution space dimensionality is low (see Fig. 8C). In other words, a lower bound is sufficient to prevent infinite spread under certain conditions. (ii) Upper bounds undoubtedly emerge from saturation of rate-limiting steps controlling the transcription, translation and/or insertion of ion channels (lines 657-659, including reference 89). With upper and lower bounds on conductance densities, the solution space is bounded regardless of its dimensionality. When the solution manifold is bounded, conductance densities cannot spread infinitely. Newly added simulations also revealed, under noisy conditions, that conductance densities drift in different preferred directions depending on regulation rates (see Fig. 8–figure supplement 1). The direction of that drift can reduce the likelihood of conductance densities ever reaching an upper bound.

In summary, we have verified that noise impacts the (stability of) solutions found by our simple homeostatic regulation mechanism. We have clarified how ion channel correlations in our model are affected. Unbounded spread is not a problem that necessitates cooperative molecular interactions. Other issues such as the initial conditions and attractiveness of the solution set (which are in fact connected) are interesting but not directly relevant to our study. We have struggled to grasp all the mathematical arguments presented in Franci et al. (2020) and were unable to implement that regulation mechanism in our model (see below), but we hope that our newly added simulations and edits to the text address concerns about Property 1.

Characteristic 2 of the model used in this paper is also non-generic. Consider the simple homeostatic parallel control scheme,

output = x+y

tau_x*dx/dt = tgt - (x+y)

tau_y*dy/dt = tgt - (x+y)

which (in line with the present paper) reaches the desired target output tgt on the 1-dimensional subspace of steady states x+y=tgt. Let's now introduce small coupling between the two variables as follows

output = x+y

tau_xdx/dt = tgt - (x+y) - epsilony

tau_ydy/dt = tgt - (x+y) - epsilonx

where epsilon>0 is small. It is easy to verify that the new model has a unique exponentially stable steady state given by

x = y; x+y= 2/(2+epsilon)*tgt ~ tgt (for epsilon sufficiently small)

Thus, introducing an arbitrary small coupling between the two regulation loops is sufficient to change the dimension of the target subspace from 1 to zero (without introducing new regulated properties!) while only leading to a small (O(epsilon)) error in the regulated property. It is also easy to show that the uncoupled/parallel model is not structurally stable, while the weakly coupled model is.

These observations lead to the question of whether the mathematical/computational results of the paper are realistic or whether they are artifacts of the non-generic modeling assumptions used for the regulation loops.

We do not understand the rationale for coupling the feedback loops. Is the motivation for doing this (i) because of experimental evidence that feedback loops are coupled, or (ii) because coupling solves some problem? We suspect it is the latter, but we will try to address each issue in turn.

(i) With respect to experimental evidence, firing rate and energy efficiency have different targets values (and different units) and the difference from target ought to be calculated separately. This relates to whether both error signals are encoded by calcium. As addressed at some length in our Discussion (see lines 332-351), we do not believe that all error signals are encoded by calcium and that feedback loops are coupled because of a common feedback signal. Even if multiple error signals are encoded by calcium, we suspect that such signals need to be functionally independent, e.g. spatially segregated and independently sensed (see lines 336-339), which would preclude the feedback loops from being coupled. We highlight evidence of other ways to encode error signals. If different error signals are encoded differently, it seems unlikely that feedback loops are coupled in the manner proposed here.

(ii ) With respect to solving some problem by coupling the feedback loops, we return to points raised above in connection with Property 1. Our main concern in this study is whether outputs can be regulated to their target value. Newly added simulations demonstrate that this occurs with uncoupled feedback loops even in the presence of noise (Fig. 8). Accordingly, we really do not see the impetus for coupling the feedback loops, especially since the experimental evidence (based on our interpretation of it) points away from this (see above).

The comment “without introducing new regulated properties” suggests that we considered additional regulated properties to stabilize the solution for property X. On the contrary, we considered additional regulated properties because we believe that neurons simultaneously regulate many properties. That regulating property Y stabilizes the solution for property X is an interesting observation, not a contrived explanation, and might obviate the need for cooperative molecular interactions (see above) if such a need exists. Insofar as uncoupled feedback loops can regulate multiple outputs, even in the presence of noise, coupling is unnecessary from our perspective and might actually compromise co-regulation. We are not starting from the assumption that the target subspace has dimension 0, and we are uncomfortable with that assumption (see above re. solutions being “too stable”). We nevertheless tried to adapt the suggested implementation, but it opened up a can of worms (see below).

If the question is ultimately whether coupling is required to enable co-regulation of multiple properties under noisy conditions, the answer is no, as now shown in Figure 8C.

Reviewer #2 (Public Review):

Yang, Shakil, Ratté, and Prescott conducted a combined dynamic clamp and modeling exploration on the geometry and dimensionality of single-output and multi-output solution sets embedded in the cellular parameter spaces of single neurons, i.e. CA1 pyramidal neurons for the dynamic clamp studies, and a generic single-compartment model with several varieties of sodium and potassium channels for the computational studies. Both types of neurons were stimulated with a randomly fluctuating current, and output measures (termed 'properties') of the neurons were measured or calculated, including rheobase, firing rate, energy consumption, and energy efficiency per spike. Ion channel maximal conductances were then varied, and the dependence of the output properties on the conductance values and their combinations were explored.

The authors define as a single-output solution set the subset of maximal conductance space containing conductance combinations that produce a value of one of the output properties within a tolerance range around a target value. These single-output solution sets can take the shape of points, curves, surfaces or volumes in parameter space. A multi-output solution set is then defined as the subset of parameter space that produces values within a tolerance range for multiple properties simultaneously, and thus lies at the intersection of several single-output solution sets (if such an intersection exists).

A major focus of the work is on the effect of channel pleiotropy - the impact of one ion channel type on more than one cellular output property - on the shape of solution sets, and whether homeostatic regulation schemes that adjust ionic membrane conductances to maintain and restore output properties in a target range can "find" the solution sets, and maintain the neuron within the solution set. The regulation schemes explored in this work directly use error signals of the output properties (the difference between an output property produced by a neuron and its target value) to increase or decrease maximal membrane constants, with pre-assigned regulation time constants.

The study is systematically executed, and results support the main conclusion, that successful regulation of n independent neuronal output properties requires that at least n ion channel densities be adjustable for a unique solution to exist, and at least n+1 for degenerate solutions. This conclusion explicitly organizes previous results obtained by other modeling studies into a coherent framework, but is not surprising.

The authors speculate that the need for neurons to regulate several of their output features may have provided the evolutionary drive for the highly diverse sets of voltage-dependencies and kinetics observed in different ion channels in nature. This speculation is intriguing, but also raises the question whether and how the unrealistically simple (and not very diverse) set of model ion channel characteristics used in this work may have impacted the extent and shape of single-property and multi-property solution sets: none of the ion channels in the model appear to have inactivation variables, and the two primarily varied ionic currents, I_Na and I_K, are identical in their voltage-dependence and activation dynamics; they differ only in their reversal potentials. It is likely that channels with such similar characteristics are more able to compensate for each other, and therefore produce more extensive and differently shaped solution sets, than more dissimilar channels.

Further exploration of the influence of solution set dimensionality on the existence and tightness of linear correlations between pairs of maximal conductances demonstrates that higher-dimensional solution sets, and larger tolerances around output property target values, lead to fewer and weaker correlations. This again is an insight that puts an organizing perspective on previous studies.

Finally, the paper provides examples of conductance regulation schemes that rely on multiple error signals (deviations of output properties from their respective target values) to differentially regulate different membrane conductances. These schemes are shown to successfully regulate neuron models and allow them to "find" solution sets in many circumstances (if solutions exist). While providing a proof-of-principle that echoes previous work by others, the biological interpretability of these regulation schemes is somewhat limited, because they can not be tied back to how the molecular machinery in a neuron would implement them. For example, it is not clear how a neuron would measure its energy efficiency per spike.

We thank the reviewer for the detailed and insightful summary of our paper. We completely agree with the shortcomings identified by the author with respect to specific molecular machinery. We kept our model deliberately simple because many details are not yet experimentally established, and it was not the goal of this study to uncover such details (which would have required very different experiments/simulations).

Author Responses

Reviewer 2 (Public Review):

This work analyzes, for the first time, changes in information flow in developing dissociated neuronal cultures using their recently developed continuous-time transfer entropy (TE) estimator. This is a timely study, since the field of network and systems neuroscience critically needs better estimators for structural, effective and/or functional connectivity. Recent technical developments allow us to track hundreds, and even thousands of neurons during development (both in vitro and in vivo) in several organisms. However, current tools to assess changes in connectivity across time are severely lacking, and this study directly tackles this problem. Their method is the state of the art and appears to be extremely well suited to this task since it is able to deal with information flow across multiple time-scales and deals with the sparsity/multiple comparisons problem with strict statistical testing.

The authors apply their transfer entropy estimator to a publicly available dataset (Wagenaar et al, 2006) consisting of multielectrode array (MEA) recordings from dissociated cortical cultures during development. The original dataset consists of over 50 cultures from 8 different batches (with different plating densities) recorded between DIV (day in vitro) 3 to 35. For this study the authors selected 4 cultures at 3-4 time points to claim that 1) Information flow undergoes a dramatic increase during development. 2) The spatial structure of information flow is “locked-in” early. 3) During bursting activity, nodes (neurons/electrodes) play a specialized role that is also “locked-in” early.

The activity of dissociated cultures is highly heterogeneous, and an appropriate sample size is needed to assess the significance of any observed features or patterns. This is well described in the original work that provided the dataset used in this study “An extremely rich repertoire of bursting patterns during the development of cortical cultures”, (Wagenaar D.A., et al, 2006, BMC Neurosci). For example, in the discussion section they state “[...] that cross-plating variability was larger than variability between sister cultures implies that it is crucial to use cultures from several different platings to obtain unbiased results.” The current study uses only 4 cultures (from 2 different batches) recorded at 4 time points (sampled around 1 week apart on average) that might belong to the original categories of “fixed-bursting” and “superbursts”. In this work, results from these 4 cultures are often reported on a case-by-case basis, and sometimes without any statistical significance assessment and with unclear summary statistics. Given that, the validity and significance of the results is difficult to assess in their current form.

We agree with the reviewer that clarifying summary statistics and statistical significance across cultures will improve the paper, and have addressed this as follows:

The new Tables III and IV in the revised manuscript contain summary statistics of the results across the different cultures, including significance tests of these summary statistics. These tables are referred to and interpreted in the main results text.

We further agree with the reviewer that the analysis will be improved by including more data.

A major strength of the TE estimator framework developed by the authors is that it can account for the statistical significance of any TE estimate. However, it is unclear how this significance test is used throughout most of the results. Figures 1a and 3 to 8 appear to consistently include points with 0 TE that have an impact on the measured quantities, like means, quartiles and correlations.

In all the analyses presented in the paper, whenever the null hypothesis of zero TE between a given source and target could not be rejected (that is, the TE estimate was not found to be statically significant), then the value of the TE between that source and target was set to zero for all subsequent analysis. It is important to still retain that zero value in analysis so as to see the overall trends in how the information flows or lack thereof change. For the means for example, if we were to remove an edge with zero TE from the mean on an earlier day, that would artificially inflate the earlier day’s mean in comparison to the mean information flow on a later day.

This step in the analysis (setting non-significant values to zero and retaining them in analysis) was strongly implied in the original submission (for instance, see line 113 of the original submission). However, it was only explicitly stated as a step in the construction of the functional networks. This was an oversight on the part of the authors. We thank the reviewer for bringing this to our attention.

We have added sentences explicitly stating that we used a value of zero whenever the TE was not significant on lines 135-137 and lines 181-183 of the revised manuscript.

Additionally, the correlation plots across days (figures 3 to 7) include least-squares fits that are often dominated by what appear to be outliers in the data (or possibly non-significant TE values). The estimates of Spearman correlation might also suffer of a similar issue due to “ties”.

We do agree that the plotted least squares fits appear at times to be dominated by outliers in the data: this is precisely the reason that we utilised Spearman instead of Pearson correlations for the quantitative analysis of the relationships here.

Further, the Spearman correlation deals naturally with ties by taking the mean rank of all tied points [1].

Regarding the “locked-in” information flow, evidence is always presented through Spearman correlations across TE scores at different days. These values are often not significant or show a weak correlation (Figures 3 and 4). An early “lock-in” of information flow would imply not only pairwise correlations, but also a long temporal correlation of a node (or edge) TE score across several days.

As above, we have provided a more systematic analysis of summary statistics / statistical significance of the trends across all experiments. To clarify the point that we are making with respect to lock in: our argument is that once the information flows are established, they are then substantially correlated with flows on later days. The early recordings in this dataset have either none or very few statistically significant information flows: without such information flows established yet in these early recordings, we’re unable to observe longer correlations of them.

We have added a brief discussion to the second last paragraph of section II E of the revised submission discussing the lack of information flows on these earlier days to be locked in.

The study of information flow within bursts is really interesting. As the authors point out, TE appears to be well poised to measure this contribution, and their burst-local TE measure appears to be equivalent to other methods that condition TE estimates on population-wide activity levels, e.g., Stetter et al, PLOS Comp Biol, 2012. In here, they analyze the correlations between the burst-local TE measures and the burst position (in time) of a node.

We thank reviewer for highlighting the work of Stetter et. al. which calculated the TE conditioned on bursting activity. As there are some similarities between that work and our burst-local TE, it is definitely worth highlighting where the similarities and differences between these approaches lie. We thank the reviewer for bringing this to our attention. We would point out, however, that Stetter et. al. extract the bursting activity and then calculate the (conditional) TE based on this bursting activity alone. By contrast, we are just extracting the contributions from the spikes that occur during bursts. The core difference comes down to how, for the burst-local TE, the non-bursting activity is still used in the estimation of log probability densities for the contributions of the spikes that occurred during bursts. In the Stetter et. al. approach, the non-bursting activity is ignored in the estimation of these densities.

We have added a brief discussion of the work of Stetter et. al. to the end of section IV H of the revised submission.

For the existence of time ordering the authors mention “[...] cultures often follow an ordered burst propagation [23, 36]”. But that does not appear to be a universal property of developing cultures. It is unclear whether the cultures used in this study show consistent temporally ordered bursting patterns. From the 2 cited references, in Maeda et al, the bursting pattern and temporal ordering changes from burst to burst (see Fig. 3). It is uncertain that an average “burst position” can be defined for any given node. Similarly, in Schroeter et al, there are several characteristic MUA patterns (Fig 4C), and even there, it might not be possible to define a consistent temporal ordering.

With regard to the burst ordering, it was not our intention to imply that there is a consistent ordering in the burst propagation. Rather, our claim is that some nodes tend to burst earlier or later on average and that this average burst location is correlated with the burst-local information flow. Indeed, in Schroeter et. al., although they do point out in Fig 4C that there are several characteristic MUA patterns, in Fig 4B they plot the average “MUA flow profile”. From that figure, it is clear that some nodes exhibit a remarkably clear tendency to spike earlier in the burst propagation than other nodes. Indeed, they then base much of their further analysis on this fact by comparing “the relative mean of peak times in the propagation chain” (that is, the mean burst position) of each node with the node’s degree in the functional network. In terms of the Wagenaar dataset, by inspecting the plots in Figs 5a and 5c of the revised and original submission, where we plot the mean burst position vs the burst-local TE, we see that there is a wide dispersion in these mean positions. This indicates that certain nodes exhibit a clear tendency to burst either later or earlier in the burst propagation.

The reviewer has highlighted to us that we have perhaps not sufficiently emphasized the fact that we are analyzing the mean burst position of what might be an inconsistent burst ordering. We thank the reviewer for bringing this to our attention.

In the abstract, we have changed “spike ordering” to “average spike ordering”. In the author summary, we have changed “burst position” to “average burst position”. We have also made changes to line 70, as well as extensive changes to section IV D and some more minor changes to the 7th paragraph of the discussion.

References

[1] Jerome L Myers, Arnold D Well, and Robert F Lorch Jr. Research design and statistical analysis. Routledge, 2013.

Author Response

Reviewer #1 (Public Review):

In Figure 1A, the authors should show TEM images of control mock treated samples to show the difference between infected and healthy tissue. Based on the data shown in Figure 1B-E that the overexpression of GFP-P in N. benthamiana leads to formation of liquid-like granules. Does this occur during virus infection? Since authors have infectious clones, can it be used to show that the virally encoded P protein in infected cells does indeed exist as liquid-like granules? If the fusion of GFP to P protein affects its function, the authors could fuse just the spGFP11 and co-infiltrate with p35S-spGFP1-10. These experiments will show that the P protein when delivered from virus does indeed form liquid-like granules in plants cells. Authors should include controls in Figure 1H to show that the interaction between P protein and ER is specific.

We agree with the reviewer and appreciate the helpful suggestion. As suggested, we added TEM images of control mock treated barley leaves. We also carried out immune-electron microscope to show the presence of BYSMV P protein in the viroplasms. Please see Figure 1–Figure supplement 1.

BYSMV is a negative-stranded RNA virus, and is strictly dependent on insect vector transmission for infecting barley plants. We have tried to fuse GFP to BYSMV P in the full-length infectious clones. Unfortunately, we could not rescue BYSMV-GFP-P into barley plants through insect transmission.

In Figure 1H, we used a PM localized membrane protein LRR84A as a negative control to show LRR84A-GS and BYSMV P could not form granules although they might associate at molecular distances. Therefore, the P granules were formed and tethered to the ER tubules. Please see Figure 1–Figure supplement 4

Data shown in Figure 2 do demonstrate that the purified P protein could undergo phase separation. Furthermore, it can recruit viral N protein and part of viral genomic RNA to P protein induced granules in vitro.

Because the full-length BYSMV RNA has 12,706 nt and is difficult to be transcribed in vitro, we cannot show whether the BYSMV genome is recruited into the droplets. We have softened the claim and state that the P-N droplets can recruit 5′ trailer of BYSMV genome as shown in Figure 3B. Please see line 22, 177 and 190.

Based on the data shown in Figure 4 using phospho-null and phospho-mimetic mutants of P protein, the authors conclude that phosphorylation inhibits P protein phase separation. It is unclear based on the experiments, why endogenous NbCK1 fails to phosphorylate GFP-P-WT and inhibit formation of liquid-like granules similar to that of GFP-P-S5D mutant? Is this due to overexpression of GFP-P-WT? To overcome this, the authors should perform these experiments as suggested above using infectious clones and these P protein mutants.

As we known, phosphorylation and dephosphorylation are reversible processes in eukaryotic cells. Therefore, as shown in Figure 5B and 6B, the GFP-PWT protein have two bands, corresponding to P74 and P72, which represent hyperphosphorylation and hypophosphorylated forms, respectively. Only overexpression of NbCK1 induced high ratio of P74 to P72 in vivo, and then abolished phase separation of BYSMV.

In Figure 5, the authors overexpress NbCK1 in N. benthamiana or use an in vitro co-purification scheme to show that NbCK1 inhibits phase separation properties of P protein. These results show that overexpression of both GFP-P and NbCK1 proteins is required to induce liquid-like granules. Does this occur during normal virus infection? During normal virus infection, P protein is produced in the plant cells and the endogenous NbCK1 will regulate the phosphorylation state of P protein. These are reasons for authors to perform some of the experiments using infectious clones. Furthermore, the authors have antibodies to P protein and this could be used to show the level of P protein that is produced during the normal infection process.

We detected the P protein existed as two phosphorylation forms in BYSMV-infected barley leaves, and λPPase treatment decreased the P44 phosphorylation form. Therefore, these results indicate that endogenous CK1 cannot phosphorylate BYSMV P completely.

Based on the data shown in Figure 6, the authors conclude that phase separated P protein state promotes replication but inhibits transcription by overexpressing P-S5A and P-S5D mutants. To directly show that the NbCK1 controlled phosphorylation state of P regulates this process, authors should knockdown/knockout NbCK1 and see if it increases P protein condensates and promote recruitment of viral proteins and genomic RNA to increase viral replication.

In our previous studies, BLAST searches showed that the N. benthamiana and barley genomes encode 14 CK1 orthologs, most of which can phosphorylated the SR region of BYSMV P. Therefore, it is difficult to make knockdown/knockout lines of all the CK1 orthologues. Accordingly, we generated a point mutant (K38R and D128N) in HvCK1.2, in which the kinase activity was abolished. Overexpression of HvCK1.2DN inhibit endogenous CK1-mediated phosphorylation of BYSMV P, indicating that HvCK1.2DN is a dominant-negative mutant.

It is important to note that both replication and transcription are required for efficient infection of negative-stranded RNA viruses. Therefore, our previous studies have revealed that both PS5A and PS5D are required for BYSMV infection. Therefore, expression of HvCK1.2DN in BYSMV vector inhibit virus infection by impairing the balance of endogenous CK1-mediated phosphorylation in BYSMV P.

Reviewer #2 (Public Review):

The manuscript by Fang et al. details the ability of the P protein from Barley yellow striate mosaic virus (BYSMV) to form phase-separated droplets both in vitro and in vivo. The authors demonstrate P droplet formation using recombinant proteins and confocal microscopy, FRAP to demonstrate fluidity, and observed droplet fusion. The authors also used an elaborate split-GFP system to demonstrate that P droplets associate with the tubulur ER network. Next, the authors demonstrate that the N protein and a short fragment of viral RNA can also partition into P droplets. Since Rhabdovirus P proteins have been shown to phase separate and form "virus factories" (see https://doi.org/10.1038/s41467-017-00102-9), the novelty from this work is the rigorous and conclusive demonstration that the P droplets only exist in the unphosphorylated form. The authors identify 5 critical serine residues in IDR2 of P protein that when hyper-phosphorylated /cannot form droplets. Next, the authors conclusively demonstrate that the host kinase CK1 is responsible for P phosphorylation using both transient assays in N. benthamiana and a co-expression assay in E. coli. These findings will likely lead to future studies identifying cellular kinases that affect phase separation of viral and cellular proteins and increases our understanding of regulation of condensate formation. Next, the authors investigated whether P droplets regulated virus replication and transcription using a minireplicon system. The minireplicon system needs to be better described as the results were seemingly conflicting. The authors also used a full-length GFP-reporter virus to test whether phase separation was critical for virus fitness in both barley and the insect vector. The authors used 1, 6-hexanediol which broadly suppresses liquid-liquid phase separation and concluded that phase separation is required for virus fitness (based on reduced virus accumulation with 1,6 HD). However, this conclusion is flawed since 1,6-hexanediol is known to cause cell toxicity and likely created a less favorable environment for virus replication, independent of P protein phase separation. These with other issues are detailed below:

1. In Figure 3B, the authors display three types of P-N droplets including uniform, N hollow, and P-N hollow droplets. The authors do not state the proportion of droplets observed or any potential significance of the three types. Finally, as "hollow" droplets are not typically observed, is there a possibility that a contaminating protein (not fluorescent) from E. coli is a resident client protein in these droplets? The protein purity was not >95% based on the SDS-PAGE gels presented in the supplementary figures. Do these abnormalities arise from the droplets being imaged in different focal planes? Unless some explanation is given for these observations, this reviewer does not see any significance in the findings pertaining to "hollow" droplets.

Thanks for your constructive suggestions. We removed the "hollow" droplets as suggested. We think that the hollow droplets might be an intermediate form of LLPS. Please see PAGE 7 and 8 of revised manuscript.

1. Pertaining to the sorting of "genomic" RNA into the P-N droplets, it is unlikely that RNA sorting is specific for BYSMV RNA. In other words, if you incubate a non-viral RNA with P-N droplets, is it sorted? The authors conclusion that genomic RNA is incorporated into droplets is misleading in a sense that a very small fragment of RNA was used. Cy5 can be incorporated into full-length genomic RNAs during in vitro transcription and would be a more suitable approach for the conclusions reached.

Thanks for your constructive suggestions. Unfortunately, we could not obtain the in vitro transcripts of the full-length genomic RNAs (12706 nucleotides). We have softened the claim and state that the P-N droplets can recruit the 5′ trailer of BYSMV genome as shown in Figure 3B. Please see line 22, 177 and 190.

According to previous studies (Ivanov, et al., 2011), the Rhabdovirus P protein can bind to nascent N moleculaes, forming a soluble N/P complex, to prevent from encapsidating cellular RNAs. Therefore, we suppose that the P-N droplets can incorporate viral genomic RNA specifically.

Reference: Ivanov I, Yabukarski F, Ruigrok RW, Jamin M. 2011. Structural insights into the rhabdovirus transcription/ replication complex. Virus Research 162:126–137. DOI: https://doi.org/10.1016/j.virusres.2011.09.025

1. In Figure 4C, it is unclear how the "views" were selected for granule counting. The methods should be better described as this reviewer would find it difficult to select fields of view in an unbiased manner. This is especially true as expression via agroinfiltration can vary between cells in agroinfiltrated regions. The methods described for granule counting and granule sizes are not suitable for publication. These should be expanded (i.e. what ImageJ tools were used?).

We agree with the reviewer that it is important to select fields of view in an unbiased manner. We selected the representative views and provided large views in the new Supplement Figures. In addition, we added new detail methods in revision. Please see Figure 4–Figure supplement 1, Figure 5–Figure supplement 1, and method (line 489-498).

1. In Figure 4F, the authors state that they expected P-S5A to only be present in the pellet fraction since it existed in the condensed state. However, WT P also forms condensates and was not found in the pellet, but rather exclusively in the supernatant. Therefore, the assumption of condensed droplets only being found in the pellet appears to be incorrect.

Many thanks for pointing this out. This method is based on a previous study (Hubstenberger et al., 2017). The centrifugation method might efficiently precipitate large granules more than small granules. As shown in Figure 4B, GFP-PS5A formed large granules, therefore GFP-PS5A mainly existed in the pellet. In contrast, GFP-PWT only existed in small granule and fusion state, thus most of GFP-PWT protein was existed in supernatant, and only little GFP-PWT protein in the pellet. These results also indicate the increased phase separation activity of GFP-PS5A compared with GFP-PWT. Please see the new Figure 4F.

Reference: Hubstenberger A, Courel M, Benard M, Souquere S, Ernoult-Lange M, Chouaib R, Yi Z, Morlot JB, Munier A, Fradet M, et al. 2017. P-Body Purification Reveals the Condensation of Repressed mRNA Regulons. Molecular Cell 68(1): 144-157 e145.

1. The authors conclude that P-S5A has enhanced phase separation based on confocal microscopy data (Fig S6A). The data presented is not convincing. Microscopy alone is difficult for comparing phase separation between two proteins. Quantitative data should be collected in the form of turbidity assays (a common assay for phase separation). If P-S5A has enhanced phase separation compared to WT, then S5A should have increased turbidity (OD600) under identical phase separation conditions. The microscopy data presented was not quantified in any way and the authors could have picked fields of view in a biased manner.

Thanks for your constructive suggestions. As suggested, turbidity assays were performed to show both GFP-PWT and GFP-PS5A had increased turbidity (OD600) compared with GFP. Please see Figure 4–Figure supplement 3.

1. The authors constructed minireplicons to determine whether mutant P proteins influence RNA replication using trans N and L proteins. However, this reviewer finds the minireplicon design confusing. How is DsRFP translated from the replicon? If a frameshift mutation was introduced into RsGFP, wouldn't this block DsRFP translation as well? Or is start/stop transcription used? Second, the use of the 2x35S promoter makes it difficult to differentiate between 35S-driven transcription and replication by L. How do you know the increased DsRFP observed with P5A is not due to increased transcription from the 35S promoter? The RT-qPCR data is also very confusing. It is not clear that panel D is only examining the transcription of RFP (I assume via start/stop transcription) whereas panel C is targeting the minireplicon.

Thank you for your questions and we are sorry for the lack of clarity regarding to the mini-replicon vectors. Here, we updated the Figure supplement 14 to show replication and transcription of BYSMV minireplicon, a negative-stranded RNA virus derivative. In addition, we insert an A after the start codon to abolish the translation of GFP mRNA, which allow us to observe phase separation of GFP-PWT, GFP-PS5A, and GFP-PS5D during virus replication. Use this system, we wanted to show the localization and phase separation of GFP-PWT, GFP-PS5A, and GFP-PS5D during replication and transcription of BYS-agMR. Please see Figure 6–Figure supplement 1.

1. Pertaining to the replication assay in Fig. 6, transcription of RFP mRNA was reduced by S5A and increased by S5D. However, the RFP translation (via Panel A microscopy) is reversed. How do you explain increased RFP mRNA transcription by S5D but very low RFP fluorescence? The data between Panels A, C, and D do not support one another.

Many thanks for pointing this out! We also noticed the interesting results that have been repeated independently. As shown the illustration of BYSMV-agMR system in Figure 6–Figure supplement 1, the relative transcriptional activities of different GFP-P mutants were calculated from the normalized RFP transcript levels relative to the gMR replicate template (RFP mRNA/gMR), because replicating minigenomes are templates for viral transcription.

Since GFP-PS5D supported decreased replication, the ratio of RFP mRNA/gMR increased although the RFP mRNA of GFP-PS5D is not increased. In addition, the foci number of GFP-PS5D is much less than GFP-PWT and GFP-PS5A, indicating mRNAs in GFP-PS5D samples may contain aberrant transcripts those cannot be translated the RFP protein. In contrast, mRNAs in GFP-PS5A samples are translated efficiently. These results were in consistent with our previous studies using the free PWT, PS5A, and PS5D.

Reference: Gao Q, et al. 2020. Casein kinase 1 regulates cytorhabdovirus replication and transcription by phosphorylating a phosphoprotein serine-rich motif. The Plant Cell 32(9): 2878-2897.

1. The authors relied on 1,6-hexanediol to suppress phase separation in both insect vectors and barley. However, the authors disregarded several publications demonstrating cellular toxicity by 1,6-hexanediol and a report that 1,6-HD impairs kinase and phosphatase activities (see below). doi: 10.1016/j.jbc.2021.100260,

We agree with the reviewer that 1, 6-hexanediol induced cellular toxicity. Therefore, we removed these results, which does not affect the main conclusion of our results.

1. The authors state that reduced accumulation of BYSMV-GFP in insects and barley under HEX treatment "indicate that phase separation is important for cross-kingdom infection of BYSMV in insect vectors and host plants." The above statement is confounded by many factors, the most obvious being that HEX treatment is most likely toxic to cells and as a result cannot support efficient virus accumulation. Also, since HEX treatment interferes with phosphorylation (see REF above) its use here should be avoided since P phase separation is regulated by phosphorylation.

We agree with the reviewer that 1, 6-hexanediol induced cellular toxicity and hereby affected infections of BYSMV and other viruses. In addition, 1, 6-hexanediol would inhibit LLPS of cellular membraneless organelles, such as P-bodies, stress granules, cajal bodies, and the nucleolus, which also affect different virus infections directly or indirectly. Therefore, we removed these results, which does not affect the main conclusion of our results.

Reviewer #3 (Public Review):

Membrane-less organelles formed through liquid-liquid phase separation (LLPS) provide spatiotemporal control of host immunity responses and other cellular processes. Viruses are obligate pathogens proliferating in host cells which lead their RNAs and proteins are more likely to be targeted by immune-related membrane-less organelles. To successfully infect and proliferate in host cells, virus need to efficiently suppressing the immune function of those immune-related membrane-less organelles. Moreover, viruses also generate exogenous membrane-less organelles/RNA granules to facilitate their proliferation. Accordingly, host cells also need to target and suppress the functions of exogenous membrane-less organelles/RNA granules generated by viruses, the underlying mechanisms of which are still mysterious.

In this study, Fang et al. investigated how plant kinase confers resistance against viruses via modulating the phosphorylation and phase separation of BYSMV P protein. They firstly characterized the phase separation feature of BYSMV P protein. They also discovered that droplets formed by P protein recruit viral RNA and other viral protein in vivo. The phase separation activity of P protein is inhibited by the phosphorylation on its intrinsically disordered region. Combined with their previous study, this study demonstrated that host casein kinase (CK1) decreases the phase separation of P protein via increasing the phosphorylation of P protein. Finally, the author claimed that the phase separation of P protein facilitates BYSMV replication but decreases its transcription. Taking together, this study uncovered the molecular mechanism of plant regulating viral proliferation via decreasing the formation of exogenous RNA granules/membraneless organelles. Overall, this paper tells an interesting story about the host immunity targeting viruses via modulating the dynamics of exogenous membraneless organelles, and uncovers the modulation of viral protein phase separation by host protein, which is a hotspot in plant immunity, and the writing is logical.

Thanks for your positive comment on our studies.

Author Response

Reviewer #1 (Public Review):

Yang, Bhoo-Pathy, Brand et al detail their investigation of a large Swedish cohort compared with age matched controls to estimate the risk of short- and long-term cardiotoxicities of breast cancer therapies in a general breast cancer patient population. They find that breast cancer patients are at significantly increased risk of developing arrhythmia and heart failure both within the first year of cancer diagnosis as well as at least 10 years after. Interestingly, they find that there is an increased risk of ischemic heart disease within the first year after diagnosis, but no increased risk of ischemic heart disease in the long term.

The authors should be commended for this large cohort study that achieves its goal of identifying the incidence and hazard ratio of cardiotoxicity associated with breast cancer treatment within a general breast cancer population. Their findings of increased risk of heart failure in patients treated with anthracyclines and trastuzumab is consistent with multiple prior studies in the field of cardio-oncology and adds to the validity of the data.

The finding that there is only a slightly increased (and statistically insignificant) risk of ischemic heart disease after left sided radiotherapy is quite interesting, and as noted by the authors, differs from prior understandings about risk of ischemic heart disease associated with breast radiation therapy. Without data on mean heart dose or total radiation administered the results are hypothesis generating, but should not be utilized to guide medical decision making.

One of the major limitations of this study is that the authors' goal is to identify the incidence and risk of cardiotoxicity associated with the various breast cancer treatment regimens and determine these risks over time, and as noted by the authors, the registry utilized only includes planned treatment not whether patients did receive this therapy (and what dose of therapy). This is a key point that should be emphasized when interpreting the results.

As noted by the reviewer, the Stockholm-Gotland Breast Cancer Register only included the intended treatment without a detailed dosage of the therapy. However, the agreement between intended and administrated treatment was about 95% in Sweden (Löfgren,L et, al BMC Public Health. 2019). We have now further explained this in the discussion section.

In Discussion: “Overall, our results indicate only small risk of heart disease due to radiotherapy in women treated in Sweden after year 2000. Further studies with detailed information on the mean heart dose of radiation or total cumulative radiation dose administered are therefore needed to confirm and provide more context to this finding.”

In Discussion: “Besides, the Stockholm-Gotland Breast Cancer Register only records intended treatment, not whether patients actually received these therapies. However, the agreement between the intended and administered breast cancer treatment in Sweden has been previously reported to be about 95% (Löfgren et al., 2019).”

There are several conclusions included in the discussion section that are not supported by the data from the results section and the authors should be careful to suggest mechanisms of cardiotoxicity from an observational population-based study. Examples include suggesting anthracyclines cause cardiotoxicity of the myocardium but not the cardiac vessels; attributing early increased risk of ischemic heart disease to emotional distress alone; and that inhibition of HER2 receptors in myocytes may explain cardiotoxicity caused by trastuzumab. These are interesting hypotheses that would be better supported by references to lab/animal model studies.

We thank the reviewer for the suggestions and have now added the reference for the suggested mechanisms of cardiotoxicity with lab/animal model studies in the discussion section.

In Discussion: “As the long-term risk was observed for heart failure but not ischemic heart disease, the cardiotoxic effect of chemotherapy might be mainly on the myocardium mediated by the effect of DNA double-strand breaks through topoisomerase (Top) 2β, but not the cardiac vessels. (Lyu et al., 2007)”

In Discussion: “The finding that risk of ischemic heart disease in breast cancer patients was only transiently elevated after diagnosis is not unexpected, considering the emotional distress of dealing with a new cancer diagnosis in the patients, which may lead to higher short-term rates of ischemic heart disease (Fang et al., 2012; Schoormans, Pedersen, Dalton, Rottmann, & van de Poll-Franse, 2016). In addition, surgery after breast cancer diagnosis might increase the risk of arterial thromboembolism (Gervaso, Dave, & Khorana, 2021), which includes myocardial infarction, and the effect appears to attenuate one year after diagnosis. (Navi et al., 2017; Navi et al., 2019).”

