Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public Review):

The study by Vengayil et al. presented a role for Ubp3 for mediating inorganic phosphate (Pi) compartmentalization in cytosol and mitochondria, which regulates metabolic flux between cytosolic glycolysis and mitochondrial processes. Although the exact function of increased Pi in mitochondria is not investigated, findings have valuable implications for understanding the metabolic interplay between glycolysis and respiration under glucose-rich conditions. They showed that UBP3 KO cells regulated decreased glycolytic flux by reducing the key Pi-dependent-glycolytic enzyme abundances, consequently increasing Pi compartmentalization to mitochondria. Increased mitochondria Pi increases oxygen consumption and mitochondrial membrane potential, indicative of increased oxidative phosphorylation. In conclusion, the authors reported that the Pi utilization by cytosolic glycolytic enzymes is a key process for mitochondrial repression under glucose conditions.

Comments on revised version:

This reviewer appreciates the author's responses addressing some of the concerns.

(1) However, the concern of reproducibility and experimental methods applied to the study is still valid, particularly considering that many conclusions were drawn from western blot analysis. The authors used separate gel loading controls for western blot analysis, which is not a valid method. Considering loading and other errors/discrepancies during the transfer phase of the assay, the direct control should be analyzing the membrane after transfer or using an internal control antibody on the same membrane. None of the western blots are indicated with marker sizes, and it isn't very clear how many repeats there are and whether those repeats are biological or technical repeats.

We thank the reviewer for raising this concern. This point requires detailed clarification regarding two key points: the first one regarding the use of Coomassie stained gels over internal ‘housekeeping gene’ antibodies, and the second one regarding the challenges in performing controls for western blots In case of high abundance proteins such as glycolytic enzymes.

(1) In our western blots, we have used Coomassie stained gel as a loading control for all our western blots. This is performed by cutting one half of the gel and using it for transfer followed by blotting and using the other half for Coomassie staining. I.e. This is not two separate gels that are loaded, but the same gel. Practically, this is no different from cutting a membrane to blot with different antibodies. This method is of course valid method for normalizing western blot data, and is used by multiple studies, for the reasons mentioned below. The historical use of a ‘house-keeping’ gene as a loading control for western blotting assumes that the protein levels of these does not change under different conditions. However, this approach has multiple, severe limitations (since a ‘housekeeping gene’ is entirely contextual, and indeed), and therefore it is correct to use total protein as a loading control. This is indeed recommended for use by multiple studies (Collins et al., 2015). Coomassie staining for total protein is far more reliable than using house-keeping genes as a loading control in western blots (Welinder and Ekblad, 2011). A notable example would be GAPDH itself, which is widely used as a loading control in many studies. As is clear from our data in this manuscript, GAPDH levels itself decrease in ubp3Δ cells. Had we used GAPDH as a loading control, we wouldn’t have identified the decrease in glycolytic enzymes in ubp3Δ cells, and this story would have met with a tragic fate very early on in its inception. We have in fact be very careful with these quantitations, and even before loading samples on gels, they are first normalized using a standard protein estimation assay (Bradford), followed by normalized loading, followed by cutting the gel into two parts - one for coomassie staining and protein normalization, and the other for the western blot for the respective proteins. However, in point (2) below, we clarify on why sometimes we have to load a separate gel with normalized protein, which should resolve this point.

(2) Glycolytic enzymes are highly abundant proteins and to achieve a signal in the linear range of western blot, the protein extracts have to be diluted (up to 25 or 50 times). As discussed under point 1, an internal control ‘housekeeping gene’ antibody is not a reliable method to use as loading control. Even if we want to use an antibody for an internal protein as a control, there are not many proteins that are as abundant as metabolic enzymes and because of this simple reason, the sample dilution results in these proteins not getting detected in the western blot since the signal will be below the limit of detection. This leaves using a separate gel loading control as the only easy to perform, reliable option.

We would like to further highlight the fact that the changes in metabolic enzymes and ETC proteins that we observe in the ubp3 mutant by western blot, were also independently observed by large scale untargeted quantitative proteomics study by  (Isasa et al., 2015), which we cite extensively in this manuscript. Since an entirelyindependent study, using a completely different (untargeted) method has also shown very similar  changes in proteins that we observe (mitochondrial, and glycolytic enzymes), there should be no room for doubt regarding the altered glycolytic enzyme and ETC protein  levels that we discover in this study.

None of the western blots are indicated with marker sizes

We have clearly indicated the marker sizes in all our western blots. Separately, raw images of the blots and Coomassie stained gels have been provided with the manuscript raw data, and is therefore easily available for any interested reader.

It isn't very clear how many repeats there are and whether those repeats are biological or technical repeats.

We have already clearly indicated the details of each blot in the figure legends. For example “A representative blot (out of three biological replicates, n=3) and their quantifications are shown. Data represent mean ± SD.” We kindly request the reviewer to thoroughly go through the figure legends for details regarding the western blots, or any other data. We hope this addresses all the reviewer concerns regarding the credibility of our western blot results and the method of using Coomassie stained gels as loading controls in this study.

(2) Concern regarding citing the Ouyang et al. paper is still valid. This paper is an essential implication in phosphate metabolism and is directly related to some of the findings associated with mitochondrial function, along with conflicting results, which should be discussed in the discussion section. As a reviewer, I do not request citing any paper from the authors in general; however, considering some of the conflicting results here, citing and discussing paper from Ouyang et al. will improve the interoperation/value of their findings.

As mentioned in detail in our previous response  letter, we do not believe that the study from Ouyang et al., present ‘conflicting results’ of any kind. Nevertheless, in response to the reviewer's suggestion, we have revised the discussion section of our manuscript and added a few points that  incorporate the insights from Ouyang et al. These are in the discussion section (“It is important to highlight that our experiments, whether involving Pi supplementation or Pi limitations, maintain the cellular Pi concentration within the millimolar range and are conducted within a short timeframe (~ 1 hour). This differs significantly from Pi starvation studies, where cells are subjected to prolonged and complete Pi deprivation, triggering extensive metabolic adjustments to sustain available Pi pools, such as an increase in mitochondrial membrane potential, independent of respiration”). We trust that this modification will enhance the interested readers' understanding of our study's overarching conclusions.

Reviewer #2 (Public Review):

Summary:

Cells cultured in high glucose tend to repress mitochondrial biogenesis and activity, a prevailing phenotype type called Crabree effect that observed in different cell types and cancer. Many signaling pathways have been put forward to explain this effect. Vengayil et al proposed a new mechanism involved in Ubp3/Ubp10 and phosphate that controls the glucose repression of mitochondria. The central hypothesis is that ∆ubp3 shift the glycolysis to trehalose synthesis, therefore lead to the increase of Pi availability in the cytosol, then mitochondrial received more Pi and therefore the glucose repression is reduced.

Strengths:

The strength is that the authors used an array of different assays to test their hypothesis. Most assays were well designed and controlled.

Weaknesses:

I think the main conclusions are not strongly supported by the current dataset. Here are my comments on authors' response and model.

(1) The authors addressed some of my concerns related to ∆ubp3. But based on the results they observed and discussed, the ∆ubp3 redirect some glycolytic flux to gluconeogenesis while the 0.1% glucose in WT does not. Similarly, the shift of glycolysis to trehalose synthesis is also not relevant to the WT cells cultured in low glucose situation. This should be discussed in the manuscript to make sure readers are not misled to think ∆ubp3 mimic low glucose. It is likely that ∆ubp3 induce proteostasis stress, which is known to activate respiration and trehalose synthesis.

But based on the results they observed and discussed, the ∆ubp3 redirect some glycolytic flux to gluconeogenesis while the 0.1% glucose in WT does not. Similarly, the shift of glycolysis to trehalose synthesis is also not relevant to the WT cells cultured in low glucose situation.

We would like to clarify that we do not observe a redirection of glycolytic flux to gluconeogenesis in ubp3 mutant. What we observe is a rewiring of glycolytic flux into increased trehalose synthesis and PPP, and decreased glycolysis. Also, the shift of glycolysis to trehalose synthesis is relevant to WT cells cultured in low glucose. It is a well-known fact that the trehalose synthesis increases with decrease in media glucose. In case of 0.1% glucose, this increase in trehalose is not due to an increase in gluconeogenesis (since the pathways utilizing alternate carbon sources still remain repressed  in 0.1% glucose (Yin et al., 2003)), but by the increase in glycolytic flux towards trehalose. This is also supported by increase in Tps2 protein levels upon decreasing glucose concentration (Shen et al., 2023). We will also note that there are very few studies that actually estimate gluconeogenic flux in cess (and they only rely on steady state measurements). Estimating gluconeogenic flux appropriately is challenging in itself (eg. see Niphadkar et al 2024). 

In case of glucose concentrations lower than 0.1%, the shift to trehalose synthesis might not be as relevant. We observe that the glycolysis defective mutant tdh2tdh3 cells does not show an increase in trehalose synthesis (Figure 3-figure supplement 1E). However, in this context, the decrease in the rate of GAPDH catalyzed reaction alone appears to be sufficient to increase the Pi levels (Figure 3F) even without an increase in trehalose. Therefore, there might be differences in the relative contributions of these two arms towards Pi balance, based on whether it is low glucose in the environment, or a mutant such as ubp3Δ that modulates glycolytic flux. In ubp3Δ cells, the combination of low rate of GAPDH catalyzed reaction and high trehalose will happen (based on how glycolytic flux is modulated), vs only the low rate of the GAPDH catalyzed reaction in tdh2tdh3 cells. As an end point the increase in Pi happens in both cases, but this happens via slightly differing outcomes. Also note: in terms of free Pi sources a low-glucose condition (with low glycolytic rate) is very different from a no-glucose, respiratory condition (where cells perform very high gluconeogenesis, at a rate that is an order of magnitude higher than in low glucose). In respiration-reliant conditions such as in ethanol, cells switch to high gluconeogenesis, where there is a large increase in trehalose synthesis as a default (eg see Varahan et al 2019). In this condition, trehalose synthesis could become a major source for Pi (eg see Gupta 2021). This could also support the increased mitochondrial respiration. In an ethanol-only medium, the directionality of the GAPDH reaction is itself reversed (i.e. G-1,3-BP → G-3-P). Therefore, this reaction now becomes an added source of Pi, instead of a net consumer of Pi (see illustration in Figure 3G). Therefore, a very reasonable inference is that a combination of increased trehalose and increased 1,3 BPG to G3P conversion can become a Pi source, supporting increased mitochondrial respiration in a non-glucose, respiratory medium.

We have now clarified these points in the discussion section in the updated version of our manuscript. Lines xxx. We hope that this updated discussion section satisfies the reviewer’s concern regarding how relevant the increase in trehalose synthesis is for altered Pi balance and increased mitochondrial respiration in WT cells.

It is likely that ∆ubp3 induce proteostasis stress, which is known to activate respiration and trehalose synthesis.

Apart from some general changes in metabolism, there are no reports whatsoever that suggest that general proteostasis stress can results in an extensive, precise metabolic rewiring - where there is an increased in respiration, mitochondrial de-repression, precise decrease in two limiting glycolytic enzyme levels, and a precise reduction in glycolytic flux, as observed in the ubp3 mutant. If this was the case, deletion of any deubiquitinase should result in an increase in trehalose and respiration which clearly does not happen (as is already clear from the large screen shown in Figure 1)

However, in response to this query, we performed experiments to assess the extent of proteostasis stress in ubp3 mutants. For this, we have now estimated the changes in global ubiquitination in WT vs ubp3 mutant, and compared this with conditions of moderate proteostasis stress (mild heat shock at 42C/~1hr). These data are now included in the revised manuscript as Figure 1- figure supplement 1J. Notably, our analysis reveals only very minor  alteration in global ubiquitination levels in ubp3 mutants compared to WT cells. This is in very stark contrast to  limited heat stress, where a clear increase in global ubiquitination can be easily observed. Given these data, we can conclude that there is no significant general proteostatic stress in ubp3 mutants, that could induce substantial metabolic rewiring of such precise nature.

(2) Pi flux: it is known that vacuole can compensate the reduction of Pi in the cytosol. The paper they cited in the response, especially the Van Heerden et al., 2014 showed that the pulse addition of glucose caused transient Pi reduction and then it came back to normal level after 10min or so. If the authors mean the transient change of glycolysis and respiration, they should point that out clearly in the abstract and introduction. If the authors are trying to put out a general model, then the model must be reconsidered.

In Van Heerden et al., the pulse addition of glucose causes transient Pi reduction due to rapid Pi consumption in glycolysis. The phosphate levels came back to normal level because of the glucose flux into trehalose synthesis releasing free Pi. This is the entire crux of the study and this is the reason why tps2 mutants which cannot synthesize trehalose exhibit a growth defect and have decreased Pi levels. As explained in detail in our early response, the cellular Pi levels are maintained by a relative balance of reactions that consume and release Pi and therefore a change in this balance can change Pi as well. Indeed, if this were not the case, the tps2 mutants would simply maintain the Pi levels similar to WT cells by increasing Pi transport from the medium, which is clearly not the case (eg see Gupta 2021).

The cytosol has ~50mM Pi (van Eunen et al., 2010 FEBSJ), while only 1-2mM of glycolysis metabolites, not sure why partial reduction of several glycolysis enzymes will cause significant changes in cytosolic Pi level and make Pi the limiting factor for mitochondrial respiration. In response to this comment, the authors explained the metabolic flux that the rapid, continuous glycolysis will drain the Pi pool even each glycolytic metabolite is only 1-2mM. However, the metabolic flux both consume and release Pi, that's why there is such measurement of overall free Pi concentration amid the active metabolism. One possibility is that the observed cytosolic Pi level changes was caused by the measurement fluctuation.

The measurement fluctuations that we mentioned in our previous response letter was in case of cells grown in high and low glucose, where there are multiple factors such as mitochondrial amount which complicates the Pi measurements. In case of ubp3 mutants which have a similar amount of total mitochondria as that of WT cells, there is minimal fluctuation for Pi measurement. We have done extensive standardization of mitochondrial isolation and Pi measurement in the isolated mitochondria (as explained in detail in the manuscript) to minimize any such fluctuations. 

However, the metabolic flux both consume and release Pi, that's why there is such measurement of overall free Pi concentration amid the active metabolism

The reviewer is correct in pointing out that metabolic flux consume and release Pi. However, in glucose grown yeast cells, the rate of glycolysis which is a Pi consuming reaction is higher than any other metabolic pathway. In fact, the glycolytic rate in glucose-grown S. cerevisiae is one of the highest ever observed in any living system. A decrease in glycolysis and an increase in trehalose therefore shifts the balance in Pi utilization and results in increased free Pi in ubp3 cells. For a more detailed theoretical reasoning on the consumption and production of Pi, see Gupta 2021.

Importantly, the authors measured Pi inside mito for ethanol and glucose, but not the cytosolic Pi, which is the key hypothesis in their model. The model here is that the glycolysis competes with mito for free cytosolic Pi, so it needs to inhibit glycolysis to free up cytosolic Pi for mitochondrial import to increase respiration. I don't see measurement of cytosolic Pi upon different conditions, only the total Pi or mito Pi. The fact is that in Fig.3C they saw WT+Pi in the medium increase total free Pi more than the ∆ubc3, while WT decrease mito Pi compared to WT control and ∆ubc3 and therefore decrease basal OCR upon Pi supplement. A simple math of Pitotal = Pi cyto + Pi mito tells us that if WT has more Pitotal (Fig.3C) but less Pi mito (fig.5 supp 1C), then it has higher Pi cyto. This is contradictory to what the authors tried to rationalize. Furthermore, as I pointed out previously, the isolated mitochondria can import more Pi when supplemented, so if there is indeed higher Picyto, then the mito in WT should import more Pi. So, to address these contradictory points, the authors must measure Pi in the cytosol, which is a critical experiment not done for their model. For example, they hypothesized that adding 2-DG, or ∆ubp3, suppress glycolysis and thus increase the supply of cytosolic Pi for mito to import, but no cytosolic Pi was measured (need absolute value, not the relative fold changes). It is also important to specific how the experiments are done, was the measurement done shortly after adding 2-DG. Given that the cells response to glucose changes/pulses differently in transient vs stable state, the authors are encouraged to specify that.

(1) Importantly, the authors measured Pi inside mito for ethanol and glucose, but not the cytosolic Pi, which is the key hypothesis in their model. The model here is that the glycolysis competes with mito for free cytosolic Pi, so it needs to inhibit glycolysis to free up cytosolic Pi for mitochondrial import to increase respiration. I don't see measurement of cytosolic Pi upon different conditions, only the total Pi or mito Pi.

As clearly described in the manuscript, the key hypothesis that emerges is the role of the availability/accessibility of Pi for the mitochondria, in the context of activity. As discussed in detail in the discussion section, this can come from a combination of available Pi pools in the cytosol and increased transport of this Pi to the mitochondria. While it is true that the decreased glycolysis in ubp3 mutants frees up available Pi pools in the cytosol, measurement of cytosolic Pi in these mutants growing in log phase might not necessarily show an increased cytosolic Pi, if the Pi is being actively transported the the mitochondria at a rate higher that the WT, as indicated by the ~6 fold increase in mitochondrial Pi in ubp3 cells. This would require tools such as intracellular fluorescence based-Pi sensors that could accurately capture temporal changes in cytosolic and mitochondrial Pi following glycolytic inhibition. However, these tools are not available till date for use in yeast and measuring cytosolic Pi following glycolytic inhibition over time using colorimetric Pi assays are extremely difficult.  

However, the reviewer does correctly state that we had not included measurement of cytosolic Pi. Since the mitochondrial Pi estimate was itself a very challenging (and critical) experiment we had originally thought that data was sufficient. We have therefore now performed a series of new experiments, where we first enrich the cytosolic fraction (without mitochondrial contamination), and estimated cytosolic Pi amounts in WT and ubp3 cells. Our Pi measurements indicate a cytosolic Pi concentration in the range of ~35 mM, which is similar to the earlier reported values in yeast. We further observe that the cytosolic Pi is about ~25% lower in ubp3 mutants (~25-27 mM) compared to WT cells (Figure 4B). As mentioned earlier, this would be consistent with higher transport of Pi from the cytosol to the mitochondria in these cells. Effectively, ubp3 cells have a total increase in cellular Pi, and with a Pi pool distribution such that there is increased Pi availability in mitochondria (Figure 4B). This further substantiates this hypothesis of an increased Pi allocation to mitochondria in ubp3 mutants. The reason for increased rate of Pi transport to mitochondria is not immediately clear, but could also come from changes in cytosolic pH - a possibility that we suggest in our discussion, and is discussed in a later section of this response letter as well.   

(2) The fact is that in Fig.3C they saw WT+Pi in the medium increase total free Pi more than the ∆ubc3, while WT decrease mito Pi compared to WT control and ∆ubc3 and therefore decrease basal OCR upon Pi supplement. A simple math of Pitotal = Pi cyto + Pi mito tells us that if WT has more Pitotal (Fig.3C) but less Pi mito (fig.5 supp 1C), then it has higher Pi cyto. This is contradictory to what the authors tried to rationalize. Furthermore, as I pointed out previously, the isolated mitochondria can import more Pi when supplemented, so if there is indeed higher Picyto, then the mito in WT should import more Pi.

a) “The fact is that in Fig.3C they saw WT+Pi in the medium increase total free Pi more than the ∆ubc3, while WT decrease mito Pi compared to WT control and ∆ubc3 and therefore decrease basal OCR upon Pi supplement. A simple math of Pitotal = Pi cyto + Pi mito tells us that if WT has more Pitotal (Fig.3C) but less Pi mito (fig.5 supp 1C), then it has higher Pi cyto.”

In WT cells supplemented with external Pi (WT+Pi), there is an increased total Pi, but a decreased mitochondrial Pi. As discussed in the discussion section in the manuscript, this could be due to the supplemented Pi not being transported to mitochondria. The reviewer is correct in pointing out that as per simple math this should mean that the cytosolic Pi in WT+Pi should be high. We have now assessed cytosolic Pi upon external Pi supplementation, and this is exactly what we observe in our cytosolic Pi measurements now included in the revised manuscript (Figure 5-figure supplement 5C). There is a higher cytosolic Pi in WT+Pi (~52 mM) compared to WT cells (~35 mM) and ubp3 cells (~27 mM). We have now pointed this out in the discussion section in the revised manuscript “Notably, this increased respiration does not happen upon direct Pi supplementation to highly glycolytic WT cells, where the Pi accumulates in cytosol, without increasing mitochondrial Pi (Figure 5-figure supplement 1C).” We hope that these new data completely addresses the reviewer’s concern regarding the Pi allocations in case of WT+Pi cells.

b) This is contradictory to what the authors tried to rationalize. Furthermore, as I pointed out previously, the isolated mitochondria can import more Pi when supplemented, so if there is indeed higher Picyto, then the mito in WT should import more Pi.

We would like to clarify that the Pi measurements in WT+Pi absolutely do not contradict our hypothesis. Furthermore, nowhere do we claim that an increase in cytosolic Pi will increase mitochondrial Pi!! On the contrary, we explain in detail that supplementing Pi to WT cells (which increases cytosolic Pi) will not increase respiration if the increased Pi is not being transported to mitochondria. This is exactly what happens in WT+Pi, where Pi accumulates in the cytosol but does not result in increased mitochondrial Pi. The reviewer argues that if there is higher cyto Pi, mitochondria should import more Pi. This is true in case of transport via diffusion where the external concentration dictates the direction of metabolite transport, but is fundamentally wrong in case of transport of metabolites where active transporters and additional regulators are involved. This is the entire basis of the idea of metabolic compartmentalisation where  cells maintain pools of metabolites in different organelles which regulate the cellular metabolic state. A well-studied example is pyruvate, whose cytosolic concentration is high in glycolytic cells, but it's transport to mitochondria is reduced in glycolysis to maintain cytosolic fermentation. As discussed in the manuscript, a logical explanation for Pi supplementation not increasing respiration and mitochondria Pi is that there might be mechanisms in highly glycolytic cells that restrict the transport of Pi to mitochondria, thereby compartmentalizing Pi in the cytosol. One such possible mechanism is pH (discussed in a later section) and it is possible that there are other mechanisms involved. 

In case of isolated mitochondria, Pi supplementation results in an increased respiration simply because it is an in vitro set up where we supplement metabolites such as pyruvate, malate and ADP along with phosphate to ensure that mitochondria is actively respiring and in this case Pi will be consumed since it is being used for ATP synthesis. This is entirely different from an in vivo scenario where cells are glycolytic, and mechanisms to prevent mitochondrial transport of metabolites such as pyruvate and phosphate are active. 

c) It is also important to specific how the experiments are done, was the measurement done shortly after adding 2-DG?

Cells were treated with 2-DG for one hour and respiration was measured. We have mentioned these details clearly in the figure legends and methods.  

d) The most likely model to me is that, which is also the consensus in the field, is that no matter 2-DG or ∆ubp3, the cells re-wiring metabolism in both cytosol and mitochondria, and it is the total network shift that cause the mitochondrial respiration increase, which requires the increase of mito import of Pi, ADP, O2, and substrates, but not caused/controlled by the Pi that singled out by the authors in their model.

The aim of our study is only to highlight the importance of mitochondrial Pi availability as a critical factor in controlling mitochondrial respiration. Of course this would require sufficient other factors such as ADP, substrates and oxygen. It cannot be otherwise. However, as we point out in the discussion, a major limiting factor might be Pi availability. While the altered glycolysis in ubp3 mutants might control availability of other factors such as pyruvate and ADP, this is not the focus of our study. We would also like to point out that prior studies show that even though cytosolic ADP decreases in the presence of glucose, this does  not limit mitochondrial ADP uptake, or decrease respiration, due to the very high affinity of the mitochondrial ADP transporter. This is discussed in our discussion section as well. Further we show that the levels of ETC proteins can be altered by changing Pi levels, which places Pi as a major regulator of respiration. We would like to point out once again that studies in other systems have also highlighted a major role of mitochondrial Pi availability in controlling respiration. These references are included in our manuscript (Scheibye-Knudsen et al., 2009, Seifer et al., 2015). This includes a recent study in T cells that clearly shows increased mitochondrial respiration upon overexpressing mitochondrial Pi transporter SLC25A3 alone (Wu et al., 2023). Our manuscript now in fact provides a contextual explanation of these diverse observations from other cellular systems where mitochondrial Pi transport appears to regulate respiration.

(3) The explanation that cytosolic pH reduction upon glucose depletion/2DG is a mistake. There are a lot of data in the literature showing the opposite. If the authors do think this is true, then need to show the data. Again, it is important to distinguish transient vs stable state for pH changes.

We observe that directly supplementing Pi to WT cells growing in high glucose does not result in higher mitochondrial Pi or increased respiration. However, supplementing Pi to WT cells increases mitochondrial respiration in the presence of glycolytic inhibitor 2-DG. We therefore merely suggest that cytosolic pH could be an additional regulator of mitochondrial Pi transport, since this will be consistent with the differences in mitochondrial Pi transport in highly glycolytic cells, and cells with decreased glycolysis ( such as 2-DG addition and ubp3 mutant). This is because in mitochondria, Pi is co-transported along with protons. Therefore, changes in cytosolic pH (which changes the proton gradient) will control the mitochondrial Pi transport (Hamel et al., 2004).  The glycolytic rate is itself a major factor that controls cytosolic pH. The cytosolic pH in highly glycolytic cells is maintained ~7, and decreasing glycolysis results in cytosolic acidification (Orij et al., 2011). Therefore, under conditions of decreased glycolysis (such as loss of Ubp3), cytosolic pH becomes acidic. Since mitochondrial Pi transport depends on the proton gradient, a low cytosolic pH would favour mitochondrial Pi transport. Therefore, under conditions of decreased glycolysis (2DG treatment, or loss of Ubp3), where cytosolic pH would be acidic, increasing cytosolic Pi might indirectly increase mitochondria Pi transport, thereby leading to increased respiration. But we certainly do leave alternate interpretations to the imagination of any reader, and are indeed open to them. These are all exciting future directions this study will enable a contextual interpretation of.

The explanation that cytosolic pH reduction upon glucose depletion/2DG is a mistake.

We have cited two independent studies which suggest that cytosolic pH decreases upon a decrease in glycolysis (Orij et al.,2011 ,Dechant et al., 2010). This control of cytosolic pH by the glycolytic rate has been extensively shown using glycolytic mutants, cells in low glucose and cells grown in the presence of glycolytic inhibitors. According to the reviewer, this is a mistake and

there are a lot of data in the literature showing the opposite.

In our literature review we did not come across any relevant studies that actually show the opposite. If the  reviewer still thinks this is a mistake, the reviewer is welcome to include some of the relevant literature that clearly shows the opposite in the comments, with actual measurements of cytosolic pH. Additionally,  the possible role of cytosolic pH in this context does not affect the conclusions of our study, and we only include this as a possibility in the discussion. Therefore, this is obviously well beyond the scope of experiments in our current study, and considering the extensive data from multiple studies that shows that cytosolic pH decreases under low glycolysis, there is no relevance  to including experiments to address the same in this study. We leave this as a point for an interested reader to think about, and it certainly can nucleate new directions of future study.

Author response:

The following is the authors’ response to the original reviews.

Summary of the changes

Changes in the manuscript were made to clarify some ambiguities raised by the reviewers and to improve the report following their recommendations. A summary of the main changes is listed below:

- The title was changed to better reflect the results of this study - Re-training the model on log transformed FACS scores.

- Testing the specificity of the FEPS to facial expression of pain within this experimental setup by comparing it to the activation maps obtained from the Warm stimulation condition.

- Testing for sensitization/habituation of the behavioral measures (FACS scores and pain ratings).

- Adding a section in the discussion to better address the limitations of this study and provide potential directions for future studies.

Other changes target areas where the original manuscript may have been ambiguous or lacked precision. To address these concerns, additional details have been incorporated, and certain terms have been revised to ensure a more precise and transparent presentation of the information.

Public Reviews:

Reviewer #1 (Public Review):

Picard et al. report a novel neural signature of facial expressions of pain. In other words, they provide evidence that a specific set of brain activations, as measured by means of functional magnetic resonance imaging (fMRI), can tell us when someone is expressing pain via a concerted activation of distinctive facial muscles. They demonstrate that this signature provides a better characterization of this pain behaviour when compared with other signatures of pain reported by past research. The Facial Expression of Pain Signature (FEPS) thus enriches this collection and, if further validated, may allow scientists to identify the neural structures subserving important non-verbal pain behaviour. I have, however, some reservations about the strength of the evidence, relating to insufficient characterization of the underlying processes involved.

We are thankful for the summary of our work. We are hopeful that the modifications made in the latest version effectively address these concerns. The changes are outlined in the summary above, and detailed in the following point-by-point response.

Strengths:

The study relies on a robust machine-learning approach, able to capitalise on the multivariate nature of the fMRI data, an approach pioneered in the field of pain by one of the authors (Dr. Tor Wager). This paper extends Wager's and other colleagues' work attempting to identify specific combinations of brain structures subserving different aspects of the pain experience while examining the extent of similarity/dissimilarity with the other signatures. In doing so, the study provides further methodological insight into fine-grained network characterization that may inspire future work beyond this specific field.

We are thankful for the positive comments.

Weaknesses:

The main weakness concerns the lack of a targeted experimental design aimed to dissect the shared variance explained by activations both specific to facial expressions and to pain reports. In particular, I believe that two elements would have significantly increased the robustness of the findings:

(1) Control conditions for both the facial expressions and the sensory input. An efficient signature should not be predictive of neutral and emotional facial expressions (e.g., disgust) other than pain expressions, as well as it should not be predictive of sensations originating from innocuous warm stimulation or other unpleasant but non-painful stimulation.

We do recognize the lack of specificity testing for the FEPS, especially towards negative emotional facial expressions. This would be relevant to test given the behavioural overlap between the facial expressions of pain and disgust, fear, anger, and sadness (Kunz et al., 2013; Williams, 2003). The experimental design used in this study did not include other negative states. However, we fully support the necessity of collecting data throughout those conditions, and we believe that the present study highlights the importance of such a demonstration. Future research should involve recording facial expressions while exposing participants to stimuli that elicit a range of negative emotions but, to our knowledge, such combination of fMRI and behavioural data is currently unavailable. As raised by the reviewer, this approach would allow us to assess the specificity of the FEPS to the facial expression evoked by pain compared to different affective states. We would like to emphasise that specificity and generalizability testing is a massive amount of work, requiring multiple studies to address comprehensively. A Limitations paragraph addressing this research direction has been added to the Discussion. A conclusion was added to the abstract as follows: “Future studies should explore other pain-relevant manifestations and assess the specificity of the FEPS against other types of aversive or emotional states.”

(2) Graded intensity of the sensory stimulation: different intensities of the thermal stimulation would have caused a graded facial expression (from neutral to pain) and graded verbal reports (from no pain to strong pain), thus offering a sensitive characterisation of the signal associated with this condition (and the warm control condition).

However, these conditions are missing from the current design, and therefore we cannot make a strong conclusion about the generalisability of the signature (regardless of whether it can predict better than other signatures - which may/may not suffer from similar or other methodological issues - another potential interesting scientific question!). The authors seem to work on the assumption that the trials where warm stimulation was delivered are of no use. I beg to disagree. As per my previous comment, warm trials (and associated neutral expressions) could be incorporated into the statistical model to increase the classification sensitivity and precision of the FEPS decoding.

The experience of pain can fluctuate for a fixed intensity or after controlling statistically for the intensity of the stimulation (Woo et al., 2017). Consistent with this, the current study focused on spontaneous facial expression in response to noxious thermal stimuli delivered at a constant intensity that produced moderate to strong pain in every participant. As the reviewer points out, this does not allow us to characterise and compare the stimulus-response function of facial expression and pain ratings. The advantage of the approach adopted is to maximise the number of trials where facial expression is more likely to occur, while ensuring that changes in facial expression and pain ratings are not confounded with changes in stimulus intensity. The manuscript has been revised to clarify that point. However, we do agree that it would be interesting to conduct more studies focusing on facial expression in response to a range of stimulus intensities. This discussion has been added to the Limitations paragraph.

Furthermore, following the reviewer’s suggestion, we performed complementary analyses on the warm trials in the proposed revisions. The dot product (FEPS scores) between the FEPS and the activation maps associated with the warm condition was computed. A linear mixed model was conducted to investigate the association between FEPS scores and the experimental condition (warm vs pain). The trials in the pain condition were divided into two conditions: null FACS scores (painful trials with no facial response; FACS scores = 0) and non-null FACS scores (painful trials with a facial response; FACS > 0). The details of this analysis have been added to the manuscript (see Response of the FEPS to pain and warm section in the Methods; lines 427 to 439) as well as the corresponding results (see Results and Discussion; lines 138 to 158). The FEPS scores were larger in the pain condition where a facial response was expressed, compared to both the pain condition without facial expression and the warm condition. These results confirmed the sensitivity of the FEPS to facial expression of pain.

Reviewer #2 (Public Review):

Summary:

The objective of this study was to further our understanding of the brain mechanisms associated with facial expressions of pain. To achieve this, participants' facial expressions and brain activity were recorded while they received noxious heat stimulation. The authors then used a decoding approach to predict facial expressions from functional magnetic resonance imaging (fMRI) data. They found a distinctive brain signature for pain facial expressions. This signature had minimal overlap with brain signatures reflecting other components of pain phenomenology, such as signatures reflecting subjective pain intensity or negative effects.

We appreciate this concise and accurate summary of our study.

Strength:

The manuscript is clearly written. The authors used a rigorous approach involving multivariate brain decoding to predict the occurrence and intensity of pain facial expressions during noxious heat stimulation. The analyses seem solid and well-conducted. I think that this is an important study of fundamental and clinical relevance.

Weaknesses:

Despite those major strengths, I felt that the authors did not suffciently explain their own interpretation of the significance of the findings. What does it mean, according to them, that the brain signature associated with facial expressions of pain shows a minimal overlap with other pain-related brain signatures?

We express our sincere gratitude for the valuable insights and constructive comments on the strengths and weaknesses of the current study. We thank reviewer 2 for the encouragement to reinforce our interpretation of the significance of the findings, while acknowledging the limitations raised by the three reviewers.

A few questions also arose during my reading.

Question 1: Is the FEPS really specific to pain expressions? Is it possible that the signature includes a facial expression signal that would be shared with facial expressions of other emotions, especially since it involves socio-affective regulation processes? Perhaps this question should be discussed as a limit of the study?

We acknowledge this limitation as outlined in response to Reviewer #1. We have incorporated a Limitations paragraph to provide a more in-depth discussion of this limitation and to explore potential future avenues (lines 225 to 268). Again, please note that the demonstration of specificity is an incremental process that requires a systematic comparison with other conditions where facial expressions are produced without pain. A concluding sentence was added to the abstract to encourage specificity testing in future studies. as indicated above.

Question 2: All AUs are combined together in a composite score for the regression. Given that the authors have other work showing that different AUs may be associated with different components of pain (affective vs. sensory), is it possible that combining all AUs together has decreased the correlation with other pain signatures? Or that the FEPS actually reflects multiple independent signatures?

The question raised is consistent with the work of Kunz, Lautenbacher, LeBlanc and Rainville (2012), and Kunz, Chen and Rainville (2020). In the current study, the pain-relevant action units were combined in order to increase the number of trials where a facial response to pain was expressed, thus enhancing the robustness of our analyses. Given the limited sample size, our current dataset is unfortunately insufficient to perform such analysis as there would not be enough trials to look at the action units separately or in subgroups. While the approach of combining the different AUs has proven to be valid and useful, we recognize the value of investigating potential independent signatures associated with the different AUs within the FEPS, and examining whether those signatures can lead to more similar patterns compared to previously developed pain signatures. This discussion has been included in the Limitations paragraph in the Discussion (lines 225 to 268).

Question 3: Is facial expressivity constant throughout the experiment? Is it possible that the expressivity changes between the beginning and the end of the experiment? For instance, if there is a habituation, or if the participant is less surprised by the pain, or in contrast if they get tired by the end of the experiment and do not inhibit their expression as much as they did at the beginning. If facial expressivity changes, this could perhaps affect the correlation with the pain ratings and/or with the brain signatures; perhaps time (trial number) could be added as one of the variables in the model to address this question.

The concern raised by the reviewer is legitimate. We conducted a mixed-effects model to assess the impact of successive trials and runs on facial expressivity. Results indicate that the FACS scores did not change significantly throughout the experiment, suggesting no notable effect of habituation or sensitization on the facial expressivity in our study. Details about the analysis and the results have been added to the Facial Expression section in the Methods (lines 335 to 346).

Reviewer #3 (Public Review):

In this manuscript, Picard et al. propose a Facial Expression Pain Signature (FEPS) as a distinctive marker of pain processing in the brain. Specifically, they attempt to use functional magnetic resonance imaging (fMRI) data to predict facial expressions associated with painful heat stimulation. The main strengths of the manuscript are that it is built on an extensive foundation of work from the research group, and that experience can be observed in the analysis of fMRI data and the development of the machine learning model. Additionally, it provides a comparative account of the similarities of the FEPS with other proposed pain signatures. The main weaknesses of the manuscript are the absence of a proper control condition to assess the specificity of the facial pain expressions, a few relevant omissions in the methodology regarding the original analysis of the data and its purpose, and a biased interpretation of the results.

I believe that the authors partially succeed in their aims, as described in the introduction, which are to assess the association between pain facial expression and existing pain-relevant brain signatures, and to develop a predictive brain activation model of the facial responses to painful thermal stimulation. However, I believe that there is a clear difference between those aims and the claim of the title, and that the interpretation of the results needs to be more rigorous.

We wish to express our appreciation for the insightful and constructive critique provided. The limitation pertaining to the absence of specificity testing had been addressed in response to Reviewer #1, and it has been incorporated into the manuscript (lines 251 to 258).

The commentary made by Reviewer #3 has drawn our attention to a critical concern, namely the potential misalignment between the study findings and our original title. Consequently, we have changed the title to “A distributed brain response predicting the facial expression of acute nociceptive pain”. We also revised the interpretation of the results in the discussion section and we have added a section on limitations.

Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

I hope the following comments will be useful to improve the manuscript.

Abstract

I felt the abstract could be more clear in terms of experimental or scientific questions, hypotheses/expectations, and findings. I also feel the abstract should briefly support the conclusive claim ("is better than...": how better? Or according to what criterion? This may be more relevant than the final conclusive general sentence that does not specifically address the significance of the findings).

The abstract was revised to reinforce the functional perspective adopted to interpret brain activity produced by noxious stimuli and predicting various pain-relevant manifestations. We also mention explicitly the other pain-relevant signatures against which the FEPS is compared in this report, and we added a concluding sentence highlighting the importance of assessing the specificity of the FEPS in future studies.

Introduction - background and rationale

I would postpone the discussion around pain signature and anticipate the one about the brain mechanisms of facial expressions of pain. This will allow you to reinforce the logical flow of rationale, literature gap/question, why the problem is important, and study aims. Only then go for a review of relevant literature on signatures before providing a more specific final paragraph about the study-specific questions, expectations, and implementation. At the moment this is limited to a single very descriptive short paragraph at the end of the intro.

The introduction was structured to guide the readers through a comprehensive understanding of different pain neurosignatures. The introduction aimed to establish a robust rationale for the subsequent analyses detailed in the results section. Indeed, the presentation of that literature ensured that the discussion around pain signatures is contextualised within a broader continuous framework. We acknowledge the reviewer’s comment on the limited description of the brain mechanisms of facial expression of pain. However, this was addressed in several previous reports of our laboratory (Kunz et al. 2011; Vachon-Presseau et al. 2016; Kunz, Chen, and Rainville 2020). We have added some more details about the brain mechanisms of facial expression, and highlighted those references in the first paragraph of the introduction.

Methods and Results

(1) Was there any indication of power based on the previous work or the other signature papers? If yes, how that would inform the present analysis?

The NPS was trained on 20 participants that experienced 12 trials at each of four different intensities. The assessment of the effect sizes was performed on the Neurological Pain Signature in Han et al. (2022). That study revealed a moderate effect size for predicting between-subject pain reports, and a large one for predicting within-subject pain reports. We trained our model on 34 participants that underwent 16 trials. We expected our results to show a smaller effect size as the current experimental design only allowed us to examine spontaneous changes in the facial expression, as noted in the comments made by Reviewer #1. However, the best way to calculate the unbiased effect size of the results presented in the current study would be to test the unchanged model on new independent datasets (see Reddan, Lindquist, and Wager, 2017). Unfortunately, such datasets do not currently exist.

(2) I would clarify to the reader what is meant by normal range of thermal pain and why is this relevant. Also, I did not find data about this assessment nor about the assessment of facial expressiveness (or reference to where it can be found).

We changed this formulation to “All participants included in this study had normal thermal pain sensitivity” and we added a few references. By targeting a healthy population with normal thermal pain sensitivity, our study sought to identify a predictive brain pattern related to facial expression evoked by typical responses to pain that could eventually be generalised to other individuals from the same population. Details about the assessment of facial expressiveness have been added in the appropriate section in the Methods.

(3) That pain ratings are only weakly associated with facial responses is, in its own right, an interesting finding, as a naïve reader would expect the two to be highly positively correlated. I'd suggest discussing this aspect (in reference to previous research) as it is interesting on both theoretical and empirical grounds.

The likelihood and the strength of pain facial expression generally increase with pain ratings in response to acute noxious stimuli of increasing physical intensities, thereby leading to a positive association between the two responses that is driven by the stimulus. However, the poor correlation or the dissociation between facial pain expression and pain rating is a very well known phenomenon that can be demonstrated easily using experimental methods where the stimulus intensity is held constant and spontaneous fluctuations are observed in both facial expression and pain ratings. This result was not discussed in the current manuscript as it was already addressed in the work of Kunz et al. (2011) and Kunz, Karos and Vervoot (2018). We added the references to these studies in the revised manuscript (lines 330 to 334).

(4) It may be worth having CIs throughout the whole set of analyses.

Thanks for the suggestions, this was an oversight. The confidence intervals have been added in the manuscript where applicable.

(5) I would clarify if there are two measures of the brain signature: dot-product and activation map. Relatedly, I cannot find where the authors explained what "FEPS pattern expression scores". Can the authors please clarify?

The clarification has been added in the manuscript (lines 413 to 414).

(6) There seems to be the assumption that the relationship between pain-relevant brain signatures and facial expressions of pain would be parametric and linear. However, this might not hold true. Did the authors test these assumptions?

We indeed decided to use a linear regression technique (i.e. LASSO regression) to model the association between the brain activity and the facial expression of pain. The algorithm choice was mainly based on the simplicity and the interpretability of that approach, and our limited number of observations. The choice was also coherent with previous studies in the domain (e.g. Wager et al., 2011; Wager et al., 2013; Krishnan et al. 2016; Woo et al., 2017). Using a linear model, we were able to predict above chance level the facial expression evoked by pain using the fMRI activation. However, it is legitimate to think that more complex non linear models can better capture the brain patterns predictive of that behavioural manifestation of pain.

(7) Did the authors assess whether the FACS were better to be transformed/normalised? More generally, I would report any data assessment/transformation that has not been reported.

Thank you for this highly relevant suggestion. FACS scores were indeed not normally distributed and the analyses were conducted again to predict the log transformed FACS scores. This transformation was effective to normalize the distribution (skewness = 0.75, kurtosis = -0.84). The predictive model was confirmed on transformed data.

(8) Page 12: I am not clear on whether all the signatures are included in the same model (like a multiple regression) or if separate regressions are calculated per signature. The authors seem to imply that several regressions have been computed (possibly one per comparison with each signature?).

The correlation between the FACS scores and the pain-related signatures was computed separately for each signature. This information has been clarified.

(9) MVPA: See my main comment about warm trials and experimental/statistical design. For example, the LASSO regression model for the pain trials could be compared with a model using warm trials besides (or instead of) the unfitted model. Otherwise, add the warm trials as another predictor or within the subject level in a dummy fixed factor comprising pain and warm trials.

The inclusion of warm trials in the model training would be inconsistent with the goal of the main analysis to predict the facial expression of pain when a noxious pain stimulus is presented. Secondary analyses were conducted to compare the response of the FEPS to the warm trials compared to noxious pain trials. The dot product between the FEPS and the activation maps (FEPS scores) associated with the warm condition was computed. A linear mixed model was conducted to investigate the association between FEPS scores and the experimental condition (warm vs pain). Additional contrasts compared the warm trials with the pain trials with and without pain facial expression. The details of this analysis have been added to the manuscript (see Response of the FEPS to pain and warm in the Methods) as well as the corresponding results (see Results and Discussion).

(10) I would clarify for the reader why the separate M1 analysis has been run. Although obvious, I feel the reader would benefit from the specific hypothesis about this control analysis being spelled out together with the other statistical hypotheses within the statistical design in a more streamlined manner.

We extended the discussion on the rationale of that analysis and its interpretation taking into account the most recent results using the log transformed FACS scores (lines 125 to 133).

(11) The mixed model aimed to assess the relationship between pain ratings FEPS scores and facial scores is a crucial finding. I believe it speaks to the importance of a more complete design, which I already highlighted. I have a couple of technical questions: did the authors assess random slopes too? And, what was the strategy used to determine the random effects structure?

The linear mixed model considered the participants as a random effect, with random intercepts, considering the grouping structure in our data (i.e., each participant completed multiple trials). The reported results in the original manuscript were considering fixed slopes. However, following the reviewer’s comment, we re-computed the mixed linear models allowing the slopes to vary according to the intensity ratings. The results were changed in the manuscript to represent the output of those models.

(12) The text from lines 63 to 67 could go in the methods.

We decided to include those lines within the Result and Discussion section to give the reader more specification about the FACS scores, as this term is subsequently referenced in the following part of the Results and Discussion section. We are concerned that putting this information only in the Methods section would disrupt the reading.

Reviewer #2 (Recommendations For The Authors):

p. 4-5. When you report the positive weight clusters, you follow up with a sentence specifying which cognitive processes those brain regions are typically associated with. However, when you report the negative weight clusters, you do not specify the cognitive processes typically associated with those brain areas. I think that providing that information would be helpful to the readers.

Thanks for noticing this omission. The information has been added in the most recent version of the manuscript (lines 119 to 121).

p. 9. You specify that the degree of expressiveness of participants was evaluated. How did you evaluate expressiveness? Did you use this variable in your analyses? Were participants excluded based on their degree of expressiveness?

Details about the assessment of facial expressiveness have been added in the appropriate section in the Methods (lines 285 to 289).

p. 10. You explain that two certified FACS-coders evaluated the video recordings to rate the frequency of AUs. Could you please provide more details about the frequency measure? I think that there are different ways in which this could have been done. For instance, were the videos decomposed into frames, and then the frequency measured by summing the number of frames in which the AU occurred? Or was it "expression-based", so one occurrence of an AU (frequency of 1) would correspond to the whole period between its activation onset and offset? Both ways have pros and cons. For example, if the frequency represents the number of frames, then it controls for the total duration of the AU activation within a trial (pro); but if there were multiple activations/deactivations of the AU within one trial, this will not be controlled for (con). And vice-versa with the second way of calculating frequency.

Details about the frequency scores have been added to the manuscript (lines 315 to 319).

p. 11. When you explained how you calculated the association between the facial expression of pain and pain-related brain signatures, I felt that there was some information missing. Did you use the thresholded maps (available in the published articles), or did you somehow have access to the complete, voxel-by-voxel, raw regression coefficient maps?

The unthresholded maps were used. The information has been clarified in the latest version of the manuscript, as well as the details about the availability of the maps (see Data Availability section at the end of the manuscript).

Reviewer #3 (Recommendations For The Authors):

Format

The authors will notice that many observations about the manuscript are related to missing information and a lack of graphical representations. I believe the topic and the content of the manuscript are too complex to condense into a short report.

Title

The claim of the title is simply not substantiated by the content of the manuscript. Demonstrating that the FEPS is a distinctive (i.e., specific) marker of pain processing requires a substantially different experimental design, with more rigorous controls and a broader set of painful stimulations. The manuscript would benefit from a more accurate title.

We agree that the title could better align with our findings. We modified the title accordingly : “A distributed brain response predicting the facial expression of acute nociceptive pain”.

Abstract

I find it puzzling that the authors claim that there is limited knowledge of the neural correlates of facial expression of pain given what they describe in the first paragraph of the introduction. Besides, they propose to reanalyze a dataset that has been extensively described in Kunz et al. (2011), which is unlikely to provide any new significant information.

We respectfully disagree with that comment. We considered that three articles (i.e., Kunz et al., 2011; Vachon-presseau et al., 2016; Kunz, Chen and Rainville, 2020) on the topic do constitute limited knowledge, especially if we compare it to the very large body of literature on the neural correlates associated with pain ratings. Except for these three studies, all the other citations pertain to behavioral studies on facial expression of pain, and do not examine the brain activity related to it. Furthermore, we believe that the complementary nature of the analyses performed in Kunz et al. (2011) and in this manuscript offers new insights into our understanding of facial expression in the context of pain. Indeed, the multivariate approach used in this study addresses some limitations present in Kunz et al. (2011) univariate analyses, mainly that it provides a quantifiable way to compare the similarity between different predictive patterns (Reddan and Wager, 2017). We submit that the assessment of the FEPS against several other pain-relevant signatures provides new and important information.

Furthermore, the abstract does not clearly state the aim, and the first line of the results does not match what the authors claim in the preceding line. The take-home message (last sentence) introduces the concept of a biomarker, which, as stated before, cannot be validated with the current data/experimental design. To put it in plain words, a given facial expression (or a composite score derived from a combination of expressions) cannot be a specific biomarker for pain, because a person can always mimic the same expression without feeling pain. Whether a given facial expression can be predicted from brain activity is a different issue, and whether that prediction can differentiate between painful and non-painful origins of the facial expression is another different issue. Unfortunately, neither of those issues can be tested with the current data/experimental design. The abstract would improve if the authors would circumscribe to what they actually tested, which is accurately described in the last sentence of the Introduction.

The abstract was revised accordingly. The term ‘biomarker’ was used in accordance with preceding studies in the field (see Reddan and Wager, 2017; Lee et al., 2021). Please note that we applied the same reasoning to fluctuations in pain expression as previous studies have applied to pain ratings. Of course, we can not dismiss the possibility of someone mimicking facial expressions. Similar reasoning applies to subjective reports, as individuals can intentionally overestimate their pain experience conveyed through verbal reports. This is another case of specificity testing that cannot be addressed in the present study (see new conclusion of the abstract and discussion of limitations). The challenge of pain assessment is a classical problem within both the scientific and the clinical literature. Here, we suggest that the consideration of multiple manifestations of pain is necessary to address this challenge and will provide a more comprehensive portrait of pain-related brain function.

Introduction

I believe that the Introduction would benefit from a strict definition of what is a marker/biomarker/neuromarkers (all those terms are used in the manuscript) and what are its desirable features (validity, reliability, specificity, etc.). I also believe that the Introduction (and the rest of the text) would benefit from a critical assessment of the term "signature". The Introduction describes four existing "signatures", all of them differing in the experimental condition in which acute nociceptive pain is studied, and proposes a fifth one. Keeping with the analogy, I'm wondering whether they should be called (pain) "signatures" if there is a different one for each experimental acute pain condition, and they are so dissimilar between them when they are tested on the same condition (this dataset).

The last part of that comment raises fundamental methodological potential limitations that should be addressed in more depth in another article. That point goes beyond the scope of a research article. Regarding the stability aspect of the signatures, most of the signatures have not been studied extensively. It is thus difficult to currently assess their reliability. However, Han et al. (2022) showed high within-individual test-retest reliability for the NPS across eight different studies. Given that pain is a multidimensional experience, it is not surprising to find different patterns of activation predictive of different aspects or dimensions of the pain experience (see Čeko et al., 2022 for a similar discussion applied to negative affect).

The authors state that "As an automatic behavioral manifestation, pain facial expression might be an indicator of activity in nociceptive systems, perceptual and evaluative processes, or general negative affect." Doesn't it reflect all three of them? (and instead of or?) Why "might"?

The original sentence has been modified as follows: “As an automatic behavioral manifestation, pain facial expression is considered to be an indicator of activity in nociceptive systems, and to reflect perceptual and affective-evaluative processes” (lines 65 to 67).

Methods

The pain scale should be described. Kunz et al. used a 0-100 scale, where 50 was the pain threshold. This is crucial to interpret the 75-80/100 score for the painful thermal intensity.

The description of the pain scale has been added to the manuscript (lines 299 to 300).

Ratings for warm and painful temperatures should be reported (ideally plotted with individual-trial/subject data). In the same line of reasoning, FACS scores should be reported as well (ideally plotted with individual-trial/subject data). It would be interesting to explore the across-trial variability of pain ratings and FACS scores. That is, do people keep giving the same ratings and making the same facial expression after 16 trials? How much variability is between trials and between subjects?

The point raised in that comment was already addressed in response to a comment made by Reviewer #1 (also see the new Figures S2 and S4; see also lines 335 to 346).

How come only painful trials are analyzed? What if the FEPS signature was the same for warm and painful stimulation, thus reflecting the settings (fMRI experiment, stimulation, etc.) rather than the brain response to the stimuli?

The point raised in that comment was already addressed in response to a comment made by Reviewer #1. There was no pain expression in the warm trials and the FEPS shows no response to warm trials. This is now illustrated in the new Figure S4B (see also lines 138 to 158).

The authors propose to predict the trial-by-trial FACS composite score from the pain ratings using a LMM. However, it is interesting that they aim for an almost constant within- and between-subject pain score (75-80/100) as stated in the Methods. This should theoretically render the linear model invalid since its first (and main) assumption would be that FACS should vary linearly with the pain score. Even if patients were not aware that the temperatures were constant across trials, the variation in pain scores should be explained by random noise for a constant stimulation intensity.

Reviewer #3 raises an important point that we need to clarify. Contrary to the expectation that FACS responses should be strongly correlated to pain ratings, we posited that these response channels depend at least in part on separate brain networks that may be differentially sensitive to a variety of modulatory mechanisms (attention, emotion, expectancy, motor priming, social context, etc.). This implies that part of the variance in FACS is independent from pain ratings. We, therefore, consider what Reviewer #3 refers to as random noise to be relevant and meaningful fluctuations reflecting endogenous processes influencing one’s experience of pain and differentially affecting various output responses.

I noticed that fMRI data was analyzed with SPM5 in the original paper (Kunz et al., 2011) and with SPM8 in this manuscript. Was fMRI data re-processed for this manuscript? Were there any differences between the original analysis and this one that might induce changes in the interpretation of results?

The data were indeed re-processed using SPM8, which was the most recent version available when we started the analyses reported here. We used trial-by-trial activation maps for MVPA, which differs from what was used in the previous study (contrast maps at the level of the conditions, not the trials). We have no reason to believe that the different versions will change the message of this manuscript since those versions do not differ significantly in terms of the fMRI preprocessing pipeline (see SPM8 release notes; https://www.fil.ion.ucl.ac.uk/spm/software/spm8/). Furthermore, the aim of this present study is not to compare the different analysis parameters implemented in SPM5 vs SPM8.

What is the rationale for including PVP in the comparison among signatures? The experimental settings in which it was devised are distant from those described here.

The inclusion of the PVP was aimed at enhancing our comparative analysis with the FEPS, as we sought to investigate the potential functional meaning of the FEPS. The PVP was developed to capture the aversive value of pain, a dimension that is conceptually proximal to the interpretation of the facial expression as a manifestation of the affective response to nociceptive pain.

The LASSO-PCR approach is, in my opinion, not a procedure for (brain) decoding in this context. It is accurately described in the section title as a method for multivariate pattern analysis, or as a variable selection and regularization method for a prediction model. Here, brain activity in specific areas related to pain processing can hardly be described as "encoded", and the method just helps select those activations relevant for explaining a certain outcome (in this case, facial expressions).

We understand the point made by reviewer #3. The term brain decoding was changed for multivariate pattern analysis in the latest version of the manuscript.

Details are missing with regards to the dataset split into training, validation, and testing.

Details about the training and testing procedure were added in the manuscript (lines 383 to 385).

This might just be ignorance from me, so I apologize in advance, but what are "contrast" fMRI images? They are mentioned three times in the text but not really described. Are they the "Pain > Warm" contrasts from the original paper?

We apologize for any confusion caused by the use of the term “contrast images” which suggests a direct comparison between two experimental conditions. We have replaced “contrast images” with “activation maps” to provide a more accurate description of the nature of the data used in the multivariate pattern analysis (lines 388 to 389).

In the "Facial expression" section, the authors run an LMM to test the association between pain ratings (response variable) and facial responses (explanatory variable). If I understand correctly, in the "Multivariate pattern analysis" section they test the association between facial composite scores (response variable) and pain ratings (explanatory variable), but they obtain different results.

The analyses were recomputed on the log transformed data, as mentioned previously in the response to reviewers 1-2. The first model (in the “Facial expression” section) used the log transformed FACS scores as a dependent variable, the pain ratings as the fixed effect, and the participants as the random effect. The results of that analysis suggested that the transformed facial expression scores were not significantly associated with the pain ratings (p = .07). The second model uses both the FEPS pattern expression scores and pain ratings as fixed effects to predict facial responses. This analysis showed the significant contribution of the FEPS to the prediction of FACS scores (p < .001) and no significant effect of the pain ratings. However, a significant interaction was found (p = .03) suggesting that the prediction of the pain facial expression by the FEPS may vary with pain ratings (i.e. moderator effect). Those results have been clarified in the “Multivariate pattern analysis” section in the Methods (lines 416 to 426).

In this same section, what are "FEPS pattern expression scores"? They are used three times in the text, but I could not find their description.

The FEPS pattern expression scores correspond to the dot product between the trial-by-trial activation maps and the unthresholded FEPS signature. This information has been added to the manuscript (lines 413 to 414).

It would not be far-fetched to hypothesize that FACS scores could be predicted using solely activity from the motor cortex. The authors attempted to do this, but only with information from M1. Why did they not use the entire motor cortex, or better, regions of the motor cortex directly linked with the AUs described in the manuscript?

The selection of the primary motor area (M1) was based on the results found in Kunz et al. (2011). In this study, M1 showed the strongest correlation with facial expression of pain. There are numerous possibilities of combinations of multiple brain regions considering a variety of criteria based on distributed networks involved in motor, affective, or pain-related processes. We limited our exploration to the region with the strongest hypothesis due to practical feasibility concerns.

Results and Discussion

As a general recommendation, results should present individual data whenever possible. For example, the association between signatures and facial expression should be plotted using scatterplots.

We have added figures showing individual data when it was applicable (Figure S2; Figure S4).

The authors state that the LASSO-PCR model accounts for the facial responses to pain. I believe this is an overstatement, considering:

- A Pearson's r of 0.49 is usually considered low/weak correlation (moderate at best). In the same line, an R2 of 0.17 means that only 17% of the variance is explained by the model.

More nuanced interpretation of the results has been added to the discussion. A section has been added to highlight the limitations of the study.

- Figure 1 needs to display individual subject data and the ideal regression line.

The model was trained using a k-fold cross-validation procedure. The regression lines thus represent the model’s prediction for each one of the 10 folds (i.e. each fold is trained and tested on a different subset of the data). A scatter plot including the ideal regression line computed across all trials and subjects was added in supplementary material to illustrate the relation between the FACS scores and the FEPS pattern expression scores (Figure S4).

- Looking at Figure 1, it is clear that the model has an intercept different from zero. This means that when the FACS score was zero (i.e., volunteers did not make any distinguishable facial expression), the model predicted a score larger than zero. This is not discussed in the manuscript, and in simple terms, it means that there are brain activation patterns when no discernible facial expression is being made by the volunteers. In the original paper by Kunz et al., two groups of subjects were categorized, and one of them was a facially low- or non-expressive group (n=13). This fact is not even mentioned in the manuscript.

The categorization in the previous report (Kunz et al., 2012) was based on a pre-experimental session. All subjects were included in the current analysis. This is now indicated in the Methods (lines 287 to 289).