In Discussion: “The cardiotoxic effect of trastuzumab meanwhile may be explained by inhibition of the HER2 receptors in myocytes, that activates the mitochondrial apoptosis pathway through modulation of Bcl-xL and -xS, which regulates cell development and growth (Grazette et al., 2004; Yeh & Bickford, 2009)”

The authors succeed in highlighting the increased risk of cardiotoxicity associated with breast cancer treatment in the observed patient population. Rather than exploring the mechanism of cardiotoxicity for the treatment regimens observed, the data presented may be more useful to propose a longitudinal cardiac monitoring schedule for patients who have been treated for breast cancer, and who the current data suggest, are at long term risk for heart failure and arrhythmia.

As we found increased long-term risk of heart failure in breast cancer patients, especially for those treated with Anthracyclines +Taxanes and Trastuzumab, we therefore suggest for a prolonged longitudinal cardiac monitoring schedule for ten or more years in these treated patients. We have added the suggestion in the discussion section.

In Discussion: “Analysis by time since diagnosis revealed long-term increased risks of arrhythmia and heart failure following breast cancer diagnosis, suggesting that a longitudinal cardiac monitoring schedule might be helpful to improve cardiac health in breast cancer patients.”

Reviewer #2 (Public Review):

This is a registry based study in which patients diagnosed with locoregional breast cancer ( stage 1-111) from 2001-2008, between the ages of 25-75 were compared to a randomly sampled cohort of 10 women matched by the year of birth and for three specific cardiac conditions as outlined in the key objective. Data was gathered by cross referencing Subject's unique identification numbers in Swedish Cancer Register, Patient Register, Cause of Death, and Migration Register. Prescribed Drug Register was reviewed to gather information about prescribed medication to perhaps infer the medical comorbid conditions for which medication was prescribed. Breast cancer treatment specific information was missing in cases and presumption of use of Anti Her2 therapy was made based on HER2 neu status in some cases. While the primary objective of the study to show increased evidence primarily Heart failure and arrythmias seem to have been met in this patient registry based study, there is some question of the specificity of the data since it was gathered from the various registers and is subject to operator dependent biases.

Strengths: Study is a long term follow up of patients treated with potential cardiotoxic drugs, confirming the previously known association of specific heart disease to the use of these drugs. Longest follow up seems to be for 16 yrs for the earliest cohort of 2001 and minimum approximately 10 yrs for the cohort of 2008. This study does confirm that long term risk that remains even after the treatment is completed and potentially suggests that more robust cardiac function monitoring guidelines for survivors may be warranted.

Weaknesses: This is a patient register based study. As outlined above, data was extracted by cross referencing various patient registers. Since the data was dependent on the ICD codes entered in the patient register, there seems to be potential for missed information.

The Swedish Patient Register has quite high validity for the heart diseases analyzed in this study, with a positive predictive value between 88%-98%, by using the main diagnosis in the register. However, it is still possible that we have missed some information for heart disease and we have emphasized this limitation in the discussion section.

In discussion: “The Swedish Patient Register has high validity for heart failure, arrhythmia and ischemic heart disease (with positive predictive value between 88%-98%) (Hammar et al., 2001; Ludvigsson et al., 2011), by analysing main diagnoses only. However, misclassification of heart diseases may still have occurred.”

Preexisting comorbidities were also extracted through Patient Registers hence may be subject to same potential for missed information.

The Swedish Patient Register has relatively high validity for the majority of comorbid diseases. However, patients without severe symptoms of the diseases might be treated in the primary health care centers, which were not included in the patient register. We have therefore pointed out this limitation in the discussion section.

In discussion: “In addition, preexisting comorbidities extracted from the patient registers may not include those patients with slight symptoms.”

In addition, information for use of Trastuzumab was extrapolated from the Her2neu status of the patient when such information may not have been accessible through Prescribed Drug Registers.

As the majority of HER-2 positive patients were treated in the clinics, the Swedish Prescribed Drug Register does not register their information. Because ~90% of HER-2 positive cancers were treated with trastuzumab between 2005 and 2008 in the Stockholm-Gotland region, we therefore used HER-2 positivity as a proxy for trastuzumab treatment. We have now further explained this in the methods section.

In Materials and Methods: “As ~90% of HER-2 positive cancers were treated with trastuzumab between 2005 and 2008 in the Stockholm-Gotland region and the Swedish Prescribed Drug Register does not cover data on treatment with trastuzumab, HER-2 positivity was used as a proxy when no registry data on trastuzumab was available during this time period (30% of the HER-2 positive patients had missing information on trastuzumab).

It is also unclear if there was any protocol in place for cardiac monitoring for patients receiving cardiotoxic chemotherapy or Anti Her2neu agents.

In Sweden, there is no cardiac monitoring for chemotherapy in routine clinical practice. For HER2-therapy, cardiac monitoring with a thorough cardiac assessment prior to treatment, including history, physical examination, and determination of left ventricular ejection fraction before, during and right after treatment has been mandatory since introduction in clinical routine. We have now added this information to the discussion.

In discussion: “As there is no cardiac monitoring for chemotherapy in routine clinical practice and cardiac assessment is only performed prior to and during the treatment period for HER-2 positive patients in Sweden, a longer-term cardiac monitoring program might be helpful for these patients.”

Reviewer #3 (Public Review):

This matched analysis uses data from patients newly diagnosed with breast cancer the Stockholm-Gotland Breast Cancer Register and data from patients in the general female population in Sweden to ask the question of whether breast cancer diagnosis (and subsequent treatments of breast cancer) is associated with an increased rate of heart disease after treatment. It is impossible to answer this question in a randomized controlled setting and would be unethical to randomize patients to not be treated for their cancer, thus a matched approach in theory would seem to make sense at face value. However, I have some concerns about the analysis that I believe impede their answering the research aims.

1. With regard to the matched analysis of time to heart disease diagnosis, I have several critiques/questions. First, for the breast cancer cohort, were patients with a diagnosis of heart disease prior to cancer diagnosis included in the analysis? If so, how was the event (which precedes time = 0) incorporated into the analysis? If not, please make sure to make note of this important restriction. I think the latter approach is the better / correct.

As suggested by Referee 3, we have now excluded those patients with a diagnosis of heart disease prior to cancer diagnosis. We have updated the results and the methods section accordingly.

In Materials and Methods:

“We included all patients diagnosed with non-metastatic breast cancer (stages I-III) and without prior diagnosis of heart disease at age 25 to 75 years (N = 8015).”

Second, for the matched cohort, what is time = 0 for these persons? i.e. how does one interpret "Time since diagnosis" on Figure 1 for a patient who has not been diagnosed with breast cancer?

We apologize for this misunderstanding and have revised it to “Time since index date (= date of diagnosis, which is the same date for corresponding matched individual from the general population) ” in Figure 1.

Third, how was the matching incorporated into the FPM? Presumably there should be a frailty term of some sort to indicate the matched groups, within which there is expected to be correlation.

In the flexible parametric survival model for matched cohort data, a shared frailty term was incorporated into the model to indicate the matched cluster. The maximum (penalized) marginal likelihood method is used to estimate the regression coefficients and the variance for the frailty. We have added this explanation in the methods part.

In Materials and Methods: “Considering the correlation within the matched clusters, a shared frailty term (as random effects) was incorporated into the model and the maximum (penalized) marginal likelihood method was used to estimate the regression coefficients and the variance for the frailty.”

1. It is noted that Kaplan Meier curves were used to estimate the cumulative incidence of heart disease. How was death of the patient prior to diagnosis of heart disease handled? I do not think that Kaplan Meier is the correct approach here but rather a Aaalen-Johansen-type estimator that treats death as a competing event. See e.g. https://pubmed.ncbi.nlm.nih.gov/10204198/ A Kaplan Meier will tend to overestimate the event rate when competing events are counted as censoring.

As suggested by the reviewer, we have now used the Aalen-Johansen method to estimate the cumulative incidence of heart disease and revised the text in the Methods, as well as the tables and figures in the supplement.

In Materials and Methods,: “Aalen-Johansen estimation was used to assess the cumulative incidences of heart diseases in breast cancer patients and matched reference individuals, while other causes of death were considered as competing events.”

1. The sentence "Missing indicators were included for the analysis of these covariates in the model" and the results in Table 3 suggest that some missing values were analyzed 'as is', meaning that missingness was used as a category itself. This of course is not desirable and there exists methodology+software for more appropriately handling these data, e.g. multiple imputation with chained equations. For example, how does one interpret that 'unknown chemotherapy' status is positively associated with heart failure but less so than anthracycline based chemo.

Missingness of the type of adjuvant treatment was considered as a category in the previous version of our manuscript. To address potential biases resulting from missing data, we have now used multiple imputation with chained equations and revised the methods and Table 3 accordingly.

In Materials and Methods: “Multiple imputation with chained equations was used to deal with the treatment categories with missing information. We replaced the missing data with 10 rounds of imputations and all the covariates were included in the imputation model.”

1. The reported HRs at the top of page 10 seem incongruous with the FPM model demonstrated in Figure 1, since there is clearly a non-linear relationship between the hazard and the outcome. In other words, there is little sense in which the hazards are proportional at all time points.

As shown in the FPM model in Fig. 1, HRs were not constant according to time since index date. Therefore, in the revised version, we only showed the HRs separately in <1, 1-2, 2-5, 5-10 and 10-17 years after diagnosis. We have revised the abstract, methods, and Table 2.

In Abstract: “Time-dependent analyses revealed long-term increased risks of arrhythmia and heart failure following breast cancer diagnosis. Hazard ratios (HRs) within the first year of diagnosis were 2.14 (95% CI = 1.63-2.81) for arrhythmia and 2.71 (95% CI = 1.70-4.33) for heart failure. HR more than 10 years following diagnosis was 1.42 (95% CI = 1.21-1.67) for arrhythmia and 1.28 (95% CI = 1.03-1.59) for heart failure. The risk for ischemic heart disease was significantly increased only during the first year after diagnosis (HR=1.45, 95% CI = 1.03-2.04).”

In Materials and Methods: “We compared the risk of heart diseases in breast cancer patients with that observed in the matched cohort, using flexible parametric model (FPM) with time since index date as underlying time scale.”

In Results: “A short-term increase in risks of arrhythmia and heart failure was found in breast cancer patients (Table 2, Figure 1, HR at first year for arrhythmia= 2.14; 95% CI = 1.63-2.81, for heart failure =2.71; 95% CI = 1.70-4.33, respectively).”

1. It seems unlikely that breast cancer diagnosis could ever be 'protective' for ischemic heart disease. A more constrained model that does not allow for the possibility of HR < 1 could provide a more sensible estimate of this time-dependent HR.

To the best of our knowledge, the inverse association between breast cancer and the long-term risk of ischemic heart disease is possible considering that some of the reproductive risk factors for breast cancer have protective effect on the risk of ischemic heart disease. We have now discussed about this in Discussion.

In Discussion: “The long term lower risk of ischemic heart disease in breast cancer patients compared to age-matched women might be explained by the opposite role of reproductive factors in breast cancer and ischemic heart disease. Women with younger age at menarche and older age at menopause were associated with increased risk of breast cancer, while decreased risk of ischemic heart disease were found among these women (Collaborative Group on Hormonal Factors in Breast, 2012; Okoth et al., 2020).”

Author Response

Reviewer #1 (Public Review):

Lopez and Wingreen proposes the idea of noise-averaging cooperation (NAC), or within-population cross-feeding driven by noisy metabolism in microbes. The authors reasoned that since microbes are small, they are prone to noisy metabolism which limits growth rate. If related bacteria can share metabolites to average out noise (e.g in biofilm), then population growth rate can be improved and sometimes, the irreversible growth arrest of individuals can be prevented in theory. The authors predict substantial noise-driven growth inefficiencies from single-cell protein abundance data, review evidence for NAC, and propose how to detect NAC in microbial populations.

Although this paper would be greatly strengthened by experimental tests (some of which may not be too difficult to do), I did enjoy reading it, and the writing is clear and thoughtful. The problem of "cheaters" (cells that take metabolites but do not leak any) will naturally arise, although the problem is mitigated in biofilms. Discussions on that will be useful.

We agree that the issue of “cheaters” deserves additional attention in the manuscript. To this end, we have augmented our discussion of NAC’s evolutionary stability to include a discussion of the existing literature on the evolution of cooperation. We now situate NAC and the results of our biofilm model in this larger context. We note that our spatial model results show that the benefits of NAC can be “privatized” among cooperators, a key requirement for the evolution of cooperation.

Author Response

Reviewer #1 (Public Review):

Oxenford and colleagues outline the basic principles of a new software tool which they developed to combine the documentation and correlation of various data sets relevant for the implantation and the control of the location of deep brain stimulation electrodes . The concept behind their Lead-OR tool is a logical extension of a software tool which they have developed earlier - the Lead-DBS package.

Multimodal data representation undoubtedly will be a step forward. It is of particular relevance that the toolbox which is shown will be made openly available by open-source platforms.

The introduction of this new tool holds great promise for future research. In particular, the use of this tool might result in a more uniform recording of the correlation of neurophysiological findings with the exact location of deep brain stimulation electrodes and ultimately of clinical outcome. A great advantage of this new Software is also ist flexibility with the option to include other sources as well like new atlases and anatomical data.

The conclusions of this paper are well supported by the data which is shown. In particular the figures nicely support the claims made in the manuscript. The clinical series of 52 patients with Parkinson disease gives an example how the new software can be used. Nevertheless, it will be necessary to demonstrate the feasibility of the tool in future clinical studies.

The software will also be useful when applying segmented leads. The authors could expand on this subject. It is certainly a disadvantage of the current software that recordings of local field potential cannot be incorporated yet. At least this should be possible post hoc.

The discussion touches upon many controversial topics and ambiguous Scenarios but it is overall well balanced. The limitations of the study are outlined very openly.

We would like to thank the reviewer for this accurate summary and their positive words about our manuscript.

Reviewer #2 (Public Review):

Oxenford et. al., describe a novel open-source DBS visualization software package, Lead-OR that aims to fill a gap in the intraoperative visualization of DBS trajectories. While theirs is certainly not the first nor only attempt at achieving this, the described software is unique in combining an open-source approach with integration of multimodality data including integration with the most commonly used planning and microelectrode recording platforms. Their software has the potential to take intraoperative DBS visualization to the next level by combining patient-specific imaging with intraoperative electrophysiology and new normalization tools to incorporate external atlases. While some may find this approach unnecessary given the trend towards decreased reliance on MER in DBS for movement disorders, the tools described will still be useful for retrospective and research analyses. The true potential of LeadOR lies in its future potential as integration across platforms grows and other developers add to its capabilities over time.

We would like to thank the reviewer for this accurate summary and the positive evaluation of our manuscript.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors investigated that vaccine which is designated RNA replicons delivered by lipid inorganic nanoparticles (LION) exhibited the protective immune response against SARS-CoV2 variants by heterologous challenging. They also provide the evidence its significant efficacy to assess pathological analysis in the lung using hamster model. However, this study presented descriptive data with a few mechanistic studies in the immune response. Concerns with the manuscript are related to data describing the relevant of protective effects in vivo and the data supporting the interpretation of vaccination efficacy against multiple SARS-CoV2 strains.

Specific concerns In previous study (Erasmus et al, 2020a), the authors developed a novel vaccine and demonstrated that this novel vaccine harboring an alphavirus-derived repRNA induced antibody production responses in mice and macaques. In this manuscript, the authors demonstrated that this novel vaccine harboring SARS-CoV2 variant derived repRNA with pre-fusion type has significant cross-neutralization activity and protective immunity against SARS-CoV2 variant.

1. The antibodies which are produced after immunization by repRNA expressing pre-fusion stabilized spike protein/LION can bind to S1 or S2 or RBD? Please define the reactivity of antibodies and also compare to those from native form.

We thank the reviewer for this suggestion, we have updated figure 2 of the manuscript with this additional data.

1. The authors demonstrated that this novel vaccine has significant efficacy with heterologous neutralizing activities. Please provide some evidence for reasons. F.i. this novel vaccine (with pre-fusion type) can induce the production of cross-reactive antibodies against SARS-CoV variant? And also it would be better to define the epitopes of these antibodies.

We propose/postulate the cross-protective efficacy is due to cross-reactive neutralizing antibodies as shown in figure 3. Although in some combinations of vaccine vs challenge the neutralizing titers are diminished. Additionally, thanks to your suggestion to characterize within S domain-binding antibodies, we also noted that the apparent increase in breadth of the B.1.1.7 vaccine did appear to correlate with this vaccine’s ability to drive higher S1-binding antibody responses relative to the A.1 vaccine.

1. In the hamster model, this novel vaccination showed the significant protective effects on lung pathology. Please provide some data that a novel vaccination induce T cell responses in hamster by the frequency of antigen specific CD4 or CD8 T cell and cytokines.

We chose to focus on neutralizing antibodies as these appear to be the primary correlate of protection against disease (https://www.nature.com/articles/s41591-021-01377-8). In this study, we therefore did not collect samples to measure T-cell responses to the vaccine. However, we have shown induction of T-cell responses in mice and non-human primates receiving the A.1-targeted vaccine (https://pubmed.ncbi.nlm.nih.gov/32690628/), suggesting T-cell responses may have been induced in hamsters. We have included an updated discussion section with discussion on this limitation of our study.

Minor concerns Miss-labeling in Figure 5, B, D, F in the manuscript. Please correct it.

We thank the reviewer for catching this error and have corrected the text in the manuscript.

Reviewer #2 (Public Review):

This paper aims to develop second-generation vaccines that protect against multiple SARS-CoV-2 variants of concern. For this purpose, the authors developed new vaccine candidates composed of SARS-CoV-2 spike protein derived from B.1.1.7 (alpha) and B.1.351 (beta) variants. The essential backbone of the vaccines they used contains alphavirus-derived sequences to be self-amplifying, and one containing spike protein of the Wuhan strain is already in clinical trials. They demonstrated no significant difference in virus removal and pathogenesis in the lower respiratory tract. However, the titer of in vitro neutralizing activity and virus removal ability in the upper respiratory tract were decreased against the strains different from the vaccine strain.

Overall, their data are convincing and valuable as a platform for a new vaccine against SARS-CoV-2 VoC in the future. Besides, I have some comments to strengthen their argument.

1) The challenge experiments in Figure 4, Figure 5, Figure 6, and Figure 7 lack data on infection protection against B.1.617.2 (delta strain). It is better to add B.1.617.2 to the challenge experiments and neutralizing assay in Figure 3. The addition of data against B.1.1.529 (Omicron) is ideal.

We appreciate the reviewer’s suggestion. However, these studies were completed prior to having a working B.1.617.2-stock which was difficult to achieve due to mutations arising in tissue culture. Nevertheless, we believe the neutralizing titers achieved against B.1.617.2 in figure 3 would suggest significant efficacy against B.1.617.2 infection. We found neutralizing titers against B.1.617.2 by the three vaccines were similar or greater than seen against B.1.351, a VoC for which we still saw near complete protection. Additionally, the complete replacement of the B.1.617.2 VoC with B.1.1.529 now makes further testing against B.1.617.2 of limited benefit. Efficacy testing against the B.1.1.529 VoC is still ongoing.

2) There are no data on T cell responses to vaccines, even in mice. If their vaccine can also induce T-cell responses, it would be more attractive. At least, it would be better to discuss the potential contribution of T-cell responses since alphavirus-based replicating RNA vaccines could be one of the nice vaccine platforms to elicit T-cell responses, according to previous works. (For example, McKay PF et al., Nat Commun. 2020 Jul 9;11(1):3523.)

As mentioned in response to reviewer 1, we chose to focus on neutralizing antibodies as these appear to be the primary correlate of protection against disease (https://www.nature.com/articles/s41591-021-01377-8). We agree that data on T-cell responses would be helpful but we did not collect samples to evaluate T-cell responses during the course of the studies presented here. We have shown induction of T-cell responses in mice and non-human primates receiving the A.1-targeted vaccine (https://pubmed.ncbi.nlm.nih.gov/32690628/). We have included an updated discussion section with discussion on this limitation of our study.

Author Response

Reviewer #1 (Public Review):

The authors use ribosome profiling (RiboSeq) and RNA sequencing (RNASeq) to characterise the transcriptome and translatome of two PRRSV species as well as the host in response to infection. One particularly exciting feature of the study is that the analysis is carried out at different times of infection, which shows how both the virus and the host regulate their gene expression. The authors identify several new regulatory mechanisms of virus gene expression. Unexpectedly, they also find that the frameshifting efficiency at the ORF1ab frameshifting site changes with time. This contradicts the dogma in the field, which states that frameshifting is constant and has evolved to be constant to produce the a particular ratio of the two protein isoforms. The strength of the paper is in its comprehensible analysis. The paper is extremely rich in data, with 12 main and 23 Supplemental Figs and 11 Supplemental Tables, all of them rather complex. The main weakness is that it is written in a technical language that will be hardly readable by a non-specialist readership. Unfortunately, the authors do not make a good job in guiding the reader through their findings and hardly identify the the most important findings, while leaving the details to the specialists. This is particularly exemplified in Fig. 12, which should present the summary of the findings and would be extremely helpful, but hardly provides any text at all. This is potentially a very interesting paper, but the impact on the field could be increased considerably by better presentation of the work.

We would like to thank this reviewer for the positive comments about the scientific findings, and for their suggestions for improving the presentation of the work. This outside perspective was very useful in helping us see which parts of the paper required clearer explanation or less detail, which can be hard to discern when very close to the work. We have incorporated all of this reviewer’s suggestions and we think this has improved the manuscript and made it easier to follow.

Reviewer #2 (Public Review):

The authors used the ribosome profiling technique to study gene expression at transcriptional and translational levels in the cells infected with porcine reproductive and respiratory syndrome virus (PRRSV-1 and PRRSV-2) using ribosome profiling. The ribosome profiling was carried out on the cells at different time points within the first 12 hours of infection, thus providing information on gene expression changes during the time of infection.

The analysis of ribosome profiling data is exceptionally detailed and includes scrupulous characterization of footprint read lengths, de novo prediction of translated ORFs, characterisation of local pauses and differential gene expression of host and viral genes. The RNA-seq analysis is on par with that, the authors did a superb job at characterising the composition of the viral transcriptome that included identification of heteroclite RNAs and defective interfering RNAs. This provided the authors with reliable information for the interpretation of translational mechanisms responsible for the translation of ORFs discovered with ribosome profiling data.

A specific focus of the manuscript was placed on the characterisation of two instances of ribosomal frameshifting occurring in PRRSVs. In addition to "canonical" -1 frameshifting at a slippery sequence stimulated by downstream RNA secondary structure (common to many viruses), PRRSVs genome contains an additional frameshifting site whose efficiency is stimulated by a viral protein. The authors demonstrated that the efficiency of this frameshifting is increasing over time which is expected since the concentration of stimulating protein is increasing. Furthermore, the authors found that the efficiency of "canonical" frameshifting is also changed. The authors describe this as surprising since it directly contradicts the common description of its function as "setting the fixed ratio" between the synthesized products upstream and downstream of the frameshift site. Perhaps it is not so surprising in the hindsight, given that the frameshifting is dependent on so many different factors, folding states of RNA pseudoknots which are dynamic, ribosome density upstream, etc. it would be more surprising if the efficiency of frameshifting were indeed fixed. I think the "fixed ratio" was proposed mainly to draw a difference to ribosomal frameshifting occurring in cellular genes (like antizyme or bacterial release factor 2) where there seems to be only one functional product, but its synthesis level depends on the efficiency of frameshifting sensing certain conditions. It is great though that the authors observed such changes and I agree with the authors' speculations that this is unlikely to be unique to PRRSVs.

While I found the work to be largely descriptive, the authors did not shy away from speculating about potential mechanisms responsible for observed regulation. The manuscript is hard to get through simply due to its large length and a lot of data, but reading it is rewarding.

Again, we would like to thank this reviewer for their positive comments about the work, and to reiterate that hopefully the revised version of the manuscript will be easier to read.

Reviewer #3 (Public Review):

The manuscript by Cook et al. describes the first comprehensive gene expression analysis of two species of PRRSV, an important agricultural pathogen. Using ribosome profiling and RNA-sequencing, the authors systematically analyze the transcriptome of the virus and its translation, and their temporal kinetics. The analysis revealed non-canonical RNA species that are suggested to contribute to translation of parts of ORF1ab, changing the stoichiometry between the NSPs. In addition, the authors use the ribosome profiling data to identify novel overlapping ORFs, including a conserved uORF in the 5' leader, and to analyze the efficiency of frame-shift in two sites in the viral genome, one of which is trans-regulated by the viral nsp1β. The frame-shift efficiency in both sites is presented to be increasing late in infection. The authors also present conservation analysis from hundreds of available genomes. Finally, analysis of host gene expression uncovers a pattern suggesting translation inhibition of induced transcripts, and by comparing a WT virus to a mutant virus lacking the nsp2 site frame-shift, the authors identify a gene (TXNIP) whose expression is affected by nsp2TF.

In this rigorous work, the authors uncover new insights on an important pathogen, which can be of value to the wider field of virology. However, due to technical issues a few of the authors claims may require reconsideration.

We are grateful to this reviewer for their comments on the rigour and the impact of the work, as well as the suggestions for improvement which they included in their more detailed review. Within the detailed review, this reviewer expressed some concerns that ribosome run-off (seen in Figure 1—figure supplement 1 [formerly Supplementary Figure 1]) might confound the comparison of ribosome densities in different regions of the viral genome (particularly ORF1ab). However, this run-off only noticeably affects the first ~100 nt of host CDSs, which is very small compared to the ~12,000 nt total length of ORF1ab. The regions of ORF1ab in which we compare ribosome density in our study are almost all > 1,000 nt downstream of this ~100 nt run-off region and will therefore not be significantly affected by run-off. The exception to this is our assessment of heteroclite sgRNA translation, where the “heteroclite” region does include the first ~100 nt of ORF1a. As such, run-off may have a slight effect on this analysis, but we expect this to be minor, as the ~100 nt run-off region represents only a small proportion of the 1,550-nt “heteroclite” region. Further, any such effect would actually lead to under-estimation of heteroclite sgRNA translation, by artefactually reducing the relative RPF density in the heteroclite region. This would therefore strengthen our conclusion that our data provide evidence for heteroclite sgRNA translation.

Author Response

Reviewer #2 (Public Review):

Romand et al investigates the role of hyperphosphorylated guanosine nucleotides (ppGpp) in acclimation of plant chloroplasts to nitrogen limitation. The signaling role of ppGpp as alarmone is well established in the stringent response of bacteria. The stringent response allows bacteria to adapt to amino acid or carbon starvation and other acute abiotic stress conditions by downregulation of resource-consuming cell processes. A series of studies, including the current one, have demonstrated the retention of the bacterial-type ppGpp-mediated signaling response in plant and algal chloroplasts. The current study convincingly demonstrates the involvement of ppGpp in remodeling of photosynthetic machinery under nitrogen limitation. Using three Arabidopsis RSH lines (two underaccumulators and one overaccumulator of ppGpp), the authors show that the ppGpp is required for preventing excess ROS accumulation, oxidative stress and death of cotyledons under nitrogen limiting condition. The authors show a transient accumulation in ppGpp upon nitrogen limitation, which is followed by a sustained increase in the ratio of ppGpp to GTP. There is a prompt decline in maximum photochemical efficiency of photosystem II (PSII) and linear electron transport under nitrogen deficiency in wild type and ppGpp overaccumulator plants. However, mutants with low amount of ppGpp have a delayed decrease in these photosynthetic parameters. PpGpp is further shown to decrease (or degrade) photosynthetic proteins, and a remodeling of PSII that involves uncoupling of LHC II from the reaction center core has been suggested to occur under nitrogen starvation. The authors also show a ppGpp-mediated downregulation of chloroplast gene transcription and a coordinated plastid-nuclear gene expression under nitrogen deficiency.

Strengths 1. The conclusions of this paper are mostly well supported by data. With three different RSH lines, there is a convincing demonstration of the specific involvement of ppGpp in nutrient acclimation. The line carrying conditional overexpression of Drosophila ppGpp hydrolase (MESH) nicely complements the RSH lines and strengthens many of the conclusions. This is a detailed analysis of ppGpp function in a plant species. The data supplement accompanying each main figure is extensive and helpful. 2. The genomic analysis in nitrogen replete and deplete wild type uncovers an interesting regulation of RSH enzymes at the transcriptional level. This is likely to be part of a signaling response that works in conjunction with allosteric modulation of RSH activity under nitrogen limitation. 3. The large-scale analysis of plastid and nuclear gene transcripts supports the involvement of ppGpp in coordinated repression of plastid and nuclear gene transcription. 4. By the inclusion of mitochondrial genes and proteins in their analysis, the authors clearly show that the ppGpp action is limited to plastids and does not extend to mitochondria, which like chloroplasts, have a bacterial ancestry. 5. The thorough demonstration of the involvement of ppGpp in low nitrogen acclimation of photosynthetic metabolism adds greatly to the understanding of plant abiotic stress tolerance mechanisms and ppGpp function in both plants and bacteria.

We thank the reviewer for these observations on our work.

Weaknesses: 1. With two earlier reports from a different laboratory (Maekawa et al 2015 and Honoki et al 2018) showing the involvement of ppGpp in acclimation to nitrogen deficiency, the novelty of the current study is diminished. The authors mention that the double mutant (rsh2 rsh3) used by Honoki et al does not show a clear phenotype other than a delay in Rubisco degradation. It is not clear to me why the lack of two major RSH isoforms, involved in synthesis of ppGpp under light, would not produce any phenotype. This discrepancy should be discussed further in the manuscript.

The work of Maekawa et al., 2015 and Honoki et al., 2018 was indeed important for highlighting the potential involvement of ppGpp in the acclimation to nitrogen deficiency. However, these studies were based on the constitutive overaccumulation of ppGpp. Here, we demonstrate a physiological requirement for ppGpp signalling by the plant to allow acclimation to an abiotic stress- we consider this to be a major step forwards in understanding the role of ppGpp in plants, and one of the few examples of a physiological requirement for ppGpp in plants.

We mention the use of an RSH2 RSH3 mutant by Honoki et al. 2018 while putting our results into the context of previous findings in the discussion. We bring the attention of the reviewer to our analysis of an RSH2 RSH3 mutant in this study, and that in our hands the mutant phenotype was indistinguishable from the RSH quadruple mutant (rshQM) (Figure 2- figure supplement 1 panel B). Therefore, we do indeed consider that RSH2 and RSH3 are the main RSH isoforms involved in ppGpp-mediated acclimation to nitrogen deficiency, and we state this ( see p7 l161-164 in original manuscript). As we explain in the discussion there are probably technical reasons for the discrepancy with the results reported by Honoki et al. 2018. We also note here that the RSH2 RSH3 mutants used in our study and by Honoki et al. 2018 are not identical: the same SAIL insertion SAIL_305_B12 was used for rsh2, while the rsh3 allele used by Honoki was the GABIkat insertion GABI129D02 and here SAIL_99_G05). We now add this difference in the genetic identity of the mutants as an additional potential explanation for the different findings in the two studies.

1. The authors at times show a tendency to overinterpret their results. A ppGpp-mediated repression of chloroplast transcription and translation is sufficient to explain most of the observations in this study. However, the authors seem to go beyond this simple explanatory framework by invoking specific roles for ppGpp in remodeling of PSII antenna-core interaction and in blocking of PSII reaction center repair. There is no data in the manuscript in support of these two propositions. A coordinated decrease in synthesis of most chloroplast proteins, including the D1 reaction center protein of PSII, is sufficient to explain the decrease in Fv/Fm. There is no evidence in the manuscript for "photoinactivation gaining an upper hand via ppGpp-mediated signaling"

The circuit breaker analogy of PSII photoinhibition that the authors discuss in support is just an interpretation. The remodeling of PSII antenna-core interaction, likewise, could be a simple consequence of the ppGpp-mediated decrease in D1 protein synthesis. The high antenna-core ratio under nitrogen starvation likely reflects the lag in the decrease of LHCB1 (which eventually decreases significantly by day 16).

Since ppGpp-signaling primarily affects plastid transcription and translation, there is a rapid decrease in plastid psbA gene product (D1) relative to the nuclear-encoded LHCB1. The unconnected LHCII might simply be a result of the mismatch in antenna-core stoichiometry rather than an active regulation of PSII functional assembly by ppGpp.

We have re-worked the discussion to make these points more clearly, and also to tone down certain points where we may have over-stretched our interpretation.

We think that our interpretation is essentially the same as the reviewer’s- the ppGpp mediated inhibition of chloroplast translation and transcription is sufficient to explain the majority of our results. In the discussion we also discuss the possibility that ppGpp stimulates the active degradation of some chloroplast proteins, and put this in context of studies showing that N-starvation activates the specific proteolysis of certain photosynthetic proteins in Chlamydomonas and has an effect on the half lives of different chloroplast proteins in plants. We do not propose or present data suggesting that ppGpp has any other specific targets/effectors- for example within the PSII repair cycle or in remodelling PSII stoichiometry- although we also cannot exclude the possibility of targets in these processes.

We think that the ppGpp dependent change in PSII stoichiometry during N-starvation is not just a side effect of a general downregulation or a temporary mismatch as suggested- but due to its size, persistence and effect on photosynthesis is likely to be part of the acclimation process. For example, the ppGpp-dependent drop in Fv/Fm is maintained at day 16 and even beyond (Fig 2D). We also see that photosynthetic proteins are still degraded in low ppGpp mutants (Fig. 3A), but that the high Fv/Fm is maintained throughout. These points and the fact that the alteration of PSII stoichiometry is not caused by the direct action of ppGpp on PSII (but via transcription/translation) does not mean that it is not important or does not play a role in acclimation. Other studies report that PSII RC inactivation can protect PSI (e.g. Tikkanen et al. 2014) and ppGpp may be working in a similar fashion here by reducing the flow of energy into the photosynthetic electron transport chain. This interpretation is consistent with our results showing that wild-type plants and high ppGpp plants (rsh1-1) accumulate less ROS and ROS-related damage than plants defective in ppGpp biosynthesis (Fig. 1).

1. The work is mostly descriptive of the involvement of ppGpp in low nitrogen tolerance without any data on how the nitrogen deficiency is sensed by the RSH enzymes and how ppGpp orchestrates the multi-faceted acclimatory response. Perhaps, these aspects are beyond scope of the current manuscript, but they could be discussed more.

We agree that these are very important questions, and also that they are out of the scope of the current work. We think that our work goes beyond the descriptive by demonstrating the physiological functions of ppGpp-signalling during nitrogen deficiency and a framework for how it occurs (i.e downregulation of chloroplast function and avoidance of excess oxidative stress).

Reviewer #3 (Public Review):

The manuscript by Romand et al. explores the role of guanosine penta- and tetraphosphate, ppGpp, in the acclimation of plants to nitrogen limitation. It shows that an early and transient ppGpp accumulation - and a controlled ppGpp/GTP ratio - is necessary for a proper acclimation of plants to such stress. The pathway is shown to act on remodeling the photosynthetic machinery and downregulating photosynthesis during stress, thus limiting ROS damage to the plants. This regulation most likely takes place by affecting chloroplast transcription, maintaining the balance between nucleus- and chloroplast-encoded proteins.