- On the other end of the range in Figure 1, differences between the FACS scores near the maximum range (40) are underestimated by 23 to 33 points! I guess that the RMSE is smaller (6-7 points), because many FACS scores are concentrated on the low end of the scale.

This is a very interesting comment. A section discussing the limits of the model to predict the lower and higher FACS scores has been added in the manuscript (lines 232 to 250).

It is of course acceptable to interpret the low similarity between signatures as a sign that each signature describes a different mechanism related to pain processing. However, I believe that a complete discussion should contemplate other competing hypotheses. Considering that all signatures were developed using a similar painful thermal stimulation protocol, it is reasonable to expect larger similarities between signatures. The fact that they are so dissimilar could be a reflection of model overfit, i.e., all these signatures are just fitted to these particular experimental protocols and data, and do not generalize to brain mechanisms of pain processing.

We appreciate the pertinent observation. We have included a limitations section in which we discussed, among other considerations, the possible overfitting of models and the necessity of pursuing generalizability studies (lines 225 to 268).

eLife assessment

Picard et al. propose a Facial Expression Pain Signature (FEPS) derived from functional magnetic resonance imaging (fMRI) data to predict facial expressions associated with painful heat stimulation. This important work advances our understanding of the brain mechanisms associated with facial expressions of pain. It provides solid evidence that facial expressions of pain contain information that is complementary to other pain-related brain processes. The work will be of broad interest to researchers from varied fields ranging from neurosciences to psychology and affective sciences.

Reviewer #2 (Public Review):

Summary.

The objective of this study was to further our understanding of the brain mechanisms associated with facial expressions of pain. To achieve this, participants' facial expressions and brain activity were recorded while they received noxious heat stimulation. The authors then used a decoding approach to predict facial expressions from functional magnetic resonance imaging (fMRI) data. They found a distinctive brain signature for pain facial expressions (FEPS). This signature had minimal overlap with brain signatures reflecting other components of pain phenomenology, such as signatures reflecting subjective pain intensity or negative effects.

Strength.

The authors used a rigorous approach involving multivariate brain decoding to predict the occurrence and intensity of pain facial expressions during noxious heat stimulation. The analyses are solid and well-conducted. This is an important study of fundamental and clinical relevance.

Weakness.

Despite those major strengths, the main weakness of the study is that the design and analyses do not allow us to know if the FEPS is really specific to pain expressions. Based on the analysis, it is possible to conclude that this brain signature is present when a participant is in a state of pain and displays a facial expression. However, it is possible that it would also be present when a participant experiences (another) negative state and displays (another) facial expression. It will be important, in future work, to investigate the specificity of this brain signature.

Reviewer #3 (Public Review):

In this manuscript, Picard et al. propose a Facial Expression Pain Signature (FEPS) as a distinctive marker of pain processing in the brain. Specifically, they attempt to use functional magnetic resonance imaging (fMRI) data to predict facial expressions associated with painful heat stimulation.

The main strengths of the manuscript are that it is built on an extensive foundation of work from the research group, and that experience can be observed in the analysis of fMRI data and the development of the machine learning model. Additionally, it provides a comparative account of the similarities of the FEPS with other proposed pain signatures. The main weaknesses of the manuscript are the absence of a proper control condition to assess the specificity of the facial pain expressions, as well as several limitations in the experimental setup.

I believe that the authors partially succeed in their aims, as described in the introduction, which are to assess the association between pain facial expression and existing pain-relevant brain signatures, and to develop a predictive brain activation model of the facial responses to painful thermal stimulation. However, they list several limitations in the study that should be addressed in future research in order to establish whether FEPS truly conveys distinctive information about the brain response to nociceptive stimuli.

eLife assessment

This paper provides important insights into the role of rice OsNF-YB7, an ortholog of Arabidopsis LEC1, in chlorophyll biosynthesis, uncovering the genetic and molecular basis for negative regulation of chlorophyll production in the rice embryo. Mutational analysis, gene expression profiles and protein interaction combine for convincing evidence that OsNF-YB7 represses chlorophyll biosynthesis.

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

Reviewer #3 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

It would be interesting to see how two similar genes have come to play opposite roles in Arabidopsis and rice. Interspecies complementation might help to understand this point.

Author response:

The following is the authors’ response to the original reviews.

eLife assessment

This is an important study on the regulation of chlorophyll biosynthesis in rice embryos. It provides insights into the genetic and molecular interactions that underlie chlorophyll accumulation, highlighting the inhibition of OsGLK1 by OsNF-YB7 and the broader implications for understanding chloroplast development and seed maturation in angiosperms. The results presented, including mutation analysis, gene expression profiles, and protein interaction studies, provide convincing evidence for the function of OsNF-YB7 as a repressor in the chlorophyll biosynthesis pathway.

Thank you very much for your positive assessment of our manuscript. We have carefully revised the manuscript according to the reviewers’ valuable suggestions and comments. For more details, please see the point-to-point response to the reviewers below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

Thank you for your insightful comments and suggestions. In the revised manuscript, we discussed the potential application of the chlorophyllous embryo (please see line 270-274). The presence of chlorophyll in the embryo facilitates photosynthesis at early developmental stages, potentially leading to improved seedling growth and vigor (Smolikova and Medvedev, 2016). In crops such as soybean and canola, green embryo is considered as a valuable trait due to its association with enhanced photosynthetic capacity, which consequently promotes fatty acid biosynthesis (Ruuska et al., 2004). However, chlorophyll degradation must be carefully managed during seed maturation to avoid negative effects on seed viability and meal quality (Chung et al., 2006). Interestingly, the green embryo of lotus (Nelumbo nucifera) is widely used as a food ingredient in Asian, Australia, and North America. It is employed in herbal medicine to treat nervous disorders, insomnia, and other conditions (Zhu et al., 2017; Ha et al., 2022), highlighting the significant potential value of the green embryo.

In many chloroembryophytes, such as Arabidopsis, the embryo occupies a large proportion of the seed. From an evolutionary perspective, the presence of chlorophyll in the embryo may promote adaptation in such chloroembryophytes because more reserves can be accumulated in the seed through active photosynthesis, better supporting the embryo development and subsequent seedling growth (Sela et al., 2020). On the other hand, some leucoembryophytes, such as rice, have persistent endosperm rich in storage reserves to nourish embryo development (Liu et al., 2022). Gaining the ability to accumulate chlorophyll in the embryo is unnecessary for such species. In agreement with this hypothesis, cholorophyllous embryos are more prevalent in non-endospermous seeds (Dahlgren, 1980). However, we would like to emphasize that the evolutionary force driving the divergence of chloroembryophytes and leucoembryophytes is currently almost completely unknown and deserves in-depth investigation in the future. We discussed the possible evolution of the ability to accumulate chlorophyll in the embryo, please find the details in Line 276-295.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

Thank you very much for your positive comments. We have carefully revised the manuscript according to your and the other reviewers’ comments and suggestions. Particularly, we emphasized the necessary to carry out similar tests in other organisms rather than relying on Arabidopsis to better understand the regulatory mechanism in rice.

Reviewer #3 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

We appreciate your insightful comments and suggestions. It is a very interesting question whether AtLEC1 can fully restore osnf-yb7, given the possible functional divergence between the genes in terms of regulation of chlorophyll biosynthesis in the embryo. We have previously expressed OsNF-YB7 in the lec1-1 background in Arabidopsis, driven by the native promoter of LEC1 (Niu et al., 2021). We found that OsNF-YB7 could almost completely rescue the embryo defects in Arabidopsis, indicating that OsNF-YB7 plays a resemble role in rice as the LEC1 does in Arabidopsis (Niu et al., 2021). We sought to determine whether AtLEC1 can complement the chlorophyll defect in osnf-yb7. However, given the fact that osnf-yb7 shows severe callus induction defect, which is not surprising, because many studies have shown that LEC1 is indispensable for somatic embryo development in various plant species, we are struggling to obtain the genetic materials for analysis. We have to transform OsNF-YB7pro::AtLEC1 into the WT background first, and then cross the transformant with the osnf-yb7 mutant. This is a time-consuming process in rice, but hopefully we will able to isolate a line expressing OsNF-YB7pro::AtLEC1 in the osnf-yb7 background from the resulting segregating population.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

A minor comment regarding the chlorophyll contents quantification in the study. Line 87: "The results showed that WT had an achlorophyllous embryo throughout embryonic development,...." In the TEM result, chloroplast was not observed in the WT embryo sections, indicating a lack of chlorophyll-containing structures, contrary to what was found in the osnf-yb7 embryos where chloroplasts were observed.

The authors stated that the embryo morphologies and Chl autofluorescence data showed that WT had an achlorophyllous embryo throughout embryonic development. However, the quantification of Chl levels in Figure 1D and Figure 4C showed that WT does produce some chlorophylls, albeit at lower levels than osnf-yb7 or OSGLK-OX embryos (WT values in the two figures are slightly different). This discrepancy warrants clarification to ensure consistency and accuracy in the manuscript's findings.

We re-evaluated the Chl content in the embryos of WT and OsGLK1-OX mature seeds. The result confirmed our previous finding that WT embryos produce a small amount of chlorophyll (please see the updated Fig. 4C). Notably, we observed that the dark-grown etiolated plants still have measurable chlorophyll content as reported in many studies (for example, Wang et al., 2017; Yoo et al., 2019), suggesting that there is potential bias in measuring chlorophyll content using an absorbance-based approach. We assume this possibly explains the concern you have raised.

Reviewer #2 (Recommendations For The Authors):

Mild editing for grammar is needed throughout, e.g. line 73, "It is still a mysterious why plant species".

We have carefully edited the grammar.

As a minor point, the placement of figure panels, such as in Figure 1, is not always intuitive.

Thank you for your suggestion. This figure has been revised as suggested. Please see the updated Fig. 1.

What is the significance of the two GFP mutants in Figures 2C and 2D? Is one of those the mislabeled Flag mutant?

The lines showed in Fig. 2C and D were not mislabeled. They were two independent transgenic events, both of which showed that OsNF-YB7 inhibited the expression of OsPORA and OsLHCB4 in rice. The transgenic lines overexpressing OsNF-YB7 tagging with the 3× Flag (NF-YB7-Flag) were also used for this experiment. In agreement, OsPORA and OsLHCB4 were significantly downregulated in the three independent NF-YB7-Flag lines (Fig. S4C), confirming the results showed in Fig. 2C and D.

In Figures 2G and 2H, what is that enormous band at the bottom of the gel?

The bands at the bottom of the gel were free probes. We indicated this in the revised figure.

Not until the Materials and Methods section did I realize that any of this study was being done in tobacco; the Introduction implies it's rice vs. Arabidopsis and it might be a good idea to mention the organism of study somewhere before Figure 6.

We apologize for any confusion caused by our previous writing. While the majority of this study was performed with rice plants or protoplasts, the split complementary LUC assays and BiFC assays were performed with tobacco. We have specified these in the revised manuscript as suggested.

Reviewer #3 (Recommendations For The Authors):

It would be nice if the author could show what the phenotype is in AtLEC1 OX in osnf-yb7 and also OsNF-YB7 OX in atlec1 mutants.

Thank you for your suggestion. We have previously expressed OsNF-YB7 in the lec1-1 background of Arabidopsis, driven by the native promoter of Arabidopsis LEC1 (Niu et al., 2021). Since OsNF-YB7 could rescue the embryo morphogenesis defects in Arabidopsis (Niu et al., 2021), we assumed that OsNF-YB7 plays a similar role in rice as the LEC1 does in Arabidopsis. However, it remains unknown whether expression of LEC1 in osnf-yb7 may restore the chlorophyllous embryo phenotype in rice. As the generation of genetic material is time-consuming, and especially given the fact that osnf-yb7 has a severe callus induction defect, we are struggling to obtain the complementary line for analysis. We have to transform OsNF-YB7pro::AtLEC1 in a WT background first, and then cross the transformant with the osnf-yb7 mutant. Hopefully, we will be able to isolate a line expressing OsNF-YB7pro::AtLEC1 in osnf-yb7 background, from the derived segregating population. We discussed the reviewer’s concern in the revised manuscript, please see Line 369-376.

Line 46, I think it is vague to mention that 'Like most plant species'. Some species might have different copy numbers, for example, a single GLK in liverwort M. polymorpha.

The statement has been revised. Please see Line 46.

Figures 2F and 5B, why was only one promoter region used for OsLHCB4? It would be better to have more regions like OsPORA.

Thank you for your comments. Here, we have examined more promoter regions (P1, P2 and P3) in the revised manuscript as suggested, among which, the previously selected promoter region (P3) contains both the G-box and CCAATC motifs that can be potentially recognized by GLK1. Consistent to our previous report, the results showed that OsNF-YB7 (left) and OsGLK1 (right) were associated with the P3 region, but showed no significant differences in the other probes. Please see the results in Fig. 2F and Fig. 5B of the revised manuscript.

Legend of Figures 2G, H, OsPORA (I), and OsLHCB (J) should be (G) and (H) respectively.

Corrected.

References

Chung, D.W., Pruzinska, A., Hortensteiner, S., and Ort, D.R. (2006). The role of pheophorbide a oxygenase expression and activity in the canola green seed problem. Plant Physiol 142, 88-97.

Ha, T., Kim, M.S., Kang, B., Kim, K., Hong, S.S., Kang, T., Woo, J., Han, K., Oh, U., Choi, C.W., and Hong, G.S. (2022). Lotus Seed Green Embryo Extract and a Purified Glycosyloxyflavone Constituent, Narcissoside, Activate TRPV1 Channels in Dorsal Root Ganglion Sensory Neurons. J Agric Food Chem 70, 3969-3978.

Liu, J., Wu, M.W., and Liu, C.M. (2022). Cereal Endosperms: Development and Storage Product Accumulation. Annu Rev Plant Biol 73, 255-291.

Niu, B., Zhang, Z., Zhang, J., Zhou, Y., and Chen, C. (2021). The rice LEC1-like transcription factor OsNF-YB9 interacts with SPK, an endosperm-specific sucrose synthase protein kinase, and functions in seed development. Plant J 106, 1233-1246.

Ruuska, S.A., Schwender, J., and Ohlrogge, J.B. (2004). The capacity of green oilseeds to utilize photosynthesis to drive biosynthetic processes. Plant Physiol 136, 2700-2709.

Sela, A., Piskurewicz, U., Megies, C., Mene-Saffrane, L., Finazzi, G., and Lopez-Molina, L. (2020). Embryonic Photosynthesis Affects Post-Germination Plant Growth. Plant Physiol 182, 2166-2181.

Smolikova, G.N., and Medvedev, S.S. (2016). Photosynthesis in the seeds of chloroembryophytes. Russ J Plant Physl+ 63, 1-12.

Wang, Z., Hong, X., Hu, K., Wang, Y., Wang, X., Du, S., Li, Y., Hu, D., Cheng, K., An, B., and Li, Y. (2017). Impaired Magnesium Protoporphyrin IX Methyltransferase (ChlM) Impedes Chlorophyll Synthesis and Plant Growth in Rice. Front Plant Sci 8, 1694.

Yoo, C.Y., Pasoreck, E.K., Wang, H., Cao, J., Blaha, G.M., Weigel, D., and Chen, M. (2019). Phytochrome activates the plastid-encoded RNA polymerase for chloroplast biogenesis via nucleus-to-plastid signaling. Nat Commun 10, 2629.

Zhu, M., Liu, T., Zhang, C., and Guo, M. (2017). Flavonoids of Lotus (Nelumbo nucifera) Seed Embryos and Their Antioxidant Potential. J Food Sci 82, 1834-1841.

eLife assessment

This important study contributes to our understanding on how prior exposure to a non-pathogenic Leptospira strain could prime the host to prevent severe leptospirosis following infection with a pathogenic strain. The work described is solid and broadly supports the claims, with minor weaknesses that could be addressed in future studies. The work will be of interest to scientists interested in host-pathogen interactions and leptospirosis.

Reviewer #3 (Public Review):

Summary:

Kundu et al. investigated the effects of pre-exposure to a non-pathogenic Leptospira strain in prevention of severe disease following subsequent infection by a pathogenic strain. They utilized a single or double exposure method to the non-pathogen prior to challenge with a pathogenic strain. They found that prior exposure to a non-pathogen prevented many of the disease manifestations of the pathogen. Bacteria, however, were able to disseminate, colonize the kidneys, and be shed in the urine. This is important foundational work to describe a novel method of vaccination against leptospirosis. Numerous studies have attempted to use recombinant proteins to vaccinate against leptospirosis, with limited success. The authors provide a new approach that takes advantage of the homology between a non-pathogen and a pathogen to provide heterologous protection. This will provide a new direction in which we can approach creating vaccines against this re-emerging disease.

Strengths:

The major strength of this paper is that it is one of the first studies utilizing a live non-pathogenic strain of Leptospira to immunize against severe disease associated with leptospirosis. They utilize two independent experiments (a single and double vaccination) to define this strategy. This represents a very interesting and novel approach to vaccine development. This is of clear importance to the field.

The authors use a variety of experiments to show the protection imparted by pre-exposure to the non-pathogen. They look at disease manifestations such as death and weight loss. They define the ability of Leptospira to disseminate and colonize the kidney. They show the effects infection has on kidney architecture and a marker of fibrosis. And they begin to define the immune response in both of these exposure methods. This provides evidence of the numerous advantages this vaccination strategy may have. Thus, this study provides an important foundation for future studies utilizing this method to protect against leptospirosis.

Weaknesses:

A direct comparison between single and double exposure to the non-pathogen is not possible with the data presented. The ages of mice infected were different between the single (8 weeks) and double (10 weeks) exposure methods, thus the phenotypes associated with LIC infection are different at these two ages. The authors state that this is expected, but do not provide a reasoning for this drastic difference in phenotypes. It cannot be determined if double-vaccination would provide an additional benefit, which is of importance to future work developing any vaccine treatment. An experiment directly comparing the two exposure methods while infecting mice at the same age would be of great relevance to and strengthen this work.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

As a reviewer for this manuscript, I recognize its significant contribution to understanding the immune response to saprophytic Leptospira exposure and its implications for leptospirosis prevention strategies. The study is well-conceived, addressing an innovative hypothesis with potentially high impact. However, to fully realize its contribution to the field, the manuscript would benefit greatly from a more detailed elucidation of immune mechanisms at play, including specific cytokine profiles, antigen specificity of the antibody responses, and long-term immunity. Additionally, expanding on the methodological details, such as immunophenotyping panels, qPCR normalization methods, and the rationale behind animal model choice, would enhance the manuscript's clarity and reproducibility. Implementing functional assays to characterize effector T-cell responses and possibly investigating the microbiota's role could offer novel insights into the protective immunity mechanisms. These revisions would not only bolster the current findings but also provide a more comprehensive understanding of the potential for saprophytic Leptospira exposure in leptospirosis vaccine development. Given these considerations, I believe that after substantial revisions, this manuscript could represent a valuable addition to the literature and potentially inform future research and vaccine strategy development in the field of infectious diseases.

Reviewer #2 (Public Review):

Summary:

The authors try to achieve a method of protection against pathogenic strains using saprophytic species. It is undeniable that the saprophytic species, despite not causing the disease, activates an immune response. However, based on these results, using the saprophytic species does not significantly impact the animal's infection by a virulent species.

Strengths:

Exposure to the saprophytic strain before the virulent strain reduces animal weight loss, reduces tissue kidney damage, and increases cellular response in mice.

Weaknesses:

Even after the challenge with the saprophyte strain, kidney colonization and the release of bacteria through urine continue. Moreover, the authors need to determine the impact on survival if the experiment ends on the 15th.

Reviewer #3 (Public Review):

Summary:

Kundu et al. investigated the effects of pre-exposure to a non-pathogenic Leptospira strain in the prevention of severe disease following subsequent infection by a pathogenic strain. They utilized a single or double exposure method to the non-pathogen prior to challenge with a pathogenic strain. They found that prior exposure to a non-pathogen prevented many of the disease manifestations of the pathogen. Bacteria, however, were able to disseminate, colonize the kidneys, and be shed in the urine. This is an important foundational work to describe a novel method of vaccination against leptospirosis. Numerous studies have attempted to use recombinant proteins to vaccinate against leptospirosis, with limited success. The authors provide a new approach that takes advantage of the homology between a non-pathogen and a pathogen to provide heterologous protection. This will provide a new direction in which we can approach creating vaccines against this re-emerging disease.

Strengths:

The major strength of this paper is that it is one of the first studies utilizing a live non-pathogenic strain of Leptospira to immunize against severe disease associated with leptospirosis. They utilize two independent experiments (a single and double vaccination) to define this strategy. This represents a very interesting and novel approach to vaccine development. This is of clear importance to the field.

The authors use a variety of experiments to show the protection imparted by pre-exposure to the non-pathogen. They look at disease manifestations such as death and weight loss. They define the ability of Leptospira to disseminate and colonize the kidney. They show the effects infection has on kidney architecture and a marker of fibrosis. They also begin to define the immune response in both of these exposure methods. This provides evidence of the numerous advantages this vaccination strategy may have. Thus, this study provides an important foundation for future studies utilizing this method to protect against leptospirosis.

Weaknesses:

Although they provide some evidence of the utility of pretreatment with a non-pathogen, there are some areas in which the paper needs to be clarified and expanded.

The authors draw their conclusions based on the data presented. However, they state the graphs only represent one of two independent experiments. Each experiment utilized 3-4 mice per group. In order to be confident in the conclusions, a power analysis needs to be done to show that there is sufficient power with 3-4 mice per group. In addition, it would be important to show both experiments in one graph which would inherently increase the power by doubling the group size, while also providing evidence that this is a reproducible phenotype between experiments. Overall, this weakens the strength of the conclusions drawn and would require additional statistical analysis or additional replicates to provide confidence in these conclusions.

A direct comparison between single and double exposure to the non-pathogen is not able to be determined. The ages of mice infected were different between the single (8 weeks) and double (10 weeks) exposure methods, thus the phenotypes associated with LIC infection are different at these two ages. The authors state that this is expected, but do not provide a reasoning for this drastic difference in phenotypes. It is therefore difficult to compare the two exposure methods, and thus determine if one approach provides advantages over the other. An experiment directly comparing the two exposure methods while infecting mice at the same age would be of great relevance to and strengthen this work.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major Comments

(1) Elucidation of Immune Mechanisms: The manuscript intriguingly suggests that exposure to saprophytic Leptospira primes the host for a Th1-biased immune response, contributing to survival and mitigation of disease severity upon subsequent pathogenic challenge. However, the underlying mechanisms remain broadly defined. A more detailed investigation into the cytokine profiles, particularly the levels of IFN-γ, IL-12, and other Th1-associated cytokines, could clarify the mechanism of Th1 bias. Moreover, exploring the role of antigen-presenting cells (APCs) in priming T cells towards a Th1 phenotype would add valuable insights.

In this study we continue to elucidate the immune mechanisms engaged by pathogenic and non-pathogenic Leptospira as a follow up to our previous work (Shetty et al, 2021 PMID: 34249775, and Kundu et al 2022 PMID 35392072). We, and others, have shown that saprophytic L. biflexa and pathogenic L. interrogans induce major chemo-cytokines associated with Th1 biased immune responses (Shetty et al. 2021; Cagliero et al. 2022; Krangvichian et al. 2023) and engage myeloid immune cells such as macrophages and dendritic cells. The role of antigen presenting cells such as dendritic cells in priming T cells and activating adaptive response is a separate question and can be addressed in the future. To further address this question, a recent mechanistic study (Krangvichian et al. 2023) showed that non-pathogenic leptospires (L. biflexa) promote MoDC maturation and stimulate the proliferation of IFN-γ-producing CD4+ T cells and potentially elicit a Th1-type response in mice, which also supports our current claim and it is referenced in our manuscript.

(2) Quantitative Analysis of Kidney Colonization: The manuscript reports that pre-exposure to L. biflexa did not prevent the colonization of kidneys by L. interrogans but led to a more regulated immune response and reduced fibrosis. A more nuanced quantification of bacterial loads in the kidneys, using techniques such as CFU counting or more sensitive qPCR methods, could provide a clearer picture of how saprophytic exposure affects the ability of pathogenic Leptospira to establish infection. Additionally, a time-course study showing the kinetics of bacterial colonization and clearance post-infection would be informative.

We are currently validating digital PCR to use in the future and plan to do time course studies.

(3) Characterization of B Cell and T Cell Responses: While the manuscript mentions increased B cell frequencies and effector T helper cell responses, specifics regarding the nature of these responses are lacking. For instance, detailing the isotype and specificity of antibodies produced, the proliferation rates of specific B and T cell subsets, and their functional capabilities (e.g., cytotoxicity, help for B cells) would significantly enrich the understanding of the immune response elicited by pre-exposure to saprophytic Leptospira.

Indeed, additional experiments need to be conducted to flush out the immune responses engaged after pre-exposure to saprophytic Leptospira followed by LIC challenge.

(4) Comparative Analysis with Other Models of Pre-exposure: The study primarily focuses on pre-exposure to a live saprophytic Leptospira. Including a comparison with pre-exposure to killed saprophytic bacteria, or even to other non-pathogenic microbes, could help discern whether the observed protective effect is unique to live saprophytic Leptospira exposure or if it represents a more general phenomenon of trained immunity.

Regarding the use of other non-pathogenic microbes, our lab has shown in the past that oral use of probiotic strain Lactobacillus plantarum (Potula et al 2017) also reduces the severity of Leptospirosis by recruiting myeloid cells. Thus, there may be a general phenomenon of trained immunity involved. We added this to the discussion.

(5) Assessment of Long-term Immunity: The study provides valuable insights into the short-term outcomes following saprophytic Leptospira exposure and subsequent pathogenic challenge. Extending these observations to assess long-term immunity, including memory B and T cell responses several months post-infection, would be crucial for understanding the potential of saprophytic Leptospira exposure in providing lasting protection against leptospirosis.

Long term immunity is a complex and separate question that we plan to address later.

Minor Comments

(1) Technical Specifics of Flow Cytometry Analysis: The manuscript could benefit from including more details on the flow cytometry gating strategy and the specific markers used to identify different immune cell subsets. This addition would aid in the reproducibility of the results and allow for a clearer interpretation of the immune profiling data.

We included the technical specifics of the flow-cytometry analysis in the materials and methods section. The gating strategy (Fig S1) and the specific markers (TableS1) used to identify different immune cell subsets were incorporated in the supplementary datasheet. The cell specific markers were incorporated in the figures (Fig 5 and 6) under each representative cell subset which facilitates clarity and reproducibility of immune profiling.

(2) Statistical Methodology for IgG Subtyping: The analysis of IgG subtypes in response to Leptospira exposure is intriguing but would be strengthened by specifying the statistical tests used to compare IgG1, IgG2a, and IgG3 levels between groups. Additionally, discussing the biological significance of the observed differences in IgG subtype levels would provide a more comprehensive understanding of the immune response.

We applied the ordinary One-way ANOVA test to compare the IgG subtypes between groups followed by a Tukey’s multiple comparison correction analysis (included in the figure legend of Fig 4). We addressed the biological relevance of the observed differences in IgG subtype levels in the discussion section.

(3) Details on Animal Welfare and Ethical Approval: While the manuscript mentions compliance with institutional animal care and use committee protocols, providing the specific ethical guidelines followed, such as the 3Rs (Replacement, Reduction, Refinement), would reinforce the commitment to ethical research practices.

This is addressed in our institutional IACUC which is approved and listed in Methods.

(4) Clarification of Figure Legends: Some figure legends are brief and could be expanded to more thoroughly describe what the figures show, including details on what specific data points, error bars, and statistical symbols represent.

We updated and expanded the figure legends (Fig 1-4).

(5) Revision of Introduction and Background: The introduction provides a good overview of leptospirosis and the rationale behind the study. However, it could be further improved by briefly summarizing current challenges in vaccine development against leptospirosis and how understanding the immune response to saprophytic Leptospira could address these challenges.

We revised the introduction keeping this comment in mind.

Reviewer #2 (Recommendations For The Authors):

- Perform the same challenge experiment with a hamster.

We clarified throughout the manuscript that all the work was done using the C3H-HeJ mouse model which was developed in our lab for the purpose of measuring differences in sublethal and lethal LIC infections. We leave the experiments using hamster to the investigators that have thoroughly validated the hamster model of lethal Leptospira infection.

- Review the written part where it is understood that the challenge with saprophyte strain before virulence prevents the disease.

We reviewed the manuscript to be understood that inoculation of mice with a saprophyte Leptospira before pathogenic challenge prevents severe leptospirosis and promotes kidney homeostasis and increased shedding of Leptospira in urine which is interesting. The last 2 sentences of the abstract read: “Thus, mice exposed to live saprophytic Leptospira before facing a pathogenic serovar may withstand infection with far better outcomes. Furthermore, a status of homeostasis may have been reached after kidney colonization that helps LIC complete its enzootic cycle.”

Reviewer #3 (Recommendations For The Authors):

(1) Line 83: The authors refer to the classification of Leptospira by old nomenclature. The bacteria are now categorized into clades P1, P2, S1 and S2. See Vincent et al. Revisiting the taxonomy and evolution of pathogenicity of the genus Leptospira through the prism of genomics. PLoS Negl Trop Dis. 2019 May 23;13(5):e0007270. doi: 10.1371/journal.pntd.0007270. PMID: 31120895; PMCID: PMC6532842.

We have included the categories (S1 for L. biflexa and P1+ for L. interrogans) in introduction and methods but we did not update the figures because we want to be specific about the species used in these experiments. We also include a few sentences on evolution of Leptospira species in discussion and reference Thibeaux 2018, Vincent 2019 and Giraud-Gatineau, 2024.

(2) Line 133: Please remove the extra line to be consistent with the rest of the method section format.

We addressed all formatting issues.

(3) Line 137: Are these primers specific to pathogenic L. interrogans? Or do they cross react with L. biflexa? If not specific, how long does L. biflexa stick around after infection?

The primers are specific to the genus Leptospira. Surdel et al. in 2022 used 16s rRNA target sequence to amplify L. biflexa Patoc in mice at 6 hours post infection. We did not detect any positive sample for L. biflexa with the 16s rRNA primer set because we do our analysis 30 days and 45 days post inoculation with L. biflexa. We clarified this issue in methods and results.

(4) Statistical analysis:

(a) Some of your graphs have more than 4 points on them (such as Figure 4), while the legend still reads "represents one of two independent experiments". Are these actually combined replicates in the same graph? Combining them would provide strength to your conclusions throughout your manuscript and may provide stronger power for comparisons. If they are not included, why are they not included together? Please clarify what is included in each graph, and why the two experiments were not included together.

We updated the legends with the total number of mice used in the experiment represented in the figure. Figures 1, 2, 4 and S2 contain the combined results from two independent experiments. Figures 3, 5 and 6 represent data from one of two independent experiments. For Fig 3 it would be redundant to show HE images of two experiments. Regarding Figs 5 and 6, the flow-cytometry equipment acquires data at different voltage every single time and biological samples vary between experiments even if all the markers and procedures are the same. So, we reproduce the experiment and show results from one experiment after confirming that the trend between individual experiments are the same.

(b) If ANOVA was used, were all columns compared to each other? Why in some graphs are "ns" labeled only for certain comparisons? I would suggest removing the "ns" comparisons and only highlighting the significant differences.

We have incorporated the comparison analysis between control (PBS) versus the PBS-LIC, LB versus LB-LIC and PBS-LIC versus LB-LIC in both the studies although we have compared significance between all groups.

(5) Line 165: Bacteria were not plated, extract was plated. Perhaps you mean "extract corresponding to 107-108 bacteria"?

We addressed it as follows: “Nunc MaxiSorp flat-bottom 96 well plates (eBioscience, San Diego, CA) were coated with extracts prepared from 107-108 bacteria per well and incubated at 4℃ overnight” …

(6) Line 260: The authors claim that "Exposure to non-pathogenic L. biflexa before pathogenic L. interrogans challenge provided a significant immune cell boost with an increase in overall B and helper T cell frequencies..." However, in Figure 5A, the number of B cells in both the PBS2LIC2 and the LB2LIC2 are not significantly different. Thus, the claim is not supported by the evidence provided. It appears that infection with LIC led to similar increases in B cells regardless of pretreatment.

We rephrased that title to reflect the finding that increased differences were measured in effector Helper T cells between PBS2LIC2 and LB2LIC2 (Figs 5D and 6B, 6C) and we re-wrote this section for clarity.

(7) Lines 314-315: The authors claim that it protected against kidney fibrosis, however, the data only supports that only a single exposure to LB reduced levels of a marker associated with kidney fibrosis. Fibrosis was never directly measured.

Indeed, we didn’t do Mason’s Trichrome stain to get supporting data for kidney fibrosis and only measured a fibrosis marker ColA1. We toned down this section: “ …. it may confer protection against kidney fibrosis.”

(8) Line 317: Authors state that pre-exposure induced higher antibodies in serum, however, this was never shown. Only an increase in IgG2a was shown. Please word this statement to make it clear total antibodies were never measured.

We did measure total anti-Leptospira interrogans IgM and IgG antibodies. We added the following sentence to description of these results: “In both experiments, total IgM and IgG were significantly increased in PBS-LIC and LB-LIC when compared to the respective controls, but not between PBS-LIC and LB-LIC.  Regarding IgG isotypes, IgG1…”

(9) Line 323: The authors state that the exposure "induced antibody responses that provided heterologous protection." There is no evidence that the protection is due to the antibody response in these experiments. In fact, they also showed that it induced increased T cell responses.

We toned down this statement: “In our study, exposure to a saprophytic Leptospira induced antibody responses that may provide heterologous protection against the pathogenic strain of Leptospira.”

(10) Line 328: The authors us the term "stark difference", however, only slight differences are seen.

We toned down that statement as follows:  “Differences in antibody titer among the L. interrogans infected….”

(11) Line 490: reword this sentence to provide clarity and easier to read: "inoculated once with 10^8 L. biflexa at 6 weeks and they were challenged with 10^8 L. interrogans SEROVAR Copenhageni FioCruz (LIC) at 8 weeks."

We revised the sentence.

(12) Figure 1 and 2: Quantifying bacteria in culture after infection is not meaningful, as there are numerous factors that can affect the replication in culture after infection, such as how the organ perhaps was cut before placing it in culture. The comparisons in Figure 2E and F therefore are not interpretable. I would suggest presenting this data as Culture Positive or Culture Negative.

We added these data to the figure under DFM (dark field microscopy).

(13) Figure 3A: H&E staining often leads to different qualities of stains. But is there a better image that can be chosen for the PBS1LIC1 that provides a better comparison with the other images chosen? This is not worth repeating the experiment to get one, just make the figure look better if you have one available.

We screened the images again but the one incorporated in the figure3A for PBS1LIC1 is the best.

(14) Figure 3D: I agree that the PBS-LIC treatment is significant, but please include P value, as it looks very similar to the LB-LIC group. The two LIC groups are not significantly different, so the conclusion would be pre-exposure does not mitigate renal fibrosis marker ColA in the double-exposure study.

We included the p-values in this figure. The two LIC groups are significantly different (ColA1) in the single exposure experiment, and the in double exposure we don’t expect to be able to measure ColA1 differences because the mice are older (10 wk) when we do the LIC challenge.

eLife assessment

This study presents a light-entrainable synthetic oscillator in bacteria, the optorepressilator. The authors develop a toolbox using optogenetics that makes the cellular oscillator easily controllable. This toolbox is valuable, contributing both to bioengineering and to the understanding of biological dynamical systems. The comparison with a mathematical model, population, and single-cell measurements demonstrate convincingly that the planned system was achieved and is suitable to control and study biological oscillators.

Reviewer #1 (Public Review):

Summary:

The "optorepressilator", an optically controllable genetic oscillator based on the famous E. coli 3-repressor (LacI, TetR, CI) oscillator "repressilator", was developed. An individual repressilator shows a stable oscillation of the protein levels with a relatively long period that extends a few doubling times of E. coli, but when many cells oscillate, their phases tend to desynchronize. The authors introduced an additional optically controllable promoter through a conformal change of CcaS protein and let it control how much additional CI is produced. By tightly controlling the leak from the added promoter, the authors successfully kept the original repressilator oscillation when the added promoter was not activated. In contrast, the oscillation was stopped by expressing the additional CI. Using this system, the authors showed that it is possible to synchronise the phase of the oscillation, especially when the activation happens as a short pulse at the right phase of the repressilator oscillation. The authors further show that, by changing the frequency of the short pulses, the repressilator was entrained to various ratios to the pulse period, and the author could reconstruct the so-called "Arnold tongues", the signature of entrainment of the nonlinear oscillator to externally added periodic perturbation. The behaviour is consistent with the simplified mathematical model that simulates the protein concentration using ordinary differential equations.

Strengths:

Optical control of the oscillation of the protein clock is a powerful and clean tool for studying the synthetic oscillator's response to perturbation in a well-controlled and tunable manner. The article utilizes the plate reader setup for population average measurements and the mother machine setup for single-cell measurements, and they complement nicely to acquire necessary information.

Reviewer #2 (Public Review):

Summary:

In this manuscript by Cannarsa et. al., the authors describe the engineering of a light-entrainable synthetic biological oscillator in bacteria. It is based on an upgraded version of one of the first synthetic circuits to be constructed, the repressilator. The authors sought to make this oscillator entrainable by an external forcing signal, analogous to the way natural biological oscillators (like the circadian clock) are synchronized. They reasoned that an optogenetic system would provide a convenient and flexible means of manipulation. To this end, the authors exploited the CcaS-CcaA light-switchable system, which allows activation and deactivation of transcription by green and red light, respectively. They used this system to make the expression of one of the repressilator's transcription factors (lacI) light-controlled, from a construct separated from the main repressilator plasmid. This way, under red light the oscillator runs freely, but exposure to green light causes overexpression of the lacI, pushing the system into a specific state. Consequently, returning to red light will restore the oscillations from the same phase in all cells, effectively synchronizing the cell population.

After demonstrating the functionality of the basic concept, the authors combined modeling and experiments to show how periodic exposure to green light enables efficient entrainment, and how the frequency of the forcing signal affects the oscillatory behavior (detuning).

This work provides an important demonstration of engineering tunability into a foundational genetic circuit, expands the synthetic biology toolbox, and provides a platform to address critical questions about synchronization in biological oscillators. Due to the flexibility of the experimental system, it is also expected to provide a fertile ground for future testing of theoretical predictions regarding non-linear oscillators.

Strengths:

* The study provides a simple and elegant mechanism for the entertainment of a synthetic oscillator. The design relies on optogenetic proteins, which enable efficient experimentation compared to alternative approaches (like using chemical inducers). This way, a static culture (without microfluidics or change of growth media) can be easily exposed to flexible temporal sequences of the zeitgeber, and continuously measured through time.

* The study makes use of both plate-reader-based population-level readout and mother-machine single-cell measurements. Synchronization through entrainment is a single cell level phenomenon, but with a clear population-level manifestation. Thus, this experimental approach combination provides a strong validation to their system. At the same time, differences between the readout from the two systems have emerged, and provided a further opportunity for model refinement and testing.

* The authors correctly identified the main optimization goal, namely the effective leakiness of their construct even under red light. Then, they successfully overcame this issue using synthetic biology approaches.

* The work is supported by a simplified model of the repressilator, which provides a convenient analytical and numerical means to draw testable predictions. The model predictions are well aligned with the experimental evidence.

Weaknesses:

* Even after optimizing the expression level of the light-sensitive gene, the system is very sensitive, i.e., a very short exposure is sufficient to elicit the strongest entertainment. This limited dynamic range might hamper some model testing and future usage.

* As a result of the previous point, the system is entrained by transiently "breaking" the oscillator: each pulse of green light represents a Hopf bifurcation into a single attractor. it means that the system cannot oscillate in constant green light. In comparison, this is generally not the case for natural zeitgebers like light and temperature for the circadian rhythms. Extreme values might prevent oscillations (not necessarily due to breaking the core oscillator), but usually, free running is possible in a wide range of constant conditions. In some cases, the free-running period length will vary as a function of the constant value.

While the approach presented in this manuscript is valid, a comprehensive analysis of more subtle modes of repressilator entrainment could also be of value.

* The entire work makes use of a single intensity and single duration of the green pulse to force entrainment. While the model has clear predictions for how different modalities should affect entrainment, more experiments are needed to validate those predictions.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews.

Reviewer #1 (Public Reviews):

Summary:

The "optorepressilator", an optically controllable genetic oscillator based on the famous E. coli 3-repressor (LacI, TetR, CI) oscillator "repressilator", was developed. An individual repressilator shows a stable oscillation of the protein levels with a relatively long period that extends a few doubling times of E. coli, but when many cells oscillate, their phases tend to desynchronize. The authors introduced an additional optically controllable promoter through a conformal change of CcaS protein and let it control how much additional CI is produced. By tightly controlling the leak from the added promoter, the authors successfully kept the original repressilator oscillation when the added promoter was not activated. In contrast, the oscillation was stopped by expressing the additional CI. Using this system, the authors showed that it is possible to synchronise the phase of the oscillation, especially when the activation happens as a short pulse at the right phase of the repressilator oscillation. The authors further show that, by changing the frequency of the short pulses, the repressilator was entrained to various ratios to the pulse period, and the author could reconstruct the so-called "Arnold tongues", the signature of entrainment of the nonlinear oscillator to externally added periodic perturbation. The behaviour is consistent with the simplified mathematical model that simulates the protein concentration using ordinary differential equations.

Strengths:

Optical control of the oscillation of the protein clock is a powerful and clean tool for studying the synthetic oscillator's response to perturbation in a well-controlled and tunable manner. The article utilizes the plate reader setup for population average measurements and the mother machine setup for single-cell measurements, and they compensate nicely to acquire necessary information.

Weakness:

The current paper added the optogenetically controlled perturbation to control the phase of oscillation and entrainment, but there are a few other works that add external perturbation to a collection of cells that individually oscillate to study phase shift and/or entrainment. The current paper lacks discussion about the pros and cons of the current system compared to previously analyzed systems.

Recommendations

Even if the main purpose of the current paper is to develop a toolbox, it is beneficial to emphasize the pros and cons of the current system compared to the existing work. In addition to the ref [36] that authors cite but do not discuss concretely, example literature about entrainment includes:

- Sanchez, P.G.L., Mochulska, V., Denis,  C.M., Mönke, G., Tomita, T., Tsuchida-Straeten, N., Petersen, Y., Sonnen, K., François, P. and Aulehla, A., 2022. Arnold tongue entrainment reveals dynamical principles of the embryonic segmentation clock. Elife, 11, p.e79575.

- Heltberg M, Kellogg RA, Krishna S, Tay S, Jensen MH. Noise induces hopping between NF-κB entrainment modes. Cell systems. 2016 Dec 21;3(6):532-9.

There is surely more literature. It is recommended that a solid discussion be added on the relation between existing works and current work.

We thank the Reviewer for their positive comments on our manuscript. Their main recommendation is to expand literature and discuss how our method compares to previously reported entrainment of genetic oscillators. In summary, we believe that the main advantages of the optorepressilator are the simplicity of the transcriptional network combined with the flexibility of optical control. In the “Discussion” section of the revised manuscript, we now try to highlight this also in connection to the suggested literature.

Reviewer #2 (Public Reviews):

Summary

In this manuscript by Cannarsa et. al., the authors describe the engineering of a light-entrainable synthetic biological oscillator in bacteria. It is based on an upgraded version of one of the first synthetic circuits to be constructed, the repressilator. The authors sought to make this oscillator entrainable by an external forcing signal, analogous to the way natural biological oscillators (like the circadian clock) are synchronized. They reasoned that an optogenetic system would provide a convenient and flexible means of manipulation. To this end, the authors exploited the CcaS-CcaA light-switchable system, which allows activation and deactivation of transcription by green and red light, respectively. They used this system to make the expression of one of the repressilator's transcription factors (lacI) light-controlled, from a construct separated from the main repressilator plasmid. This way, under red light the oscillator runs freely, but exposure to green light causes overexpression of the lacI, pushing the system into a specific state. Consequently, returning to red light will restore the oscillations from the same phase in all cells, effectively synchronizing the cell population.

After demonstrating the functionality of the basic concept, the authors combined modeling and experiments to show how periodic exposure to green light enables efficient entrainment, and how the frequency of the forcing signal affects the oscillatory behavior (detuning).

This work provides an important demonstration of engineering tunability into a foundational genetic circuit, expands the synthetic biology toolbox, and provides a platform to address critical questions about synchronization in biological oscillators. Due to the flexibility of the experimental system, it is also expected to provide a fertile ground for future testing of theoretical predictions regarding non-linear oscillators.

Strengths:

The study provides a simple and elegant mechanism for the entertainment of a synthetic oscillator. The design relies on optogenetic proteins, which enable efficient experimentation compared to alternative approaches (like using chemical inducers). This way, a static culture (without microfluidics or change of growth media) can be easily exposed to flexible temporal sequences of the zeitgeber, and continuously measured through time.

The study makes use of both plate-reader-based population-level readout and mother-machine single-cell measurements. Synchronization through entrainment is a single cell level phenomenon, but with a clear population-level manifestation. Thus, this experimental approach combination provides a strong validation to their system. At the same time, differences between the readout from the two systems have emerged, and provided a further opportunity for model refinement and testing.

The authors correctly identified the main optimization goal, namely the effective leakiness of their construct even under red light. Then, they successfully overcame this issue using synthetic biology approaches.

The work is supported by a simplified model of the repressilator, which provides a convenient analytical and numerical means to draw testable predictions. The model predictions are well aligned with the experimental evidence.

Weaknesses:

Even after optimizing the expression level of the light-sensitive gene, the system is very sensitive, i.e., a very short exposure is sufficient to elicit the strongest entertainment. This limited dynamic range might hamper some model testing and future usage.

As a result of the previous point, the system is entrained by transiently "breaking" the oscillator: each pulse of green light represents a Hopf bifurcation into a single attractor. it means that the system cannot oscillate in constant green light. In comparison, this is generally not the case for natural zeitgebers like light and temperature for the circadian rhythms. Extreme values might prevent oscillations (not necessarily due to breaking the core oscillator), but usually, free running is possible in a wide range of constant conditions. In some cases, the free-running period length will vary as a function of the constant value. While the approach presented in this manuscript is valid, a comprehensive analysis of more subtle modes of repressilator entrainment could also be of value.

The entire work makes use of a single intensity and single duration of the green pulse to force entrainment. While the model has clear predictions for how those modalities should affect entrainment, none of the experiments attempted to validate those predictions.

While we agree with the Reviewer that all reported experiments were performed with pulses of constant amplitude and duration, we do not see this as a necessary limitation for future studies on the optorepressilator. Using pulse-width modulation, green light intensity could be easily and continuously modulated from zero to a maximum value (as in Fig. 4), exploring a wide range of intermediate intensity levels and therefore of mean LacI production rates from the optogenetic promoter. We do not include additional experiments in the revised manuscript but we have greatly expanded the theoretical discussion on the low amplitude regime, both for a constant illumination (new Supplementary Materials Section 5) and the pulsed case (new Supplementary Fig. 8).

Recommendations for the Authors:

(1) The introduction emphasized the utility of entrainment as a means to achieve population-wide synchrony. It is worth mentioning also that it enables synchronization of the internal oscillator with an external zeitgeber, to achieve a specific phase-locking between them. Often, this is the main utility attributed to entrainment, e.g., in circadian clocks.

Following Reviewer’s suggestion we now say in the introduction:

These oscillations maintain a constant phase relation to the external light cue that can act as a zeitgeber.

(2) It is sometimes unclear at first glance which of the figure panels show simulation data and which show experimental data (e.g., Figure 5a,b; Figure 6a,b). More explicitly labeling the panels could help.

We thank the reviewer for pointing this out, we now explicitly label all the panels.

(3) Figure 3b - please add a color bar to indicate the meaning of the red-green scale, and enlarge the markers so their color is more visible. Also, can add additional controls of (i) sfGFP expression without the ccaR, and (ii) the autofluorescent signal from wild type. Please also provide the raw data (not the time derivatives) in a supplementary figure.

A colorbar has been added and markers enlarged.

(i) Unfortunately we do not have a control for GFP expression without ccaR.

(ii) autofluorescence signal from “a negative control consisting of DHL708 with plasmids pNO286-3 and pSR58-0 (optogenetic plasmids without sfGFP cassette)” has been added for comparison to Fig.3b. This modification was actually very helpful in understanding that the sensitivity threshold in our experiments is mainly determined by autofluorescence. OD600 and fluorescence raw data are now provided in Supplementary Fig. 6.

(4) Figure 3d - the claim in the text is that the purple optorepressilator and the wildtype repressilator have identical periods and amplitude. However, it seems from the figure that there is a small difference in the period length. This deviation is not problematic in any way, but I wondered whether it might actually be explained by the model, assuming that there is still a very weak leak from the new construct. In other words, would the model predict a bifurcation diagram in which an increasing x' concentration causes a gradual decrease in amplitude and increase in period, before the loss of rhythmicity? If so, Figure 3d can serve not only as a technical optimization demonstration but also as a nice validation of the model.

We thank the reviewer for raising this interesting point. We now report, in Supplementary Materials Section 5, a theoretical prediction of the period with respect to a constant concentration of x'. For our choice of parameters (adjusted to reproduce the main experimental quantitative features) we find a period that decreases with x'. Leakage would therefore lead to a shorter period, contrary to what is observed experimentally. To explain the longer period observed in the optorepressilator we went back to extract the average growth rates of bacteria in the purple optorepressilator and repressilator curves in Fig.3d. As we now discuss in the main text:

“The slight difference in period can be explained by the presence of additional plasmids in the optorepressilator strain, which results in a lower growth rate (Supplementary Figures 4 and 5). As found in the digital approximation, the repressilator period is mainly controlled by the inverse growth rate (see Figure 1a and Supplementary Figure 9) meaning a lower growth rate results in a longer oscillation period. When we normalize the time with the growth rate the two oscillations overlap nicely (Supplementary Figure 4).”

(5) Supplementary Figure 10 has no reference from the main text. it is unclear what's the difference from Figure 3. In general, many items in the supplementary materials are not referenced from the text. In addition, on many occasions, there is a reference to "supplementary information" without a specific address, which is not so useful to the reader. In any case possible, please be more specific. Also, note that there's inconsistency in referring to the supplemental section as "supplementary materials" vs "supplemental information".

We now explicitly reference all Supplementary Figures in the main text and use consistent reference to Supplementary Materials.

(6) The discussion at the bottom of p.7 ("Optogenetic entrainment") is missing a reference to the duration and intensity of the zeitgeber: In the example from human circadian rhythms it doesn't indicate light intensity; In the modeling of the PRC, both modalities are absent. it is important at least to indicate the parameters used for the simulation and experiments. It would be even better to explore in the model how these modalities affect the PRC and entrainment. And it would be incredible if the authors could show this also experimentally.

We now report the light intensity values for:

- our experiments:

“We first demonstrate this by monitoring the population signal from CFP (reporting TetR or 𝑦 in the model) in multiwell cultures under constant red illumination (9.82 W/m^2) interrupted by green light pulses (5.64 W/m^2) with a duration of 2 h and period 𝑇 = 18 h.”

For mother machine experiments “Green and red light stimuli were provided by the two LEDs (Thorlabs M530L4, Thorlabs M660L4) with respective intensities 6 W/m^2 and 26 W/m^2 for the synchronization experiments, and 1.1 W/m^2 and 4.5 W/m^2 for the entrainment experiments.”

- and simulations:

“In Fig. 5a we report the phase shift produced by a single pulse (with duration tau=2 h and intensity beta’=80 h-1 fixed for all the simulations) as a function of the pulse arrival phase ϕ.”

We also added an additional supplementary figure (Supplementary Fig. 7) that explores how the duration and intensity of the light pulses affect the PRC in the model. An approximate analytic result is also derived for the PRC in the digital approximation that compares very well with simulation, providing physical insight into PRC shape (Supplementary Materials Section 7).

(7) The experimental validation of the PRC can be much more thorough. Notably, an entrainment experiment with repeated pulses does not provide the same level of validation as a proper PRC experiment. This is because many differently shaped PRCs can give rise to the same entrainment pattern, as long as their fixed-point phases are the same.

Luckily, there might already be a decent amount of data from the mother machine experiments to fit with the PRC prediction, given the authors have pulsed a non-synchronized population that spans the entire x-axis of the PRC. It is possible that a proper PRC experiment wouldn't be too difficult with the plate reader either, given the throughput of the author's system.

This is a very interesting suggestion but unfortunately, in our mother machine data, the first pulse arrives before the cells have completed a full cycle, so although different cells receive the first pulse at a sufficiently randomized phase, we can’t extract their individual phases at the pulse arrival time.

Indeed it would be possible to design a plate reader experiment for the specific purpose of directly measuring the PRC. However, our current protocol involves continuous manual dilutions, which makes it rather laborious. We are currently working on an automated procedure that will allow us to systematically address this and other interesting suggestions in the future.

An indirect experimental validation of the PRC is however still possible using available data. See added red points in Fig.5a and reply to point 10 below.

(8) The discrepancy between the mother machine and plate reader experiments in Figure 5 is explained by a difference in growth rate variability in the two systems. It is not readily obvious how a difference in variability rather than the mean value of the period length can cause a shifted mean phase. It is only hinted in the text that growth rate has two different effects - on the period as well as the amplitude. I hypothesize that because of this period and amplitude correlation, there is a bias contribution to the sum of trajectories that have resulted in a shifted mean phase. Maybe there is another contribution from the asymmetric waveform of the signal? or from the distribution the alpha is sampled from? A direct discussion on that point will make the results much clearer. If the period-amplitude speculation above is right, please add also a panel that shows it. It will also be helpful to show the predicted PRC for the two parameter regimens.

We thank the reviewer for highlighting this point. In the previous version of the manuscript we omitted the fact that in order to better match experimental signals we chose slightly different values for T_L/T_0 for simulations in Fig. 5d and 5e. We now report the values of all simulation parameters in the revised manuscript. This difference could also contribute to the shift in the mean phase for the two cases. We added this information in the main text.

“The bottom panel in Fig. 5d shows the result of a numerical simulation with the same parameters as in Fig. 1b and the addition of a periodic light stimulation, with period $T_L/T_0 = 1$} [...] For the simulations in the lower panel of Fig.5e, all parameters remained the same as in Fig.5d with the exception of the period of the light pulses (T_L/T_0 = 0.97) and the standard deviation of the growth rate distribution, which was increased from 0.034 h^-1 to 0.071 h^-1 to better reproduce the experimental observations in the mother machine.”

Additionally, we added a supplementary figure (Supplementary Fig. 9) demonstrating the correlation between period and amplitude of the oscillations, for simulations with varying growth rate.

(9) The results from the detuning experiments are really nice, especially the decomposition in high frequency shown in Figure 6c. However, the experiments explore only the very high forcing amplitude conditions. Is there any way to test the weaker forcing regimens, as these are expected to uncover the interesting areas in between the Arnold's tongues? If this is experimentally difficult, it would be interesting to include at least the model prediction.

We thank the reviewer for stimulating us to go in this direction. We have performed simulations to explore model predictions for areas between the Arnold’s tongues. We find onset of entrainment as the amplitude increases and also the existence of intermediate plateaus at fractional frequency ratios. These results are now included in the Supplementary Fig. 8.

(10) Another prediction from the Arnold's tongue would be the relative phase of entrainment in different f/v0 conditions. The text refers to it very briefly, but this is a quantitative prediction that can be demonstrated clearly in a figure - how well do they match? It can be shown, for example, by a plot with f/v0 on the x-axis, the phase difference between the pulse and peak expression on the y-axis, a curve representing the model prediction for that function, and dots (with error bars) representing the calculated values from the experimental data.

Generally, when suitable, this kind of direct comparison is more useful to the reader than the way the authors chose to compare simulation and experiments throughout the manuscript.

We thank the reviewer for this very interesting suggestion. We have completely rewritten the discussion on entrainment commenting on how the same PRC (phase shift vs pulse arrival phase) can be interpreted as a T_L/T_0-1 vs phase difference plot. Indeed in the new Fig.5a we plot over the theoretical PRC curve, the values of the relative phase of entrainment for three values of the period of the light pulses (from the data in Fig. 6b). The agreement is remarkably good, providing a further experimental validation of the predicted PRC.

(11) The raw data can be valuable for the community for reanalysis and further hypothesis testing. Hence, it will be very useful to make all of the data (e.g., the fluorescence signal quantification tables from all the experiments) publicly available.

We prepared files with all raw data, to be made available to the community.

eLife assessment

This important study reports the cryo-electron microscopy structure of a multi-protein complex that recognizes the 5'-end cap of mRNAs and plays a critical role in mRNA export. The structural and biochemical analyses in this study provide convincing evidence to support the major claims of the authors, with the inclusion of more functional characterizations in cell-based systems having corroborated the claims further and and thus strengthening the study. This paper would be of interest to structural biologists and RNA biologists working on mRNA metabolism.

Reviewer #1 (Public Review):

Summary:

The authors use a combination of biochemistry and cryo-EM studies to explore a complex between the cap binding complex and an RNA binding protein, ALYREF, that coordinates mRNA processing and export.

Strengths:

The biochemistry and structural biology are supported by mutagenesis that tests the model in vitro. The structure provides new insight into how key events in RNA processing and export are likely to be coordinated.

Weaknesses:

The authors provide biochemical studies to confirm the interactions that they identify; however, they do not perform any studies to test these models in cells or explore the consequences for mRNA export from the nucleus. In fact, several of the amino acids that they identified in ALYREF that are critical for the interaction, as determined by their own biochemical studies are conserved in budding yeast Yra1 (residues E124/E128 are E/Q in budding yeast and residues Y135/V138/P139 are F/S/P), where the impact on poly(A) RNA export from the nucleus could be readily evaluated. The authors mention the potential for future studies in the manuscript, but they do not perform any analysis in this study that would explore the contributions of these new interactions.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Bradley and his colleagues represented the cryo-EM structure of the nuclear cap-binding complex (CBC) in complex with an mRNA export factor, ALYREF, providing a structural basis for understanding CBC regulating gene expression.

Strengths:

The authors successfully modeled the N-terminal region and the RRM domain of ALYREF (residues 1-183) within the CBC-ALYREF structure, which revealed that both the NCBP1 and NCBP2 subunits of the CBC interact with the RBM domain of ALYREF. Further mutagenesis and pull-down studies provided additional evidence to the observed CBC-ALYREF interface. Additionally, the authors engaged in a comprehensive discussion regarding other cellular complexes containing CBC and/or ALYREF components. They proposed potential models that elucidated coordinated events during mRNA maturation. This study provided structural evidence to show how CBC effectively recruits mRNA export factor machinery, enhancing our understanding of CBC regulating gene expression during mRNA transcription, splicing, and export.

Weaknesses:

Absence of functional data to support the proposed models in this study.

Reviewer #3 (Public Review):

Summary:

The authors carried out structural and biochemical studies to investigate the multiple functions of CBC and ALYREF in RNA metabolism.

Strengths:

For the structural study part, the authors successfully revealed how NCBP1 and NCBP2 subunits interact with mALYREF (residues 1-155). Their binding interface was then confirmed by biochemical assays (mutagenesis and pull-down assays) presented in this study.

Weaknesses:

The model derived from the cryo-EM structure will likely need to be validated in future functional studies.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Reviews):

Summary: 

The authors use a combination of biochemistry and cryo-EM studies to explore a complex between the cap-binding complex and an RNA binding protein, ALYREF, that coordinates mRNA processing and export.

Strengths: 

The biochemistry and structural biology are supported by mutagenesis which tests the model in vitro. The structure provides new insight into how key events in RNA processing and export are likely to be coordinated.

Weaknesses: 

The authors provide biochemical studies to confirm the interactions that they identify; however, they do not perform any studies to test these models in cells or explore the consequences of mRNA export from the nucleus. In fact, several of the amino acids that they identified in ALYREF that are critical for the interaction, as determined by their own biochemical studies, are conserved in budding yeast Yra1 (residues E124/E128 are E/Q in budding yeast and residues Y135/V138/P139 are F/S/P), where the impact on poly(A) RNA export from the nucleus could be readily evaluated. The authors could at least mention this point as part of the implications and the need for future studies. No one seems to have yet targeted any of these conserved residues, so this would be a logical extension of the current work.

We thank the reviewer for the feedback on our work. ALYREF coordinates pre-mRNA processing and export through interactions with a plethora of mRNA biogenesis factors including the DDX39B subunit of the TREX complex, CBC, EJC, and 3’ processing factors. ALYREF mediates the recruitment of the TREX complex on nascent transcripts which depends on its interactions with both CBC and EJC. Our work and studies by others indicate that ALYREF uses overlapping interfaces including both the N-terminal WxHD motif and the RRM domain to bind CBC and EJC. Thus, ALYREF mutants deficient in CBC interaction will also disrupt the ALYREF-EJC interaction and are not ideal for functional studies. In addition, the CBC plays important roles in multiple steps of mRNA metabolism through interactions with a plethora of factors, which often interact competitively with CBC. Identification of separation-of-function mutations on CBC or ALYREF that specifically disrupt their interaction but not other cellular complexes containing CBC or ALYREF would be an important future area to test the model in cells. 

We appreciate the reviewer’s insightful comments regarding yeast Yra1. Thus far, the physical and functional connection between Yra1 and CBC in yeast has not been demonstrated. There are major differences between yeast Yra1 and human ALYREF. Given the lack of an EJC in S. cerevisiae, it is unclear whether Yra1 acts in a similar manner as human ALYREF. In addition, Yra1 does not contain a WxHD motif in its N-terminal unstructured region, which is involved in CBC and EJC interactions in ALYREF. Characterization of the Yra1-CBC interaction will be an interesting future direction. We now include a discussion about yeast Yra1 in the newly added “Conclusion and perspectives” section. 

Specific suggestions:

The authors could put their work in context by speculating how some of the amino acids that they identify as being critical for the interactions they identify could contribute to cancer. For example, they mention mutations of interacting residues in NCBP2 are associated with human cancers, pointing out that NCBP2 R105C amino acid substitution has been reported in colorectal cancer and the NCBP2 I110M mutation has been found in head and neck cancer. Do the authors speculate that these changes would decrease the interaction between NCBP2 and ALYREF and, if so, how would this contribute to cancer? They also mention that a K330N mutation in NCBP1 in human uterine corpus endometrial carcinoma, where Y135 on the α2 helix of mALYREF2 makes a hydrogen bond with K330 of NCBP1. How do they speculate loss of this interaction would contribute to cancer?

In the revised manuscript, we include a discussion about these CBC mutants found in human cancers in the “Conclusion and perspectives” section. We think some of these CBC mutants, such as NCBP-1 K330N, could reduce interaction with ALYREF. Compromised CBC-ALYREF interaction will affect the recruitment of the TREX complex on nascent transcripts and cause dysregulation of mRNA export. In addition, that could also change the partition of CBC and ALYREF in different cellular complexes and cause perturbation of various steps in mRNA biogenesis that are regulated by CBC and ALYREF. Thus far, it is unclear whether and how loss of the CBC-ALYREF interaction directly contributes to cancer. Our work and that of others provide molecular insights to test in future studies. 

Reviewer #2 (Public Reviews):

Summary: 

In this manuscript, Bradley and his colleagues represented the cryo-EM structure of the nuclear cap-binding complex (CBC) in complex with an mRNA export factor, ALYREF, providing a structural basis for understanding CBC regulating gene expression.

Strengths: 

The authors successfully modeled the N-terminal region and the RRM domain of ALYREF (residues 1-183) within the CBC-ALYREF structure, which revealed that both the NCBP1 and NCBP2 subunits of the CBC interact with the RBM domain of ALYREF. Further mutagenesis and pull-down studies provided additional evidence to the observed CBC-ALYREF interface. Additionally, the authors engaged in a comprehensive discussion regarding other cellular complexes containing CBC and/or ALYREF components. They proposed potential models that elucidated coordinated events during mRNA maturation. This study provided good evidence to show how CBC effectively recruits mRNA export factor machinery, enhancing our understanding of CBC regulating gene expression during mRNA transcription, splicing, and export. 

Weaknesses: 

No in vivo or in vitro functional data to validate and support the structural observations and the proposed models in this study. Cryo-EM data processing and structural representation need to be strengthened. 

We appreciate the reviewer’s comments and suggestions. The fact that ALYREF uses highly overlapped binding interfaces for CBC and EJC interactions prevents us from a clear functional dissection of the ALYREF-CBC interaction using in vitro assays or in cells at the current stage. Please also see our response to Reviewer 1. 

In this revised manuscript, we have reprocessed the cryo-EM data using a different strategy which yields significantly improved maps. We have made improvements to the presentation of the structural work based on the reviewer’s specific comments. 

Reviewer #3 (Public Reviews):

Summary: 

The authors carried out structural and biochemical studies to investigate the multiple functions of CBC and ALYREF in RNA metabolism.

Strengths: 

For the structural study part, the authors successfully revealed how NCBP1 and NCBP2 subunits interact with mALYREF (residues 1-155). Their binding interface was then confirmed by biochemical assays (mutagenesis and pull-down assays) presented in this study. 

Weaknesses: 

The authors did not provide functional data to support their proposed models. The authors should include more details regarding the workflow of their cryo-EM data processing in the figure. 

We thank the reviewer for the comments. We completely agree that testing the proposed models in cells would be ideal. However, as we also respond to the other reviewers, functional studies are premature at the current stage because both ALYREF and CBC are components of many cellular complexes that regulate mRNA metabolism. Separation-of-function mutations on CBC or ALYREF first need to be identified in future studies for further investigation. Please also see our response to Reviewer 1. 

As suggested by the reviewer, we have included more details of the cryo-EM workflow in this revised manuscript. We have also included various validation measures including 3DFSC analyses, map vs model FSC curves, and representative density maps at various protein-protein binding interfaces. 

Recommendations for the Authors:

Reviewer #1 (Recommendations for the Authors):

Major points:

The authors should take advantage of Figure 1, which shows the domain structures of NCBP1, NCBP2, and ALYREF to indicate for the reader specifically which protein domains are included in the biochemical and structural analyses. In the current version of the manuscript, there is plenty of space to indicate below each domain structure precisely what regions are included.

In this revised manuscript, we have revised Figure 1A to indicate the protein constructs used in this work. 

Although it is fine to combine the Results and Discussion, the authors should really offer a concluding paragraph to highlight the novel results from this study and put the results in context.

We thank the reviewer for the recommendation. We now include a “Conclusion and perspectives” section in this revised manuscript.  

Minor comments:

Page 5, last sentence (and others) starts a sentence with the word "Since" when likely "As" which does not imply a time element to the phrase, is the correct word.

"Since the ALYREF/mALYREF2 interaction with the CBC is conserved and mALYREF2 exhibits better solubility, we focused on mALYREF2 in the cryo-EM investigations."

Would be more correct as: "As the ALYREF/mALYREF2 interaction with the CBC is conserved and mALYREF2 exhibits better solubility, we focused on mALYREF2 in the cryo-EM investigations."

We thank the reviewer for the comments. We have made the corrections. 

The word 'data' is plural so the sentence at the bottom of p.9 that includes the phrase "...in vivo data shows.." should read "..in vivo data show.." 

Corrected in the revised manuscript.

Reviewer #2 (Recommendations for the Authors):

Major points:

(1) The authors claimed the improved solubility of mouse ALYREF2 (mALYREF2, residues 1-155) compared to the previously employed ALYREF construct. However, human ALYREF has already been purified successfully for pull down assay, indicating soluble human ALYREF obtained, why not use human ALYREF directly? Please clarify. 

Pull-down studies were performed with GST-tagged ALYREF. For cryo-EM studies, untagged ALYREF is preferred to avoid potential issues that may arise from the expression tag. However, untagged ALYREF is less soluble than GST-tagged ALYREF and is not amenable for structural studies. We have revised the text to clarify this point. 

(2) The authors confirmed CBC-ALYREF interfaces through mutagenesis and pull-down assays in vitro. However, it would be more informative and interesting to include functional assays in vitro or/and in vivo with mutagenesis. 

We completely concur with the reviewer that testing the proposed models in vitro and in vivo would be important. However, as we pointed out in our response to public reviews, the highly overlapped binding interfaces on ALYREF for CBC and EJC interactions pose a great challenge for functional studies. Furthermore, both ALYREF and CBC are multifunctional factors and interact with a number of partners. Ideally, separation-of-function mutants that specifically disrupt the CBC-ALYREF interaction but not others need to be identified in future studies in order to perform functional studies. 

(3) About cryo-EM data processing and structural representation:

(1) In the description of the cryo-EM data processing, the authors claimed they did heterogeneous refinement, homogenous refinement, and then local refinement. This reviewer is puzzled by this process because the normal procedure should be non-uniform refinement following homogenous refinement. If the authors did not perform non-uniform refinement, they should do it because it would significantly improve the quality and resolution of cryo-EM maps. In addition, the right local refinement should include mask files and only show the density/map of the local region. 

We thank the reviewer for the suggestions. In response to the reviewer’s comment on the preferred orientation issue (point 5 below), we reprocessed the cryo-EM data and obtained significantly improved cryo-EM maps. In this revised manuscript, the CBC-mALYREF map was refined using homogeneous refinement; the CBC map was refined using homogenous refinement followed by non-uniform refinement. Refinement masks are included in Figure 2-figure supplement1. 

(2) Further local refinements with signal subtraction should be performed to improve the density and resolution of mALYREF2. 

We tested local refinement with or without signal subtraction using masks covering mALYREF2 and various regions of CBC. Unfortunately, this approach did not improve the density of mALYREF2. We suspect that the small size of mALYREF2 (77 residues for the RRM domain) and the intrinsic flexibility of CBC are the limiting factors in these attempts. 

(3) Figures with cryoEM map showing the side chains of the residues on the CBC-mALYREF2 interface should be included to strengthen the claims. Authors could add the map to Figure 3b/c or present it as a supplementary figure.

We include new supplementary figures (Figure 3-figure supplement 1) to show the electron densities corresponding to the views in Figure 3B and 3C. Residues labeled in Figure 3B and 3C are shown in sticks in these supplementary figures.

(4) For cryo-EM date processing, the authors have omitted lots of important details. Could the authors elaborate on the data processing with more details in the corresponding Figure and Methods Sections? Only one abi-initial model from the picked good particles was displayed in the figure. Are there any other different conformations of 3D classes for the dataset? In addition, too few classes have been considered in 3D classification, more classes may give a class with better density and resolution.

We thank the reviewer for the comments. We have reprocessed the cryo-EM data. A major change is to use Topaz for particle picking. We now include more details for data processing in Figure 2-figure supplement 1 and the method section. The cryo-EM sample is relatively uniform. Ab-initio reconstruction and heterogenous refinement yielded only one good class and the other classes are “junk” classes (omitted in the workflow figure). No major conformational changes were observed throughout the multiple rounds of heterogenous refinement for both CBC and CBCmALYREF2. In this revised manuscript, we have been able to obtain significantly improved maps through the new data processing strategy employing Topaz as illustrated in Figure 2-figure supplement 1 to 5.

(5) Angular distribution plots should be included to show if there is a preferred orientation issue. Based on the presented maps in validation reports, there may exist a preferred orientation issue for the reported two cryo-EM maps. Detailed 3D-Histogram and directional FSC plots for all the cryo-EM maps using 3DFSC web server should be presented to show the overall qualities (https://www.nature.com/articles/nmeth.4347 and https://3dfsc.salk.edu/).

We thank the reviewer for the recommendations. In response to the reviewer’s comment on the preferred orientation issue, we reprocessed the cryo-EM data. Topaz was used for particle picking instead of template picking. 3DFSC analyses indicate that the new CBC-mALREF2 map has a sphericity of 0.946, which is a significant improvement from the previous map which has a sphericity of 0.815. Consistently, the maps presented in this revised manuscript show significantly improved densities. We now include angular distribution and 3DFSC analyses of the EM maps (Figure 2-figure supplement 2 and 4). 

(6) Figures of model-to-map FSCs need to be present to demonstrate the quality of the models and the corresponding ones (model resolution when FSC=0.5) should also be included in Table 1. The accuracy of the model is important for structural explanations and description.

The model-to-map FSCs are now included in Figure 2-figure supplement 3A and 5A. The model resolutions of CBC-mALYREF2 and CBC are estimated to be 3.5 Å and 3.6 Å at an FSC of 0.5. These numbers are now included in Table 1. 

(7) In addition, figures of local density maps with different regions of the models, showing side chains, are necessary and important to justify the claimed resolutions. 

We now include density maps overlayed with residue side chains at various regions. For the CBCmALYREF2 map, density maps are shown at the mALYREF2-NCBP1 interfaces (Figure 3-figure supplement 1A and 1B), mALYREF2-NCBP2 interface (Figure 3-figure supplement 1C), NCBP1NCPB2 interface (Figure 2-figure supplement 5B), and the region near m7G (Figure 2-figure supplement 5C). For the CBC map, density maps are shown at the NCBP1-NCPB2 interface (Figure 2-figure supplement 3B) and the region near m7G (Figure 2-figure supplement 3C). 

Minor points:

(1) A figure superimposing the models from the CBC-mALYREF2 amp and mALYREF2 alone map is necessary to present that there are no other CBC binding-induced conformational changes in CBC except the claimed by the authors. In addition, a figure showing the density of m7GpppG should be included as well.  

Overlay of CBC and CBC-mALYREF2 models is now presented in Figure 2-figure supplement 3D. Comparing CBC and CBC-mALYREF2, NCBP1 and NCBP2 have a RMSD of 0.32 Å and 0.30 Å, respectively. The density maps near the M7G cap analog are shown in Figure 2-figure supplement 3C for CBC and Figure 2-figure supplement 5C for CBC-mALYREF2. 

(2) Authors obtained the two maps from one dataset, so "we first determined" and "we next determined" (page 6) should be replaced with something like "One class of 3D cryo-EM map revealed' and "Another class of 3D cryo-EM map defined". 

We have revised the text as suggested by the reviewer.  

(3) In 'Abstract', 'a mRNA export factor' should be 'an mRNA export factor'. 

Corrected in the revised manuscript.

(4) In 'Abstract', the final sentence 'Comparison of CBC- ALYREF to other CBC and ALYREF containing cellular complexes provides insights into the coordinated events during mRNA transcription, splicing, and export' doesn't read smoothly, I would suggest revising it to 'Comparing CBC-ALYREF with other cellular complexes containing CBC and/or ALYREF components provides insight into the coordinated events during mRNA transcription, splicing, and export.' 

We thank the reviewer for the recommendation and have revised accordingly. 

(5) In paragraph 'CBC-ALYREF and viral hijacking of host mRNA export pathway', line 6, the sentences preceding and following the term 'However' indicate a progressive or parallel relationship, rather than a transitional one. To enhance the coherence, I would suggest replacing 'However' with 'Furthermore' or 'In addition'. 

Corrected in the revised manuscript.

(6) In both Figure 5 and Figure 6, the depicted models are proposed and constructed exclusively through the comparison of the CBC-partial ALYREF with other cellular complexes containing components of CBC and/or ALYREF, which need to be confirmed by more studies. To prevent potential confusion and misunderstandings, it is recommended to replace the term 'model' with 'proposed model'. 

Corrected in the revised manuscript.

Reviewer #3 (Recommendations for the Authors):

Major points:

(1) In the Results and Discussion section, the authors mentioned "Recombinant human ALYREF protein was shown to interact with the CBC in RNase-treated nuclear extracts." However, they used mouse ALYREF for cryo-EM investigations. Can the authors include an explanation for this choice during the revision?  

In our work, we used a mixture of glutamic acid and arginine to increase the solubility of GSTALYREF. For cryo-EM studies, we use untagged ALYREF to avoid potential issues that may arise from the expression tag. However, untagged ALYREF is less soluble than GST-tagged ALYREF and is not suitable for structural studies in standard buffers. We have made further clarification on this point in this revised manuscript. 

(2) In the paragraph on "CBC-ALYREF interfaces", the authors stated "For example, E97 forms salt bridges with K330 and K381 of NCBP1. Y135 on the α2 helix of mALYREF2 makes a hydrogen bond with K330 of NCBP1. The importance of this interface between ALYREF and NCBP1 is highlighted by a K330N mutation found in human uterine corpus endometrial carcinoma." I fail to see a strong connection between their structural observations and previous findings regarding the role of a K330N mutation found in human uterine corpus endometrial carcinoma. The authors should add more words to thread these two parts.  

In response to the reviewer’s comment, we now move the discussion of these CBC mutants to the newly added “Conclusion and perspectives” section. 

(3) The authors should include side chains of the residues in their figure of Local resolution estimation and FSC curves, especially when they are presenting the binding interface between two components. 

We have now included density maps that are overlayed with structural models showing side chains of critical residues. These maps include the NCBP1-mALYREF2 interfaces (Figure 3-figure supplement 1A and 1B), NCBP2-mALYREF2 interface (Figure 3-figure supplement 1C), NCBP1NCBP2 interface (Figure 2-figure supplement 3B and 5B), and the m7G cap region (Figure 2figure supplement 3C and 5C). 

Minor points: 

(1) Some grammatical mistakes need to be corrected. For example, it is "an mRNA" instead of "a mRNA".  

Corrected in the revised manuscript.

(2) The authors can provide more information for the audience to know better about ALYREF when it first appears in the 5th line in the Abstract section. For example, "It promotes mRNA export through direct interaction with ALYREF, a key mRNA export factor, ...". 

We have revised the sentence based on the reviewer’s comment.

eLife assessment

The author demonstrates that deficiency or pharmacological inhibition of O-glcNac transferase (OGT) enhances tumor immunity in colorectal cancer models. This useful study unveils that OGT deficiency triggers a DNA damage response that can affect immune status in colorectal cancers. It provides convincing evidence showing that OGT-mediated processing of HSF1 is crucial in maintaining genomic integrity.

Reviewer #1 (Public Review):

Summary:

This study provides the detailed molecular mechanism of how OGT, an O-GlcNac transferase, promotes cancer progression. Using loss-of-function OGT models, the authors demonstrated that OGT cleaves HCF-1, an important guardian of genomic stability. The resulting genomic instability in OGT-knockout tumors leads to cytosolic DNA accumulation, the activation of cGAS-mediated type I IFN responses, and increased CD8+ T cell infiltration into the tumors. Moreover, treatment with OGT inhibitor synergized with anti-PDL1 immune-checkpoint blockade.

Strengths:

Novel findings of how OGT promotes tumor progression.

Reviewer #2 (Public Review):

Summary:

In this study, the author demonstrates that deficiency or pharmacological inhibition of O-glcNac transferase (OGT) enhances tumor immunity in colorectal cancer models. The authors propose that OGT deficiency triggers a DNA damage response, activating the cGAS-STING innate immunity pathway and promoting a Type I interferon response. They suggest that OGT-mediated processing of HSF1 is crucial in maintaining genomic integrity. This research is significant as it identifies OGT inhibition as a potential immunomodulatory target in cancer treatment.

Strengths:

The strength of the paper lies primarily in the in vivo data, demonstrating the impact of OGT deficiency or inhibition on modulating tumor growth and anti-tumor immunity. The experiments are well-controlled. However, there are several unresolved questions:

Weaknesses:

The mechanisms of how OGT deficiency can trigger DNA damage and the role of this response in promoting immunity are only partially addressed in the manuscript.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Recommendations For The Authors):

Some of the data is problematic and does not always support the authors' conclusions:

(1) Fig. 1K and H are identical.

Thank you for pointing out this problem in manuscript. We apologize for this unintentional mistake and have replaced Fig. 1K.

(2) The graph in Figure 2B contradicts the text. It is not obvious how the image was quantified to produce the histological score graph..

We thank the reviewer for pointing out this problem in manuscript, as the reviewer suggested, we have replaced the Figure 2B.

(3) In Figures 2C and D, there is no clear pattern of changes in pro-inflammatory or anti-inflammatory cytokines, despite the authors' claims in the text.

We appreciate the comment, we think the reason is that the level of cytokines in the tissue is low, so the pattern of changes is not obvious.

(4) It is unclear why the anti-dsDNA antibody does not stain the nucleus in Figure 4B. The staining with anti-dsDNA and DAPI does not match well. Figure 5H shows there is still lots of cytosolic DNA in OGT-/- HCF-1-C, measured by DAPI. These data do not support the authors' conclusion that HCFC600 eliminates cytosolic DNA accumulation (line 229). There is no support for the authors' claim that HCF-1 restrains the cGAS-STING pathway (line 330).

We thank these insightful comments, the most critical step in staining cytosolic DNA is to proceed to a low-permeabilization as to allow the antibody to cross the cellular membrane but not the nuclear membrane, that’s why the anti-dsDNA antibody does not stain the nucleus. In Figure 5H, we think we used a high concentrated DAPI to do the staining and nucleus DNA get stained, looks like it’s the cytosolic DNA. 

(5) In Figure 5B, there is no increase in HCF-1 cleavage after OGT over-expression.

We appreciate the reviewer for his/her comment, we think the reason is that we used the cell line to stably overexpress OGT-GFP and we may have missed the time point when the increase in HCF-1 cleavage occurred, so there is no big increase of it. However, there is a significant increase in Figure 5C.

(6) In Figure 7, the TNF-a staining does not inspire confidence.

We thank the reviewer for his/her comment, from both Figure 7K (MC38 tumor model) and Figure 7N (LLC tumor model), we observed a significant increase in TNF-α+ CD8+ T cells in the group treated with the combination of OSMI-1 and anti-PD-L1 compared to the control group, as evidenced by the clear clustering.

The writing needs significant improvement:

(1) There are multiple English grammar mistakes throughout the paper. It is recommended that the authors run the manuscript through an editing service.

We thank the reviewer for his/her suggestion. We apologize for the poor language of our manuscript. We worked on the manuscript for a long time and the repeated addition and removal of sentences and sections obviously led to poor readability. We have now worked on both language and readability and have also involved native English speakers for language corrections. We really hope that the flow and language level have been substantially improved.

(2) Some passages are misleading -- lines 161-162, line 217, lines 241-242, 263-264, 299-300. They need to be changed substantially.

We apologize for these mistakes, we have changed them.

(3) Figure legends should be rewritten. Currently, they are too abbreviated to be understood.

We apologize for that, we have rewritten them.

(4) Discussion should also be thoroughly reworked. Currently, it is merely restating the authors' findings. The authors should put their findings in the broader context of the field.

We apologize for that. For a better understanding of our study, we have reworked the discussion.

Reviewer #2 (Recommendations For The Authors):

(1) Previous studies (DOI: 10.1093/nar/gkw663, 10.1016/j.jgg.2015.07.002, 10.1016/j.dnarep.2022.103394) have suggested that OGT deficiency triggers DNA damage, connecting it to DNA repair and maintenance through various mechanisms. This should be acknowledged in the manuscript. Conversely, the role of HCF1 and its cleaved products in maintaining genomic integrity hasn't been previously shown. The authors investigate HCF1's role solely in the context of OGT inhibition. It is unclear whether this is also true under other stimuli that trigger DNA damage, whether fragments of HCF1 specifically reduce DNA damage, or if HSF1 is involved in the basal machinery that would be defective only in the absence of OGT.

We have acknowledged the manuscript mentioned above. In this paper we focused on the OGT function, which is related to HCF1. The role of HCF1 and its cleaved products in maintaining genomic integrity is an interesting topic, we may focus on it in next project.

(2) In villin-CRE-deficient mice, the authors observe generic inflammation in the intestine unrelated to tumor development. It's unclear if this also occurs in the presence of OGT inhibitors in mice, whether these inhibitors induce a systemic inflammatory (Type I interferon) response, or if certain tissues like the intestine or proliferating tumor cells are more susceptible to such a response.

We thank the comment, yes, investigating whether OGT inhibitors induce an inflammatory response, either systemically or tissue-specifically, is a very interesting project to focus on. However, in our current paper, we use a genetic method to identify the role of OGT deficiency in intestine inflammation-induced tumor development. This approach provides convincing evidence for our hypothesis. We may test the effect of OGT inhibitors on inflammation and tumor development in our next project.

(3) Another critical observation is the magnitude of the interferon response triggered by DNA damage in the OGT-deficient models. While it's known that DNA damage can activate cGAS-STING, the response's extent in the absence of OGT prompts the question of whether additional OGT-specific features could explain this phenomenon. For example, Lamin A, essential for nuclear envelope integrity and shown to be O-glycosylated (DOI: 10.3390/cells7050044), and other components of the nuclear envelope or its repair might be affected by OGT. The impact of OGT inhibition on nuclear envelope integrity compared to other DNA-damaging agents could be explored.

We appreciate the comment, in this project, we find an OGT binding protein, HCF1, though LC–MS/MS assay, it’s a top one candidate in binding profiles, so we focus on it. Like Lamin A and other components of the nuclear envelope still are good targets to check, we may explore these in our next project.

(4) The authors also demonstrate a correlation between OGT expression in tumors compared to healthy tissues. However, the reason is unclear, raising questions about whether this is a consequence of proliferation or metabolic deregulation in the cancer. The authors should address this aspect.

We appreciate the reviewer’s insightful point. It is very good questions and very interesting research. However, in this paper we focused on how OGT influence its downstream molecules to promote tumor, we didn’t check why OGT is increased in tumors, it is not the scope of this current work, we would love to investigate it in the future.

Minor points

Please add the legend to Figures S2, S3 and S5.

We thank the comment, we have added the legend to Figures S2, S3 and S5.

The sentence line 137 should be clarified as OGT deficiency seems more related to increased inflammation in this model.

We thank the comment, we have corrected the sentence line 137.

Line 732 has a ( typo before the number 34.

We thank the comment, we have corrected the sentence line 732.

eLife assessment

In this important study, the authors manually assessed randomly selected images published in eLife between 2012 and 2022 to determine whether they were accessible for readers with deuteranopia, the most common form of color vision deficiency. They then developed an automated tool designed to classify figures and images as either "friendly" or "unfriendly" for people with deuteranopia. Such a tool could be used by journals or researchers to monitor the accessibility of figures and images, and the evidence for its utility was solid: it performed well for eLife articles, but performance was weaker for a broader dataset of PubMed articles, which were not included in the training data. The authors also provide code that readers can download and run to test their own images, and this may be of most use for testing the tool, as there are already several free, user-friendly recoloring programs that allow users to see how images would look to a person with different forms of color vision deficiency. Automated classifications are of most use for assessing many images, when the user does not have the time or resources to assess each image individually.

Reviewer #1 (Public Review):

The authors of this study developed a software application, which aims to identify images as either "friendly" or "unfriendly" for readers with deuteranopia, the most common color-vision deficiency. Using previously published algorithms that recolor images to approximate how they would appear to a deuteranope (someone with deuteranopia), authors first manually assessed a set of images from biology-oriented research articles published in eLife between 2012 and 2022, as well as an additional hold-out set of 2000 articles selected randomly from the PubMed Central Open Access Subset. The researchers identified 636 out of 4964 images as difficult to interpret ("unfriendly") for deuteranopes in the eLife dataset. In the PubMed Central dataset 104 out of 1191 non-grayscale images were identified as unfriendly. The results for the eLife dataset show a decrease in "unfriendly" images over time and a higher probability for articles from cell-oriented research fields to contain "unfriendly" images.

The researchers used the manually classified images from eLife to develop, train, and validate an automated screening tool. They also created a user-friendly web application of the tool, where users can upload images and be informed about the status of each image as "friendly" or "unfriendly" for deuteranopes.

Strengths:

The authors have identified an important accessibility issue in the scientific literature: the use of color combinations that make figures difficult to interpret for people with color-vision deficiency. The metrics proposed and evaluated in the study are a valuable theoretical contribution. The automated screening tool they provide is well-documented, open source, and relatively easy to install and use. It has the potential to provide a useful service to the scientists who want to make their figures more accessible. The data are open and freely accessible, well documented, and a valuable resource for further research. The manuscript is well-written, logically structured, and easy to follow.

Weaknesses:

(1) The authors themselves acknowledge the limitations that arise from the way they defined what constitutes an "unfriendly" image. There is a missed chance here to have engaged deuteranopes as stakeholders earlier in the experimental design. This would have allowed to determine to what extent spatial separation and labelling of problematic color combinations responds to their needs and whether setting the bar at a simulated severity of 80% is inclusive enough. A slightly lowered barrier is still a barrier to accessibility.

(2) The use of training images from a single journal limits the generalizability of the empirical findings as well as of the automated screening tool itself. This is evidenced by a decrease in performance of the tool on the holdout dataset from PubMed Central. Machine-learning algorithms are highly configurable but also notorious for their lack of transparency and for being easily biased by the training data set. A quick and unsystematic test of the web application shows that the classifier works well for electron microscopy images but fails at recognizing the classical diagnostic images for color-vision deficiency (Ishihara test images) as "unfriendly". A future iteration of the tool should be trained on a wider variety of images, ideally enriched with diagnostic images found in scientific publications.

Reviewer #2 (Public Review):

Summary:

An analysis of images in the biology literature that are problematic for people with a color-vision deficiency (CVD) is presented, along with a machine learning-based model trained on an eLife dataset to identify such images and a web application that uses the model to flag problematic images. Their analysis reveals that about 13% of the images could be problematic for people with CVD and that the frequency of such images decreased over time. Their best model (convolutional neural network, CNN) yields 0.89 AUROC score and 0.77 AUPRC on held-out eLife articles, but lower scores (0.78 and 0.39, respectively). It is proposed that their approach could help making biology literature accessible to diverse audiences.

Strengths:

The manuscript focuses on an important yet mostly overlooked problem and makes contributions both in expanding our understanding of the extent of the problem and in developing solutions to mitigate the problem. The paper is generally well-written and clearly organized. Their CVD simulation combines five different metrics. The dataset has been assessed by two researchers and is likely to be of high-quality. Machine learning algorithm used (CNN) is an appropriate choice for the problem. The evaluation of various hyperparameters for the CNN model is extensive.

Weaknesses:

While the study has significant strengths, it also has some limitations. Specifically, the focus on one type of CVD (deuteranopia) and selecting images from a single journal (eLife) for training limit the generalizability of the models. This is, to some extent, shown by applying the model to PMC articles, which yields lower performance. "Probably problematic" and "probably okay" classes are excluded from the analysis.

Reviewer #3 (Public Review):

Summary:

This work focuses on accessibility of scientific images for individuals with color vision deficiencies, particularly deuteranopia. The research involved an analysis of images from eLife and PubMed Central published in 2012-2022. The authors manually reviewed nearly 7,000 images, comparing them with simulated versions representing the perspective of individuals with deuteranopia, and also evaluated several methods to automatically detect such images including training a machine-learning algorithm to do so, which performed the best. The authors found that nearly 13% of the images could be challenging for people with deuteranopia to interpret. There was a trend toward a decrease in problematic images over time, which is encouraging.

After the first round of review, the addition of a random sample of biomedical articles in the evaluation set strengthens the generalizability of the algorithm, and the change to evaluate articles at the article level to address pseudoreplication is appropriate.

Author response:

The following is the authors’ response to the original reviews.

eLife assessment

In this important study, the authors manually assessed randomly selected images published in eLife between 2012 and 2020 to determine whether they were accessible for readers with deuteranopia, the most common form of color vision deficiency. They then developed an automated tool designed to classify figures and images as either "friendly" or "unfriendly" for people with deuteranopia. While such a tool could be used by publishers, editors or researchers to monitor accessibility in the research literature, the evidence supporting the tools' utility was incomplete. The tool would benefit from training on an expanded dataset that includes different image and figure types from many journals, and using more rigorous approaches when training the tool and assessing performance. The authors also provide code that readers can download and run to test their own images. This may be of most use for testing the tool, as there are already several free, user-friendly recoloring programs that allow users to see how images would look to a person with different forms of color vision deficiency. Automated classifications are of most use for assessing many images, when the user does not have the time or resources to assess each image individually.

Thank you for this assessment. We have responded to the comments and suggestions in detail below. One minor correction to the above statement: the randomly selected images published in eLife were from articles published between 2012 and 2022 (not 2020).

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors of this study developed a software application, which aims to identify images as either "friendly" or "unfriendly" for readers with deuteranopia, the most common color-vision deficiency. Using previously published algorithms that recolor images to approximate how they would appear to a deuteranope (someone with deuteranopia), authors first manually assessed a set of images from biology-oriented research articles published in eLife between 2012 and 2022. The researchers identified 636 out of 4964 images as difficult to interpret ("unfriendly") for deuteranopes. They claim that there was a decrease in "unfriendly" images over time and that articles from cell-oriented research fields were most likely to contain "unfriendly" images. The researchers used the manually classified images to develop, train, and validate an automated screening tool. They also created a user-friendly web application of the tool, where users can upload images and be informed about the status of each image as "friendly" or "unfriendly" for deuteranopes.

Strengths:

The authors have identified an important accessibility issue in the scientific literature: the use of color combinations that make figures difficult to interpret for people with color-vision deficiency. The metrics proposed and evaluated in the study are a valuable theoretical contribution. The automated screening tool they provide is well-documented, open source, and relatively easy to install and use. It has the potential to provide a useful service to the scientists who want to make their figures more accessible. The data are open and freely accessible, well documented, and a valuable resource for further research. The manuscript is well written, logically structured, and easy to follow.

We thank the reviewer for these comments.

Weaknesses:

(1) The authors themselves acknowledge the limitations that arise from the way they defined what constitutes an "unfriendly" image. There is a missed chance here to have engaged deuteranopes as stakeholders earlier in the experimental design. This would have allowed [them] to determine to what extent spatial separation and labelling of problematic color combinations responds to their needs and whether setting the bar at a simulated severity of 80% is inclusive enough. A slightly lowered barrier is still a barrier to accessibility.

We agree with this point in principle. However, different people experience deuteranopia in different ways, so it would require a large effort to characterize these differences and provide empirical evidence about many individuals' interpretations of problematic images in the "real world." In this study, we aimed to establish a starting point that would emphasize the need for greater accessibility, and we have provided tools to begin accomplishing that. We erred on the side of simulating relatively high severity (but not complete deuteranopia). Thus, our findings and tools should be relevant to some (but not all) people with deuteranopia. Furthermore, as noted in the paper, an advantage of our approach is that "by using simulations, the reviewers were capable of seeing two versions of each image: the original and a simulated version." We believe this step is important in assessing the extent to which deuteranopia could confound image interpretations. Conceivably, this could be done with deuteranopes after recoloration, but it is difficult to know whether deuteranopes would see the recolored images in the same way that non-deuteranopes see the original images. It is also true that images simulating deuteranopia may not perfectly reflect how deuteranopes see those images. It is a tradeoff either way. We have added comments along these lines to the paper.

(2) The use of images from a single journal strongly limits the generalizability of the empirical findings as well as of the automated screening tool itself. Machine-learning algorithms are highly configurable but also notorious for their lack of transparency and for being easily biased by the training data set. A quick and unsystematic test of the web application shows that the classifier works well for electron microscopy images but fails at recognizing red-green scatter plots and even the classical diagnostic images for color-vision deficiency (Ishihara test images) as "unfriendly". A future iteration of the tool should be trained on a wider variety of images from different journals.

Thank you for these comments. We have reviewed an additional 2,000 images, which were randomly selected from PubMed Central. We used our original model to make predictions for those images. The corresponding results are now included in the paper.

We agree that many of the images identified as being "unfriendly" are microscope images, which often use red and green dyes. However, many other image types were identified as unfriendly, including heat maps, line charts, maps, three-dimensional structural representations of proteins, photographs, network diagrams, etc. We have uploaded these figures to our Open Science Framework repository so it's easier for readers to review these examples. We have added a comment along these lines to the paper.

The reviewer mentioned uploading red/green scatter plots and Ishihara test images to our Web application and that it reported they were friendly. Firstly, it depends on the scatter plot. Even though some such plots include green and red, the image's scientific meaning may be clear. Secondly, although the Ishihara images were created as informal tests for humans, these images (and ones similar to them) are not in eLife journal articles (to our knowledge) and thus are not included in our training set. Thus, it is unsurprising that our machine-learning models would not classify such images correctly as unfriendly.

(3) Focusing the statistical analyses on individual images rather than articles (e.g. in figures 1 and 2) leads to pseudoreplication. Multiple images from the same article should not be treated as statistically independent measures, because they are produced by the same authors. A simple alternative is to instead use articles as the unit of analysis and score an article as "unfriendly" when it contains at least one "unfriendly" image. In addition, collapsing the counts of "unfriendly" images to proportions loses important information about the sample size. For example, the current analysis presented in Fig. 1 gives undue weight to the three images from 2012, two of which came from the same article. If we perform a logistic regression on articles coded as "friendly" and "unfriendly" (rather than the reported linear regression on the proportion of "unfriendly" images), there is still evidence for a decrease in the frequency of "unfriendly" eLife articles over time.

Thank you for taking the time to provide these careful insights. We have adjusted these statistical analyses to focus on articles rather than individual images. For Figure 1, we treat an article as "Definitely problematic" if any image in the article was categorized as "Definitely problematic." Additionally, we no longer collapse the counts to proportions, and we use logistic regression to summarize the trend over time. The overall conclusions remain the same.

Another issue concerns the large number of articles (>40%) that are classified as belonging to two subdisciplines, which further compounds the image pseudoreplication. Two alternatives are to either group articles with two subdisciplines into a "multidisciplinary" group or recode them to include both disciplines in the category name.

Thank you for this insight. We have modified Figure 2 so that it puts all articles that have been assigned two subdisciplines into a "Multidisciplinary" category. The overall conclusions remain the same.

(4) The low frequency of "unfriendly" images in the data (under 15%) calls for a different performance measure than the AUROC used by the authors. In such imbalanced classification cases the recommended performance measure is precision-recall area under the curve (PR AUC: https://doi.org/10.1371%2Fjournal.pone.0118432) that gives more weight to the classification of the rare class ("unfriendly" images).

We now calculate the area under the precision-recall curve and provide these numbers (and figures) alongside the AUROC values (and figures). We agree that these numbers are informative; both metrics lead to the same overall conclusions.

Reviewer #2 (Public Review):

Summary:

An analysis of images in the biology literature that are problematic for people with a color-vision deficiency (CVD) is presented, along with a machine learning-based model to identify such images and a web application that uses the model to flag problematic images. Their analysis reveals that about 13% of the images could be problematic for people with CVD and that the frequency of such images decreased over time. Their model yields 0.89 AUC score. It is proposed that their approach could help making biology literature accessible to diverse audiences.

Strengths:

The manuscript focuses on an important yet mostly overlooked problem, and makes contributions both in expanding our understanding of the extent of the problem and in developing solutions to mitigate the problem. The paper is generally well-written and clearly organized. Their CVD simulation combines five different metrics. The dataset has been assessed by two researchers and is likely to be of high-quality. Machine learning algorithm used (convolutional neural network, CNN) is an appropriate choice for the problem. The evaluation of various hyperparameters for the CNN model is extensive.

We thank the reviewer for these comments.

Weaknesses:

The focus seems to be on one type of CVD (deuteranopia) and it is unclear whether this would generalize to other types.

We agree that it would be interesting to perform similar analyses for protanopia and other color-vision deficiencies. But we leave that work for future studies.

The dataset consists of images from eLife articles. While this is a reasonable starting point, whether this can generalize to other biology/biomedical articles is not assessed.

This is an important point. We have reviewed an additional 2,000 images, which were randomly selected from PubMed Central, and used our original model to make predictions for those images. The corresponding results are now included in the paper.

"Probably problematic" and "probably okay" classes are excluded from the analysis and classification, and the effect of this exclusion is not discussed.

We now address this in the Discussion section.

Machine learning aspects can be explained better, in a more standard way.

Thank you. We address this comment in our responses to your comments below.

The evaluation metrics used for validating the machine learning models seem lacking (e.g., precision, recall, F1 are not reported).

We now provide these metrics (in a supplementary file).

The web application is not discussed in any depth.

The paper includes a paragraph about how the Web application works and which technologies we used to create it. We are unsure which additional aspects should be addressed.

Reviewer #3 (Public Review):

Summary:

This work focuses on accessibility of scientific images for individuals with color vision deficiencies, particularly deuteranopia. The research involved an analysis of images from eLife published in 2012-2022. The authors manually reviewed nearly 5,000 images, comparing them with simulated versions representing the perspective of individuals with deuteranopia, and also evaluated several methods to automatically detect such images including training a machine-learning algorithm to do so, which performed the best. The authors found that nearly 13% of the images could be challenging for people with deuteranopia to interpret. There was a trend toward a decrease in problematic images over time, which is encouraging.

Strengths:

The manuscript is well organized and written. It addresses inclusivity and accessibility in scientific communication, and reinforces that there is a problem and that in part technological solutions have potential to assist with this problem.

The number of manually assessed images for evaluation and training an algorithm is, to my knowledge, much larger than any existing survey. This is a valuable open source dataset beyond the work herein.

The sequential steps used to classify articles follow best practices for evaluation and training sets.

We thank the reviewer for these comments.

Weaknesses:

I do not see any major issues with the methods. The authors were transparent with the limitations (the need to rely on simulations instead of what deuteranopes see), only capturing a subset of issues related to color vision deficiency, and the focus on one journal that may not be representative of images in other journals and disciplines.

We thank the reviewer for these comments. Regarding the last point, we have reviewed an additional 2,000 images, which were randomly selected from PubMed Central, and used our original model to make predictions for those images. The corresponding results are now included in the paper.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

N/A

Thank you.

Reviewer #2 (Recommendations For The Authors):

- The web application link can be provided in the Abstract for more visibility.

We have added the URL to the Abstract.

- They focus on deuteranopia in this paper. It seems that protanopia is not considered. Why? What are the challenges in considered this type of CVD?

We agree that it would be interesting to perform similar analyses for protanopia and other color-vision deficiencies. But we leave that work for future studies. Deuteranopia is the most common color-vision deficiency, so we focused on the needs of these individuals as a starting point.

- The dataset is limited to eLife articles. More discussion of this limitation is needed. Couldn't one also include some papers from PMC open access dataset for comparison?

We have reviewed an additional 2,000 images, which we randomly selected from PubMed Central, and used our original model to make predictions for those images. The corresponding results are now included in the paper.

- An analysis of the effect of selecting a severity value of 0.8 can be included.

We agree that this would be interesting, but we leave it for future work.

- "Probably problematic" and "probably okay" classes are excluded from analysis, which may oversimplify the findings and bias the models. It would have been interesting to study these classes as well.

We agree that this would be interesting, but we leave it for future work. However, we have added a comment to the Discussion on this point.

- Some machine learning aspects are discussed in a non-standard way. Class weighting or transfer learning would not typically be considered hyperparameters."corpus" is not a model. Description of how fine-tuning was performed could be clearer.

We have updated this wording to use more appropriate terminology to describe these different "configurations." Additionally, we expanded and clarified our description of fine tuning.

- Reporting performance on the training set is not very meaningful. Although I understand this is cross-validated, it is unclear what is gained by reporting two results. Maybe there should be more discussion of the difference.

We used cross validation to compare different machine-learning models and configurations. Providing performance metrics helps to illustrate how we arrived at the final configurations that we used. We have updated the manuscript to clarify this point.

- True positives, false positives, etc. are described as evaluation metrics. Typically, one would think of these as numbers that are used to calculate evaluation metrics, like precision (PPV), recall (sensitivity), etc. Furthermore, they say they measure precision, recall, precision-recall curves, but I don't see these reported in the manuscript. They should be (especially precision, recall, F1).

We have clarified this wording in the manuscript.

- There are many figures in the supplementary material, but not much interpretation/insights provided. What should we learn from these figures?

We have revised the captions and now provide more explanations about these figures in the manuscript.

- CVD simulations are mentioned (line 312). It is unclear whether these methods could be used for this work and if so, why they were not used. How do the simulations in this work compare to other simulations?

This part of the manuscript refers to recolorization techniques, which attempt to make images more friendly to people with color vision deficiencies. For our paper, we used a form of recolorization that simulates how a deuteranope would see a figure in its original form. Therefore, unless we misunderstand the reviewer's question, these two types of simulation have distinct purposes and thus are not comparable.

- relu -> ReLU

We have corrected this.

Reviewer #3 (Recommendations For The Authors):

The title can be more specific to denote that the survey was done in eLife papers in the years 2012-2022. Similarly, this should be clear in the abstract instead of only "images published in biology-oriented research articles".

Thank you for this suggestion. Because we have expanded this work to include images from PubMed Central papers, we believe the title is acceptable as it stands. We updated the abstract to say, "images published in biology- and medicine-oriented research articles"

Two mentions of existing work that I did not see are to Jambor and colleagues' assessment on color accessibility in several fields: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8041175/, and whether this work overlaps with the 'JetFighter' tool

(https://elifesciences.org/labs/c2292989/jetfighter-towards-figure-accuracy-and-accessibility).

Thank you for bringing these to our attention. We have added a citation to Jambor, et al.

We also mention JetFighter and describe its uses.

Similarly, on Line 301: Significant prior work has been done to address and improve accessibility for individuals with CVD. This work can be generally categorized into three types of studies: simulation methods, recolorization methods, and estimating the frequency of accessible images.

- One might mention education as prior work as well, which might in part be contributing to a decrease in problematic images (e.g., https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8041175/)

We now suggest that there are four categories and include education as one of these.

Line 361, when discussing resources to make figures suitable, the authors may consider citing this paper about an R package for single-cell data: https://elifesciences.org/articles/82128

Thank you. We now cite this paper.

The web application is a good demonstration of how this can be applied, and all code is open so others can apply the CNN in their own uses cases. Still, by itself, it is tedious to upload individual image files to screen them. Future work can implement this into a workflow more typical to researchers, but I understand that this will take additional resources beyond the scope of this project. The demonstration that these algorithms can be run with minimal resources in the browser with tensorflow.js is novel.

Thank you.

General:

It is encouraging that 'definitely problematic' images have been decreasing over time in eLife. Might this have to do with eLife policies? I could not quickly find if eLife has checks in place for this, but given that JetFighter was developed in association with eLife, I wonder if there is an enhanced awareness of this issue here vs. other journals.

This is possible. We are not aware of a way to test this formally.

eLife assessment

This study presents a valuable strategy to co-deliver peptides and adjuvants to antigen-presenting cells by engineering the Virus-like particle (VLP). The evidence supporting the claims of the authors is convincing, but the antitumour efficacy is unimpressive and would benefit from more antitumor experiments. The work will be of broad interest to bioengineers and medical biologists focusing on cancer vaccines.

Reviewer #1 (Public Review):

Summary:

The authors fabricated a novel cancer vaccine using endogenous virus-like particles with tumor neoantigen. The vaccine ePAC was proven to elicit strong immune stimulation with an increased killing effect against tumor cells in 2 mouse models.

Strengths:

The author achieved high protein loading and transfection efficiency using PEG10 self-assembly while packaging tumor neoantigens inside for cancer immunotherapy. The author also enhanced the targeting effect towards dendritic cells by surface modification using CpG-ODN.

Weaknesses:

There were some minor issues but they have been resolved in the revision process. It would be great if the authors could compare this with commercially available treatments and other vaccines.

Discussion:

Since the ePAC vaccine particle functions as a delivery platform, it can be tailored to different tumors when packed with their specific tumor neoantigens. Thus, the ePAC platform can be potentially employed in a broad range of cancer vaccine therapies. It would be exciting to see this platform being developed for other major cancer types.

Reviewer #2 (Public Review):

Summary:

The authors provided a novel antigen delivery system which showed remarkable efficacy in transporting antigens to develop cancer therapeutic vaccine.

Strengths:

This manuscript was innovative, meaningful, and had a rich amount of data.

Comments on the revised version:

All my concerns have been addressed by the authors

Reviewer #3 (Public Review):

Summary:

The authors harnessed the potential of mammalian endogenous virus-like protein to encapsulate virus-like particles (VLPs), enabling the precise delivery of tumor neoantigens. Through meticulous optimization of the VLP component ratios, they achieved remarkable stability and efficiency in delivering these crucial payloads. Moreover, the incorporation of CpG-ODN further heightened the targeted delivery efficiency and immunogenicity of the VLPs, solidifying their role as a potent tumor vaccine. In a diverse array of tumor mouse models, this novel tumor vaccine, termed ePAC, exhibited profound efficacy in activating the murine immune system. This activation manifested through the stimulation of dendritic cells in lymph nodes, the generation of effector memory T cells within the spleen, and the infiltration of neoantigen-specific T cells into tumors, resulting in robust anti-tumor responses.

Strengths:

This study delivered tumor neoantigens using VLPs, pioneering a new method for neoantigen delivery. Additionally, the gag protein of VLP is derived from mammalian endogenous virus-like protein, which offer greater safety compared to virus-derived gag proteins, thereby presenting a strong potential for clinical translation. The study also utilized a humanized mouse model to further validate the vaccine's efficacy and safety. Therefore, the anti-tumor vaccine designed in this study possesses both innovation and practicality.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Tang et al present an important manuscript focused on endogenous virus-like particles (eVLP) for cancer vaccination with solid in vivo studies. The author designed eVLP with high protein loading and transfection efficiency by PEG10 self-assembling while packaging neoantigens inside for cancer immunotherapy. The eVLP was further modified with CpG-ODN for enhanced dendritic cell targeting. The final vaccine ePAC was proven to elicit strong immune stimulation with increased killing effect against tumor cells in 2 mouse models. Below are my specific comments:

Thanks very much to comment our work as “important”. We sincerely appreciate the extremely helpful comments from the reviewer to significantly improve the quality of our manuscript.

(1) The figures were well prepared with minor flaws, such as missed scale bars in Figures 4B, 4K, 5B, and 5C. The author should also add labels representing statistical analysis for Figures 3C, 3D, and 3E. In Figure 6G, the authors should label which cell type is the data for.

Thanks very much for the very suggestive comments. The scale bars and statistical analysis have been added in Figures 4B, 4K, 5B, 5C, 3C, 3D, and 3E. For Figure 6G, we have added “CD44+ CD62L- in CD8+ T cells” to explain the cell type.

(2) In Figure 3H, the antigen-presenting cells (APCs) increased significantly, but there was also a non-negligible 10% of APCs found in the control group, indicating some potential unwanted immune response; the authors need to explain this phenomenon or add a cytotoxic test on the normal liver or other cell lines for confirmation.

Thanks very much for this extremely helpful suggestion. The antigen-presenting cells (APCs) in Figure 3H were isolated from mouse bone marrow and then cultured in vitro for about 5 days with cytokine stimulation (IL-4 and GM-CSF). Due to the stimulation effects of IL-4 and GM-CSF, a small proportion of the APCs (~10%) was tending to mature (co-expressing CD80 and CD86) in the control group, as pointing out by the reviewer. Similarly, in Figure 3I, these 10% activated APCs can activate T cells in vitro and exhibit certain cytotoxicity. Since APCs must be induced and cultured in vitro before using in this experiment, the background cytotoxicity induced by cytokines is unavoidable, and this has been well documented in literatures.

(3) In Figure 3I, the ePAC seems to have a very similar effect on cytotoxic T-cell tumor killing compared to the peptides + CpG group. If the concentrations were also the same, based on that, questions will arise as to what is the benefit of using the compact vector other than just free peptide and CpG? Please explain and elaborate.

Thanks very much for the comment. In vitro experiments indeed demonstrated that peptides + CpG had the same T cell activating ability as ePAC, as pointing out by the reviewer. However, due to the instability of peptides and the lack of targeting, the efficiency of activating the immune system for peptides + CpG after subcutaneous injection is significantly lower than that for ePAC in vivo, as shown in Figure 3D and Figure 2A. Then, as expected, the antitumor efficacy induced by peptides alone + CpG is significantly lower than that induced by ePAC in Figure 5. We have provided a detailed description in “Results” section of “Antitumor effect of ePAC in subcutaneous HCC model” as follows: Furthermore, ePAC with the ability to target DCs and increased stability by encapsulating peptides, exhibited significantly higher tumor growth inhibition efficiency (p=0.0002) comparing with the eVLP + CpG-ODN treated group similar to the simple mixture of neoantigen peptides and adjuvant (Figures 5B and 5C). Meanwhile, the Kaplan-Meier analysis of tumor progression free survival (PFS) also clearly demonstrated the therapeutic advantages of our ePAC (p=0.0194, Figure 5B).

(4) In the animal experiment in Figures 4F to L, the activation effect of APCs was similar between ePAC and CpG-only groups with no significance, but when it comes to the HCC mouse model in Figure 5, the anti-tumor effect was significantly increased between ePAC and CpG-only group. The authors should explain the difference between these two results.

Thanks very much for the comment. Since PEG10 protein does not have an adjuvant effect, the adjuvant effect of ePAC mainly comes from the modified CpG. Therefore, although ePAC can effectively deliver tumor neoantigens, it does not have a significant advantage over free CpG in activating APCs. However, CpG only possesses the adjuvant effect and does not carry neoantigens. While it can promote the maturation of APCs, it cannot generate neoantigen-specific T cells. Consequently, the antitumor effect of CpG-only is much lower than that of ePAC in Figure 5.

Reviewer #2 (Public Review):

Summary:

The authors provided a novel antigen delivery system that showed remarkable efficacy in transporting antigens to develop cancer therapeutic vaccines.

Strengths:

This manuscript was innovative, meaningful, and had a rich amount of data.

Weaknesses:

There are still some issues that need to be addressed and clarified.

Thanks very much to comment our work as “innovative”. We sincerely appreciate the extremely helpful comments from the reviewer to significantly improve the quality of our manuscript, and the listed weaknesses have been all carefully addressed.

(1) The format of images and data should be unified. Specifically, as follows: a. The presentation of flow cytometry results; b, The color schemes for different groups of column diagrams.

Thanks very much. Following the reviewer’s comment, we have unified the format of all images and data as suggested.

(2) The P-value should be provided in Figures, including Figure 1F, 1H, 3C, 3D, and 3E.

Thanks very much. We have provided the corresponding P-values in Figure 1F, 1H, 3C, 3D, and 3E.

(3) The quality of Figure 1C was too low to support the conclusion. The author should provide higher-quality images with no obvious background fluorescent signal. Meanwhile, the fluorescent image results of "Egfp+VSVg" group were inconsistent with the flow cytometry data. Additionally, the reviewer recommends that the authors use a confocal microscope to repeat this experiment to obtain a more convincing result.

Thanks very much for this comment. Following the reviewer’s suggestion, we uniformly adjusted the original images in Figure 1C to reduce background interference and increase its quality. After eliminating background interference, the fluorescence image of the "Egfp+VSVg" group was consistent with the flow cytometry result.

(4) The survival situation of the mouse should be provided in Figure 5, Figure 6, and Figure 7 to support the superior tumor therapy effect of ePAC.

Thanks very much for the extremely helpful comment. Following the reviewer’s suggestion, we have added the progression free survival (PFS) of mice in Figure 5 and described this result in the “Results” section of “Antitumor effect of ePAC in subcutaneous HCC model” as follows: Meanwhile, the Kaplan-Meier analysis of tumor progression free survival (PFS) also clearly demonstrated the therapeutic advantages of our ePAC (p=0.0194, Figure 5B). For Figure 6 and Figure 7, to promptly detect the immune changes in the tumor microenvironment after vaccination, we were unable to conduct long-term observations on tumor-bearing mice, and therefore, we did not provide the survival curve. However, we monitored the tumor volume changes in real-time, which also can serve as an important measure for evaluating antitumor efficacy.

(5) To demonstrate that ePAC could trigger a strong immune response, the positive control group in Figure 4K should be added.

Thanks very much for this very helpful comment. Following the reviewer’s suggestion, the mouse anti-CD3 antibody was used as the positive control in vitro to activate splenic T cells for ELISPOT assay, and the corresponding results have been added in revised Figure 4K. To address this, we have provided a detailed description in “Figure legends” section of “Figure 4. ePAC delivery and immune activation in vivo” as follows: The mouse anti-CD3 antibody was used to activate splenic T cells in vitro as the positive control for ELISPOT assay.

(6) In Figure 6G-I and other figures, the author should indicate the time point of detection. Meanwhile, there was no explanation for the different numbers of mice in Figure 6G-I. If the mouse was absent due to death, it may be necessary to advance the detection time to obtain a more convincing result.

Thanks very much for the comment. The samples for Figure 6 G-I data were collected and analyzed at the day 28 after the start of treatment. Following the reviewer’s suggestion, we have specifically marked the time point of “Sacrifice for sampling” in Figure 6A. And we have provided a detailed description in “Figure legends” section of “Figure 6. Evaluation ePAC antitumor efficacy in orthotopic HCC model by αTIM-3 combination” as follows: The mice were sacrificed and sampled for analysis on the day of 28 after initiating treatment. In addition, in Figure 6G-I we have clearly indicated the sample size for each group. Although three mice in the PBS group died, we still have obtained enough samples for statistical analysis (n>3).

(7) In Figure 6B, the rainbow color bar with an accurate number of maximum and minimum fluorescence intensity should be provided. In addition, the corresponding fluorescence intensity in Figure 6B should be noted.

Thanks very much for this very helpful comment. Following the reviewer’s suggestion, we have added the rainbow color bar with an accurate number of maximum and minimum fluorescence intensity, and the statistic results in revised Figure 6B.

(8) The quality of images in Figure 1D and Figure S1B could not support the author's conclusion; please provide higher-quality images.

Thanks very much. In Figure 1D and Figure S1B, to ensure the authenticity of the results, we tried our best to improve the quality of the pictures and provided the WB results with the full membrane scan. Although some non-specific bands appeared in the results, the target bands remained prominent. Additionally, we used two tags (HA and eGFP) for verification, which fully guarantees the reliability of our findings.

(9) In Figure 2F, the bright field in the overlay photo may disturb the observation. Meanwhile, the scale bar should be provided in enlarged images.

Thanks very much. Following the reviewer’s suggestion, we have deleted the bright field in revised Figure 2F and added the scale bar in the enlarged images.

Reviewer #3 (Public Review):

Summary:

The authors harnessed the potential of mammalian endogenous virus-like proteins to encapsulate virus-like particles (VLPs), enabling the precise delivery of tumor neoantigens. Through meticulous optimization of the VLP component ratios, they achieved remarkable stability and efficiency in delivering these crucial payloads. Moreover, the incorporation of CpG-ODN further heightened the targeted delivery efficiency and immunogenicity of the VLPs, solidifying their role as a potent tumor vaccine. In a diverse array of tumor mouse models, this novel tumor vaccine, termed ePAC, exhibited profound efficacy in activating the murine immune system. This activation manifested through the stimulation of dendritic cells in lymph nodes, the generation of effector memory T cells within the spleen, and the infiltration of neoantigen-specific T cells into tumors, resulting in robust anti-tumor responses.

Strengths:

This study delivered tumor neoantigens using VLPs, pioneering a new method for neoantigen delivery. Additionally, the gag protein of VLP is derived from mammalian endogenous virus-like protein, which offers greater safety compared to virus-derived gag proteins, thereby presenting a strong potential for clinical translation. The study also utilized a humanized mouse model to further validate the vaccine's efficacy and safety. Therefore, the anti-tumor vaccine designed in this study possesses both innovation and practicality.

Thanks very much to comment our work as “novel”, “innovation” and “practicality”. We sincerely appreciate the extremely helpful comments from the reviewer to significantly improve the quality of our manuscript.

Weaknesses:

(1) CpG-ODN is an FDA-approved adjuvant with various sequence structures. Why was CpG-ODN 1826 directly chosen in this study instead of other types of CpG-ODN? Additionally, how does DEC-205 recognize CpG-ODN 1826, and can DEC-205 recognize other types of CpG-ODN?