The manuscript proposes a thorough analysis of the ppGpp-induced response including extensive wild type and mutant analyses at the gene and protein expression level as well as at the physiological level under nitrogen limitation together with heterologous expression of ppGpp hydrolase from Drosophila. The conclusions are carefully backed by the data (but for the lack of gene expression analysis in the high ppGpp line, rsh1-1), the figures and text clear, well-written and easy to follow. Altogether it represents a solid new step in improving the comprehension of plant response to nitrogen limitation, as well as on the role of ppGpp in plants and possibly throughout the green lineage. An alternative hypothesis to ppGpp photoprotective role could be discussed in that photoprotection may be an indirect effect due to photosynthetic protein degradation enabled by ppGpp, possibly through modulation of ppGpp/GTP ratio affecting chloroplast protease activity.

On this last point we agree with the reviewer- our data indicates that the photoprotective role of ppGpp is via the ppGpp-dependent control of the abundance of photosynthetic proteins. This is indirect in the sense that we have no evidence that ppGpp itself interacts with components of the photosynthetic machinery. However, as discussed below we do not think that photoprotection is just a side-effect of ppGpp’s action- we show that the capacity to synthetise ppGpp is required for avoiding the generation of ROS and tissue death.

Author Response

Reviewer #1 (Public Review):

In this paper, the authors examine the role of feedback from primary visual cortex (V1) to the dorsolateral geniculate nucleus of the thalamus (dLGN) under a variety of visual stimulus conditions. This is a well-defined circuit originating from a specific population of Layer 6 cells in the cortex, and the authors test the role of this projection by recording in dLGN during silencing of V1 via ChR2 expression in PV inhibitory cells. This is a well-established technique for strong silencing of cortex. However, because there are other disynaptic pathways from V1 to thalamus, they also perform a similar set of experiments using more targeted optogenetic inhibition of a genetically-defined class of Layer 6 (NTSR1) cells that make up most of the L6 corticothalamic projections. The fact that these experiments elicit similar results supports their interpretation that these direct projections are largely responsible for the observed results. While previous studies have manipulated corticothalamic projections pharmacologically, via V1 lesions, or via optogenetics, the authors rightly point out that most previous studies have focused on simple parametric stimuli and/or have been performed in anesthetized animals. The results of this study suggest feedback during natural visual stimuli and locomotion reveal effects that are distinct from these previous studies.

Overall, these are important and carefully-performed experiments that significantly advance our understanding of the role of corticothalamic feedback to the dLGN.

We thank the reviewer for the appreciation of our methods and results.

The authors suggestion that the different effects observed during simple and complex stimuli may be due to increased surround suppression during the full-field gratings seems reasonable, but I didn’t understand how the analysis of blank periods during these two conditions supported this argument. It wasn’t clear to me what mechanisms would be expected to support the alternative outcome, where suppressing feedback during the blank periods interleaved with the two different stimuli would have different effects - unless they are testing whether natural movies elicit some longer-lasting state change that would change the results observed during blank periods. This seems somewhat implausible, and unless the authors wish to expand the study to include different stimulus sizes, I think the interpretation regarding surround suppression is best left to the discussion, where it is already treated well.

We thank the reviewer for the recommendation. We fully agree that explaining the difference in CT feedback across blanks, gratings, and movies will require more experiments. We have followed the recommendation of the reviewer and removed the interpretation related to differences in surround suppression from the results section and treat it now in the discussion only.

The paper would benefit from more clearly highlighting results that agree or disagree with previous studies, with a brief mention of how the authors interpret these similarities or differences. For example the results of Olsen et al 2012 seem to be consistent with what the authors observe here with gratings but not with natural movies, and although Olsen et al performed some awake recordings, I think the LGN recordings were all under anesthesia. Specifically highlighting these differences (and suggesting an interpretation for them) would help emphasize the novelty of the study.

We thank the reviewer for the recommendation and now highlight throughout the results and discussion where our results agree or disagree with previous studies. As mentioned by the reviewer, we have similar results for gratings to the results obtained by Olsen et al. (2012), although in our study we have not explicitly centered the full field gratings on the RFs and we have not measured surround suppression. The results for the blank stimuli and the movies, however, are different, at least in terms of how CT feedback affects ring rate. A key insight of our study, at least in our view, is that CT feedback effects might well differ for different stimuli, and understanding the underlying mechanism (e.g., differential engagement of the excitatory and indirect inhibitory CT feedback pathway) will be an important avenue of research in the future.

The authors should comment more on the spatial extent of V1 silencing and potential effects of the variability observed across mice, especially given that they appear to have made only a single injection of ChR2 to label PV cells. While silencing with this method extends beyond the injection site, it probably doesn’t cover all of V1. Was any analysis done of variability across mice based on the size or location of the ChR2 expression measured post-hoc?

Unfortunately, we did not preserve enough slices to precisely quantify the extent of expression across animals. However, visual inspection of the slices revealed that even a single injection typically resulted in a widespread pattern of expression. In fact, we think that activation of PV neurons was determined in its spatial extent not so much by the virus expression but rather by the photoactivation light. With a distance of 0.5 0.1 mm of the optical fibre from the cortical surface, most of V1 was covered by light. A previous study performing a quantitative characterization of the lateral spread of optogenetic suppression by PV activation demonstrates that pyramidal neuron ring can be suppressed 2 3 mm from the laser center Li et al. (2019). Hence, we think that variability in opsin expression across mice is unlikely to have a substantial impact on our results.

The decrease in reliability and sparseness during running is attributed partially to increased eye movements. In cortex this has been studied in awake animals with natural movies in a variety of studies where the opposite effects are observed including Froudarakis et al 2014 where there was a small increase in both metrics during running, and Reimer et al 2014 where reliability strongly increased during pupil dilation. If there is enough data to condition on running periods where eye movements are stable or dilation outside of running to measure the effects of feedback suppression during these periods, this would be useful information.

We thank the reviewer for bringing up this interesting issue. We fully agree that our results recorded in dLGN are different from those measured by Froudarakis et al. (2014) and Reimer et al. (2014) in V1.

As suggested by the reviewer, we have repeated the analysis proposed by Reimer et al. (2014) to identify periods in the movie with the most rapid pupil dilation / constriction in face of continuous changes in overall luminance. Besides the effects of pupil dilation / constriction on ring rate, we have computed reliability both according to what we had used throughout our manuscript and in the way proposed in Reimer et al. (2014), which resembles our measure of SNR. We find that both measures of reliability are unaffected by pupil dilation.

Interestingly, in the meantime other studies have also reported that reliability might be differently affected by behavioral state in V1 compared to dLGN. For instance, Nestvogel and McCormick (2022) found that consistent with our results variability of membrane potential in visual thalamic neurons was not significantly altered by locomotion or whisker movement.

Reviewer #2 (Public Review):

Spacek et al. study the corticothalamic feedback of different visual stimuli on visual thalamus. With optogenetic suppression of visual cortex feedback and simultaneous multi-channel recordings in visual thalamus, the authors succeeded to acquire important data about this essential feedback loop in awake, behaving animals. The authors show in detail that the cortical feedback acts as a gain factor in thalamus for the transmission of signals from retina to cortex. They also show that naturalistic scenes result in robust feedback from cortex. As expected from anatomy, the authors find that modulatory feedback from cortex and modulatory input from brain stem act rather independently on thalamus. The paper is technically very impressive and the results are important for a wide range of readers.

We thank the reviewer for the positive feedback.

It is advisable to revise the Introduction and Discussion to better integrate the new findings into the existing literature.

We thank the reviewer for this advice, and have revised the title, abstract, introduction and discussion to better integrate our new findings into the existing literature, and highlight our advances in relation to previous findings.

The authors distinguish between awake, resting state and running state. However, the awake, resting state in mice comprises a wide range of alertness levels. This range of alertness will most likely affect the bursting probability of thalamocortical neurons.

We thank the reviewer for this comment. So far, our manuscript had only taken locomotion as a proxy for behavioral state, as locomotion typically goes along with increased pupil size (Erisken et al., 2014; McGinley et al., 2015) and increased levels of arousal (McGinley et al., 2015; Vinck et al., 2015). To also study the effects of locomotion-independent arousal, we have now applied the analysis mentioned by the reviewer: following methods originally suggested by Reimer et al. (2014), we identified periods of the movie presentation without locomotion that corresponded to the upper or the lower quartile of pupil size change. Similar to the results that Reimer et al. (2014) found for primary visual cortex, we observed that ring rate in dLGN is enhanced during times when the pupil was dilating faster than usual vs. when it was constricting faster than usual. Like the effects of running, the modulations by pupil-indexed arousal persisted even with V1 suppression. We present these new results in Figure 5 - Supplement 2.

Author Response

Reviewer #1 (Public Review):

The goal of this Tools and Resources article was to present a new method for optogenetic stimulation and optical imaging at the same time in two different cortical layers in vivo, and through 3 sets of experiments, highlight the promise and wide applicability of this method.

The method itself presents an elegant solution to several outstanding drawbacks among the many recent innovations in these lines of methodology, including high expense, lack of specificity and excessive brain tissue damage. The paper provides what I believe to be a fair account of the capabilities and limitations of existing methods and a clear description of how the new method builds on and overcomes these.

The three sets of experiments work well because they demonstrate reliability and feasibility in replicating previous findings from older techniques such as the phenonmenon of 'backpropagation-activated calcium spike firing' and net inhibitory influence of layer 2/3 cells on layer 5 cells, while also extending beyond those findings by verifying that some effects generalise to other areas than previous observations - the layer 2/3-5 interaction previously seen in primary somatosensory is here extended to motor cortex - and uncovering interesting phenomena that are relatively unexplored to date - the great variability in the degree of mirroring of activity in two layers receiving axonal input from the same thalamic area.

The method presents exciting possibilities for the fine-grained study of cortical microcircuits and how they enable perception and cognition and relate to behaviour. The simplicity and low cost of the solution opens it up to a wider range of laboratories globally, and its low-profile imprint on the cortex ensures that it most likely reflects activity of normal, intact, rather than damaged, cortical tissue.

We thank Reviewer #1 for recognizing “exciting possibilities” and advantages of our method.

Reviewer #2 (Public Review):

This manuscript reported a new approach to conduct neural activity imaging and manipulation in two different cortical layers. Two periscopes, each constructed from a micro-prism, a GRIN lens and a multi-mode fiber, could be inserted to the brain at different depths, and each can either perform imaging or optogenetics. The authors demonstrated a few applications: stimulation of L5 soma and superficial layer dendrites to evoke backpropagating action potential; optogenetically stimulating cells in L2/3 and observing response in L5 to investigate interaction between cells in two different layers; and simultaneously recording axon terminals from posteromedial thalamic nucleus at two different depths in cortex. This works combines the ideas of fiber photometry to access deep layers and using microprism to turn the optical field of view by 90 deg.

Major strengths

• Using microprism to perform layer specific imaging or optogenetics.

• Low cost

• Demonstrations of a few applications that require layer specific imaging and optogenetics.

We thank Reviewer #2 for recognizing these strengths.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors describe a generative model-based framework to better analyze stochastic growth data, including bacterial cell growth.

This work is well-supported by simulations and data analysis and will likely be of interest to those trying to understand the processes governing bacterial growth, as well as those studying stochastic growth processes in biology more broadly.

We thank Reviewer 1 for appreciating the methods used in the work and its scope.

It would be good to have a more extensive discussion about what is specifically new here. This is not my particular field, so having a bit more of an introduction about methods beyond binning (if any) that have emerged to understand these data.

Binning and linear regression are the most commonly used methods for probing the correlations between variables obtained using single cell data analysis [Ho et al. (2018), Jun et al. (2018)]. In this paper, we try to address the pitfalls associated with applying these simple procedures. In the revised version, we put more emphasis on linear regression throughout the manuscript for example in the ”Introduction”,

“While binning may provide a smooth non-linear relation between variables, linear regression is used to find a linear relationship between the variables. In addition to binning, we use the ordinary least squares regression where the slope and the intercept of the best linear fit line are obtained by minimizing the squared sum of the difference between the dependent variable raw data and the predicted value. Here, the best fit/the best linear fit is obtained using the raw data and not the binned data. Similar to binning, the assumption underlying linear regression is that our knowledge of x-axis variable is precise while the noise is in the y-axis variable.”

Following this comment, we added the best linear fits to the Figures 2C, 2D and 3A. We also try to clearly point out the sections which are not novel to the paper. For example, the adder model in Figure 1A has been discussed previously. We emphasize that in the revised text,

“This previously discussed example demonstrates and reiterates the use of statistical analysis on single-cell data to understand the underlying cell regulation mechanisms.” Similarly, the novel results of the paper such as obtaining the best linear fits for the plots ln( LLdb ) vs ⟨λ⟩Td and its flipped axes are based on a class of models studied by Eun et al. (2018). We try to make it clearer in p.7 line 133 of the revised manuscript,

“For that purpose, we use a previously studied model [Eun et al. (2018)] which considers growth to be exponential with the growth rate distributed normally and independently between cell cycles with mean growth rate ⟨λ⟩ and standard deviation CVλ⟨λ⟩.”

Reviewer #2 (Public Review):

The final result (Fig 4) is somewhat disconnected from the majority of the paper that precedes it. Specifically, the authors’ procedure that resolves exponential vs. nonexponential growth results in E. coli in alanine being deemed exponential (Fig 2B) only to later be revealed as non-exponential (Fig 4A), albeit weakly. Furthermore, the procedure advertised as distinguishing exponential from linear growth (Fig 3B), when applied to the data, reveals neither (Fig 4). This makes the main point of the paper (the demonstration and resolution of pitfalls) feel disconnected from its application to a particular case, which is more nuanced and likely leaves many questions unanswered.

We attempt to resolve the gap between Figure 4 and the text preceding it by showing that growth rate vs age plot can be used to infer the modes of growth, including, but not limited to, exponential and linear growth. To verify this, we simulate the adder model for cells undergoing super-exponential growth. The binned growth rate trend as a function of age for super-exponential growth is shown in Figure 3B and the following text is added to the revised manuscript,

“Thus, the two growth modes (exponential and linear) could be differentiated using the growth rate vs age plot (for details see Section 5.7). However, the growth rate vs age plots can be used to infer the mode of growth beyond the two discussed above. We show this by using simulations of cells following the adder model and undergoing faster than exponential or super-exponential growth (see Section 5.11.2 for details). In such a case, the growth rate is expected to increase. This increase in growth rate is shown in Figure 3B using simulations. The binned data trend (red triangles) again matches the growth rate mode used in the simulations (red dotted line). Thus, the growth rate vs age plots are a consistent method to distinguish linear from exponential and super-exponential growths.”

The details about the simulation of super-exponential growth has been added to Section 5.11.2. We have also added theoretical predictions (dotted lines of same color) to the growth rate vs age curves of different models shown in Figure 3B of the revised manuscript, that agree well with our simulations.

The title (”To bin or not to bin...”) implies that binning is the main culprit behind potentially misleading analysis, but I would argue that in the end, it is linear regression. Each of the two main pitfalls and their resolution would be unchanged if the data were never binned, I believe. Binning affects the apparent curvature of the y vs x relationship, but this reads as a more minor point. Therefore, the title may be a bit misleading in service of its poeticism.

We thank the reviewer for the comment and we have changed the title to a more apt one for the manuscript- ”Distinguishing different modes of growth using single-cell data”.

Reviewer #3 (Public Review):

Kar et al. examine an interesting and important question of how to make sense of large sets of observational data, specifically cell length data, which may or may not be consistent with various underlying biological mechanisms. As datasets improve in their technical quality (increasing spatiotemporal resolution, increasing numbers of observations), there is hope that the community will be able to resolve differences between underlying cell biological mechanisms of cell size homeostasis. As the authors point out, these interpretations and analyses require statistical analysis that can accurately perform the model selection or parameter estimation task of interest.

We thank Reviewer 3 for the comments. Indeed, our message in the paper is to use underlying biological models to aid the inference of biological mechanisms using various statistical analyses methods.

1. The authors succeed in bringing attention to the issue of appropriate binning when analyzing large datasets. The authors focus their figures and discussion on an important, and practical issue, as many researchers perform linear regression on binned data. The title and framing of the manuscript imply that it will provide a comparison with statistical methods that do not involve binning. The authors look at different choices of binning dimensions, but do not sufficiently explore the power of their generative model to perform (un)weighted regression or parameter estimation from the not-binned data. They do explore the unbinned data from an analytical statistics approach in section 5.4.1 and 5.5 but this not yet extensively explored in the figures and/or discussion.

We apologize for the confusion. Throughout the paper, we perform linear regression on the raw data and not the binned data. We have now added a clarification statement in the revised text,

"Here, the best fit/the best linear fit is obtained using the raw data and not the binned data."

Further, we have changed the title of the manuscript to ”Distinguishing different modes of growth using single-cell data”. The paper aims to bring forth the issues in both binning and linear regression which arise from similar sources i.e., the intrinsic noise affecting the x-axis variable and the inspection bias. We discuss these issues in relation to mode of growth in single cells as the new title now states.

In addition to section 5.4.1 and 5.5 where we discuss calculating the best fit line for exponential and linear growth, we also try to explicitly mention linear regression on non-binned data in the figures, and the Results and Discussion section. This is shown by the addition of the best linear fit/best fit in Figures 2C, 2D and 3A.

Author Response

Reviewer #1(Public Review)

Maji et al demonstrate co-storage of prolactin (PRL) and galanin (GAL) as functional amyloids in secretory granules of the female rat. In a series of detailed experiments, they show that both hormones promote their aggregation to amyloid. They show that PRL and GAL co-localize in the pituitary and that there is co-fibril formation, forming a new type of hybrid fibril. They further demonstrate that there is a unidirectional cross-seeding of GAL aggregation for PRL seeds, while cross seeding by mixed fibrils does not occur. Molecular dynamic studies show that co-aggregation of PRL and GAL induce the formation of a β-sheet at the protein surface. Overall, more efficient storage of the hormones in secretory granules is demonstrated, as well as faster release, as compared to the homotypic counterparts. Strengths include the rigorous techniques that were used, including biophysical techniques with transmission electron microscopy and the use of molecular dynamics to delineate the mechanism of PRL and GAL interactions at the atomic level. An additional strength is the novel observation of the unidirectional, heterotypic templating competency of PRL fibril seeds for GAL monomers, inducing GAL fibril formation.

We appreciate your comments and thank you for providing deep insight into our manuscript and stating the importance of our findings.

Reviewer #2 (Public Review):

Research on peptide hormones released from the Pituitary, including Prolactin, has shown that the hormones are stored as functional amyloids. Furthermore, it is well established that Prolactin and Galanin are co-stored in secretory granules of the anterior pituitary until they are released into the bloodstream. However, the mechanism by which hormones are stored and released remains a mystery. This study describes the co-aggregation and functional heterotypic amyloid formation of Prolactin and neuropeptide Galanin in secretory granules. This study suggests that the Prolactin and Galanin interact with each other at high specificity and form functional amyloids. These functional amyloids are heterotypic. Moreover, they demonstrated that Prolactin-Galanin amyloids can form surface-induced secondary fibrils on the surfaces of others. Galanin forms secondary fibrils on Prolactin seeds and Prolactin does not form secondary fibrils on Galanin seeds, indicating that this process occurs in a highly regulated manner. Additionally, they analyzed the release of hormone monomers from amyloids in vitro. They found that Prolactin-Galanin functional amyloids are released faster than amyloids formed by Prolactin or Galanin homotypic fibrils. To understand the interactions between Prolactin and Galanin at the atomic level, they have also performed molecular dynamics simulations and docking studies.

A high point of the study is the identification of Prolactin's capability to cross-seed Galanin. This causes amyloid fibrils to be formed. However, in contrast, the Galanin failed in cross-seed the Prolactin. It emphasizes the specificity and regulation in functional amyloid formation. Additionally, the understanding of the interactions between Prolactin and Galanin at the atomic level from MD simulations strengthens the findings. The results of this study did not confirm the possibility of heteromeric fibril formation.

In this study, the authors succeeded in achieving their goals and their conclusions were backed up by their results.

Undoubtedly, this work will have a significant impact on the field of endocrinology and protein aggregation. By studying secretory granules of the pituitary gland, researchers have successfully stepped one step closer to understanding peptide hormone synthesis and release.

We appreciate you for the elaborate analysis of our manuscript and for commenting on the relevance of our findings.

Reviewer #3 (Public Review):

Maji and coworkers present a tour de force study of the coaggregation of two hormones, prolactin and galanin. Protein aggregation in vivo is much more of a "messy" affair than in the tidy lab of an Eppendorf tube and the authors demonstrate an intimate collaboration between these two hormones in the aggregation process. Their work ranges from IHC of tissue slices over experimental biophysics to computational studies, presented in a clear, user-friendly and illustrative manner and overall, the conclusions are sound. I found the cartoon diagrams in various figures particularly helpful and of high quality.

Whether their conclusions can be extended to higher-order complexes between multiple hormones (even closer to real life) is the next question to address - but the mind boggles at the number of possibilities to explore.

We thank you for your detailed analysis of the studies in our manuscript and for highlighting the importance of our work.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors find CpGs within 500Kb of a gene that associate with transcript abundance (cis-eQTMs) in children from the HELIX study. There is much to admire about this work. With two notable exceptions, their work is solid and builds/improves on the work that came before it. Their catalogue of eQTMs could be useful to many other researchers that utilize methylation data from whole blood samples in children. Their annotation of eQTMs is well thought out and exhaustive. As this portion of the work is descriptive, most of their methods are appropriate.

Unfortunately, their use of results from a model that does not account for cell-type proportions across samples diminishes the utility and impact of their findings. I believe that their catalog of eQTMs contains a great deal of spurious results that primarily represent the differences in cell-type proportions across samples.

Lastly, the authors postulate that the eQTM gene associations found uniquely in their unadjusted model (in comparison to results from a model that does account for cell type proportion) represent cell-specific associations that are lost when a fully-adjusted model is assumed. To test this hypothesis, the authors appear to repurpose methods that were not intended for the purposes used in this manuscript. The manuscript lacks adequate statistical validation to support their repurposing of the method, as well as the methodological detail needed to peer review it. This section is a distraction from an otherwise worthy manuscript. But provide evidences that enriched for cell sp CpGs.

Major points

1. Line 414-475: In this section, the authors are suggesting that CpGs that are significant without adjusting for cell type are due to methylation-expression associations that are found only in one cell type, while association found in the fully adjusted model are associations that are shared across the cell types. I do not agree with this hypothesis, as I do not agree that the confounding that occurs when cell-type proportions are not accounted for would behave in this way. Although restricting their search for eQTMs to only those CpGs proximal to a gene will reduce the number of spurious associations, a great deal of the findings in the authors' unadjusted model likely reflect differences in cell-type proportions across samples alone. The Reinius manuscript, cited in this paper, indicates that geneproximal CpGs can have methylation patterns that vary across cell types.

Following reviewers’ recommendations, we have reconsidered our initial hypothesis about the role of cellular composition in the association between methylation and gene expression. Although we still think that some of the eQTMs only found in the model unadjusted for cellular composition could represent cell specific effects, we acknowledge that the majority might be confounded by the extensive gene expression and DNA methylation differences between cell types. Also, we recognize that more sophisticated statistical tests should be applied to prove our hypothesis. Because of this, we have decided to report the eQTMs of the model adjusted for cellular composition in the main manuscript and keep the results of the model unadjusted for cellular composition only in the online catalogue.

1. Line 476-488: Their evidence due to F-statistics is tenuous. The authors do not give enough methodological detail to explain how they're assessing their hypothesis in the results or methods (lines 932-946) sections. The methods they give are difficult to follow. The results in figure S19A are not compelling. The citation in the methods (by Reinius) do not make sense, because Reinius et al did not use F-statistics as a proxy for cell type specificity. The citation that the authors give for this method in the results does not appear to be appropriate for this analysis, either. Jaffe and Irizarry state that a CpG with a high Fstatistic indicates that the methylation at that CpG varies across cell type. They suggest removing these CpGs from significant results, or estimating and correcting for cell type proportions, as their presence would be evidence of statistical confounding. The authors of this manuscript indicate that they find higher F-statistics among the eQTMs uniquely found in the unadjusted model, which seems to only strengthen the idea that the unadjusted model is suffering from statistical confounding.

We recognize the miss-interpretation of the F-statistic in relation to cellular composition. We have deleted all this part from the updated version of the manuscript.

1. The methods used to generate adjusted p-values in this manuscript are not appropriate as they are written. Further, they are nothing like the methods used in the paper cited by the authors. The Bonder paper used permutations to estimate an empirical FDR and cites a publication by Westra et al for their method (below). The Westra paper is a better one to cite, because the methods are more clear. Neither the Bonder nor the Westra paper uses the BH procedure for FDR.

Westra, H.-J. et al. Systematic identification of trans eQTLs as putative drivers of known disease associations. Nat. Genet. 45, 1238-1243 (2013).

We apologize for this misleading citation. Although Bonder et al applied a permutation approach to adjust for multiple testing, our approach was inspired by the method applied in the GTEx project (GTEx consortium, 2020), using CpGs instead of SNPs. The citation has been corrected in the manuscript. Moreover, we have explained in more detail the whole multiple-testing processes in the Material and Methods section (page 14, line 316):

“To ensure that CpGs paired to a higher number of Genes do not have higher chances of being part of an eQTM, multiple-testing was controlled at the CpG level, following a procedure previously applied in the Genotype-Tissue Expression (GTEx) project (Gamazon et al., 2018). Briefly, our statistic used to test the hypothesis that a pair CpGGene is significantly associated is based on considering the lowest p-value observed for a given CpG and all its pairs Gene (e.g. those in the 1 Mb window centered at the TSS). As we do not know the distribution of this statistic under the null, we used a permutation test. We generated 100 permuted gene expression datasets and ran our previous linear regression models obtaining 100 permuted p-values for each CpG-Gene pair. Then, for each CpG, we selected among all CpG-Gene pairs the minimum p-value in each permutation and fitted a beta distribution that is the distribution we obtain when dealing with extreme values (e.g. minimum) (Dudbridge and Gusnanto, 2008). Next, for each CpG, we took the minimum p-value observed in the real data and used the beta distribution to compute the probability of observing a lower p-value. We defined this probability as the empirical p-value of the CpG. Then, we considered as significant those CpGs with empirical p-values to be significant at 5% false discovery rate using BenjaminiHochberg method. Finally, we applied a last step to identify all significant CpG-Gene pairs for all eCpGs. To do so, we defined a genome-wide empirical p-value threshold as the empirical p-value of the eCpG closest to the 5% false discovery rate threshold. We used this empirical p-value to calculate a nominal p-value threshold for each eCpG, based on the beta distribution obtained from the minimum permuted p-values. This nominal p-value threshold was defined as the value for which the inverse cumulative distribution of the beta distribution was equal to the empirical p-value. Then, for each eCpG, we considered as significant all eCpG-Gene variants with a p-value smaller than nominal p-value.”

References:<br /> GTEx consortium, The GTEx Consortium atlas of genetic regulatory effects across human tissues, Science (2020) Sep 11;369(6509):1318-1330. doi: 10.1126/science.aaz1776.

Reviewer #2 (Public Review):

Strength:

Comprehensive analysis Considering genetic factors such as meQTL and comparing results with adult data are interesting.

We thank the reviewer for his/her positive feedback on the manuscript. We agree that the analysis of genetic data and the comparison with eQTMs described in adults are two important points of the study.

Weakness:

• Manuscript is not summarized well. Please send less important findings to supplementary materials. The manuscript is not well written, which includes every little detail in the text, resulting in 86 pages of the manuscript.

Following reviewers’ comments, we have simplified the manuscript. Now only the eQTMs identified in the model adjusted for cellular composition are reported. In addition, functional enrichment analyses have been simplified without reporting all odds ratios (OR) and p-values, which can be seen in the Figures.

• Any possible reason that the eQTM methylation probes are enriched in weak transcription regions? This is surprising.

Bonder et al also found that blood eQTMs were slightly enriched for weak transcription regions (TxWk). Weak transcription regions are highly constitutive and found across many different cell types (Roadmap Epigenetics Consortium, 2015). However, hematopoietic stem cells and immune cells have lower representation of TxWk and other active states, which may be related to their capacity to generate sub-lineages and enter quiescence.

Given that we analyzed whole blood and that ROADMAP chromatin states are only available for blood specific cell types, each CpG in the array was annotated to one or several chromatin states by taking a state as present in that locus if it was described in at least 1 of the 27 bloodrelated cell types. By applying this strategy we may be “over-representing” TxWk chromatin states, in the case TxWk are cell-type specific. As a result, even if each blood cell type might have few TxWk, many positions can be TxWk in at least one cell type, inflating the CpGs considered as TxWk. This might have affected some of the enrichments.

On the other hand, CpG probe reliability depends on methylation levels and variance. TxWk regions show high methylation levels, which tend to be measured with more error. This also might have impacted the results, however the analysis considering only reliable probes (ICC >0.4) showed similar enrichment for TxWk.

Besides these, we do not have a clear answer for the question raised by the reviewer.

References:

Bonder MJ, Luijk R, Zhernakova D V, Moed M, Deelen P, Vermaat M, et al. Disease variants alter transcription factor levels and methylation of their binding sites. Nat Genet [Internet]. 2017 [cited 2017 Nov 2];49:131–8. Available from: http://www.ncbi.nlm.nih.gov/pubmed/27918535

Roadmap Epigenomics Consortium, Kundaje A, Meuleman W, Ernst J, Bilenky M, Yen A, Heravi-Moussavi A, Kheradpour P, Zhang Z, Wang J, Ziller MJ, Amin V, Whitaker JW, Schultz MD, Ward LD, Sarkar A, Quon G, Sandstrom RS, Eaton ML, Wu YC, Pfenning AR, Wang X, Claussnitzer M, Liu Y, Coarfa C, Harris RA, Shoresh N, Epstein CB, Gjoneska E, Leung D, Xie W, Hawkins RD, Lister R, Hong C, Gascard P, Mungall AJ, Moore R, Chuah E, Tam A, Canfield TK, Hansen RS, Kaul R, Sabo PJ, Bansal MS, Carles A, Dixon JR, Farh KH, Feizi S, Karlic R, Kim AR, Kulkarni A, Li D, Lowdon R, Elliott G, Mercer TR, Neph SJ, Onuchic V, Polak P, Rajagopal N, Ray P, Sallari RC, Siebenthall KT, Sinnott-Armstrong NA, Stevens M, Thurman RE, Wu J, Zhang B, Zhou X, Beaudet AE, Boyer LA, De Jager PL, Farnham PJ, Fisher SJ, Haussler D, Jones SJ, Li W, Marra MA, McManus MT, Sunyaev S, Thomson JA, Tlsty TD, Tsai LH, Wang W, Waterland RA, Zhang MQ, Chadwick LH, Bernstein BE, Costello JF, Ecker JR, Hirst M, Meissner A, Milosavljevic A, Ren B, Stamatoyannopoulos JA, Wang T, Kellis M. Integrative analysis of 111 reference human epigenomes. Nature. 2015 Feb 19;518(7539):317-30. doi: 10.1038/nature14248. PMID: 25693563; PMCID: PMC4530010.

• The result that the magnitude of the effect was independent of the distance between the CpG and the TC TSS is surprising. Could you draw a figure where x-axis is the distance between the CpG site and TC TSS and y-axis is p-value?

As suggested by the reviewer, we have taken a more detailed look at the relationship between the effect size and the distance between the CpG and the TC’s TSS. First, we confirmed that the relative orientation (upstream or downstream) did not affect the strength of the association (p-value=0.68). Second, we applied a linear regression between the absolute log2 fold change and the log10 of the distance (in absolute value), finding that they were inversely related. We have updated the manuscript with this information (page 22, line 504):

“We observed an inverse linear association between the eCpG-eGene’s TSS distance and the effect size (p-value = 7.75e-9, Figure 2B); while we did not observe significant differences in effect size due to the relative orientation of the eCpG (upstream or downstream) with respect to the eGene’s TSS (p-value = 0.68).”

Results are shown in Figure 2B. Of note, we winsorized effect size values in order to improve the visualization. The winsorizing process is also explained in Figure 2 legend. Moreover, we have done the plot suggested by the reviewer (see below). It shows that associations with smallest p-values are found close to the TC’s TSS. Nonetheless, as this pattern is also observed for the effect sizes, we have decided to not include it in the manuscript.

• Concerned about too many significant eQTMs. Almost half of genes are associated with methylation. I wonder if false positives are well controlled using the empirical p-values. Using empirical p-value with permutation may mislead since especially you only use 100 permutations. I wonder the result would be similar if they compare their result with the traditional way, either adjusting p-values using p-values from entire TCs or adjusting pvalues using a gene-based method as commonly used in GWAS. Compare your previous result with my suggestion for the first analysis.

Despite the number of genes (TCs) whose expression is associated with DNA methylation is quite high, we do not think this is due to not correctly controlling false positives. Our approach is based on the method used by GTEx (GTEx consortium) and implemented in the FastQTL package (Ongen et al. 2016), to control for positives in the eQTLs discovery. As in GTEx, we run 100 permutations to estimate the parameters of a beta distribution, which we used to model the distribution of p-values for each CpG. Then, to correct for the number of TCs among significant CpGs, we applied False Discovery Rate (FDR) at a threshold < 0.05. Finally, we defined the final set of significant eQTMs using the beta distribution defined in a previous step.

For illustration, we compared the number of eQTMs with our approach to what we would obtain by uniquely applying the FDR method (adjusted p-value <0.05), getting fewer associations with our approach: eQTMs (45,203 with FDR vs 39,749 with our approach), eCpGs (24,611 vs 21,966) and eGenes (9,937 vs 8,886). Among the 8,886 significant eGenes, 6,288 of them are annotated to coding genes, thus representing 27% of the 23,054 eGenes coding for a gene included in the array.

References:

GTEx consortium, The GTEx Consortium atlas of genetic regulatory effects across human tissues, Science (2020) Sep 11;369(6509):1318-1330. doi: 10.1126/science.aaz1776.

Ongen et al. Fast and efficient QTL mapper for thousands of molecular phenotypes, Bioinformatics (2016) May 15;32(10):1479-85. doi: 10.1093/bioinformatics/btv722. Epub 2015 Dec 26.

• I recommend starting with cell type specific results. Without adjusting cell type, the result doesn't make sense.

As suggested by other reviewers, we have withdrawn the model unadjusted for cellular composition.

Reviewer #3 (Public Review):

Although several DNA methylation-gene expression studies have been carried out in adults, this is the first in children. The importance of this is underlined by the finding that surprisingly few associations are observed in both adults and children. This is a timely study and certain to be important for the interpretation of future omic studies in blood samples obtained from children.

We agree with the reviewer that eQTMs in children are important for interpreting EWAS findings conducted in child cohorts such as those of the Pregnancy And Childhood Epigenetics (PACE) consortium.

It is unfortunate that the authors chose to base their reporting on associations unadjusted for cell count heterogeneity. They incorrectly claim that associations linked to cell count variation are likely to be cell-type-specific. While possible, it is probably more likely that the association exists entirely due to cell type differences (which tend to be large) with little or no association within any of the cell types (which tend to be much smaller). In the interests of interpretability, it would be better to report only associations obtained after adjusting for cell count variation.

Following reviewers’ recommendations, we have reconsidered our initial hypothesis about the role of cellular composition in the association between methylation and gene expression. Although we still think that some of the eQTMs only found in the model unadjusted for cellular composition could represent cell specific effects, we acknowledge that the majority might be confounded by the extensive gene expression and DNA methylation differences between cell types. Also, we recognize that more sophisticated statistical tests should be applied to prove our hypothesis. Because of this we have decided to report the eQTMs of the model adjusted for cellular composition in the main manuscript and keep the results of the model unadjusted for cellular composition only in the online catalogue.

Several enrichments could be related to variation in probe quality across the DNA methylation arrays.

For example, enrichment for eQTM CpG sites among those that change with age could simply be due to the fact age and eQTM effects are more likely to be observed for CpG sites with high quality probes than low quality probes. It is more informative to instead ask if eQTM CpG sites are more likely to have increasing rather than decreasing methylation with age. This avoids the probe quality bias since probes with positive associations with age would be expected to have roughly the same quality as those with negative associations with age. There are several other analyses prone to the probe quality bias.

See answer to question 2, below.

Author Response

Reviewer #1 (Public Review):

Peter Dietrich and his collaborators performed a complex experimental study aiming at exploring an interactive effect of selection history (offspring of plants grown in low- and high-diversity plots), soil origin (soil from low- and high-diversity plots) and experimental treatments (drought or nitrogen addition) on performance of four grass species. The authors did so to examine eco-evolutionary feedbacks between plant community diversity and global change drivers. Specifically, the authors hypothesize that decline in species richness due to the drivers can induce a selection regime that will select for traits that will make species more vulnerable to the further effects of global change drivers, amplifying thus the initial diversity decline. The authors indeed found that all three factors, and their interaction can affect plant performance, though the effects detected here were often species-specific.

We thank the reviewer for the positive evaluation of our study. In the revised version, we express more clearly the fact that the plant responses to global change were species-specific. We agree that this is a highly relevant finding that needs to be stressed.

Reviewer #2 (Public Review):

The authors present work from a greenhouse experiment testing the influence of plant and soil histories on seedling responses to global change. They grew seedlings of 4 grass species via seeds collected from different historical levels of plant community diversity (2 vs 6 species) as well as in home and away soil inoculum and a combination of these. The authors find that certain plant species respond differently to global change depending on the historical plant diversity (6 vs 2 species) and to a lesser extent the soil history. These effects were primarily species specific and affected plant traits rather than biomass.

Strengths of this study include the thorough experimental approach and novel question regarding how plant diversity may modulate plant-soil interactions under global change. Weaknesses of this study include weak or unclear support for several of the proposed hypotheses as well as lack of clear results to support the main conclusions and title of this paper.

We are thankful for the detailed advice to improve our manuscript. We added additional text to the introduction to better introduce our hypotheses and rephrased the title, abstract, and conclusion to better match our results.

Author Response

Reviewer #2 (Public Review):

The visual system must extract two basic features of visual stimuli: luminance, which we perceive as brightness, and contrast, the change in luminance over space or time (this paper focuses on changes over time). Contrast is separately processed by ON and OFF pathways, which encode luminance increments or decrements, respectively. Contrast must be robustly detected even if the overall luminance changes rapidly, as might occur if an animal is moving in and out of shadows. This paper addresses how such a luminance correction occurs in the fly.

In the fly, three types of first-order interneurons - L1, L2, and L3 - transmit information from photoreceptors to the medulla, where ON and OFF encoding emerges. Previous work suggested that all three interneurons primarily encode contrast signals and that they project to distinct pathways: L1 to the ON pathway and L2 and L3 to the OFF pathway. Ketkar et al. show that, contrary to this model, these interneurons encode both contrast and luminance in specific ways and are not cleanly segregated into ON versus OFF inputs.

This study reveals several new insights into early visual processing that are interesting and well-supported by the data:

1) The authors show that behavioral responses to ON stimuli can compensate for rapid changes in luminance. However, the purported sole input to the ON pathway, L1, shows activity that is highly dependent on luminance. This suggests that a luminance correction must arise downstream of L1. These results are analogous to findings previously made by the same group regarding the OFF pathway (Ketkar et al., 2020). The previous paper showed that L2 provides contrast information to the OFF pathway, and L3 provides luminance information to allow for a luminance correction in downstream contrast encoding. But unlike the multiple inputs to the OFF pathway, the ON pathway was thought to only receive input from L1, provoking the question of whether L1 is able to provide both contrast and luminance information.

2) Using well-designed calcium imaging studies, the authors surveyed the responses of the three interneurons and found that they encode different stimulus features: L1 encodes both contrast and luminance, L2 purely encodes contrast, and L3 purely encodes luminance (with a different dependence than L1). These are interesting and important findings revealing how both contrast and luminance encoding are distributed across the three interneurons.

3) Using neuronal manipulations, the authors dissected the contributions of the three interneurons to ON and OFF behavior under changing luminance. These experiments showed that L1 and L3 are required for the luminance correction in the behavior. Moreover, the finding that all three interneurons contribute to both ON and OFF behavior contrasts with the existing model of segregated pathways. Thus, this paper could change the way we think about early visual processing in the fly: rather than relaying similar information to distinct downstream pathways, first-order interneurons relay distinct information to common pathways.

Overall, the major claims of this paper are important and supported by the experiments. There are just a few concerns that I would note:

Thank you for the overall positive evaluation of our work, as well as for the constructive criticism, which we are going to address below.

1) The authors state that they have shown luminance invariance in ON behavior (e.g. line 376-377 of the Discussion), but this is not entirely accurate: the ON behavior decreases as luminance increases. This is still an interesting effect since it's the opposite of what L1 activity does, so it's clear that the circuit is implementing a luminance correction, but it is not "luminance invariance".

As pointed out in response to essential comment #2, we carefully edited the manuscript to talk about ‘near’ luminance invariance, or data approaching luminance invariance. More prominently, we rephrased the text to highlight the need for a luminance gain to scale behavioral responses to contrast, even if the resulting behavior is not entirely luminance invariant.

2) The visual stimuli presented for most imaging experiments (full-field) are not the same as those presented for behavior (moving edges). It is possible neuronal responses and their encoding of luminance and contrast may differ if tested with the moving edge stimuli (if so, this would be concerning). The authors did image L1 with both types of stimuli and could compare these responses. Also, testing behavior at 34º and imaging at 20º presents a possible discrepancy in comparing these data.

We use moving ON edges in Figure 1, and these data suggest that the transient response of L1 scales with step changes in luminance, consistent with data in Figure 2B. Although we did not point this out in the paper, the L1 responses in Figure 1 also decay to different response levels, consistent with the luminance-sensitive component that static stimuli reveal in Figure 2. Furthermore, for other ongoing projects in the lab, we have for example measured physiological responses in L2 with the same stimuli used in behavior, and there is no discrepancy with the data reported here. Overall, there is no reason to believe, following a vast amount of literature in Drosophila and other flies, that LMCs would respond any different to moving vs. static stimuli.

We can additionally point out that the behavioral data of L3 silencing (at 34ºC) nicely correlate with physiological contrast responses of L1 and L2 (at 20ºC, predicted from electrophysiological recordings for LMCs in Ketkar et al. 2020, measured for L1 here). Many previous studies, for example in motion detection, have linked data from physiological recordings at room temperature with behavioral experiments done at higher temperature (e.g., Ammer et al., 2015; Clark et al., 2011; Creamer et al., 2019; Fisher et al., 2015; Leonhardt et al., 2017; Salazar-Gatzimas et al., 2016; Serbe et al., 2016; Silies et al., 2013; Strother et al., 2017). We therefore do not think that these are major concerns.

3) I find it puzzling that silencing L1 has little effect on ON behavior at 100% contrast and varying luminance (Figure 3A), but severely affects ON behavior to 100% contrast (and lower values) when different contrasts are interleaved (Figure S1). The authors note this but do not provide a clear explanation of why this might be the case. Aside from mechanism, it is not clear whether the difference is due to varying luminance in the first experiment or varying contrast in the second one (e.g. they could test 100% contrast without varying luminance).

The two stimulus sets used here do not allow us to pinpoint why the L1 silencing phenotype differs between them, since they comprise more than one difference as discussed above (see point 4) in “Essential Revisions”). We now include two additional experiments that dissect the role of different stimulus parameters (Supp. Figure 2). To understand whether the difference is due to varying luminance, we tested responses to ON edges of fixed (100%) contrast and luminance at the same stimulus parameters (motion duration, speed) as used in Figure 3, and did not find reduced turning responses when silencing L1. Thus, varying luminance does not change the effect of L1 on ON behavior. However, when repeating this experiment with a bright inter-stimulus interval, L1 silencing lead to a strong response deficit. Therefore, differences in the interval luminance explain the differences in the L1 silencing phenotype observed not only in this study but also across studies. Although we hypothesize a role of contrast adaptation that may function differently with altered contrast statistics, a more detailed investigation would be necessary to understand the mechanism. Nevertheless, our experiments allow us to conclude that L1 is not the sole major input to the ON pathway, even though it is required under certain stimulus conditions.

4) I do not entirely agree with the authors' interpretation of the L1 ort rescue experiment for OFF behavior. They state that rescue flies "responded similarly to positive controls". However, the graph shows that the rescue flies generally fall in between the mutant and heterozygote control flies; they resemble the controls at low luminance but resemble the mutants at high luminance. One may conclude that L1 is sufficient to enhance OFF behavior at low luminance, but it is a stretch to say it's a complete rescue.

Sorry, we just meant to say that they “responded similarly to positive controls (...) at low luminance”, but the sentence was badly written. We corrected this to: “L1 ort rescue flies responded similarly to positive controls at low luminances, rescuing responses to OFF edges at dim backgrounds.”

5) The authors typically use t-tests to analyze experiments with 2 variables (genotype and luminance) and 3 or more conditions per variable. This is not the most appropriate statistical test; typically one would use a two-way ANOVA. At the least, it should be clear whether they are performing corrections for multiple comparisons if performing many t-tests on the same dataset.

Thank you for the suggestion, we now use a two-way ANOVA followed by corrected pairwise comparisons and state this clearly in the figure captions (also addressed above in essential comment #5).

Reviewer #3 (Public Review):

Ketkar et al combine calcium imaging and behavioral experiments to investigate the encoding of luminance and contrast in 3 first-order interneurons in the Drosophila lamina: L1, L2, and L3, as well as the role of these signals in moving ON edge behavior across luminance. The behavioral experiments are well performed. The rescue experiments are particularly interesting. Together with silencing they support and nicely extend previous work showing that L1/2/3 are not simply segregated between ON and OFF pathways. My main issue is the link that the authors make between the cellular responses and the behaviors performed and therefore the overall conclusions and claims of the paper about the roles of contrast vs luminance encoding of each neuron type (particularly L1) in the behaviors.

Major concerns:

1) The authors state that the main behavior they study, namely optomotor response to moving light edges at 100% contrast, is "luminance invariant". A strict definition of this would be that behavioral responses are constant with increasing luminance. However, there are very few plots in this paper where this is the case. In almost all examples, the response is decreasing with respect to increasing luminance. The authors do qualify a "nearly" invariant behavior, but this does not change the fact that interpretation of the data in the context of the framing of the paper is often problematic.

We thank the reviewer for this critical comment. The main point (that we apparently failed to make clear enough) is that there is a clear requirement for a luminance gain. Physiological LMC responses measured using calcium imaging to ON stimuli in Figure 1, or predicted from previous electrophysiological recordings to OFF stimuli in (Ketkar et al., 2020) cannot account for any of the (control) behavioral data. We now edited the text to tone down statements about luminance invariance, and instead highlighted the need for a luminance gain.

2) The manuscript would benefit from clear definitions of luminance and contrast, as well as an explanation of how contrast and luminance sensitivity can be inferred from experiments. In particular, the authors use transient vs. sustained response properties in L1, L2, and L3 as indicators of contrast and luminance sensitivity, but this is not stated clearly. It would be important to explain this to the reader early on.

We now added definitions of general terms to the introduction and added data and analysis to the manuscript (Figure S1, and Figure 2B-D) to more clearly test which component of the neurons’ responses encode contrast or luminance.

3) In the manuscript, it is often stated that "calcium imaging experiments reveal that each first order interneuron is unique in its contrast and luminance encoding properties" (line 110). This was shown clearly for L2 and L3 in their previous work in Ketkar et al. 2020, with a welldesigned two-step stimulus that was able to tease apart contrast vs. luminance invariance. Unfortunately it does not seem that this level of experimental detail and analysis is applied to L1 here. In particular, the authors state " L1 encodes both contrast and luminance in distinct response components." Line 112, in the summary of their findings. I would not agree that the authors have actually shown this properly in this manuscript.

Addressed above, in point 6 of “Essential Revisions”

4) The results as they are stated, are at times not well supported by the data. The manuscript would benefit from a careful assessment of the accuracy and precision of the language used to interpret the data. Sometime just moving some conclusions to the discussion and explaining the assumptions made to reach a particular conclusion would be enough. A few of examples:

We carefully edited the entire manuscript, in addition to addressing the specific points below.

o Figure 2: "Lamina neuron types L1-L3 are differently sensitive to contrast and luminance". It is overall true that from the raw traces, the response are different. However the quantification in C-E only pertains to luminance.

As stated above, we now did further analysis on the contrast encoding properties of L1 and L2 and pointed out the major differences between these neurons (Figure 2B-D).

o Figure 3: "L1 is not required but sufficient for ON behavior across luminance". The data convincingly shows this. I would however point out that the statement "this data [..] highlights its behavioral relevant role of its luminance component" line 231 is an overstatement.

We deleted this statement at the end of the paragraph.

o Figure 6: "L1 luminance signal is required and sufficient for OFF behavior" the data presented shows convincingly that when L1 is inactive the behavior becomes (more) intensity variant. However, it does not show that it is the "luminance signal" in L1 that is required for this effect. In general, because L1 has a sustained and a transient response, it is difficult to strictly implicate one or the other in supporting any behavior, short of manipulating L1 to make it fully transient or fully sustained.

We agree. The figure title now reads “L1 function is required and sufficient for OFF behavior”.

o It is often not clear which conclusions stem from this work and which from their previous work Ketkar et al. 2020, or even other previous work on contrast sensitivity in particular. Clarifying this might help with my concern about statements not well supported by the data in this paper, and also justify their overall novelty. In general the manuscript assumes familiarity with this previous work, which is not always helpful for the reader.

As stated above, we now more clearly separate previous findings from novel findings in the abstract, and throughout the text. We also expanded the introduction to better explain the core concepts that are needed to understand this work, without having read Ketkar et al. 2020.

Author Response

Reviewer #1 (Public Review):

In this paper, Fernandes et al. take advantage of synthetic constructs to test how Bicoid (Bcd) activates its downstream target Hunchback (Hb). They explore synthetic constructs containing only Bcd, Bcd and Hb, and Bcd and Zelda binding sites. They use these to develop theoretical models for how Bcd drives Hb in the early embryo. They show that Hb sites alone are insufficient to drive further Hb expression.

The paper's first half focuses on how well the synthetic constructs replicate the in vivo expression of hb. This approach is generally convincing, and the results are interesting. Consistent with previous work, they show that Bcd alone is sufficient to drive an expression profile that is similar to wild‐type, but the addition of Hb and Zelda are needed to generate precise and rapid formation of the boundaries. The experimental results are supported by modelling. The model does a nice job of encapsulating the key conclusions and clearly adds value to the analysis.

In the second part of the paper, the authors use their synthetic approach to look at how the Hb boundary alters depending on Bcd dosage. This part asks whether the observed Bcd gradient is the same as the activity gradient of Bcd (i.e. the "active" part of Bcd is not a priori the same as the protein gradient). This is a very interesting problem and good the authors have tried to tackle this. However, the strength of their conclusions needs to be substantially tempered as they rely on an overestimation of the Bcd gradient decay length.

Comments:

‐ My major concern regards the conclusions for the final section on the activity gradient. In the Introduction it is stated: "[the Bcd gradient has] an exponential AP gradient with a decay length of L ~ 20% egg‐length (EL)". While this was the initial estimate (Houchmandzadeh et al., Nature 2002), later measurements by the Gregor lab (see Supplementary Material of Liu et al., PNAS 2013) found that "The mean length constant was reduced to 16.5 ± 0.7%EL after corrections for EGFP maturation". The original measurements by Houchmandzadeh et al. had issues with background control, that also led to the longer measured decay length. In later work, Durrieu et al., Mol Sys Biol 2018, found a similar scale for the decay length to Liu et al. Looking at Figure 5, a value of 16.5%EL for the decay length is fully consistent with the activity and protein gradients for Bcd being similar. In short, the strength of the conclusions clearly does not match the known gradient and should be substantially toned down.

The reviewer is right: several studies aiming to quantitatively measure the Bicoid protein gradient ended‐up with quite different decay lengths.

A summary of the various decay lengths measured, and the method used for these measurements is given below:

As indicated, these measurements are quite variable among the different studies and the differences can potentially be attributed to different methods of detection (antibody staining on fixed samples vs fluorescent measurements on live sample) or to the type of protein detected (endogenous Bicoid vs fluorescently tagged).

We agree with the reviewer that given these discrepancies, the exact value of the Bcd protein gradient decay length is not known and that we only have measurements that put it in between 16 and 25 % EL (see the Table above). Therefore, we agree that we should tone down the difference between the protein vs activity gradient and focus on the measurements of the effective activity gradient decay length allowed by our synthetic reporters. This allows us to revisit the measurement of the Hill coefficient of the transcription step‐like response, which is based on the decay‐length for the Bcd protein gradient, and assumed in previous published work to be of 20% EL (Gregor et al., Cell, 2007a; Estrada et al., 2016; Tran et al., PLoS CB, 2018). Importantly, the new Hill coefficient allows us to set the Bcd system within the limits of an equilibrium model.

As mentioned by the reviewer, it is possible that the decay length of the protein gradient measured using antibody staining (Houchmandzadeh et al,, Nature, 2002) was not correct due to background controls. Such measurements were also performed in Xu et al. (2015) which agree with the original measurements (Houchmandzadeh et al., Nature 2002). As indicated in the table above, all the other measurements of the Bcd protein gradient decay length were done using fluorescently tagged Bcd proteins and we cannot exclude the possibility the wt vs tagged protein might have different decay lengths due to potentially different diffusion coefficients or half‐lives. Before drawing any conclusion on the exact value of the endogenous Bcd protein gradient decay length, it is essential to measure it again in conditions that correct for the background issues for immuno‐staining as it was done in Liu et al., PNAS, 2013 for the Bcd‐eGFP protein. In this study, the authors only measured the decay length of the Bcd fusion protein using immuno‐staining for the Bcd protein. Unfortunately, in this study, the authors did not measure again the decay length of the endogenous Bcd protein gradient using immuno‐staining and the same procedure for background control. Therefore, they do not firmly exclude the possibility that the endogenous vs tagged Bcd proteins might have different decay length.

We thank the reviewer for his comment which helped us to clarify the message. In addition, as there is clearly an issue for the measurements of the Bcd protein gradient, we added a section in the SI (Section E) and a Table (Table S4) describing the various decay length measured for the Bcd or the Bcd‐fluorescently tagged protein gradients from previous studies. In the discussion, together with the possibility that there might be a protein vs activity gradient (as we originally proposed and believe is still a valid possibility), we also discuss the alternative possibility proposed by the reviewer which is that the protein vs activity gradients have the same decay lengths but that the decay length of the Bcd protein gradient was potentially not correctly evaluated.

‐ All of the experiments are performed in a background with the hb gene present. Does this impact on the readout, as the synthetic lines are essentially competing with the wild‐type genes? What controls were done to account for this?

We agree with the reviewer that this concern might be particularly relevant at the hb boundary where a nucleus has been shown to only contain ~ 700 Bicoid molecules (Gregor et al., Cell, 2007b). However, ~1000 Bicoid binding regions have been identified by ChIP seq experiments in nc14 embryos (Hannon et al., Elife, 2017) and given that several Bcd binding sites are generally clustered together in a Bcd region, the number of Bcd binding sites in the fly genome is likely larger than 1000. It is much greater than the number of Bicoid binding sites in our synthetic reporters. Therefore, we think that it is unlikely that adding the synthetic reporters (which in the case of B12 only represents at most 1/100 of the Bcd binding sites in the genome) will severely alter the competition for Bcd binding between the other Bcd binding sites in the genome. Additionally, the insertion of a BAC spanning the endogenous hb locus with all its Bcd‐dependent enhancers did not affect (as far as we can tell) the regulation of the wildtype gene (Lucas, Tran et al., 2018).

We have added a sentence concerning this point in the main text (lines 108 to 111).

‐ Further, the activity of the synthetic reporters depends on the location of insertion. Erceg et al. PLoS Genetics 2014 showed that the same synthetic enhancer can have different readout depending on its genomic location. I'm aware that the authors use a landing site that appears to replicate similar hb kinetics, but did they try random insertion or other landing site? In short, how robust are their results to the specific local genome site? This should have been tested, especially given the boldly written conclusions from the work.

This concern of the reviewer has been tested and is addressed Fig S1 where we compare two random insertions of the hb‐P2 transgene (on chromosome II and III; Lucas, Tran et al., 2018) and the insertion at the VK33 landing site that was used for the whole study. As shown Fig. S1, the dynamics of transcription (kymographs) are very similar. In the main text, the reference Fig. S1 is found in the Materials and Methods section (bottom of the 1st paragraph concerning the Drosophila stocks, lines 518).

‐ Related to the above, it's also not obvious that readout is linear ‐ i.e. as more binding sites are added, there could be cooperativity between binding domains. This may have been accounted for in the model but it is not clear to me how.

The reviewer is totally correct. It is clear from our data that readout is not linear: comparing (increase of 1.5 X in the number of BS) B6 with B9 leads to a 4.5 X greater activation rate and this argues against independent activation of transcription by individual bound Bcd TF. There is almost no impact of adding 3 more sites when comparing B9 to B12 (even though it corresponds to an increase of 1.33 X in the number of BS). This issue has been rephrased in the main text (lines 200 to 203) and further developed for the modeling aspects in the SI section C and Figure S3. It is also discussed in the second paragraph of the discussion (lines 380 to 383).

‐ It would be good in the Introduction/Discussion to give a broader perspective on the advantages and disadvantages of the synthetic approach to study gene regulation. The intro only discusses Tran et al. Yet, there is a strong history of using this approach, which has also helped to reveal some of the approaches shortcoming. E.g. Gertz et al. Nature 2009 and Sharon et al. Nature Biotechnology 2012. Again, I may have missed, but from my reading I cannot see any critical analysis of the pros/cons of the synthetic approach in development. This is necessary to give readers a clearer context.

One sentence was added in the introduction concerning this point (lines 79 to 82).

A short review concerning the synthetic approach in development has also been added at the beginning of the discussion (lines 347 to 359).

Reviewer #2 (Public Review):

It is known that Bicoid increases in concentration across the syncytial division cycles, the gradient length scale for Bicoid does not change, and hunchback also increases in concentration during the syncytial cycles but the sharp boundary of the hunchback gradient is constantly seen despite the change in concentration of Bicoid. This manuscript shows that by increasing the Bicoid concentration or by adding Zelda binding sites, the expression of hunchback can be recapitulated to that of a previously studied promoter for hunchback.

I have the following comments to understand the implications of the study in the context of increasing concentrations of Bicoid during the syncytial division cycles:

‐ Bicoid itself is also increasing over the syncytial division cycles, how does this change in concentration of Bicoid affect the activation of the hunchback promoter given the cooperative binding of Bicoid and Bicoid and Zelda as documented by the study?

We thank the reviewer for this remark about the dynamics of the Bcd gradient, which we may have taken for granted. A seminal work on the dynamics of the Bcd gradient using fluorescent‐tagged Bcd (Gregor et al, Cell, 2007a) has shown that the gradient of Bcd nuclear concentration (this nuclear concentration is the one that matter for transcription) remains stable over nuclear cycles, despite a global increase of Bcd amount in the embryo. This can be explained by the fact that Bcd molecules are imported in the nuclei and that the number of nuclei double at every cycle, such that both processes compensate each other. Thus, we assumed that the gradient of Bcd nuclear concentration was stable over nc11 to nc13.

We have clarified this assumption in the model section in the manuscript (lines 165‐168).

Supporting our assumption, when looking at the transcription dynamics regulated by Bcd, in Lucas et al, PLoS Gen, 2018, we observed very reproducible expression pattern dynamics of the hb‐P2 reporter at each cycle nc11 to nc13. Such reproducibility in the pattern dynamics were also observed in this current work for hb‐P2, B6, B9, B12 and H6B6 reporters (Fig. S6A). Also, in Lucas et al, PLoS Gen, 2018, the shift in the established boundary positions of hb‐P2 reporter between nc11 to nc13 is ~2%EL (approximately a nucleus length ~10μm) and it is thus marginal.

In addition, as mentioned in the text (lines 105 to 107), we only focused our analysis on nc13 data which are statistically stronger given the higher number of nuclei analyzed. Thus, any change of Bcd nuclear concentration that would happen over nuclear cycles will not matter.

Concerning Zelda: Zelda’s transcriptional activity when measured on a reporter with only 6 Zld binding sites changes drastically over the nuclear cycles, with strong activity at nc11 and much weaker activity at nc13 (Fig S4A). This indicates that the changes in expression pattern dynamics of Z2B6 from nc11 to nc13 are caused predominantly by decreasing Zelda activity: the effect of Zld on the Z2B6 promoter is very strong during nc11 and nc12. It is also very strong at the beginning of nc13 (even though the Z6 reporter is almost silent) and became a bit weaker in the second part of nc13 (Fig S4B‐D).

‐ Does the change in concentration of Bicoid across the nuclear cycles shift the gradient similar to the change in numbers of Bicoid binding sites?

In both Lucas et al, PLoS Gen, 2018 and in this work (Fig. 1, Fig. 3 and Fig. S6A), we found that the positions of the expression boundary are very reproducible and stable in time for hb‐P2, B6, B9, B12, H6B6 during the interphase of nc12 to 13. For hb‐P2, the averaged shift of the established boundary position in nc11, 12 and 13 is within 2 %EL. This averaged shift between the cycles is of similar magnitude to the difference caused by embryo‐to‐embryo variability within nc13 (~2 %EL) (Gregor et al, Cell, 2007b, Lucas et al, PloS Gen, 2018). This shift is much smaller than the difference between the expression boundary positions of B6 and B9 (~ 8 % EL) and between B6 and Z2B6 (~17.5 %EL) in nc13.

For these reasons, we conclude that the difference between the expression patterns of B6, B9 and Z2B6 are caused predominantly by changing the TF binding site configurations of the reporters, rather than variability in the Bcd gradient.

The assumption of gradient stability has been clarified in the previous answer and in the manuscript (lines 165‐168).

‐ The intensity is a little higher for B9 and B12 at the anterior in 2B? Is this statistically different? is this likely to change the amount of Bicoid expression at the locus and lead to more robust activation?

We performed statistical tests to distinguish the spot intensities at the anterior pole for every pair of reporters in Fig. 2B (hb‐P2, B6, B9 and B12). All p‐values from pair‐wise KS tests are greater than 0.067, suggesting that the spot intensities at the anterior pole are not distinguishable between these reporters.

We have clarified this in the manuscript (line 157).

‐Are the fraction of active loci not changing across the syncytial cycles when the concentration of Bicoid also changes and consistent with the synthetic promoters?

To measure the reproducibility of the expression pattern dynamics in different nuclear cycles, we compared the boundary position of the fraction of active loci pattern as a function of time for all hbP2 and synthetic reporters (Fig. S6A). In this figure panel, for all reporters except Z2B6, the curves in nc12 and nc13 largely overlap, suggesting high reproducibility in the pattern dynamics between cycles and consequently low sensitivity to the subtle variation in the Bcd nuclear concentration gradient between the cycles.

For Z2B6, we attributed the difference in pattern dynamics between nc12 and nc13 to the changes in Zelda activity, as validated independently with a synthetic reporter with only 6 Zld binding sites (Fig. S4A).

‐How do the numbers of Hb BS change the expression of Hb? H6B6 has 6 Hb BS whereas the Hb‐P2 has 1? Are more controls needed to compare these 2 contexts?

As our goal was to determine to which mechanistic step of our model each TF (Bcd, Hb, Zld) contributed, we added BS numbers that are much higher than in the hb‐P2 promoter. The added number of Hb BS remains very low when compared to total number of Hb binding sites in the entire genome (Karplan et al, PLOS Gen, 2011), therefore, it is very unlikely to affect the endogenous expression of Hb protein.

We clarified this in the manuscript (lines 211 to 212).

Does Zelda concentration change across the syncytial division cycles? How does the change in concentration in the natural context affect the promoter activation of Hb?

Zelda concentration is stable over the nuclear cycles, as observed with the fluorescently‐tagged Zld protein (Dufourt et al., Nat Com, 2018). However, Zelda’s transcriptional activity when measured on a reporter with only 6 Zld binding sites changes drastically over the nuclear cycles, with strong activity at nc11 and much weaker activity at nc13 (Fig S4A, this work).

The impact of this change in Zld activity can be observed with the Z2B6 promoter, with the expression boundary moving from the posterior region toward the anterior region over the nuclear cycles (Fig. S4B‐D). However, we don’t detect any changes in the expression pattern dynamics of hb‐P2 over the nuclear cycles (Fig. S6A and in Lucas et al., PLoS Gen, 2018).

We have clarified this in lines 250‐251 of the main manuscript.

‐Changing the dose of Bicoid shifts the boundary of hunchback expression. It would be nice to model or test this in the context of varing doses of zelda or even reason this with respect to varying doses of zelda across the syncytial division cycles.

We thank the reviewer for this insight. Concerning Zelda, we did not perform any experiment reducing the amount of Zelda in the embryo. However, in a previous study (Lucas et al., PLoS Genetics, 2018), we observed that the boundary of hb was shifted towards the anterior when decreasing the amount of Zelda consistent to the fact that the dose of Zelda is critical to set the boundary position and the threshold of Bcd concentration required for activation. However, as Zelda is distributed homogeneously along the AP axis, it cannot bring per se positional information to the system.

Reviewer #3 (Public Review):

I think the framing could be improved to better reflect the contribution of the work. From the abstract, for example, it's unclear to me what the authors think is the most meaningful conclusion. Is it the observations about the finer details of TF regulation (bursting dynamics), the fact that Bcd is probably the sole source of "positional information" for hb‐p2, that Bcd exists in active/inactive form, or the fact that an equilibrium model probably suffices to explain what we observe? The first sentence itself seems to suggest this paper will discuss "dynamic positional information", in which case it's somewhat misleading to say this kind of work is "largely unexplored"; Johannes Jaeger in particular has been a strong proponent of this view since at least 2004. On that note some particularly relevant recent papers in the Drosophila early embryo include:

1) Jaeger and Verd (2020) Curr Topics Dev Biol

2) Verd et al. (2017) PLoS Comp Biol

3) Huang, Amourda, et al. and Saunders (2017) eLife

4) Yang, Zhu, et al. (2020) eLife [see also the second half of Perkins (2021) PLoS Comp Biol for further discussion of that model]

‐Some reviews from James Briscoe also discuss this perspective.

We agree with the reviewer that the phrasing of the abstract was not clear enough to emphasize the contribution of the work and we are also sorry if it suggested that the dynamic positional information is largely unexplored because this was not at all our intention.

We rephrased the abstract aiming to better highlight the most meaningful conclusions.

‐I would also recommend modifying the title to reflect the biology found in the new results.

We modified the title to better reflect the new results:<br /> “Synthetic reconstruction of the hunchback promoter specifies the role of Bicoid, Zelda and Hunchback in the dynamics of its transcription”

‐A major point that the authors should address is the design of the synthetic constructs. From table S1, the sites are often very closely linked (4‐7 base pairs). From the footprint of these proteins, we know they can cover DNA across this size (see, https://pubmed.ncbi.nlm.nih.gov/8620846/). As such, there may be direct competition/steric hindrance (see https://pubmed.ncbi.nlm.nih.gov/28052257/). What impact does this have on their interpretations? Note also that the native enhancer has spaced sites with variable identities.

We completely agree with the reviewer comment in the sense that we named our reporters according to the number (N) of Bcd binding sites sequences that they contain, even though we cannot prove definitively that they can effectively be bound simultaneously by N Bcd molecules. It is thus possible that B9 is not a B9 but an effective B6 (i.e. B9 can only be bound simultaneously by 6 molecules) if, for instance, the binding of a Bcd molecule to one site would prevent by the binding of another Bcd molecule to a nearby site (as proposed by the reviewer in the case of direct competition or steric hindrance).

Even though we cannot exclude this possibility, we think that our use of B6, B9, B12, in reference to the 6 Bcd BS of hb‐P2 promoter, is relevant for several reasons : i) some of the Bcd BS in the hb‐P2 promoter are also very close from each other (see Table S1); ii) the design of the synthetic construct was made by multimerizing a series of 3 strong Bcd binding sites with a similar spacing as found for the closest sites in the hb‐P2 promoter (as shown in Figure 1A and Table S1); iii) the binding of the Bicoid protein has been shown in foot printing experiments in vitro to be more efficient on sites of the hb‐P2 promoter that are close from each other, and this has even been interpreted as binding cooperativity (Ma et al., 1996); iv) even though these experiments were not performed with full‐length proteins, two molecules of the paired homeodomain (from the same family of DNA binding domain as Bcd) are able to simultaneously bind to two binding sites separated by only 2 base pairs. This binding to very close sites is even cooperative while when the two sites are distant by 5 base pairs or more, the simultaneous binding to the two sites occurs without cooperativity (Wilson et al., 1993).

Conversely, as it is very difficult to demonstrate that 9 Bcd molecules can effectively bind to our B9 promoter, it is very difficult to know exactly how many binding sites for Bcd the hb‐P2 contains, and a large debate concerning not only the number but also the identity of the Bcd sites in the hb promoter is still ongoing (Park et al., 2019; Ling et al., 2019).

As we cannot exclude the possibility that B9 is an effective B6, it remains possible that B9 and hb‐P2 (which is supposed to only contains 6 sites) have the same number of effective Bcd binding site and this could explain why the two reporters have very similar transcription dynamics and features.

Regarding other interpretations in the manuscript, we identified two other aspects that will be affected if our synthetic reporters have fewer effective sites than the number of sites they carry. The first one concerns the synergy, as the increase in the number of sites of 1.5 from B6 to B9 might be over‐estimated but this would even increase the synergistic effect given the 4.5 difference in activity of the two reporters (Fig. S3). The second one concerns the discussion on the Hill coefficient and the decay length where the effective number of binding sites (N) is required to determine the limit of concentration sensing (Fig. 5). This would particularly be important for the hb‐P2 promoter.

Except for these specific points, we don’t think that the possibility that reporters do not exactly contain as many as effective binding sites than proposed, has a huge impact on our interpretations and the general message conveyed in this manuscript. Most importantly, it is very clear that our B6 and B9 reporters differ only by three Bcd binding sites and have yet very distinct expression dynamics: while B9 recapitulates almost all transcription features of hb‐P2, B6 is far from achieving it. Similarly, H6B6 and Z2B6 have very different transcription features than B6 and these differences have been key for understanding the mechanistic functions of the three TF we studied.

This discussion has been added to the discussion (lines 400 to 414)

Author Response

Reviewer #2 (Public Review):

In this interesting and beautifully illustrated study, the authors are addressing the question of the emergence of craniofacial tissues by dissecting the interplay between skeletal muscle progenitors and associated connective tissue cells. By combining sophisticated lineage-tracing single cell RNA-seq experiments with potent computational analysis tools followed by in situ validations, the authors have identified a population of Myf5+ bipotent progenitors that give rise to both muscle and connective tissue. However, some conclusions are solely based on the RNA-Seq data that would require further experimental validations.

We thank the Reviewer for evaluating our work and their encouraging comments. We agreed with the assessment and have now added more in-situ validations and quantifications to support the in-silico analyses.

Reviewer #3 (Public Review):

In this manuscript, Grimaldi et al. present evidence for the existence of Myf5+ bipotent progenitors for myogenic and connective lineages in the dorsal regions of the mouse head, which is not populated by neural crest cell-derived connective tissue. The study relies heavily on scRNA-seq dataset obtained from cell populations sorted at defined time points, and refined computational analysis, including trajectory and gene network inference using the established tools RNA velocity and SCENIC, respectively. The proposed model is partially validated by in situ staining experiments, including genetic labeling, which identified Pdgfra+ non-myogenic cells within the Myf5+ lineages, notably in association with extraocular muscles (EOM). The authors propose a myogenic origin for the connective tissue, in regions devoid of neural crest cells, and show that loss of Myf5 function causes an increase in the proportion of Sox9+ cells among Myf5+ lineage cells, which is consistent with a binary fate choice from Myf5+ progenitors. The authors tentatively identify signaling molecules and transcription regulators underlying both fate decisions and cell-cell communications between myogenic and non-myogenic cell populations.