Thanks very much for the comment. CpG-ODNs are classified into three main types based on their structural composition: A, B, and C. Among them, only the B-class CpG-ODNs 1668, 1826, and 2006 have been directly proven to effectively bind DEC-205 and activate DC cells [1]. Therefore, in this study, B-class CpG-ODN 1826 was chosen as the ligand targeting DEC-205 on the surface of DC cells. DEC-205 primarily binds sequences containing the CpG motif core in a pH-dependent manner, thus theoretically allowing DEC-205 to bind a wide range of CpG-ODNs.

[1] Lahoud MH et al. DEC-205 is a cell surface receptor for CpG oligonucleotides. PNAS. 2012

(2) Why was it necessary to treat DCs with virus-like particles three times during the in vitro activation of T cells? Can this in vitro activation method effectively obtain neoantigen-responsive T cells?

Thanks very much for the comment. DCs need to be pre-stimulated before being used to activate T cells. Although Single DC stimulation can activate T cells, but the activation efficiency is insufficient. Current research suggests that three DC-T interactions can more effectively activate T cells [2]. Therefore, we prepared virus-like particle stimulated DCs for three times to fully activate T cells. Our results in Figures 3I and 7D also demonstrate that three-time stimulations effectively activated antigen-specific T cells, resulting in stronger tumor cell killing effects.

[2] Ali M et al. Induction of neoantigen-reactive T cells from healthy donors. Nature protocol. 2019.

(3) In the humanized mouse model, the authors used Hepa1-6 cells to construct the tumor model. To achieve the vaccine's anti-tumor function, these Hepa1-6 cells were additionally engineered to express HLA-A0201. However, in the in vitro experiments, the authors used the HepG2 cell line, which naturally expresses HLA-A0201. Why did the authors not continue to use HepG2 cells to construct the tumor model, instead of Hepa1-6 cells?

Thanks very much for the comment. HepG2 cells are derived from human liver cancer. When directly implant into immunocompetent mice, they will be cleared by the mouse immune system and will not form tumors. Therefore, we have not continued to use HepG2 cells to construct the tumor model.

(4) The advantages of low immunogenicity viruses as vaccines compared with conventional adenovirus and lentivirus, etc. should be discussed.

Thanks very much for the very suggestive comment. In the introduction starting from line 76, we first described the structure and function of lentiviruses and discussed the design and application of virus-like particles (VLPs) based on lentiviruses. To provide a more comprehensive comparison, we included a discussion on VLPs, lentiviruses, and adenoviruses in the discuss section (from line 441 to line 447) as follows: “Furthermore, comparing to the virus-based delivery vectors, the lentiviruses although can stably integrate into the host genome but carry risks of insertional mutagenesis; adenoviruses although have high transduction efficiency but strong immunogenicity, which leads to fast clearance by the immune system of the host and affects the efficiency of the secondary injection. Instead, our VLPs offer low immunogenicity and superior safety, making them more suitable for repeated use and vaccine development.”

(5) In Figure 6B, the authors should provide statistical results.

Thanks very much. We have provided the statistical results in revised Figure 6B following the reviewer’s suggestion.

(6) The entire article demonstrates a clear logical structure and substantial content in its writing. However, there are still some minor errors, such as the misspelling of "Spleenic" in Figure 3B, and the sentence from line 234 should be revised.

Thanks very much. We have carefully checked and corrected the typos throughout the whole manuscript as much as possible.

(7) The authors demonstrated the efficiency of CpG-ODN membrane modification by varying the concentration of DBCO, ultimately determining the optimal modification scheme for eVLP as 3.5 nmol of DBCO. However, in Figure 2B, the author did not provide the modification efficiency when the DBCO concentration is lower than 3.5 nmol. These results should be provided.

Thanks very much for the suggestion. We have repeated the experiment and reduced the concentration of DBCO to 2.1 nmol and 0.7 nmol, respectively. The results showed that in a 200 µl eVLP reaction system, 3.5 nmol DBCO achieved the highest modification efficiency. We have provided a detailed description in “Results” section of “Envelope decoration of neoantigen-loaded eVLP” as follows: Furthermore, by varying the concentration of DBCO-C6-NHS Ester from 0 to 14 nmol, ePAC exhibited different CpG-ODN loading efficiency as evidenced by agarose gel electrophoresis (Figure 2B and Figure S3). And the results showed that in a 200 µl eVLP reaction system, 3.5 nmol DBCO achieved the highest modification efficiency.

(8) In Figure 3, the authors presented a series of data demonstrating that ePAC can activate mouse DC2.4 cells and BMDCs in vitro. However, in Figure 7, there is no evidence showing whether human DC cells can be activated by ePAC in vitro. This data should be provided.

Thanks very much for this very helpful suggestion. We used ePAC to activate human DCs and the results indicate that, compared to the blank control group, both eVLP and ePAC increased the co-expression of CD80 and CD86 in DCs, and ePAC was the most efficient. We have provided a detailed description in the “Results” section of “Antitumor effect by HLA-A*0201 restricted vaccine” as follows: After the stimulation, the DCs in ePAC treated group showed the highest level of maturation comparing to the eVLP treated group and control group (Figure S4), by using flow cytometry analysis.”

eLife assessment

This manuscript describes a valuable study aimed at identifying the substrate specificity of two cell wall hydrolases LSS and LytM in S. aureus. The authors show that LytM has a novel function of cleaving D-Ala-Gly instead of only Gly-Gly by using synthetic substrates and compelling NMR-based real-time kinetics measurements.

Reviewer #1 (Public Review):

Summary:

The manuscript aimed at elucidating the substrate specificity of two M23 endopeptidase Lysostaphin (LSS) and LytM in S. aureus. Endopeptidases are known to cleave the glycine-bridges of staphylococcal cell wall peptidoglycan (PG). To address this question, various glycine-bridge peptides were synthesized as substrates, the catalytic domain of LSS and LytM were recombinantly expressed and purified, and the reactions were analyzed using solution-state NMR. The major finding is that LytM is not only a Gly-Gly endopeptidase, but also cleaves D-Ala-Gly. Technically, the advantage of using real-time NMR was emphasized in the manuscript. The study explores an interesting aspect of cell wall hydrolases in terms of substrate-level regulation. It potentially identified new enzymatic activity of LytM. However, the biological significance and relevance of the conclusions remain clear, as the results are mostly from synthetic substrates.

Strengths:

The study explores an interesting aspect of cell wall hydrolases in terms of substrate-level regulation. It potentially identified new enzymatic activity of LytM.

Comments on the revised version:

The authors have addressed most of my concerns. I agree that the physiological functions of LytM are not in the scope of the current study.

Reviewer #2 (Public Review):

Summary:

This work investigates the enzymatic properties of lysostaphin (LSS) and LytM, two enzymes produced by Staphylococcus aureus and previously described as glycyl-glycyl endopeptidases. The authors use synthetic peptide substrates mimicking peptidoglycan fragments to determine the substrate specificity of both enzymes and identify the bonds they cleave.

Strengths:

- This work is addressing a real gap in our knowledge since very little information is available about the substrate specificity of peptidoglycan hydrolases.<br /> - The experimental strategy and its implementation are robust and provide a thorough analysis of LSS and LytM enzymatic activities. The results are very convincing and demonstrate that the enzymatic properties of the model enzymes studied need to be revisited.<br /> - I think the experimental work is extremely well designed and way beyond what people usually do in the field. I believe that this sets a precedent that is worth acknowledging.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Recommendations For The Authors):

(1) Figure 2B and 2D: unlike what is written in the results part, the results are not consistent, but opposite: LSS has higher activity in 2B, less in 2D. 

The activities in Figure 2B come from NMR kinetic experiments with pGly, whereas Figure 2D reports on activity towards whole S. aureus cells. The LytM and LSS activities in these two experiments are indeed not directly comparable, but served to highlight the fact that simple pentaglycine is a poor model substrate for M23 enzymes. We carried out a turbidity assay with pristine enzymatic preparation and indeed it is highly consistent both with the kinetic assay using pentaglycine (Fig. 2B) as well as with larger PG fragments (Fig. 2K) indicating that the catalytic domain of LSS is significantly more efficient than LytM in hydrolyzing cells from community acquired methicillin resistant S. aureus strain USA300 as well as synthetic PG fragments.  The corresponding paragraph in Results has now been updated and rephrased.

(2) Figure 2, panel K missing statistical analysis, which makes it difficult to appreciate if the difference is significant. If it is a one-time experiment or a single value, the value should be presented as a table. The corresponding text in the results part is confusing. The fold change or drop in percentage is unclear in the figure. 

We have added a table (panel L) to Figure 2, which shows absolute values of LSS and LytM hydrolysis rates. Indeed, most of the values are from single NMR kinetic measurements, however, PG fragment (2) for LSS and PG fragment (3) for LytM were measured as duplicates to verify the reproducibility of the data. This is now mentioned in Figure 3 legend and in the Materials and Methods. Also, the corresponding text in the Results has been updated and rephrased.

(3) Figure 3H: the cleavage of D-ala-gly is unclear, the cleavage products need to be labeled and quantified. The experiment used purified PG treated with mutanolysin. Presumably, mixed monomers, dimers, trimers, and multimers are used. It would be helpful to show the HPLC profile of the purified muropeptide. It would be informative to analyze which fractions generate D-ala-gly. In addition, the intact murein sacculus should be included. 

For the sake of clarity, we have moved the 13C-HMBC spectra presented in Figure 3H to Fig. S7 in the Supplementary Material. The full carbonyl carbon region of the reference (prior to addition of enzyme) 13C-HMBC spectrum together with larger expansions of spectra acquired from enzyme-treated muropeptides are now shown. Furthermore, graphical presentations of identified PG fragments due to LSS/LytM activity are included. No HPLC analysis of the muropeptides was performed at this stage. Being insoluble, the intact murein sacculus is not amenable to liquid-state NMR studies, but we envisage studies of this remarkably complex structure also with solid-state NMR.

Reviewer #2 (Recommendations For The Authors): 

Overall, the experiments address the question asked by the authors and no additional experiments are required to strengthen the conclusions drawn. 

Abstract: 

The abstract is not well written and more specific (and accurate) information should be provided by the authors. 

We are grateful for the constructive and helpful comments to improve our manuscript. The abstract has now been modified by taking into account the Reviewer’s suggestions.

Introduction 

The intro is relatively long and wordy. It could most certainly be shortened and written in a more simple way to make it more impactful.

The introduction has now been modified by taking into account the Reviewer’s suggestions.

(2) One of the peptide stems in Figure 1 is missing a pentaglycine side chain; I would recommend increasing the font size; the peptide stem looks like it is attached to the carbon in position 2, it may be a good idea to move it to the left? 

We thank the Reviewer for this comment. Figure 1 has been improved, the frameshift has been fixed and the non-cross-linked pGly bridge has been included to the lysine side-chain in tetraStem.

Results 

Figure 2 is a bit overwhelming and its description is sketchy. Fig 2B shows a much higher activity of LSS on pGly as compared to LytM whilst 2K shows a very similar rate. 

We have rearranged Figures 1 and 2 by moving the original panel J in Figure 2 (structures of PG fragments) to Figure 1 panel C. The bar graph in Figure 2J now shows absolute rates of substrate hydrolysis for 2 mM LSS and LytM. These indicate that LSS is much more efficient against PG fragments in vitro in comparison to LytM. Rates normalized with respect to pGly are shown in Figure 2K. Also, a table showing absolute rates of hydrolysis for 2 mM LSS and 50 mM LytM has been included in Figure 2, panel L. In this Table, the values for PG fragments 2 and 3 were determined by two independent measurements to test and accredit the reproducibility of the method. This is also now elaborated further in the Materials and Methods.

Figure 3 is impressive and very informative but again hard to follow. 

- Panels 3A and 3B are nicely conceived but the resolution is rather poor and it is difficult to know exactly where the arrows point. 

We very much value suggestions given by the Reviewer to improve readability of our manuscript. In the case of Figure 3, we have now greatly enhanced the resolution and readability of the figure by horizontal scaling of panels A and B.

Figure 4 shows a comparative analysis of catalytic rate using various substrates, the authors may want to present graphs with the same y-axis to get the most out of the comparison between substrates. 

The scaling of the y-axis is the same for all the substrates now. In addition, we have reorganized the panels in the figure to enhance readability.

Figure 5: - The same remark as above, please cite all panels in alphabetical order. 

Citing to Figure 5 has now been revised.

Material and methods: 

- How were the peptide concentrations determined? It may be useful to indicate if specific conditions were required to solubilize some peptides, pGly is particularly insoluble in aqueous solutions. 

- Page 19, replace cpm by rpm; biological or technical replicates?

These have now been added and edited accordingly.

eLife assessment

This is an important study on changes in newborns' neural abilities to distinguish auditory signals at 37 weeks of gestation. The evidence of change in neural discrimination as a function of gestational age is convincing, but, as the authors acknowledge, further control of the acoustic signals and infants' language environment is necessary for the results to be used in clinical applications. The work contributes to the field of neurodevelopment.

Reviewer #1 (Public Review):

Summary:

This manuscript aimed to investigate the emergence of emotional sensitivity and its relationship with gestational age. Using an oddball paradigm and event-related potentials, the authors conducted an experiment in 120 healthy neonates with a gestational age range of 35 to 40 weeks. A significant developmental milestone was identified at 37 weeks gestational age, marking a crucial juncture in neonatal emotional responsiveness.

Strengths:

This study has several strengths, by providing profound insights into the early development of social-emotional functioning and unveiling the role of gestational age in shaping neonatal perceptual abilities. The methodology of this study demonstrates rigor and well-controlled experimental design, particularly involving matched control sounds, which enhances the reliability of the research. Their findings not only contribute to the field of neurodevelopment, but also showcase potential clinical applications, especially in the context of autism screening and early intervention for neurodevelopmental disorders.

Reviewer #2 (Public Review):

This is an important and very interesting report on a change in newborns' neural abilities to distinguish auditory signals as a function of the gestational age (GA) of the infant at birth (from 35 weeks GA to 40 weeks GA). The authors tested neural discrimination of sounds that were labeled 'happy' vs 'neutral' by listeners that represent two categories of sound, either human voices or auditory signals that mimic only certain properties of the human vocal signals. The finding is that a change occurs in neural discrimination of the happy and neutral auditory signals for infants born at or after 37 weeks of gestation, and not prior (at 35 or 36 weeks of gestation), and only for discrimination of the human vocal signals; no change occurs in discrimination of the nonhuman signals over the 35- to 40-week gestational ages tested. The neural evidence of discrimination of the vocal happy-neutral distinction and the absence of the discrimination of the control signals is convincing. The authors interpret this as a 'landmark' in infants' ability to detect changes in emotional vocal signals, and remark on the potential value of the test as a marker of the infants' interest in emotional signals, underscoring the fact that children at risk for autism spectrum disorder may not show the discrimination.

[Editors' note: The authors addressed the reviewers' main concern by clearly stating the limits of the study's implications.]

Author response:

The following is the authors’ response to the previous reviews.

Reviewer #1:

After reviewing the authors' response letter and the revised manuscript, I believe they have done a commendable job in addressing my comments.

Additionally, I concur with the concerns raised by Reviewer #2 regarding several potential confounding factors that require better control in their experimental design. These include the differences in physical properties between vocal and nonvocal stimuli, as well as the infant's exposure to the speech/auditory environment. These concerns should be thoroughly and explicitly discussed in the manuscript, ensuring a clearer understanding for the readers.

Thank you for the suggestion. We have discussion these limitations in our revised manuscript. In this round of revision, we have tempered our conclusion due to these limitations.

Reviewer #2:

The revised manuscript does discuss the limitations of the control stimuli, as well as the limitations with regard to conclusions that can be drawn from this data set. I therefore expected the authors to temper a bit their recommendation that this could be a 'screening' signal for autism because these data are not sufficiently strong to make that recommendation. Also, in the same vein, perhaps the title might be adjusted somewhat to suggest less certainty, for example, by using the word "change" rather than "milestone"'? The data are of interest, but the limitations are genuine limitations.

Thank you for your expert comments and considerations. We have moderated our recommendation for autism screening and softened the statement of “milestone” throughout the manuscript. Please see the updated article title, abstract, significance statement, and discussion.

eLife assessment

This work revealed numerous distinct lineages that evolved within a local human population in Alberta, Canada, leading to persistent cases of E. coli O157:H7 infections for over a decade and highlighting the ongoing involvement of local cattle in disease transmission, as well as the possibility of intermediate hosts and environmental reservoirs. This is a useful study that also showed a shift towards more virulent stx2a-only strains becoming predominant in the local lineages. The paper's evidence supporting the role played by cattle in the transmission system of E. coli O157:H7 in Alberta is currently incomplete, based on potential sampling issues associated with the selection of isolates as raised by the reviewers.

Reviewer #1 (Public Review):

Summary:

A nice study trying to identify the relationship between E. coli O157 from cattle and humans in Alberta, Canada.

Strengths:

(1) The combined human and animal sampling is a great foundation for this kind of study.

(2) Phylogenetic analyses seem to have been carried out in a high-quality fashion.

Weaknesses:

I think there may be a problem with the selection of the isolates for the primary analysis. This is what I'm thinking:

(1) Transmission analyses are strongly influenced by the sampling frame.

(2) While the authors have randomly selected from their isolate collections, which is fine, the collections themselves are not random.

(3) The animal isolates are likely to represent a broad swathe of diversity, because of the structured sampling of animal reservoirs undertaken (as I understand it).

(4) The human isolates are all from clinical cases. Clinical cases of the disease are likely to be closely related to other clinical cases, because of outbreaks (either detected, or undetected), and the high ascertainment rate for serious infections.

(5) Therefore, taking an equivalent number of animal and clinical isolates, will underestimate the total diversity in the clinical isolates because the sampling of the clinical isolates is less "independent" (in the statistical sense) than sampling from the animal isolates.

(6) This could lead to over-estimating of transmission from cattle to humans.

(7) "We hypothesize that the large proportion of disease associated with local transmission systems is a principal cause of Alberta's high E. coli O157:H7 incidence" - this seems a bit tautological. There is a lot of O157 because there's a lot of transmission. What part of the fact it is local means that it is a principal cause of high incidence? It seems that they've observed a high rate of local transmission, but the reasons for this are not apparent, and hence the cause of Alberta's incidence is not apparent. Would a better conclusion not be that "X% of STEC in Alberta is the result of transmission of local variants"? And then, this poses a question for future epi studies of what the transmission pathway is.

Reviewer #2 (Public Review):

This study identified multiple locally evolving lineages transmitted between cattle and humans persistently associated with E. coli O157:H7 illnesses for up to 13 years. Furthermore, this study mentions a dramatic shift in the local persistent lineages toward strains with the more virulent stx2a-only profile. The authors hypothesized that this phenomenon is the large proportion of disease associated with local transmission systems is a principal cause of Alberta's high E. coli O157:H7 incidence. These opinions more effectively explain the role of the cattle reservoir in the dynamics of E. coli O157:H7 human infections.

(1) The authors acknowledge the possibility of intermediate hosts or environmental reservoirs playing a role in transmission. Further discussion on the potential roles of other animal species commonly found in Alberta (e.g., sheep, goats, swine) could enhance the understanding of the transmission dynamics. Were isolates from these species available for analysis? If not, the authors should clearly state this limitation.

(2) The focus on E. coli O157:H7 is understandable given its prominence in Alberta and the availability of historical data. However, a brief discussion on the potential applicability of the findings to non-O157 STEC serogroups, and the limitations therein, would be beneficial. Are there reasons to believe the transmission dynamics would be similar or different for other serogroups?

(3) The authors briefly mention the need for elucidating local transmission systems to inform management strategies. A more detailed discussion on specific public health interventions that could be targeted at the identified LPLs and their potential reservoirs would strengthen the paper's impact.

(4) "Understanding the relationship between specific risk factors and E. coli O157:H7 infections is essential for developing effective prevention strategies. Have case-control or cohort studies been conducted to assess the correlation between identified risk factors and the incidence of E. coli O157:H7 infections? What methodologies were employed to control for potential confounders in these studies?"

(5) The study's findings are noteworthy, particularly in the context of E. coli O157:H7 epidemiology. However, the extent to which these results can be replicated across different temporal and geographical settings remains an open question. It would be constructive for the authors to provide additional data that demonstrate the replication of their sampling and sequencing experiments under varied conditions. This would address concerns regarding the specificity of the observed patterns to the initial study's parameters.

Author response:

Reviewer #1 (Public Review):

Summary:

A nice study trying to identify the relationship between E. coli O157 from cattle and humans in Alberta, Canada.

Strengths:

(1) The combined human and animal sampling is a great foundation for this kind of study.

(2) Phylogenetic analyses seem to have been carried out in a high-quality fashion.

Weaknesses:

I think there may be a problem with the selection of the isolates for the primary analysis. This is what I'm thinking:

(1) Transmission analyses are strongly influenced by the sampling frame.

(2) While the authors have randomly selected from their isolate collections, which is fine, the collections themselves are not random.

(3) The animal isolates are likely to represent a broad swathe of diversity, because of the structured sampling of animal reservoirs undertaken (as I understand it).

(4) The human isolates are all from clinical cases. Clinical cases of the disease are likely to be closely related to other clinical cases, because of outbreaks (either detected, or undetected), and the high ascertainment rate for serious infections.

(5) Therefore, taking an equivalent number of animal and clinical isolates, will underestimate the total diversity in the clinical isolates because the sampling of the clinical isolates is less "independent" (in the statistical sense) than sampling from the animal isolates.

(6) This could lead to over-estimating of transmission from cattle to humans.

We appreciate the reviewer’s careful thoughts about our sampling strategy. We agree with points (1) and (2), and we will provide additional details on the animal collections as requested.

We agree with point (3) in theory but not in fact. As shown in Figure 3a, the cattle isolates were very closely related, despite the temporal and geographic breadth of sampling within Alberta. The median SNP distance between cattle sequences was 45 (IQR 36-56), compared to 54 (IQR 43-229) SNPs between human sequences from cases in Alberta during the same years. Additionally, as shown in Figure 2, only clade A and B isolates – clades that diverge substantially from the rest of the tree – were dominated by human cases in Alberta. We will better highlight this evidence in the revision.

We agree with the reviewer in point (4) that outbreaks can be an important confounder of phylogenetic inference. This is why we down-sampled outbreaks (based on genetic relatedness, not external designation) in our extended analyses (lines 192-194). We did not do this in the primary analysis, because there were no large clusters of identical isolates. Figure 3b shows a limited number of small clusters; however, clustered cattle isolates outnumbered clustered human isolates, suggesting that any bias would be in the opposite direction the reviewer suggests. Regarding severe cases being oversampled among the clinical isolates, this is absolutely true and a limitation of all studies utilizing public health reporting data. We will make this limitation to generalizability clearer in the discussion. However, as noted above, clinical isolates were more variable than cattle isolates, so it does not appear to have heavily biased the analysis.

We disagree with the reviewer on point (5). While the bias toward severe cases could make the human isolates less independent, the relative sampling proportions are likely to induce greater distance between clinical isolates than cattle isolates, which is exactly what we observe (see response to point (3) above). Cattle are E. coli O157:H7’s primary reservoir, and humans are incidental hosts not able to sustain infection chains long-term. Not only is the bacteria prevalent among cattle, cattle are also highly prevalent in Alberta. Thus, even with 89 sampling points, we are still capturing a small proportion of the E. coli O157:H7 in the province. Being able to sample only a small proportion of cattle’s E. coli O157:H7 increases the likelihood of only sampling from the center of the distribution, making extreme cases such as that shown at the very bottom of the tree in Figure 3b, rare and important. In comparison, sampling from human cases constitutes a higher proportion of human infections relative to cattle, and is therefore more representative of the underlying distribution, including extremes. We will add this point to the limitations. As with the clustering above, if anything, this outcome would have biased the study away from identifying cattle as the primary reservoir. Additionally, the relatively small proportion of cattle sampled makes our finding that 15.7% of clinical isolates were within 5 SNPs of a cattle isolate, the distance most commonly used to indicate transmission for E. coli O157:H7, all the more remarkable.

Because of the aforementioned points, we disagree with the reviewer’s conclusion in point (6). We believe transmission from cattle-to-humans is likely underestimated for the reasons given above. Not only do all prior studies indicate ruminants as the primary reservoirs of E. coli O157:H7, and humans as only incidental hosts, our specific data do not support the reviewer’s individual contentions. That said, we will conduct a sensitivity analysis as recommended to determine the impact of sampling and inclusion of the small clusters on our primary findings.

(7) We hypothesize that the large proportion of disease associated with local transmission systems is a principal cause of Alberta's high E. coli O157:H7 incidence" - this seems a bit tautological. There is a lot of O157 because there's a lot of transmission. What part of the fact it is local means that it is a principal cause of high incidence? It seems that they've observed a high rate of local transmission, but the reasons for this are not apparent, and hence the cause of Alberta's incidence is not apparent. Would a better conclusion not be that "X% of STEC in Alberta is the result of transmission of local variants"? And then, this poses a question for future epi studies of what the transmission pathway is.

The reviewer is correct, and the suggestion for the direction of future studies was our intent with this statement. We will revise it.

Reviewer #2 (Public Review):

This study identified multiple locally evolving lineages transmitted between cattle and humans persistently associated with E. coli O157:H7 illnesses for up to 13 years. Furthermore, this study mentions a dramatic shift in the local persistent lineages toward strains with the more virulent stx2a-only profile. The authors hypothesized that this phenomenon is the large proportion of disease associated with local transmission systems is a principal cause of Alberta's high E. coli O157:H7 incidence. These opinions more effectively explain the role of the cattle reservoir in the dynamics of E. coli O157:H7 human infections.

(1) The authors acknowledge the possibility of intermediate hosts or environmental reservoirs playing a role in transmission. Further discussion on the potential roles of other animal species commonly found in Alberta (e.g., sheep, goats, swine) could enhance the understanding of the transmission dynamics. Were isolates from these species available for analysis? If not, the authors should clearly state this limitation.

We will expand the discussion of other species in Alberta, as suggested, including other livestock, wildlife, and the potential role of birds and flies. Unfortunately, we did not have sequences available from other species, and we will add this to the limitations. Sequences from other species may be available from sequences collected by others, which as we note in the limitations do not have sufficient metadata to assign them to Alberta vs. the rest of Canada. While we have requested this data, we have been unsuccessful in obtaining it. We will continue to pursue it.

(2) The focus on E. coli O157:H7 is understandable given its prominence in Alberta and the availability of historical data. However, a brief discussion on the potential applicability of the findings to non-O157 STEC serogroups, and the limitations therein, would be beneficial. Are there reasons to believe the transmission dynamics would be similar or different for other serogroups?

We appreciate this comment and will expand our discussion of relevance to non-O157 STEC. Other authors have proposed that transmission dynamics differ, and studies of STEC risk factors, including our own, support this. However, there has been very little direct study of non-O157 transmission dynamics and there is even less cross-species genomic and metadata available for non-O157 isolates of concern.

(3) The authors briefly mention the need for elucidating local transmission systems to inform management strategies. A more detailed discussion on specific public health interventions that could be targeted at the identified LPLs and their potential reservoirs would strengthen the paper's impact.

We agree with the reviewer that this would be a good addition to the manuscript. The public health implications for control are several and extend to non-STEC reportable zoonotic enteric infections, such as Campylobacter and Salmonella. We will add a discussion of these.

(4) Understanding the relationship between specific risk factors and E. coli O157:H7 infections is essential for developing effective prevention strategies. Have case-control or cohort studies been conducted to assess the correlation between identified risk factors and the incidence of E. coli O157:H7 infections? What methodologies were employed to control for potential confounders in these studies?

Yes, there have been several case-control studies of reported cases. Many of these are referenced in the discussion in terms of the contribution of different sources to infection. However, we will add a more explicit discussion of risk factors.

(5) The study's findings are noteworthy, particularly in the context of E. coli O157:H7 epidemiology. However, the extent to which these results can be replicated across different temporal and geographical settings remains an open question. It would be constructive for the authors to provide additional data that demonstrate the replication of their sampling and sequencing experiments under varied conditions. This would address concerns regarding the specificity of the observed patterns to the initial study's parameters.

We appreciate the reviewer’s comment, as we are currently building on this analysis with an American dataset with different types of data available than were used in this study. We will add a discussion of this. We will also be adding a sensitivity analysis to the manuscript simulating a different sampling approach, which should also be informative to this question.

eLife assessment

This important study shows that Type 3 secretion translocons in E. tarda and other bacteria activate the NAIP-NLRC4 inflammasome. The data from cellular and biochemical experiments showing that EseB is required for activation of the NLRC4 inflammasome are convincing, and comparing other translocons and additional cellular assays will provide further strength. This paper is broadly relevant to those investigating host-pathogen interactions in diverse organisms.

Reviewer #1 (Public Review):

Summary:<br /> In this study, Zhao and colleagues investigate inflammasome activation by E. tarda infections. They show that E. tarda induces the activation of the NLRC4 inflammasome as well as the non-canonical pathway in human THP1 macrophages. Further dissecting NLRC4 activation, they find that T3SS translocon components eseB, eseC and eseD are necessary for NLRC4 activation and that delivery of purified eseB is sufficient to trigger NAIP-dependent NLRC4 activation. Sequence analysis reveals that eseB shares homology within the C-terminus with T3SS needle and rod proteins, leading the authors to test if this region is necessary for inflammasome activation. They show that the eseB CT is required and that it mediates interaction with NAIP. Finally, they that homologs of eseB in other bacteria also share the same sequence and that they can activate NLRC4 in a HEK293T cell overexpression system.

Strengths:<br /> This is a very nice study that convincingly shows that eseB and its homologs can be recognized by the human NAIP/NLRC4 inflammasome. The experiments are well designed, controlled and described, and the papers is convincing as a whole.

Weaknesses:<br /> The authors need to discuss their study in the context of previous papers that have shown an important role for E. tarda flagellin in inflammasome activation and test whether flagellin and/or E. tarda T3SSs needle or rod can activate NLRC4.

The authors show that eseB and its homologs can activate NLRC4, but there are also other translocon proteins that are very different such as YopB or PopB. and share little homology with eseB. It would be nice to include a section comparing the different type 3 secretion systems. are there 2 different families of T3SSs, those that feature translocon components that are recognized by NAIP-NLRC4 and those that cannot be recognized?

Reviewer #2 (Public Review):

Summary:<br /> This work by Zhao et al. demonstrates the role of the Edwardsiella tarda type 3 secretion system translocon in activating human macrophage inflammation and pyroptosis. The authors show the requirement of both the bacterial translocon proteins and particular host inflammasome components for E. tarda-induced pyroptosis. In addition, the authors show that the C-terminal region of the translocon protein, EseB, is both necessary and sufficient to induce pyroptosis when present in the cytoplasm. The most terminal region of EseB was determined to be highly conserved among other T3SS-encoding pathogenic bacteria and a subset of these exhibited functionally similar effects on inflammasome activation. Overall, the data support the conclusions and interpretations and provide interesting insights into interactions between bacterial T3SS components and the host immune system.

Strengths:<br /> The authors use established and reliable molecular biology and bacterial genetics strategies to characterize the roles of the bacterial T3SS translocon and host inflammasome pathways to E. tarda-induced pyroptosis in human macrophages. These observations are naturally expanded upon by demonstrating the specific regions of EseB that are required for inflammasome activation and the conservation of this sequence among other pathogenic bacteria.

Weaknesses:<br /> The functional assessment of EseB homologues is limited to inflammasome activation at the protein level but does not include the effects on cell viability as shown for E. tarda EseB. Confirmation that EseB homologues have similar effects on cell death would strengthen this portion of the manuscript.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Weaknesses:

The authors need to discuss their study in the context of previous papers that have shown an important role for E. tarda flagellin in inflammasome activation and test whether flagellin and/or E. tarda T3SSs needle or rod can activate NLRC4.

We will add discussions on E. tarda flagellin and examine whether E. tarda flagellin or T3SS needle/rod can activate NLRC4.

The authors show that eseB and its homologs can activate NLRC4, but there are also other translocon proteins that are very different such as YopB or PopB. and share little homology with eseB. It would be nice to include a section comparing the different type 3 secretion systems. are there 2 different families of T3SSs, those that feature translocon components that are recognized by NAIP-NLRC4 and those that cannot be recognized?

The reviewer raises an interesting question. We will explore this question and provide relevant discussions/hypothesis in the revised manuscript.

Reviewer #2 (Public Review):

Weaknesses:

The functional assessment of EseB homologues is limited to inflammasome activation at the protein level but does not include the effects on cell viability as shown for E. tarda EseB. Confirmation that EseB homologues have similar effects on cell death would strengthen this portion of the manuscript.

According to the reviewer’s suggestion, we plan to examine the effects of representative EseB homologs on cell death.

eLife assessment

This valuable study presents interesting results aimed at explaining the effects of a human mutation on the mitochondrial import protein TIMM50 on mitochondrial function and neuronal excitability. While the evidence supporting the conclusions is solid, the interpretation of some of the results requires revision and moderation. This paper will be of interest to scientists in the mitochondria field.

Reviewer #1 (Public Review):

Mitochondria are essential organelles consisting in mammalian cells of about 1500 different proteins. Most of those are synthesized in the cytosol as precursor proteins, imported into mitochondria, and sorted into one of the four sub-mitochondrial compartments. The TIM23 complex, which is embedded in the mitochondrial inner membrane, facilitates the import of proteins that harbor Mitochondrial Targeting Sequence (MTS) at their N-terminus. Such proteins are sorted mainly to the mitochondrial matrix while some sub-groups are destined also to the inner membrane or the intermembrane space. TIMM50 (Tim50 in yeast) is an essential component of the TIM23 complex and mutations in this protein were reported to cause several diseases.

Summary:

In the current study, the authors analyzed the impact of TIMM50 mutations on the mitochondrial proteome in both patients' cells and mouse neurons. They provide compelling evidence for several surprising and highly interesting observations: (i) TIMM50 mutations affect the steady-state levels of only a portion of the putative TIMM50 substrates, (ii) such mutations result in increased electrical activity in mice neurons and in reduced levels of some potassium ion channels in the plasma membrane. These findings shed new light on mitochondrial biogenesis in mammalian cells and hint at an unexpected link between mitochondria and ion channels at the plasma membrane.

Strengths:

The authors used both cells from patients and neurons from mice to investigate the impact of mutations in TIMM50 on mitochondrial proteome and function.

Weaknesses:

(1) It will be interesting to monitor the levels of another MIM insertase namely, OXA1. This will help to understand whether some of the observed changes in levels of OXPHOS subunits are related to alterations in the amounts of this insertase.

(2) The authors did not provide explanations for several key findings like:<br /> A. Figure 3: How do the authors explain that although TIMM17 and TIMM23 were found to be significantly reduced by Western analysis they were not detected as such by the Mass Spec. method?<br /> B. How do the authors explain the higher levels of some proteins in the TIMM50 mutated cells?<br /> C. Can the authors elaborate on why mutated cells are impaired in their ability to switch their energetic emphasis to glycolysis when needed?

Reviewer #2 (Public Review):

Summary:

Mitochondria import hundreds of precursor proteins from the cytosol. The TOM and TIM23 complexes facilitate the import of the matrix-targeting pathway of mitochondria. In yeast, Tim50 is a critical and essential subunit of the TIM23 complex that mediates the transition of precursors from the outer to the inner membrane. The human Tim50 homolog TIMM50 is highly similar in structure and a comparable function of Tim50 and TIMM50 was proven by several biochemical and genetic studies in the past.

In this study, the authors characterize human cells that express lower levels or mutated versions of TIMM50. They found that in these TIMM50-depletion cells, the levels of other TIM23 core subunits are also diminished but many mitochondrial proteins are unaffected. Moreover, they observed alterations in the electrical activity and the levels of potassium channels in neuronal cells of TIMM50-deficient mice. They propose that these changes explain the pathology of patients who often suffer from epilepsy.

Strengths:

The paper is written by experts in the field, and it is very clear. The experiments are of high quality and sufficiently well-controlled. The study is interesting for a broad readership.

Weaknesses:

However, there is a problem that needs to be fixed: The interpretation of the results needs to be downgraded. The authors claim in the abstract, the introduction, and the discussion that TIMM50 and the TIM23 translocase might not be relevant for mitochondrial protein import in mammals. This is misleading and certainly wrong!!! What they do show is that the depletion of TIMM50 to about 20% of the normal levels is still tolerated in cultured cells grown in a glucose-rich medium. This is similar to the situation of cytochrome oxidase deficiency where lower levels are often well tolerated, and only very low levels (<20%) lead to Leigh syndrome. Still, it would be wrong to claim that respiration can occur without the terminal enzyme. Thus, it is essential that the authors change the wording here. In the discussion they offer several explanations: Mitochondria might import more proteins than they need and just degrade the excess. The TIMM50 depletion cells might increase the expression of mitochondrial proteins as a compensatory mechanism. Translocation across the TIM23 complex might not be the rate-limiting step in mitochondrial protein biogenesis. The authors do not have to sort this out on a molecular level, however, they have to be more cautious with the conclusions they make! Except for this issue, this is a very interesting study that will raise the interest of the mitochondrial community.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

(1) It will be interesting to monitor the levels of another MIM insertase namely, OXA1. This will help to understand whether some of the observed changes in levels of OXPHOS subunits are related to alterations in the amounts of this insertase.

OXA1 was not detected in the untargeted mass spectrometry analysis, most likely due to the fact that it is a polytopic membrane protein, spanning the membrane five times (1,2). Consequently, we measured OXA1 levels with immunoblotting, comparing patient fibroblast cells to the HC. No significant change in OXA1 steady state levels was observed. 

See the results below. These results will be added and discussed in the revised manuscript.

Author response image 1.

(2) Figure 3: How do the authors explain that although TIMM17 and TIMM23 were found to be significantly reduced by Western analysis they were not detected as such by the Mass Spec. method?

The untargeted mass spectrometry in the current study failed to detect the presence of TIMM17 for both, patient fibroblasts and mice neurons, while TIMM23 was detected only for mice neurons and a decrease was observed for this protein but was not significant. This is most likely due to the fact that TIMM17 and TIMM23 are both polytopic membrane proteins, spanning the membrane four times, which makes it difficult to extract them in quantities suitable for MS detection (2,3).

(3) How do the authors explain the higher levels of some proteins in the TIMM50 mutated cells?

The levels of fully functional TIM23 complex are deceased in patients' fibroblasts. Therefore, the mechanism by which the steady state level of some TIM23 substrate proteins is increased, can only be explained relying on events that occur outside the mitochondria. This could include increase in transcription, translation or post translation modifications, all of which may increase their steady state level albite the decrease in the steady state level of the import complex.

(4) Can the authors elaborate on why mutated cells are impaired in their ability to switch their energetic emphasis to glycolysis when needed?

Cellular regulation of the metabolic switch to glycolysis occurs via two known pathways: 1) Activation of AMP-activated protein kinase (AMPK) by increased levels of AMP/ADP (4). 2) Inhibition of pyruvate dehydrogenase (PDH) complexes by pyruvate dehydrogenase kinases (PDK) (5). Therefore, changes in the steady state levels of any of these regulators could push the cells towards anaerobic energy production, when needed. In our model systems, we did not observe changes in any of the AMPK, PDH or PDK subunits that were detected in our untargeted mass spectrometry analysis (see volcano plots below, no PDK subunits were detected in patient fibroblasts). Although this doesn’t directly explain why the cells have an impaired ability to switch their energetic emphasis, it does possibly explain why the switch did not occur de facto.

Author response image 2.

Reviewer #2 (Public Review):

(1) The authors claim in the abstract, the introduction, and the discussion that TIMM50 and the TIM23 translocase might not be relevant for mitochondrial protein import in mammals. This is misleading and certainly wrong!!!

Indeed, it was not in our intention to claim that the TIM23 complex might not be relevant. We have now rewritten the relevant parts to convey the correct message:

Abstract – 

Line 25 - “Strikingly, TIMM50 deficiency had no impact on the steady state levels of most of its putative substrates, suggesting that even low levels of a functional TIM23 complex are sufficient to maintain the majority of complex-dependent mitochondrial proteome.”

Introduction – 

Line 87 - Surprisingly, functional and physiological analysis points to the possibility that low levels of TIM23 complex core subunits (TIMM50, TIMM17 and TIMM23) are sufficient for maintaining steady-state levels of most presequence-containing proteins. However, the reduced TIM23CORE component levels do affect some critical mitochondrial properties and neuronal activity.

Discussion – 

Line 339 – “…surprising, as normal TIM23 complex levels are suggested to be indispensable for the translocation of presequence-containing mitochondrial proteins…”

Line 344 – “…it is possible that unlike what occurs in yeast, normal levels of mammalian TIMM50 and TIM23 complex are mainly essential for maintaining the steady state levels of intricate complexes/assemblies.”

Line 396 – “In summary, our results suggest that even low levels of TIMM50 and TIM23CORE components suffice in maintaining the majority of mitochondrial matrix and inner membrane proteome. Nevertheless, reductions in TIMM50 levels led to a decrease of many OXPHOS and MRP complex subunits, which indicates that normal TIMM50 levels might be mainly essential for maintaining the steady state levels and assembly of intricate complex proteins.”

(1) Homberg B, Rehling P, Cruz-Zaragoza LD. The multifaceted mitochondrial OXA insertase. Trends Cell Biol. 2023;33(9):765–72. 

(2) Carroll J, Altman MC, Fearnley IM, Walker JE. Identification of membrane proteins by tandem mass spectrometry of protein ions. Proc Natl Acad Sci U S A.

2007;104(36):14330–5. 

(3) Dekker PJT, Keil P, Rassow J, Maarse AC, Pfanner N, Meijer M. Identification of MIM23, a putative component of the protein import machinery of the mitochondrial inner membrane. FEBS Lett. 1993;330(1):66–70. 

(4) Trefts E, Shaw RJ. AMPK: restoring metabolic homeostasis over space and time. Mol Cell [Internet]. 2021;81(18):3677–90. Available from:

https://doi.org/10.1016/j.molcel.2021.08.015

(5) Zhang S, Hulver MW, McMillan RP, Cline MA, Gilbert ER. The pivotal role of pyruvate dehydrogenase kinases in metabolic flexibility. Nutr Metab. 2014;11(1):1–9.

eLife assessment

Periods in which experience regulates early plasticity in sensory circuits are well established, but the mechanisms that control these critical periods are poorly understood. In this important study, the authors examine early-life critical periods that regulate the Drosophila antennal lobe and show that constant odor exposure markedly reduces the volume, synapse number, and function of a specific glomerulus. The authors offer mostly compelling evidence, that these changes are mediated by the invasion of ensheathing glia into the glomerulus where they phagocytose connections via a mechanism involving the engulfment receptor Draper.

Reviewer #1 (Public Review):

Time periods in which experience regulates early plasticity in sensory circuits are well established, but the mechanisms that control these critical periods are poorly understood. In this manuscript, Leier and Foden and colleagues examine early-life critical periods that regulate the Drosophila antennal lobe, a model sensory circuit for understanding synaptic organization. Using early-life (0-2 days old) exposure to distinct odorants, they show that constant odor exposure markedly reduces the volume, synapse number, and function of the VM7 glomerulus. The authors offer evidence that these changes are mediated by invasion of ensheathing glia into the glomerulus where they phagocytose connections via a mechanism involving the engulfment receptor Draper.

This manuscript is a striking example of a study where the questions are interesting, the authors spent a considerable amount of time to clearly think out the best experiments to ask their questions in the most straightforward way, and expressed the results in a careful, cogent, and well-written fashion. It was a genuine delight to read this paper. I have two experimental suggestions that would really round out existing work to better support the existing conclusions and some instances where additional data or tempered language in describing results would better support their conclusions. Overall, though, this is an incredibly important finding, a careful analysis, and an excellent mechanistic advance in understanding sensory critical period biology.

Reviewer #2 (Public Review):

Sensory experiences during developmental critical periods have long-lasting impacts on neural circuit function and behavior. However, the underlying molecular and cellular mechanisms that drive these enduring changes are not fully understood. In Drosophila, the antennal lobe is composed of synapses between olfactory sensory neurons (OSNs) and projection neurons (PNs), arranged into distinct glomeruli. Many of these glomeruli show structural plasticity in response to early-life odor exposure, reflecting the sensitivity of the olfactory circuitry to early sensory experiences.

In their study, the authors explored the role of glia in the development of the antennal lobe in young adult flies, proposing that glial cells might also play a role in experience-dependent plasticity. They identified a critical period during which both structural and functional plasticity of OSN-PN synapses occur within the ethyl butyrate (EB)-responsive VM7 glomerulus. When flies were exposed to EB within the first two days post-eclosion, significant reductions in glomerular volume, presynaptic terminal numbers, and postsynaptic activity were observed. The study further highlights the importance of the highly conserved engulfment receptor Draper in facilitating this critical period plasticity. The authors demonstrated that, in response to EB exposure during this developmental window, ensheathing glia increase Draper expression, infiltrate the VM7 glomerulus, and actively phagocytose OSN presynaptic terminals. This synapse pruning has lasting effects on circuit function, leading to persistent decreases in both OSN-PN synapse numbers and spontaneous PN activity as analyzed by perforated patch-clamp electrophysiology to record spontaneous activity from PNs postsynaptic to Or42a OSNs.

In my view, this is an intriguing and potentially valuable set of data. However, since I am not an expert in critical periods or habituation, I do not feel entirely qualified to assess the full significance or the novelty of their findings, particularly in relation to existing research.

eLife assessment

This study offers a useful discussion of the well-accepted abundance-occupancy relationship in macroecology. While using the ebird large dataset to revisit the theme is interesting, multiple unresolved confounding factors exist, leaving the results inadequate to overturn the repeatedly confirmed abundancy-occupancy relationship.

Reviewer #1 (Public Review):

Summary:

This article presents a meta-analysis that challenges established abundance-occupancy relationships (AORs) by utilizing the largest known bird observation database. The analysis yields contentious outcomes, raising the question of whether these findings could potentially refute AORs.

Strengths:

The study employed an extensive aggregation of datasets to date to scrutinize the abundance-occupancy relationships (AORs).

Weaknesses:

While the dataset employed in this research holds promise, a rigorous justification of the core assumptions underpinning the analytical framework is inadequate. The authors should thoroughly address the correlation between checklist data and global range data, ensuring that the foundational assumptions and potential confounding factors are explicitly examined and articulated within the study's context.

Reviewer #2 (Public Review):

Summary:

The goal is to ask if common species when studied across their range tend to have larger ranges in total. To do this the authors examined a very large citizen science database which gives estimates of numbers, and correlated that with the total range size, available from Birdlife. The average correlation is positive but close to zero, and the distribution around zero is also narrow, leading to the conclusion that, even if applicable in some cases, there is no evidence for consistent trends in one or other direction.

Strengths:

The study raises a dormant question, with a large dataset.

Weaknesses:

This study combines information from across the whole world, with many different habitats, taxa, and observations, which surely leads to a quite heterogeneous collection.

First, scale. Many of the earlier analyses were within smaller areas, and for example, ranges are not obviously bounded by a physical barrier. I assume this study is only looking at breeding ranges; that should be stated, as 40% of all bird species migrate, and winter limitation of populations is important. Also are abundances only breeding abundances or are they measured through the year? Are alien distributions removed?

Second, consider various reasons why abundance and range size may be correlated (sometimes positively and sometimes negatively) at large scales. Combining studies across such a large diversity of ecological situations seems to create many possibilities to miss interesting patterns. For example:

(1) Islands are small and often show density release.

(2) North temperate regions have large ranges (Rapoport's rule) and higher population sizes than the tropics.

(3) Body size correlates with global range size (I am unsure if this has recently been tested but is present in older papers) and with density. For example, cosmopolitan species (barn owl, osprey, peregrine) are relatively large and relatively rare.

(4) In the consideration of alien species, it certainly looks to me as if the law is followed, with pigeon, starling, and sparrow both common and widely distributed. I guess one needs to make some sort of statement about anthropogenic influences, given the dramatic changes in both populations and environments over the past 50 years.

(5) Wing shape correlates with ecological niche and range size (e.g. White, American Naturalist). Aerial foraging species with pointed wings are likely to be easily detected, and several have large ranges reflecting dispersal (e.g. barn swallow).

Third, biases. I am not conversant with ebird methodology, but the number appearing on checklists seems a very poor estimate of local abundance. As noted in the paper, common species may be underestimated in their abundance. Flocking species must generate large numbers, skulking species few. The survey is often likely to be in areas favorable to some species and not others. The alternative approach in the paper comes from an earlier study, based on ebird but then creating densities within grids and surely comes with similar issues.<br /> Biases are present in range as well. Notably, tropical mountain-occupying species have range sizes over-estimated because holes in the range are not generally accounted for (Ocampo-Peñuela et al Nature communications). These species are often quite rare too.

Fourth, random error. Random error in ebird assessments is likely to be large, with differences among observers, seasons, days, and weather (e.g. Callaghan et al. 2021, PNAS). Range sizes also come with many errors, which is why occupancy is usually seen as the more appropriate measure.

If we consider both range and abundance measurements to be subject to random error in any one species list, then the removal of all these errors will surely increase the correlation for that list (the covariance shouldn't change but the variances will decrease). I think (but am not sure) that this will affect the mean correlation because more of the positive correlations appear 'real' given the overall mean is positive. It will definitely affect the variance of the correlations; the low variance is one of the main points in the paper. A high variance would point to the operation of multiple mechanisms, some perhaps producing negative correlations (Blackburn et al. 2006).

On P.80 it is stated: "Specifically, we can quantify how AOR will change in relation to increases in species richness and sampling duration, both of which are predicted to reduce the magnitude of AORs" I haven't checked the references that make this statement, but intuitively the opposite is expected? More species and longer durations should both increase the accuracy of the estimate, so removing them introduces more error? Perhaps dividing by an uncertain estimate introduces more error anyway. At any rate, the authors should explain the quoted statement in this paper.

It would be of considerable interest to look at the extreme negative and extreme positive correlations: do they make any biological sense?

Discussion:

I can see how publication bias can affect meta-analyses (addressed in the Gaston et al. 2006 paper) but less easily see how confirmation bias can. It seems to me that some of the points made above must explain the difference between this study and Blackburn et al. 2006's strong result.

Certainly, AOR really does seem to be present in at least some cases (e.g. British breeding birds) and a discussion of individual cases would be valuable. Previous studies have also noted that there are at least some negative and some non-significant associations, and understanding the underlying causes is of great interest (e.g. Kotiaho et al. Biology Letters).

Reviewer #3 (Public Review):

Summary:

This paper claims to overturn the longstanding abundance occupancy relationship.

Strengths:

(1) The above would be important if true.<br /> (2) The dataset is large.

Weaknesses:

(1) The authors are not really measuring the abundance-occupancy relationship (AOR). They are measuring abundance-range size. The AOR typically measures patches in a metapopulation, i.e. at a local scale. Range size is not an interchangeable notion with local occupancy.

(2) Ebird is a poor dataset for this. The sampling unit is non-standard. So abundance can at best be estimated by controlling for sampling effort. Comparisons across space are also likely to be highly heterogenous. They also threw out checklists in which abundances were too high to be estimated (reported as "X"). As evidence of the biases in using eBird for this pattern, the North American Breeding Bird Survey, a very similar taxonomic and geographic scope but with a consistent sampling protocol across space does show clear support for the AOR.

(3) In general, I wonder if a pattern demonstrated in thousands of data sets can be overturned by findings in one data set. It may be a big dataset but any biases in the dataset are repeated across all of those observations.

Overturning a major conclusion requires careful work. This paper did not rise to this level.

eLife assessment

This study presents valuable experimental and numerical results on the motility of a magnetotactic bacterium living in sedimentary environments, particularly in environments of varying magnetic field strengths. The evidence supporting the claims of the authors is solid, although the statistical significance comparing experiments with the numerical work is weak. The study will be of interest to biophysicists interested in bacterial motility.

Reviewer #1 (Public Review):

Summary:<br /> The authors present experimental and numerical results on the motility Magnetospirillum gryphiswaldense MSR-1, a magnetotactic bacterium living in sedimentary environments. The authors manufactured microfluidic chips containing three-dimensional obstacles of irregular shape, that match the statistical features of the grains observed in the sediment via micro-computer tomography. The bacteria are furthermore subject to an external magnetic field, whose intensity can be varied. The key quantity measured in the experiments is the throughput ratio, defined as the ratio between the number of bacteria that reach the end of the microfluidic channel and the number of bacteria entering it. The main result is that the throughput ratio is non-monotonic and exhibits a maximum at magnetic field strength comparable with Earth's magnetic field. The authors rationalize the throughput suppression at large magnetic fields by quantifying the number of bacteria trapped in corners between grains.

Strengths:<br /> While magnetotactic bacteria's general motility in bulk has been characterized, we know much less about their dynamics in a realistic setting, such as a disordered porous material. The micro-computer tomography of sediments and their artificial reconstruction in a microfluidic channel is a powerful method that establishes the rigorous methodology of this work. This technique can give access to further characterization of microbial motility. The coupling of experiments and computer simulations lends considerable strength to the claims of the authors, because the model parameters (with one exception) are directly measured in the experiments.

Weaknesses:<br /> The main weakness of the manuscript pertains to the discussion of the statistical significance of the experimental throughput ratio. Especially when comparing results at zero and 50 micro Tesla. The simulations seem to predict a stronger effect than seen in the experiments. The authors do not address this discrepancy.

Reviewer #2 (Public Review):

Summary:<br /> simulation study of magnetotactic bacteria in microfluidic channels containing sediment-mimicking obstacles. The obstacles were produced based on micro-computer tomography reconstructions of bacteria-rich sediment samples. The swimming of bacteria through these channels is found experimentally to display the highest throughput for physiological magnetic fields. Computer simulations of active Brownian particles, parameterized based on experimental trajectories are used to quantify the swimming throughput in detail. Similar behavior as in experiments is obtained, but also considerable variability between different channel geometries. Swimming at strong field is impeded by the trapping of bacteria in corners, while at weak fields the direction of motion is almost random. The trapping effect is confirmed in the experiments, as well as the escape of bacteria with reducing field strength.

Strengths:<br /> This is a very careful and detailed study, which draws its main strength from the fruitful combination of the construction of novel microfluidic devices, their use in motility experiments, and simulations of active Brownian particles adapted to the experiment. Based on their results, the authors hypothesize that magnetotactic bacteria may have evolved to produce magnetic properties that are adapted to the geomagnetic field in order to balance movement and orientation in such crowded environments. They provide strong arguments in favor<br /> of such a hypothesis.

Weaknesses:<br /> Some of the issues touched upon here have been studied also in other articles. It would be good to extend the list of references accordingly and discuss the relation briefly in the text.

eLife assessment

This important study integrates microfluidic experiments and mathematical modeling to investigate how flow dynamics and biofilm growth and detachment influence each other. Using Pseudomonas aeruginosa as a model organism, the study identifies several key effects and stages in biofilm development, albeit with some weaknesses in clearly defining the setup and some of their interpretations. The comparison between experimental results and theoretical models is convincing, providing a robust analysis of the biofilm's behavior under varying flow conditions. The findings will be helpful for researchers working on biofilms and their applications.

Reviewer #1 (Public Review):

Summary:<br /> The paper investigates the interplay between fluid flow and biofilm development using Pseudomonas aeruginosa PAO1 in microfluidic channels. By combining experimental observations with mathematical modeling, the study identifies the significant impact of nutrient limitation and hydrodynamic forces on biofilm growth and detachment. The authors demonstrate that nutrient limitation drives the longitudinal distribution of biomass, while flow-induced detachment influences the maximum clogging and temporal dynamics. The study highlights that pressure buildup plays a critical role in biofilm detachment, leading to cyclic episodes of sloughing and regrowth. A stochastic model is used to describe the detachment process, capturing the apparent randomness of sloughing events. The findings offer insights into biofilm behavior during clogging and fouling, potentially relevant to infections, environmental processes, and engineering applications.

Strengths:<br /> This paper demonstrates a strong integration of experimental work and mathematical modeling, providing a comprehensive understanding of biofilm dynamics in straight microfluidic channel. The simplicity of the microchannel geometry allows for accurate modeling, and the findings have the potential to be applied to more complex geometries. The detailed analysis of nutrient limitation and its impact on biofilm growth offers valuable insights into the conditions that drive biofilm formation. The model effectively describes biofilm development across different stages, capturing both initial growth and cyclic detachment processes. While cyclic pressure buildup has been studied previously, the incorporation of a stochastic model to describe detachment events is a novel and significant contribution, capturing the complexity and randomness of biofilm behavior. Finally, the investigation of pressure buildup and its role in cyclic detachment and regrowth enhances our understanding of the mechanical forces at play, making the findings applicable to a wide range of technological and clinical contexts.

Weaknesses:<br /> The study achieves its primary goal of integrating experiments and modeling to understand the coupling between flow and biofilm growth and detachment in a microfluidic channel, but it should have highlighted the weaknesses of the methods. I list the ones that, in my opinion, are the main ones:

• The study does not consider biofilm porosity, which could significantly affect the flow and forces exerted on the biofilm. Porosity could impact the boundary conditions, such as the no-slip condition, which should be validated experimentally.<br /> • The research suggests EPS development as a stage in biofilm growth but does not probe it using lectin staining. This makes it impossible to accurately assess the role of EPS in biofilm development and detachment processes.<br /> • While the force and flow are three-dimensional, the images are taken in two dimensions. The paper does not clearly explain how the 2D images are extrapolated to make 3D assessments, which could lead to inaccuracies.<br /> • Although the findings are tested using polysaccharide-deficient mutants, the results could have been analyzed in greater detail. A more thorough analysis would help to better understand the role of matrix composition on the stochastic model of detachment.

Reviewer #2 (Public Review):

This manuscript develops well-controlled microfluidic experiments and mathematical modelling to resolve how the temporal development of P. aeruginosa biofilms is shaped by ambient flow. The experiment considers a simple rectangular channel on which a constant flow rate is applied and UV LEDs are used to confine the biofilm to a relatively small length of device. While there is often considerable geometrical complexity in confined environments and feedback between biofilm/flow (e.g. in porous media), these simplified conditions are much more amenable to analysis. A non-dimensional mathematical model that considers nutrient transport, biofilm growth and detachment is developed and used to interpret experimental data. Regimes with both gradual detachment and catastrophic sloughing are considered. The concentration of nutrients in the media is altered to resolve the effect of nutrient limitation. In addition, the role of a couple of major polysaccharide EPS components are explored with mutants, which leads results in line with previous studies.

There has been a vast amount of experimental and modelling work done on biofilms, but relatively rarely are the two linked together so tightly as in this paper. Predictions on influence of the non-dimensional Damkohler number on the longitudinal distribution of biofilm and functional dependence of flow on the maximum amount of biofilm (phi_max) are demonstrated. The study reconfirms a number of previous works that showed the gradual detachment rate of biofilms scales with the square root of the shear stress. More challenging are the rapid biofilm detachment events where a large amount of biofilm is detached at once. These events occur are identified experimentally using an automated analysis pipeline and are fitted with probability distributions. The time between detachment events was fitted with a Gamma distribution and the amplitude of the detachment events was fitted with a log-normal distribution, however, it is not clear how good these fits are. Experimental data was then used as an input for a stochastic differential equation, but the output of this model is compared only qualitatively to that of the experiments. Overall, this paper does an admirable job of developing a well-constrained experiments and a tightly integrated mathematical framework through which to interpret them. However, the new insights this provides the underlying physical/biological mechanisms are relatively limited.

eLife assessment

This important study explores how cells maintain subcellular structures in the face of constant protein turnover, focusing on neurons, whose synapses must be kept stable over long periods of time for memory storage. Using proteins from knock-in mice expressing tagged variants of the synaptic scaffold protein PSD95, nanobodies, and multiple imaging methods, there is compelling evidence that PSD95 proteins form complexes at synapses in which single protein copies are sequentially replaced over time. This happens at different rates in different synapse types and is slowest in areas where PSD95 lifetime is the longest and long-term memories are stored. While of general relevance to cell biology, these findings are of particular interest to neuroscientists because they support the hypothesis put forward by Francis Crick that stable synapses, and hence stable long-term memories, can be maintained in the face of short protein lifetimes by sequential replacement of individual subunits in synaptic protein complexes.