The general message of the study offers a potentially new paradigm to study neural crest cell-independent mesodermal fate decision in the vertebrate head, and is thus poised to augment our understanding of craniofacial development, and potential diseases.

Unfortunately, there are shortcomings that strongly reduce enthusiasm for this manuscript. Strictly speaking, there is no clear demonstration for the existence of bipotent progenitors in the absence of clonal analysis. The study relies excessively on computational analysis of descriptive scRNA-seq datasets, with a general paucity of secondary experimental validation. The manuscript would benefit from a refined focus on the key point, and addition of validation for the initial conclusions, at the expense of somewhat convoluted analyses (e.g. Figs. 6 and 7)

We thank the Reviewer for their constructive comments. We have now provided additional in-situ validations on embryos and quantifications to support the in-silico analyses.

Author Response:

Evaluation Summary:

This paper will be of interest to researchers who perform single-molecule fluorescence imaging experiments as well as those who want to include machine learning in their data analyses. The authors have developed a machine learning algorithm that addresses some of the data analysis challenges in the field of single-molecule fluorescence imaging. The methods are rigorously benchmarked using simulated data and tested using real data. There are some concerns whether Tapqir is general enough for use by the broader community of single-molecule fluorescence researchers.

We thank the reviewers for their thorough review of the manuscript. In response to the reviewer comments, we posted to bioRxiv a revised manuscript with new data and edits to text. Concerns about generality are addressed in the revised manuscript and in the responses to specific reviewer comments below.

Reviewer #1 (Public Review):

"Bayesian machine learning analysis of single-molecule fluorescence colocalization images" by Ordabayev, et al. reports the development, benchmarking, and testing of a Bayesian machine learning-based method, which the authors name Tapqir, for analyzing single-molecule fluorescence colocalization data. Unlike currently available, more conventional analysis methods, Tapqir attempts to holistically model the microscopy images that are recorded during a colocalization experiment. Tapir uses a physics-based, global model with parameters describing all of the features of the experiment that are expected to contribute to the recorded microscopy images, including shot noise of the spots and background, camera noise, size and shape of the spots, and specific- and non-specific binders. Based on benchmarking on simulated data with widely varying properties (e.g., signal-to-noise; amounts, rates, and locations of specific and non-specific binders; etc.), Tapqir generally does as well and, in some cases, better than currently existing methods. The authors also test Tapqir on real microscopy images with similarly varying properties from studies that have been previously published by their research group and demonstrate that their Tapqir-based analysis is able to faithfully reproduce the previously published results, which were obtained using the more conventional analysis methods available at the time the data were originally published. This is a well-designed and executed study, Tapqir represents a conceptual and practical advance in the analysis of single-molecule fluorescence colocalization experiments, and its performance has been comprehensively and rigorously benchmarked on simulated data and tested on real data. The conclusions of this study are well supported by the data, but some of the limitations of the method need to be clarified and discussed in more depth, as outlined below.

1. Given that the AOI is centered at the target molecule and there is a strong prior for the binder also being located at the center of the AOI, the performance of Tapqir is dependent on several variables of the microscopy/optical system (e.g., the microscope point-spread function, magnification, accurate alignment of target and binder imaging channels, accurate drift correction, etc.). Although this caveat is mentioned and some of these factors are listed in the main text of the manuscript, the authors could have expanded this discussion in order to clarify the extent to which the performance of Tapqir depends on these factors.

We added relevant new data to the revised manuscript in Table 5. The question about alignment accuracy is now discussed in the Materials and Methods:

“Tests on data simulated with increasing proximity parameter values σxy (true) (i.e., with decreasing precision of spatial mapping between the binder and target image channels) confirm that the cosmos model accurately learns σxy (fit) from the data (Figure3–Figure Supplement 3D; Table 5). This was the case even if we substituted a less-informative σxy prior (Uniform vs. Exponential; Table 5).

The CoSMoS technique is premised on colocalization of the binder spots with the known location of the target molecule. Consequently, for any CoSMoS analysis method, classification accuracy will in general decline when the images in the target and binder channels are less accurately mapped. However, for the Tapqir cosmos model, low mapping precision has little effect on classification accuracy at typical non-specific binding densities (λ = 0.15; see MCC values in Table 5).”

The more general point about priors is now addressed in the Materials and Methods as follows:

“All simulated and experimental data sets in this work were analyzed using the prior distributions and hyperparameter values given above, which are compatible with a broad range of experimental conditions (Table 1). Many of the priors are uninformative and we anticipate that these will work well with images taken on variety of microscope hardware. However, it is possible that highly atypical microscope designs (e.g., those with effective magnifications that are sub-optimal for CoSMoS) might require adjustment of some fixed hyperparameters and distributions (those in Eqs. 6a, 6b, 11, 12, 13, 15, and 16). For example, if the microscope point spread function is more than 2 pixels wide, it may be necessary to increase the range of the w prior in Eq. 13. The Tapqir documentation (https://tapqir.readthedocs.io/en/stable/) gives instructions for changing the hyperparameters.”

1. The Tapqir model has many parameters, each with its own prior. The majority of these priors are designed to be uninformative and/or weak and the only very strong prior is the probability that a specific binder is located at or very near the center of the AOI. The authors could have tested and commented on how the strength of the prior on the location of a specific binder affects the performance of Tapqir.

The revised manuscript includes new data on and expanded discussion of this point. In our model, the position of a target-specific spot relative to the target position has a prior distribution illustrated as the green curve in Figure 2-Figure supplement 2. Importantly, the peak in this distribution does not have an a priori set width. Instead, the width of the peak is a model hyperparameter, σxy, that is learned from the image data set without user intervention. To make sure that this point is understood, we expanded and clarified the relevant Methods section and modified the legend of Figure 2-Figure supplement 2.

To address the reviewers’ specific question, we constructed simulated data sets with different mapping precision values and analyzed them; the results are presented in the (new) Table 5 and discussed:

“The CoSMoS technique is premised on colocalization of the binder spots with the known location of the target molecule. Consequently, for any analysis method, classification accuracy declines when the images in the target and binder channels are less accurately mapped. For the Tapqir cosmos model, low mapping precision has little effect on classification accuracy at typical non-specific binding densities (λ = 0.15; see MCC values in Table 5).”

1. Given the priors and variational parameters they report, the authors show that Tapqir performs robustly and seems to require no experiment-to-experiment optimization. This is expected to be the case for the simulated data, since they were simulated using the same model that Tapqir uses to perform the analysis. With regard to the real data, however, it is quite likely that this is due to the fact that the analyzed data all come from the same laboratory and, therefore, likely the same microscope(s). It would have therefore been very useful if the authors would have listed and discussed which microscope settings, experimental conditions, and/or other considerations, beyond those described in point 1 above, would result in a need for re-optimization of the priors and/or variational parameters.

As noted above, we now address this point in the Materials and Methods as follows:

“All simulated and experimental data sets in this work were analyzed using the prior distributions and hyperparameter values given above, which are compatible with a broad range of experimental conditions (Table 1). Many of the priors are uninformative and we anticipate that these will work well with images taken on variety of microscope hardware. However, it is possible that highly atypical microscope designs (e.g., those with effective magnifications that are sub-optimal for CoSMoS) might require adjustment of some fixed hyperparameters and distributions (those in Eqs. 6a, 6b, 11, 12, 13, 15, and 16). For example, if the microscope point spread function is more than 2 pixels wide, it may be necessary to increase the range of the w prior in Eq. 13. The Tapqir documentation (https://tapqir.readthedocs.io/en/stable/) gives instructions for changing the hyperparameters.”

1. Based on analysis of the simulated data shown in Figure 5, where the ground truth is known, the use of Tapqir to infer kinetics is less accurate that the use of Tapqir to infer equilibrium binding constants. The authors do a great job of discussing possible reasons for this. In the case of the real data analyzed in Figure 6 and in Figure 6 - Figure Supplements 1 and 2, the kinetic results obtained using Tapqir have different means and generally larger error bars than those obtained using Spot-Picker. To more comprehensively assess the performance of Tapqir versus Spot-Picker, the authors could have used the association and dissociation rates to calculate the corresponding equilibrium binding constants and then compared these kinetically calculated equilibrium binding constants to the population-calculated equilibrium binding constants that the authors calculate and report in the bottom plot in Panel D of Figure 6 and Figure 6 - Figure Supplements 1 and 2. This would provide some information on the accuracy of the kinetics in that the closer the kinetically and population-calculated equilibrium binding constants are to each other, the more accurately the kinetics have been estimated. Performing this type of analysis for the kinetics obtained using Tapqir and Spot-Picker would have allowed a more comprehensive comparison of the two methods.

This comment seems to reflect a misunderstanding. Fig. 6 and its figure supplements do not report any dissociation kinetics or binding equilibrium constants. Instead, they report ka (pseudo first-order target-specific association rate constant), kns (pseudo first-order target non-specific association rate constant), and Af (the active faction, i.e., the fraction of target molecules capable of association with binder). ka and Af values from the two methods agree within experimental uncertainty for all four data sets analyzed. kns values differ, but as we point out:

“We noted some differences between the two methods in the non-specific association rate constants kns. Differences are expected because these parameters are defined differently in the different non-specific binding models used in Tapqir and spot-picker (see Materials and Methods).”

(There is additional discussion of this point in Materials and Methods). The reviewer is correct that the estimated uncertainties (i.e., error bars in panels D) in ka and Af are generally larger for Tapqir than for spot-picker. This is expected, for the reasons that we explain:

“In general, previous approaches in essence assume that spot classifications are correct, and thus the uncertainties in the derived molecular properties (e.g., equilibrium constants) are systematically underestimated because the errors in spot classification, which can be large, are not accounted for. By performing a probabilistic spot classification, Tapqir enables reliable inference of molecular properties, such as thermodynamic and kinetic parameters, and allows statistically well-justified estimation of parameter uncertainties. This more inclusive error estimation likely accounts for the generally larger kinetic parameter error bars obtained from Tapqir compared to those from the existing spot-picker analysis method (Figure 6, Figure 6–Figure Supplement 1, Figure 6–Figure Supplement 2, and Figure 6–Figure Supplement 3). ”

Reviewer #2 (Public Review):

The work by Ordabayev et al. details a Bayesian inference-based data analysis method for colocalization single molecule spectroscopy (CoSMoS) experiments used to investigate biochemical and biophysical mechanisms. By using this probabilistic framework, their method is able to quantify the colocalization probabilities for individual molecules while accounting for the uncertainty in individual binding events, and accounting for camera and optical noise and even non-specific binding. The software implementation of this method, called Tapqir, uses a Python-based probabilistic programming language (PPL) called pyro to automate and speed-up the optimization of a variational Bayes approximation to the posterior probability distribution. Overall, Tapqir is a powerful new way to analyze CoSMoS data.

Tapqir works by analyzing small regions (14x14 pixels) of fluorescence microscopy images surrounding previously identified areas of interest (AOI). The collection of images of these AOIs through time are then analyzed collectively using a probabilistic model that accounts for each time frame of each AOI and is able to determine whether up to K "binders" (K=2 here) are present and which of them is specifically bound. This approach of directly modeling the contents of the image data is relatively novel, and few other examples exist. The details of the probabilistic model used incorporate an impressive amount of physical insight (e.g., camera gain) without overparameterization.

We thank the reviewer for these positive comments.

The gamma-distributed noise model used in Tapqir captures quite a lot of physics and, given the analyses in Figs. 3-6, clearly works, but might be limited to certain types of cameras used in the fluorescence microscopy (e.g., EMCCDs). For instance, sCMOS cameras have pixel-dependent amplification and noise profiles, rather than a single gain parameter, and are sometimes approximately modeled as normal distributions with both mean and variance having an intensity-dependent and independent contribution that is different for each pixel on the camera. It is unclear how Tapqir performs on different cameras.

In the revised manuscript, we expanded the discussion of the Image likelihood component of our model to emphasize that 1) all data sets we analyze are experimental or simulated EMCCD images, 2) sCMOS images have the different noise characteristics alluded to by the reviewer, and 3) optimal sCMOS image analysis might require a modified model, possibly including the ability to use per-pixel calibration data as a prior as was done in super-resolution work (now cited) that uses sCMOS data.

sCMOS cameras have in recent years become very popular for some kinds of single-molecule imaging (e.g., PALM/STORM or live-cell single-particle tracking). However, for the low-background/low-signal in vitro single-molecule TIRF that is our target application for the approach described in the manuscript, EMCCD is still preferable over sCMOS for many, but not all, imaging conditions (see https://andor.oxinst.com/learning/view/article/what-is-the-best-detector-for-single-molecule-studies). Thus, we think there will be plenty of interest in the approach we describe in the manuscript even if (which is not certain) the program functions better with EMCCD than with sCMOS images.

Going forward to develop and test an sCMOS-targeted version of the model, as we have done for EMCCD, will require revised model and code, but will also necessitate accurately simulating sCMOS CoSMoS images, obtaining experimental sCMOS CoSMoS images reflecting a broad range of realistic experimental conditions, and using the simulated and experimental images to test the new model. These may well be useful things to do in the future but would be a considerable step beyond the scope of the present manuscript.

The variational Bayes solution used by Tapqir provides many computational benefits, such as numerical tractability using pyro and speed. It is possible that the exact posterior, e.g., as obtained using a Markov chain Monte Carlo method, would be insignificantly different with the amount of data typical for CoSMoS experiments; however, this difference is not explored in the current work.

We agree. However, since we have not done any analyses using MCMC, there is nothing in particular that we can say about it in the context of CoSMoS data analysis. Implementation of an MCMC approach using our model will be easier in the future because the Pyro developers are currently working to optimize the implementations of MCMC methods in their software.

The intrinsic use of prior probability distributions in any Bayesian inference algorithm is extremely powerful, and in Tapqir offers the opportunity to "chain together" subsequent analyses by using the marginalized posteriors from one experiment as the basis for the priors for subsequent experiments (e.g., in \sigma^{xy}) for extremely high accuracy inference. While the manuscript discusses setting and leveraging the power of priors, it does not explore the power of such "chaining" and the positive effects upon accuracy.

Chaining is beneficial in principle. However, in practice it will help significantly only if the uncertainty in the posterior parameter values from the non-chained analysis is larger than the experiment-to-experiment variability in the “true” parameter values. For σxy we obtain very narrow credence intervals without chaining (Table 1). In our judgement, these are unlikely to be made more accurate by using prior information from another experiment where such factors as microscope focus adjustment may be slightly different.

A significant number of CoSMoS experiments use multiple, distinct color fluorophores to probe the colocalization of different species to the target. The current work focuses only upon analyzing data with a single color-channel. Extensions to multiple independent wavelengths are computationally trivial, given the automated variational inference ability of PPLs such as pyro, and would increase the impact of the work in the field.

Our current approach can be used to analyze multi-channel data simply by analyzing each channel independently. However, we agree that there would be advantages to joint analysis of multiple wavelength channels (especially if there is crosstalk between channels) and that implementing multi-channel analysis is a logical extension of our study. It is straightforward (though not trivial, in our experience) to implement such multi-wavelength models. However, testing the functioning of candidate models and validating them using simulation and experimental data would require extensive work that in our view goes beyond what is reasonable to include in the present manuscript.

Tapqir analysis provides time series of the probability of a specific binding event, p(specific), for each target analyzed (c.f., Fig. 5B), and kinetic parameters are extracted from these time series using secondary analyses that are distinct from Tapqir itself.

The method reported here is well designed, sound, and its utility is well supported by the analyses of simulated and experimental data sets reported here. Tapqir is a cutting-edge image analysis approach, and its proper treatment of the uncertainty inherent to CoSMoS experiments will certainly make an impact upon the analysis of CoSMoS data. However, many of the (necessary) assumptions about the data (e.g., fluorescence microscopy) and desired information (e.g., off-target vs on-target binding) are quite specific to CoSMoS experiments and therefore limit the direct applicability of Tapqir for the analysis of other single-molecule microscopy techniques. With that in mind, the direct Bayesian inference-based analysis of image data, as opposed to integrated time series, as demonstrated here is very powerful, and may encourage and inspire related methods to be developed.

Our approach is a powerful way to analyze CoSMoS data in part because it is specific to CoSMoS – it is premised on a physics-based model that incorporates known features of CoSMoS experiments. We agree that the general approach could be adapted to other image analysis applications.

Reviewer #3 (Public Review):

In this manuscript, the authors seek to improve the reproducibility and eliminate sources of bias in the analysis of single molecule colocalization fluorescence data. These types of data (i.e., CoSMoS data) have been obtained from a number of diverse biological systems and represent unique challenges for data analysis in comparison with smFRET. A key source of bias is what constitutes a binding event and if those events are colocalized or not with a surface-tethered molecule of interest. To solve these issues, the authors propose a Bayesian-based method in which each image is analyzed individually and locally around areas of interest (AOIs) identified from the surface tethered molecules. A strength of the research is that the approach eliminates many sources of bias (i.e., thresholding) in analysis, models realistic image features (noise), can be automated and carried out by novice users "hands-free", and returns a probability score for each event. The performance of the method is superb under a number of conditions and with varying levels of signal-to-noise. The analysis on a GPU is fairly quick-overnight-in comparison with by-hand analysis of the traces which can take days or longer. Tapqir has the potential to be the go-to software package for analysis of single molecule colocalization data.

The weaknesses of this work involve concerns about the approach and its usefulness to the single-molecule community at large as wells as a lack of information about how users implement and use the Tapqir software. For the first item, there are a number of common scenarios encountered in colocalization analysis that may exclude use of Tapqir including use of CMOS rather than EM-CCD cameras, significant numbers of tethered molecules on the surface that are dark/non-fluorescent, a high density/overlapping of AOIs, and cases where event intensity information is critical (i.e., FRET detection or sequential binding and simultaneous occupancy of multiple fluorescent molecules at the same AOI). In its current form, the use of Tapqir may be limited to only certain scenarios with data acquired by certain types of instruments.

In the following paragraphs, we address 1) concerns about application to CMOS, 2) dark target molecules, 3) overlapping AOIs, and 4) application to methods (e.g., smFRET) that require extraction of both colocalization and intensity data.

1) Application to CMOS images.

In the revised manuscript, we expanded the discussion of the Image likelihood component of our model to emphasize that 1) all data sets we analyze are experimental or simulated EMCCD images, 2) sCMOS images have the different noise characteristics alluded to by the reviewer, and 3) optimal sCMOS image analysis might require a modified model, possibly including the ability to use per-pixel calibration data as a prior as was done in super-resolution work (now cited) that uses sCMOS data.

sCMOS cameras have in recent years become very popular for some kinds of single-molecule imaging (e.g., PALM/STORM or live-cell single-particle tracking). However, for the low-background/low-signal in vitro single-molecule TIRF that is our target application for the approach described in the manuscript, EMCCD is still preferable over sCMOS for many, but not all, imaging conditions (see https://andor.oxinst.com/learning/view/article/what-is-the-best-detector-for-single-molecule-studies). Thus, we think there will be plenty of interest in the approach we describe in the manuscript even if (which is not certain) the program functions better with EMCCD than with sCMOS images.

Going forward to develop and test an sCMOS-targeted version of the model, as we have done for EMCCD, will require revised model and code, but will also necessitate accurately simulating sCMOS CoSMoS images, obtaining experimental sCMOS CoSMoS images reflecting a broad range of realistic experimental conditions, and using the simulated and experimental images to test the new model. These may well be useful things to do in the future but would be a considerable step beyond the scope of the present manuscript.

2) Dark target molecules.

In their detailed comments, the reviewers suggested a “no target molecules in sample” (NTIS) control instead of the “no fluorescent target molecules in control AOIs” (NFTICA) design that we illustrate in Fig. 1. Both types can be used as a Tapqir control dataset without any modification of the program or model. We have edited the Fig. 1 caption to explain that either type is acceptable. The reviewers are correct that, all else being equal, NTIS may be better if the target molecules are incompletely labeled. However, in practice experimenters usually know the fraction of molecules that are labeled and reduce the fluorescent target molecule surface density to hold the fraction of spots with two or more coincident target molecules (fluorescent or not) below a chosen threshold (typically 1 % or less), negating the possible advantage of NTIS (but at the expense of collecting less data per sample). On the other hand, NFTICA has the practical advantage that it is a control internal to the sample and is thus immune to problems caused by temporal or sample-to-sample variability (e.g., of surface properties).

3) Overlapping AOIs.

The method does not require non-overlapping AOIs – we used partially overlapping AOIs in the experimental data analyzed in the manuscript. Even though our analysis used larger AOI sizes (and hence, more overlap) than the spot-picker method, there was good agreement in the results, indicating that overlap does not cause any undue problems.

In the revised manuscript Results section we added the following discussion of the effect of AOI size:

“Since target-nonspecific spots are built into the cosmos model, there is no need to choose excessively small AOIs in an attempt to exclude non-specific spots from analysis. We found that reducing AOI size (from 14 x 14 to 6 x 6 pixels) did not appreciably affect analysis accuracy on simulated data (Table 2). In analysis of experimental data, smaller AOI sizes caused occasional changes in calculated p(specific) values reflecting apparent missed detection of a few spots (Figure 3–Figure supplement 4). Out of caution, we therefore used 14 x 14 pixel AOIs routinely, even though the larger AOIs somewhat reduced computation speed (Table 2 and Figure 3–Figure Supplement 4).”

4) Methods requiring extraction of intensity data.

The cosmos model we describe in the manuscript does not incorporate phenomena where the spot intensity at a single target changes, such as when there is FRET or multiple binders. As we point out in the final paragraph of the Discussion, more elaborate versions of the cosmos model that incorporate these phenomena could be developed. This would entail implementation, optimization, and validation with simulations and real data of the new model, which is beyond the scope of the present manuscript.

Second, for adoption by non-expert users information is missing in the main text about practical aspects of using the Tapqir software including a description of inputs/outputs, the GUI (I believe Taqpir runs at the command line but the output is in a GUI), and if Tapqir integrates the kinetic modeling or not.

This information is given in the online Tapqir documentation. The kinetic analysis (as in Fig. 6) is a simple Python script that is run after Tapqir; the instructions for using it are included in the documentation. Tapqir runs can be initiated using either a CLI or GUI. Output can be viewed in Tensorboard, in a Tapqir GUI, and/or passed to a Jupyter notebook or Python script for further analysis, plotting, etc.

Given that a competing approach has already been published by the Grunwald lab, it would be useful to compare these methods directly in both their accuracy, usefulness of the outputs, and calculation times.

The reviewer does not explain why comparing with the Grunwald method would be preferable to the comparison with spot-picker that is included in the manuscript. To be sure there is no misunderstanding, the following are the same for the two methods and therefore are not reasons to prefer one or the other of these methods for the comparison in Fig. 6 (see also Discussion):

1) Like Tapqir, both spot-picker and Grunwald methods analyze 2-D images, not integrated intensities.

2) Unlike Tapqir, neither spot-picker nor Grunwald is fully objective; both require subjective selection of classification thresholds by the analyst in order to tune the algorithm performance for analysis of a particular dataset.

3) Neither spot-picker nor Grunwald is a Bayesian method. “Bayesian” in the Grunwald paper title refers to their excellent work on a separate analytical method (described in the same paper) for evaluating the number of binder molecules colocalized with a target spot; this method is not relevant to a comparison with the model presented in our manuscript.

4) Unlike Tapqir, neither spot-picker nor Grunwald estimate classification probabilities. Instead, they simply assign binary spot/no-spot classifications that do not convey to downstream analyses the extent of uncertainty in each classification.

5) Neither spot-picker nor Grunwald has been validated previously using simulated image data. Consequently, the validity of image classification has not been established for either.

The comparison of Fig. 6 and supplements does not claim to and is not intended to show that Tapqir is better than spot-picker for real experimental data; we cannot make such a claim for these or any other methods because we do not know the true kinetic process and rate constants that generated the experimental data. Instead, our comparison uses experimental data sets with a broad range of characteristics (Table 1) to show that Tapqir yields similar association rate constants to those produced by spot-picker even though the former is objective and automatic while the latter requires subjective tuning by an analyst. Our choice to use spot-picker over Grunwald for this comparison was dictated by the fact that among the co-authors we have such an expert in the use of spot-picker, whereas we lack comparable expertise with Grunwald. We have little doubt that Grunwald would also produce results similar to the other methods in the hands of an expert user who is able to subjectively adjust classification parameters.

Along these lines, the utility of calculating event probability statistics (Fig. 6A) is not well fleshed-out. This is a key distinguishing feature between Tapqir and methods previously published by Grunwald et al. In the case of Tapqir, the probability outputs are not used to their fullest in the determination of kinetic parameters. Rather a subjective probability threshold is chosen for what events to include. This may introduce bias and degrade the objective Tapqir pipeline used to identify these same events.

This comment reflects a misunderstanding. No probability threshold is used in the kinetic analyses (Figs. 5 and 6). Instead, we make full use of the p(specific) probability output using the posterior sampling strategy that is illustrated in Fig. 5B and is described in the Results and in Materials and Methods. In the revised manuscript we modified the Results section to further emphasize this point.

Finally, the manuscript could be improved by clearly distinguishing between the fundamental approach of Bayesian image analysis from the Tapqir software that would be used to carry this out.

We have revised the manuscript to adopt this recommendation. We now call the mathematical model “the cosmos model” and use “Tapqir” to refer to the software.

A section devoted to describing the Tapqir interface and the inputs/outputs would be valuable. In the manuscript's current form, the lack of information on the interface along with the potential requirement for a GPU and need for the use of a relatively new programming language (Pyro) may hamper adoption and interest in colocalization methods by general audiences.

Description of the interface and inputs/outputs is given in the online Tapqir documentation.

Users do not need to own a GPU; they can instead run the program on a readily available cloud computing service. We have now added to Table 1 data showing that computation time on the Google Colab Pro cloud service is actually faster than that on our local GPU system. Colab Pro is inexpensive, readily accessible, and user friendly. We have added to the user manual a tutorial that shows how to run a sample data set using Tapqir on Colab.

Users do not need any knowledge of Pyro to use Tapqir; Pyro is merely used internally in the coding of Tapqir.

Author Response

Evaluation Summary:

In this manuscript, the authors provide promising results for the treatment of age-related sarcopenia with AdipoRon, a drug that targets the receptors for adiponectin. This is a well done study using an agonist (AdipoRon) involved in lipid and mitochondrial metabolism regulation to mitigate age related muscle loss in mice.

Thank you for these positive comments – we are excited about the potential of this agent as a means to prevent and treat sarcopenia.

Reviewer #1 (Public Review):

Strengths and Accomplishments:

1) This study tests an exciting potential intervention for sarcopenia, is well supported by prior literature investigating the effects of AdipoRon in age-related metabolic diseases, and now extends these data into aging.

2) The study uses a diversity of techniques and systems (in vitro, in vivo, and ex vivo, chronic and acute treatments, young and old mice) to investigate the effects and relevant mechanisms of AdipoRon from the level of the whole organism into the muscle fibers and further into cellular signaling pathways.

3) Similar cellular findings across species and cell types argues for strong conservation of the downstream effects of AdipoRon.

4) This study provides coherent and conserved downstream molecular mechanisms (e.g. PGC-1a) and physiological changes (fiber types, mitochondrial function, insulin sensitivity) that should be readily translatable into mechanistically-designed non-human primate and human clinical studies.

5) The presentation is well organized and logical, showing the effects of chronic AdipoRon treatment in old and then young male mice, followed by acute treatment in young mice and cells, moving from clinical to physiological to cellular/molecular findings.

We thank the reviewer for these comments and are eager to continue our work in this area – the absence of a pharmacological agent to treat sarcopenia is a major gap in geriatric and rehabilitation medicine.

Weaknesses and Limitations:

1) The key mouse studies are underpowered, resulting in inconclusive rotarod data in the aged group and no behavioral testing in the young group. There is no other whole-organism functional data to support the clinical relevance of the ex vivo and postmortem physiological and molecular findings.

We acknowledge that this study is a first step toward identifying an agent to prevent and treat sarcopenia. As this reviewer will appreciate it can be challenging to overcome the natural increase in variance that occurs with age, the upshot is that the magnitude of effect needs to be quite large to find statistically significant outcomes when conducting comparisons among aged animals. We are careful to distinguish between statistically significant differences and those that are numerically different. We would argue that the absence of statistical significance does not mean that an observation is not informative or biologically meaningful. We would like to add that the data described here prompted a follow up study in male and female mice where our plans include more extensive investigation of the functional, tissue-level, and systemic outcomes of AdipoRon treatment. In addition, we have applied for funding to support a nonhuman primate study on the impact of AdipoRon on sarcopenia, physical function, and metabolism, that we anticipate will have greater translational value.

2) The in vitro cellular use fibroblasts and immune cells, which supports an argument for broad conservation of AdipoRon mechanisms but does not directly support the primary muscle physiological findings.

The purpose of including the cell culture experiments was to define the cellular response to AdipoRon and to determine whether indices such as gene expression that hinted at changes in metabolism were actually associated with functional differences in cellular energetics. In response to this comment and comments from the other reviewers, we have conducted experiments in differentiated C2C12 myotubes and confirm that the molecular signatures initially reported in the fibroblasts and primate PBMCs are also induced in the murine myotube culture model in response to AdipoRon. We fully acknowledge that differentiated C2C12, being “muscle like”, are a better model for interrogating the mechanisms of AdipoRon action as they relate to skeletal muscle specifically.

3) Using different strains for young and old mice limits the interpretation of young vs old differences, which could be due to strain differences instead.

We appreciate this point; at the time that this work was undertaken we were constrained by what was available. We would note that we see the same responses to AdipoRon in our ongoing study that was conducted in a C3B6F1 hybrid line and included mice of 6, 22, and 28 months of age. We are confident that the results described here are genuinely reflective of the actions of AdipoRon as a function of age of the treated mouse and not due to differences in mouse genetic background.

Reviewer #2 (Public Review):

This is a straightforward study, demonstrating utility of an agonist targeting energy metabolism pathways in aging mouse muscle. Rather than the treatment improving muscle function generally, it appears selective to muscles predominantly affected by age-related muscle loss (type II fibers). As the authors acknowledge, these results need to be replicated in females, as they only looked at male mice.

We agree that it will be important to follow up this study using a cohort with males and females (see response to Reviewer 1 comment 1 above). Interestingly, our nonhuman primate studies have indicated that there is sex dimorphism in skeletal muscle aging. Males are bulkier and with greater gains there are apparently greater losses as the animals advance in age. The females show less of a decline in total muscle with age than males in terms of DEXA estimates of appendicular muscle bulk; however, at the cellular and molecular level it is clear that aging is having an impact. We have identified improvements in metabolic indices including fasting insulin and RER in mice treated with AdipoRon, and improvement in endurance treadmill performance that was significant in AdipoRon treated males. That study, that includes more animals and two aging time points, will allow for detailed tissue and molecular level analysis so that we can identify which processes are sensitive to aging and to AdipoRon and track those pathways against physical performance at the individual level.

Reviewer #3 (Public Review):

In this manuscript the authors sought to investigate whether an adiponectin-receptor agonist could reduce the incidence of sarcopenia in aged mice. The authors provide compelling evidence that AdipoRon improves skeletal muscle function in aged mice, remodels muscle fibers, and appears to improve mitochondrial function at least in vitro.

The authors provide multiple lines of evidence for the effects of AdipoRon, from live measurements of muscle function in aged rodents, to ex-vivo muscle activity assays, to in vitro assessment of mitochondrial function and activation of pathways involved in mitochondrial remodeling.

The experiments complement one another very well, though it is unclear why two different strains were used for young and old mice, nor why the analysis was restricted to male animals only.

Overall, the study details a promising intervention to restore muscle function in elderly individuals and identifies a druggable pathway that can be exploited for this goal.

We thank the reviewer for these positive remarks. We acknowledge the limitation of looking only at male mice at this stage and have undertaken a follow up study that includes both sexes. The use of AdipoRon was inspired by our work in caloric restriction where adiponectin increase is a hallmark of CR in rodents and in nonhuman primates. At the time that this work began we had access to these aged male mice from NIA but the young mice came from an internal colony. We are eager to share these data in the hope that others will be interested in testing AdipoRon as a means to prevent or treat sarcopenia and would love to see studies in rehabilitative research being undertaken too.

Author Response:

Reviewer #2 (Public Review):

The authors have developed a new method that allows for two-color STED imaging. They have applied this method to measure spine head size and PSD95 changes following exposure to an enriched environment.

Strengths

-The new method is well-described and seems to have considerably less crosstalk than previous attempts at in vivo two-color STED imaging. The analyses and controls of the method are compelling. I think that this method could be valuable for examining how different components of the synapse are changing in response to sensory or environmental changes.

-The method is appropriate for measuring the size of PSD95 and spine head size in the enriched environment paradigm they use here. They find that in the short-term spine head size and PSD95 size are not always correlated.

-They also find that there is less variability in the spine head size in animals in an enriched environment.

Weaknesses<br /> -The authors use an enriched environment plasticity paradigm to showcase the method and measure spine head and PSD95 size and how they change over short periods of time. This particular biological study is not well-motivated and there is not a stated reason for studying the short-term (30-120 minutes) dynamics of PSD95 and spine head size, and their correlations. They also show that the variability in spine head size is decreased with the enriched environment, but do not show what the implications of that change would be from a biological point of view for synaptic dynamics or synaptic function.

-The authors show that there are differences in the morphology of PSD95 between mice reared in enriched environments and those in control environments. While this quantification is done blindly by three different analysts, it is not done in a quantitative way. Also the authors do not show or explain the biological relevance of differences in the morphologies of PSD95, thus it is not clear what this measure means for synaptic plasticity or function.

-The authors use a cranial window preparation, which is commonly used in the literature. However, it is not clear how long they wait to image the mice after the cranial window. Previous work from Xu et al. (PMID: 17417634) suggests that there is in an increase in glial activation for a period of up to a month after surgery. The authors have not shown the degree of glial activation that follows after their surgeries and if they have not waited a month, there may be upregulation of microglia, which may alter synaptic stability (also demonstrated in the same paper). The authors have not discussed this point or the implications for their findings.

We thank the reviewer for his/her valuable input.

The time-scale we study is similar to what is known from structural changes after LTP and thus we wanted to study the same time scale in vivo. We revised the motivation and explained better the biological relevance of the observed changes. We absolutely agree with the reviewer on his/her concern for chronic imaging. However, we performed acute experiments and imaged directly after implanting the window in the same session. After imaging the mice were sacrificed.

Reviewer #3 (Public Review):

Wegner et al. use two-color STED to follow spines and their PSDs in layer1 of mouse visual cortex over 2 hours under anesthesia. They compare mice that were kept in an enriched environment (EE) to control mice housed in standard laboratory cages. Spines in EE mice are larger and show larger fluctuations in size. PSDs in EE mice shrink during anesthesia and tend to change their nanostructure. Very importantly, changes in spine size were not driven by PSD size changes, or vice versa. Technologically, this is a landmark study, as tracking two different labeled structures in individual synapses at the nanoscale can obviously be applied to a large number of synaptic proteins and organelles, two at a time. Single-color superresolution microscopy is much less useful, as 'puncta in space', without cellular context, are difficult to interpret. This pioneering work is the first proof-of-concept of two-color in-vivo STED and of major importance for the community. Although stochastic processes seem to drive much of the synaptic dynamics under anesthesia, the environment shapes the spine size distribution and affects synaptic dynamics in a lasting fashion.

One major comment:

l.259: "These results suggest that Ctr housed mice undergo stronger morphological changes." This I find a bit misleading. What about: These results suggest that anesthesia induces stronger morphological changes in Ctr housed mice? Altogether, a discussion of the potential effects of anesthesia on spine/PSD dynamics is missing (see e.g. Yang et al., DOI: 10.1371/journal.pbio.3001146). The fact that there was weak correlation between spine head and PSD fluctuation could have something to do with the state of suppressed activity the system was in during imaging. Under conditions of intense processing of visual information, changes might have been more rapid and more tightly correlated. This could be mentioned as a perspective for the future - to visually stimulate the anesthetized animal.

We agree with the reviewer that it should be mentioned here that the morphological change was observed under anesthesia. However, the sentence suggested by the reviewer is also a bit misleading since it suggests that the anesthesia has triggered the change. We think that anesthesia might affect the amplitude and dynamic of the observed changes but does not induce the change. Thus we rephrased as follows: These results suggest that Ctr housed mice undergo stronger morphological changes under anesthesia.

We absolutely agree about the potential influence of the anesthesia on the spine and PSD95 nanoplasticity and added the following comment. Of course, we would like to perform the measurement in the future also in awake mice and after visual stimulation.

Added to discussion: However, it was shown that MMF anesthesia reduces spiking activity and mildly increases spine turnover in the hippocampus (Yang et al., 2021). Thus, the plasticity of spine heads and PSD95 assemblies might be different in the awake state and under intense processing of visual information.

Author Response:

Reviewer #2 (Public Review):

The reported study includes an overall well-conducted and well-presented set of experiments. Ample data are reported and a clear and conclusive picture of the findings is portrayed.

1. The Introduction falls short of providing the background needed for fully appreciating the current findings and their importance. The authors don't present the current understanding regarding the role of 4-vinylanisole in locusts (mostly their own work). Nor do they present the accepted knowledge of the control of sexual maturation in locusts (mostly several decades-old work). Moreover, the importance of reproductive synchrony in the life history of gregarious locusts, including its tentative roles in maintenance of the homogeneity and integrity of the swarm, in ensuring high density conditions for the next generation, and more, is also not adequately presented.

We appreciate the reviewer’s helpful comments. According to these comments, we have revised the introduction part by enriching the significance of reproductive synchrony in ecological adaption of gregarious locusts and the research progresses on sexual maturation control in locusts. Details were shown as: “Depending on population density, locusts display striking phenotypic plasticity, with a cryptic solitarious phase and an active gregarious phase (Wang and Kang, 2014). Gregarious locusts, compared to solitarious conspecifics, show much higher synchrony in physiological and behavioral events, such as egg hatching and sexual maturation, as well as synchronous feeding and marching behaviors (Norris, 1954, Uvarov, 1977). Reproductive synchrony in gregarious locusts provides benefits for individuals in several aspects, such as more favorable microenvironment, lower risk of predation, efficiently forging, as well we more encounters with mates, therefore ensures high density conditions for the next generation, and is essential for maintenance of locust swarm (Beekman et al., 2008, Maeno et al., 2021). Some sort of vibratory stimulus, maternal microRNAs, and SNARE protein play important roles in the egg-hatching synchrony of gregarious locusts (Chen et al., 2015b, He et al., 2016, Nishide and Tanaka, 2016). It has been revealed that the presence of mature male adults has effectively accelerating effects on synchrony of sexual maturation of immature male and female conspecifics in two locust species, Schistocerca gregaria and Locusta migratoria (Norris, 1952, Loher, 1961, Guo and Xia, 1964, Norris, 1964). The accelerating effects of several prominent volatiles released by gregarious mature males in male maturation have been exampled in the desert locust. Four volatile pheromones (benzaldehyde, veratrole, phenylacetonitrile, and 4-vinylveratrole) have significantly stimulatory effects on sexual maturation of male adults, with phenylacetonitrile having the most pronounced effect. (Mahamat et al., 1993, Assad et al., 1997). However, how conspecific interaction affects female sexual maturation remains unclear and the pheromones those contribute to maturation synchrony of females have not been determined so far”. In the current study, we identify 4-vinylanisole as a key pheromone promoting sexual maturation synchrony through validating the role of five gregarious male-abundant volatiles one by one, instead of following up our previous work on 4-VA. Thus, we have fully elaborated the multifunction of 4-VA as both aggregation pheromone and maturation accelerating pheromone in the formation and maintenance of locust swarm in the discussion part.

2. Research on pheromonal signaling in locusts have traditionally focused on compounds with a putative role in density-dependent phase-specific behaviors. Hence, it is common to compare the response of crowd-reared vs. solitary locusts to applied chemicals. The challenge, however, is maintaining the density context, while attempting to conduct controlled similar experiments with locusts of the two phases (i.e. keeping the solitary phase locusts isolated, while the gregarious locusts must always be crowded). This is even more challenging when studying reproductive physiology. By the basic nature of the two phases, there can be a multitude of interacting factors (behavioral and/or physiological) affecting the much-desired reproductive synchronization in gregarious locusts, while such synchronization is not expected at all in solitary ones (it may even be claimed to have no fitness-related advantage).

3. In general, the authors of the current report have dealt well with these challenges, taking extra care to conduct multiple controls and making an effort to specifically test all the possible factors. However, there are several points that raise some uncertainties. For example:

o If I am not mistaken, females of both phases were included in the study only if already mated by day A+7 (LL355-357). While this is reasonable for gregarious locusts, it may not be suitable for the solitary locusts, imposing an undesired and unequal selection criterion.

We thank the reviewer’s comments. We don’t think the criterion (mated at PAE 6-7 days) cause significant bias in either gregarious locusts or solitarious locusts. In fact, the limitation of mating before PAE 7 days is used to rule out the effects on oviposition synchrony caused by difference in mating age among individuals. This criterion is only limited during the analysis of the first oviposition date. On the premise of consistent mating time, oviposition consistency in gregarious female adults may largely present the sexual maturation synchrony among individuals (Figure 1A). For subsequent experiments, we mainly concentrate on regulation of sexual maturation using only virgin females in all experiments.

o In the test of the effects of conspecifics interactions, 10 gregarious locusts provided stimulation to the tested gregarious female, while only one insect was the stimulating factor for the solitary female.

Actually, we carried out two independent experiments to test the effects of conspecifics interactions. The population densities were kept in solitarious context for comparison of female sexual maturation synchrony between typical gregarious and solitarious phases (Figure 1D). For locust emissions treatments, ten solitarious locusts were used to ensure the stimulations at the same density level (Figure 1F). Both of two experiments suggested that solitarious male adults had no effects on female sexual maturation.

o It is not clear how were egg pods attributed to specific gregarious females (maintained in groups of 10)

Thanks for the reviewer’s comments. To monitor the oviposition activities of each individual of gregarious females in a group, locusts were individually marked, and their first oviposition times were determined by collecting egg pods every 4 hours per day after mating. Females those laid new eggs could be easily distinguished by much thinner abdomen with white foam around ovipositor. We have provided the method details in the revised manuscript.

Overall, since the focus of this study is actually not on the comparison between the phases, it might have been beneficial to the readers if the focus was on the gregarious locusts only, with maybe a couple of experiments conducted on solitary insects and presented separately.

We understand the reviewer’s concern. Actually, the aim of this study is to explore the mechanism underlying sexual maturation synchrony by comparing phase- and sex-dependent conspecific interactions in locusts. The reproductive synchrony in gregarious might be not highlighted without comparison with solitarious locusts, including both first oviposition time and sexual maturation, although the mechanism studies were mostly performed in gregarious locusts. Moreover, phase-dependent comparison of volatile contents is helpful for us to screen candidate volatiles responsible for the acceleration of sexual maturation synchrony in females.

4. Assuming that within a locust group there is overall agreement in the age of males and females, there seem to be a not-fully-explained mismatch between the age of max 4-VA release by males (linearly increasing with age) and the age of max effect in females (critical period at A+3-4)

We appreciate the reviewer’s query. We have provided additional discussions on the “mismatch” of between age-dependent release of 4-VA by males and the age of max effect in females (PAE 3-4 days). Details were shown as: “. We find that the release of 4-VA by gregarious males continuously increased after adult eclosion, with maximal 4-VA release at PAE 8 days. The age of maximal 4-VA production outwardly seems to be unmatched with the sensitive developmental stage to 4-VA of females (PAE 3-4 days). In insects, it is very common for males to mature earlier than females (Alonzo, 2013). In the locust, male adults also display earlier sexual maturation for several days, compared to females. In given locust population, individuals emerge to adults successively in a couple of days, not in completely synchronous period. Therefore, age-dependent increase in 4-VA release in gregarious male adults presents a persistent stimulus for less-developed young female adults, and thus maximizes synchronous maturation of female locusts, which could reduce male competitions for mate selection”.

5. Similar to the introduction, the discussion section also does not present comprehensive arguments regarding the importance of reproductive synchronization in female locusts. Points that could have been discussed include: females' oviposition disrupting migration, synchronization affecting sexual selection, accelerating intra-sex competition over mates as well as oviposition sites, and more.

We appreciate the reviewer’s nice suggestions. We have provided additional discussions on this point following these suggestions. Details were shown as: “Reproduction synchrony involves consistence in maturation, mating, and egg laying, among which sexual maturation synchrony serves as the most foundational step for oviposition uniformity (Hassanali et al., 2005). Extremely high energy cost for female reproduction could restrict migration to pre, post, or inter oviposition period in locusts, thus have crucial effects on collective movement of local populations (Min et al., 2004). Given this, a balance of sexual maturation timing among female members presents an essential subject for maintenance of locust swarms. We here demonstrated that young female adults reared with older gregarious male adults show faster and more synchronous sexual maturation in the migratory locust, supporting the accelerate role of crowding in sexual maturation of females (Guo and Xia, 1964, Norris and Richards, 1964,). Together with the accelerating effects on immature male sexual maturation induced by older gregarious male adults reported previously (Torto et al., 1994, Mahamat et al., 2000), young adults of both sexes lived in gregarious conditions prefers more synchronous maturation than individuals reared in solitary. The consistent maturation in both sexes will greatly reduce intra- and inter-sexes competitions for mate selection and thus ensures reproductive synchronous in whole locust populations. We demonstrated that a single minor component (4-VA) of the volatiles abundantly released by gregarious male adults is sufficient to induce the maturation synchrony of female adults. By comparison, four volatiles (benzaldehyde, veratrole, phenylacetonitrile, and 4-vinylveratrole) showed stimulatory effects on male maturation (Mahamat et al., 2000). Thus, there might exist a sex-dependent action modes of maturation-accelerating pheromones: multi-component pheromones for males and single active component for females, possibly due to different selective pressures between two sexes in response to social interaction. Further exploration will be performed to confirm this hypothesis by determining whether 4-VA has maturation-accelerating effects on male adults in the migratory locust in future”.

Reviewer #3 (Public Review):

Strengths: Grouping behavior for marching, sexual maturation, swarming, oviposition and egg hatching in gregarious locusts is complex and it's mediated by a combination of cues-olfactory, tactile, and visual cues to ensure synchronous behavior. The authors show that only olfactory cues released by gregarious adult males mediates maturation synchrony of females. This finding is a confirmatory result of a well-established phenomenon for maturation synchrony in both sexes of adult locusts, although in this study, the authors focused on only females. Further, the authors validated their findings using gene editing techniques to show that maturation synchrony was diffused in Or35-/- mutant adult females but not in wild type females exposed to adult male volatiles and the individual component identified as 4-vinylanisole among five male-abundant volatiles as promoting synchronous sexual maturation in only post adult eclosion females (PAE) 3-4 days old. Use of molecular and single sensillum recordings, followed by physiological experiments focused on the interaction between this specific adult pheromone and juvenile hormone to validate the behavioral results found for females add scientific value to the study.

Weaknesses: Firstly, synchronous and accelerated sexual maturation of young adults by older pheromone-producing ones, is a primer effect driven by males and this facilitates 'integration and cohesion' of both sexes of adults. In my view, the fact that this study focused on only females but not on both sexes, weakens the contribution of the study towards increased understanding of the biology/ecology of locusts.

We accepted the reviewer’s comment that synchronous and accelerated sexual maturation of young adults by older pheromone-producing ones occurs in both sexes. In fact, early studies have reported that mature males can accelerate sexual maturation of young males through several candidate compounds (Mahamat et al.,1993, Chemoecology; and Mahamat et al., 2000; International Journal of Tropical Insect Science). However, the effects of conspecific interaction on sexual maturation of females are rarely reported. Moreover, distinct volatiles that can accelerate female sexual maturation have not been characterized before this work. Therefore, we focus on female sexual maturation synchrony in the current study. A comparison of regulatory mechanisms underlying sexual maturation synchrony in males and females has been discussed in the revised manuscript.

There are also weaknesses in the methods, such as focusing on only the five-abundant male volatiles based on heat maps. Basically, the decision as to which components in adult male volatiles may be contributing to sexual maturation should be made by antennae of different ages of PAE females and males to avoid selecting only abundant compounds based on artificial intelligence (AI). Since most studies in this subject area have demonstrated that there is no direct correlation between volatile abundance and detection at the periphery or central nervous systems of an insect, I believe that the authors will agree with me that often some of the minor volatile components tend to contribute more to the chemical ecology of an insect than the more abundant components. Without testing minor components identified in male volatiles as a blend or individually, as additional controls to increase the robustness of the study, I am not convinced that the authors have fully achieved their aim in identifying a male-produced volatile that promotes sexual maturation in females.

We agree the reviewer’s comments that the activities of volatiles are not always determined by the absolute contents. In fact, in our work, the selection of candidate effective compounds for female sexual maturation did not rely on the absolute content of these volatiles, but mainly based on comparative analysis of their relative contents between gregarious and solitarious male adults, because only volatiles from gregarious male adults could accelerate sexual maturation of females (Figure 1C-F). In the revision process, given that the volatiles released by gregarious males, rather than gregarious females and solitarious males, have the accelerate effects on female sexual maturation, we further performed more comparative analysis of volatile contents among these three groups (G-males, G-females, and S-males). Compared to volatiles released by G-females, and S-males, only five kinds of volatiles display significantly higher emission in G-males (PAN, guaicol, 4-VA, vertrole, and anisole). The roles of five candidate volatiles in female sexual maturation were individually validated by removing the volatile from the stimulation blend one by one. The results showed that only the omission of 4-VA from the blends lost the accelerating effects on sexual maturation synchrony of gregarious females (Figure 2B). Based on these findings, we inferred that 4-VA played major roles in promoting female sexual maturation synchrony.

JH experiments- My main concern is the lack of proper controls to fully investigate the interactive effect of the male-produced pheromone promoting sexual maturation and juvenile hormone production. JH titers were not measured in females exposed to the other male-abundant compounds including PAN, guaiacol, veratrole and anisole or blend/individual minor components.

We understand the reviewer’s query. In fact, the potential role of JH pathway was inferred firstly by the RNA-seq analysis of CC-CA, which showed that the expression levels of JH metabolism-related genes were significantly affected by 4-VA treatment at PAE 3-4 days. The measurement of JH titer after 4-VA treatment was further performed to support the involvement of JH in 4-VA-accelerated sexual maturation in female adults. Since other male-abundant compounds have been excluded due to the omission of any of the four volatiles (Figure 2B), we don’t think it is necessary to detect their effects on JH titers in females including PAN, guaiacol, veratrole, or anisole.

Another notable weakness is the 'JH Rescue Experiment'. The authors did not inhibit JH synthesis in the corpora allata (allalectomized locusts) in treated locusts before injecting the JH-analog methoprene to accelerate maturation and reproduction in females.

Thanks for the reviewer’s comments. The JH rescue experiments in Figure 4D-F were performed in Or35 female mutants, which showed lower JH levels and sexual maturation rate. Thus, the JH analog was applied to Or35^-/- females to test whether activation of JH pathway could recover sexual maturation rate and Vg expression. To provide additional evidence, we performed addition rescue experiments in WT females by inhibiting JH synthesis using Precocene (PI) before JH treatment. The results showed that PI treatment significantly inhibited sexual maturation rate and Vg expression in 4-VA-exposed WT females, whereas JH treatment post PI application can obviously recovered the sexual maturation rate and Vg expression (Figure 4G-I).

Author Response:

Reviewer #1 (Public Review):

In this report, Shekhar et al, have profiled developing retinal ganglion cells from embryonic and postnatal mouse retina to explore the diversification of this class of neurons into specific subtypes. In mature retina, scRNAseq and other methods have defined approximately 45 different subtypes of RGCs, and the authors ask whether these arise from a common postmitotic precursor, or many ditinct subtypes of precursors. The overall message, is that subtype diversification arises as a "gradual, asynchronus fate restriction of postmitotic multipotential precursors. The authors find that over time, clusters of cells become "decoupled" as they split into subclusters. This process of fate decoupling is associated with changes in the expression of specific transcription factors. This allows them to both predict lineage relationships among RGC subtypes and the time during development when these specification events occur. Although this conclusion based almost entirely on a computational analysis of the relationships among cells sampled at discrete times, the evidence presented supports the overall conclusion. Future experimental validation of the proposed lineage relationships of RGC subtypes will be needed, but this report clearly outlines the overall pattern of diversification in this cell class.

We thank the reviewer for their thoughtful assessment of our study.

Reviewer #2 (Public Review):

The manuscript "Diversification of multipotential postmitotic mouse retinal ganglion cell precursors into discrete types" by Shekhar and colleagues represents an in-depth analysis of an additional transcriptomic datasets of retinal single-cells. It explores the progression of retinal ganglion cells diversity during development and describes some of aspects of fate acquisition in these postmitotic neurons. Altogether the findings provide another resource on which the neural development community will be able to generate new hypotheses in the field of retinal ganglion cell differentiation. A key point that is made by the authors regards the progression of the number of ganglion cell types in the mouse retina, i.e., how, and when neuronal "classes diversify into subclasses and types" (also p. 125). In particular, the authors would like to address whether postmitotic neurons follow either a predetermination or a stepwise progression (Fig. 2a). This is indeed a fascinating question, and the analysis, including the one based on the Waddington-OT method is conceptually interesting.

Comments and questions:

Is the transcriptomic diversity, based on highly variable genes (the number of which is not detailed in the study) a robust proxy to assess cell types? One could argue that early on predetermined cell types are specified by a small set of determinants, both at the proteomic and transcriptomic level, and that it takes several days or week to generate the cascade that allows the detection of transcriptional diversity at the level of >100 gene expression levels.

We had tested the dependence of our results on the number of highly variable genes (HVGs) used. This analysis, shown in Figure 2h, demonstrates that results are robust over the range tested – 1244-3003 total HVGs. Since the analysis in the paper employs 2800 HVGs (~800- 1500 at each stage), we are confident that we are in comfortable excess of the number at which we would need to worry. We have expanded the discussion to avoid confusion on this point. We also address the possibility that a small set of determinants are sufficient to define cell state in a transcriptomic study. This is a common argument, but we believe it is a tenuous one. We believe that the only way a small number of genes can truly define cell state is if they are expressed at very high levels. If these are expressed at high levels, they should be detected in our data and should drive the clustering. If they are expressed at extremely low levels, then given the nature of molecular fluctuations in cells, they cannot be expected to serve as a stable scaffold for differentiation. Indeed, a small set of determinants (usually transcription factors) may be necessary to specify a cell type. However, sufficiency of specification requires the expression of a usually much larger of number downstream regulators.

Since there are many RGC subsets (45) that share a great number of their gene expression, is it possible that a given RGC could transition from one subset to another between P5 and P56? Or even responding to a state linked to sustained activity? Was this possibility tested in the model?

We cannot address the possibility that cells swap types postnatally so that the cells comprising type X at P5 are not the same ones that comprise type X at P56. It does seem pretty unlikely, as the cell types are well-separated in transcriptional space (~250 DE genes on average). Regarding activity, we have made some initial tests by preventing visually evoked activity from birth to P56 in three different ways (dark-rearing and two mutant lines). We find no statistically significant effect on diversification. These results are currently being prepared for publication.

The authors state that early during development there is less diversity than later. This statement seems obvious but how much. Can this be due to differential differentiation stage? At E16 RGC are a mix of cells born from E11 to E16, with the latter barely located in the GCL. Does this tend to show a continuum that is may be probably lost when the analysis is performed on cells isolated a long time after they were born (postnatal stages)? Alternatively, would it be possible to compare RGC that have been label with birth dating methods?

Regarding the amount of diversification, we quantified this using the Rao diversity index (Figure 2h), which suggests an overall increase in 2-fold transcriptional diversity at P56 compared to the early stages. The continuum is likely because cells at early stage are close to the precursor stage and not very differentiated. Regarding combining RNA-seq with birthdating, although elegant methods now make this combination possible, it falls beyond the scope of this study.

Comparing data produced by different methods can be challenging. Here the authors compared transcriptomic diversity between embryonic dataset produced with 10X genomics (E13 to P0) and, on the other hand, postnatal P5 that were produced using a different drop-seq procedure). Is it possible to control that the differences observed are not due to the different methods?

It is correct that most of the P5 data was produced using Drop-seq, but that dataset also includes transcriptomes obtained by the 10X method. The relative frequency of RGC clusters and the average gene expression values obtained using either method was highly correlated (Reviewer Fig. 1). This is now pointed out in the “Methods.”

Reviewer Fig. 1. Comparison between the relative frequency of types (left) and the average gene expression levels (right) at P5 between 10X data (y-axis) and Drop-seq data (x-axis). R corresponds to the Pearson correlation coefficient. The axes are plotted in the logarithmic scale.

It might be important to control the conclusion that diversity is lower at E13 vs P5 when we see that thrice less cells (5900 vs 180000) were analyzed at early stage (BrdU, EdU, CFSE...)? A simple downsampling prior to the analysis may help.

Although we collected different numbers of cells at different ages, we noted in the text that they do not influence the number of clusters. Regarding P5 specifically, Rheaume et al. (who we now discuss) obtained very similar results to ours with only 6000 cells (3x lower).

Ipsilateral RGC: It is striking that the DEG between C-RGC and I-RGC reflect a strong bias with cells scored as" ipsi" are immature RGC while the other ("contra") are much more mature. This bias comes from the way ipsilateral RGC were "inferred" using non-specific markers. Can the author try again the analysis by identifying RGC using more robust markers? (eg. EphB1). Would it be possible to select I-RGC and C-RGC that share same level of differentiation? Previous studies already identified I-RGC signature using more specific set-up (Wang et al., 2016 from retrogradely labelled RGC; Lo Giudice et al., 2019 with I-RGC specific transgenic mouse).

We are not sure how the reviewer concludes that the putative I-RGCs are more immature than the putative C-RGCs. As discussed earlier, insofar as expression levels of pan-RGC markers are indicative of maturational stage, we found no evidence that clustering is driven by maturation gradients. Thus, we expect our putative I-RGCs and C-RGCs to not differ in differentiation state. Following the reviewer’s suggestion, we now include EphB1(Ephb1) in our I-RGC signature. The impact of replacing Igfbp5 with Ephb1 on the inferred proportion of I-RGCs within each terminal type was minimal (Reviewer Fig. 2). We would like to note that to assemble our IRGC/C-RGC signatures we relied on data presented Wang et al. (2016). Outside of wellestablished markers (e.g. Zic2, and Isl2), we chose the RNA-seq hits in Wang et al. that had been validated histologically in the same paper or that are correlated with Zic2 expression in our data. This nominated Igfbp5, Zic1, Fgf12, and Igf1.

Reviewer Fig. 2. Comparison of inferred I-RGC frequency within each terminal type (points) using two I-RGC signature reported in the paper. For the y-axis we used Zic2 and EphB1.

It would be important to discuss how their findings differs from the others (including Rheaume et al., 2018). To make a strong point, I-RGC shall be isolated at a stage of final maturation (P5?) and using retrograde labelling, which is a robust method to ensure the ipsilateral identity of postnatal RGCs.

We cite Rheaume et al. in several places. In fact, there is good transcriptional correspondence between our dataset and theirs (Figure S1i), despite the differences in the number of cells profiled (~6000 vs ~18000) and technologies (10X vs. Drop-seq/10X). We now mention this is the text. Note also that we had compared our P56 data with Rheaume et al.’s, P5 data in an earlier publication (Tran et al., 2019) and observed a similar tight correspondence between clusters. Zic1 is expressed in I-RGCs (Wang et al., 2016) at early stages, and in our dataset its expression at E13 and E14 is similar to that of Zic2 (Supplementary Fig. 8); Postnatally, however, it marks W3B RGCs (Tran et al., 2019), many of which project contralaterally (Kim et al., J. Neurosci. 2010). Regarding retrograde labeling, as noted above, additional experiments would take a prohibitively long time (up to a year) to complete.

It is unclear how good Zic1 and Igf1 can be used as I-RGC marker. Can the author specify how specific to I-RGC they are? Have they been confirmed as marker using retrograde labelling experiments?

We have relied on previous work, primarily from the Mason lab, to choose I-RGC and C-RGC markers. Igf1 is a C-RGC marker that is expressed in a complementary fashion with Igfbp5, an I-RGC marker as noted in Wang et al, 2016. They also perform ISH to show that Igf1 is not expressed in the VT crescent, while Igfbp5 is (see Fig. 5 in Wang et al., 2016). Similarly, Zic1 is also cited in Wang et al. as an RNA-seq hit for I-RGCs. Although Zic1 was not validated using ISH, we found its expression pattern to be highly correlated with Zic2 at E13 (Supplementary Fig. 8c).

The enrichment procedure may deplete the RGC subpopulation that express low levels of Thy1 or L1CAM. A comparison on that point could be done with the other datasets analysed in the study.

We presume the reviewer is referring to the data of Lo Guidice and Clark/Blackshaw, which we show in comparison to ours in Figure S1. In both of those studies, all retinal cells were analyzed, whereas we enriched RGCs. As noted in the text, RGCs comprise a very small fraction of all retinal cells, so Lo Giudice and Clark/Blackshaw lacked the resolution to resolve RGC diversity at later time points. Indeed, there is no whole retina dataset available in which RGCs are numerous enough for comprehensive subtyping. Our approach to this issue was to collect RGCs with both Thy1 and L1 at E13, E14, E16 and P0, with the idea that the markers might have complementary strengths and weaknesses. In fact, at each age, all clusters are present in both collection types, although frequencies vary. This concordance supports the idea that neither marker excludes particular types. We now stress this point in results and in the Supplementary Fig. 2 legend.

In supplemental Fig. S1e: why are cells embedded from "Clark" datasets only clusters on the right side of the UMAP while the others are more evenly distributed?

Actually, both the Clark et al. and Lo Giudice et al. datasets are predominantly clustered on the right side of the UMAP. This reflects the methodological difference noted above: they profiled the whole retina, whereas we isolated RGCs. Thus, their datasets contain a much higher abundance of RPCs and non-neurogenic precursors compared to ours. The right clusters represent RPCs due to their expression of Fgf15 and other markers, while the left clusters represent RGCs based on their expression of Nefl. Indeed, a main reason for including these plots was to illustrate the relative abundance of RGCs in our data (also see Supplementary Fig. S1h).

What could explain that CD90 and L1CAM population are intermingled at E14, distinct at E16, and then more mixed at P0?

We believe the reviewer is referring to Supplementary Figs. S2a-c. Given the temporal expression level changes in Thy1 and L1cam (Supplementary Fig. S1c) in RGCs, a likely possibility is that they enrich RGC precursor subsets at different relative frequencies. We now note this in the Supplementary Fig. 2 legend.

On Fig. 6: the E13 RGC seems to be segregated in early born RGC expressing Eomes and later born expressing neurod2. Thus, fare coupling with P5 seems to suggest that Eomes population at P5 may have been generated first, and Neurod2 generated later. Is that possible?

That the Eomes RGCs are specified before Neurod2 RGCs is one of our conclusions from the fate decoupling analysis (Figures 6f-h). Whether this is because the former arise from early born cells and the latter arise from later born cells is not clear. There is disagreement in the literature on whether ipRGCs are born at a different time than other RGCs, so we prefer not to make a comment.

Methods: The Methods section is extensive, and yet it is presented in a rather complex manner so that it is difficult to understand for a broad audience. It would be valuable if the authors could simplify or better explain some parts (the WOT section in particular).

We believe that the sections on animals, molecular biology and histology are quite straightforward, but agree that the sections describing the computational analysis are hard going. We have modified them in several places as requested. As regards better explanation of the WOT, we now precede that section with an “overview” as a way of making it easier to follow. (We had already included an overview of the clustering procedures.) We have also provided further detail on some of the reviewer’s subsequent questions on this section, including the use of HVGs, the Classifier, and the strategy for inferring I-RGCs (see below). Perhaps most important, we have worked to make the “Results” and “Discussion” sections accessible to a broad audience.

*Highly variable genes (HVG) used for clustering and dimensionality reduction: how many of them and what are they? Are they the same used for each stage?

Since clustering was performed at each stage independently, we determined HVGs at each stage separately using a statistical method introduced in one of our previous studies (Pandey et al., Current Biology, 2018). The total number of HVGs at each stage were as follows: E13: N=1094 E14: N=834 E16: N=822 P0: N=881 P5: N=1105 P56: N=1510

We note that these are not necessarily the same at each stage due to the temporal variation in gene expression. Together these correspond to 2854 unique genes (union of all HVGs). The WOT analysis was done using this full set.

*In the methods p9: "The common features G = GR ∩ GT are used to train a third classifier ClassR on the reference atlas AR. This ensures that inferred transcriptomic correspondences are based on "core" gene expression programs that underlie cell type identity rather than maturation-associated genes." Could the authors explain the relevance of using a third model and, more importantly, is there any genes that eliminated through the procedure that could be important to drive the diversification process? If so, would it be possible to estimate their number and the relative impact?

The rationale for this was as follows. Our goal is to map cells from one time point to a type at another time point. The naïve way to do this would be to use a classifier trained entirely at either of the time point. However, the features of such a classifier is likely to contain genes that are not expressed at the earlier time point, and likely to generate spurious mappings (since the set of cluster specific genes are not identical). Therefore, we sought to train a classifier that is trained using genes that are part of conserved transcriptional signatures at both time points, which corresponds to the third model.

When this filtering was not performed, the temporal correspondences in the supervised classification model were less specific than those reported. In particular, ARI values dropped by about 15% on average. The simple reason for this is that a cluster specific gene at E13 (for e.g.) may no longer be expressed at E14, and vice-versa. Thus, by restricting the features to a common set of cluster specific genes, we obtained the “best possible” transcriptomic correspondences between clusters at consecutive time points. We note that the correspondences obtained in this way (Figure 3) were recovered through WOT when the results of the latter were collapsed at the cluster level (Supplementary Fig. 5).

*Methods page 15: Inference of ipsilaterally-projecting RGC types. Wouldn't it be more valuable to consider more markers to distinguish RGC precursors?

As indicated before, we used I-RGC genes and C-RGC genes reported in Wang et al., 2016 (Table 2), in addition to the well-known markers Zic2 and Isl2. Here, we prioritized genes that had been histologically validated (Figs. 4 and 5), which were expressed in our data (Sema3e and Tbx20 were not considered as these undetectable at E13 in our data). Following the reviewer’s earlier suggestion, we also noted that including Ephb1 in our signature minimally impacts the results.

Discussion: *Is there somewhat a plasticity that allow the RGC subgroups to switch over time? (IF we were to record the transcriptome of the same cell over time, will one observe that the cell belong to another cluster / subgroup?

One can only speculate. Other than long-term in vivo imaging combined with vital type-specific markers we know of no way to experimentally address the possibility that cells swap types postnatally so that the cells comprising type x at P5 are not the same ones that comprise type x at P56. It does seem pretty unlikely though.

*While the data appears technically rigorous, and the number of cells sequenced very high, the results seem redundant with several prior studies and the discrepancies are not sufficiently discussed.

We are confused by this point, since the reviewer does not cite the papers to which s/he refers. To our knowledge there is no study at present that has described RGC diversification, so it is not clear what would be discrepant.

Author Response:

Joint Public Review:

A highly robust result when investigating how neural population activity is impacted by performance in a task is that the trial to trial correlations (noise correlations) between neurons is reduced as performance increases. However the theoretical and experimental literature so far has failed to account for this robust link since reduced noise correlations do not systematically contribute to improved availability or transmission of information (often measured using decoding of stimulus identity). This paper sets out to address this discrepancy by proposing that the key to linking noise correlations to decoding and thus bridging the gap with performance is to rethink the decoders we use : instead of decoders optimized to the specific task imposed on the animal on any given trial (A vs B / B vs C / A vs C), they hypothesize that we should favor a decoder optimized for a general readout of stimulus properties (A vs B vs C).

To test this hypothesis, the authors use a combination of quantitative data analysis and mechanistic network modeling. Data were recorded from neuronal populations in area V4 of two monkeys trained to perform an orientation change detection task, where the magnitude of orientation change could vary across trials, and the change could happen at cued (attended) or uncued (unattended) locations in the visual field. The model, which extends previous work by the authors, reproduces many basic features of the data, and both the model and data offer support for the hypothesis.

The reviewers agreed that this is a potentially important contribution, that addresses a widely observed, but puzzling, relation between perceptual performance and noise correlations. The clarity of the hypothesis, and the combination of data analysis and computational modelling are two essential strengths of the paper.

Overall this paper exhibits a new factor to be taken into account when analysing neural data : the choice of decoder and in particular how general or specific the decoder is. The fact that the generality of the decoder sheds light on the much debated question of noise correlations underscores its importance. The paper therefore opens multiple avenues for future research to probe this new idea, in particular for tasks with multiple stimuli dimensions.

Nonetheless, as detailed below, the reviewers believe the manuscript clarity could be further improved in several points, and some additional analysis of the data would provide more straightforward test of the hypothesis.

1. It would be important to verify that the model reproduces the correlation between noise and signal correlations since this is really a key argument leading to the author's hypothesis.

We have incorporated this verification of the model into the manuscript, as referred to below in the Results:

“Importantly, this model reproduces the correlation between noise and signal correlations (Figure 2–figure supplement 1) observed in electrophysiological data (Cohen & Maunsell, 2009; Cohen & Kohn, 2011). This correlation between the shared noise and the shared tuning is a key component of the general decoder hypothesis. We observed this strong relationship between noise and signal correlations in our recorded neurons (Figure 2–figure supplement 1A) as well as in our modeled data (Figure 2–figure supplement 1B). Using this model, we were able to measure the relationship between noise and signal correlations for varying strengths of attentional modulation. Consistent with the predictions of the general decoder hypothesis, attention weakened the relationship between noise and signal correlations (Figure 2–figure supplement 1C).”

The new figure is as below:

Figure 2–figure supplement 1. The model reproduces the relationship between noise and signal correlations that is key to the general decoder hypothesis. (A) As previously observed in electrophysiological data (Cohen & Maunsell, 2009; Cohen & Kohn, 2011), we observe a strong relationship between noise and signal correlations. During additional recordings collected during most recording sessions (for Monkey 1 illustrated here, n = 37 days with additional recordings), the monkey was rewarded for passively fixating the center of the monitor while Gabors with randomly interleaved orientations were flashed at the receptive field location (‘Stim 2’ location in Figure 1C). The presented orientations spanned the full range of stimulus orientations (12 equally spaced orientations from 0 to 330 degrees). We calculated the signal correlation for each pair of units based on their mean responses to each of the 12 orientations. We define the noise correlation for each pair of units as the average noise correlation for each orientation. The plot depicts signal correlation as a function of noise correlation across all recording sessions, binned into 8 equally sized sets of unit pairs. Error bars represent SEM. (B) The model reproduces the relationship between noise and signal correlations. Signal correlation is plotted as a function of noise correlation, binned into 20 equally sized sets of unit pairs (n = 2000 neurons), for each attentional modulation strength (green: least attended; yellow: most attended). The results were averaged over 50 tested orientations. (C) The slope of the relationship between noise and signal correlations (y-axis) decreases with increasing attentional modulation (x-axis). This suggests that noise is less aligned with signal correlation with increasing attentional modulation.