Joint Public Review

The present study explored the principles that allow cells to maintain complex subcellular proteinaceous structures despite the limited lifetimes of the individual protein components. This is particularly critical in the case of neurons, where the size and protein composition of synapses define synaptic strength and encode memory.

PSD95 is an abundant synapse protein that acts as a scaffold in the recruitment of transmitter receptors and other signaling proteins and is required for memory formation. The authors used super-resolution microscopy to study PSD95 super-complexes isolated from the brains of mice expressing tagged PSD variants (Halo-Tag, mEos, GFP). Their results show compellingly that a large fraction (~25%) of super-complexes contains two PSD95 copies about 13 nm apart, that there is substantial turnover of PSD95 proteins in super-complexes over a period of seven days, and that ~5-20% of the super-complexes contain new and old PSD95 molecules. This percentage is higher in synaptic fractions as compared to total brain lysates, and highest in isocortex samples (~20%). These important findings support the hypothesis put forward by Crick that sequential subunit replacement gives synaptic super-complexes long lifetimes and thus aids in memory maintenance. Overall, this is a very interesting study that provides key insights into how synaptic protein complexes are formed and maintained. On the other hand, the actual role of these PSD95 super-complexes in long-term memory storage remains unknown. Specifically, a direct correlation between PSD95 stability and memory formation remains hypothetical - but the present findings indicate important new directions for studying the mechanisms that control postsynaptic protein organisation and the maintenance of postsynaptic proteinaceous substructures.

Strengths

(1) The study employed an appropriate and validated methodology.<br /> (2) Large numbers of PSD95 super-complexes from three different mouse models were imaged and analyzed, providing adequately powered sample sizes.<br /> (3) State-of-the-art super-resolution imaging techniques (PALM and MINFLUX) were used, providing a robust, high-quality, cross-validated analysis of PSD95 protein complexes that is useful for the community.<br /> (4) The result that PSD95 proteins in dimeric complexes are on average 12.7 nm apart is useful and has implications for studies on the nanoscale organization of PSD95 at synapses.<br /> (5) The finding that postsynaptic protein complexes can continue to exist while individual components are being renewed is important for our understanding of synapse maintenance and stability.<br /> (6) The data on the turnover rate of PSD95 in super-complexes from different brain regions provide a first indication of potentially meaningful differences in the lifetime of super-complexes between brain regions.

Weaknesses

(1) The manuscript emphasizes the hypothesis that stable super-complexes, maintained through sequential replacement of subunits, might underlie the long-term storage of memory. While an interesting idea, this notion requires considerably more research. The presented experimental data are indeed consistent with this notion, but there is no evidence that these complexes are causally related to memory storage.<br /> (2) Much of the presented work is performed on biochemically isolated protein complexes. The biochemical isolation procedures rely on physical disruption and detergents that are known to alter the composition and structure of complexes in certain cases. Thus, it remains unclear how the protein complexes described in this study relate to PSD95 complexes in intact synapses.<br /> (3) Because not all GFP molecules mature and fold correctly in vitro and the PSD95-mEos mice used were heterozygous, the interpretation of the corresponding quantifications is not straightforward.<br /> (4) It was not tested whether different numbers of PSD95 molecules per super-complex might contribute to different retention times of PSD95, e.g. in synaptic vs. total-forebrain super-complexes.<br /> (5) The conclusion that the population of 'mixed' synapses is higher in the isocortex than in other brain regions is not supported by statistical analysis.<br /> (6) The validity of conclusions regarding PSD95 degradation based on relative changes in the occurrence of SiR-Halo-positive puncta is limited.

Author response:

The following is the authors’ response to the original reviews.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

The work is well performed and thoroughly convincing. 

However, a few points could be improved, by adjusting the manuscript: 

(1) The wording of the abstract is confusing for the casual reader. The initial impression is that the 2-copy complexes contain the majority of the PSD95 copies. This is not the case, as shown in panel cii. It would be important for the authors to explain in the abstract the exact percentage of molecules found within 2-copy complexes. 

We have now amended the abstract, making it clear that it’s not most of the complexes.  

(2) Did the authors find a sizeable population of 2-copy complexes by investigating wild-type proteins, using nanobody labeling (Figure S2)? It would be important to quantify and discuss these data. 

It was not possible to perform this analysis on the wild-type proteins. The quantification would rely on all the PSD95 molecules being bound by the antibody, which we cannot guarantee. Furthermore, the nanobody labeling would need to be stoichiometric. 

(3) The authors quote the separation value of 12.7 nm throughout their text, including the abstract. This may be somewhat misleading since the authors investigate the PSD95-GFP molecules, labeled using anti-GFP nanobodies. The large size of the two GFP molecules (~3 nm), and that of the nanobodies, will influence the readout. Two groups have already reported a separation of ~7-8 nm between neighboring PSD95 molecules in synapses, using PSD95 nanobodies, to minimize the linkage

error: https://doi.org/10.1101/2022.08.03.502284 and https://doi.org/10.1101/2023.10.18.562 700  

The difference observed here is consistent with an effect of the additional GFP moieties; the authors should cite these works (albeit they are now only provided as biorXiv pre-prints) and should mention this discrepancy, and its potential tagging-related explanation. 

We have now referenced the work and referred to this in the discussion.

(4) The authors may want to re-check the manuscript; some minor problems should be corrected, such as the mislabeling of Figure 2 and "Figure 5". 

This has now been corrected.  

Reviewer #2 (Recommendations For The Authors): 

The authors suggest that the stability of the PSD95 dimeric complex correlates with memory formation. However, the turnover experiments were conducted only on three-month-old animals, which can be considered to be at a stage of lower synaptic functionality turnover. It would be appropriate to study dimer turnover during the memory formation period at three to four weeks of age, for example in comparison to the oldest mice. 

Alternatively, it might be interesting to study the turnover in the hippocampus following exposure to a memory test. 

Whilst potentially useful, these experiments are outside of the scope of this manuscript.   

It is not clear whether the different turnover identified in various brain areas is statistically significant, as apparently no statistical analysis has been conducted. 

The findings were significant, and the SI table containing the p-values has been emphasized further in the manuscript.  

Reviewer #3 (Recommendations For The Authors): 

(1) In the last paragraph of the Results section, it could be made clearer what the nature is of the correlation between PSD95 half-life and mixed supercomplexes to understand how to interpret this correlation. In the discussion, it is concluded that stable synapses have long protein lifetimes and slow replacement of scaffolding proteins. However, this is based on the correlation of protein lifetime and mixed supercomplexes in the cortex, which does not provide any evidence that this relation is true in single synapses or is specific for stable synapses. To make this statement, the authors could for instance directly correlate the stoichiometry of supercomplexes with the protein lifetime and size of individual synapses. 

Unfortunately, we can’t directly measure the lifetime of each complex, and so it’s only possible to compare region-to-region. In doing so, we found that there was a correlation between the protein lifetime and the “mixed” population.  

(2) Some essential parts seem missing: the materials and methods and Figure 2 are not included. Also, the numbering of figures is incorrect. Both in the figure legends and the text. 

This has been added. 

(3) Figure 1a could contain more details of the experimental procedures. For example, it could be made clearer how PSD95 supercomplexes are isolated from brain homogenate. 

This is now presents in the methods. 

(4) In Figure 1c, single molecules of PSD95 are identified using PALM with a resolution of 30 nm. However, in Figure 1d it is shown that PSD95 molecules reside on average 13 nm apart, indicating that a resolution of 30 nm is not sufficient to resolve single PSD95 molecules. In addition, it would be of interest to show the distribution of fluorophore separation (assessed with MINFLUX) of only the supercomplexes with two PSD95 molecules, since only these were used to calculate the average distance. 

The 13 nm distance was measured using MINFLUX, as stated in the text. The fluorophore separation distances are shown in Figure 1dii.

(5) In the introduction, the authors could be more explicit in their explanation of memory formation and storage and how the presented study contributes to that field. 

We thank the reviewer for the suggestion, but feel that such a discussion in the introduction would detract from the main points of the manuscript.  

(6) Throughout the manuscript the authors prominently cite their own work, but relevant literature on synaptic plasticity and synapse nanostructure (EM and super-resolution studies) is lacking. 

Further references have now been added.  

(7) The results depicted in Figure 4b would be easier to interpret if a stacked histogram (including error bars) was used. 

We agree that the data could be presented in such a way, but that would prevent the results from the biological repeats, along with the variation, being presented.

eLife assessment

This important study reports that a transcription factor stimulating mRNA synthesis can stabilize its target transcripts. The convincing results demonstrate, with multiple independent approaches, co-transcriptional binding, stabilization of a family of mRNAs, and cytoplasmic activities of the transcription factor Sfp1. The results lead to the conclusion that the co-transcriptional association of Sfp1 with specific transcripts is a critical step in the stabilization of such transcripts in the cytoplasm.

Reviewer #1 (Public Review):

This manuscript builds upon the authors' previous work on the cross-talk between transcription initiation and post-transcriptional events in yeast gene expression. These prior studies identified an mRNA 'imprinting' phenomenon linked to genes activated by the Rap1 transcription factor (TF), a surprising role for the Sfp1 TF in promoting RNA polymerase II (RNAPII) backtracking, and a role for the non-essential RNAPII subunits Rpb4/7 in the regulation of mRNA decay and translation. Here the authors aimed to extend these observations to provide a more coherent picture of the role of Sfp1 in transcription initiation and subsequent steps in gene expression. They provide evidence for (1) a physical interaction between Sfp1 and Rpb4, (2) Sfp1 binding and stabilization of mRNAs derived from genes whose promoters are bound by both Rap1 and Sfp1 and (3) an effect of Sfp1 on Rpb4 binding or conformation during transcription elongation.

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #2 (Public Review):

Summary:

The manuscript by Kelbert et al. presents results on the involvement of the yeast transcription factor Sfp1 in the stabilisation of transcripts whose synthesis it stimulates. Sfp1 is known to affect the synthesis of a number of important cellular transcripts, such as many of those that code for ribosomal proteins. The hypothesis that a transcription factor can remain bound to the nascent transcript and affect its cytoplasmic half-life is attractive. However, the association of Sfp1 with cytoplasmic transcripts remains to be validated, as explained in the following comments:

A two-hybrid based assay for protein-protein interactions identified Sfp1, a transcription factor known for its effects on ribosomal protein gene expression, as interacting with Rpb4, a subunit of RNA polymerase II. Classical two-hybrid experiments depend on the presence of the tested proteins in the nucleus of yeast cells, suggesting that the observed interaction occurs in the nucleus. Unfortunately, the two-hybrid method cannot determine whether the interaction is direct or mediated by nucleic acids. The revised version of the manuscript now states that the observed interaction could be indirect.

To understand to which RNA Sfp1 might bind, the authors used an N-terminally tagged fusion protein in a cross-linking and purification experiment. This method identified 264 transcripts for which the CRAC signal was considered positive and which mostly correspond to abundant mRNAs, including 74 ribosomal protein mRNAs or metabolic enzyme-abundant mRNAs such as PGK1. The authors did not provide evidence for the specificity of the observed CRAC signal, in particular what would be the background of a similar experiment performed without UV cross-linking. This is crucial, as Figure S2G shows very localized and sharp peaks for the CRAC signal, often associated with over-amplification of weak signal during sequencing library preparation.

(1) To rule out possible PCR artifacts, we used a UMI (Unique Molecular Identifier) scan. UMIs are short, random sequences added to each molecule by the 5’ adapter to uniquely tag them. After PCR amplification and alignment to the reference genome, groups of reads with identical UMIs represent only one unique original molecule. Thus, UMIs allow distinguishing between original molecules and PCR duplicates, effectively eliminating the duplicates.

(2) Looking closely at the peaks using the IGV browser, we noticed that the reads are by no means identical. Each carrying a mutation [probably due to the cross-linking] in a different position and having different length. Note that the reads are highly reproducible in two replicate.

(3) CRAC+ genes do not all fall into the category of highly transcribed genes.  On the contrary, as depicted in Figure 6A (green dots), it is evident that CRAC+ genes exhibit a diverse range of Rpb3 ChIP and GRO signals. Furthermore, as illustrated in Figure 7A, when comparing CRAC+ to Q1 (the most highly transcribed genes), it becomes evident that the Rpb4/Rpb3 profile of CRAC+ genes is not a result of high transcription levels.

(4) Only a portion of the RiBi mRNAs binds Sfp1, despite similar expression of all RiBi.

(5) The CRAC+ genes represent a distinct group with many unique features. Moreover, many CRAC+ genes do not fall into the category of highly transcribed genes.

(6) The biological significance of the 262 CRAC+ mRNAs was demonstrated by various experiments; all are inconsistent with technical flaws. Some examples are:

a) Fig. 2a and B show that most reads of CRAC+ mRNA were mapped to specific location – close the pA sites.

b) Fig. 2C shows that most reads of CRAC+ mRNA were mapped to specific RNA motif.

c) Most RiBi CRAC+ promoter contain Rap1 binding sites (p= 1.9x10-22), whereas the vast majority of RiBi CRAC- promoters do not contain Rap1 binding site. (Fig. 3C).

d) Fig. 4A shows that RiBi CRAC+ mRNAs become destabilized due to Sfp1 deletion, whereas RiBi CRAC- mRNAs do not. Fig. 4B shows similar results due to

e) Fig. 6B shows that the impact of Sfp1 on backtracking is substantially higher for CRAC+ than for CRAC- genes. This is most clearly visible in RiBi genes.

f) Fig. 7A shows that the Sfp1-dependent changes along the transcription units is substantially more rigorous for CRAC+ than for CRAC-.

g) Fig. S4B Shows that chromatin binding profile of Sfp1 is different for CRAC+ and CRAC- genes

In a validation experiment, the presence of several mRNAs in a purified SFP1 fraction was measured at levels that reflect the relative levels of RNA in a total RNA extract. Negative controls showing that abundant mRNAs not found in the CRAC experiment were clearly depleted from the purified fraction with Sfp1 would be crucial to assess the specificity of the observed protein-RNA interactions (to complement Fig. 2D).

GPP1, a highly expressed genes, is not to be pulled down by Sfp1 (Fig. 2D). GPP1 (alias RHR2) was included in our Table S2 as one of the 264 CRAC+ genes, having a low CRAC value. However, when we inspected GPP1 results using the IGV browser, we realized that the few reads mapped to GPP1 are actually anti-sense to GPP1 (perhaps they belong to the neighboring RPL34B genes, which is convergently transcribed to GPP1) (see Fig. 1 at the bottom of the document). Thus, GPP1 is not a CRAC+ gene and would now serve as a control. See  We changed the text accordingly (see page 11 blue sentences). In light of this observation, we checked other CRAC genes and found that, except for ALG2, they all contain sense reads (some contain both sense and anti-sense reads). ALG2 and GPP1 were removed leaving 262 CRAC+ genes.

The CRAC-selected mRNAs were enriched for genes whose expression was previously shown to be upregulated upon Sfp1 overexpression (Albert et al., 2019). The presence of unspliced RPL30 pre-mRNA in the Sfp1 purification was interpreted as a sign of co-transcriptional assembly of Sfp1 into mRNA, but in the absence of valid negative controls, this hypothesis would require further experimental validation. Also, whether the fraction of mRNA bound by Sfp1 is nuclear or cytoplasmic is unclear.

Further experimental validation was provided in some of our figures (e.g., Fig. 5C, Fig. 3B).

We argue that Sfp1 binds RNA co-transcriptionally and accompanies the mRNA till its demise in the cytoplasm: Co-transcriptional binding is shown in: (I) a drop in the Sfp1 ChIP-exo signal that coincides with the position of Sfp1 binding site in the RNA (Fig. 5C), demonstrating a movement of Sfp1 from chromatin to the transcript, (II) the dependence of Sfp1 RNA-binding on the promoter (Fig. 3B) and binding of intron-containing RNA. Taken together these 3 different experiments demonstrate that Sfp1 binds Pol II transcript co-transcriptionally.  Association of Sfp1 with cytoplasmic mRNAs is shown in the following experiments: (I) Figure 2D shows that Sfp1 pulled down full length RNA, strongly suggesting that these RNA are mature cytoplasmic mRNAs. (II) mRNA encoding ribosomal proteins, which belong to the CRAC+ mRNAs group are degraded by Xrn1 in the cytoplasm (Bresson et al., Mol Cell 2020). The capacity of Sfp1 to regulates this process (Fig. 4A-D) is therefore consistent with cytoplasmic activity of Sfp1. (III) The effect of Sfp1 on deadenylation (Fig. 4D), a cytoplasmic process, is also consistent with cytoplasmic activity of Sfp1. 

To address the important question of whether co-transcriptional assembly of Spf1 with transcripts could alter their stability, the authors first used a reporter system in which the RPL30 transcription unit is transferred to vectors under different transcriptional contexts, as previously described by the Choder laboratory (Bregman et al. 2011). While RPL30 expressed under an ACT1 promoter was barely detectable, the highest levels of RNA were observed in the context of the native upstream RPL30 sequence when Rap1 binding sites were also present. Sfp1 showed better association with reporter mRNAs containing Rap1 binding sites in the promoter region. Removal of the Rap1 binding sites from the reporter vector also led to a drastic decrease in reporter mRNA levels. Co-purification of reporter RNA with Sfp1 was only observed when Rap1 binding sites were included in the reporter. Negative controls for all the purification experiments might be useful.

In the swapping experiment, the plasmid lacking RapBS serves as the control for the one with RapBS and vice versa (see Bregman et al., 2011). Remember, that all these contracts give rise to identical RNA. Indeed, RabBS affects both mRNA synthesis and decay, therefore the controls are not ideal. However, see next section.

More importantly, in Fig. 3B “Input” panel, one can see that the RNA level of “construct F” was higher than the level of “construct E”. Despite this difference, only the RNA encoded by construct E was detected in the IP panel. This clearly shows that the detection of the RNA was not merely a result of its expression level.

To complement the biochemical data presented in the first part of the manuscript, the authors turned to the deletion or rapid depletion of SFP1 and used labelling experiments to assess changes in the rate of synthesis, abundance and decay of mRNAs under these conditions. An important observation was that in the absence of Sfp1, mRNAs encoding ribosomal protein genes not only had a reduced synthesis rate, but also an increased degradation rate. This important observation needs careful validation,

Indeed, we do provide validations in Fig. 4C Fig. 4D Fig. S3A and during the revision we included an  additional validation as Fig. S3B. Of note, we strongly suspect that GRO is among the most reliable approaches to determine half-lives (see our response in the first revision letter).

As genomic run-on experiments were used to measure half-lives, and this particular method was found to give results that correlated poorly with other measures of half-life in yeast (e.g. Chappelboim et al., 2022 for a comparison). As an additional validation, a temperature shift to 42{degree sign}C was used to show that , for specific ribosomal protein mRNA, the degradation was faster, assuming that transcription stops at that temperature. It would be important to cite and discuss the work from the Tollervey laboratory showing that a temperature shift to 42{degree sign}C leads to a strong and specific decrease in ribosomal protein mRNA levels, probably through an accelerated RNA degradation (Bresson et al., Mol Cell 2020, e.g. Fig 5E).

This was cited. Thank you. 

Finally, the conclusion that mRNA deadenylation rate is altered in the absence of Sfp1, is difficult to assess from the presented results (Fig. 3D).

This type of experiment was popular in the past. The results in the literature are similar to ours (in fact, ours are nicer). Please check the papers cited in our MS and a number of papers by Roy Parker.

The effects of SFP1 on transcription were investigated by chromatin purification with Rpb3, a subunit of RNA polymerase, and the results were compared with synthesis rates determined by genomic run-on experiments. The decrease in polII presence on transcripts in the absence of SFP1 was not accompanied by a marked decrease in transcript output, suggesting an effect of Sfp1 in ensuring robust transcription and avoiding RNA polymerase backtracking. To further investigate the phenotypes associated with the depletion or absence of Sfp1, the authors examined the presence of Rpb4 along transcription units compared to Rpb3. An effect of spf1 deficiency was that this ratio, which decreased from the start of transcription towards the end of transcripts, increased slightly. To what extent this result is important for the main message of the manuscript is unclear.

Suggestions: a) please clearly indicate in the figures when they correspond to reanalyses of published results.

This was done.

b) In table S2, it would be important to mention what the results represent and what statistics were used for the selection of "positive" hits. 

This was discussed in the text.

Strengths:

- Diversity of experimental approaches used.

- Validation of large-scale results with appropriate reporters.

Weaknesses:

- Lack of controls for the CRAC results and lack of negative controls for the co-purification experiments that were used to validate specific mRNA targets potentially bound by Sfp1.

- Several conclusions are derived from complex correlative analyses that fully depend on the validity of the aforementioned Sfp1-mRNA interactions.

We hope that our responses to Reviewer 2's thoughtful comments have rulled out concerns regarding the lack of controls.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Please review the text for spelling errors. While not mandatory, wig or begraph files for the CRAC results would be very useful for the readers.

Author response image 1.

A snapshot of IGV GPP1 locus showing that all the reads are anti-sense (pointing at the opposite direction of the gene (the gene arrows [white arrows over blue, at the bottom] are pointing to the right whereas the reads’ orientations are pointing to the left).

Author response:

The following is the authors’ response to the current reviews.

The concerns raised during the review have been incorporated into the discussion of the results, and the need for further research is acknowledged in the paper. This is not possible in the present study, as the clinical project has been completed and further patients cannot be enrolled without starting a new project. We are confident that the results are scientifically valid and that the methodology was scientifically sound and up to date. They were obtained on a dataset that was obviously large enough to allow 20% of it to be set aside and a machine-learned classifier to be trained on the remaining 80%, which then assigned samples to neuropathy with an accuracy better than guessing.

Furthermore, our results are at least tentatively replicated in a completely independent data set from another patient cohort. The strengths and limitations of the study design, in particular the latter, are discussed in the necessary depth. In summary, the machine-learned results provided major hits on one side and probably unimportant lipids on the other side of the variable importance scale. Both could be verified in vitro. We are therefore confident that we have contributed to the advancement of knowledge about cancer therapy-associated neuropathy and look forward to further developments in this area.

---

The following is the authors’ response to the original reviews.

Weaknesses Reviewer 1: 

There are a number of weaknesses in the study. The small sample size is a significant limitation of the study. Out of 31 patients, only 17 patients were reported to develop neuropathy, with significant neuropathy (grade 2/3) in only 5 patients. The authors acknowledge this limitation in the results and discussion sections of the manuscript, but it limits the interpretation of the results. Also acknowledged is the limited method used to assess neuropathy. 

We agree with the reviewer that the cohort size and assessment of neuropathy are limitations of our study as we already described in the corresponding section of the manuscript. However, occurrence and grade of the neuropathy are in line with results reported from previous studies. From these studies, the expected occurrence of neuropathy with our therapeutic regimen is around 50-70% (54.9% in our cohort), and most patients (80-90%) are expected to experience Grade 1 neuropathy after 12 weeks (13). In these studies, neuropathy is assessed by using questionnaires or by grading via NCTCTCAE as in our study. In summary, assessment and occurrence of neuropathy of our reported cohort are in line with previous reports.

Potentially due to this small number of patients with neuropathy, the machine learning algorithms could not distinguish between samples with and without neuropathy. Only selected univariate analyses identified differences in lipid profiles potentially related to neuropathy.  

The data analysis consistently followed a "mixture of experts" approach, as this seems to be the most successful way to deal with omics data. We have elaborated on this in the Methods section, including several supporting references. Regarding the quoted sentence from the results section, after rereading it, we realized that it was somewhat awkwardly worded. What we mean is now better worded in the results section, namely “Although the three algorithms detected neuropathy in new cases, unseen during training, at balanced accuracy of up to 0.75, while only the guess level of 0.5 was achieved when using permuted data for training, the 95% CI of the performance measures was not separated from guess level”. Therefore, multivariate feature selection was not considered a valid approach, since it requires that the algorithms from which the feature importance is read can successfully perform their task of class assignment (4). Therefore, univariate methods (Cohen's d, FPR, FWE) were preferred, as well as a direct hypothesis transfer of the top hits from the abovementioned day1/2 assessments to neuropathy. Classical statistics consisting of direct group comparisons using Kruskal-Wallis tests (5) were performed.” 

It was our approach to investigate the data set in an unbiased manner by different machine learning algorithms and select those lipids that the majority of the algorithms considered important for distinguishing the patient groups (majority voting). This way, the inconsistencies and limitations of a single evaluation method, such as regression analysis, that occur in some datasets, can be mitigated. 

Three sphingolipid mediators including SA1P differed between patients with and without neuropathy at the end of treatment. These sphingolipids were elevated at the end of treatment in the cohort with neuropathy, relative to those without neuropathy. However, across all samples from pre to post-paclitaxel treatment, there was a significant reduction in SA1P levels. It is unclear from the data presented what the underlying mechanism for this result would be. 

We agree with the reviewer that our study does not identify the mechanism by which paclitaxel treatment alters sphingolipid concentrations in the plasma of patients. It has been reported before that paclitaxel may increase expression and activity of serine palmitoyltransferase (SPT) which is the crucial enzyme and rate-limiting step in the denovo synthesis of sphingolipids. This may be associated with a shift towards increased synthesis of 1-deoxysphingolipids and a decrease of “classical” sphingolipids (6) and may explain the general reduction of SA1P and other sphingolipid levels after paclitaxel treatment in our study. 

It is also conceivable that paclitaxel reduces the release of sphingolipids into the plasma. Paclitaxel is a microtubule stabilizing agent (7) that may interfere with intracellular transport processes and release of paracrine mediators. 

The mechanistic details of paclitaxel involvement in sphingolipid metabolism or transport are highly interesting but identifying them is beyond the scope of our manuscript.

If elevated SA1P is associated with neuropathy development, it would be expected to increase in those who develop neuropathy from pre to post-treatment time points. 

There is a general trend of reduced plasma SA1P concentrations following paclitaxel treatment. Nevertheless, patients experiencing neuropathy exhibit significantly elevated SA1P levels post-treatment. 

It has been shown before that paclitaxel-induced neuropathic pain requires activation of the S1P1 receptor in a preclinical study (8). Moreover, a meta-analysis of genome-wide association studies (GWAS) from two clinical cohorts identified multiple regulatory elements and increased activity of S1PR1 associated with paclitaxel-induced neuropathy (9). These data imply that enhanced S1P receptor activity and signaling are key drivers of paclitaxel-induced neuropathy. It seems that both, increased levels of the sphingolipid ligands in combination with enhanced expression and activity of S1P receptors can potentiate paclitaxel-induced neuropathy in patients. This explains why also decreased SA1P concentrations after paclitaxel treatment can still enhance neuropathy via the S1PRTRPV1 axis in sensory neurons.

We added this paragraph to the discussions section of our manuscript.

Primary sensory neuron cultures were used to examine the effects of SA1P application.

SA1P application produced calcium transients in a small proportion of sensory neurons. It is not clear how this experimental model assists in validating the role of SA1P in neuropathy development as there is no assessment of sensory neuron damage or other hallmarks of peripheral neuropathy. These results demonstrate that some sensory neurons respond to SA1P and that this activity is linked to TRPV1 receptors. However, further studies will be required to determine if this is mechanistically related to neuropathy.

As we detected elevated levels of SA1P in the plasma of PIPN patients, we can assume higher concentrations in the vicinity of sensory neurons. These neurons are the main drivers for neuropathy and neuropathic pain and are strongly affected by paclitaxel in their activity (10-15). Also, TRPV1 shows altered activity patterns in response to paclitaxel treatment (16). Because of its relevance for nociception and pathological pain, TRPV1 activity is a suitable and representative readout for pathological pain states in peripheral sensory neurons (17, 18), which is why we investigated them.

We would like to point out the potency of SA1P to increase capsaicin-induced calciumtransients in sensory neurons at submicromolar concentrations. 

We also agree with the reviewer that further studies need to investigate the underlying mechanisms in more detail. We added this sentence to the final paragraph in the discussion section of our manuscript.

Weaknesses Reviewer 2: 

The article is poorly written, hindering a clear understanding of core results. While the study's goals are apparent, the interpretation of sphingolipids, particularly SA1P, as key mediators of paclitaxel-induced neuropathy lacks robust evidence. 

We agree that the relevance of SA1P as key mediator of paclitaxel-induced neuropathy might be overstated and changed the wording throughout the manuscript accordingly. However, we would like to point out the potency of this lipid to increase capsaicin-induced calcium-transients in sensory neurons at submicromolar concentrations. 

Also, the lipid signature in the plasma of PIPN patients shows a unique pattern and sphingolipids are the group that showed the strongest alterations when comparing the patient groups. We also measured eicosanoids, such as prostaglandins, linoleic acid metabolites, endocannabinoids and other lipid groups that have previously been associated with influences on pain perception or nociceptor sensitization. However, none of these lipids showed significant differences in their concentrations in patient plasma. This is why we consider sphingolipids as contributors to or markers of paclitaxel-induced neuropathy in patients.

We also revised the entire article to improve its clarity.

The introduction fails to establish the significance of general neuropathy or peripheral neuropathy in anticancer drug-treated patients, and crucial details, such as the percentage of patients developing general neuropathy or peripheral neuropathy, are omitted. This omission is particularly relevant given that only around 50% of patients developed neuropathy in this study, primarily of mild Grade 1 severity with negligible symptoms, contradicting the study's assertion of CIPN as a significant side effect. 

As we already described in the introduction, CIPN is a serious dose- and therapy-limiting side effect, which affects up to 80% of treated patients. This depends on dose and combination of chemotherapeutic agents. For paclitaxel, therapeutic doses range from 80 – 225 mg/m². As CIPN symptoms are dose-dependent, the number of PIPN patients that receive a high paclitaxel dose is higher than the number of PIPN patient receiving a low dose.

In our study, we mainly used a low dose paclitaxel, because this therapeutic regimen is the most widely used paclitaxel monotherapy. From previous studies, the expected occurrence of neuropathy with this therapeutic regimen is around 50-70%, and most patients (8090%) are expected to experience Grade 1 neuropathy after 12 weeks (1-3).

Our results are within the range reported by these studies (54.9% patients with neuropathy). Also, as we highlight in Table S1, the neuropathy symptoms persist in most cases for several years after chemotherapy, affecting quality of life of these patients which makes it far from being a negligible symptom.

We added some more information concerning PIPN in the introduction section in which we emphasize the clinical problem.

The lack of clarity in distinguishing results obtained by lipidomics using machine learning methods and conventional methods adds to the confusion. The poorly written results section fails to specify SA1P's downregulation or upregulation, and the process of narrowing down to sphingolipids and SA1P is inadequately explained. 

We have tried to keep the machine learning part in the main manuscript short and moved major parts of it to a supplement. However, as this has been claimed to have led to a lack of clarity, we have expanded the description of the data analysis and added extensive explanations and supporting references for the mixed expert approach that was used throughout the analysis. We hope this is now clear.

Integrating a significant portion of the discussion section into the results section could enhance clarity. An explanation of the utility of machine learning in classifying patient groups over conventional methods and the citation of original research articles, rather than relying on review articles, may also add clarity to the usefulness of the study. 

As suggested by the reviewer, we moved the relevant parts from the discussion to the results section in the revised version of our manuscript.

Reviewer #1 (Recommendations For The Authors): 

Figure 2 should be better explained or removed. In its current form, it does not add to the interpretation of the manuscript.  

As mentioned above, we have expanded the description of the ESOM/U-matrix method in the Methods section and rewritten the figure legend. In addition, we have annotated the U-matrix in the figure. The method has been reported extensively in the computer science and biomedical literature, and a more detailed description in the referenced papers would go beyond the current focus on lipidomics. However, we believe that this discussion is sufficiently detailed for the readers of this report: "… a second unsupervised approach was used to verify the agreement between the lipidomics data structure and the prior classification, implemented as self-organizing maps (SOM) of artificial neurons (19). In the special form of an “emergent” SOM (ESOM (20)), the present map consisted of 4,000 neurons arranged on a two-dimensional toroidal grid with 50 rows and 80 columns (21, 22). ESOM was used because it has been repeatedly shown to correctly detect subgroup structures in biomedical data sets comparable to the present one (20, 22, 23). The core principle of SOM learning is to adjust the weights of neurons based on their proximity to input data points. In this process, the best matching unit (BMU) is identified as the neuron closest to a given data point. The adaptation of the weights is determined by a learning rate (η) and a neighborhood function (h), both of which gradually decrease during the learning process. Finally, the groups are projected onto separate regions of the map. On top of the trained ESOM, the distance structure in the high-dimensional feature space was visualized in the form of a so-called U-matrix (24) which is the canonical tool for displaying the distance structures of input data on ESOM (21). 

The visual presentation facilitates data group separation by displaying the distances between BMUs in high-dimensional space in a color-coding that uses a geographical map analogy, where large "heights" represent large distances in feature space, while low "valleys" represent data subsets that are similar. "Mountain ranges" with "snow-covered" heights visually separate the clusters in the data. Further details about ESOM can be found in (24)."

The second patient cohort is only included in the discussion - with cohort details in the supplementary material and figures included in the main text. Perhaps these data should be removed entirely. The findings are described as trends and not statistically significant and multiple issues with this second cohort are mentioned in the discussion. 

We agree with the reviewer that including the second patient cohort in the discussion is inadequate. Of course, there are differences between the patient cohorts that do not allow direct comparison and that are highlighted in the section on limitations of the study. However, we still think it is interesting and relevant to show these data, because we used our algorithms trained on the first patient cohort to analyze the second cohort. And these data support the main results. 

We therefore moved the entire paragraph to the results section of to improve coherence of our manuscript. The passage was introduced with the subheading:  “Support of the main results in an independent second patient cohort”.

The title does not reflect the content of the paper and should be changed to better reflect the content and its significance. 

We change the title to “Machine learning and biological validation identify sphingolipids as potential mediators of paclitaxel-induced neuropathy in cancer patients” to avoid overstating the results as suggested by the Reviewer.

Further, the discussion should be modified to avoid overstating the results. 

As the reviewer suggests, we changed the wording to avoid overstating the results. 

Reviewer #2 (Recommendations For The Authors): 

Please address the absence of clear neuropathy in the majority of patients after treatment with paclitaxel in your discussion. 

As stated above, occurrence and grade of the neuropathy are in line with the results from previous studies. From these studies, the expected occurrence of neuropathy with our therapeutic regimen is around 50-70%, (the variability is due to differences in the assessment methods) and most patients (80-90%) are expected to experience Grade 1 neuropathy after 12 weeks (1-3). 

We added this information in the discussion section of the revised manuscript.

Line 65: Kindly replace review articles with original research articles for proper citation. 

We replaced the review articles with original publications, focusing on clinical observations. We added the following publications: Jensen et al., Front Neurosci 2020; Chen et al., Neurobiol Aging 2018; Igarashi et al., J Alzheimers Dis. 2011; Kim et al., Oncotarget 2017 as references 17-20 in the revised version of our manuscript.

Line 260: The mention of SA1P is introduced here without prior reference (do not use words like "again", or "see above", if it is not previously mentioned). Adjust the text for coherence.

We agree with the reviewer that the introduction of SA1P in this passage in incoherent. We replaced the sentence in line 260 with: 

The small set of lipid mediators emerging from all three methods as informative for neuropathy included the sphingolipid sphinganine-1-phosphate (SA1P), also known as dihydrosphingosine-1-phosphate (DH-S1P)…”

Lines 301-315: Consider relocating several lines from this section to the results section for improved clarity. 

We moved the lines 309-312 explaining the algorithm selection and their validation success in the corresponding results section (Lipid mediators informative for assigning postpaclitaxel therapy samples to neuropathy).

Lines 382-396: Move this content to the results section to enhance the organization and coherence of the manuscript. 

We moved the entire paragraph to the results section of our manuscript to improve coherence. The passage was introduced with the subheading:  “Support of the main results in an independent second patient cohort”.

References

(1) Barginear M, Dueck AC, Allred JB, Bunnell C, Cohen HJ, Freedman RA, et al. Age and the Risk of Paclitaxel-Induced Neuropathy in Women with Early-Stage Breast Cancer (Alliance A151411): Results from 1,881 Patients from Cancer and Leukemia Group B (CALGB) 40101. Oncologist. 2019;24(5):617-23.

(2) Mauri D, Kamposioras K, Tsali L, Bristianou M, Valachis A, Karathanasi I, et al. Overall survival benefit for weekly vs. three-weekly taxanes regimens in advanced breast cancer: A metaanalysis. Cancer Treat Rev. 2010;36(1):69-74.

(3) Budd GT, Barlow WE, Moore HC, Hobday TJ, Stewart JA, Isaacs C, et al. SWOG S0221: a phase III trial comparing chemotherapy schedules in high-risk early-stage breast cancer. J Clin Oncol. 2015;33(1):58-64.

(4) Lötsch J, and Ultsch A. Pitfalls of Using Multinomial Regression Analysis to Identify ClassStructure-Relevant Variables in Biomedical Data Sets: Why a Mixture of Experts (MOE) Approach Is Better. BioMedInformatics. 2023;3(4):869-84.

(5) Kruskal WH, and Wallis WA. Use of Ranks in One-Criterion Variance Analysis. J Am Stat Assoc. 1952;47(260):583-621.

(6) Kramer R, Bielawski J, Kistner-Griffin E, Othman A, Alecu I, Ernst D, et al. Neurotoxic 1deoxysphingolipids and paclitaxel-induced peripheral neuropathy. FASEB J. 2015;29(11):4461-72.

(7) Field JJ, Diaz JF, and Miller JH. The binding sites of microtubule-stabilizing agents. Chem Biol. 2013;20(3):301-15.

(8) Janes K, Little JW, Li C, Bryant L, Chen C, Chen Z, et al. The development and maintenance of paclitaxel-induced neuropathic pain require activation of the sphingosine 1-phosphate receptor subtype 1. J Biol Chem. 2014;289(30):21082-97.

(9) Chua KC, Xiong C, Ho C, Mushiroda T, Jiang C, Mulkey F, et al. Genomewide Meta-Analysis Validates a Role for S1PR1 in Microtubule Targeting Agent-Induced Sensory Peripheral Neuropathy. Clin Pharmacol Ther. 2020;108(3):625-34.

(10) Kawakami K, Chiba T, Katagiri N, Saduka M, Abe K, Utsunomiya I, et al. Paclitaxel increases high voltage-dependent calcium channel current in dorsal root ganglion neurons of the rat. J Pharmacol Sci. 2012;120(3):187-95.

(11) Pittman SK, Gracias NG, Vasko MR, and Fehrenbacher JC. Paclitaxel alters the evoked release of calcitonin gene-related peptide from rat sensory neurons in culture. Exp Neurol. 2013.

(12) Luo H, Liu HZ, Zhang WW, Matsuda M, Lv N, Chen G, et al. Interleukin-17 Regulates NeuronGlial Communications, Synaptic Transmission, and Neuropathic Pain after Chemotherapy.

Cell reports. 2019;29(8):2384-97 e5.

(13) Pease-Raissi SE, Pazyra-Murphy MF, Li Y, Wachter F, Fukuda Y, Fenstermacher SJ, et al. Paclitaxel Reduces Axonal Bclw to Initiate IP3R1-Dependent Axon Degeneration. Neuron. 2017;96(2):373-86 e6.

(14) Duggett NA, Griffiths LA, and Flatters SJL. Paclitaxel-induced painful neuropathy is associated with changes in mitochondrial bioenergetics, glycolysis, and an energy deficit in dorsal root ganglia neurons. Pain. 2017.

(15) Li Y, Adamek P, Zhang H, Tatsui CE, Rhines LD, Mrozkova P, et al. The Cancer Chemotherapeutic Paclitaxel Increases Human and Rodent Sensory Neuron Responses to TRPV1 by Activation of TLR4. J Neurosci. 2015;35(39):13487-500.

(16) Hara T, Chiba T, Abe K, Makabe A, Ikeno S, Kawakami K, et al. Effect of paclitaxel on transient receptor potential vanilloid 1 in rat dorsal root ganglion. Pain. 2013;154(6):882-9.

(17) Jardin I, Lopez JJ, Diez R, Sanchez-Collado J, Cantonero C, Albarran L, et al. TRPs in Pain Sensation. Front Physiol. 2017;8:392.

(18) Julius D. TRP Channels and Pain. Annual review of cell and developmental biology.

2013;29:355-84.

(19) Kohonen T. Self-Organized Formation of Topologically Correct Feature Maps. Biol Cybern. 1982;43(1):59-69.

(20) Lötsch J, Lerch F, Djaldetti R, Tegder I, and Ultsch A. Identification of disease-distinct complex biomarker patterns by means of unsupervised machine-learning using an interactive R toolbox (Umatrix). Big Data Analytics. 2018;3(1):5.

(21) Ultsch A. 2003.

(22) Lotsch J, Geisslinger G, Heinemann S, Lerch F, Oertel BG, and Ultsch A. Quantitative sensory testing response patterns to capsaicin- and ultraviolet-B-induced local skin hypersensitization in healthy subjects: a machine-learned analysis. Pain. 2018;159(1):11-24.

(23) Lötsch J, Thrun M, Lerch F, Brunkhorst R, Schiffmann S, Thomas D, et al. Machine-Learned Data Structures of Lipid Marker Serum Concentrations in Multiple Sclerosis Patients Differ from Those in Healthy Subjects. Int J Mol Sci. 2017;18(6).

(24) Lötsch J, and Ultsch A. Cham: Springer International Publishing; 2014:249-57.

eLife assessment

The manuscript presents a potentially important strategy to stimulate mammalian Müller glia to proliferate in vivo by manipulating cell cycle components. The findings are likely to appeal to retinal specialists and neuroscientists in general. However, the evidence that these cells become neurogenic is lacking/incomplete, suggesting that additional barriers exist to stimulate the regeneration of retinal neurons.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Wu et al. introduce a novel approach to reactivate the Muller glia cell cycle in the mouse retina by simultaneously reducing p27Kip1 and increasing cyclin D1 using a single AAV vector. The approach effectively promotes Muller glia proliferation and reprograming without disrupting retinal structure or function. Interestingly, reactivation of the Muller glia cell cycle downregulates IFN pathway, which may contribute to the induced retinal regeneration. The results presented in this manuscript may offer a promising approach for developing Müller glia cell-mediated regenerative therapies for retinal diseases.

Strengths:

The data are convincing and supported by appropriate, validated methodology. These results are both technically and scientifically exciting and are likely to appeal to retinal specialists and neuroscientists in general.

Weaknesses:

There are some data gaps that need to be addressed.

(1) Please label the time points of AAV injection, EdU labeling, and harvest in Figure 1B.

(2) What fraction of Müller cells were transduced by AAV under the experimental conditions?

(3) It seems unusually rapid for MG proliferation to begin as early as the third day after CCA injection. Can the authors provide evidence for cyclin D1 overexpression and p27 Kip1 knockdown three days after CCA injection?

(4) The authors reported that MG proliferation largely ceased two weeks after CCA treatment. While this is an interesting finding, the explanation that it might be due to the dilution of AAV episomal genome copies in the dividing cells seems far-fetched.

Reviewer #2 (Public Review):

This manuscript by Wu, Liao et al. reports that simultaneous knockdown of P27Kip1 with overexpression of Cyclin D can stimulate Muller glia to re-enter the cell cycle in the mouse retina. There is intense interest in reprogramming mammalian muller glia into a source for neurogenic progenitors, in the hopes that these cells could be a source for neuronal replacement in neurodegenerative diseases. Previous work in the field has shown ways in which mouse Muller glia can be neurogenically reprogrammed and these studies have shown cell cycle re-entry prior to neurogenesis. In other works, typically, the extent of glial proliferation is limited, and the authors of this study highlight the importance of stimulating large numbers of Muller glia to re-enter the cell cycle with the hopes they will differentiate into neurons. While the evidence for stimulating proliferation in this study is convincing, the evidence for neurogenesis in this study is not convincing or robust, suggesting that stimulating cell cycle-reentry may not be associated with increasing regeneration without another proneural stimulus.

Below are concerns and suggestions.

Intro:

(1) The authors cite past studies showing "direct conversion" of MG into neurons. However, these studies (PMID: 34686336; 36417510) show EdU+ MG-derived neurons suggesting cell cycle re-entry does occur in these strategies of proneural TF overexpression.

(2) Multiple citations are incorrectly listed, using the authors first name only (i.e. Yumi, et al; Levi, et al;). Studies are also incompletely referenced in the references.

Figure 1:<br /> (3) When are these experiments ending? On Figure 1B it says "analysis" on the end of the paradigm without an actual day associated with this. This is the case for many later figures too. The authors should update the paradigms to accurately reflect experimental end points.

(4) Are there better representative pictures between P27kd and CyclinD OE, the EdU+ counts say there is a 3 fold increase between Figure 1D&E, however the pictures do not reflect this. In fact, most of the Edu+ cells in Figure 1E don't seem to be Sox9+ MG but rather horizontally oriented nuclei in the OPL that are likely microglia.

(5) Is the infection efficacy of these viruses different between different combinations (i.e. CyclinD OE vs. P27kd vs. control vs. CCA combo)? As the counts are shown in Figure 1G only Sox9+/Edu+ cells are shown not divided by virus efficacy. If these are absolute counts blind to where the virus is and how many cells the virus hits, if the virus efficacy varies in efficiency this could drive absolute differences that aren't actually biological.

(6) According to the Jax laboratories, mice aren't considered aged until they are over 18months old. While it is interesting that CCA treatment does not seem to lose efficacy over maturation I would rephrase the findings as the experiment does not test this virus in aged retinas.

(7) Supplemental Figure 2c-d. These viruses do not hit 100% of MG, however 100% of the P27Kip staining is gone in the P27sh1 treatment, even the P27+ cell in the GCL that is likely an astrocyte has no staining in the shRNA 1 picture. Why is this?

Figure 2<br /> (8) Would you expect cells to go through two rounds of cell cycle in such a short time? The treatment of giving Edu then BrdU 24 hours later would have to catch a cell going through two rounds of division in a very short amount of time. Again the end point should be added graphically to this figure.

Figure 3<br /> (9) I am confused by the mixing of ratios of viruses to indicate infection success. I know mixtures of viruses containing CCA or control GFP or a control LacZ was injected. Was the idea to probe for GFP or LacZ in the single cell data to see which cells were infected but not treated? This is not shown anywhere?

(10) The majority of glia sorted from TdTomato are probably not infected with virus. Can you subset cells that were infected only for analysis? Otherwise it makes it very hard to make population judgements like Figure 3E-H if a large portion are basically WT glia.

(11) Figure 3C you can see Rho is expressed everywhere which is common in studies like this because the ambient RNA is so high. This makes it very hard to talk about "Rod-like" MG as this is probably an artifact from the technique. Most all scRNA-seq studies from MG-reprogramming have shown clusters of "rods" with MG hybrid gene expression and these had in the past just been considered an artifact.

(12) It is mentioned the "glial" signature is downregulated in response to CCA treatment. Where is this shown convincingly? Figure H has a feature plot of Glul , which is not clear it is changed between treatments. Otherwise MG genes are shown as a function of cluster not treatment.

Figure 4<br /> (13) The authors should be commended for being very careful in their interpretations. They employ the proper controls (Er-Cre lineage tracing/EdU-pulse chasing/scRNA-seq omics) and were very careful to attempt to see MG-derived rods. This makes the conclusion from the FISH perplexing. The few puncta dots of Rho and GNAT in MG are not convincing to this reviewer, Rho and GNAT dots are dense everywhere throughout the ONL and if you drew any random circle in the ONL it would be full of dots. The rigor of these counts also comes into question because some dots are picked up in MG in the INL even in the control case. This is confusing because baseline healthy MG do not express RNA-transcripts of these Rod genes so what is this picking up? Taken together, the conclusion that there are Rod-like MG are based off scRNA-seq data (which is likely ambient contamination) and these FISH images. I don't think this data warrants the conclusion that MG upregulate Rod genes in response to CCA.

Figure 5<br /> (14) Similar point to above but this Glul probe seems odd, why is it throughout the ONL but completely dark through the IPL, this should also be in astrocytes can you see it in the GCL? These retinas look cropped at the INL where below is completely black. The whole retinal section should be shown. Antibodies exist to GS that work in mouse along with many other MG genes, IHC or western blots could be done to better serve this point.

Figure 6<br /> (15) Figure 6D is not a co-labeled OTX2+/ TdTomato+ cell, Otx2 will fill out the whole nucleus as can be seen with examples from other MG-reprogramming papers in the field (Hoang, et al. 2020; Todd, et al. 2020; Palazzo, et al. 2022). You can clearly see in the example in Figure 6D the nucleus extending way beyond Otx2 expression as it is probably overlapping in space. Other examples should be shown, however, considering less than 1% of cells were putatively Otx2+, the safer interpretation is that these cells are not differentiating into neurons. At least 99.5% are not.

(16) Same as above Figure 6I is not convincingly co-labeled HuC/D is an RNA-binding protein and unfortunately is not always the clearest stain but this looks like background haze in the INL overlapping. Other amacrine markers could be tested, but again due to the very low numbers, I think no neurogenesis is occurring.

(17) In the text the authors are accidently referring to Figure 6 as Figure 7.

Figure 7<br /> (18) I like this figure and the concept that you can have additional MG proliferating without destroying the retina or compromising vision. This is reminiscent of the chick MG reprogramming studies in which MG proliferate in large numbers and often do not differentiate into neurons yet still persist de-laminated for long time points.

General:<br /> (19) The title should be changed, as I don't believe there is any convincing evidence of regeneration of neurons. Understanding the barriers to MG cell-cycle re-entry are important and I believe the authors did a good job in that respect, however it is an oversell to report regeneration of neurons from this data.

(20) This paper uses multiple mouse lines and it is often confusing when the text and figures switch between models. I think it would be helpful to readers if the mouse strain was added to graphical paradigms in each figure when a different mouse line is employed.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Wu et al. introduce a novel approach to reactivate the Muller glia cell cycle in the mouse retina by simultaneously reducing p27Kip1 and increasing cyclin D1 using a single AAV vector. The approach effectively promotes Muller glia proliferation and reprograming without disrupting retinal structure or function. Interestingly, reactivation of the Muller glia cell cycle downregulates IFN pathway, which may contribute to the induced retinal regeneration. The results presented in this manuscript may offer a promising approach for developing Müller glia cell-mediated regenerative therapies for retinal diseases.

Strengths:

The data are convincing and supported by appropriate, validated methodology. These results are both technically and scientifically exciting and are likely to appeal to retinal specialists and neuroscientists in general.

Weaknesses:

There are some data gaps that need to be addressed.

(1) Please label the time points of AAV injection, EdU labeling, and harvest in Figure 1B.

We thank the reviewer for highlighting the lack of clarity in our experimental design. We will label all experiment timelines in the figures where appropriate in the revised version.

(2) What fraction of Müller cells were transduced by AAV under the experimental conditions?

We apologize for not clearly conveying the transduction efficiency. The retinal region adjacent to the injection site, typically near the central retina, exhibits a transduction efficiency of nearly 100%. In contrast, the peripheral retina shows a lower transduction efficiency compared to the central region. We will include the quantification of AAV transduction efficiency in the revised manuscript.

The quantification of Edu+ MG or other markers was conducted in the area with the highest efficiency. 

(3) It seems unusually rapid for MG proliferation to begin as early as the third day after CCA injection. Can the authors provide evidence for cyclin D1 overexpression and p27 Kip1 knockdown three days after CCA injection?

In our pilot study, we tested the onset time of GFP expression from AAV-GFAP-GFP following intravitreal injection. We observed GFP expression in MG as early as two days post-infection. These findings will be included in the revised manuscript. Additionally, we plan to perform qPCR or Western blot analysis to confirm cyclin D1 overexpression and p27kip1 knockdown at the onset of Müller glia proliferation, which will also be included in the revised manuscript.

(4) The authors reported that MG proliferation largely ceased two weeks after CCA treatment. While this is an interesting finding, the explanation that it might be due to the dilution of AAV episomal genome copies in the dividing cells seems far-fetched.

We believe that the lack of durability in high Cyclin D1 and low p27kip1 levels in MG contributes to the cessation of their proliferation. A potential reason for the loss of high Cyclin D1 overexpression and p27kip1 knockdown during MG proliferation could be the dilution of the AAV episomal genome. However, testing this hypothesis is challenging. Instead, we plan to provide direct evidence in the revised manuscript by examining the levels of Cyclin D1 and p27kip1 in the retina treated with CCA before and after the peak of MG proliferation.

Reviewer #2 (Public Review):

This manuscript by Wu, Liao et al. reports that simultaneous knockdown of P27Kip1 with overexpression of Cyclin D can stimulate Muller glia to re-enter the cell cycle in the mouse retina. There is intense interest in reprogramming mammalian muller glia into a source for neurogenic progenitors, in the hopes that these cells could be a source for neuronal replacement in neurodegenerative diseases. Previous work in the field has shown ways in which mouse Muller glia can be neurogenically reprogrammed and these studies have shown cell cycle re-entry prior to neurogenesis. In other works, typically, the extent of glial proliferation is limited, and the authors of this study highlight the importance of stimulating large numbers of Muller glia to re-enter the cell cycle with the hopes they will differentiate into neurons. While the evidence for stimulating proliferation in this study is convincing, the evidence for neurogenesis in this study is not convincing or robust, suggesting that stimulating cell cycle-reentry may not be associated with increasing regeneration without another proneural stimulus.

Below are concerns and suggestions.

Intro:

(1) The authors cite past studies showing "direct conversion" of MG into neurons. However, these studies (PMID: 34686336; 36417510) show EdU+ MG-derived neurons suggesting cell cycle re-entry does occur in these strategies of proneural TF overexpression.

We thank the reviewer for pointing this out. We will revise the statement to "MG neurogenesis," which encompasses both direct conversion and Müller glia proliferation followed by neuronal differentiation.

(2) Multiple citations are incorrectly listed, using the authors first name only (i.e. Yumi, et al; Levi, et al;). Studies are also incompletely referenced in the references.

We apologize for the mistake with the reference. We will fix these mistakes in the revised version.

Figure 1:

(3) When are these experiments ending? On Figure 1B it says "analysis" on the end of the paradigm without an actual day associated with this. This is the case for many later figures too. The authors should update the paradigms to accurately reflect experimental end points.

We thank the reviewer for highlighting the lack of clarity in our experimental design. We will label all experiment timelines in the figures where appropriate in the revised version.

(4) Are there better representative pictures between P27kd and CyclinD OE, the EdU+ counts say there is a 3 fold increase between Figure 1D&E, however the pictures do not reflect this. In fact, most of the Edu+ cells in Figure 1E don't seem to be Sox9+ MG but rather horizontally oriented nuclei in the OPL that are likely microglia.

Thanks to the reviewer for pointing this out. We will replace the image of Cyclin D1 which a better representative image.

(5) Is the infection efficacy of these viruses different between different combinations (i.e. CyclinD OE vs. P27kd vs. control vs. CCA combo)? As the counts are shown in Figure 1G only Sox9+/Edu+ cells are shown not divided by virus efficacy. If these are absolute counts blind to where the virus is and how many cells the virus hits, if the virus efficacy varies in efficiency this could drive absolute differences that aren't actually biological.

Because the AAV-GFAP-Cyclin D1 and AAV-GFAP-Cyclin D1-p27kip1 shRNA viruses do not carry a fluorescent reporter gene, we cannot easily measure viral efficacy in the same experiment. We believe that variations in viral efficacy cannot account for the significant differences in MG proliferation for two reasons: 1) We injected the same titer for all three viruses, and 2) Viral infection efficacy is very high, approaching 100% in the central retina. Nonetheless, to rule out the possibility that the differences in MG proliferation among the Cyclin D overexpression, p27kip1 knockdown, and CCA groups are due to variations in viral efficacy, we will include the p27kip1 knockdown and Cyclin D1 overexpression efficiencies for all four groups using qPCR and/or Western blot analysis in the revised manuscript.

(6) According to the Jax laboratories, mice aren't considered aged until they are over 18months old. While it is interesting that CCA treatment does not seem to lose efficacy over maturation I would rephrase the findings as the experiment does not test this virus in aged retinas.

Thank you to the reviewer for bringing this to our attention. We will void using “aged mice” in our revised manuscript.

(7) Supplemental Figure 2c-d. These viruses do not hit 100% of MG, however 100% of the P27Kip staining is gone in the P27sh1 treatment, even the P27+ cell in the GCL that is likely an astrocyte has no staining in the shRNA 1 picture. Why is this?

For Supplementary Figure 2c-d, we focused on the central area where knockdown efficiency was high, approaching 100%. We will replace this image with one that includes both high and low Müller glia transduction efficiency regions, clearly demonstrating the complete loss of p27kip1 staining in the area of high transduction efficiency.

Figure 2

(8) Would you expect cells to go through two rounds of cell cycle in such a short time? The treatment of giving Edu then BrdU 24 hours later would have to catch a cell going through two rounds of division in a very short amount of time. Again the end point should be added graphically to this figure.

We thank the reviewer for raising this important point. While the typical cell cycle time for human cells is approximately 24 hours, we hypothesized that 24 hours would be the most likely timepoint to capture cells continuously progressing through the cell cycle. However, we acknowledge that we cannot exclude the possibility of some cells entering a second cell cycle at much later timepoints.

In the revised manuscript, we will carefully qualify our conclusion to state that the majority of MG do not immediately undergo another cell division, rather than making a definitive statement. This more cautious phrasing will better reflect the limitations of the 24-hour timepoint and allow for the potential of a small subset of cells proceeding through additional rounds of division at later stages.

Figure 3

(9) I am confused by the mixing of ratios of viruses to indicate infection success. I know mixtures of viruses containing CCA or control GFP or a control LacZ was injected. Was the idea to probe for GFP or LacZ in the single cell data to see which cells were infected but not treated? This is not shown anywhere?

The virus infection was not uniform across the entire retina. To mark the infection hotspots, we added 10% GFP virus to the mixture. Regions of the retina with low infection efficiency were removed by dissection and excluded from the scRNA-seq analysis. We apologize for not clearly explaining this methodological detail in the original text, and will update the Methods section accordingly.

(10) The majority of glia sorted from TdTomato are probably not infected with virus. Can you subset cells that were infected only for analysis? Otherwise it makes it very hard to make population judgements like Figure 3E-H if a large portion are basically WT glia.

This question is related to the last one. Since the regions with high virus infection efficiency were selectively dissected and isolated for analysis, the percentage of CCA-infected MG should constitute the majority in the scRNA-seq data.

(11) Figure 3C you can see Rho is expressed everywhere which is common in studies like this because the ambient RNA is so high. This makes it very hard to talk about "Rod-like" MG as this is probably an artifact from the technique. Most all scRNA-seq studies from MG-reprogramming have shown clusters of "rods" with MG hybrid gene expression and these had in the past just been considered an artifact.

We agree that the low levels of Rho in other MG clusters (such as quiescent, reactivated, and proliferating MG) are likely due to RNA contamination. However, the level of Rho in the rod-like MG is significantly higher than in the other clusters, indicating that this is unlikely to be solely due to contamination.

As shown in Supplementary Figure 7A-C, a cluster of MG-rod hybrid cells (cluster C4) was present in all three experimental groups at similar ratios, and this hybrid cluster was excluded from further analysis. In contrast, the rod-like Müller glia (cluster C3) were predominantly found in the CCA and CCANT groups, suggesting a genuine response to CCA treatment.

Furthermore, we will conduct Rho and Gnat1 RNA in situ hybridization on the dissociated retinal cells to further support the conclusion that rod-specific genes are upregulated in a subset of MG in the revised manuscript.

(12) It is mentioned the "glial" signature is downregulated in response to CCA treatment. Where is this shown convincingly? Figure H has a feature plot of Glul , which is not clear it is changed between treatments. Otherwise MG genes are shown as a function of cluster not treatment.

We will add box plots of several MG-specific genes to better illustrate the downregulation of the glial signature in the relevant cell cluster in the revised manuscript.

Figure 4

(13) The authors should be commended for being very careful in their interpretations. They employ the proper controls (Er-Cre lineage tracing/EdU-pulse chasing/scRNA-seq omics) and were very careful to attempt to see MG-derived rods. This makes the conclusion from the FISH perplexing. The few puncta dots of Rho and GNAT in MG are not convincing to this reviewer, Rho and GNAT dots are dense everywhere throughout the ONL and if you drew any random circle in the ONL it would be full of dots. The rigor of these counts also comes into question because some dots are picked up in MG in the INL even in the control case. This is confusing because baseline healthy MG do not express RNA-transcripts of these Rod genes so what is this picking up? Taken together, the conclusion that there are Rod-like MG are based off scRNA-seq data (which is likely ambient contamination) and these FISH images. I don't think this data warrants the conclusion that MG upregulate Rod genes in response to CCA.

We performed RNA in situ hybridization on retinal sections because we aimed to correlate cell localization with rod gene expression. We understand the reviewer’s concern that the punctate signals of Rho and GNAT1 in the ONL MG may actually originate from neighboring rods. In the revised manuscript, we will conduct RNAscope on dissociated retinal cells to avoid this issue.

Figure 5

(14) Similar point to above but this Glul probe seems odd, why is it throughout the ONL but completely dark through the IPL, this should also be in astrocytes can you see it in the GCL? These retinas look cropped at the INL where below is completely black. The whole retinal section should be shown. Antibodies exist to GS that work in mouse along with many other MG genes, IHC or western blots could be done to better serve this point.

Indeed, the GCL was cropped out in Figure 5 A-B. We have other images with all retinal layers, which we will use in the revised manuscript. Additionally, we will perform the GS antibody staining to demonstrate partial MG dedifferentiation following CCA treatment.

Figure 6

(15) Figure 6D is not a co-labeled OTX2+/ TdTomato+ cell, Otx2 will fill out the whole nucleus as can be seen with examples from other MG-reprogramming papers in the field (Hoang, et al. 2020; Todd, et al. 2020; Palazzo, et al. 2022). You can clearly see in the example in Figure 6D the nucleus extending way beyond Otx2 expression as it is probably overlapping in space. Other examples should be shown, however, considering less than 1% of cells were putatively Otx2+, the safer interpretation is that these cells are not differentiating into neurons. At least 99.5% are not.

We have additional examples of Otx2+ Tdt+ Edu+ cells, which suggest that MG neurogenesis to Otx2+ cells does occur, despite the low efficiency. We will include these images in the revised manuscript.

(16) Same as above Figure 6I is not convincingly co-labeled HuC/D is an RNA-binding protein and unfortunately is not always the clearest stain but this looks like background haze in the INL overlapping. Other amacrine markers could be tested, but again due to the very low numbers, I think no neurogenesis is occurring.

We have additional examples of HuC/D+ Tdt+ Edu+ cells, which we will show in the revised manuscript.

(17) In the text the authors are accidently referring to Figure 6 as Figure 7.

We thank the reviewer for pointing out the mistake. We will correct the mistake in the revised manuscript.

Figure 7

(18) I like this figure and the concept that you can have additional MG proliferating without destroying the retina or compromising vision. This is reminiscent of the chick MG reprogramming studies in which MG proliferate in large numbers and often do not differentiate into neurons yet still persist de-laminated for long time points.

General:

(19) The title should be changed, as I don't believe there is any convincing evidence of regeneration of neurons. Understanding the barriers to MG cell-cycle re-entry are important and I believe the authors did a good job in that respect, however it is an oversell to report regeneration of neurons from this data.

We thank the reviewer for the suggestion. We will consider changing the title in the revised manuscript.

(20) This paper uses multiple mouse lines and it is often confusing when the text and figures switch between models. I think it would be helpful to readers if the mouse strain was added to graphical paradigms in each figure when a different mouse line is employed.

We will label the mouse lines used in each experiment in the figures where appropriate.

eLife assessment

The authors provide solid evidence that any contribution of oligodendrocyte precursors to the developing cortex from the lateral ganglionic eminence is minimal in scope. The methods used support the conclusions, with some technical concerns that the authors can address with further experimentation. These are considered valuable additions to our understanding of the origins of oligodendrocytes in the forebrain during development.

Reviewer #1 (Public Review):

Summary:

In this manuscript the authors re-examine the developmental origin of cortical oligodendrocyte (OL) lineage cells using a combination of strategies, focussing on the question of whether the LGE generates cortical OL cells. The paper is interesting to myelin biologists, the methods used are appropriate and, in general, the study is well-executed, thorough, and persuasive, but not 100% convincing.

Strengths, weaknesses, and recommendations:

The first evidence presented that the LGE does not generate OLs for the cortex is that there are no OL precursors 'streaming' from the LGE during embryogenesis, unlike the MGE (Figure 1A). This in itself is not strong evidence, as they might be more dispersed. In fact, in the images shown, there is no obvious 'streaming' from the MGE either. Note that in Figure 1 there is no reference to the star that is shown in the figure.

The authors then electroporate a reporter into the LGE at E13.5 and examine the fate of the electroporated cells (Figures 1C-E). They find that electroporated cells became neurons in the striatum and in the cortex but no OLs for the cortex. There are two issues with this: first, there is no quantification, which means there might indeed be a small contribution from the LGE that is not immediately obvious from snapshot images. Second, it is unexpected to find labelled neurons in the cortex at all since the LGE does not normally generate neurons for the cortex! Electroporations are quite crude experiments as targeting is imprecise and variable and not always discernible at later stages. For example, in Figure 1D, one can see tdTOM+ cells near the AEP, as well as the striatum. Hence, IUE cannot on its own be taken as proof that there is no contribution of the LGE to the cortical OL population.

The authors then use an alternative fate-mapping approach, again with E13.5 electroporations (Figure 2). They find only a few GFP+ cells in the cortex at E18 (Figures 2C-D) and P10 (Figure 2E) and these are mainly neurons, not OL lineage cells. Again, there is no quantification.

Figure 3 is more convincing, but the experiments are incomplete. Here the authors generate triple-transgenic mice expressing Cre in the cortex (Emx1-Cre) and the MGE (Nkx2.1-Cre) as well as a strong nuclear reporter (H2B-GFP). They find that at P0 and P10, 97-98% of OL-lineage cells (SOX10+ or PDGFRA+) in the cortex are labelled with GFP (Figure 3). This is a more convincing argument that the LGE/CGE might not contribute significant numbers of OL lineage cells to the cortex, in contrast to the Kessaris et at. (2006) paper, which showed that Gsh2-Cre mice label ~50% of SOX10+ve cells in the motor cortex at P10. The authors of the present paper suggest that the discrepancy between their study and that of Kessaris et al. (2006) is based on the authors' previous observation (Zhang et al 2020) (https://doi.org/10.1016/j.celrep.2020.03.027) that GSH2 is expressed in intermediate precursors of the cortex from E18 onwards. If correct, then Kessaris et al. might have mistakenly attributed Gsh2-Cre+ lineages to the LGE/CGE when they were in fact intrinsic to the cortex. However, the evidence from Zhang et al 2020 that GSH2 is expressed by cortical intermediate precursors seems to rest solely on their location within the developing cortex; a more convincing demonstration would be to show that the GSH2+ putative cortical precursors co-label for EMX1 (by immunohistochemistry or in situ hybridization), or that they co-label with a reporter in Emx1-driven reporter mice. This demonstration should be simple for the authors as they have all the necessary reagents to hand. Without these additional data, the assertion that GSX2+ve cells in the cortex are derived from the cortical VZ relies partly on an act of faith on the part of the reader.

Note that Tripathi et al. (2011, "Dorsally- and ventrally-derived oligodendrocytes have similar electrical properties but myelinate preferred tracts." J. Neurosci. 31, 6809-6819) found that the Gsh-Cre+ OL lineage contributed only ~20% of OLs to the mature cortex, not ~50% as reported by Kessaris et al. (2006). If it is correct that these Gsh2-derived OLs are from the cortical anlagen as the current paper claims, then it would raise the possibility that the ventricular precursors of GSH2+ intermediate progenitors are not uniformly distributed through the cortical VZ but are perhaps localized to some part of it. Then the contribution of Gsh2-derived OLs to the cortical population could depend on precisely where one looks relative to that localized source. It would be a nice addition to the current manuscript if the authors could explore the distribution of their GSH2+ intermediate precursors throughout the developing cortex. In any case, Tripathi et al. (2011) should be cited.

Finally, the authors deleted Olig2 in the MGE and found a dramatic reduction of PDGFRA+ and SOX10+ cells in the cortex at E14 and E16 (Figure 4A-F). This further supports their conclusion that, at least at E16, there is no significant contribution of OLs from ventral sources other than the MGE/AEP. This does not exclude the possibility that the LGE/CGE generates OLs for the cortex at later stages. Hence, on its own, this is not completely convincing evidence that the LGE generates no OL lineage cells for the cortex.

Comments on the latest version:

The revised manuscript has addressed the issues we raised previously. The addition of the new Figure 3 supplement 1A-C demonstrating that Gsx2+ve cells in the cortex are generated from Emx1-Cre precursors is convincing, although there is nothing to prove that the GFP+, Gsh2+ double-labelled nuclei are oligodendrocyte lineage and not, for example, astrocytes. It would be helpful to include a Gsh2, Olig2 (or Gsh2, Sox10) double-label image to prove this point. Also, to make the figure more clear, the authors should also show a small area at high magnification, splitting the green and red channels so that the reader can see more clearly that all the red cells are also green.

Reviewer #2 (Public Review):

Traditional thinking has been that cortical oligodendrocyte progenitor cells (OPCs) arise in the development of the brain from the medial ganglionic eminence (MGE), lateral/caudal ganglionic eminence (LGE/CGE), and cortical radial glial cells (RGCs). Indeed a landmark study demonstrated some time ago that cortical OPCs are generated in three waves, starting with a ventral wave derived from the medial ganglionic eminence (MGE) or the anterior entopeduncular area (AEP) at embryonic day E12.5 (Nkx2.1+ lineage), followed by a second wave of cortical OLs derived from the lateral/caudal ganglionic eminences (LGE/CGE) at E15.5 (Gsx2+/Nkx2.1- lineage), and then a final wave occurring at P0, when OPCs originate from cortical glial progenitor cells (Emx1+ lineage). However, the authors challenge the idea in this paper that cortical progenitors are produced from the LGE. They have found previously that cortical glial progenitor cells were also found to express Gsx2, suggesting this may not have been the best marker for LGE-derived OPCs. They have used fate mapping experiments and lineage analyses to suggest that cortical OPCs do not derive from the LGE.

Strengths:

(1) The data is high quality and very well presented, and experiments are thoughtful and elegant to address the questions being raised.

(2) The authors use two elegant approaches to lineage trace LGE derived cells, namely fate mapping of LGE-derived OPCs by combining IUE (intrauterine electroporation) with a Cre recombinase-dependent IS reporter, and Lineage tracing of LGE-derived OPCs by combining IUE with the PiggyBac transposon system. Both approaches show convincingly that labelled LGE-derived cells that enter the cortex do not express OPC markers, but that those co-labelling with oligodendrocyte markers remain in the striatum.

(3) The authors then use further approaches to confirm their findings. Firstly they lineage trace Emx1-Cre; Nkx2.1-Cre; H2B-GFP mice. Emx1-Cre is expressed in cortical RGCs and Nkx2.1-Cre is specifically expressed in MGE/AEP RGCs. They find that close to 98% of OPCs in the cortex co-label with GFP at later times, suggesting the contribution of OPCs from LGE is minimal.

(4) They use one further approach to strengthen the findings yet further. They cross Nkx2.1-Cre mice with Olig2 F/+ mice to eliminate Olig2 expression in the SVZ/VZ of the MGE/AEP (Figures 4A-B). The generation of MGE/AEP-derived OPCs is inhibited in these Olig2-NCKO conditional mice. They find that the number of cortical progenitors at E16.5 is reduced 10-fold in these mice, suggesting that LGE contribution to cortical OPCs is minimal.

Impact of Study:

The authors show elegantly and convincingly that the contribution of the LGE to the pool of cortical OPCs is minimal. The title should perhaps be that the LGE contribution is minimal rather than no contribution at all, as they are not able to rule out some small contribution from the LGE. These findings challenge the traditional belief that the LGE contributes to the pool of cortical OPCs. The authors do show that the LGE does produce OPCs, but that they tend to remain in the striatum rather than migrate into the cortex. It is interesting to wonder why their migration patterns may be different from the MGE-derived OPCs which migrate to the cortex. The functional significance of these different sources of OPCs for adult cortex in homeostatic or disease states remains unclear though.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Summary:

In this manuscript the authors re-examine the developmental origin of cortical oligodendrocyte (OL) lineage cells using a combination of strategies, focussing on the question of whether the LGE generates cortical OL cells. The paper is interesting to myelin biologists, the methods used are appropriate and, in general, the study is well-executed, thorough, and persuasive, but not 100% convincing.

Thank you very much for approving our paper.

Strengths, weaknesses, and recommendations:

The first evidence presented that the LGE does not generate OLs for the cortex is that there are no OL precursors 'streaming' from the LGE during embryogenesis, unlike the MGE (Figure 1A). This in itself is not strong evidence, as they might be more dispersed. In fact, in the images shown, there is no obvious 'streaming' from the MGE either. Note that in Figure 1 there is no reference to the star that is shown in the figure.

We totally agree with you. While OPC migration stream is not strong evidence to support that the LGE does not generate OPCs for the cortex, when considering our additional evidence, the absence of obvious 'streaming' from LGE to cortex provided supplementary support for this conclusion. Finally, we have removed the star in the figure.

The authors then electroporate a reporter into the LGE at E13.5 and examine the fate of the electroporated cells (Figures 1C-E). They find that electroporated cells became neurons in the striatum and in the cortex but no OLs for the cortex. There are two issues with this: first, there is no quantification, which means there might indeed be a small contribution from the LGE that is not immediately obvious from snapshot images. Second, it is unexpected to find labelled neurons in the cortex at all since the LGE does not normally generate neurons for the cortex. Electroporations are quite crude experiments as targeting is imprecise and variable and not always discernible at later stages. For example, in Figure 1D, one can see tdTOM+ cells near the AEP, as well as the striatum. Hence, IUE cannot on its own be taken as proof that there is no contribution of the LGE to the cortical OL population.

Thank you for your constructive suggestions.

(1) Following the reviewer's suggestion, we have added these statistics, please see Figure 1F.

(2) The reviewer raised a good point. We occasionally found a very small number of electroporated cells in the MGE/AEP VZ in our IUE system. Therefore, we can identify these electroporated cells in the cortex, most of them expressed the neuronal marker NeuN. We suspect these are MGE-derived cortical interneurons. It's worth noting that these electroporated cells (MGE-derived) are not glia cells. The probable reason may be that MGE/AEP generate cortical OPCs mainly before E13.5 (in this study we performed IUE at E13.5).

The authors then use an alternative fate-mapping approach, again with E13.5 electroporations (Figure 2). They find only a few GFP+ cells in the cortex at E18 (Figures 2C-D) and P10 (Figure 2E) and these are mainly neurons, not OL lineage cells. Again, there is no quantification.

Thank you very much for your suggestions. Actually, in this fate-mapping approach, the electroporated cells in the cortex is very few. We analyzed four mice, and found that all GFP positive cells (139 GFP+) did not express OLIG2, SOX10 and PDGFRA.

Figure 3 is more convincing, but the experiments are incomplete. Here the authors generate triple-transgenic mice expressing Cre in the cortex (Emx1-Cre) and the MGE (Nkx2.1-Cre) as well as a strong nuclear reporter (H2B-GFP). They find that at P0 and P10, 97-98% of OL-lineage cells (SOX10+ or PDGFRA+) in the cortex are labelled with GFP (Figure 3). This is a more convincing argument that the LGE/CGE might not contribute significant numbers of OL lineage cells to the cortex, in contrast to the Kessaris et at. (2006) paper, which showed that Gsh2-Cre mice label ~50% of SOX10+ve cells in the motor cortex at P10. The authors of the present paper suggest that the discrepancy between their study and that of Kessaris et al. (2006) is based on the authors' previous observation (Zhang et al 2020) (https://doi.org/10.1016/j.celrep.2020.03.027) that GSH2 is expressed in intermediate precursors of the cortex from E18 onwards. If correct, then Kessaris et al. might have mistakenly attributed Gsh2-Cre+ lineages to the LGE/CGE when they were in fact intrinsic to the cortex. However, the evidence from Zhang et al 2020 that GSH2 is expressed by cortical intermediate precursors seems to rest solely on their location within the developing cortex; a more convincing demonstration would be to show that the GSH2+ putative cortical precursors co-label for EMX1 (by immunohistochemistry or in situ hybridization), or that they co-label with a reporter in Emx1-driven reporter mice. This demonstration should be simple for the authors as they have all the necessary reagents to hand. Without these additional data, the assertion that GSX2+ve cells in the cortex are derived from the cortical VZ relies partly on an act of faith on the part of the reader. Note that Tripathi et al. (2011, "Dorsally- and ventrally-derived oligodendrocytes have similar electrical properties but myelinate preferred tracts." J. Neurosci. 31, 6809-6819) found that the Gsh-Cre+ OL lineage contributed only ~20% of OLs to the mature cortex, not ~50% as reported by Kessaris et al. (2006). If it is correct that these Gsh2-derived OLs are from the cortical anlagen as the current paper claims, then it would raise the possibility that the ventricular precursors of GSH2+ intermediate progenitors are not uniformly distributed through the cortical VZ but are perhaps localized to some part of it. Then the contribution of Gsh2-derived OLs to the cortical population could depend on precisely where one looks relative to that localized source. It would be a nice addition to the current manuscript if the authors could explore the distribution of their GSH2+ intermediate precursors throughout the developing cortex. In any case, Tripathi et al. (2011) should be cited.

Thank you for your constructive suggestions.

(1) We used the Emx1Cre; RosaH2B-GFP mouse and found that nearly all GSX2+ cells in the cortical SVZ are derived from the Emx1+ lineage at P0 (Please see our new Figure 3-supplement 1A-C). 

(2) According to your suggestion, we have cited this paper (Tripathi et al.) in our revised manuscript.

(3) The study conducted by Kessaris et al. (2006) revealed that roughly 50% of cortical oligodendrocytes (OLs) originate from the Gsx2 lineage (LGE/CGE-derived). In contrast, Tripathi et al. (2011) observed that Gsx2-derived OLs contribute only around 20% to the corpus callosum (CC). To investigate the reasons behind these disparate findings, we conducted three experiments. Firstly, using Emx1Cre; RosaH2B-GFP mice, we found that approximately 89% of lateral CC (LCC) OLs originate from the Emx1 lineage, with only around 11% derived from the ventral source (refer to Author response image 1A and B below). Secondly, employing Nkx2-1Cre; RosaH2B-GFP mice, we determined that approximately 11% of LCC OLs originate from the Nkx2.1 lineage (refer to pictures C and D below). Finally, we found that approximately 98.3% of lateral LCC OLs originate from both Emx1 and Nkx2.1 lineages, with only around 1.7% possibly derived from the LGE (see Author response image 1E and F below). Taken together, our results indicate that approximately 89% of LCC OLs originate from the Emx1 lineage, while 11% of LCC OLs are derived from the medial ganglionic eminence (MGE).

It is worth noting that OLs from Emx1 and Nkx2.1 lineages were equally distributed in the medial CC (mCC) (see Author response image 1G below). This finding suggests that MGE-derived OLs exhibit spatial heterogeneity in their distribution within the CC. These results provide evidence that the contribution of the lateral ganglionic eminence (LGE) and caudal ganglionic eminence (CGE) to CC OLs is minimal.

Author response image 1.

Finally, the authors deleted Olig2 in the MGE and found a dramatic reduction of PDGFRA+ and SOX10+ cells in the cortex at E14 and E16 (Figure 4A-F). This further supports their conclusion that, at least at E16, there is no significant contribution of OLs from ventral sources other than the MGE/AEP. This does not exclude the possibility that the LGE/CGE generates OLs for the cortex at later stages. Hence, on its own, this is not completely convincing evidence that the LGE generates no OL lineage cells for the cortex.

There are three reasons why we didn't analyze Olig2-NCKO mice after E16.5. 1. The expression of Nkx2.1Cre is lower within the dorsal-most region of the MGE than other Nkx2.1-expressing regions. Even at E15.5, we can still find a small number of OPCs in the lateral cortex. We speculate that these OPCs are derived from dorsal MGE. 2. Considering the possibility of incomplete recombination in Olig2 gene locus, we guess OPCs (Olig2+) in the lateral cortex are derived from MGE. Indeed, we found a few OPCs in the MGE/AEP in the Olig2-NCKO mice (Figure 4F). 3. The recent study (bioRxiv preprint doi: https://doi.org/10.1101/2024.01.23.576886) showed that the contribution of LGE/CGE to cortical OPCs is minimal, which further supporting our findings. Taken together, our results provide additional evidence supporting the limited contribution of the LGE/CGE to cortical OPCs (OLs).

Reviewer #2 (Public Review):

Traditional thinking has been that cortical oligodendrocyte progenitor cells (OPCs) arise in the development of the brain from the medial ganglionic eminence (MGE), lateral/caudal ganglionic eminence (LGE/CGE), and cortical radial glial cells (RGCs). Indeed a landmark study demonstrated some time ago that cortical OPCs are generated in three waves, starting with a ventral wave derived from the medial ganglionic eminence (MGE) or the anterior entopeduncular area (AEP) at embryonic day E12.5 (Nkx2.1+ lineage), followed by a second wave of cortical OLs derived from the lateral/caudal ganglionic eminences (LGE/CGE) at E15.5 (Gsx2+/Nkx2.1- lineage), and then a final wave occurring at P0, when OPCs originate from cortical glial progenitor cells (Emx1+ lineage). However, the authors challenge the idea in this paper that cortical progenitors are produced from the LGE. They have found previously that cortical glial progenitor cells were also found to express Gsx2, suggesting this may not have been the best marker for LGE-derived OPCs. They have used fate mapping experiments and lineage analyses to suggest that cortical OPCs do not derive from the LGE.

Strengths:

(1) The data is high quality and very well presented, and experiments are thoughtful and elegant to address the questions being raised.

(2) The authors use two elegant approaches to lineage trace LGE derived cells, namely fate mapping of LGE-derived OPCs by combining IUE (intrauterine electroporation) with a Cre recombinase-dependent IS reporter, and Lineage tracing of LGE-derived OPCs by combining IUE with the PiggyBac transposon system. Both approaches show convincingly that labelled LGE-derived cells that enter the cortex do not express OPC markers, but that those co-labelling with oligodendrocyte markers remain in the striatum.

(3) The authors then use further approaches to confirm their findings. Firstly they lineage trace Emx1-Cre; Nkx2.1-Cre; H2B-GFP mice. Emx1-Cre is expressed in cortical RGCs and Nkx2.1-Cre is specifically expressed in MGE/AEP RGCs. They find that close to 98% of OPCs in the cortex co-label with GFP at later times, suggesting the contribution of OPCs from LGE is minimal.

(4) They use one further approach to strengthen the findings yet further. They cross Nkx2.1-Cre mice with Olig2 F/+ mice to eliminate Olig2 expression in the SVZ/VZ of the MGE/AEP (Figures 4A-B). The generation of MGE/AEP-derived OPCs is inhibited in these Olig2-NCKO conditional mice. They find that the number of cortical progenitors at E16.5 is reduced 10-fold in these mice, suggesting that LGE contribution to cortical OPCs is minimal.

We thank the reviewer for summarizing the strengths of our manuscript.

Weaknesses:

(1) The authors use IUE in experiments mentioned in point 2 of 'Strengths' above (Figures 1 and 2) and claim that the reporter was delivered specifically into LGE VZ at E13.5 using this IUE. It would be nice to see some sort of time course of delivery after IUE to show the reporter is limited to LGE VZ at early times post-IUE.

Thank you very much for your suggestions. Indeed, when using IUE in our system, we occasionally found a small number of electroporated cells in the MGE/AEP VZ. Thus, we can find very few electroporated cells (MGE/AEP-derived) in the cortex and these electroporated cells are neuron (perhaps interneuron).

(2) In the experiments mentioned in point 3 of 'Strengths' (Figure 3), statistical analysis showed that only approximately 2% of OPCs were GFP-negative cells. This 2% could possibly be derived from the LGE/CGE so does not totally rule out that LGE contributes some cortical OPCs.

Thank you for your constructive suggestions. We apologize for any imprecise descriptions. Despite we suspect that this 2% may originate from MGE {Considering the possibility of incomplete recombination in Olig2 gene locus, we guess the OPCs (Olig2+) may be derived from MGE. Indeed, we found a few OPCs in the MGE/AEP in the Olig2-NCKO mice (Figure 4F)} or from the dMGE (The expression of Nkx2.1Cre is lower within the dorsal-most region of the MGE than in other Nkx2.1-expressing regions). Anyway, we have softened the assertion everywhere in our revised manuscript.

(3) In the experiments mentioned in point 4 of 'Strengths' (Figure 4), they do still find cortical OPCs at E16.5 in the Olig2-NCKO conditional mice. It is unclear whether this is due to the recombination efficiency of the CRE enzyme not being 100%, or whether there is some LGE contribution to the cortical OPCs.

This experiment alone may not provide strong evidence to support that LGE do not contribute to the cortical OPCs during development. However, when combing our other results with this result, we can confirm that the contribution of LGE to cortical OPCs is minimal. Furthermore, a recent study reported that LGE/CGE-derived OLs make minimum contributions to the neocortex and corpus callosum，which further supporting the reliability of our conclusion.

We would like to thank the reviewers and editors for their valuable comments and suggestions again.

Impact of Study:

The authors show elegantly and convincingly that the contribution of the LGE to the pool of cortical OPCs is minimal. The title should perhaps be that the LGE contribution is minimal rather than no contribution at all, as they are not able to rule out some small contribution from the LGE. These findings challenge the traditional belief that the LGE contributes to the pool of cortical OPCs. The authors do show that the LGE does produce OPCs, but that they tend to remain in the striatum rather than migrate into the cortex. It is interesting to wonder why their migration patterns may be different from the MGE-derived OPCs which migrate to the cortex. The functional significance of these different sources of OPCs for adult cortex in homeostatic or disease states remains unclear though.

Recommendations for the authors:

Reviewer #1 (Recommendations for The Authors):

(1) Change the title to e.g. 'limited contribution of the LGE to cortical oligodendrocytes'. Alternatively, It might be more useful to highlight where they come from, e.g. "Cortical oligodendrocytes originate predominantly or exclusively from the MGE and cortical VZ"

As suggested, we have changed the old title to the following: The lateral/caudal ganglionic eminence makes a limited contribution to cortical oligodendrocytes

(2) Demonstrate using lineage tracing that GSH2+ cells in the cortex are derived from the Emx1-lineage, e.g. using immunohistochemistry for GSX2 and a reporter in Emx1-Cre mice crossed to a reporter.

In our revised manuscript, we have added a new figure (Figure 3-supplement 1A-C) to demonstrate that the GSX2+ cells in the cortex are derived from the Emx1-lineage.

(3) Make it clear in their discussion that they have not explored the CGE so it is possible that this region generates some OLs.

The Emx1Cre; Nkx2.1Cre; H2B-GFP mice showed that only ~2% cortical OLs are derived from LGE/CGE. Actually, considering the efficiency of Cre enzyme recombination and the relatively low Cre activity in the dMGE of Nkx2.1Cre, the actual contribution of LGE/CGE-derived cortical OLs could be even lower than our current observation. Therefore, our results demonstrate that the LGE/CGE generate very few，possibly even no，OLs for the cortex.

(4) Soften the assertion that the LGE does not generate any OL lineage cells that reach the cortex by e.g. changing the word 'sole' to 'predominant' (line 88) and, elsewhere in the paper, leaving open the possibility that small numbers of LGE-derived OLs might enter the cortex, depending on where exactly one looks.

As suggested, we have softened the assertion everywhere in our manuscript.

(5) Lines 255-260: 'First, the time window during which the MGE generates OLs is very brief, perhaps occurring before MGE neurogenesis. The high level of SHH in the MGE allows for the production of a small population of cortical OPCs around E12.5. Subsequently, multipotent intermediate progenitors begin to express DLX transcription factors resulting in ending the generation of OPCs in the MGE'. What is the evidence that OL genesis precedes neurogenesis? If there is none (as I suspect) then this statement should be removed.

The editors raised a good point. We have no strong evidence to support that OL genesis precedes neurogenesis in MGE, thus, we removed these sentences in our manuscript.

(6) Figure 1E should show quantification of cells as a % of electroporated cells and as a % of PDGFRA+ or OLIG2+ or SOX10+ cells, so that the reader might have a clear view of the extent of labelling.

Done.

(7) Figure 4: This is interesting but incomplete. At E14.5 the authors show the presence of PDGFRA+cells in the telencephalon. However, at E16.5 they show images only of the dorsal-most region of the cortex. If the LGE/CGE begins to generate OLPs for the early cortex, they would be expected to appear near the cortico-striatal boundary, as shown in Kessaris 2006 Fig1g-h. In the current manuscript, the authors do not show these regions, or the LGE and CGE, in their images. It is essential to show PDGFRA immunolabelling at the cortico-striatal boundary and also in the LGE and CGE at E16.5 in control and Olig2 mutant mice. It is also necessary to extend this analysis to E18.5, perhaps showing PDGFRA+ cells streaming from the cortical VZ/SVZ.

There are three reasons why we didn't analyze Olig2-NCKO mice after E16.5. 1.Frankly, the expression of Nkx2.1Cre is lower within the dorsal-most region of the MGE than other Nkx2.1-expressing regions. Even at E15.5, we can still find a small number of OPCs in the lateral cortex. We guess these OPCs are derived from dMGE. 2. Considering the possibility of incomplete recombination in Olig2 gene locus, we guess OPCs (Olig2+) are derived from MGE. In fact, we found a few OPCs in the MGE/AEP in the Olig2-NCKO mice (Figure 4F). 3. The recent study (bioRxiv preprint doi: https://doi.org/10.1101/2024.01.23.576886) showed that the contribution of LGE/CGE to cortical OPCs is minimal. Taken together, our results provide additional evidence supporting the limited contribution of the LGE/CGE to cortical OPCs (OLs).

(8) Cite Tripathi et al. (2011) and mention the disparity between the findings of that paper and Kessaris et al. (2006) and possible reasons - see main review above.

Done.

eLife assessment

Shore et al. report the important effects of a heterozygous mutation in the KCNT1 potassium channel on ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of KCNT1-Y777H mice. The authors provide solid evidence of physiological differences between this heterozygous mutation and their previous work with homozygotes. The reviewers appreciated the inclusion of recordings in ex vivo slices and dissociated cortical neurons, as well as the additional evidence showing an increase in persistent sodium currents in parvalbumin-positive interneurons in heterozygotes.

Reviewer #1 (Public Review):

Summary:

This manuscript reports the effects of a heterozygous mutation in the KCNT1 potassium channels on the properties of ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of mice expressing KCNT1-Y777H. In humans, this mutation as well as multiple other heterozygotic mutations produce very severe early-onset seizures and produce a major disruption of all intellectual function. In contrast, in mice, this heterozygous mutation appears to have no behavioral phenotype or any increased propensity to seizures. A relevant phenotype is, however, evident in mice with the homozygous mutation, and the authors have previously published the results of similar experiments with the homozygotes. As perhaps expected, the neuronal effects of the heterozygous mutation presented in this manuscript are generally similar but markedly smaller than the previously published findings on homozygotes. There are, however, some interesting differences, particularly on PV+ interneurons, which appear to be more excitable than wild type in the heterozygotes but more excitable in the heterozygotes. This raises the interesting question, which has been explicitly discussed by the authors in the revised manuscript, as to whether the reported changes represent homeostatic events that suppress the seizure phenotype in the mouse heterozygotes or simply changes in excitability that do not reach the threshold for behavioral outcomes.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shore et al. investigate the consequent changes in excitability and synaptic efficacy of diverse neuronal populations in an animal model of juvenile epilepsy. Using electrophysiological patch-clamp recordings from dissociated neuronal cultures, the authors find diverging changes in two major populations of inhibitory cell types, namely somatostatin (SST)- and parvalbumin (PV)-positive interneurons, in mice expressing a variant of the KCNT1 potassium channel. They further suggest that the differential effects are due to a compensatory increase in the persistent sodium current in PV interneurons in pharmacological and in silico experiments. It remains unclear why this current is selectively enhanced in PV-interneurons.

Strengths:

(1) Heterozygous KCNT1 gain of function variant was used which more accurately models the human disorder.

(2) The manuscript is clearly written, and the flow is easy to follow. The authors explicitly state the similarities and differences between the current findings and the previously published results in the homozygous KCNT1 gain of function variant.

(3) This study uses a variety of approaches including patch clamp recording, in silico modeling and pharmacology that together make the claims stronger.

(4) Pharmacological experiments are fraught with off-target effects and thus it bolsters the authors' claims when multiple channel blockers (TTX and VU170) are used to reconstruct the sodium-activated potassium current.

Reviewer #3 (Public Review):

Summary:

The present manuscript by Shore et al. entitled Reduced GABAergic Neuron Excitability, Altered Synaptic Connectivity, and Seizures in a KCNT1 Gain-of-Function Mouse Model of Childhood Epilepsy" describes in vitro and in silico results obtained in cortical neurons from mice carrying the KCNT1-Y777H gain-of-function (GOF) variant in the KCNT1 gene encoding for a subunit of the Na+-activated K+ (KNa) channel. This variant corresponds to the human Y796H variant found in a family with Autosomal Dominant Nocturnal Frontal lobe epilepsy. The occurrence of GOF variants in potassium channel encoding genes is well known, and among potential pathophysiological mechanisms, impaired inhibition has been documented as responsible for KCNT1-related DEEs. Therefore, building on a previous study by the same group performed in homozygous KI animals, and considering that the largest majority of pathogenic KCNT1 variants in humans occur in heterozygosis, the Authors have investigated the effects of heterozygous Kcnt1-Y777H expression on KNa currents and neuronal physiology among cortical glutamatergic and the 3 main classes of GABAergic neurons, namely those expressing vasoactive intestinal polypeptide (VIP), somatostatin (SST), and parvalbumin (PV), crossing KCNT1-Y777H mice with PV-, SST- and PV-cre mouse lines, and recording from GABAergic neurons identified by their expression of mCherry (but negative for GFP used to mark excitatory neurons).

The results obtained revealed heterogeneous effects of the variant on KNa and action potential firing rates in distinct neuronal subpopulations, ranging from no change (glutamatergic and VIP GABAergic) to decreased excitability (SST GABAergic) to increased excitability (PV GABAergic). In particular, modelling and in vitro data revealed that an increase in persistent Na current occurring in PV neurons was sufficient to overcome the effects of KCNT1 GOF and cause an overall increase in AP generation.

Strengths:

The paper is very well written, the results clearly presented and interpreted, and the discussion focuses on the most relevant points.<br /> The recordings performed in distinct neuronal subpopulations (both in primary neuronal cultures and, for some subpopulations, in cortical slices, are a clear strength of the paper. The finding that the same variant can cause opposite effects and trigger specific homeostatic mechanisms in distinct neuronal populations is very relevant for the field, as it narrows the existing gap between experimental models and clinical evidence.

Author response:

The following is the authors’ response to the previous reviews.

eLife assessment

Shore et al. report important effects of a heterozygous mutation in the KCNT1 potassium channel on ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of KCNT1-Y777H mice. The authors provide solid evidence of physiological differences between this heterozygous mutation and their previous work with homozygotes. The reviewers appreciated the inclusion of recordings in ex vivo slices and dissociated cortical neurons, as well as the additional evidence showing an increase in persistent sodium currents (INaP) in parvalbumin-positive interneurons in heterozygotes. However, they were unclear regarding the likelihood of the increased sodium influx through INaP channels increasing sodium-activated potassium currents in these neurons.

Regarding the last sentence of the eLife assessment, we’ve added a new paragraph to the Discussion section of the paper to address this concern. Please see the response to comment 1B of Reviewer #1 below for more details. We feel that the question of whether an increase in INaP would further increase KCNT1 activity is a valid discussion point but not a limitation of the importance or rigor of the work itself.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript reports the effects of a heterozygous mutation in the KCNT1 potassium channels on the properties of ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of mice expressing KCNT1-Y777H. In humans, this mutation as well as multiple other heterozygotic mutations produce very severe early-onset seizures and produce a major disruption of all intellectual function. In contrast, in mice, this heterozygous mutation appears to have no behavioral phenotype or any increased propensity to seizures. A relevant phenotype is, however, evident in mice with the homozygous mutation, and the authors have previously published the results of similar experiments with the homozygotes. As perhaps expected, the neuronal effects of the heterozygous mutation presented in this manuscript are generally similar but markedly smaller than the previously published findings on homozygotes. There are, however, some interesting differences, particularly on PV+ interneurons, which appear to be more excitable than wild type in the heterozygotes but more excitable in the heterozygotes. This raises the interesting question, which has been explicitly discussed by the authors in the revised manuscript, as to whether the reported changes represent homeostatic events that suppress the seizure phenotype in the mouse heterozygotes or simply changes in excitability that do not reach the threshold for behavioral outcomes.

Strengths and Weaknesses:

(1) The authors find that the heterozygous mutation in PV+ interneurons increases their excitability, a result that is opposite from their previous observation in neurons with the corresponding homozygous mutation. They propose that this results from the selective upregulation of a persistent sodium current INaP in the PV+ interneurons. These observations are very interesting ones, and they raised some issues in the original submission:

A) The protocol for measuring the INaP current could potentially lead to results that could be (mis)interpreted in different ways in different cells. First, neither K currents nor Ca currents are blocked in these experiments. Instead, TTX is applied to the cells relatively rapidly (within 1 second) and the ramp protocol is applied immediately thereafter. It is stated that, at this time, Na currents and INaP are fully blocked but that any effects on Na-activated K currents are minimal. In theory this would allow the pre- to post- difference current to represent a relatively uncontaminated INaP. This would, however, only work if activation of KNa currents following Na entry is very slow, taking many seconds. A good deal of literature has suggested that the kinetics of activation of KNa currents by Na influx vary substantially between cell types, such that single action potentials and single excitatory synaptic events rapidly evoke KNa currents in some cell types. This is, of course, much faster than the time of TTX application. Most importantly, the kinetics of KNa activation may be different in different neuronal types, which would lead to errors that could produce different estimates of INaP in PV+ interneurons vs other cell types.

In their revised manuscript, the authors have provided good data demonstrating that, at least for the PV and SST neurons, loss of KNa currents after TTX application is slow relative to the time course of loss of INaP, justifying the use of this protocol for these neuronal types.

B) As the authors recognize, INaP current provides a major source of cytoplasmic sodium ions for the activation. An expected outcome of increased INaP is, therefore, further activation of KNa currents, rather than a compensatory increase in an inward current that counteracts the increase in KNa currents, as is suggested in the discussion.

The authors comment in the rebuttal that, despite the fact that sodium entry through INaP is known to activate KNa channels, an increase in INaP does not necessarily imply increased KNa current. This issue should be addressed directly somewhere in the text, perhaps most appropriately in the discussion.

We’ve added the following new paragraph to the Discussion section of the manuscript to address this concern:

“As the persistent sodium current has been shown to act as a source of cytoplasmic sodium ions for KCNT1 channel activation in some neuron types (Hage & Salkoff, 2012), one might expect that the compensatory increase in INaP in YH-HET PV neurons would further increase, rather than counteract, KNa currents. Unfortunately, there is insufficient information on the relative locations of the INaP and KCNT1 channels, as well as the kinetics of sodium transfer to KCNT1 channels, among cortical neuron subtypes, and even less is known in the context of KCNT1 GOF neurons; thus, it is difficult to predict how alterations in one of these currents may affect the other. One plausible reason that increased INaP would not alter KNa currents in YH-HET PV neurons is that the particular sodium channels that are responsible for the increased INaP are not located within close proximity to the KCNT1 channels. Moreover, homeostatic mechanisms that modify the length and/or location of the sodium channel-enriched axon initial segment (AIS) in neurons in response to altered excitability are well described (Grubb & Burrone, 2010; Kuba et al., 2010); thus, it is possible that in YH-HET PV neurons, the length or location of the AIS is altered, leading to uncoupling of the sodium channels that are responsible for the increased INaP to the KCNT1 channels. Future studies will aim to further investigate potential mechanisms of neuron-type-specific alterations in NaP and KNa currents downstream of KCNT1 GOF.”  

C) The numerical simulations, in general, provide a very useful way to evaluate the significance of experimental findings. Nevertheless, while the in-silico modeling suggests that increases in INaP can increase firing rate in models of PV+ neurons, there is as yet insufficient information on the relative locations of the INaP channels and the kinetics of sodium transfer to KNa channels to evaluate the validity of this specific model.

The authors have now put in all of the appropriate caveats on this very nicely in the revised manuscript.

(2) The effects of the KCNT1 channel blocker VU170 on potassium currents are somewhat larger and different from those of TTX, suggesting that additional sources of sodium may contribute to activating KCNT1, as suggested by the authors. Because VU170 is, however, a novel pharmacological agent, it may be appropriate to make more careful statements on this. While the original published description of this compound reported no effect on a variety of other channels, there are many that were not tested, including Na and cation channels that are known to activate KCNT1, raising the possibility of off-target effects.

In the revised version, the authors have added more to the manuscript on this issue and have added a very clear discussion of this to the text (in the discussion section).

This is a very clear and thorough piece of work, and the authors are to be congratulated on this. My one remaining suggestion would be to make an explicit statement about whether increased sodium influx through INaP channels, which is thought to activate KNa channels, would be likely to increase KNa current in these neurons (see comment 1B).

Please see response to comment 1B.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shore et al. investigate the consequent changes in excitability and synaptic efficacy of diverse neuronal populations in an animal model of juvenile epilepsy. Using electrophysiological patch-clamp recordings from dissociated neuronal cultures, the authors find diverging changes in two major populations of inhibitory cell types, namely somatostatin (SST)- and parvalbumin (PV)-positive interneurons, in mice expressing a variant of the KCNT1 potassium channel. They further suggest that the differential effects are due to a compensatory increase in the persistent sodium current in PV interneurons in pharmacological and in silico experiments. It remains unclear why this current is selectively enhanced in PV-interneurons.

Strengths:

(1) Heterozygous KCNT1 gain of function variant was used which more accurately models the human disorder.

(2) The manuscript is clearly written, and the flow is easy to follow. The authors explicitly state the similarities and differences between the current findings and the previously published results in the homozygous KCNT1 gain of function variant.

(3) This study uses a variety of approaches including patch clamp recording, in silico modeling and pharmacology that together make the claims stronger.

(4) Pharmacological experiments are fraught with off-target effects and thus it bolsters the authors' claims when multiple channel blockers (TTX and VU170) are used to reconstruct the sodium-activated potassium current.

Weaknesses:

(1) This study mostly relies on recordings in dissociated cortical neurons. Although specific WT interneurons showed intrinsic membrane properties like those reported for acute brain slices, it is unclear whether the same will be true for those cells expressing KCNT1 variants, especially when the excitability changes are thought to arise from homeostatic compensatory mechanisms. The authors do confirm that mutant SST-interneurons are hypoexcitable using an ex vivo slice preparation which is consistent with work for other KCTN1 gain of function variants (e.g. Gertler et al., 2022). However, the key missing evidence is the excitability state of mutant PV-interneurons, given the discrepant result of reduced excitability of PV cells reported by Gertler et al in acute hippocampal slices.

Reviewer #3 (Public Review):

Summary:

The present manuscript by Shore et al. entitled Reduced GABAergic Neuron Excitability, Altered Synaptic Connectivity, and Seizures in a KCNT1 Gain-of-Function Mouse Model of Childhood Epilepsy" describes in vitro and in silico results obtained in cortical neurons from mice carrying the KCNT1-Y777H gain-of-function (GOF) variant in the KCNT1 gene encoding for a subunit of the Na+-activated K+ (KNa) channel. This variant corresponds to the human Y796H variant found in a family with Autosomal Dominant Nocturnal Frontal lobe epilepsy. The occurrence of GOF variants in potassium channel encoding genes is well known, and among potential pathophysiological mechanisms, impaired inhibition has been documented as responsible for KCNT1-related DEEs. Therefore, building on a previous study by the same group performed in homozygous KI animals, and considering that the largest majority of pathogenic KCNT1 variants in humans occur in heterozygosis, the Authors have investigated the effects of heterozygous Kcnt1-Y777H expression on KNa currents and neuronal physiology among cortical glutamatergic and the 3 main classes of GABAergic neurons, namely those expressing vasoactive intestinal polypeptide (VIP), somatostatin (SST), and parvalbumin (PV), crossing KCNT1-Y777H mice with PV-, SST- and PV-cre mouse lines, and recording from GABAergic neurons identified by their expression of mCherry (but negative for GFP used to mark excitatory neurons).

The results obtained revealed heterogeneous effects of the variant on KNa and action potential firing rates in distinct neuronal subpopulations, ranging from no change (glutamatergic and VIP GABAergic) to decreased excitability (SST GABAergic) to increased excitability (PV GABAergic). In particular, modelling and in vitro data revealed that an increase in persistent Na current occurring in PV neurons was sufficient to overcome the effects of KCNT1 GOF and cause an overall increase in AP generation.

Strengths:

The paper is very well written, the results clearly presented and interpreted, and the discussion focuses on the most relevant points.

The recordings performed in distinct neuronal subpopulations (both in primary neuronal cultures and, for some subpopulations, in cortical slices, are a clear strength of the paper. The finding that the same variant can cause opposite effects and trigger specific homeostatic mechanisms in distinct neuronal populations is very relevant for the field, as it narrows the existing gap between experimental models and clinical evidence.

Weaknesses:

My main concern regarding the epileptic phenotype of the heterozygous mice investigated has been clarified in the revision, where the infrequent occurrence of seizures is more clearly stated. Also, a more detailed statistical analysis of the modeled neurons has been added in the revision.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

This is a very clear and thorough piece of work, and the authors are to be congratulated on this. My one remaining suggestion would be to make an explicit statement about whether increased sodium influx through INaP channels, which is thought to activate KNa channels, would be likely to increase KNa current in these neurons (see comment 1B).

Please see response to comment 1B.

Reviewer #2 (Recommendations For The Authors):

This revised manuscript is significantly improved and addresses most of my concerns. However, I would still recommend including the ex vivo slice recordings in mutant PV-interneurons as the authors proposed in their rebuttal. The I-V recordings using sequential TTX and VU170 blockade in WT SST and PV-interneurons that are provided in the rebuttal are interesting and may point to a preferential expression of persistent sodium currents in PV-interneurons normally. It would be helpful to readers as a supplemental figure.

As proposed in the rebuttal, we are currently recording PV neurons using ex vivo slice preparations from WT and Kcnt1-YH Het mice. We look forward to including those data in a future manuscript.

We agree with the reviewer that the differences in INaP between WT PV and SST neurons are notable. The data provided in the rebuttal were only from 5 neurons/group, and they were meant to illustrate a side-by-side comparison of TTX and VU170 subtraction methods to assess KNa currents. However, in Figure 7 of the manuscript, we performed more robust measurements of INaP and observed differences in the current between WT PV and SST neurons. Thus, we’ve added the following sentence to the Results section:

“Interestingly, the mean peak amplitude of INaP in WT PV neurons was 70% larger than that in WT SST neurons (-1.42 ± 0.16 vs. -0.85 ± 0.07 pA/pF; Fig. 7B and 7D), suggesting there may be differences in sodium channel expression, localization, or regulation inherent to each neuron type that confer their differential response to KCNT1 GOF.”

References

Grubb, M. S., & Burrone, J. (2010). Activity-dependent relocation of the axon initial segment fine-tunes neuronal excitability. Nature, 465(7301), 1070-1074. https://doi.org/10.1038/nature09160

Hage, T. A., & Salkoff, L. (2012). Sodium-activated potassium channels are functionally coupled to persistent sodium currents. J Neurosci, 32(8), 2714-2721. https://doi.org/10.1523/JNEUROSCI.5088-11.2012

Kuba, H., Oichi, Y., & Ohmori, H. (2010). Presynaptic activity regulates Na(+) channel distribution at the axon initial segment. Nature, 465(7301), 1075-1078. https://doi.org/10.1038/nature09087

eLife assessment

Goswami and colleagues used rod-specific Gls1 (the gene encoding glutaminase 1) knockout mice to investigate the role of GLS1 in photoreceptor health when GLS1 was deleted from developing or adult photoreceptor cells. This study is important as it shows the critical role of glutamine catabolism in photoreceptor cell health using in vivo model systems. The evidence supporting the authors' claims is convincing. The current manuscript would further benefit from validating the evidence with additional supporting data from IND-cKO with tamoxifen induction at adult age, testing GLS1 activity to provide glutamate for synaptic transmission, and examining metabolic crosstalk between RPE and neural retinas.

Reviewer #1 (Public Review):

Summary:

The authors show for the first time that deleting GLS from rod photoreceptors results in the rapid death of these cells. The death of photoreceptor cells could result from loss of synaptic activity because of a decrease in glutamate, as has been shown in neurons, changes in redox balance, or nutrient deprivation.

Strengths:

The strength of this manuscript is that the author shows a similar phenotype in the mice when Gls was knocked out early in rod development or the adult rod. They showed that rapid cell death is through apoptosis, and there is an increase in the expression of genes responsive to oxidative stress.

Weaknesses:

In this manuscript, the authors show a "metabolic dependency of photoreceptors on glutamine catabolism in vivo". However, there is a potential bias in their thinking that glutamine metabolism in rods is similar to cancer cells where it feeds into the TCA cycle. They should consider that as in neurons, GLS1 activity provides glutamate for synaptic transmission. The modest rescue shown by providing α-ketoglutarate in the drinking water suggests that glutamine isn't a key metabolic substrate for rods when glucose is plentiful. The ERG studies performed on the iCre-Glsflox/flox mice showed a large decrease in the scotopic b wave at saturating flashes which could indicate a decrease in glutamate at the rod synapse as stated by the authors. While EM micrographs of wt and iCre-Glsflox/flox mice were shown for the outer retina at p14, the synapse of the rods needs to be examined by EM.

The authors note that the outer segments are shorter but they do not address whether there is a decrease in the number of cones.

Rod-specific Gls ko mice with an inducible promoter were generated by crossing the Pde6g-CreERT2 and homozygous for either the WT or floxed Gls allele (IND-cKO). In Figure 3 the authors document that by western blots and antibody labeling the GLS1 expression is lost in the IND-cKO 10 days post tamoxifen. OCT images show a decrease in the thickness of the outer nuclear layer between 17 and 38 days post-TAM. Ergs should be performed on the animals at 10 and 30 days post TAM, before and after major structural changes in rod photoreceptor cells, to determine if changes in light-stimulated responses are observed. These studies could help to parse out the cause of photoreceptor cell death.

The studies in Figure 4 were all performed on iCre-Glsflox/flox and control mice at p14, why weren't the IND-cKO mice used for these studies since the findings would not be confounded by development?

In all rescue studies, the endpoint was an ONL thickness, which only addressed rod cell death. The authors should also determine whether there are small improvements in the ERG, which would distinguish the role of GLS in preventing oxidative stress.

Reviewer #2 (Public Review):

Summary:

Photoreceptor neurons are crucial for vision, and discovering pathways necessary for photoreceptor health and survival can open new avenues for therapeutics. Studies have shown that metabolic dysfunction can cause photoreceptor degeneration and vision loss, but the metabolic pathways maintaining photoreceptor health are not well understood. This is a fundamental study that shows that glutamine catabolism is critical for photoreceptor cell health using in vivo model systems.

Strengths:

The data are compelling, and the consideration of potential confounding factors (such as glutaminase 2 expression) and additional experiments to examine the synaptic connectivity and inner retina added strength to this work. The authors were also careful not to overstate their claims, but to provide solid conclusions that fit the results and data provided in their study. The findings linking asparagine supplementation and the inhibition of the integrated stress response to glutamine catabolism within the rod photoreceptor cell are intriguing and innovative. Overall, the authors provide convincing data to highlight that photoreceptors utilize various fuel sources to meet their metabolic needs, and that glutamine is critical to these cells for their biomass, redox balance, function, and survival.

Weaknesses:

Recent studies have explored the metabolic "crosstalk" that exists within the mammalian retina, where metabolites are transferred between the various retinal cells and the retinal pigment epithelium. It would be of interest to test whether the conditional knockout mice have changes in metabolism (via qPCR such as shown in Figure 4 - Supplemental Figure 1) within the retinal pigment epithelium that may be contributing to the authors' findings in the neural retina. Additionally, the authors have very compelling data to show that inhibition of eIF2a or supplementation with asparagine can delay photoreceptor death via OCT measurements in their conditional knockout mouse model (Figure 6G, H). However, does inhibition of eIF2a or asparagine adversely impact the WT retina? It would also be impactful to know whether this has a prolonged effect, or if it is short-term, as this would provide strength to potential therapeutic targeting of these pathways to maintain photoreceptor health.

Reviewer #3 (Public Review):

Summary:

The authors explored the role of GLS, a glutaminase, which is an enzyme that catalyzes the conversion of glutamine to glutamate, in rod photoreceptor function and survival. The loss of GLS was found to cause rapid autonomous death of rod photoreceptors.

Strengths:

Interesting and novel phenotype. Two types of cre-lines were rigorously used to knockout the Gls gene in rods. Both of the conditional knockouts led to a similar phenotype, i.e. rod death. Histology and ERG were carefully done to characterize the loss of rods over specific ages. A necessary metabolomic study was performed and appreciated. Some rescue experiments were performed and revealed possible mechanisms.

Weaknesses:

No major weaknesses were identified. The mechanism of GLS-loss-induced rod death seems not fully elucidated by this study but could be followed up in the future, and the same for GLS's role in cones.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors show for the first time that deleting GLS from rod photoreceptors results in the rapid death of these cells. The death of photoreceptor cells could result from loss of synaptic activity because of a decrease in glutamate, as has been shown in neurons, changes in redox balance, or nutrient deprivation. 

Strengths: 

The strength of this manuscript is that the author shows a similar phenotype in the mice when Gls was knocked out early in rod development or the adult rod. They showed that rapid cell death is through apoptosis, and there is an increase in the expression of genes responsive to oxidative stress. 

We thank the reviewer for their time reviewing the manuscript and their comments regarding the potential mechanism(s) by which rod photoreceptors rapidly degenerate upon knockout of GLS.

Weaknesses: 

In this manuscript, the authors show a "metabolic dependency of photoreceptors on glutamine catabolism in vivo". However, there is a potential bias in their thinking that glutamine metabolism in rods is similar to cancer cells where it feeds into the TCA cycle. They should consider that as in neurons, GLS1 activity provides glutamate for synaptic transmission. The modest rescue shown by providing α-ketoglutarate in the drinking water suggests that glutamine isn't a key metabolic substrate for rods when glucose is plentiful. The ERG studies performed on the iCre-Glsflox/flox mice showed a large decrease in the scotopic b wave at saturating flashes which could indicate a decrease in glutamate at the rod synapse as stated by the authors. While EM micrographs of wt and iCre-Glsflox/flox mice were shown for the outer retina at p14, the synapse of the rods needs to be examined by EM. 

We agree with the reviewer that in the presence of sufficient glucose, it appears a lack of GLS-driven glutamine (Gln) catabolism does not drastically alter the levels of TCA cycle metabolites or mitochondrial function as we demonstrated in Figure 4, and supplementation with alpha-ketoglutarate improved outer nuclear layer thickness by only a small amount as observed in Figure 5e. Hence, as we stated in the Results and Discussion, at least in the mouse where Gls is selectively deleted from rod photoreceptors by crossing Glsfl/fl mice with Rho-Cre mice (Glsfl/fl; Rho-Cre+, cKO), Gln’s role in supporting the TCA cycle is not the major mechanism by which rod photoreceptors utilize Gln to suppress apoptosis.

With regards to GLS-driven Gln catabolism providing glutamate (Glu) for synaptic transmission, we again agree with the reviewer that Glu is an important excitatory neurotransmitter, but it is also a key metabolite necessary for the synthesis of glutathione, amino acids, and proteins. As noted and discussed at length in the manuscript, a lack of GLS-driven Gln catabolism in rod photoreceptors leads to reduced levels of oxidized glutathione (Figure 4D) possibly signaling an overall reduction in the biosynthesis of glutathione as Glu is directly and indirectly responsible for its synthesis. Furthermore, Gln and GLS-derived Glu play a central role in the biosynthesis of several nonessential amino acids and proteins. To this end, we see a reduction in the level of Glu, which is the product of the GLS reaction and further confirms the loss of GLS function. We also noted a significant decrease in aspartate (Asp), which can be constructed from the carbons and nitrogens of Gln as discussed at length in the manuscript (Figure 6A). Finally, we noted a significant decrease in global protein synthesis in the cKO retina as compared to the wild-type animal as well (Figure 6E). Therefore, the data suggest that GLS-driven Gln catabolism is critical for amino acid metabolism and protein synthesis and to some degree redox balance; although, the small but statistically significant changes in oxidized glutathione, NADP/NADPH, and redox gene expression may not fully account for the rapid and complete photoreceptor degeneration observed. Future studies are necessary to shed light on the role of redox imbalance in this novel transgenic mouse model.

Glu also plays a role in synaptic transmission, and we considered this scenario as described in Figure 1 – figure supplement 5. Here, the synaptic connectivity between photoreceptors and the inner retina did not demonstrate significant differences in the labeling of photoreceptor synaptic membranes in the outer plexiform layer nor alterations in the labeling of a key protein (Bassoon) in ribbon synapses. These data suggest that the synaptic connectivity between photoreceptors and second-order neurons was unaltered at P14 in the cKO retina, which is the time just prior to rapid photoreceptor degeneration. We agree, though, that to obtain greater insight into the alterations in the ribbon synapse, EM images can be examined. The EM images shown in Figure 1 – figure supplement 4 are from P21 and will be utilized to assess the ribbon synapse for the revised version of the article.

With regards to the ERG changes noted in Figure 2, we agree with the reviewer that a large decrease was noted in the scotopic b-wave at P21 and P42 in the cKO. However, an even larger reduction in the scotopic a-wave was noted at these ages as well. In animal models that disrupt photoreceptor synaptic function (Dick et al. Neuron. 2003; Johnson et al. J Neuroscience. 2007; Haeseleer et al. Nature Neuroscience. 2004; Chang et al. Vis Neurosci. 2006), a more negative ERG pattern is typically observed with the b-wave altered to a much larger degree than the a-wave. Additionally, in these models that disrupt photoreceptor synaptic transmission, the overall structure of the retina with respect to thickness is maintained (Dick et al. Neuron. 2003) or noted to have modest changes in the outer plexiform layer within the first two months of age with the outer nuclear layer not significantly altered until 8-10 months of age (Haeseleer et al. Nature Neuroscience. 2004). In contrast, a rapid decline in the outer nuclear layer thickness was observed in the cKO retina after P14 likely contributing to the ERG changes noted in Figure 2.  Also, Gln is catabolized to Glu primarily by GLS as suggested by the approximately 50% reduction in Glu levels in the cKO retina (Figure 6A), but other enzymes are also capable of catabolizing Gln to Glu, so Glu levels in the rod photoreceptors are unlikely to be zero. Coupling this with the fact that rods are equipped with a self-sufficient Glu recollecting system at their synaptic terminals (Hasegawa et al. Neuron. 2006; Winkler et al. Vis Neurosci. 1999) and that GLS activity is at least two-fold higher in the photoreceptor inner segments, which support energy production and metabolism, than any other layer in the retina (Ross et al. Brain Res. 1987) suggests that altered synaptic transmission secondary to reduced levels of Glu likely does not account in full for the rapid and robust photoreceptor degeneration observed in the cKO retina.