2. Testing the hypothesis of the general decoder:<br /> 2.1 In the data, the authors compare mainly the specific (stimulus) decoder and the monkey's choice decoder. The general stimulus decoder is only considered in fig. 3f, because data across multiple orientations are available only for the cued condition, and therefore the general and specific decoders cannot be compared for changes between cued and uncued. However, the hypothesized relation between mean correlations and performance should also be true within a fixed attention condition (cued), comparing sessions with larger vs. smaller correlation. In other words, if the hypothesis is correct, you should find that performance of the "most general" decoder (as in fig. 3f) correlates negatively with average noise correlations, across sessions, more so than the "most specific" decoder.<br /> We have added a new supplementary figure to the manuscript:

Figure 3–figure supplement 1. Based on the electrophysiological data, the performance of the monkey’s decoder was more related to mean correlated variability than the performance of the specific decoder within each attention condition. (A) Within the cued attention condition, the performance of the monkey’s decoder was more related to mean correlated variability (left plot; correlation coefficient: n = 71 days, r = -0.23, p = 0.058) than the performance of the specific decoder (right plot; correlation coefficient: r = 0.038, p = 0.75). The correlation coefficients associated with the two decoders were significantly different from each other (Williams’ procedure: t = 3.8, p = 1.5 x 10^-4). Best fit lines plotted in gray. Data from both monkeys combined (Monkey 1 data shown in orange: n = 44 days; Monkey 2 data shown in purple: n = 27 days) with mean correlated variability z-scored within monkey. (B) The data within the uncued attention condition showed a similar pattern, with the performance of the monkey’s decoder more related to mean correlated variability (n = 69 days, r = -0.20, p = 0.14) than the performance of the specific decoder (r = 0.085, p = 0.51; Williams’ procedure: t = 2.0, p = 0.049). Conventions as in (A) (Monkey 1: n = 42 days – see Methods for data exclusions as in Figure 3C; Monkey 2: n = 27 days).

2.2 In figure 3f, a more straightforward and precise comparison is to use the stimulus decoders to predict the choice, and test whether the more specific or the more general can predict choices more accurately.

We have added a new panel to Figure 3 (Figure 3G) that illustrates the results of this analysis comparing whether the specific or more-general decoders predict the monkey’s trial-by-trial choices more accurately:

Figure 3… (G) The more general the decoder (x-axis), the better its performance predicting the monkey’s choices on the median changed orientation trials (y-axis; the proportion of leave-one-out trials in which the decoder correctly predicted the monkey’s decision as to whether the orientation was the starting orientation or the median changed orientation). Conventions as in (F) (see Methods for n values).

The description of this new panel in the Results section is as below:

“Further, the more general the decoder, the better it predicted the monkey’s trial-by-trial choices on the median changed orientation trials (Figure 3G).”

The updated Methods section describing this new panel is as below:

“For Figure 3G, we performanced analyses similar to those performed for Figure 3F, in that we tested each stimulus decoder: ‘1 ori’ decoders (n = 8 decoders; 1 specific decoder for either the first, second, fourth, or fifth largest changed orientation, for each of the 2 monkeys), ‘2 oris’ decoders (n = 12 decoders; 1 decoder for each of the 6 combinations of 2 changed orientations, for each of the 2 monkeys), ‘3 oris’ decoders (n = 8 decoders; 1 decoder for each of the 4 combinations of 3 changed orientations, for each of the 2 monkeys), and ‘4 oris’ decoders (n = 2 decoders; 1 decoder for the 1 combination of 4 changed orientations, for each of the 2 monkeys). However, unlike in Figure 3F, where the performance of the stimulus decoders was compared to the performance of the monkey’s decoder on the median orientation-change trials, here we calculated the performance of the stimulus decoder when tasked with predicting the trial-by-trial choices that the monkey made on the median orientation-change trials. We plotted the proportion of leave-one-out trials in which each decoder correctly predicted the monkey’s choice as to whether the orientation was the starting orientation or the median changed orientation.”

3. The main goal of the manuscript is to determine the impact of noise correlations on various decoding schemes. The figures however only show how decoding co-varies with correlations, but a direct, more causal analysis of the effect of correlations on decoding seems to be missing. Such an analysis can be obtained by comparing decoding on simultaneously recorded activity with decoding on trial-shuffled activity, in which noise-correlations are removed.

We have added the following Discussion section to address this point:

“The purpose of this study was to investigate the relationship between mean correlated variability and a general decoder. We made an initial test of the overarching hypothesis that observers use a general decoding strategy in feature-rich environments by testing whether a decoder optimized for a broader range of stimulus values better matched the decoder actually used by the monkeys than a specific decoder optimized for a narrower range of stimulus values. We purposefully did not make claims about the utility of correlated variability relative to hypothetical situations in which correlated variability does not exist in the responses of a group of neurons, as we suspect that this is not a physiologically realistic condition. Studies that causally manipulate the level of correlated variability in neuronal populations to measure the true physiological and behavioral effects of increasing or decreasing correlated variability levels, through pharmacological or genetic means, may provide important insights into the impact of correlated variability on various decoding strategies.”

4. How different are the four different decoders (specific/monkey, cued/uncued)? It would be interesting to see how much they overlap. More generally, the authors should discuss the alternative that attention modulates also the readout/decoding weights, rather than or in addition to modulating V4 activity.

We have added the following to the manuscript:

“A fixed readout mechanism

A prior study from our lab found that attention, rather than changing the neuronal weights of the observer’s decoder, reshaped neuronal population activity to better align with a fixed readout mechanism (Ruff & Cohen, 2019). To test whether the neuronal weights of the monkey’s decoder changed across attention conditions (attended versus unattended), Ruff and Cohen switched the neuronal weights across conditions, testing the stimulus information in one attention condition with the neuronal weights from the other. They found that even with the switched weights, the performance of the monkey’s decoder was still higher in the attended condition. The results of this study support the conclusion that attention reshapes neuronal activity so that a fixed readout mechanism can better read out stimulus information. In other words, differences in the performance of the monkey’s decoder across attention conditions may be due to differences in how well the neuronal activity aligns with a fixed decoder.

Our study extends the findings of Ruff and Cohen to test whether that fixed readout mechanism is determined by a general decoding strategy. Our findings support the hypothesis that observers use a general decoding strategy in the face of changing stimulus and task conditions. Our findings do not exclude other potential explanations for the suboptimality of the monkey’s decoder, nor do they exclude the possibility that attention modulates decoder neuronal weights. However, our findings together with those of Ruff and Cohen shed light on why neuronal decoders are suboptimal in a manner that aligns the fixed decoder axis with the correlated variability axis (Ni et al., 2018; Ruff et al., 2018).”

5. Quantifying the link between model and data :<br /> 5.1 the text providing motivation for the model could be improved. The motivation used in the manuscript is, essentially, that the model allows to extrapolate beyond the data (more stimuli, more repetitions, more neurons). The dangers of extrapolation beyond the range of the data are however well known. A model that extrapolates beyond existing data is useful to design new experiments and test predictions, but this is not done here. Because the manuscript is about information and decoding, a better motivation is the fact that this model takes an actual image as input, and produces tuning and covariance compatible with each other because they are constrained by an actual network that processes the input (as opposed to parametric models where tuning and covariance can be manipulated independently).

We have modified the manuscript as below:

“Here, we describe a circuit model that we designed to allow us to compare the specific and monkey’s decoders from our electrophysiological dataset to modeled ideal specific and general decoders. The primary benefit of our model is that it can take actual images as inputs and produce neuronal tuning and covariance that are compatible with each other because of constraints from the simulated network that processed the inputs (Huang et al., 2019). Parametric models in which tuning and covariance can be manipulated independently would not provide such constraints. In our model, the mean correlated variability of the population activity is restricted to very few dimensions, matching experimentally recorded data from visual cortex demonstrating that mean correlated variability occupies a low-dimensional subset of the full neuronal population space (Ecker et al., 2014; Goris et al., 2014; Huang et al., 2019; Kanashiro et al., 2017; Lin et al., 2015; Rabinowitz et al., 2015; Semedo et al., 2019; Williamson et al., 2016).”

“Our study also demonstrates the utility of combining electrophysiological and circuit modeling approaches to studying neural coding. Our model mimicked the correlated variability and effects of attention in our physiological data. Critically, our model produced neuronal tuning and covariance based on the constraints of an actual network capable of processing images as inputs.”

We have also removed the Results and Discussion text that suggested that the model allowed us to extrapolate beyond the data.

5.2 The ring structure, and the orientation of correlations (Fig 2b) seem to be key ingredients of the model, but are they based on data, or ad-hoc assumptions?

We have modified the manuscript to clarify this point, as below:

“As the basis for our modeled general decoder, we first mapped the n-dimensional neuronal activity of our model in response to the full range of orientations to a 2-dimensional space. Because the neurons were tuned for orientation, we could map the n-dimensional population responses to a ring (Figure 2B, C). The orientation of correlations (the shape of each color cloud in Figure 2B) was not an assumed parameter, and illustrates the outcome of the correlation structure and dimensionality modeled by our data. In Figure 2B, we can see that the fluctuations along the radial directions are much larger than those along other directions for a given orientation. This is consistent with the low-dimensional structure of the modeled neuronal activity. In our model, the fluctuations of the neurons, mapped to the radial direction on the ring, were more elongated in the unattended state (Figure 2B) than in the attended state (Figure 2C).”

5.3 In the model, the specific decoder is quite strongly linked to correlated variability and the improvement of the general decoder is clear but incremental (0.66 vs 0.83) whereas in the data there really is no correlation at all (Fig 3c). This is a bit problematic because the author's begin by stating that specific decoders cannot explain the link between noise correlations and accuracy but their specific decoder clearly shows a link.

We appreciate this point and have modified the manuscript as below:

“Indeed, we found that just as the performance of the physiological monkey’s decoder was more strongly related to mean correlated variability than the performance of the physiological specific decoder (Figure 3C; see Figure 3–figure supplement 1 for analyses per attention condition), the performance of the modeled general decoder was more strongly related to mean correlated variability than the performance of the modeled specific decoder (Figure 3D). We modeled much stronger relationships to correlated variability (Figure 3D) than observed with our physiological data (Figure 3C). We observed that the correlation with specific decoder performance was significant with the modeled data but not with the physiological data. This is not surprising as we saw attentional effects, albeit small ones, on specific decoder performance with both the physiological and the modeled data (Figure 3A, B). Even small attentional effects would result in a correlation between decoder performance and mean correlated variability with a large enough range of mean correlated variability values. It is possible that with enough electrophysiological data, the performance of the specific decoder would be significantly related to correlated variability, as well. As described above, our focus is not on whether the performance of any one decoder is significantly correlated with mean correlated variability, but on which decoder provides a better explanation of the frequently observed relationship between performance and mean correlated variability. The performance of the general decoder was more strongly related to mean correlated variability than the performance of the specific decoder.”

“Our results suggest that the relationship between behavior and mean correlated variability is more consistent with observers using a more general strategy that employs the same neuronal weights for decoding any stimulus change.”

6. General decoder: Some parts of the text (eg. Line 60, Line 413) refer to a decoder that accounts for discrimination along different stimulus dimensions (eg. different values of orientation, or different color of the visual input). But the results of the manuscripts are about a general decoder for multiple values along a single stimulus dimension. The disconnect should be discussed, and the relation between these two scenarios explained.

We have modified the manuscript as below:

“Here, we report the results of an initial test of this overarching hypothesis, based on a single stimulus dimension. We used a simple, well-studied behavioral task to test whether a more-general decoder (optimized for a broader range of stimulus values along a single dimension) better explained the relationship between behavior and mean correlated variability than a more-specific decoder (optimized for a narrower range of stimulus values along a single dimension). Specifically, we used a well-studied orientation change-detection task (Cohen & Maunsell, 2009) to test whether a general decoder for the full range of stimulus orientations better explained the relationship between behavior and mean correlated variability than a specific decoder for the orientation change presented in the behavioral trial at hand.

This test based on a single stimulus dimension is an important initial test of the general decoder hypothesis because many of the studies that found that performance increased when mean correlated variability decreased used a change-detection task…”

“We performed this initial test of the overarching general decoder hypothesis in the context of a change-detection task along a single stimulus dimension because this type of task was used in many of the studies that reported a relationship between perceptual performance and mean correlated variability (Cohen & Maunsell, 2009; 2011; Herrero et al., 2013; Luo & Maunsell, 2015; Mayo & Maunsell, 2016; Nandy et al., 2017; Ni et al., 2018; Ruff & Cohen, 2016; 2019; Verhoef & Maunsell, 2017; Yan et al., 2014; Zénon & Krauzlis, 2012). This simple and well-studied task provided an ideal initial test of our general decoder hypothesis.

This initial test of the general decoder hypothesis suggests that a more general decoding strategy may explain observations in studies that use a variety of behavioral and stimulus conditions.”

“This initial study of the general decoder hypothesis tested this idea in the context of a visual environment in which stimulus values only changed along a single dimension. However, our overarching hypothesis is that observers use a general decoding strategy in the complex and feature-rich visual scenes encountered in natural environments. In everyday environments, visual stimuli can change rapidly and unpredictably along many stimulus dimensions. The hypothesis that such a truly general decoder explains the relationship between perceptual performance and mean correlated variability is suggested by our finding that the modeled general decoder for orientation was more strongly related to mean correlated variability than the modeled specific decoder (Figure 3D). Future tests of a general decoder for multiple stimulus features would be needed to determine if this decoding strategy is used in the face of multiple changing stimulus features. Further, such tests would need to consider alternative hypotheses for how sensory information is decoded when observing multiple aspects of a stimulus (Berkes et al., 2009; Deneve, 2012; Lorteije et al., 2015). Studies that use complex or naturalistic visual stimuli may be ideal for further investigations of this hypothesis.”

7. Some statements in the discussion such as l 354 "the relationship between behavior and mean correlated variability is explained by the hypothesis that observers use a general strategy" should be qualified : the authors clearly show that the general decoder amplifies the relationship but in their own data the relationship exists already with a specific decoder.

We have modified the manuscript as below:

“Our results suggest that the relationship between behavior and mean correlated variability is more consistent with observers using a more general strategy that employs the same neuronal weights for decoding any stimulus change.

“Together, these results support the hypothesis that observers use a more general decoding strategy in scenarios that require flexibility to changing stimulus conditions.”

“This initial test of the general decoder hypothesis suggests that a more general decoding strategy may explain observations in studies that use a variety of behavioral and stimulus conditions.”

8. Low-Dimensionality, beginning of Introduction and end of Discussion: experimentally, cortical activity is low-dimensional, and the proposed model captures that. But some of the reviewers did not understand the argument offered for why this matters, for the relation between average correlations and performance. It seems that the dimensionality of the population covariance is not relevant: The point instead is that a change in amplitude of fluctuations along the f'f' direction necessarily impact performance of a "specific" decoder, whereas changes in all other dimensions can be accounted for by the appropriate weights of the "specific" decoder. On the other hand, changes in fluctuation strength along multiple directions may impact the performance of the "general" decoder.

We have modified the manuscript as below:

“These observations comprise a paradox because changes in this simple measure should have a minimal effect on information coding. Recent theoretical work shows that neuronal population decoders that extract the maximum amount of sensory information for the specific task at hand can easily ignore mean correlated noise (Kafashan et al., 2021; Kanitscheider et al., 2015b; Moreno-Bote et al., 2014; Pitkow et al., 2015; Rumyantsev et al., 2020; for review, see Kohn et al., 2016). Decoders for the specific task at hand can ignore mean correlated variability because it does not corrupt the dimensions of neuronal population space that are most informative about the stimulus (Moreno-Bote et al., 2014).”

“Our results address a paradox in the literature. Electrophysiological and theoretical evidence supports that there is a relationship between mean correlated variability and perceptual performance (Abbott & Dayan, 1999; Clery et al., 2017; Haefner et al., 2013; Jin et al., 2019; Ni et al., 2018; Ruff & Cohen, 2019; reviewed by Ruff et al., 2018). Yet, a specific decoding strategy in which different sets of neuronal weights are used to decode different stimulus changes cannot easily explain this relationship (Kafashan et al., 2021; Kanitscheider et al., 2015b; Moreno-Bote et al., 2014; Pitkow et al., 2015; Rumyantsev et al., 2020; reviewed by Kohn et al., 2016). This is because specific decoders of neuronal population activity can easily ignore changes in mean correlated noise (Moreno-Bote et al., 2014).”

Author Response:

Reviewer #1 (Public Review):

The recent development of AlphaFold2 has improved the ability to predict protein fold from sequence. However, this approach typically yields a defined structural fold, while it is known that proteins exhibit structural diversity through different conformations. In particular, membrane transport proteins and receptors are known to adopt distinct conformational states in order to allow for alternate access or signaling across the membrane. In this study, the authors demonstrate that by reducing the size of the input sequence alignment fed into AlphaFold2, conformational diversity in the structural predictions is increased, with some of these corresponding to known experimentally determined structures. They test this with a diverse set of transporters where the structures have been solved in both inward and outward facing conformations, as well as GPCRs in active and inactive states. Decreasing the size of the sequence alignment from 5120 to 32 leads to a general increase in conformational diversity with the predicted structures and that these structures are generally bounded by the experimental structures. The RMSF analysis of residues amongst the different models, corresponds to RMSD of residues in the experimental structures, and principal component analysis demonstrates that these models connect the two known conformations. Altogether, this analysis validates that the ability to predict alternate conformations of transporters and receptors is already present in the AlphaFold2.

This validation is important, but further analysis is necessary to move beyond a demonstration and towards a procedure for predicting relevant conformations. Along these lines, quantification of the robustness of the approach along different parameters is needed. Furthermore, the study stops short of defining how to statistically weed through the ensemble of models to predict meaningful conformations. AlphaFold2 may generate highly accurate models, but how does the user pick which ones are likely to be relevant? Therefore, this is an interesting study that is expected to be broadly impactful for the study of all proteins, not just membrane proteins tested here. However, limitations remain on the interpretation of the results and a clarification is needed to demonstrate how others may use this approach to predict new biologically relevant conformations.

We believe the approach used in this manuscript can only sample the energy minimum; identification of the relevant individual states of interest will likely require experimental validation. Thus, we have modified the text to reinforce this point in various parts of the manuscript. We have edited the text at the end of “Introduction”:

"Finally, we propose a modeling pipeline for researchers interested in sampling alternative conformations of specific membrane proteins, which we apply to the structurally unknown GPR114/AGRG5 adhesion GPCR as an example."

Additional clarification is provided in “Results and Discussion” subsection “Distributions of predicted models relative to the experimental structures”:

"Indeed, the models with the most extreme PC1 values were also among the most accurate: average TM-scores were 0.94 for the top one, top three and top ten PC1 models, and Pearson correlation coefficients between PC1 and TM-scores of the ensemble of models exceeded 0.8 for all transporters in this dataset. Moreover, the experimental structures virtually always flanked the AF2 models along PC1. The exception, PTH1R, was determined in a partially inactive and active conformation29, suggesting that models extending beyond the former state along PC1 may represent the fully inactive conformation. Therefore, these results indicate that accurate representative models of conformations of interest can be selected from the extreme positions along PC1."

Finally, we have added a sentence in subsection "Concluding remarks":

"Accurate representatives of distinct conformers were generally obtainable with exhaustive sampling and could be identified by performing PCA and selecting models at the extreme positions of PC1."

Reviewer #3 public review:

This manuscript describes a workflow for using AlphaFold2 (AF2) to model membrane proteins in different conformations. It then evaluates the models generated by this workflow on eight different membrane protein structures representing different structural classes and mechanisms. The authors conclude that AF2 can provide models with reasonable accuracy and conformational diversity of membrane proteins, but additional improvements are needed to be able to sample biologically relevant conformations.

In principle, the research presented in this study is timely and can be of general interest to the community. It attempts to address the question of whether AF2 can accurately predict membrane protein dynamics. As the authors state, they provide "a hack" for modeling membrane proteins with AF2. My main concern with this manuscript is that the adopted workflow needs to be optimized and assessed more rigorously, in order to support the conclusions regarding the usefulness of AF2 for modeling membrane proteins.

In addition to the importance of the topic, some strengths of the study include: focusing on proteins representing different folds and families, using different measures for structural evaluation, and presenting several examples in greater detail, particularly of important human proteins.

My specific comments can be found below:

A significant concern is that the Methods section of this manuscript is lacking. Additional details are needed in order to be able to evaluate the validity of the approach and reproduce these results. I list below some specific issues.

The alignments used to develop the models should be provided. Specific details on how the visual inspection of the alignments guided their refinement should also be included. I could imagine that the alignment quality may correlate with model accuracy. This is an important analysis to include.

We introduced modifications to the manuscript to clarify that all alignment subsampling was performed randomly by the AF2 program. As the major modification discussed here is the reduction of the size of the MSA subsampled at each iteration of the program, our pipeline did not provide an opportunity for either modification or saving of the alignments by the user. Analysis of the alignments responsible for producing specific models is therefore not possible.

For some of the targets, the template-based modeling clearly improved sampling of various conformations and for others it did not. The authors only vaguely discussed this observation without providing a detailed analysis. For example, how were the template selected for the template-based modeling? Was the performance of AF2 dependent on the sequence similarity between the template(s) and the target? These are critical points that are needed to understand the utility of the approach and how one can adopt the proposed workflow.

In response to a similar comment made by another Reviewer, we have expanded the relevant section in Methods regarding the use of templates. However, due to the relatively small size of this test set, a thorough quantitative analysis is likely not currently possible.

A key conclusion of this study is that there is no one-model fits-all approach with AF2 for accurately sampling the conformational space of membrane proteins. Although this conclusion sounds plausible, the authors do not provide significant evidence to support it: they tested the performance of the models for a very limited set of parameters. For example, they only used a few MSA depths, and they do not report performances for templates with different similarities to the target. Also, is it possible that a "one-model fits-all" exists for particular folds or families? For example, LAT1 and MCT1 each represent very large protein families and a clear workflow for each would represent an important advance in the field.

Per the recommendation of another Reviewer, we carried out a more rigorous analysis of MSA depths (see Figure 1 - figure supplement 1). However, these results support our general conclusion that there are too few proteins to confidently identify the optimal set of parameters for accurate prediction of multiple conformations. We have rewritten a sentence in “Concluding remarks”:

"Thus, while the results presented here provide a blueprint for obtaining AF2 models of alternative conformations, they also argue against an optimal one-size-fits-all approach for sampling conformational space of every protein with high accuracy."

How were misfolded models were identified? Providing a reference is not sufficient here. It is also stated that "padding MSAs with additional sequences had the desirable effect of decreasing the proportion of these models, it also limited the extent to which alternative conformations were sampled. Thus, our results revealed a delicate balance that must be achieved to generate models that are both diverse and natively folded. No general pattern was readily apparent regarding the ideal MSA depth required to achieve this balance.". While this is interesting initial observation, finding a pattern in the ability to detect those misfolded structures (for at least some folds or protein families) could increase the impact of the work.

We have rewritten this paragraph and remade Figure S2 (now numbered Figure 1 - figure supplement 1) in response to a similar comment made by another Reviewer.

In general, the definition of the different conformations is nuanced for each structural class and a better explanation is needed for those proteins that are discussed in greater detail. For example, when discussing one of these proteins, MCT1, the authors state: "One target, MCT1, was exclusively modeled by AF2 in either IF or fully occluded conformations regardless of MSA depth. Notably, these results closely parallel those reported by DeepMind during their attempt to model multiple conformations of LmrP in CASP14.". Could the authors elaborate on this statement? Could they provide quantitative data defining how occluded and open conformations are defined? Many of the readers are unlikely to know the LmrP example from a previous publication.

We agree with this statement and have rewritten the paragraph to remove the reference to the CASP14 in this section.

The authors evaluate the models on structures that were not included in the AF2 training set. It would be useful to provide the list of the PDB ids that were included in the training of the AF2 version that was used in this study. This is important because the structures of some of these proteins were solved a few years ago with minor differences, even though they were classified as a "different conformation". As mentioned in the point above, the definition of "different conformation" can be highly nuanced depending on the protein family and the mechanism used by the protein.

We have edited the first paragraph of “Results and Discussion” to more explicitly state that the structures of the proteins used in this test set were entirely absent from the version of the PDB used to train AF2. This design decision was critical in allowing us to sidestep this question of whether the conformations of interest, or similar conformations, were present or absent from the training set.

In the section "Alternative conformations cannot be predicted for proteins with structures in the training set", the results should be described in a more quantitative way. Specifically, the following statement should be accompanied by quantitative data: "virtually every transporter model superimposed nearly perfectly with the training set conformation, and none resembled the alternative conformation".

Per recommendations made by another Reviewer, we have added metrics to quantify the similarity of these models to the training set conformers. This also allows us to establish the similarity of these predictions to those of MCT1.

Author Response:

Reviewer #2 (Public Review):

This work aimed to advance knowledge of the roles of polycystin-1 and polycystin-2 (PC-1, PC-2) in the vascular endothelium. For this, the authors developed tamoxifen-inducible Cre-lox models to delete PC-1, PC-2 or both specifically in endothelial cells of mice. Evidence is presented that flow or sheer stress activates PC-1-dependent current in endothelial cells, which is associated with NOS and KCa channel activation, smooth muscle hyperpolarization, and flow-dependent vasodilation. The Jaggar laboratory has recently reported that deletion of endothelial PC-2, a member of the TRP family, leads to loss of flow-induced Ca2+ influx, NOS and SK/IK activation, reduced vasodilation, and higher blood pressure. Thus, the novelty of the current work is the finding that PC-1 is similarly critical for activation of this pathway by flow, and that it is a physical interaction between membrane-localized PC-1 and PC-2 that underlies complex activation by flow.

Strengths of the current study include the use of powerful inducible knockout models in combination with a wide array of in vivo and ex vivo methods to test hypotheses. Thus, conclusions are based on multiple approaches and are mostly well supported. However, there are some concerns, specifically related to a lack of clarity on the interactions and purported interdependence between PC-1 and PC-2 that warrant further consideration.

1.The prospective impact of the current study is based on the suggestion that interactions between PC-1 and PC-2 via coiled-coil domains are required for activation of inward current by flow. However, the authors did not show evidence, via fluorescence imaging or otherwise (e.g., coIP), that peptides generated to disrupt this interaction actually do so. Does treatment with the coiled-coil domain peptides cause a shift in the PC-1-to-PC-2 distance (using TIRF-SMLM as in Fig 5)?

We have performed new experiments and now show that scrambled peptides of either the PC-1 or PC-2 coiled-coil domains do not alter flow-activated I_Cat in endothelial cells (Figure 6E-G, Figure 6 – figure supplement 2). In contrast, peptides corresponding to the coiled-coil domains present in PC-1 or PC-2 similarly inhibit flow-activated cation currents in endothelial cells.

Multiple different domains in PC-1 and PC-2 physically interact to form the heteromeric complex. Several groups have demonstrated that PC-1 and PC-2 couple via their C-terminal coiled-coils (Qian et al, Nat. Genet. 1997; Zhu et al., PNAS 2011; Yu et al., PNAS 2009; Tsiokas et al., PNAS 1997). Recombinant PC-1 and PC-2 lacking coiled-coils also interact via N-terminal loops (Babich et al, JBC 2004; Feng et al., JBC 2008). The structure of a PC-1/PC-2 heterotetramer that lacked N- and Ctermini was resolved using cryo-EM and indicated that a region between TM6 and TM11 of PC-1 interdigitates with PC-2 (Su et al, Science 2018). As such, it is unlikely that that the coiled-coil domain peptides physically separate PC-1 and PC-2 subunits. Rather, these data suggest that coiled-coil domain coupling in PC-1 and PC-2 is required for flow to activate non-selective cation currents in endothelial cells. In response to your comment, we have expanded discussion of this point in the manuscript.

2.The use of immunoFRET to test for PC-1/PC-2 proximity is not ideal. At minimum, proper negative controls (e.g., use of cells from KO models) should be provided to demonstrate the specificity of this technique for PC-1/PC-2 interactions in endothelial cells.

We agree. As suggested, we have performed new experiments and now provide immunoFRET data for Pkd1 ecKO and Pkd2 ecKO endothelial cells (Figure 4B, C; Figure 4 - figure supplement 1A, B). These data show that N-FRET between PC-1 and PC-2 antibodies is extremely low in Pkd1 ecKO and Pkd2 ecKO endothelial cells.

3.The authors conclude that PC-1/PC-2 clusters in KO cells in SMLM experiments are likely due to non-specific antibody binding. While I agree with this, it raises a question as to the meaning of cluster size data. Considering that the approach relies on fluorophore-tagged antibodies, which cannot be assumed to be in 1:1 stoichiometry with proteins of interest, how relevant is cluster size?

This is an interesting question. All immunofluorescence techniques rely on the use of antibodies to tag proteins. We recognize that the size of clusters reflects the size of both the proteins and antibodies. We now include text in the Discussion stating that the size of the PC-1 and PC-2 clusters reported is the size of both the proteins and the antibodies.

4.Based on data shown in Figure 1, the authors conclude that there is a reduction in inward current with flow. Since the applied technique measures total current, couldn't this result also reflect an increase in outward current (e.g., K+) due to flow that depends on the presence of Ca2+? Also related to these data, the magnitude of initial flow-induced transient current was quite variable (~8 - ~45 pA). Was this due to differences in cell size? The authors should consider expressing data from current recordings in terms of density (pA/pF).

We agree that presenting data as current density is useful and now do so throughout the manuscript, including in figure 1. The results in figure 1 do reflect a flow-activated increase in K^+ current as this response is partially inhibited by apamin/tram-34 (Mackay et al. eLife 2020). We state that there is “a reduction in inward current” as the entire current range in these experiments is negative of 0 pA.

5.Endothelium-specific deletion of PC-1 increased blood pressure, implying that the proposed role for PC-1 is generally applicable to the resistance arterial network; yet here, only small mesenteric vessels were studied. Given the known heterogeneity in the regulation of vascular tone by sheer stress among different arterial beds, is the identified role of PC-1 observed outside of the mesenteric circulation?

We agree that the blood pressure phenotype in Pkd1 ecKO mice suggest that flowactivates PC-1 in endothelial cells of other vascular beds to induce vasodilation. We have now discussed this concept in the manuscript.

Author Response:

Reviewer #2:

In this study, Jairaman et al used iPSC-derived microglia in which the AD-associated TREM2 gene has been knocked out to determine the impact of TREM2 loss of function on receptor-evoked Ca2+ signaling and chemotaxis. Cytoslic Ca2+ measurements were performed using the genetically-encoded ratiometric indicator Salsa6f previously developed by this laboratory. The authors made the critical discovery that loss of TREM2 leads to enhanced sensitivity and increased Ca2+ signaling of microglia to purinergic agonists, in particular to ADP. They showed that Store-operated Ca2+ entry in response to passive -maximal-store depletion by SERCA blockers was not altered in TREM2 KO cells. Rather, the enhanced sensitivity of the TREM2 KO cells was shown to originate from an upregulation of the purinergic receptors P2YR12 and P2YR13, leading to a left shift in EC50 of Ca2+ responses to ADP. The enhanced Ca2+ responses of TREM KO cells were associated with altered directional chemotaxis, whereby TREM2 KO cells showed enhanced displacement but reduced directionality. This phenotype was rescued with the application of P2YR antagonists in ADP-dependent chemotaxis assays. These results are novel, significant and of potentially broad impact to the pathology of AD. Although the molecular mechanisms of how lack of TREM2 leads to enhanced P2YRs is beyond the scope of this study, one moderate criticism of this manuscript pertains to lack of insights on how enhanced cytosolic Ca2+ leads to reduced directional chemotaxis and the potential effector proteins/pathways mediating this effect. Other relatively moderate issues and suggestions regarding controls have also been noted.

We thank the reviewer for the positive comments and a thorough evaluation of the manuscript. We have addressed specific points related to the mechanism of purinergic Ca2+ signaling in TREM2 KO microglia. The issue of precisely how Ca2+ regulates chemotaxis differently in WT and TREM2 KO microglia, while no doubt a very important question, would involve a comprehensive evaluation of how Ca2+ affects different proteins involved in microglial motility and is best suited as part of a follow up study.

Author Response:

Reviewer #1:

The manuscript by Piccolo and colleagues employs an in vitro neuruloid system to investigate the role of Hippo/YAP signaling pathway in early ectodermal fate specification. The authors examine YAP expression in forming neuruloids and test how manipulation of Hippo/Yap signaling affects their cellular composition. They observe that YAP expression is dynamic and enriched in cells occupying periphery of the neuruloid. Overactivation of the YAP activity by the Lats-kinase inhibitor TRULI leads to an expansion of TFAP2A+ cells (NNE) at early stages and of KRT18+ cells (epidermal) at later stages of development. Accordingly, the authors propose that YAP acts as a lineage determinant that (i) promotes a NNE fate during early development and (ii) impacts the fate of NNE cells by promoting an epidermal instead of a neural crest fate. Finally, the authors report that neuruloids developed with cells harboring mutations characteristics of Huntington's disease display elevated Yap activity.

The study takes advantage of the neuruloid system to examine the role of Hippo-Yap in early development and disease. A strength of the study is the use of the neuruloid as a proxy for the human embryo, which allows the authors to examine the control of spatial patterning in early development (in both wild type and altered cellular states). Yet, this model also presents significant limitations. Some of the results indicate a high degree of variability in YAP activity (and ectodermal patterning) in neuruloids obtained from different inductions. This raises the concern that the neuruloid system may interfere with Hippo/YAP. Furthermore, the model proposed by the authors is not consistent with the functional manipulations with pharmacological agents (e.g., pharmacological activation of YAP results in an increase of both neural and NNE cells; inhibition of YAP does not result in the expected phenotypes).

We thank the reviewer for her/his compliments on our work. The reviewer also points to the limitations of our neuruloid models and asks for clarifications.

The authors propose that YAP activation promotes a non-neural ectodermal (NNE) fate in early neuruloids, and subsequently drives NNE to differentiate into epidermis. However, manipulation of Hippo signaling with pharmacological inhibitors does not entirely support this, as treatment of neuruloids with agonist TRULI leads to expansion of both the PAX6 neural population and the NNE Tfap2a population. A prediction of the model is that treatment with verteporfin should neuralize the organoids, which is not the case (Fig 6A). This disconnect between the model presented in Figure 6D and the experimental results should be addressed by the authors.

We would like to thank the reviewer for this request. In our experiments we observed a dual effect of YAP activation (or HD mutation). As noted by the reviewer, ectodermal lineage- specification occurs both early (increased NNE induction) and late (enhanced epidermis differentiation and contraction of NC differentiation). Moreover, we observed a structural consequence of increased YAP activation in neuruloids, failure of the NE domain to fully close. Following the reviewer suggestion, we have now included an additional panel in Figure 6 to illustrate the phenotype alongside the difference in ectodermal lineage specification (panel E). We have also added in the Discussion a paragraph that highlights the architectural aspect of the observed phenotype.

Regarding the interpretation of the effect of pharmacological inhibition of YAP, we believe that the result of verteporfin treatment on WT neuruloids indicates that YAP activity is not required for this specification but can skew the differentiation towards NNE and epidermis. This is now included in the Results, and a new paragraph has been added in the Discussion directly addressing this point.

The study at times conflates YAP expression with activation of the Hippo-YAP pathway. While the images in figures 1,2, and 4 show changes in YAP expression, confirmation of Hippo-YAP pathway activity should include the use of a reporter (e.g., HOP-Flash) or at least high magnification images showing translocation of YAP to the nucleus. Overall, inclusion of better quantification of YAP-activity is crucial to support the manuscript's conclusions (the authors should also state the number of micropatterns used in each quantitative experiment).

Our evidence correlating YAP nuclear localization with activity is based on: (i) Immunoblots (Figures 1D and 2B); (ii) Confocal image analysis (Figures 1E, 2D, and 4B); and (iii) Induction of YAP target-genes expression as demonstrated by our scRNA-seq analysis, occurs in same epidermal (KRT18+) lineage cells that display the highest levels of YAP nuclear accumulation (Figure 2). However, to strengthen this argument and following the reviewer’s advice, we have now added magnified confocal microscope images of YAP/DAPI staining used to measure nuclear YAP localization at D4 (Figure 1—figure supplement 5). We have also added a slowed and magnified videos of the YAP-GFP/H2B-mCherry (and YAP-GFP alone) at D3-D4, which illustrates the dynamic accumulation of YAP in the nucleus of cells upon BMP4 stimulation (Figure 1—video 2, Figure 1—video 3, Figure 1—video 5, Figure 1—video 6, Figure 4—video 2 and Figure 4—video 3). Finally, the number of colonies analyzed for each experiment is now added in the Figure Legends.

A limitation of the study is that it does not investigate the possibility that Hippo/Yap could be affecting cell proliferation in the different lineages, instead of acting as a cell fate determinant. This is particularly important since Hippo is affected by cell density, which varies from the center to the periphery of the neuruloid. Different rates of proliferation over several days could potentially lead to drastic changes in neuruloid cellular composition.

To address the reviewer’s legitimate point, and assess to potential effects of YAP activation in HD-neuruloids, we performed three sets of experiments. First, we performed RNA-velocity analysis to determine the cellular trajectories within each lineage (FigureXA, below), and calculated the velocity of Seurat’s “cell cycle-associated” genes in each cell population in our scRNA-seq dataset at D4. This analysis indicates that the three ectodermal progenitors have a comparable rate of cell division, with NE being slightly faster than the others and epidermis being the slowest (Figure XB). However, these differences are subtle: the mean velocity of these cell-cycle genes within each population are not significantly different across the three ectodermal lineages (FigureXC). Second, comparison of velocity values between WT and HD, highlighted a significant HD-associated increase in the dynamic of cell-cycle associated genes only within the NE population (FigureXD), consistent with the observation that YAP is ectopically active in this lineage. This increase is also not very dramatic, for the mean velocity of these genes is not significantly different in any comparison at this time (Figure XE).

Figure X. Proliferation rate analysis of D4 neuruloid from scRNAseq dataset. A) transcriptional trajectories were identified in the three ectodermal lineages. B) Velocity of cell cycle associated genes show that NNE lineages (NC and E) are slightly faster than NE. C) However this is not significant the mean population level. D) NE in HD D4 neuruloids display subtle increase in the velocity of cell cycle associated genes. E) Such effect disappears at the mean population level.

Finally, quantification of the number of mitotic nuclei per colony as marked by phospho-histone H3 (Kim et al., 2017) at different time points, demonstrated that YAP activation by TRULI leads to an increase in cell proliferation, especially in late neuruloids. This evidence is now presented in the new Supplemental Figure 4—figure supplement 3. We thank the reviewer for bringing this point to our attention.

It is also important to note that our study does not suggest that YAP is a bona fide cell-fate determinant, but rather that that the global phenotypic signature of YAP activation is influenced by differential regulation of cell-cycle dynamics. Moreover, inasmuch as YAP inhibition with verteporfin does not effect neuruloid formation, we believe that YAP is more of a booster signal operating on top of differentiation programs.

The results of the study contradict a previous reports, and some of these contradictions are not sufficiently addressed. The authors state that the activation of YAP in culture leads to a "complete loss of NC-like SOX10+ colonies"; however, a number of studies in in vivo models support a role for YAP as a positive regulator of neural crest specification.

We thank the reviewer for pointing to the results observed in model systems. We have now included a paragraph in which we acknowledge that YAP has been previously associated with NC specification and survival. However, it should be noted that these conclusions are based on data obtained from non-human model organisms such as Xenopus, or relied on differentiation protocols that are independent of BMP4 stimulation. We believe that the phenotype of unbalanced specification of the NNE depends on an epistatic relationship between BMP4 and Hippo-YAP pathway, which might play a crucial role during human neurulation.

Furthermore, the authors briefly speculate on the finding that Huntington's disease neuruloids have high YAP activity (whereas tissues from patients have low activity), but there is no real clear link to the pathophysiology of the disease.

In our in vitro assay that recapitulates aspects of human neurulation, we observed an early increase (D4) followed by a later decline (D7) in YAP activity associated with HD mutation, which is comparable to a dysregulation of the Hippo pathway that was observed in HD patients. To better clarify this aspect and its potential implication during embryogenesis we have now expanded our Discussion on the possible connection between HD and embryonic development.

Experimental results presented in different figures are often inconsistent throughout the manuscript. This should be examined by the authors since it suggests a lack of reproducibility in the neuruloid protocol. For example, the expression of TFAP2A at D4 neuruloids is a sparse halo at D4 in Fig4D, but robust in Fig1E.

The reviewer is correct in pointing to a certain degree of variability between experiments, especially during the period (D4) when the first NNE lineage begin to emerge (i.e., Supplemental Figure 4—figure supplement 2). Because parallel experimental conditions such as comparison with HD samples or TRULI treatment show consistent trends, however, we believe that our interpretation of these results is fundamentally correct.

The western blot in fig1D shows bands for tYAP and pYAP at D4, while in Fig2B the bands are not present (Fig1D also shows double bands for both markers while fig2B presents single bands).

There are several splicing alternative isoforms of human YAP (Vrbský et al., 2021). Immunoblots for YAP in YAP-GFP biallelically tagged cell lines (Figure 1—figure supplement 1B) show that two isoforms are detectable at pluripotency. During neural induction (D1-D3) both isoforms are downregulated, and upon BMP4 stimulation the larger isoform (top band) is primarily upregulated, so that from D4 onwards only the top band is visible (Figure 2B). To better clarify this point, we now discuss this in the Results and include Supplemental Figures with the quantification of the top and bottom bands (D1-D4, Figure 1D) and only of the top band (D4D7, Figure 2B and Figure 1—figure supplement 4).

As Hippo responds very quickly to cell density, mechanical forces, etc., these inconsistencies could affect the proposed analyses.

As previously mentioned, we have assessed the effect on proliferation rate due to YAP activation by TRULI or HD mutation in neuruloids by scRNA-seq analysis and by counting the number of mitotic cells at different times. Our manuscript leaves open the relationship between HTT mutation and YAP hyperactivation, which likely is mediated in part by these factors, but we do address possible connections in the discussion.

Reviewer #2:

This manuscript by Piccolo et al identifies YAP signalling as key player in lineage determination during development of early human ectoderm. Additionally, the authors show that neuroloids generated using cells engineered to express penetrant levels of CAG repeats in the HTT gene display aberrant YAP signalling during ectodermal specification and that this phenotype can be partially rescued by inhibition of this pathway. This is interesting study and the similarity of the YAP-activated neuroloids and the HD neuroloids is striking. The value of this work would be increased by providing experiments to definitively demonstrate the role of YAP signalling in NNE specification and in HD neuroloids.

We also thank this reviewer for her/his compliments on our work. The reviewer also expresses specific recommendations listed below:

Specific comment: The authors describe the emergence of non-neuronal ectoderm (NNE) at the edges of the printed island cell colony and neuronal ectoderm (NE) within this circular colony. However, they do not show images of any lineage markers confirming that these regions are, in fact, NNE and NE.

We show in Figure 1E that the edges of the neuruloids are positive for TFAP2A, a marker for the NNE lineage. In Figure 4D we also show TFAP2A at the edge (NNE) and PAX6 at the center (NE). Additionally, the spatial identity of the various ectodermal lineages was full characterized in our previous study (Haremaki et al., 2018).

They also don't show that this YAP-GFP cell line recapitulates endogenous fix-and-stains of YAP in these colonies.

Figure 1E shows YAP expression at D4 by immunolabeling for YAP/DAPI acquired by confocal microscopy, which recapitulates that of immunofluorescence detection of nuclear YAP , shown in Figure 4B , and the results obtained by live fluorescence (YAP-GFP/H2B, Figure 4A).

Author Response:

Reviewer #2:

Weaknesses:

The competition assay used in this study may not truly reflect the competitiveness of SSIMS males. The mating assay used 20 virgin WT females and 4 males (including both WT and SSIMS), resulting 5:1 sex ratio so the males are not really competing for females. A more competitive ratio (such as WT females: WT males: SSIMA males at 1:1:1) should be designed to address this. Also, the sperm competition assay mixed the mated WT females with SSIMS males for 12 days, allowing plenty of time for the females to remate with these males. Therefore, it's more like a sperm replacement assay rather than competition assay. The authors should either repeat it with a strict time control, or soften their statements for sperm competitiveness.

We have repeated the experiment at a 1:1:1 ratio as suggested. The new results are reported in the revised Figure 3. It is not clear to us how the timing of the mating experiments differentiates sperm competition versus sperm displacement, but we agree that sperm displacement is a better term to describe what we did. We have repeated the sperm displacement experiment with strict time control based on several published literature precedents and describe the results in the revised manuscript.

Some necessary information or statistics are not shown or mis-presented. For example, the alternative splicing diagram in Figure 1c likely was taken from the original transformer gene, but here it's the tTA gene so the male intron should be removed since it's not in the construct;

We have revised text in the manuscript to clarify some of these points. First of all, the male intron is still in the construct, even though we fused the intron to the tTA gene. The alternative splicing between males and females is caused by use of alternative 5' splice sites, which means the intron that is spliced out in males is just a smaller section of the intron that is spliced out in females. Use of an alternative 5' splice site in males means that a protein-coding sequence with multiple stop codons is incorporated to the mature mRNA. We do not support the precise splicing mechanism with empirical data in this paper, but this has been done in a number of previous publications (https://doi.org/10.1016/j.ibmb.2014.06.001; https://doi.org/10.1371/journal.pone.0056303).

Because the construct works as predicted (100% female lethality in the absence of tetracycline), and we did not change the genetic design in a way that would impact the mechanism of female lethality, we think there is little reason to believe that the splicing is occurring in a different way.

the panels of Figure 2 were not consistent to the legend and confusing; the statistics for different tetracycline concentration tests were not shown in Figure 2 or text to answer their hypothesis "(to) optimize rearing of SSIMS stock, …..we titrated Tet in the food";

We re-wrote the text describing Figure 2 to make the results more clear. We clarified in the legend that the symbol signifies p<0.0001 (we were not trying to imply that all experiments had this level of significance, only the ones marked with the symbol in the figure). We removed the word ‘optimize’ from the main text. Optimization was not the true aim of the experiment, and as the review points out, we did not statistically determine an optimal concentration of Tet. Our main goal was to show a dose- dependent response in the number of females surviving on Tet-free medium, which the data supports and which does not require statistical support.

Figure 3b shows 5-8 day old females were used but in the text it's 5-6 day, and it didn't mention the duration of the first crossing and time lag until the second crossing which are critical in such experiments; the conclusion and statistics for Figure 3c among tests with mixed males should also be mentioned.

We have corrected the figure (now Figure 3c) to indicate that the females were 5-6 days old. The first mating was for 5-6 days and there was no lag time between being co-housed with different males. We have performed multiple new experiments in revision that have been added to Figure 3. We have revised the discussion of these new experiments (and how they relate to the originally performed experiments) in the revised submission.

The discussion is largely towards the merits of SSIMS but missing some key points that might decide how it can be translated into applications or transferred to other species. First, the actual basis for tTA lethality that employed in this study is still unknown which is subject to suppression by a pre-existing inherent variation in the targeted field population. The very phenomenon may also be true for any gene-overexpression-based lethality including EGI lines generated here. Second, the complete penetrance observed from the relatively small sample size here can be hardly used to predict field or mass-rearing condition. Previous study showed that mutations in such lethal construct could occur at a one out of 10,000 frequency, and typical SIT program release millions of sterile insects every week. Third, while the authors claimed SSIMS is "one of the most complex engineered systems in insects", they also proposed that "the genetic design is likely to be portable to other species" without mention any potential obstacles along the way. Therefore, efforts should be made to give full picture of SSIMS including rain and sunshine.

We have added discussion of possible failure modes for this genetic biocontrol approach to the discussion section. We have also added text to discuss how the complexity of SSIMS is a potential obstacle to its translation to non-model organisms.

Author Response:

Reviewer #1 (Public Review):

This manuscript is a follow-up of an earlier manuscript using the LRET technology, but extends the study by identifying a new "open" state and using experimental distance constraints to provide molecular models of the different states. All in all, the manuscript is well written, the experiments are described in sufficient details and experiments are done to high quality with the appropriate controls. The data corroborate the partially open state as published early, but extend the study to a second, open state. It is very good to see that the observed states are not only present in the catalytic head but the authors also use the full-length protein and find similar states. However, in the present manuscript, I find the conceptual advance with respect to the mechanism of MR somewhat limited. The authors curiously do not include any DNA in their structural studies, so the observed states are only relevant for the free MR complex, but not the complex "in action" bound to DNA where quite different conformations might occur. As one consequence, the structurally proposed states do not directly correlate with the functional nuclease states that are necessarily bound to DNA. Perhaps as a consequence, in the author's model, Rad50 is merely a gate-keeper for Mre11, but this is not the case as recent structural work shows that Rad50 forms a joint DNA binding surface with Mre11. Likewise, biochemical studies are done with physiologically unclear/less relevant 3' exonuclease activity only, but not with the physiological important 5' endonuclease activity. In my opinion, it is important for a publication in a journal with the scope of eLife and addressed to a broad audience to provide structural analysis in the presence of DNA and validate the structures using the endonuclease activity.

We thank the reviewer for these comments.

Specific recommendations:

1) Instead of using the physiological unclear exo activity, I suggest to use the more relevant endonuclease activity to validate the mutants.

We now include plate- and gel-based endonuclease activity assays, using a variety of DNA substrates, for all of the validation mutants. We have expanded Fig. 3 and included a new Supplemental Fig. S4 to show this data. We have expanded the Results section of the modified manuscript to present and discuss these findings.

2) Since the authors mutated one side of newly identified/proposed salt-bridges, I also suggest to test whether a charge reversal on both sides of the salt bridge rescues the phenoptype. I find this important because MR has quite many conformations, and mutating a single residue might not unambiguously validate the proposed conformation, a rescue by a charge reversed salt bridge is much stronger.

We thank the Reviewer for this suggested experiment, and we tried to do it. Although we were successful in generating each of the charge reversal mutations in full-length Rad50, all of the mutants unfortunately had issues with either expression or purification. For example, the 6x His-tag for several of the new Rad50 mutants was not accessible to the TEV protease for cleavage indicating that the mutated proteins were mis-folded (the His-tag of the WT full-length Rad50 is readily cleaved off by TEV). As such, we did not feel confident using these proteins in subsequent MR activity assays.

3) Since all LRET experiments are done without DNA, the authors do not capture relevant DNA processing states and comparison of structural (w/o DNA) and biochemical data (w/ DNA) is not really justified, in my opinion. Also, they might miss critical conformations. Is there a technical reason for not including DNA in the LRET studies?

We have collected LRET data on ATP-bound MRNBD in the presence of a hairpin DNA or a ssDNA as substrates. We still observe three states in the presence of both DNAs; however, the open conformation appears to be slightly more compact (i.e., closer distance between Rad50NBD protomers) in the presence of ssDNA. As described above, we have added to the Results section of the modified manuscript and included a new figure (Fig. 4) describing these data.

4) If the authors want to claim processive movement coupled to partially open/open state interchanges, they should provide experimental evidence. Where would the energy come from for such a movement, this is not clear from the model?

On the surface, ATP hydrolysis by Rad50 would seem to be the perfect source of energy for the conformational changes that drive the sequential and/or processive nuclease functions of the MR complex. However, the D313K mutant is not as good at ATP hydrolysis as the wild type enzyme (Fig. 3E), and the data in Fig. 3 and Supplemental Fig. S4 clearly demonstrate that D313K is by far the best nuclease. If the free energy for the movement does not come from ATP hydrolysis, where else could it come? Richardson and co-workers measured a release of -5.3 kcal mol-1 (-22.17 kJ mol-1) of free energy for the hydrolysis of a DNA phosphodiester bond (Dickson, K.S. et al. 2000 J. Biol. Chem. 275:15828–15831). Thus, the free energy released from the Mre11 nuclease activity could be the driving force for the conformational changes we propose. We have made this point in the Discussion of the revised manuscript.

5) The SAXS data for the "open" state do not validate the model, in my opinion. Experimental data and model are not inconsistent, but the curve looks to me as if the open state is perhaps much more flexible (i.e. an ensemble) or extended? Please comment.

We agree with the Reviewer on this point. We have updated Fig. 5A (original Fig. 4) to include the two-state fits to the experimental SAXS data. Although the multi-state fit to the apo MR SAXS data is better than any of the single model fits (2 = 1.05 vs. 1.26, respectively), the 2 is still larger than the multi-state fits to the ATP-bound MR SAXS data. Thus, an additional unobserved conformation (perhaps the so-called “extended”) might be present in solution for apo MRNBD. We have added a sentence to the revised manuscript with this point.

To explore the possibility that the previously described “extended” structure might be contributing to the SAXS data, we built a model of the extended conformation of Pf MRNBD based on the Tm MRNBD structure (PDB: 3QG5) and used Rosetta to connect the coiled-coils and add the linker to the Mre11 HLH. When this model was used in the FoXS calculations for the apo SAXS data, the 2 was 4.77 (versus 2 of 1.26 for the “open” model). The MultiFoXS two-state fit gave 90% open + 10% closed (2 of 1.04), whereas the three-state fit gave 65% open + 20% extended + 15% part open (2 of 0.84). Thus, there is some improvement when using the extended model, but since that model is not measurable in our LRET experiments and we are unsure of its validity as we have modeled it for Pf MR, we have chosen to omit it from the analysis.

6) Distance errors for the full complex are much smaller than those for the catalytic module only (Fig. 1d). Does that mean that the full complex is more rigid, please comment?

From looking at the data presented in Fig. 1D, it is logical to suggest that the full-length complex may be more rigid or better defined by the LRET data. However, we note that there are nearly as many distance errors which are similar between MRNBD and MR as there are MR errors less than MRNBD. And although many are not identical, most are of a similar magnitude. Because of this, we do not think the variations in LRET errors are systematic (i.e., related to a more rigid full-length complex).

Author Response:

Reviewer #1 (Public Review):

Summary

The authors have discovered and characterized a novel genetic pathway responsive to hypoxia, which acts in parallel to the canonical response through activation of Hypoxia-Inducible Factor (HIF). Specifically, the authors discovered that the Caenorhabditis elegans nuclear hormone receptor NHR-49, ortholog to mammalian PPAR-alpha, is essential for survival under hypoxic conditions and regulates target gene expression that is hif-1-independent; identifying an essential role of autophagy. Further the authors discover both positive and negative regulators of NHR-49 and a putative feedback loop.

Overall analysis

The genetic analysis conducted by the authors is outstanding. However, the study is lacking in a few key areas and the authors may have over-interpreted results in a few places, which diminishes my overall enthusiasm. These concerns are addressable and doing so would greatly strengthen the manuscript. I highlight individual major concerns below, and save minor concerns and specific suggestions for private recommendations for the authors.

Major concerns

1 The authors have provided strong genetic evidence for a parallel mechanism to canonical HIF-1 activity in response to hypoxia. The authors should more rigorously test whether there is evidence for cross-talk between the two mechanisms. In the discussion the authors' highlight findings in mammals that support this possibility. For example, does loss of one lead to hyperactivation of the other in an attempt to compensate for hypoxia?

We thank the reviewer for suggesting these interesting experiments to examine cross-talk!

Specific examples:

• In regards to lines 425-426, does loss of hpk-1 stabilize HIF-1 (or does hpk-1(oe) repress hif-1)?

We attempted to study HPK-1–HIF-1 cross talk via GFP imaging of the UL1447 HIF-1::GFP strain after hpk-1 RNAi (Figure R4, below). However, although we did observe an increase in GFP levels in hypoxia (vs. normoxia), we did not observe nuclear localization, possibly due to the rapid degradation of HIF-1 in normoxia, which occurs inevitably during our experimental procedure. We therefore opted not to include these data in the manuscript.

Figure R4: Regulation of HIF-1::GFP. Quantification of GFP levels in UL1447 (unc-119(ed3) III; leEx1447 [hif-1::GFP + unc-119(+)) adult animals expressing HIF-1::GFP. Animals were fed EV RNAi or nhr-49, hif-1, hpk-1, or nhr-67 RNAi as indicated and exposed to 4 hr of 0.5% O2 without recovery (three repeats totalling >30 individual animals per strain). X/, XXX,**** p <0.05, 0.001, 0.0001 (two-way ANOVA corrected for multiple comparisons using the Tukey method).

• Does loss of hif-1 or nhr-49 alter the expression, stability, or activity of the other (either under normoxic or hypoxic conditions)?

We appreciate the reviewer’s interest in examining the interaction between nhr-49 and hif-1. To address this, we generated an NHR-49::GFP;hif-1(-) strain and analysed it by imaging after exposure to normoxia or hypoxia. Although loss of hif-1 does result in a slight whole-body up-regulation of NHR-49::GFP, this increase was not significant (new Figure 2—figure supplement 1C, D). Higher magnification images did not show a tissue-specific effect in NHR-49::GFP increase in the hif-1(-) background either (new Figure 2D, Figure 2—figure supplement 1E, F). For reasons mentioned above, the HIF-1::GFP;nhr-49(RNAi) experiment was inconclusive.

• Can overexpression of either hif-1 or nhr-49 rescue the developmental defects caused by loss of the other (i.e. overexpress hif-1 in nhr-49 mutant animals, and vice versa).

With the new NHR-49::GFP;hif-1(-) strain, we were able to study compensatory effects of overexpressing NHR-49 in hif-1 mutants by performing embryo hypoxia survival experiments (new Figure 2E). Excitingly, while NHR-49 overexpression does not provide enhanced hypoxia survival at baseline (vs. non-GFP siblings), NHR-49 overexpression rescued the deficiency of hif-1 mutants. This suggests that nhr-49 can partially compensate for loss of the hif-1 pathway. Testing whether HIF-1::GFP overexpression rescues nhr-49 loss requires non-GFP sibling controls. Although the UL1447 strain expresses HIF-1::GFP from an extrachromosomal array, in our hands, we never observed non-GFP worms (i.e. 100% HIF-1::GFP offspring), and therefore were unable to test whether HIF-1 overexpression compensates for nhr-49 loss.

• Does NHR-67 negatively regulate hif-1 (specificity to NHR-49)?

As noted above, we were unfortunately unable to conclusively assessed HIF-1::GFP levels, likely due to rapid degradation during the normoxia that occurs during animal harvest.

2 The role of autophagy in hypoxia should be explored in greater detail. While the evidence presented by the authors clearly demonstrates autophagy is essential for hypoxic survival, autophagy is an important component of many biological processes. Thus, it's critical to distinguish whether autophagy is merely required (perhaps for very indirect reasons) or whether autophagy is a part of an adaptive response to hypoxia. The authors (Miller lab) previously failed to find a role for autophagy in hypoxia (Fawcett et al. 2015 Aging Cell), which should be addressed. Has autophagy been previously linked to hypoxia in C. elegans? The novelty of this discovery should be discussed in greater detail.

We appreciate that the link of autophagy to hypoxia survival needed to be examined further. We now provide substantial new evidence showing that not only are autophagy genes and autophagosome formation induced in hypoxia, but also that mutations in autophagy genes result in hypoxia sensitivity. In our opinion, this strongly supports a key role for autophagy in hypoxia adaptation.

We note that the study by Fawcett et al., 2015 studied only two genes in hypoxia, bec-1 and unc-51, none of which were found to be regulated by hypoxia in our RNA-seq analysis. Another study from the Miller lab found that an 18-hour anoxia exposure of L2/L3 stage C. elegans results in a significant induction of autophagy in the intestine (Chapin et al., 2015; Fig 4B, C). Although the conditions in this study are different than in ours (anoxia vs. hypoxia, exposure time, animal developmental stage), this study, like ours, thus finds that that low oxygen availability induces autophagy. Besides the Miller lab, there are several other publications that show an important role for autophagy in hypoxia adaptation across species (Samokhvalov et al., 2008; Zhang et al., 2008). Especially relevant to our manuscript is a recent paper published while we were revising our manuscript, which shows that autophagy gene induction is HIF-1 independent in Drosophila melanogaster (Valko et al., 2021). This agrees well with our exciting new discoveries. We have revised the text to better discuss this context.

3 The authors have possibly over-interpreted their results in Figure 4B and the possibility that NHR-49 acts cell non-autonomously. The authors speculate that tissue specific genetic rescue by NHR-49 over-expression could indicate the existence of a signaling molecule (line 499). Ectopic over-expression of a transcription factor within one tissue is always tricky to interpret, as it may not be physiologically relevant, which I fear may be the case as rescue is achieved when NHR-49 is over-expressed within any tissue (i.e. there is no specificity). An alternative explanation, which is a more indirect model, is that NHR-49 over-expression shifts metabolism within a tissue to generate metabolites that are released throughout the organism to sustain it during hypoxia.

We thank the reviewer for this excellent point, and agree that indirect action of NHR-49 remains a possibility. We have added discussion to this point in the revised manuscript.

4 As an extension of MC#3, the authors demonstrate that NHR-49 is induced throughout the animal after hypoxia (Figure 5A). Presumably sites of NHR-49 induction (tissues) equates to the sites where nhr-49 is necessary. However, the images within 5A cannot be resolved to identify individual tissues, higher resolution images are necessary and quantification of GFP expression within individual tissues could lend biological insight.

We now provide higher resolution images of NHR-49::GFP in Figure 2D, Figure 2—figure supplement 1E, F.

5 The gene expression analysis is lacking details. For example, the RNA-seq data shown in Figure 3A&B is confusing. The numbers in the text do not match the figure and it is unclear whether the intersection in the Venn Diagram represent inverse relationships (i.e. the proportion of genes that are upregulated in wild-type that are either hif-1 or nhr-49 dependent). Greater detail and explanation is needed, as presented little biological insight can be discerned from the Figure 3A&B. Next, qRT-PCR validation of autophagy gene expression found in Figure 3C should be provided with that result. Lastly, are there existing datasets for changes in gene expression of C. elegans exposed to hypoxia? If so, how do the datasets compare?

We apologize for the confusion and have revised our text describing the RNA-seq analysis as well as the Figure legend. We also provide validation of the RNA-seq data with GFP-reporters and have compared our dataset to a previous study on hypoxia dependent gene regulation in C. elegans.

6 The authors identify a putative negative feedback loop between NHR-67 and NHR-49, and suggest this regulation is at the protein level (Figure 5F,G) based on a translational reporter and not transcriptional regulation based on qRT-PCR results and similar results previously found with hpk-1 (Figures S5A, 7a, and a previous study). However, the authors should more rigorously rule out dynamic changes in expression between tissues that cannot be ascertained by qRT-PCR (i.e. test whether nhr-49p::GFP expression is altered after nhr-67(RNAi) +/- hypoxia.

We agree and have more rigorously studied this interaction.

Author Response:

Reviewer #1 (Public Review):

The manuscript by Gaubitz et al. reports structures of the yeast clamp loader (RFC)-sliding clamp (PCNA) complex in 6 different states during the clamp loading cycle. Although structures of yeast, human, E. coli and T4 clamp-loader-clamp complexes have been determined previously in various states, a major advance of the authors' work is to obtain structures of distinct intermediates in a single system. These structures provide a detailed description of the conformational changes in both RFC and PCNA during clamp loading, explaining ordered PCNA and primer/template DNA binding by RFC, the mechanism of clamp opening and closing, and the regulation of RFC's ATPase activity. In addition, the structures reveal differences in the mode of primer/template recognition between yeast and T4/E. coli clamp loaders. RFC melts the final base pair of the primer/template duplex using a separation pin in RFC-A, which is not seen in T4 or E coli clamp loaders. The authors confirm this interesting and unexpected observation biochemically. Although the authors speculate this mechanism could be used for distinguishing primer/template substrates from other DNA structures, the physiological significance of DNA melting and base flipping by RFC remains unclear. Overall, the findings reveal new nuances of the clamp loading cycle but the manuscript could be strengthened by solidifying the importance of base flipping for substrate recognition and RFC function.

We thank the reviewer for their support. As mentioned above, we report new experiments examining the role of base-flipping residues on DNA binding and cell physiology (Figure 6 – Figure Supplements 2&3)

Reviewer #2 (Public Review):

In this study, Gausman et al. use cryo-electron microscopy to elucidate structures of complexes between the eukaryotic clamp loader (RFC) and its ligands, the DNA polymerase processivity clamp (PCNA) and DNA. Clamp loaders and clamps are required for DNA replication and repair in all domains of life. Understanding of the molecular mechanisms of clamp loading is not only important for DNA replication and repair, but also because clamp loaders are members of a larger group of motor proteins which are critical to many aspects of cellular metabolism. To date, our structural understanding of clamp loader mechanisms is based on comparison of structures for different clamp loader-ligand intermediate complexes from a variety of organisms including E. coli, yeast, bacteriophage, and humans. This paper presents the first structural data for multiple clamp loader-ligand intermediate complexes from a single organism, Saccharomyces cerevisiae, and sheds new light on protein-ligand interactions. Importantly, this work highlights structural features of the clamp loader that give rise to the order of ligand binding where the clamp loader binds and opens the clamp before binding DNA.

To capture clamp loader ligand complexes, RFC was bound to the slowly hydrolyzable ATP analog, ATPγS, and intermediate complexes were further stabilized by protein crosslinking, predominantly intramolecular crosslinking of RFC subunits. Two types of RFC-PCNA complexes were observed, one in which the PCNA ring closed and a second where it is open. A family of closed complexes was observed in which three of the five RFC subunits contact the surface of the PCNA ring. Rigid body modeling suggests that this closed complex is dynamic such that the plane of the ring 'swings' relative to the clamp loader to potentially allow all five clamp loader subunits to engage the clamp to open the ring. In the open complex, the diameter of the complex expands and the opening in the PCNA ring is large enough to allow ds DNA to enter the ring and the chamber formed by the RFC subunits. A large hinge-like conformational change in the RFC-A subunit on going from closed to open complexes creates a channel for the ssDNA template to bind and exit the chamber. These remarkable structures show that the clamp loader is not in a suitable conformation to bind DNA prior to forming an open clamp complex which favors clamp binding before DNA binding.

This manuscript provides remarkable insight into intermediate complexes that exist in the clamp loading reaction pathway. Having a family of structures for a single clamp loader and clamp provides a clearer picture of and highlights differences in clamp loading mechanisms from different organisms. Overall, this work well done, but perhaps some of the mechanistic conclusions drawn from static structures should be viewed with caution in the absence of rigorous dynamic or kinetic approaches.

1) Crosslinking the proteins to stabilize intermediates could potentially bias the pool of conformations that are observed.

We agree that crosslinking can bias the population of conformations observed. That is one of the reasons why we refrain from interpreting the number of particles in each class as being representative of the actual population of that intermediate.

2) A statistical analysis of the differences in the ATPase activities of wild-type and mutant clamp loaders would be helpful to determine whether the mutations have an effect on the activity. Moreover, steady-state ATPase activity was measured in this experiment and these rates may not reveal differences in rates of intermediate steps in the clamp loading reactions. For the mutations to affect the ATPase activity, they would have to either change the rate of the rate-limiting step in the pathway or change the identity of the rate-limiting step. Thus, the decrease in ATPase activity for W638G mutant could be interesting if statistically significant.

As mentioned above, we now report this analysis and interpretation in more detail.

3) Given that Phe-582 and Trp-638 seem to be important for binding DNA at the 3' end, an analysis of the effects of mutations to these residues on DNA binding activity would be informative.

As mentioned above, we report experiments examining these residues on DNA binding (Figure 6 – Figure Supplement 1) and new experiments measuring ATPase activity in the presence of various DNA substrates (Figure 6 – Figure Supplement 2).

4) Kinetic data in the literature support a mechanism in which the clamp loader hydrolyzes ATP prior to clamp closing. In the absence of supporting kinetic data, it may be overinterpreting structural data to assert that the clamp loader need not hydrolyze ATP prior to closing the clamp.

As mentioned above in detail, we agree and have toned down the interpretation.

Author Response:

Reviewer #1:

Suction feeding is recognized as a nearly ubiquitous prey capture mode in fishes, and the hydrodynamics of these flows are reasonably understood. Provoni et al. deal with a role that is as important but much less understood, i.e. the role of these flows in intra-oral prey transport. Specifically, they ask how the flows within the buccal cavity can help transport the prey into the mouth. The major obstacle to understand these flows is that they are internal, so it was difficult to quantify them.

Here, the authors developed and used a technique that enabled tracking of tracer particles that are smaller and less dense than the prey, thereby improving our ability to quantify the flows. They show that the suction flows can be directed towards the esophagus at least in one of the species they used, and that repeated bidirectional flows can be used to redirect particles trapped at the branchial basket towards the esophagus. In doing so, they highlight the role of the suction flows in transport of food, providing a possible explanation to the ubiquity of suction flows even among fish that don't rely on the external flows to capture their prey.

Quantifying internal flows is a demanding task, and the paper presents new and exciting data. As is typical to new techniques, there are important limitations to its current use. The tracers are larger than those used for particle imaging velocimetry, and are heavier than the water. Therefore, they don't track the water precisely. It is difficult to predict the error generated due to this limitation, because it depends on the velocity gradients in the flow (for example accelerations). Additionally, the number of tracers is limited, so they provide a partial representation of the flows within the mouth. It stands to reason that particles drawn from different locations will have different trajectories, however this is not quantitatively analyzed.

Particle tracking can lend itself to a quantitative analysis of the transport flows, but unfortunately the paper does not take full advantage of these capacities. The intake flow patterns are qualitatively described, and a quantitative estimate of the volume of water that passes near the esophagus are examples for such potential. Other important parameters such as efficiency can be potentially derived directly.

The most important message of the results presented is that the flow of water inside the mouth has a functional role in moving the prey towards the esophagus, and that it can differ between species. These results teach us that the suction flows are important not only to prey capture but also to prey transport.

Thank you for your interesting public review.

In a revised version of the paper, we have evaluated the effect of size and density on tracking performance of our particles using CFD analysis. The results are presented in a new Figure (Figure 8), which is further illustrated by a video (Figure 8 – video 1). It serves to quantify the limitations due to particle size and buoyancy imperfection.

The CFD results reassure that the finite size (1.4 mm diameter) and density (up to about 1050 kg m-3) of the current sample of particles (Figure 7) does not hinder a realistic assessment of the suction flows by fish. A small deviation of the path in the direction of gravity can be expected (Figure 8b), but this should be smaller than 1 mm even for the heaviest particles of 1050 kg m-3. Lag during flow acceleration and overshoot during deceleration for the slightly negatively buoyant particles was relatively small (Figure 8c) and therefore acceptable to describe general patterns of flow during suction feeding.

Reviewer #2:

This is a fascinating study that adds great resolution to the mechanisms of water flow in the mouth of fish during suction feeding. Using high-speed x-ray video (XROMM) to track food items and particles in the water, the authors show convincingly that fish have an intriguing ability to generate flows that center the food at the esophagus, and that intraoral flow differs between species. The video is impressive, showing all the particles flow into the mouth, and separation to direct food to the gullet and water to the outflow exit (gill arches).

The methods of XROMM and particle tracking are quite well known -- there is nothing new in either approach, nor in combining them to track the prey item. However, the authors created a new kind of marker to enable tracking water flow patterns; a bead surrounded by foam, to create neutral buoyancy, that worked really well. Overall a fascinating study that adds to our understanding of suction feeding in fish.

Thank you for your nice public review.

We agree that our statement about the method novelty was confusing in the original version of the manuscript, especially in the sentence from the introduction. We rewrote it to: “Here, we develop a new technique based on biplanar high-speed X-ray videography to quantify the 3D pathlines of intraoral water and combine it with existing methods to track food and quantify 3D skeletal motions.” This should clearly separate the new contribution from the existing methods and make it clear that we see the tracking of water as a separate method in addition to the tracking of food. The latter has indeed been done previously in many 2D x-ray studies, and in more recent 3D biplanar X-ray studies. The revised paragraph in the discussion now reverts back to the x-ray particle tracking protocols that have been used in industrial settings (reference Drake et al. 2011).