The authors note that the outer segments are shorter but they do not address whether there is a decrease in the number of cones. 

The number of cones will be assessed and provided in the revised version of the article.

Rod-specific Gls ko mice with an inducible promoter were generated by crossing the Pde6g-CreERT2 and homozygous for either the WT or floxed Gls allele (IND-cKO). In Figure 3 the authors document that by western blots and antibody labeling the GLS1 expression is lost in the IND-cKO 10 days post tamoxifen. OCT images show a decrease in the thickness of the outer nuclear layer between 17 and 38 days post-TAM. Ergs should be performed on the animals at 10 and 30 days post TAM, before and after major structural changes in rod photoreceptor cells, to determine if changes in light-stimulated responses are observed. These studies could help to parse out the cause of photoreceptor cell death. 

We agree with the reviewer that the IND-cKO is a useful tool to help parse out the cause of photoreceptor cell death in this model as well as shed light on the role of GLS-driven Gln catabolism in photoreceptor synaptic transmission as discussed at length above. Hence, ERG analyses will be provided for these animals in the revised version of the article.

The studies in Figure 4 were all performed on iCre-Glsflox/flox and control mice at p14, why weren't the IND-cKO mice used for these studies since the findings would not be confounded by development? 

To gain further insight into the role of GLS-driven Gln catabolism in the maintenance of rod photoreceptors as compared to their development/maturation, we will provide ERG and targeted metabolomic analyses of the IND-cKO retina in the revised version of the article.

In all rescue studies, the endpoint was an ONL thickness, which only addressed rod cell death. The authors should also determine whether there are small improvements in the ERG, which would distinguish the role of GLS in preventing oxidative stress. 

Optical coherence tomography (OCT) provides a sensitive in vivo method to detect small changes in retinal thickness without potential artifacts incurred through histological processing. Considering the Gls cKO retina demonstrates significant and rapid photoreceptor degeneration, we wanted to assess pathways that may be critical to photoreceptor survival downstream of GLS-driven Gln catabolism using rescue experiments with pharmacologic treatment or metabolite supplementation. That said, disruption of GLS-driven Gln catabolism may also significantly alter rod photoreceptor function beyond that which is secondary to photoreceptor cell death. As such, changes in ERG will be examined and provided in the revised version of the article for certain rescue experiments that demonstrated a robust change in ONL thickness.

Reviewer #2 (Public Review): 

Summary: 

Photoreceptor neurons are crucial for vision, and discovering pathways necessary for photoreceptor health and survival can open new avenues for therapeutics. Studies have shown that metabolic dysfunction can cause photoreceptor degeneration and vision loss, but the metabolic pathways maintaining photoreceptor health are not well understood. This is a fundamental study that shows that glutamine catabolism is critical for photoreceptor cell health using in vivo model systems. 

Strengths: 

The data are compelling, and the consideration of potential confounding factors (such as glutaminase 2 expression) and additional experiments to examine the synaptic connectivity and inner retina added strength to this work. The authors were also careful not to overstate their claims, but to provide solid conclusions that fit the results and data provided in their study. The findings linking asparagine supplementation and the inhibition of the integrated stress response to glutamine catabolism within the rod photoreceptor cell are intriguing and innovative. Overall, the authors provide convincing data to highlight that photoreceptors utilize various fuel sources to meet their metabolic needs, and that glutamine is critical to these cells for their biomass, redox balance, function, and survival. 

We greatly appreciate the reviewer’s thoughtful comments and time spent reviewing this manuscript.

Weaknesses: 

Recent studies have explored the metabolic "crosstalk" that exists within the mammalian retina, where metabolites are transferred between the various retinal cells and the retinal pigment epithelium. It would be of interest to test whether the conditional knockout mice have changes in metabolism (via qPCR such as shown in Figure 4 - Supplemental Figure 1) within the retinal pigment epithelium that may be contributing to the authors' findings in the neural retina. Additionally, the authors have very compelling data to show that inhibition of eIF2a or supplementation with asparagine can delay photoreceptor death via OCT measurements in their conditional knockout mouse model (Figure 6G, H). However, does inhibition of eIF2a or asparagine adversely impact the WT retina? It would also be impactful to know whether this has a prolonged effect, or if it is short-term, as this would provide strength to potential therapeutic targeting of these pathways to maintain photoreceptor health. 

We agree with the reviewer that metabolic communication in the outer retina is crucial to the function and survival of both photoreceptors and RPE. We will perform qRT-PCR on the eyecups of these mice to assess any changes in the expression of metabolic genes. This data will be provided in the revised manuscript.

We have data demonstrating systemic treatment with ISRIB does not adversely impact the anatomy of the wild-type retina; this data will be included in the revised manuscript as a supplement to Figure 6. Additionally, we have recent data to suggest that the effect of ISRIB extends beyond P21 in the cKO mouse. This data will be included in the revised manuscript.

Reviewer #3 (Public Review): 

Summary: 

The authors explored the role of GLS, a glutaminase, which is an enzyme that catalyzes the conversion of glutamine to glutamate, in rod photoreceptor function and survival. The loss of GLS was found to cause rapid autonomous death of rod photoreceptors. 

Strengths: 

Interesting and novel phenotype. Two types of cre-lines were rigorously used to knockout the Gls gene in rods. Both of the conditional knockouts led to a similar phenotype, i.e. rod death. Histology and ERG were carefully done to characterize the loss of rods over specific ages. A necessary metabolomic study was performed and appreciated. Some rescue experiments were performed and revealed possible mechanisms. 

We thank the reviewer for their comments and appreciation of the methods utilized herein to address the role of GLS-driven Gln catabolism in rod photoreceptors.

Weaknesses: 

No major weaknesses were identified. The mechanism of GLS-loss-induced rod death seems not fully elucidated by this study but could be followed up in the future, and the same for GLS's role in cones.

We agree with the reviewer that the downstream metabolic and molecular mechanisms by which Gln catabolism impacts rod photoreceptor health are not fully elucidated. Defining these mechanisms will advance our understanding of photoreceptor metabolism and identify therapeutic targets promoting photoreceptor resistance to stress. Future studies are underway to uncover these mechanisms. Additionally, while outside the scope of the current manuscript, we have generated mice lacking GLS in cone photoreceptors specifically and are currently elucidating the role of GLS in cone photoreceptor metabolism, function, and survival. These results will be published in a separate manuscript.

eLife assessment

This study is a potentially important contribution to the field of protein biosynthesis pathways and their link to aging, especially regarding the thorough analysis of variation in measures expected to correlate with elongation rate in old and new daughter cells derived from old and new mother cells. However, the imaging results, analysis, and methodologies are incomplete, as in its current form several key questions remain unanswered.

Reviewer #1 (Public Review):

The research by Lin Chao, Chun Kuen Chen, Chao Shi, and Camilla U. Rang addresses the asymmetric distribution of ribosomes in single E. coli cells during aging by time-lapse microscopy, as well as its correlation to protein misfolding. The presented research is an important contribution to the field of protein biosynthesis pathways and their link to aging, especially in regard to the thorough analysis of variation in cells elongation rate in old and new daughter cells derived from old and new mother cells.

Comments on current version:

I thank the authors for their thoughtful responses. Yet the centrality of protein aggregate distribution analysis to this manuscript requires further evidence to support the link to ribosome asymmetrical distribution and aging.

The authors suggest this is beyond the scope of this study. This then requires a major revising of the study, as in its current form, it is one of its main claims.

Author response:

The following is the authors’ response to the original reviews.

Response to reviewers

A general comment was that this study left several key questions unanswered, in particular the causal mechanism for the reported ribosomal distributions.  We have been interested in the evolution of asymmetric bacterial growth and aging for many years. However, a motivational difference is that we are more interested in the evolutionary process, and evolution by natural selection works on the phenotype.  Thus, we wanted to start with the phenotype closest to fitness, appropriately defined for the conditions, work downwards.  We examined first the asymmetry of elongation rates in single cells, then gene products, and now ribosomes.  As we have pointed out, our demonstration of ribosomal asymmetry shows that the phenomenon was not peculiar and unique to the gene products we examined.  Rather, the asymmetry is acting higher up in the metabolic network and likely affecting all genes.  We find such conceptual guidance to be important.  In the ideal world, of course we would have liked to have worked out the causal mechanisms in one swoop.  In a less than ideal situation, it is a subjective decision as where to stop.  We believe that the publication of this manuscript is more than appropriate at this juncture.  We work at the interface of evolutionary theory and microbiology.  Our results could appeal to both fields.  If we attract new researchers, progress could be accelerated.  Could the delay caused by publishing only completed stories slow the rate of discovery?  These questions are likely as old as science (e.g., https://telliamedrevisited.wordpress.com/2021/01/28/how-not-to-write-a-response-to-reviewers/).

We present below our response to specific comments by reviewers.  We have not added a new discussion of papers suggested by Reviewer #1 because we feel that the speculations would have been too unfocused.  We were already criticized for speculation in the Discussion about a link between aggregate size and ribosomal density.

Respond to Major comments by Reviewer #1.

a) Fig. 1 only shows 2 divisions (rather than 3 as per Rev1) to avoid an overly elaborate figure.  We have added text to the figure legend that the old and new poles and daughters in the subsequent 3, 4, 5, 6, and 7 generations can be determined by following the same notations and tracking we presented for generations 1 and 2 in Fig. 1.  For example, if we know the old and new poles of any of the four daughters after 2 divisions (as in Fig. 1), and allow that daughter to elongate, become a mother, and divide to produce 2 “grand-daughters”, the polarity of the grand-daughters can also be determined.

b) Because division times were normalized and analyzed as quartiles, the raw values were never used.  Rather than annotating unused values, we have provided the mean division times in the Material and Methods section on normalization to provide representative values.

c) We did not quantify in our study the changes over generations for three reasons.  First, the sample sizes for the first generations (cohorts of 1, 2, 4, and 8 cells) are statistically small.  Second, and most importantly, cells on an agar pad in a microscope slide, despite being inoculated as fresh exponentially growing cells, experience a growth lag, as all cells transferred to a new physiological condition.  Thus, to be safe, we do not collect data from cohorts 1, 2, 4, and 8 to ensure that our cells are as much as possible physiologically uniform.  Lastly, as we noted in the Material and Methods they also slow down after 7 generations (128 cells).  Thus, we have collected ribosome and length measurements primarily from cohorts 16, 32, 64, and 128.  Measurable cells from the 128 cohort are actually rare because a colony with that many cells often starts to form double layers, which are not measurable.  Most of our measurements came from the 16, 32, and 64 cohorts, in which case a time series would not be meaningful.  Some of these details were not included in our manuscript but have been added to the Material and Methods (Microscopy and time-lapse movies).  For these reasons we have not added a time series as requested by the reviewer.

d) We have added the additional figure as requested, but as a supplement rather than in the main article (Supplemental Materials Fig. S1).  This figure showed the normalized density of ribosomes along the normalized length of old and new daughters.  The density was continuous rather than quartiles.  This figure was included in the original manuscript, but readers recommended that it be removed because the all the analyzed data had been done with quartiles.  Readers felt mislead and confused.

eLife assessment

This valuable manuscript reports on the relationship between GTP hydrolysis parameters and kinase activity of LRRK2, which is associated with Parkinson's disease. The authors provide a detailed accounting of the catalytic efficiency of the ROC GTPase domain of pathogenic variants of LRRK2, in comparison with the wild-type enzyme. The authors propose that phosphorylation of T1343 inhibits kinase activity and influences monomer-dimer transitions, but the experimental evidence is currently incomplete.

Reviewer #1 (Public Review):

Summary:

This study presents careful biochemical experiments to understand the relationship between LRRK2 GTP hydrolysis parameters and LRRK2 kinase activity. The authors report that incubation of LRRK2 with ATP increases the KM for GTP and decreases the kcat. From this they suppose an autophosphorylation process is responsible for enzyme inhibition. LRRK2 T1343A showed no change, consistent with it needing to be phosphorylated to explain the changes in G-domain properties. The authors propose that phosphorylation of T1343 inhibits kinase activity and influences monomer-dimer transitions.

Strengths:

The strengths of the work are the very careful biochemical analyses and interesting results for wild type LRRK2.

Weaknesses:

The conclusions related to the involvement of a monomer-dimer transition are to this reviewer, premature and an independent method needs to be utilized to bolster this aspect of the story.

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study presents careful biochemical experiments to understand the relationship between LRRK2 GTP hydrolysis parameters and LRRK2 kinase activity. The authors report that incubation of LRRK2 with ATP increases the KM for GTP and decreases the kcat. From this they suppose an autophosphorylation process is responsible for enzyme inhibition. LRRK2 T1343A showed no change, consistent with it needing to be phosphorylated to explain the changes in G-domain properties. The authors propose that phosphorylation of T1343 inhibits kinase activity and influences monomer-dimer transitions.

Strengths:

Strengths of the work are the very careful biochemical analyses and interesting result for wild type LRRK2.

Weaknesses:

The conclusions related to involvement of a monomer-dimer transition are to this reviewer, premature and an independent method needs to be utilized to bolster this aspect of the story.

The monomer-dimer transition has been described in detail in our recent preprint Guaitoli et al., 2023 (doi: 10.1101/2023.08.11.549911). Where we in addition to mass-photometry have used blue-native page. Furthermore, to better elucidate the mechanistic impact of the phosphorylation, we have provided AlphaFold3 models. As the new AlphaFold version allows to consider PTMs as well as small molecules, we compared the models of the GDP vs the GTP-state of pT1343 LRRK2. Interestingly, the AF3 model suggests, that the phosphate of the pT1343 is orientated inwards thereby substituting the gamma phosphate (see Supplementary Figure 5). This finding is in well agreement with MD simulations published recently (Stormer et al., 2023, doi: 10.1042/BCJ20230126). As we are determining GTP hydrolysis in a multi turnover situation, the pT1343 might hamper the hydrolysis by competing with GTP re-binding. Final models have been deposited on Zenodo (https://doi.org/10.5281/zenodo.11242230).

Reviewer #2 (Public Review):

As discussed in the original review, this manuscript is an important contribution to a mechanistic understanding of LRRK2 kinase. Kinetic parameters for the GTPase activity of the ROC domain have been determined in the absence/presence of kinase activity. A feedback mechanism from the kinase domain to GTP/GDP hydrolysis by the ROC domain is convincingly demonstrated through these kinetic analyses. However, a regulatory mechanism directly linking the T1343 phosphosite and a monomer/dimer equilibrium is not fully supported. The T1343A mutant has reduced catalytic activity and can form similar levels of dimer as WT. The revised manuscript does point out that other regulatory mechanisms can also play a role in kinase activity and GTP/GDP hydrolysis (Discussion section). The environmental context in cells cannot be captured from the kinetic assays performed in this manuscript, and the introduction contains some citations regarding these regulatory factors. This is not a criticism, the detailed kinetics here are rigorous, but it is simply a limitation of the approach. Caveats concerning effects of membrane localization, Rab/14-3-3 proteins, WD40 domain oligomers, etc... should be given more prominence than a brief (and vague) allusion to 'allosteric targeting' near the end of the Discussion.

We thank the reviewer for the evaluation of the manuscript and suggestions made. With respect to the mentioned caveats regarding the complex regulation of LRRK2 in its native cellular environment by effectors, localization and effector binding, we have revised the discussion, accordingly. We nevertheless, want to emphasize that the phospho-null mutant T1343A leads to an increase in Rab10 phosphorylation in cells, demonstrating a relevance of this regulatory mechanism under near physiological conditions (shown in Figure 6). In addition, to further elucidate the molecular mechanisms of the p-loop phosphorylation at T1343, we have performed AlphaFold3 modelling allowing to include phosphoresidues (see comment above, Supplemental Figure 5).

Specific comments

(1) The revised version is better organized with respect to the significance of monomer/dimer equilibrium and the relevance of the GTP-binding region of ROC domain that encompasses the T1343 phospho-site. The relevance of monomers/dimers of LRRK2 from previous studies is better articulated and readers are able to follow the reasoning for the various mutations.

We thank the reviewer for the positive feedback. 

(2) As a suggestion I would change the following on page 6 to clarify for readers: "...would show no change in kcat and KM values upon in vitro ATP treatment" to:

"...would show no change in kcat and KM values for GTP hydrolysis upon in vitro

ATP treatment"

(3) The levels of dimer in WT (+ATP) and T1343A (+/- ATP) are the same, about 40-45%. These data are cited when the authors state that ATP-induced monomerization is 'abolished' (page 6). My suggestion is to re-phrase this conclusion for consistency with data (Fig 5). For example, one can state that 'ATP incubation does not affect the percentage of dimer for the T1343A variant of LRRK2'. This would be similar to the authors' description of these data on page 8 - 'no difference in dimer formation upon ATP treatment'.

We thank the reviewer for the suggestions. We revised the manuscript accordingly. Changes have been highlighted in the version provided for reviewing purposes.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Minor revisions

-change 'Although functional work on LRRK2 has been made significant progress...' to 'Although there is significant progress toward functional characterization of LRRK2...'

-change 'exact mechanisms' to 'precise mechanisms', and similarly 'exact interplay' to 'precise interplay'

-change 'On a contrary' to 'On the contrary' in Discussion

-change remained to be unchanged' to 'remains unchanged', page 8

We thank the reviewer for having noticed this. We have revised the manuscript accordingly.

eLife assessment

This study provides valuable new insights into insect cognition and problem-solving in bumblebees. The authors present convincing evidence that bumblebees lack causal understanding in a string-pulling task, and find support for bumblebees instead using image-matching for this task.

Reviewer #1 (Public Review):

Summary:

In this paper the researchers aimed to address whether bees causally understand string-pulling through a series of experiments. I first briefly summarize what they did:

- In experiment 1, the researchers trained bees without string and then presented them with flowers in the test phase that either had connected or disconnected strings, to determine what their preference was without any training. Bees did not show any preference.

- In experiment 2, bees were trained to have experience with string and then tested on their choice between connected vs. disconnected string.

- Experiment 3 was similar except that instead of having one option which was an attached string broken in the middle, the string was completely disconnected from the flower.

- In experiment 4, bees were trained on green strings and tested on white strings to determine if they generalize across color.

- In experiment 5, bees were trained on blue strings and tested on white strings.

- In experiment 6, bees were trained where black tape covered the area between the string and the flower (i.e. so they would not be able to see/ learn whether it was connected or disconnected).

- In experiments 2-6, bees chose the connected string in the test phase.

- In experiment 7, bees were trained as in expt 3 and then tested where string was either disconnected or coiled i.e. still being 'functional' but appearing different.

- In experiment 8, bees were trained as before and then tested on string that was in a different coiled orientation, either connected or disconnected.

- In experiments 7 and 8 the bees showed no preference.

Strengths:

I appreciate the amount of work that has gone into these experiments and think they are a nice, thorough set of experiments. I enjoyed reading the paper and felt that it was overall well-written and clear. I think experiment 1 shows that bees do not have an untrained understanding of the function of the string in this context. The rest of the experiments indicate that with training, bees have a preference for unbroken over broken string and likely use visual cues learned during training to make this choice. They also show that as in other contexts, bees readily generalize across different colors.

The 'weaknesses' that I previously listed were dealt with by the authors in the revised version of the manuscript. I think the only point that we disagreed on was relating to the ecological relevance of the task to the bees.

Here is my previous comment:

I think the paper would be made stronger by considering the natural context in which the bee performs this behavior. Bees manipulate flowers in all kinds of contexts, and scrabble with their legs to achieve nectar rewards. Rather than thinking that it is pulling a string, my guess would be that the bee learns that a particular motor pattern within their usual foraging repertoire (scrabbling with legs), leads to a reward. I don't think this makes the behavior any less interesting - in fact, I think considering the behavior through an ecological lens can help make better sense of it.

The authors disagreed, writing the following:

"Here we respectfully disagree. The solving of Rubik s cube by humans could be said to be version of finger movements naturally required to open nuts or remove ticks from fur, but this is somewhat beside the point: it s not the motor<br /> sequences that are of interest, but the cognition involved. A general approach in work on animal intelligence and cognition is to deliberately choose paradigms that are outside the animals daily routines this is what we have done here, in asking whether there is means end comprehension in bee problem solving. Like comparable studies on this question in other animals, the experiments are designed to probe this question, not one of ecological validity."

I think the difference would be that humans know that they are doing a rubik's cube whereas I do not think that the bee knows that it is pulling string- I think the bee thinks that it is foraging on a flower. Therefore, I stand by my statement that I think it's worth considering what the bee is experiencing in this task and how it relates to what it would be doing while foraging. I think that as animal cognition researchers we can design tasks that are distinct from what the animal would naturally encounter to ask specific questions about what they are thinking- but that we can never remove the ecological context since the animal will always be viewing the task through that lens. However, I think this may be a philosophical difference in opinion and I am happy with the manuscript as it stands.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, the researchers aimed to address whether bees causally understand string-pulling through a series of experiments. I first briefly summarize what they did:

- In experiment 1, the researchers trained bees without string and then presented them with flowers in the test phase that either had connected or disconnected strings, to determine what their preference was without any training. Bees did not show any preference.

- In experiment 2, bees were trained to have experience with string and then tested on their choice between connected vs. disconnected string.

- experiment 3 was similar except that instead of having one option which was an attached string broken in the middle, the string was completely disconnected from the flower.

- In experiment 4, bees were trained on green strings and tested on white strings to determine if they generalize across color.

- In experiment 5, bees were trained on blue strings and tested on white strings.

- In experiment 6, bees were trained where black tape covered the area between the string and the flower (i.e. so they would not be able to see/ learn whether it was connected or disconnected).

- In experiments 2-6, bees chose the connected string in the test phase.

- In experiment 7, bees were trained as in experiment 3 and then tested where the string was either disconnected or coiled i.e. still being 'functional' but appearing different.

- In experiment 8, bees were trained as before and then tested on a string that was in a different coiled orientation, either connected or disconnected.

- In experiments 7 and 8 the bees showed no preference.

Strengths:

I appreciate the amount of work that has gone into this study and think it contains a nice, thorough set of experiments. I enjoyed reading the paper and felt that overall it was well-written and clear. I think experiment 1 shows that bees do not have an untrained understanding of the function of the string in this context. The rest of the experiments indicate that with training, bees have a preference for unbroken over broken string and likely use visual cues learned during training to make this choice. They also show that as in other contexts, bees readily generalize across different colors.

Weaknesses:

(1) I think there are 2 key pieces of information that can be taken from the test phase - the bees' first choice and then their behavior across the whole test. I think the first choice is critical in terms of what the bee has learned from the training phase - then their behavior from this point is informed by the feedback they obtain during the test phase. I think both pieces of information are worth considering, but their behavior across the entire test phase is giving different information than their first choice, and this distinction could be made more explicit. In addition, while the bees' first choice is reported, no statistics are presented for their preferences.

We agree with the reviewer that the first choice is critical in terms of what the bumblebees have learned from the training phase. We analyzed the bees’ first choice in Table 1, and we added the tested videos. The entire connected and disconnected strings were glued to the floor, the bees were unable to move either the connected or disconnected strings, and avoid learning behavior during the tests. We added the data of bee's each choice in the Supplementary table.

(2) It seemed to me that the bees might not only be using visual feedback but also motor feedback. This would not explain their behavior in the first test choice, but could explain some of their subsequent behavior. For example, bees might learn during training that there is some friction/weight associated with pulling the string, but in cases where the string is separated from the flower, this would presumably feel different to the bee in terms of the physical feedback it is receiving. I'd be interested to see some of these test videos (perhaps these could be shared as supplementary material, in addition to the training videos already uploaded), to see what the bees' behavior looks like after they attempt to pull a disconnected string.

We added supplementary videos of testing phase. As noted in General Methods, both connected and disconnected strings were glued to the floor to prevent the air flow generated by flying bumblebees’ wings from changing the position of the string during the testing phase. The bees were unable to move either the connected or disconnected strings during the tests, and only attempted to pull them. Therefore, the difference in the friction/weight of pulling the both strings cannot be a factor in the test.

(3) I think the statistics section needs to be made clearer (more in private comments).

We changed the statistical analysis section as suggested by the reviewer.

(4) I think the paper would be made stronger by considering the natural context in which the bee performs this behavior. Bees manipulate flowers in all kinds of contexts and scrabble with their legs to achieve nectar rewards. Rather than thinking that it is pulling a string, my guess would be that the bee learns that a particular motor pattern within their usual foraging repertoire (scrabbling with legs), leads to a reward. I don't think this makes the behavior any less interesting - in fact, I think considering the behavior through an ecological lens can help make better sense of it.

Here we respectfully disagree. The solving of Rubik’s cube by humans could be said to be version of finger-movements naturally required to open nuts or remove ticks from fur, but this is somewhat beside the point: it’s not the motor sequences that are of interest, but the cognition involved. A general approach in work on animal intelligence and cognition is to deliberately choose paradigms that are outside the animals’ daily routines-this is what we have done here, in asking whether there is means-end comprehension in bee problem solving. Like comparable studies on this question in other animals, the experiments are designed to probe this question, not one of ecological validity.

Reviewer #2 (Public Review):

Summary:

The authors wanted to see if bumblebees could succeed in the string-pulling paradigm with broken strings. They found that bumblebees can learn to pull strings and that they have a preference to pull on intact strings vs broken ones. The authors conclude that bumblebees use image matching to complete the string-pulling task.

Strengths:

The study has an excellent experimental design and contributes to our understanding of what information bumblebees use to solve a string-pulling task.

Weaknesses:

Overall, I think the manuscript is good, but it is missing some context. Why do bumblebees rely on image matching rather than causal reasoning? Could it have something to do with their ecology? And how is the task relevant for bumblebees in the wild? Does the test translate to any real-life situations? Is pulling a natural behaviour that bees do? Does image matching have adaptive significance?

We appreciate the valuable comment from the reviewer. Our explanation, which we have now added to the manuscript, is as follows:

“Different flower species offer varying profitability in terms of nectar and pollen to bumblebees; they need to make careful choices and learn to use floral cues to predict rewards (Chittka, 2017). Bumblebees can easily learn visual patterns and shapes of flower (Meyer-Rochow, 2019); they can detect stimuli and discriminate between differently coloured stimuli when presented as briefly as 25 ms (Nityananda et al., 2014). In contrast, causal reasoning involves understanding and responding to causal relationships. Bumblebees might favor, or be limited to, a visual approach, likely due to the efficiency and simplicity of processing visual cues to solve the string-pulling task. ”

As above, it worth noting that our work is not designed as an ecological study, but one about the question of whether causal reasoning can explain how bees solve a string-pulling puzzle. We have a cognitive focus, in line with comparable studies on other animals. We deliberately chose a paradigm that is to some extent outside of the daily challenges of the animal.

Reviewer #3 (Public Review):

Summary:

This paper presents bees with varying levels of experience with a choice task where bees have to choose to pull either a connected or unconnected string, each attached to a yellow flower containing sugar water. Bees without experience of string pulling did not choose the connected string above chance (experiment 1), but with experience of horizontal string pulling (as in the right-hand panel of Figure 4) bees did choose the connected string above chance (experiments 2-3), even when the string colour changed between training and test (experiments 4-5). Bees that were not provided with perceptual-motor feedback (i.e they could not observe that each pull of the string moved the flower) during training still learned to string pull and then chose the connected string option above chance (experiment 6). Bees with normal experience of string pulling then failed to discriminate between connected and unconnected strings when the strings were coiled or looped, rather than presented straight (experiments 7-8).

Weaknesses:

The authors have only provided video of some of the conditions where the bees succeeded. In general, I think a video explaining each condition and then showing a clip of a typical performance would make it much easier to follow the study designs for scholars. Videos of the conditions bees failed at would be highly useful in order to compare different hypotheses for how the bees are solving this problem. I also think it is highly important to code the videos for switching behaviours. When solving the connected vs unconnected string tasks, when bees were observed pulling the unconnected string, did they quickly switch to the other string? Or did they continue to pull the wrong string? This would help discriminate the use of perceptual-motor feedback from other hypotheses.

We added the test videos as suggested by the reviewer, and we added the data for each bee's choice. However, both connected and disconnected strings were glued to the floor, and therefore perceptual-motor feedback was equal and irrelevant between the choices during the test.

The experiments are also not described well, for my below comments I have assumed that different groups of bees were tested for experiments 1-8, and that experiment 6 was run as described in line 331, where bees were given string-pulling training without perceptual feedback rather than how it is described in Figure 4B, which describes bees as receiving string pulling training with feedback.

We now added figures of Experiment 6 and 7 in the Figure 1B, and we mentioned that different groups of bees were tested for Experiments 1-9.

The authors suggest the bees' performance is best explained by what they term 'image matching'. However, experiment 6 does not seem to support this without assuming retroactive image matching after the problem is solved. The logic of experiment 6 is described as "This was to ensure that the bees could not see the familiar "lollipop shape" while pulling strings....If the bees prefer to pull the connected strings, this would indicate that bees memorize the arrangement of strings-connected flowers in this task." I disagree with this second sentence, removing perceptual feedback during training would prevent bees memorising the lollipop shape, because, while solving the task, they don't actually see a string connected to a yellow flower, due to the black barrier. At the end of the task, the string is now behind the bee, so unless the bee is turning around and encoding this object retrospectively as the image to match, it seems hard to imagine how the bee learns the lollipop shape.

We agree with the reviewer that while solving the task in the last step during training, the bees don't actually see a string connected to a yellow flower, due to the black barrier. Since the full shape is only visible after the pulling is completed and this requires the bee to “check back” on the entire display after feeding, to basically conclude “ this is the shape that I need to be looking for later”.

Another possibility is that bumblebees might remember the image of the “lollipop shape” while training the bees in the first step, in which the “lollipop shape” was directly presented to the bumblebee in the early step of the training.

We added the experiment suggested by the reviewer, and the result showed that when a green table was placed behind the string to obscure the “lollipop shape” at any point during the training phase, the bees were unable to identify the connected string. The result further supports that bumblebees learn to choose the connected string through image matching.

Despite this, the authors go on to describe image matching as one of their main findings. For this claim, I would suggest the authors run another experiment, identical to experiment 6 but with a black panel behind the bee, such that the string the bee pulls behind itself disappears from view. There is now no image to match at any point from the bee's perspective so it should now fail the connectivity task.

Strengths:

Despite these issues, this is a fascinating dataset. Experiments 1 and 2 show that the bees are not learning to discriminate between connected and unconnected stimuli rapidly in the first trials of the test. Instead, it is clear that experience in string pulling is needed to discriminate between connected and unconnected strings. What aspect of this experience is important? Experiment 6 suggests it is not image matching (when no image is provided during problem-solving, but only afterward, bees still attend to string connectivity) and casts doubt on perceptual-motor feedback (unless from the bee's perspective, they do actually get feedback that pulling the string moves the flower, video is needed here). Experiments 7 and 8 rule out means-end understanding because if the bees are capable of imagining the effect of their actions on the string and then planning out their actions (as hypotheses such as insight, means-end understanding and string connectivity suggest), they should solve these tasks. If the authors can compare the bees' performance in a more detailed way to other species, and run the experiment suggested, this will be a highly exciting paper

We appreciate the valuable comment from the reviewer. We compared the bees' performance to other species, and conducted the experiment as suggested by the reviewer.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Smaller comments:

Line 64: is the word 'simple' needed here? It could also be explained by more complex forms of associative learning, no?

We deleted “simple”.

Methods:

Line 230: was it checked that this was high-contrast for the bees?

We added the relevant reference in the revised manuscript.

Line 240: how much sucrose solution was present in the flowers?

We added 25 microliters sucrose solution in the flowers. We added the information in the revised manuscript.

Line 266: check grammar.

We checked the grammar as follows: “During tests, both strings were glued to the floor of the arena to prevent the air flow generated by flying bumblebees’ wings from changing the position of the string.”

Statistical analysis:

- What does it mean that "Bees identity and colony were analyzed with likelihood ratio tests"?

Bees identity and colony was set as a random variable. We changed the analysis methods in the revised manuscript, and results of the all the experiments did not changed.

- Line 359: do you mean proportion rather than percentage?

We mean the percentage.

- "the number of total choices as weights" - this should be explained further. This is the number of choices that each bee made? What was the variation and mean of this number? If bees varied a lot in this metric, it might make more sense to analyze their first choice (as I see you've done) and their first 10 choices or something like that - for consistency.

This refers to the total number of choices made by each bumblebee. We added the mean and standard error of each bee’s number of choices in Table 1. Some bees pulled the string fewer than 10 times; we chose to include all choices made by each bee.

- More generally I think the first test is more informative than the subsequent choices, since every choice after their first could be affected by feedback they are getting in that test phase. Or rather, they are telling you different things.

All the bees were tested only once, however, you might be referring to the first choice. We used Chi-square test to analyze the bumblebees’ first choices in the test. It is worth noting that both connected and disconnected strings were glued to the floor. The bees were unable to move either the connected or disconnected strings during the tests, and only attempted to pull them. Therefore,the feedback from pulling either the connected or disconnected strings is the same.

- Line 362: I think I know what you mean, but this should be re-phrased because the "number of" sounds more appropriate for a Poisson distribution. I think what you are testing is whether each individual bee chose the connected or the disconnected string - i.e. a 0 or 1 response for each bee?

We agree with the reviewer that each bee chose the connected or the disconnected string - i.e. a 0 or 1 response for each bee, but not the number. We clarify this as: “The total number of the choices made by each bee was set as weights.” 

- Line 364-365: here and elsewhere, every time you mention a model, make it clear what the dependent and independent variables are. i.e. for the mixed model, the 'bee' is the random factor? Or also the colony that the bee came from? Were these nested etc?

We clarify this in the revised manuscript. The bee identity and colony is the random factor in the mixed model.

- Line 368: "Latency to the first choice of each bee was recorded" - why? What were the hypotheses/ predictions here?

The latency to the first choice was intended to see if the bumblebees were familiarizing with the testing pattern. A shorter delay time might indicate that the bumblebees were more familiar with the pattern.

- Line 371: "Multiple comparisons among experiments were.." - do you mean 'within' experiments? It seems that treatments should not be compared between different experiments.

We mean multiple comparisons among different experiments; we clarify this in the revised manuscript.

Results

Experiment 1: From the methods, it sounded like you both analyzed the bees' first choice and their total no. of choices, but in the results section (and Figure 1) I only see the data for all choices combined here.

In table 1 and in the text you report the number of bees that chose each option on their first choice, but there are no statistical results associated with these results. At the very least, a chi square or binomial test could be run.

Line 138: "Interestingly, ten out of fifteen bees pulled the connected string in their first choice" - this is presented like it is a significant majority of bees, but a chi-square test of 10 vs 5 has a p-value = 0.1967

We used the Chi square test to analyzed of the bees’ first choice. We also added the analyzed data in the Table 1.

Line 143: "It makes sense because the bees could see the "lollipop shape" once they pulled it out from the table." - this feels more like interpretation (i.e. Discussion) rather than results.

We moved the sentence to the discussion.

Line 162: again this feels more like interpretation/ conjecture than results.

We removed the sentence in the results.

Line 184: check grammar.

We checked the grammar. We changed “task” to “tasks”.

Figures

I really appreciated the overview in Figure 5 - though I think this should be Figure 1? Even if the methods come later in eLife, I think it would be nice to have that cited earlier on (e.g. at the start of the results) to draw the reader's attention to it quickly, since it's so helpful. It also then makes the images at the bottom of what is currently Figure 1 make more sense. I also think that the authors could make it clearer in Figure 5 which strings are connected vs disconnected in the figure (even if it means exaggerating the distance more than it was in real life). I had to zoom in quite a bit to see which were connected vs. not. Alternatively, you could have an arrow to the string with the words "connected" "disconnected" the first time you draw it - and similar labels for the other string conditions.

We appreciate the valuable comment from the reviewer. We changed Figure 5 to Figure 2, and Figure 4 to Figure 1. We cited the Figures at the start of the results. We also changed the gap distance between the disconnected strings. Additionally, we added arrows to indicate “connected” and “disconnected” strings in the Figure.

Figure 1 - I think you could make it clearer that the bars refer to experiments (e.g. have an x-axis with this as a label). Also, check the grammar of the y-axis.

We added the experiments number in the Figures. Additionally, we checked the grammar of the y-axis. We changed “percentages” to “parentage”. 

I also think it's really helpful to see the supplementary videos but I think it would be nice to see some examples of the test phase, and not just the training examples.

We added Supplementary videos of the testing phase.

Reviewer #2 (Recommendations For The Authors):

Below are also some minor comments:

L40: "approaches".

We changed “approach” to “approaches”.

L42: but likely mainly due to sampling bias of mammals and birds.

We changed the sentence as follows: String pulling is one of the most extensively used approaches in comparative psychology to evaluate the understanding of causal relationships (Jacobs & Osvath, 2015), with most research focused on mammals and birds, where a food item is visible to the animal but accessible only by pulling on a string attached to the reward (Taylor, 2010; Range et al., 2012; Jacobs & Osvath, 2015; Wakonig et al., 2021).

L64: remove "in this study"

We removed “in this study”.

L64: simple associative learning of what? Isn't your image matching associative too?

We removed “ simple”.

L97: remove "a" before "connected".

We removed “a” before “connected”.

L136-138: but maybe they could still feel the weight of the flower when pulling?

Because both strings were glued to the floor in the test phase, the feedback was the same and therefore irrelevant. This information is noted in the General Methods.

L161: what are these numbers?

We removed the latency in the revised manuscript.

L167/ Table 1: I realise that the authors never tried slanted strings to check if bumblebees used proximity as a cue. Why?

This was simply because we wanted to focus on whether bumblebees could recognize the connectivity of the string.

Discussion: Why did you only control for colour of the string? What if you had used strings with different textures or smells? Unclear if the authors controlled for "bumblebee smell" on the strings, i.e., after a bee had used the string, was the string replaced by a new one or was the same one used multiple times?

We used different colors to investigate featural generalization of the visual display of the string connected to the flower in this task. We controlled for color because it is a feature that bumblebees can easily distinguish.

Both the flowers and the strings were used only once, to prevent the use of chemosensory cues. We clarify this in the revised manuscript.

L182: since what?

We deleted “since” in the revised manuscript.

L182-188: might be worth mentioning that some crows and parrots known for complex cognition perform poorly on broken strings (e.g., https://doi.org/10.1098/rspb.2012.1998 ; https://doi.org/10.1163/1568539X-00003511 ; https://doi.org/10.1038/s41598-021-94879-x ) and Australian magpies use trial and error (https://doi.org/10.1007/s00265-023-03326-6).

We added the following sentences as suggested by the reviewer: “It is worth noting that some crows and parrots known for complex cognition perform poorly on the broken string task without perceptual feedback or learning. For example, New Caledonian crows use perceptual feedback strategies to solve the broken string-pulling task, and no individual showed a significant preference for the connected string when perceptual feedback was restricted (Taylor et al., 2012). Some Australian magpies and African grey parrots can solve the broken string task, but they required a high number of trials, indicating that learning plays a crucial role in solving this task (Molina et al., 2019; Johnsson et al., 2023).”

L193: maybe expand on this to put the task into a natural context?

We added the following sentences as suggested by the reviewer:

“Different flower species offer varying profitability in terms of nectar and pollen to bumblebees; they need to make careful choices and learn to use floral cues to predict rewards (Chittka, 2017). Bumblebees can easily learn visual patterns and shapes of flower (Meyer-Rochow, 2019); they can detect stimuli and discriminate between differently coloured stimuli when presented as briefly as 25 ms (Nityananda et al., 2014). In contrast, causal reasoning involves understanding and responding to causal relationships. Bumblebees might favor, or be limited to, a visual approach, likely due to the efficiency and simplicity of processing visual cues to solve the string-pulling task. ”

L204: is causal understanding the same as means-end understanding?

Means-end understanding is expressed as goal-directed behavior, which involves the deliberate and planned execution of a sequence of steps to achieve a goal. Includes some understanding of the causal relationship (Jacobs & Osvath, 2015; Ortiz et al., 2019). .

L235: this is a very big span of time. Why not control for motivation? Cognitive performance can vary significantly across the day (at least in humans).

Bumblebee motivation is understood to be rather consistent, as those that were trained and tested came to the flight arena of their own volition and were foragers looking to fill their crop load each time to return it to the colony.

L232: what is "(w/w)" ? This occurs throughout the manuscript.

“w/w” represents the weight-to-weight percentage of sugar.

L250: this sentence sounds odd. "containing in the central well.." ?? Perhaps rephrase? Unclear what central well refers to? Did the flowers have multiple wells?

We rephrased the sentence as follows: For each experiment, bumblebees were trained to retrieve a flower with an inverted Eppendorf cap at the center, containing 25 microliters of 50% sucrose solution, from underneath a transparent acrylic table

L268: why euthanise?

The reason for euthanizing the bees is that new foragers will typically only become active after the current ones were removed from the hive.

L270: chemosensory cues answer my concern above. Maybe make it clear earlier.

We moved this sentence earlier in the result.

L273: did different individuals use different pulling strategies? Do you have the data to analyse this? This has been done on birds and would offer a nice comparison.

We analyzed the string-pulling strategies among different individuals, and provided Supplementary Table 1 to display the performances of each individual in different string-pulling experiments.

L365: unclear why both models. Would be nice to see a GLM output table.

The duration of pulling different kinds of strings were first tested with the Shapiro-Wilk test to assess data normality. The duration data that conforms to a normal distribution was compared using linear mixed-effects models (LMM), while the data that deviates from normality were examined with a generalized linear-mixed model (GLMM). We added a GLM and GLMM output table in the revised manuscript.

L377: should be a space between the "." and "This".

We added a space between the “.” and “This”.

L383-390: some commas and semicolons are in the wrong places.

We carefully checked the commas and semicolons in this sentence.

Reviewer #3 (Recommendations For The Authors):

Minor comments

Line 32: seems to be missing a word, suggest "the bumblebees' ability to distinguish".

we added “the” in the revised manuscript.

Line 47: it would be good to reference other scholars here, this is the central focus of all work in comparative psychology.

We added the reference in the revised manuscript.

Line 50-61: I think the string-pulling literature could be described in more detail here, with mention of perceptual-motor feedback loops as a competing hypothesis to means-end understanding (see Taylor et al 2010, 2012). It seems a stretch to suggest that "String-pulling studies have directly tested means-end comprehension in various species", when perceptual-motor feedback is a competing hypothesis that we have positive evidence for in several species.

We mentioned the perceptual-motor feedback in the introduction as follow:

“Multiple mechanisms can be involved in the string-pulling task, including the proximity principle, perceptual feedback and means-end understanding (Taylor et al., 2012; Wasserman et al., 2013; Jacobs & Osvath, 2015; Wang et al., 2020). The principle of proximity refers to animals preferring to pull the reward that is closest to them (Jacobs & Osvath, 2015). Taylor et al. (2012) proposed that the success of New Caledonian crows in string-pulling tasks is based on a perceptual-motor feedback loop, where the reward gradually moves closer to the animal as they pull the strings. If the visual signal of the reward approaching is restricted, crows with no prior string-pulling experience are unable to solve the broken string task (Taylor et al., 2012).

However, when a green table was placed behind the string to obscure the “lollipop” structure during the training, the bees could not see the “lollipop” during the initial training stage or after pulling the string from under the table. In this situation, the bees were unable to identify the connected string, further proving that bumblebees chose the connected string based on image matching.

Line 68: suggest remove 'meticulously'.

We removed “meticulously”.

Line 99: This is an exciting finding, can the authors please provide a video of a bee solving this task on its first trial?

We added videos in the supplementary materials.

Line 133: perceptual-motor feedback loops should be introduced in the introduction.

We introduced perceptual-motor feedback loops in the revised manuscript.

Line 136: please clarify the prior experience of these bees, it is not clear from the text.

We clarified the prior experience of these bees as follow: Bumblebees were initially attracted to feed on yellow artificial flowers, and then trained with transparent tables covered by black tape (S7 video) through a four-step process.

Line 138: from the video it is not possible to see the bee's perspective of this occlusion. Do the authors have a video or image showing the feedback the bees received? I think this is highly important if they wish to argue that this condition prevents the use of both image matching and a perceptual-motor feedback loop.

We prevented the use of image matching: the bees were unable to see the flower moving towards them above the table during the training phase in this condition. But the bees may receive visual image both after pulling the string out from the table and in the initial stages of training in this condition.

Line 147: please clarify what experience these bees had before this test.

We added the prior experience of bumblebees before training as follow: We therefore designed further experiments based on Taylor et al. (2012) to test this hypothesis. Bumblebees were first trained to feed on yellow artificial, and then trained with the same procedure as Experiment 2, but the connected strings were coiled in the test.

Line 155: This is a highly similar test to that used in Taylor et al 2012, have the authors seen this study?

We mentioned the reference in the revised manuscript as follows: We therefore designed further experiments based on Taylor et al. (2012) to test this hypothesis.

Line 183: This sentence needs rewriting "Since the vast majority of animals, including dogs 183 (Osthaus et al., 2005), cats (Whitt et al., 2009), western scrub-jays (Hofmann et al.,2016) and azure-winged magpies (Wang et al., 2019) are failing in such tasks spontaneously".

We changed the sentence as suggested by the reviewer as follow:  Some animals, including dogs (Osthaus et al., 2005), cats (Whitt et al., 2009), western scrub-jays (Hofmann et al., 2016) and azure-winged magpies (Wang et al., 2019) fail in such task spontaneously.

Line 186: "complete comprehension of the functionality of strings is rare" I am not sure the evidence in the current literature supports any animal showing full understanding, can the authors explain how they reach this conclusion?

We wished to say that few animal species could distinguish between connected and disconnected strings without trial and error learning. We revised the sentence as follows:

It is worth noting that some crows and parrots known for complex cognition perform poorly on broken string task without perceptual feedback or learning. For example, New Caledonian crows use perceptual feedback strategies to solve broken string-pulling task, and no individual showed a significant preference for the connected string when perceptual feedback is restricted (Taylor et al., 2012). Some Australian magpies and African grey parrots can solve the broken string task, but it required a high number of trials, indicating that learning plays a crucial role in solving this task (Molina et al., 2019; Johnsson et al., 2023).

Line 190: the authors need to clarify which part of their study provides positive evidence for this conclusion.

We added the evidence for this conclusion as follows: Our findings suggest that bumblebees with experience of string pulling prefer the connected strings, but they failed to identify the interrupted strings when the string was coiled in the test.

Line 265: was the far end of the string glued only?

The entire string was glued to the floor, not just the far ends of the string.

eLife assessment

This study reports important results and new insights into humoral immune responses to Plasmodium falciparum sexual stage proteins. The experiments are based on the use of target-agnostic memory B cell sorting and screening approaches as well as several state-of-the-art technologies. The authors present compelling evidence that one antibody, B1E11K, is cross-reactive with multiple proteins containing glutamate-rich repeats through homotypic interactions, a process similar to what has been observed for Plasmodium circumsporozoite protein repeat-directed antibodies.

Reviewer #2 (Public Review):

This manuscript by Amen, Yoo and Fabra-Garcia et al describes a human monoclonal antibody B1E11K, targeting EENV repeats which are present in parasite antigens such as Pfs230, RESAs and Pf11.1. The authors isolated B1E11K using an initial target agnostic approach for antibodies that would bind gamete/gametocyte lysate which they made 14 mAbs. Following a suite of highly appropriate characterization methods from Western blotting of recombinant proteins to native parasite material, use of knockout lines to validate specificity, ITC, peptide mapping, SEC-MALS, negative stain EM and crystallography, the authors have built a compelling case that B1E11K does indeed bind EENV repeats. In addition, using X-ray crystallography they show that two B1E11K Fabs bind to a 16 aa RESA repeat in a head-to-head conformation using homotypic interactions and provide a separate example from CSP, of affinity-matured homotypic interactions.

The authors have addressed most of our previous comments in their revised manuscript.

One of the main conclusions in the paper is the binding of B1E11K to RESAs which are blood stage antigens that are exported to the infected parasite surface. In the future, it would be interesting to understand if B1E11K mAb binds to the red cell surface of infected blood stage parasites to understand its cellular localization in those stages.

Materials and Methods:<br /> PBMC sampling: While the authors have provided clarification that they obtained informed consent from the PBMC donor, they have not added the ethics approval codes in this section.

Reviewer #3 (Public Review):

The manuscript from Amen et al reports the isolation and characterization of human antibodies that recognize proteins expressed at different sexual stages of Plasmodium falciparum. The isolation approach was antigen agnostic and based on the sorting, activation, and screening of memory B cells from a donor whose serum displays high transmission-reducing activity. From this effort, 14 antibodies were produced and further characterized. The antibodies displayed a range of transmission-reducing activities and recognized different Pf sexual stage proteins. However, none of these antibodies had substantially higher TRA than previously described antibodies.

The authors then performed further characterization of antibody B1E11K, which was unique in that it recognized multiple proteins expressed during sexual and asexual stages. Using protein microarrays, B1E11K was shown to recognize glutamate-rich repeats, following an EE-XX-EE pattern. An impressive set of biophysical experiments were performed to extensively characterize the interactions of B1E11K with various repeat motifs and lengths. Ultimately, the authors succeeded in determining a 2.6 A resolution crystal structure of B1E11K bound to a 16AA repeat-containing peptide. Excitingly, the structure revealed that two Fabs bound simultaneously to the peptide and made homotypic antibody-antibody contacts. This had only previously been observed before with antibodies directed against CSP repeats.

Overall I found the manuscript to be very well written. Strengths of the manuscript include the target-agnostic screening approach and the thorough characterization of antibodies. The demonstration that B1E11K is cross-reactive to multiple proteins containing glutamate-rich repeats, and that the antibody recognizes the repeats via homotypic interactions, similar to what has been observed for CSP repeat-directed antibodies, should be of interest to many in the field.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews: 

Reviewer #1 (Public Review):

Summary: 

In this paper, the authors used target agnostic MBC sorting and activation methods to identify B cells and antibodies against sexual stages of Plasmodium falciparum. While they isolated some Mabs against PFs48/45 and PFs230, two well-known candidates for "transmission blocking" vaccines, these antibodies' efficacies, as measured by TRA, did not perform as well as other known antibodies. They also isolated one cross-reactive mAb to proteins containing glutamic acid-rich repetitive elements, that express at different stages of the parasite life cycle. They then determined the structure of the Fab with the highest protein binder they could determine through protein microarray, RESA, and observed homotypic interactions. 

Strengths: 

-  Target agnostic B cell isolation (although not a novel methodology). 

-  New cross-reactive antibody with some "efficacy" (TRA) and mechanism (homotypic interactions) as demonstrated by structural data and other biophysical data. 

Weaknesses: 

The paper lacks clarity at times and could benefit from more transparency (showing all the data) and explanations. 

We have added the oocyst count data from the SMFA experiments as Supplementary Table 2, and ELISA binding curves underlying Figure 4B as Supplementary Figure 5.

In particular: 

- define SIFA 

- define TRAbs 

We have carefully gone through the manuscript and have introduced abbreviations at first use, removed unnecessary abbreviations and removed unnecessary jargon to increase readability.

- it is not possible to read the Figure 6B and C panels. 

We regret that the labels in Supplementary Figures 6 and 7 were of poor quality and have now included higher resolution images to solve this issue.

Reviewer #2 (Public Review): 

This manuscript by Amen, Yoo, Fabra-Garcia et al describes a human monoclonal antibody B1E11K, targeting EENV repeats which are present in parasite antigens such as Pfs230, RESAs, and 11.1. The authors isolated B1E11K using an initial target agnostic approach for antibodies that would bind gamete/gametocyte lysate which they made 14 mAbs. Following a suite of highly appropriate characterization methods from Western blotting of recombinant proteins to native parasite material, use of knockout lines to validate specificity, ITC, peptide mapping, SEC-MALS, negative stain EM, and crystallography, the authors have built a compelling case that B1E11K does indeed bind EENV repeats. In addition, using X-ray crystallography they show that two B1E11K Fabs bind to a 16 aa RESA repeat in a head-to-head conformation using homotypic interactions and provide a separate example from CSP, of affinity-matured homotypic interactions. 

There are some minor comments and considerations identified by this reviewer, These include that one of the main conclusions in the paper is the binding of B1E11K to RESAs which are blood stage antigens that are exported to the infected parasite surface. It would have been interesting if immunofluorescence assays with B1E11K mAb were performed with blood-stage parasites to understand its cellular localization in those stages. 

In the current manuscript, we provide multiple lines of evidence that B1E11K binds (with high affinity) to repeats that are present in RESAs, i.e. through micro-array studies, in vitro binding experiments such as Western blot, ELISA and BLI, and through X-ray crystallography studies on B1E11k – repeat peptide complexes. Taken together, we think we provide compelling evidence that B1E11k binds to repeats present in RESA proteins. We do agree that studies on the function of this mAb against other stages of the parasite could be of interest, but as our manuscript focuses on the sexual stage of the parasite, we feel that this is beyond scope of the current work. However, this line of inquiry will be strongly considered in follow up studies.   

Reviewer #3 (Public Review): 

The manuscript from Amen et al reports the isolation and characterization of human antibodies that recognize proteins expressed at different sexual stages of Plasmodium falciparum. The isolation approach was antigen agnostic and based on the sorting, activation, and screening of memory B cells from a donor whose serum displays high transmission-reducing activity. From this effort, 14 antibodies were produced and further characterized. The antibodies displayed a range of transmission-reducing activities and recognized different Pf sexual stage proteins. However, none of these antibodies had substantially lower TRA than previously described antibodies. 

The authors then performed further characterization of antibody B1E11K, which was unique in that it recognized multiple proteins expressed during sexual and asexual stages. Using protein microarrays, B1E11K was shown to recognize glutamate-rich repeats, following an EE-XX-EE pattern. An impressive set of biophysical experiments was performed to extensively characterize the interactions of B1E11K with various repeat motifs and lengths. Ultimately, the authors succeeded in determining a 2.6 A resolution crystal structure of B1E11K bound to a 16AA repeat-containing peptide. Excitingly, the structure revealed that two Fabs bound simultaneously to the peptide and made homotypic antibody-antibody contacts. This had only previously been observed with antibodies directed against CSP repeats. 

Overall I found the manuscript to be very well written, although there are some sections that are heavy on field-specific jargon and abbreviations that make reading unnecessarily difficult. For instance, 'SIFA' is never defined. 

We have carefully gone through the manuscript and have introduced abbreviations at first use, removed unnecessary abbreviations and removed unnecessary jargon to increase readability.

Strengths of the manuscript include the target-agnostic screening approach and the thorough characterization of antibodies. The demonstration that B1E11K is cross-reactive to multiple proteins containing glutamate-rich repeats, and that the antibody recognizes the repeats via homotypic interactions, similar to what has been observed for CSP repeat-directed antibodies, should be of interest to many in the field. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Figure 1 - why only gametes ELISA and Spz or others?  

The volumes of the single B cell supernatants were too small to screen against multiple antigens/parasite stages. As we aimed to isolate antibodies against the sexual stages of the parasite, our assay focused on this stage and supernatants were not tested against other stages. Furthermore, we screened for reactivity against gametes as TRA mAbs likely target gametes rather than other forms of sexual stage parasites.

Figure 2 A 

(a) Wild type (WT) and Pfs48/45 knock-out (KO) gametes.

(b) I am a bit confused about what GMT is vs Pfs48/45 

We have changed the column titles in Figure 2A to “wild-type gametes” and “Pfs48/45 knockout gametes” to improve clarity.  

(c) Binding is high % why is it red? 

We chose to present the results in a heatmap format with a graded color scale, from strong binders in red to weak binders in green. It has now been clarified in the legend of the figure. 

Please state acronyms clearly 

TRA - transmission reducing activity 

SMFA - standard membrane feeding assay 

We have added the full terms to clarify the acronyms.

1123- VRC01 (not O1)

We have corrected this.

Figure 2 C bottom panels, clarify which ones are TRAbs (Assuming the Mabs with over 80% TRA at 500 ug/ml) (right gel) and the ones that are not (left gel)? 

In the Western blot in Figure 2c, we have marked the antibodies with >80% TRA with an asterisk.

Furthermore, we have replaced ‘TRAbs’ by ‘mAbs with >80% TRA at 500 µg/mL’ in the figure legend.

ITC show the same affinity of the Fab to the 2 peptides but not the ELISA, not the BLI/SPR would be more appropriate. Any potential explanation?  

The way binding affinity is determined across various techniques can result in slight differences in determined values. For instance, ELISAs utilize long incubation times with extensive washing steps and involve a spectroscopic signal, isothermal titration calorimetry (ITC) uses calorimetric signal at different concentration equilibriums to extract a KD, and BLI determines kinetic parameters for KD determination. Discrepancies in binding affinities between orthologous techniques have indeed been observed previously in the context of peptide-antibody binding (e.g. PMID: 34788599).

Despite this, regardless of technique, the relative relationships in all three sets of data is the same - higher binding affinity is observed to the longer P2 peptide. This is the main takeaway of the section. As the reviewer suggests, BLI is likely the most appropriate readout here and is the only value explicitly mentioned in the main text. We primarily use ITC to support our proposed binding stoichiometry which is important to substantiate the SEC-MALS and nsEM data in Figure 4H-I. We added the following sentences to help reinforce these points: “The determined binding affinity from our ITC experiments (Table 1) differed from our BLI experiments (Fig. 4D and 4E), which can occur when measuring antibody-peptide interactions. Regardless, our data across techniques all trend toward the same finding in which a stronger binding affinity is observed toward the longer RESA P2 (16AA) peptide.”

Figure 5C - would be helpful to have the peptide sequence above referring to what is E1, E2 etc... 

We added two panels (Figure 5C-D) showcasing the binding interface that shows the peptide numbering in the context of the overall complex. We hope that this will help better orient the reader. 

Figure S4 - maybe highlight in different colors the EENVV, EEIEE, Etc, etc 

Repeats found in the sequence of the various proteins in Figure S4 have now been highlighted with different colors.

Line 163 - why 14 mabs if 11 wells? Isn't it 1 B cell per well? The authors should explain right away that some wells have more than 1 B cell and some have 1 HC, 1LC, and 1 KC. 

We agree that this was somewhat confusing and have modified the text which now reads: “We obtained and cloned heavy and light chain sequences for 11 out of 84 wells. For three wells we obtained a kappa light chain sequence and for five wells a lambda light chain sequence. For three wells we obtained both a lambda and kappa light chain sequence suggesting that either both chains were present in a single B cell or that two B cells were present in the well. For all 14 wells we retrieved a single heavy chain sequence. Following amplification and cloning, 14 mAbs, from 11 wells, were expressed as full human IgG1s (Table S1) (Dataset S1).”

Line 166-167 - were they multiple HC (different ones) as well when Lambda and kappa were present?

This is not clear at first. 

We clarified this point in the text, see also comment above.

Line 177 - expressed Pfs48/45 and Pfs230, is it lacking both or just Pfs48/45 (as stated on line 172)? 

Pfs48/45 binds to the gamete surface via a GPI anchor, while Pfs230 is retained to the surface through binding to Pfs48/45. Hence, the Pfs48/45 knockout parasite will therefore also lack surfacebound Pfs230. We have added a sentence to the Results clarifying this: “The mAbs were also tested for binding to Pfs48/45 knock-out female gametes, which lack surface-bound Pfs48/45 and Pfs230”.

Show the ELISA data used to calculate EC50 in Figure 3. 

ELISA binding curves are now shown as Figure S5.

Line 313-315 - what if you reverse, capture the Fab (peptide too small even if biotinylated?) 

As anticipated by the Reviewer, immobilizing the Fab and dipping into peptide did not yield appreciable signal for kinetic analysis and thus the experiment from this setup is not reported. 

Line 341 - add crystal structure 

This has now been added.

There is a bit too much speculation in the discussion. For e.g. "The B1C5L and B1C5K mAbs were shown to recognize Domain 2 of Pfs48/45 and exhibited moderate potency, as previously described for Abs with such specificity (27). These 2 mAbs were isolated from the same well and shared the same heavy chain; their three similar characteristics thus suggest that their binding is primarily mediated by the heavy chain". Actual data will reinforce this statement. 

As B1C5L and B1C5K recognized domain 2 of Pfs48/45 with similar affinity, this strongly suggests that binding is mediated though the heavy chain. Structural analysis could confirm this statement, but this is out of the scope of this study.  

Reviewer #2 (Recommendations For The Authors): 

Figure 1: This figure provides a description of the workflow. To make it more relevant for the paper, the authors could add relevant numbers as the workflow proceeds. 

(a) For example, how many memory B cells were sorted, how many supernatants were positive, and then how many mAbs were produced? These numbers can be attached to the relevant images in the workflow. 

We modified the figure to include the numbers. 

(b) For the "Supernatant screening via gamete extract ELISA", please change to "Supernatant screening via gamete/gametocyte extract ELISA". 

We modified the statement as suggested. 

Line 155: The manuscript states that 84 wells reacted with gamete/gametocyte lysate. The following sentence states that "Out of the 21 supernatants that were positive...". Can the authors provide the summary of data for all 84 wells or why focus on only 21 supernatants? 

We screened all supernatants against gamete lysate, and only a subset against gametocyte lysate. In total, we found 84 positive supernatants that were reactive to at least one of the two lysates. 21 of those 84 positive were screened against both lysates. We have modified the text to clarify the numbers:

“After activation, single cell culture supernatants potentially containing secreted IgGs were screened in a high-throughput 384-well ELISA for their reactivity against a crude Pf gamete lysate (Fig. S1B). A subset of supernatants was also screened against gametocyte lysate (S1C). In total, supernatants from 84 wells reacted with gamete and/or gametocyte lysate proteins, representing 5.6% of the total memory B cells. Of the 21 supernatants that were screened against both gamete and gametocyte lysates, six recognized both, while nine appeared to recognize exclusively gamete proteins, and six exclusively gametocyte proteins.”

Please note that all 84 positive wells were taken forward for B cell sequencing and cloning. 

Line 171: SIFA is introduced for the first time and should be completely spelled out.

We have corrected this. 

Figure 2: 

(a) In Figure 2A, can you change the column title from "% pos KO GMT" to "% pos Pfs48/45 KO GMT"?

We have changed the column titles.  

(b) In Figure 2B, the SMFA results have been converted to %TRA. Can the authors please provide the raw data for the oocyst counts and number of mosquitoes infected in Supplementary Materials? 

We have added oocyst count data in Table S2, to which we refer in the figure legend. 

(c) For Figure 2F, the authors do have other domains to Pfs230 as described in Inklaar et al, NPJ Vaccines 2023. An ELISA/Western to the other domains could identify the binding site for B2C10L, though we appreciate this is not the central result of this manuscript. 

We thank the reviewer for this suggestion. We are indeed planning to identify the target domain of B2C10L using the previously described fragments, but agree with the reviewer that this not the focus of the current manuscript and decided to therefore not include it in the current report.

Line 116: The word sporozoites appears in subscript and should be corrected to be normal text. 

We have corrected this.

Line 216: Typo "B1E11K" 

We have corrected this.

Materials and Methods: 

(a) PBMC sampling: Please add the ethics approval codes in this section. 

Donor A visited the hospital with a clinical malaria infection and provided informed consent for collection of PBMCs. We have modified the method section to clarify this. 

“Donor A had lived in Central Africa for approximately 30 years and reported multiple malaria infections during that period. At the time of sampling PBMCs, Donor A had recently returned to the Netherlands and visited the hospital with a clinical malaria infection. After providing informed consent, PBMCs were collected, but gametocyte prevalence and density were not recorded.”

(b) Gamete/Gametocyte extract ELISA: Can the authors please provide the concentration of antibodies used for the positive and negative controls (TB31F, 2544, and 399) 

We have added the concentrations for these mAbs in the methods section.

Recombinant Pfs48/45 and Pfs230 ELISA: Please state the concentration or molarity used for the coating of recombinant Pfs48/45 and Pfs230CMB. 

We have added the concentrations, i.e. 0.5 µg/mL, to the methods section.

Western Blotting: The protocol states that DTT was added to gametocyte extracts (Line 594), but Western Blots in Figures 2 and 3 were performed in non-reducing conditions. Please confirm whether DTT was added or not. 

Thank you for noting this. We did not use DTT for the western blots and have removed this line from the methods section.

Reviewer #3 (Recommendations For The Authors): 

Below are a few minor comments to help improve the manuscript. 

(1) In Figure 4E, are the BLI data fit to a 1:1 binding model? The fits seem a bit off, and from ITC and X-ray studies it is known that 2 Fabs bind 1 peptide. The second Fab should presumably have higher affinity than the first Fab since the second Fab will make interactions with both the peptide and the first Fab. It may be better to fit the BLI data to a 2:1 binding model. 

The 2:1 (heterogeneous ligand) model assumes that there are two different independent binding sites. However, the second binding event described is dependent on the first binding event and thus this model also does not accurately reflect the system. Given that there is not an ideal model to fit, we instead are careful about the language used in the main text to describe these results. Additionally, we also include a sentence to the results section to ensure that the proper findings/interpretations are highlighted: “…our data all trend toward the same finding in which a stronger binding affinity is observed toward the longer RESA P2 (16AA) peptide.”

(2) The sidechain interactions shown in Figures 5C and D could probably be improved. The individual residues are just 'floating' in space, causing them to lack context and orientation. 

We added two panels (Fig. 5C-D) showcasing the binding interface that shows the peptide numbering in the context of the overall complex. We hope that this will help orient the reader.  

(3) The percentage of Ramachandran outliers should be listed in Table 2. Presumably, the value is 0.2%, but this is omitted in the current table. 

Table 2 has been modified to include the requested information explicitly.

eLife assessment

The ThermoMaze represents a valuable tool to control the rest/exploration states of an animal. The data, collected and analyzed using solid and validated methodology, demonstrate its use in addressing previously elusive questions. This will facilitate future work with more in-depth analysis of place cell activity to further support for some of the claims.

Reviewer #1 (Public Review):

Summary:

This manuscript introduced a new behavioral apparatus to regulate the animal's behavioral state naturally. It is a thermal maze where different sectors of the maze can be set to different temperatures; once the rest area of the animal is cooled down, it will start searching for a warmer alternative region to settle down again. They recorded with silicon probes from the hippocampus in the maze and found that the incidence of SWRs was higher at the rest areas and place cells representing a rest area were preferentially active during rest-SWRs as well but not during non-REM sleep.

Strengths:

The maze can have many future applications, e.g., see how the duration of waking immobility can influence learning, future memory recall, or sleep reactivation. It represents an out-of-the-box thinking to study and control less-studies aspects of the animals' behavior.

Weaknesses:

The impact is only within behavioral research and hippocampal electrophysiology.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

This manuscript introduced a new behavioral apparatus to regulate the animal's behavioral state naturally. It is a thermal maze where different sectors of the maze can be set to different temperatures; once the rest area of the animal is cooled down, it will start searching for a warmer alternative region to settle down again. They recorded with silicon probes from the hippocampus in the maze and found that the incidence of SWRs was higher at the rest areas and place cells representing a rest area were preferentially active during rest-SWRs as well but not during non-REM sleep.

We thank the reviewer for carefully reading our manuscript and providing useful and constructive comments.

Strengths:

The maze can have many future applications, e.g., see how the duration of waking immobility can influence learning, future memory recall, or sleep reactivation. It represents an out-of-the-box thinking to study and control less-studies aspects of the animals' behavior.

Weaknesses:

The impact is only within behavioral research and hippocampal electrophysiology.

We agree with this assessment but would like to add that the intersection of electrophysiological recordings in behaving animals is a very large field. Behavioral thermoregulation is a hotly researched area also by investigators using molecular tools as well. The ThermoMaze can be used for juxtacellular/intracellular recordings in behaving animals. Restricting the animal’s movement during these recordings can improve the length of recording time and recorded single unit yield in these experiments. 

Moreover, the fact that animals can sleep within the task can open up new possibilities to compare the role of sleep in learning without having to move the animal from a maze back into its home cage. The cooling procedure can be easily adapted to head-fixed virtual reality experiments as well.

I have only a few questions and suggestions for future analysis if data is available.

Comment-1: Could you observe a relationship between the duration of immobility and the preferred SWR activation of place cells coding for the current (SWR) location of the animal? In the cited O'Neill et al. paper, they found that the 'spatial selectivity' of SWR activity gradually diminished within a 2-5min period, and after about 5min, SWR activity was no longer influenced by the current location of the animal. Of course, I can imagine that overall, animals are more alert here, so even over more extended immobility periods, SWRs may recruit place cells coding for the current location of the animal.

We thank the reviewer for raising this question, which is a fundamental issue that we attempted to address using the ThermoMaze. First, we indeed observed persistent place-specific firing of CA1 neurons for up to around 5 minutes, which was the maximal duration of each warm spot epoch, as shown by the decoding analysis (based on firing rate map templates constructed during SPW-Rs) in Figure 5C and D. However, we did not observe above-chance-level decoding of the current position of the animal during sharp-wave ripples using templates constructed during theta, which aligns with previous observation that CA1 neurons during “iSWRs” (15–30 s time windows surrounding theta oscillations) did not show significant differences in their peak firing rate inside versus outside the place field (O’Neil et al., 2006). We reasoned that this could be potentially explained by a different (although correlated, see Figure 5E) neuronal representation of space during theta and during awake SPW-R.

Comment-2: Following the logic above, if possible, it would be interesting to compare immobility periods on the thermal maze and the home cage beyond SWRs, as it could give further insights into differences in rest states associated with different alertness levels. E.g., power spectra may show a stronger theta band or reduced delta band compared to the home cage.

If we are correct the Reviewer would like to know whether the brain state of the animal was similar in the ThermoMaze (warm spot location) and in the home cage during immobility. A comparison of the time-evolved power spectra shows similar changes from walking to immobility in both situations without notable differences. This analysis was performed on a subset of animals (n = 17 sessions in 7 mice) that were equipped with an accelerometer (home cage behavior was not monitored by video). We detected rest epochs that lasted at least 2 seconds during wakefulness in both the home cage and ThermoMaze. Using these time points we calculated the event-triggered power spectra for the delta and theta band (±2 s around the transition time) and found no difference between the home cage and ThermoMaze (Suppl. Fig. 4D).

Prompted by the Reviewer’s question, we further quantified the changes in LFP in the two environments. We did not find any significant change in the frequencies between 1-40 Hz during Awake periods, but we did find higher delta power (1-4 Hz) in some animals in the ThermoMaze (Suppl. Fig. 4A, B). 

We have also quantified the delta and theta power spectra in the few cases, when the warm spot was maintained, and the animal fell asleep. The time-resolved spectra classified the brain state as NREM, similar to sleeping in the home cage. Both delta and theta power were higher in the ThermoMaze following Awake-NREM transitions (±30 seconds around the transition, Suppl. Fig. 4C). It might well be that immobility/sleep outside the mouse’s nest might reflect some minor (but important) differences but our experiments with only a single camera recording do not have the needed resolution to reveal minor differences in posture.

We added these results to the revised Supplementary material (Suppl. Fig. 4).

Comment-3: Was there any behavioral tracking performed on naïve animals that were placed the first time in the thermal maze? I would expect some degree of learning to take place as the animal realizes that it can find another warm zone and that it is worth settling down in that area for a while. Perhaps such a learning effect could be quantified.

Unfortunately, we did not record videos during the first few sessions in the ThermoMaze. Typically, we transferred a naïve animal into the ThermoMaze for an hour on the first day to acclimatize them to the environment. This was performed without video analysis. In addition, because the current version of the maze is relatively small (20 x 20 cm), the animal usually walked around the edges of the maze before settling down at a heated warm spot. It appeared to us that there was only a very weak drive to learn the sequence and location of the warm spot, and therefore we did not quantified learning in the current experiment. We agree with the reviewer that in future studies, it will be interesting to explore whether the ThermoMaze could be adapted to a land-version of the Morris water maze by increasing the size of the maze and performing more controlled behavioral training and testing.

Comment-4: There may be a mislabeling in Figure 6g because the figure does not agree with the result text - the figure compares the population vector similarly of waking SWR vs sleep SWRs to exploration vs waking SWR and exploration vs sleep SWRs.

We thank the reviewer for raising the point, we have updated the labels accordingly.

Reviewer #2 (Public Review):

In this manuscript, Vöröslakos and colleagues describe a new behavioural testing apparatus called ThermoMaze, which should facilitate controlling when a mouse is exploring the environment vs. remaining immobile. The floor of the apparatus is tiled with 25 plates, which can be individually heated, whereas the rest of the environment is cooled. The mouse avoids cooled areas and stays immobile on a heated tile. The authors systematically changed the location of the heated tile to trigger the mouse's exploratory behaviours. The authors showed that if the same plate stays heated longer, the mouse falls into an NREM sleep state. The authors conclude their apparatus allows easy control of triggering behaviours such as running/exploration, immobility and NREM sleep. The authors also carried out single-unit recordings of CA1 hippocampal cells using various silicone probes. They show that the location of a mouse can be decoded with above-chance accuracy from cell activity during sharp wave ripples, which tend to occur when the mouse is immobile or asleep. The authors suggest that consistent with some previous results, SPW-Rs encode the mouse's current location and any other information they may encode (such as past and future locations, usually associated with them).

We thank the reviewer for carefully reading our manuscript and providing useful and constructive comments.

Strengths:

Overall, the apparatus may open fruitful avenues for future research to uncover the physiology of transitions from different behavioural states such as locomotion, immobility, and sleep. The setup is compatible with neural recordings. No training is required.

Weaknesses:

I have a few concerns related to the authors' methodology and some limitations of the apparatus's current form. Although the authors suggest that switching between the plates forces animal behaviour into an exploratory mode, leading to a better sampling of the enclosure, their example position heat maps and trajectories suggest that the behaviour is still very stereotypical, restricted mostly to the trajectories along the walls or the diagonal ones (between two opposite corners). This may not be ideal for studying spatial responses known to be affected by the stereotypicity of the animal's trajectories. Moreover, given such stereotypicity of the trajectories mice take before and after reaching a specific plate, it may be that the stable activity of SWR-P ripples used for decoding different quadrants may be representing future and/or past trajectories rather than the current locations suggested by the authors. If this is the case, it may be confusing/misleading to call such activity ' place-selective firing', since they don't necessarily encode a given place per se (line 281).

We agree with the reviewer that the current version of the ThermoMaze does not necessarily motivate the mice to sample the entire maze during warm spot transitions. However, we did show correlational evidence that neuronal firing during awake sharp-wave ripples is place-selective. Both firing rate ratios and population vectors of CA1 neurons showed a reliable correlation between those during movement and awake sharp-wave ripples (Figure 5 E and F), indicating that spatial coding during movement persists into awake SWR-P state. This finding rejects the hypothesis that neuronal firing during ripples throughout the Cooling sub-session encodes past/future trajectories, which could be explained by a lack of goal-directed behavior in order to perform the task. We hope to test whether such place-specific firing during ripples can be causally involved in maintaining an egocentric representation of space in a future study.

Besides, we have attempted to motivate the animal to visit the center of the maze during the Cooling sub-session. Moving the location of warm spots from the corners can shape the animals’ behavior and promote more exploration of the environment as we show in Suppl. Fig. 5. We agree with the Reviewer that the current size of the ThermoMaze poses these limitations. However, an example future application could be to warm the floor of a radial-arm maze by heating Peltier elements at the ends of maze arms and center in an otherwise cold room, allowing the experimenter to induce ambulation in the 1-dimensional arms, followed by extended immobility and sleep at designated areas.

Another main study limitation is the reported instability of the location cells in the Thermomaze. This may be related to the heating procedure, differences in stereotypical sampling of the enclosure, or the enclosure size (too small to properly reveal the place code). It would be helpful if the authors separate pyramidal cells into place and non-place cells to better understand how stable place cell activity is. This information may also help to disambiguate the SPW-R-related limitations outlined above and may help to solve the poor decoding problem reported by the authors (lines 218-221).

The ThermoMaze is a relatively small enclosure (20 x 20 cm) compared to typical 2D arenas (60 x 60 cm) used in hippocampal spatial studies. Due to the small environment, one possibility is that CA1 neurons encode less spatial information and only a small number of place cells could be found. Therefore, we identified place cells in each sub-session. We found 40.90%, 45.32%, and 41.26% of pyramidal cells to be place cells in the Pre-cooling, Cooling, and Post-cooling sub-sessions, respectively. Furthermore, we found on average 17.36% of pyramidal neurons pass the place cell criteria in all three sub-sessions in a daily session. Therefore, the strong decorrelation of spatial firing maps across sub-sessions cannot be explained by poor recording quality or weak neuronal encoding of spatial information but is potentially due to changes in environmental conditions.

Some additional points/queries:

Comment-1: Since the authors managed to induce sleeping on the warm pads during the prolonged stays, can they check their hypothesis that the difference in the mean ripple peak frequency (Fig. 4D) between the home cage and Thermomaze was due to the sleep vs. non-sleep states?

In response to the reviewer’s comment, we compared the ripple peak frequency that occurred during wakefulness and NREM epochs in the home cage and ThermoMaze (n = 7 sessions in 4 mice). We found that the peak frequency of the awake ripples was higher compared to both home cage and ThermoMaze NREM sleep (one-way ANOVA with Tukey’s posthoc test, ripple frequencies were: 171.63 ± 11.69, 172.21 ± 11.86, 168.19 ± 11.10 and 168.26 ± 11.08 Hz mean±SD for home cage awake, ThermoMaze awake, home cage NREM and ThermoMaze NREM conditions, p < 0.001 between awake and NREM states). We added this quantification to the revised manuscript.

Author response image 1.

NREM sleep either in home cage or in ThermoMaze affects ripple mean peak frequency similarly.

Comment-2: How many cells per mouse were recorded? How many of them were place cells? How many place cells at the same time on average? What are the place field size, peak, and mean firing rate distributions in these various conditions? It would be helpful if they could report this.

For each animal on a given day, the average number of cells recorded was 57.5, which depended on the electrodes and duration after implantation. We first applied peak firing rate and spatial information thresholds to identify place cells in each sub-session (see more details in the revised Methods section for place cell definition). We found 40.90%, 45.32%, and 41.26% of pyramidal cells to be place cells in the Pre-cooling, Cooling, and Post-cooling sub-sessions respectively. Furthermore, we found on average 17.36% of pyramidal neurons pass the place cell criteria in all three sub-sessions in a daily session.

For place cells identified in each sub-session, their place fields size is on average 61.03, 79.86, and 57.51 cm2 (standard deviation = 60.13, 69.98, and 49.64 cm2; Pre-cooling, Cooling, and Post-cooling correspondingly). A place field was defined to be a contiguous region of at least 20 cm2 (20 spatial bins) in which the firing rate was above 60% of the peak firing rate of the cell in the maze (Roux and Buzsaki et al., 2017). A place field also needs to contain at least one bin above 80% of the peak firing rate in the maze. With such definition, the average place field peak firing rate is 5.84, 5.22, and 6.48 Hz (standard deviation = 5.11, 4.65, and 5.83 Hz) and the average mean firing rate within the place fields is 4.54, 4.05, and 5.07 Hz (standard deviation = 4.00, 3.60, and 4.60).

We would like to point out that these values depend strongly on the definition of place fields, which vary widely across studies. We reason that the ThermoMaze paradigm induced place field remapping which has been reported to occur upon changes in the environment such as visual cues (Leutgeb et al., 2009). We hypothesize that temperature gradient is an important aspect among the environmental cues, thus remapping is expected. Overall, we did not aim for biological discoveries in the first presentation of the ThermoMaze. Instead, our limited goal was the detailed description of the method and its validation for behavioral and physiological experiments.

References

(1) Mizuseki K, Royer S, Diba K, Buzsáki G. Activity dynamics and behavioral correlates of CA3 and CA1 hippocampal pyramidal neurons. Hippocampus. 2012 Aug;22(8):1659-80. doi: 10.1002/hipo.22002. Epub 2012 Feb 27. PMID: 22367959; PMCID: PMC3718552.

(2) Skaggs WE,McNaughton BL,Gothard KM,Markus EJ. 1993. An information-theoretic approach to deciphering the hippocampal code. In: SJ Hanson, JD Cowan, CL Giles, editors. Advances in Neural Information Processing Systems, Vol. 5. San Francisco, CA: Morgan Kaufmann. pp 1030–1037.

(3) Roux L, Hu B, Eichler R, Stark E, Buzsáki G. Sharp wave ripples during learning stabilize the hippocampal spatial map. Nat Neurosci. 2017 Jun;20(6):845-853. doi: 10.1038/nn.4543. Epub 2017 Apr 10. PMID: 28394323; PMCID: PMC5446786.

(4) Markus, E.J., Barnes, C.A., McNaughton, B.L., Gladden, V.L. & Skaggs, W.E. Spatial information content and reliability of hippocampal CA1 neurons: effects of visual input. Hippocampus 4, 410–421 (1994).

eLife assessment

Based on analyses of retinae from genetically modified mice, and from wild-type ground squirrel and macaque, employing microscopic imaging, electrophysiology, and pharmacological manipulations, this valuable study on the role of Cav1.4 calcium channels in cone photoreceptor cells (i) shows that the expression of a Cav1.4 variant lacking calcium conductivity supports the development of cone synapses beyond what is observed in the complete absence of Cav1.4, and (ii) indicates that the cone pathway can partially operate even without calcium flux through Cav1.4 channels, thus preserving behavioral responses under bright light. The evidence for the function of Cav1.4 protein in synapse development is convincing and in agreement with a closely related earlier study by the same authors on rod photoreceptors. The mechanism of compensation of Cav1.4 loss by Cav3 remains unclear but appears to involve post-transcriptional processes. As congenital Cav1.4 dysfunction can cause stationary night blindness, this work relates to a wide range of neuroscience topics, from synapse biology to neuro-ophthalmology.

Public Review (Joint Version of all Reviewers)

Cav1.4 calcium channels control voltage-dependent calcium influx at photoreceptor synapses, and congenital loss of Cav1.4 function causes stationary night blindness CSNB2. Based on a broad portfolio of methodological approaches - genetic mouse models, immunolabeling and microscopic imaging, serial block-face-SEM, ERGs, and electrophysiology - the authors show that cone photoreceptor synapse development is strongly perturbed in the absence of Cav1.4 protein, and that expression of a nonconducting Cav1.4 channel mitigates these perturbations. Further data indicate that Cav3 channels are present, which, according to the authors, may compensate for the loss of Cav1.4 calcium currents and thus maintain cone synaptic transmission. These data, which are in agreement with a similar study by the same authors on rod photoreceptor synapses, help to explain what functional defects exactly cause CSNB2 and why it is accompanied by only mild visual impairment.

The strengths of the present study are its conceptual and experimental soundness, the broad spectrum of cutting-edge methodological approaches pursued, and the convincing differential analysis of mutant phenotypes. Weaknesses mainly concern the fact that the mechanism by which Cav3 channels might partially compensate for the loss of Cav1.4 calcium currents remains unclear.

Author response:

The following is the authors’ response to the previous reviews.

Intro. 

47-48 rewrite sentence

This sentence has been rewritten as: Photoreceptor synapses are specialized with a vesicle-associated ribbon organelle and postsynaptic neurites of horizontal and bipolar cells that invaginate deep within the terminal

Results 

Major comment. Lines 100-103 

The new rod data presented here looks like an n = 1. Neither the Results section nor Supp Fig S1, describe the number of cells used. Nor do the authors offer a statistical description with averages, etc.. In addition, the single traces are much improved over their previous study (Maddox et al eLife 2020), but the authors have not described any new approach or trick that improved their rod Ica. Neither Methods section nor Supp section describes the procedure for patching rods (solutions, or Vh which is critical for assessing T-type currents). 

Suggestion, if more data exists, then present it. Otherwise, drop the argument. 

The recording methodology for recording rods was like that for cones and this has been clarified in the Methods section (lines 725-752). Averaged data (n= at least 5 per group) and statistical analyses have been added to Fig.S1 (renamed Figure 2-Figure Supplement 1), and clearly show that no Ca2+ currents are present in the KI rods.

Supp Fig S2. The legend needs to be fixed. Conversion to PDF file may have created these formatting errors. 

This has been corrected (renamed Figure 3-Figure Supplement 2).

Fig 8 a. The position of the light stimulus bar in the KO panel appears to be out of place, shifted too far to the left. 

This has been corrected.

Major comments. 219-221 

The use of Fluo3-AM is not properly stated here. The text reads "cone pedicles filled with the Ca2+ indicator Fluo3". The wording used could be wrongly interpreted as: whole-cell filling of the cones via patch electrode. However, the Methods section describes bathing the retina in Fluo3-AM, which presumably fills PRs, HCs tips, Mueller glia and bpc dendrites. The Results section should acknowledge that the retina was loaded with Fluo3-AM. 

The cell types, and their processes (Muellers, HCs, bpc, PRs), present in a cone pedicle ROI will likely contribute to the Fluo3 readout of Ca2+ in the OPL, because 1) the EM images in Fig 7 highlight how interdigitated the processes are with the presynapse, 2) all express Cav channels, and many if not all express L-Type Cavs in their processes (glia, HC, on-bcs and PRs), and 3) all are depolarized with the addition of high extracellular KCl. The inclusion of Isradipine will inhibit L-type Cavs on pre- and post-synaptic targets, failing to specifically isolate PR Ca2+. Furthermore, Glu Receptor blockers are used here, which would be a great idea if the cones were stimulated with light; however, KCl bypasses the excitatory synaptic pathway and depolarizes all processes within the ROI. Hence, all cellular parts in the ROI will potentially contribute to Fluo3-Ca2+ signals. 

Suggestions for presentation of these findings. Ultimately your conclusion is suitable " 233 to 234...... Taken together, our results suggest that Cav3 channels nominally support Ca2+ signals and synaptic transmission in cones of G369i KI mice". The dramatic reduction in Fluo3-Ca2+ signals in the OPL G369i retinas (Fig 9) is a valuable finding for the following reasons: 1) the results do not show a clear compensation from intracellular stores that could potentially supersede the T-type currents in the G369i (which is an argument you make), and 2) there is a massive loss of Ca2+ influx in the OPL of G369i retinas. Since G369i is specific to the PRs, and only cones are present in the mutant G369i, the loss of Fluo3-Ca2+ signal in the mutant ROI reflects in large part loss of cone Fluo3-Ca2+ signals. Your findings illustrate the severity of the mutation, which has also been addressed in the various electro-physio sections of the MS. 

Figure 9 also needs to be more clear about 1) the loading of the cells with AM-dye, and 2) the presence of glia, HCs and bc dendrites in the PNA demarcated ROIs. 

We regret that we did not make this more clear, but our Fluo 3 loading protocol of whole retina followed by vertical slicing allowed for loading primarily of photoreceptors in the portion of the outer retina that we imaged. We clarified this with the following edit to the text (lines 220-226):

“To test if the diminished HC light responses correlated with lower presynaptic Ca2+ signals in G369i KI cones, we performed 2-photon imaging of vertical slices prepared from whole retina that was incubated  with the Ca2+ indicator Fluo3-AM and  Alexa-568-conjugated peanut agglutinin (PNA) to demarcate regions of interest (ROIs) corresponding to cone pedicles. With this approach Fluo3 fluorescence was detected only in photoreceptors and ganglion cells and not inner retinal cell-types (e.g., horizontal cells, bipolar cells, Mueller cell soma). Thus, Ca2+ signals reported by Fluo3 fluorescence near PNA-labeling originated primarily from cones.”

We also note that given the considerably larger volume of the cone pedicle relative to the postsynaptic neurites of horizontal and bipolar cells, as well as neighboring glia, it seems unlikely that the latter would contribute significantly to the isradipine-sensitive Ca2+ signal measured in the ROI above the PNA labeling. Moreover, to our knowledge the contribution of Cav1 L-type channels to postsynaptic Ca2+ signals in the dendritic tips of horizontal cells and bipolar cells has not been demonstrated.

Author response:

The following is the authors’ response to the current reviews.

Reviewer #1 (Public Review):

Major shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analyses for several experiments. Because of these omissions, it is difficult to conclude that the data justify the conclusions. The significance of the data presented is overstated, as many of the experiments presented confirm/support previously published work. The study provides a modest advance in the understanding of the complex issue of SHH membrane extraction.

Major shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analysis for several experiments.

This statement is not correct for the revised manuscript: The normalization strategies used are clearly described in the manuscript and are not unusual. Each experiment is now statistically analyzed.

The significance of the data presented is overstated, as many of the experiments presented confirm/support previously published work.

As reviewer 2 correctly points out, there are many competing models for Hedgehog release. Our study cannot possibly support them all - the reviewer's statement is therefore misleading. In fact, our careful biochemical analysis of the mechanistics of Dispatched- mediated Shh export supports only two of them: The model of proteolytic processing of Shh lipid anchors (shedding) and the model of lipoprotein-mediated Shh transport. In contrast, our study does not support the predominant model of Dispatched-mediated extraction of dual-lipidated Shh and delivery to Scube2, which is currently thought to act as a soluble Shh chaperone. We also do not support Dispatched function in Shh endocytic recycling and cytoneme loading, or any of the other models such as exosome-mediated or micelle Shh transport.

Reviewer #2 (Public Review):

A novel and surprising finding of the present study is the differential removal of Shh N- or C- terminal lipid anchors depending on the presence of HDL and/or Disp. In particular, the identification of a non-palmitoylated but cholesterol-modified Shh variant that associates with lipoproteins is potentially important. The authors use RP-HPLC and defined controls to assess the properties of processed forms of Shh, but their precise molecular identity remains to be defined. One caveat is the heavy reliance on overexpression of Shh in a single cell line. The authors detect Shh variants that are released independently of Disp and Scube2 in secretion assays, but these are excluded from interpretation as experimental artifacts. Therefore, it would be important to demonstrate key findings in cells that endogenously secrete Shh.

We would like to respond as follows:

The authors use RP-HPLC and defined controls to assess the properties of processed forms of Shh, but their precise molecular identity remains to be defined.

This is the original reviewers statement regarding our original manuscript submission. We believe that the biochemical and functional data presented in the VOR clearly describe the molecular identity of solubilized Shh: it is monolipidated, lipoprotein-associated, and highly biologically active in two established Shh bioassays.

One caveat is the heavy reliance on overexpression of Shh in a single cell line.

As stated by reviewer 1, the strength of our work is the use of a bicistronic SHH-Hhat system to consistently generate doubly lipidated ligand to determine the amount and lipidation status of SHH released into cell culture media. This unique system therefore eliminates the artifacts of protein overexpression. We have also added two other cell lines to our VOR that produce the same results (including Panc1 cells that endogenously produce Shh, Supplementary Figure 1).

The authors detect Shh variants that are released independently of Disp and Scube2 in secretion assays, but these are excluded from interpretation as experimental artifacts.

As the reviewer correctly points out, these variants are released independently of Disp and Scube2, both of which are known as essential release factors in vivo. These variants are therefore by definition experimental artifacts. The forms we have included in our analysis are the alternative forms that are clearly dependent on Dispatched and Scube2 for their release - as shown in the first figure in the manuscript, and in pretty much every other figure after that.

---

The following is the authors’ response to the previous reviews.

Reviewer #1 (Public Review):

Key shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analyses for several experiments.

In the updated version of the paper, we have addressed all of this reviewer's criticisms. Most importantly, we have performed several additional experiments to address the concern that unusual normalization strategies were used in our paper and that quantification and statistical analyses were lacking for several experiments. We have now analyzed the full set of release conditions for Shh and engineered proteins from Disp-expressing n.t. control cells and Disp-/- cells both in the presence and absence of Scube2 (Figure 1A'-D', Figure 2E added to the paper, Figure 3B'-D', Figure 5C and Figure S2F-H). Previously, we had only quantified protein release from n.t. controls and Disp-/- cells in the presence but not in the absence of Scube2 under serum-depleted conditions. Quantifications of serum-free protein release and Shh release under conditions ranging from 0.05% FCS to 10% FCS were completely missing from the earlier versions of the manuscript, but have now been added to our paper. In addition, we have reanalyzed all of the data sets in the above figures, as well as Figures 2C and S1B, to address the issue of "unusual normalization strategies": unlike previous assays in which the highest amount of protein detected in the media was set to 100% and all other proteins in that experiment were expressed relative to that value, we now directly compare the relative amounts of cellular and corresponding solubilized proteins as a method to quantify release without the need for data normalization (Figs. 1A'-D', 2C,E, 3B'-D', E, 5C, Fig. S1B, S2F-H).

We have also repeated the qPCR analyses in C3H10T1/2 cells and now show that the same Shh/C25AShh activities can be observed when using another Shh responsive cell line, NIH3T3 cells (Fig. 4B, 6B, fig. S5B).

We would like to point out that if the criticism refers to the presentation of our RP-HPLC and SEC data, the normalization of the strongest eluted protein signal to 100% for all proteins tested is necessary to put their behavior in a clearer relationship. This is because only the relative positions of protein elution, and not their amounts, are important in these experiments.

The significance of the data provided is overstated because many of the presented experiments confirm/support previously published work.

To mitigate the first reviewer's comment that the significance of the data presented is overstated, we now clearly distinguish between our novel results and the known aspect of Hh release on lipoproteins throughout our paper. We now clearly describe what is new and important in our paper: First, contrary to the general perception in the field, Disp and Scube2 are not sufficient to solubilize Shh, casting doubt on the currently accepted model that Scube2 accepts dual-lipidated Shh from Disp and transports it to the receptor Ptch. Second, lipoproteins shift dual Shh processing to N-terminal peptide processing only to generate different soluble Hh forms with different activities (as shown in Figure 4C). Third, and again contrary to popular belief, this new release mode does not inactivate Shh, as we now show in two established cellular assays for Hh biofunction (Figures 4A-C, 5B'', 6B and S5C-G). Fourth, and most importantly, we show that spatiotemporally controlled, Disp-, Scube2- and HDL-mediated Shh release absolutely requires dual lipidation of the membrane-associated Shh precursor prior to its release. This finding (as shown in Figures 1 and S2) changes the interpretation of previously published in vivo data that have long been interpreted as evidence for the requirement of dual Shh lipidation for full receptor binding and activation.

The study provides a modest advance in our understanding of the complex issue of Shh membrane extraction.

Although we agree that our results integrate our novel observations into previously established concepts of Hh release and trafficking, we also hope that our data cast well-founded doubt on the current view that the issue of Hh release and trafficking is largely resolved by the model of Disp-mediated Shh hand-over to Scube2 and then to Ptch, which requires interactions with both Shh lipids. Our data show that this is clearly not the case in the presence of lipoproteins. Thus, the significance of our data is that models of Shh lipid-regulated signaling to Ptch obtained using the dual-lipidated Shh precursor prior to its Disp- and Scube2-mediated conversion into a delipidated or monolipidated, HDL-associated soluble ligand are likely to describe a non-physiological interaction. Instead, our work describes a highly bioactive soluble ligand with only one lipid still attached, which has not been described before in the literature. The in vivo endpoint analyses presented in Fig. S8 suggest that this new protein variant is likely to play an important role during development.

Reviewer #2 (Public Review):

The precise molecular identity (of the released Shh) remains to be defined.

We would like to respond that the direct comparison of soluble proteins and their well-defined double-lipidated precursors side-by-side in the same experiment, as shown in our paper, determines all relevant molecular changes in the Shh release process. Most importantly, we show by SDS-PAGE and RP-HPLC that HDL restricts Shh processing to the N-terminus and that the absence of HDL results in double processing of Shh during its release. We also show by SEC that the C-terminus binds the protein to HDL. In addition, the fly experiments confirm the requirement for N-terminal Hh processing, but not for processing of the C-terminal peptide, and suggest that the N-terminal Cardin-Weintraub sequence replaced by the functionally blocking tag represents the physiological cleavage site.

It would be important to demonstrate key findings in cells that secrete Shh endogenously.

We now confirm the key findings of our study in Panc1 cells that endogenously produce and secrete Shh: As shown in Fig. S1D, we find that soluble proteins are processed but retain the C-cholesterol, which we now directly confirm by RP-HPLC (Fig. S4F-H). The in vivo analyses shown in Fig. S8 suggest that the key finding - that N-terminal but not C-terminal Hh shedding is required for release - can be supported, at least in the fly: here, Hh variants impaired in their ability to be processed N-terminally strongly repress the endogenous protein, whereas the same protein impaired in its ability to be processed C-terminally does not.

The authors detect Shh variants that are expressed independently of Disp and Scube2 in secretion assays, but are excluded from interpretation as experimental artifacts.

We agree with the reviewer's criticism that the amounts of Shh released independently of Disp and Scube2 in secretion assays were not quantified and analyzed statistically to justify their proposed status as not physiologically relevant. We now show that these forms are indeed secretion artifacts (Fig. 3E and Fig. S2F-H show quantification of the lower electrophoretic mobility protein fraction (i.e., the "top" band representing the double-lipidated soluble protein fraction)) because this fraction is released independently of Disp and Scube2.

eLife assessment

This study uses a deep neural network approach to challenge the role of spatially selective neurons like place, head or border cells for position decoding. The findings are important as they suggest that such functional cell types may emerge naturally from object recognition in complex visual environments, but are neither necessary, nor particularly critical for position decoding. However, direct evidence supporting this conclusion remains incomplete.

Author response:

We thank the reviewers for their engagement and constructive comments. This provisional response aims to clarify key misconceptions, address major criticisms, and outline our revision plans.

A primary concern of the reviewers appears to be our model's limitations in addressing a broad range of empirical findings. This, however, misinterprets our core contribution. Our work centers on a cautionary tale that before advocating for newly discovered cell types and their purported special roles in spatial cognition—an approach prevalent in the field—such claims must be tested against alternative (null) hypotheses that may contradict intuitive expectations. We present such an alternative hypothesis regarding spatial cells and their assumed privileged roles. We show that key findings in the field - spatial “cell types”,  arise in a set of null models without spatial grounding (including untrained variants) despite the models not being a model for spatial processing, and we also found that they had no privileged role for representing spatial information.

Our proposal is not a new model attempting to explain the brain, and therefore we do not aim to capture every empirical finding. Indeed, we would not expect an object recognition model (and its untrained variant) with no explicit spatial grounding to account for all phenomena in spatial cognition. This underscores our key point: if there exists a basic, spatially agnostic model that can explain certain degrees of empirical findings using criteria from the literature (i.e. place, head-direction and border cells), what implications does this have for the more complex theories and models proposed as underlying mechanisms of special cell types?

Regarding concerns about the limited scope and generalizability of our setting, we will clarify that we considered multiple DNN architectures, both trained and untrained, on multiple decoding tasks (position, head direction, and nearest-wall distance). We plan to extend our experiments further as detailed in the revision plan below.

Further, there was a methodological concern about using a linear decoder on a fixed DNN for spatial decoding tasks being a form of "hacking". However, linear readout is standard practice in neuroscience to characterize information available in a neural population. Moreover, our tests on untrained networks also showed spatial decoding capabilities, suggesting it's not solely due to the linear readout.

For our full revision plan:

(1) We will revise the manuscript to better reflect these above points, clarifying our paper's stance and improving the writing to reduce misconceptions.

(2) We will address individual public reviews in more detail.

(3) We intend to address key reviewer recommendations, focusing on better situating our work within the broader context of the existing literature whilst emphasizing the null hypothesis perspective.

(4) In general, we will consider additional aspects of the literature and conduct new experiments to strengthen the relevance of our work to existing work. We highlight a number of potential experiments which we believe can address reviewer concerns:

a. Blurring the visual inputs to DNNs to match rodent perception.

b. Vary environmental settings to verify whether our findings are more

generalizable (which we predict to be the case).

c. Vary the environment to assess remapping effects, which will strengthen the

connection of our work to the literature.

Reviewer #1 (Public Review):

Summary:<br /> This study investigated spatial representations in deep feedforward neural network models (DDNs) that were often used in visual tasks. The authors create a three-dimensional virtual environment, and let a simulated agent randomly forage in a smaller two-dimensional square area. The agent "sees" images of the room within its field of view from different locations and heading directions. These images were processed by DDNs. Analyzing model neurons in DDNs, they found response properties similar to those of place cells, border cells and head direction cells in various layers of deep nets. A linear readout of network activity can recover key spatial variables. In addition, after removing neurons with strong place/border/head direction selectivity, one can still decode these spatial variables from the remaining neurons in the DNNs. Based on these results, the authors argue that that the notion of functional cell types in spatial cognition is misleading.

Strengths:<br /> This paper contains interesting and original ideas, and I enjoy reading it. Most previous studies (e.g., Banino, Nature, 2018; Cueva & Wei, ICLR, 2018; Whittington et al, Cell, 2020) using deep network models to investigate spatial cognition mainly relied on velocity/head rotation inputs, rather than vision (but see Franzius, Sprekeler, Wiskott, PLoS Computational Biology, 2007). Here, the authors find that, under certain settings, visual inputs alone may contain enough information about the agent's location, head direction and distance to the boundary, and such information can be extracted by DNNs. If confirmed, this is potentially an interesting and important observation.

Weaknesses:<br /> While the findings reported here are interesting, it is unclear whether they are the consequence of the specific model setting, and how well they would generalize. Furthermore, I feel the results are over-interpreted. There are major gaps between the results actually shown and the claim about the "superfluousness of cell types in spatial cognition". Evidence directly supporting the overall conclusion seems to be weak at the moment.

Major concerns:

(1) The authors reported that, in their model setting, most neurons throughout the different layers of CNNs show strong spatial selectivity. This is interesting and perhaps also surprising. It would be useful to test/assess this prediction directly based on existing experimental results. It is possible that the particular 2-d virtual environment used is special. The results will be strengthened if similar results hold for other testing environments.

In particular, examining the pictures shown in Fig. 1A, it seems that local walls of the 'box' contain strong oriented features that are distinct across different views. Perhaps the response of oriented visual filters can leverage these features to uniquely determine the spatial variable. This is concerning because this is a very specific setting that is unlikely to generalize.

(2) Previous experimental results suggest that various function cell types discovered in rodent navigation circuits persist in dark environments. If we take the modeling framework presented in this paper literally, the prediction would be that place cells/head direction cells should go away in darkness. This implies that key aspects of functional cell types in the spatial cognition are missing in the current modeling framework. This limitation needs to be addressed or explicitly discussed.

(3) Place cells/border cell/ head direction cells are mostly studied in the rodent's brain. For rodents, it is not clear whether standard DNNs would be good models of their visual systems. It is likely that rodent visual system would not be as powerful in processing visual inputs as the DNNs used in this study.

(4) The overall claim that those functional cell types defined in spatial cognition are superfluousness seems to be too strong based on the results reported here. The paper only studied a particular class of models, and arguably, the properties of these models have a major gap to those of real brains. Even though, in the DNN models simulated in this particular virtual environment, (i) most model neurons have strong spatial selectivity; (ii) removing model neurons with the strongest spatial selectivity still retain substantial spatial information, why this is relevant to the brain? The neural circuits may operate in a very different regime. Perhaps a more reasonable interpretation of the results would be: these results raise the possibility that those strongly selective neurons observed in the brain may not be essential for encoding certain features, as something like this is observed in certain models. It is difficult to draw definitive conclusions about the brain based on the results reported.

eLife assessment

This important study examined the complexity of emergent dynamics of large-scale neural network models after perturbation (perturbational complexity index, PCI) and used it as a measurement of consciousness to account for previous recordings of humans at various anesthetized levels. The evidence supporting the conclusion is solid and constitutes a unified framework for different observations related to consciousness. There are many fields that would be interested in this study, including cognitive neuroscience, psychology, complex systems, neural networks, and neural dynamics.

Reviewer #1 (Public Review):

Summary:

This paper attempts to measure the complex changes of consciousness in the human brain as a whole. Inspired by the perturbational complexity index (PCI) from classic research, authors introduce simulation PCI (𝑠𝑃𝐶𝐼) of a time series of brain activity as a measure of consciousness. They first use large-scale brain network modeling to explore its relationship with the network coupling and input noise. Then the authors verify the measure with empirical data collected in previous research.

Strengths:

The conceptual idea of the work is novel. The authors measure the complexity of brain activity from the perspective of dynamical systems. They provide a comparison of the proposed measure with four other indexes. The text of this paper is very concise, supported by experimental data and theoretical model analysis.

Weaknesses:

(1) Consciousness is a network phenomenon. The measure defined by the authors is to consider the maximal sPCI across the nodes stimulated. This measure is based on the time series of one node. The measure may be less effective in quantifying the ill relationship between nodes. This may contribute to the less predictive power of anesthesia (Figure 4b).

(2) One of the focuses of the work is the use of a dynamic model of brain networks. The explanation of the model needs to be in more detail.

(3) The equations should be checked. For example, there should be no max on the left side of the first equation on page 13.

(4) The quality of the figures should be improved.

(5) Figure 4 should be discussed and analyzed more in the text.

(6) The usage of the terms PCI and sPCI should be distinguished.

Reviewer #2 (Public Review):

Summary:

Breyton and colleagues analysed the emergent dynamics from a neural mass model, characterised the resultant complexity of the dynamics, and then related these signatures of complexity to datasets in which individuals had been anaesthetised with different pharmacological agents. The results provide a coherent explanation for observations associated with different time series metrics, and further help to reinforce the importance of modelling when integrating across scientific studies.

Strengths:

* The modelling approach was clear, well-reasoned, and explicit, allowing for direct comparison to other work and potential elaboration in future studies through the augmentation with richer neurobiological detail.

* The results serve to provide a potential mechanistic basis for the observation that the Perturbational Complexity Index changes as a function of the consciousness state.

Weaknesses:

* Coactivation cascades were visually identified, rather than observed through an algorithmic lens. Given that there are numerous tools for quantifying the presence/absence of cascades from neuroimaging data, the authors may benefit from formalising this notion.

* It was difficult to tell, graphically, where the model's operating regime lay. Visual clarity here will greatly benefit the reader.

eLife assessment

This is a conceptually appealing study in which the authors identify genes whose function is important for the development of inhibitory (GABA) neurons, and then demonstrate that a diet rich in ketone body β-hydroxybutyrate partially suppresses specific mutant phenotypes. The authors provide compelling evidence that features methods, data and analyses more rigorous than the current state-of-the-art. Conceptually, this is evidence of a rescue of a developmental defect with dietary metabolic intervention, linking, in an elegant way, the underpinning genetic mechanisms with novel metabolic pathways that could be used to circumvent the defects.

Reviewer #1 (Public Review):

Summary

This interesting study, which has greatly improved in the current revised version, explores the mechanism behind an increased susceptibility of daf-18/PTEN mutant nematodes to paralyzing drugs that exacerbate cholinergic transmission. The authors use state-of-the-art genetics and neurogenetics coupled with locomotor behavior monitoring and neuroanatomical observations using gene expression reporters to show that the susceptibility occurs due to low levels of DAF-18/PTEN in developing inhibitory GABAergic neurons early during larval development (specifically, during the larval L1 stage). DAF-18/PTEN is convincingly shown to act cell-autonomously in these cells upstream of the PI3K-PDK-1-AKT-DAF-16/FOXO pathway, consistent with its well-known role as an antagonist of this conserved signaling pathway. The authors exclude a role for the TOR pathway in this process and present evidence implicating selectivity towards-developing GABAergic neurons of the ventral nerve cord in comparison to excitatory cholinergic neurons. Finally, the authors show that a diet supplemented with a ketogenic body, β-hydroxybutyrate, which also counteracts the PI3K-PDK-1-AKT pathway, promoting DAF-16/FOXO activity, partially rescues the proper development (morphology and function) of GABAergic neurons in daf-18/PTEN mutants, but only if the diet is provided early during larval development. This strongly suggests that the critical function of DAF-18/PTEN in developing inhibitory GABAergic neurons is to prevent excessive PI3K-PDK-1-AKT activity during this critical and particularly sensitive period of their development in juvenile L1 stage worms. Whether or not the sensitivity of GABAergic neurons to DAF-18/PTEN function is a defining and widespread characteristic of this class of neurons in C. elegans and other animals, or rather a particularity of the early developmental stage of the GABAergic neurons investigated remains to be determined.

Strengths:

The study reports interesting and important findings, advancing the knowledge of how daf-18/PTEN and the PI3K-PDK-1-AKT pathway can influence neurodevelopment, and providing a valuable paradigm to study the selectivity of gene activities towards certain neurons. It also defines a solid paradigm to study the potential of dietary interventions (such as ketogenic diets) or other drug treatments to counteract (prevent or revert?) neurodevelopment defects and stimulate DAF-16/FOXO activity.

Weaknesses:

The fact that other non-GABAergic C. elegans neurons (i.e., AIY and HSN neurons) are also sensitive to DAF-18/PTEN activity during development suggests that the particular sensitivity observed in the GABAergic ventral nerve cord neurons in this study could be unrelated to their neurotransmitter class (GABAergic) per se, but rather to some other neuronal property (a critical period of plasticity or activity-based wiring?) that these neurons share with the AIY and HSN neurons, and not with the other surveyed ventral nerve cord neurons (the excitatory cholinergic neurons). The relevance of this possibility within the framework of understanding the role of DAF-18/PTEN in E/I imbalance across clades is not fully clear at this stage.

Reviewer #2 (Public Review):

Summary:

Disruption of the excitatory/inhibitory (E/I) balance have been reported in Autism Spectrum disorders (ASD) to which PTEN mutations have been associated. Giunti et al choose to explore the impact of PTEN mutations on the balance between E/I signaling using as a platform the C. elegans neuromuscular system where both cholinergic (E) and GABAergic (I) motor neurons regulate muscle contraction and relaxation. Mutations in daf-18/PTEN specifically affect morphologically and functionally the GABAergic (I) system, while leaving the cholinergic (E) system unaffected. The study further reveals that the observed defects in the GABAergic system in daf-18/PTEN mutants are attributed to reduced activity of DAF-16/FOXO during development.<br /> Moreover, ketogenic diets (KGDs), known for their effectiveness in disorders associated with E/I imbalances such as epilepsy and ASD, are found to induce DAF-16/FOXO during early development. Supplementation with β-hydroxybutyrate in the nematode at early developmental stages proves to be both necessary and sufficient to correct the effects on GABAergic signaling in daf-18/PTEN mutants.

Strengths:

The authors combined pharmacological, behavior and optogenetic experiments to show the GABAergic signaling impairment at the C. elegans neuromuscular junction in DAF-18/PTEN and DAF-16/FOXO mutants. Moreover, by studying the neuron morphology, they point towards neurodevelopmental defects in the GABAergic motoneurons involved in locomotion. Using the same set of experiments, they demonstrate that a ketogenic diet can rescue the inhibitory defect in the daf-18/PTEN mutant at an early stage.

Weaknesses:

The morphological experiments hint towards a pre-synaptic defect to explain the GABAergic signaling impairment, but it would have also been interesting to check the post-synaptic part of the inhibitory neuromuscular junctions such as the GABA receptor clusters to assess if the impairment is only presynaptic or both post and presynaptic. Moreover, analysing post-synaptic functionality in-depth using electrophysiology would be beneficial too.<br /> Nevertheless, this question alone could be entirely the subject of another paper and is not essential to the primary message of the paper.

Conclusion:

Giunti et al provide fundamental insights into the connection between PTEN mutations and neurodevelopmental defects through DAF-16/FOXO and shed light on the mechanisms through which ketogenic diets positively impact neuronal disorders characterized by E/I imbalances.

Reviewer #3 (Public Review):

Summary:

This is a conceptually appealing study by Giunti et al in which the authors identify a role for PTEN/daf-18 and daf-16/FOXO in the development of inhibitory GABA neurons, and then demonstrate that a diet rich in ketone body β-hydroxybutyrate partially suppresses the PTEN mutant phenotypes. The authors use three assays to assess their phenotypes: 1) pharmacological assays (with levamisole and aldicarb); 2) locomotory assays and 3) cell morphological assays. These assays are carefully performed and the article is clearly written. While neurodevelopmental phenotypes had been previously demonstrated for PTEN/daf-18 and daf-16/FOXO (in other neurons), and while KB β-hydroxybutyrate had been previously shown to increase daf-16/FOXO activity (in the context of aging), this study is significant because it demonstrates the importance of KB β-hydroxybutyrate and DAF-16 in the context of neurodevelopment. Conceptually, and to my knowledge, this is the first evidence I have seen of a rescue of a developmental defect with a dietary metabolic intervention, linking, in an elegant way, the underpinning genetic mechanisms with novel metabolic pathways that could be used to circumvent the defects.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This interesting study explores the mechanism behind an increased susceptibility of daf-18/PTEN mutant nematodes to paralyzing drugs that exacerbate cholinergic transmission. The authors use state-of-theart genetics and neurogenetics coupled with locomotor behavior monitoring and neuroanatomical observations using gene expression reporters to show that the susceptibility occurs due to low levels of DAF-18/PTEN in developing inhibitory GABAergic neurons early during larval development (specifically, during the larval L1 stage). DAF-18/PTEN is convincingly shown to act cell-autonomously in these cells upstream of the PI3K-PDK-1-AKT-DAF-16/FOXO pathway, consistent with its well-known role as an antagonist of this conserved signaling pathway. The authors exclude a role for the TOR pathway in this process and present evidence implicating selectivity towards developing GABAergic neurons. Finally, the authors show that a diet supplemented with a ketogenic body, β-hydroxybutyrate, which also counteracts the PI3K-PDK-1-AKT pathway, promoting DAF-16/FOXO activity, partially rescues the proper development (morphology and function) of GABAergic neurons in daf-18/PTEN mutants, but only if the diet is provided early during larval development. This strongly suggests that the critical function of DAF18/PTEN in developing inhibitory GABAergic neurons is to prevent excessive PI3K-PDK-1-AKT activity during this critical and particularly sensitive period of their development in juvenile L1 stage worms. Whether or not the sensitivity of GABAergic neurons to DAF-18/PTEN function is a defining and widespread characteristic of this class of neurons in C. elegans and other animals, or rather a particularity of the unique early-stage GABAergic neurons investigated remains to be determined.

Strengths:

The study reports interesting and important findings, advancing the knowledge of how daf-18/PTEN and the PI3K-PDK-1-AKT pathway can influence neurodevelopment, and providing a valuable paradigm to study the selectivity of gene activities towards certain neurons. It also defines a solid paradigm to study the potential of dietary interventions (such as ketogenic diets) or other drug treatments to counteract (prevent or revert?) neurodevelopment defects and stimulate DAF-16/FOXO activity.

Weaknesses:

(1) Insufficiently detailed methods and some inconsistencies between Figure 4 and the text undermine the full understanding of the work and its implications.

The incomplete methods presented, the imprecise display of Figure 4, and the inconsistency between this figure and the text, make it presently unclear what are the precise timings of observations and treatments around the L1 stage. What exactly do E-L1 and L1-L2 mean in the figure? The timing information is critical for the understanding of the implications of the findings because important changes take place with the whole inhibitory GABAergic neuronal system during the L1 stage into the L2 stage. The precise timing of the events such as neuronal births and remodelling events are welldescribed (e.g., Figure 2 in Hallam and Jin, Nature 1998; Fig 7 in Mulcahy et al., Curr Biol, 2022). Likewise, for proper interpretation of the implication of the findings, it is important to describe the nature of the defects observed in L1 larvae reported in Figure 1E - at present, a representative figure is shown of a branched commissure. What other types of defects, if any, are observed in early L1 larvae? The nature of the defects will be informative. Are they similar or not to the defects observed in older larvae?

We thank the reviewer for highlighting these areas for improvement. We have updated and clarified the timing of observation in the text, figures, and methodology section accordingly.

All experiments were conducted using age-synchronized animals. Gravid worms were placed on NGM plates and removed after two hours. The assays were then carried out on animals that hatched from the eggs laid during this specific timeframe.

Regarding the detailed timings outlined in the original Figure 4 (now Figure 5 in the revised version), we provided the following information in the revised version: For experiments involving continuous exposure to βHB throughout development, the gravid worms were placed on NGM plates containing the ketone body and removed after two hours. Therefore, this exposure covered the ex-utero embryonic development period up to the L4-Young adult stage when the experiments were conducted.

In experiments involving exposure at different developmental stages as those depicted in Figure 4 of the original version, (now Figure 5, revised version), animals were transferred between plates with and without βHB as required. We exposed daf-18/PTEN mutant animals to βHB-supplemented diets for 18-hour periods at different developmental stages (Figure 5A, revised version). The earliest exposure occurred during the 18 hours following egg laying, covering ex-utero embryonic development and the first 8-9 hours of the L1 stage. The second exposure period encompassed the latter part of the L1 stage, the entire L2 stage, and most of the L3 stage. The third exposure spanned the latter part of the L3 stage (~1-2 hours), the entire L4 stage, and the first 6-7 hours of the adult stage.

All this information has been conveniently included in Figure 5, text (Page13, lines 259-276), and in methodology (Page 4, Lines 85-90, Revised Methods and Supplementary information) of the revised manuscript.

In response to the reviewer's suggestion, we have also included photos of daf-18 worms at the L1 stage (30 min/1h post-hatching). Defects are already present at this early stage, such as handedness and abnormal branching commissures, which are also observed in adult worm neurons (see Supplementary Figure 4, revised version). 

These defects manifest in DD neurons shortly after larval birth. The prevalence of animals with errors is higher in L4 worms (when both VDs and DDs are formed) compared to early L1s (Figures 3 C-E and Supplementary Figure 4, revised version). This suggests that defects in VD neurons also occur in daf-18 mutants. Indeed, when we analyzed the neuronal morphology of several wild-type and daf-18 mutant animals, we found defects in the commissures corresponding to both DD and VD neurons (Supplementary Figure 3, revised version). 

These data are now included in the revised version (Results (Page 10, lines 177-196), Discussion (Pages 14-16), Main Figure 3, and Supplementary Figures 3, 4 and 7 revised version)

(2) The claim of proof of concept for a reversal of neurodevelopment defects is not fully substantiated by data.

The authors state that the work "constitutes a proof of concept of the ability to revert a neurodevelopmental defect with a dietary intervention" (Abstract, Line 56), however, the authors do not present sufficient evidence to distinguish between a "reversal" or prevention of the neurodevelopment defect by the dietary intervention. This clarification is critical for therapeutic purposes and claims of proof-of-concept. From the best of my understanding, reversal formally means the defect was present at the time of therapy, which is then reverted to a "normal" state with the therapy. On the other hand, prevention would imply an intervention that does not allow the defect to develop to begin with, i.e., the altered or defective state never arises. In the context of this study, the authors do not convincingly show reversal. This would require showing "embryonic" GABAergic neuron defects or showing convincing data in newly hatched L1 (0-1h), which is unclear if they do so or not, as I have failed to find this information in the manuscript. Again, the method description needs to be improved and the implications can be very different if the data presented in Figure 2D-E regard newly born L1 animals (0-1h) or L1 animals at say 5-7h after hatching. This is critical because the development of the embryonically-born GABAergic DD neurons, for instance, is not finalized embryonically. Their neurites still undergo outgrowth (albeit limited) upon L1 birth (see DataS2 in Mulcahy et al., Curr Biol 2022), hence they are susceptible to both committing developmental errors and to responding to nutritional interventions to prevent them. In contrast to embryonic GABAergic neurons, embryonic cholinergic neurons (DA/DB) do not undergo neurite outgrowth post-embryonically (Mulcahy et al., Curr Biol 2022), a fact which could provide some mechanistic insight considering the data presented. However, neurites from other post-embryonically-born neurons also undergo outgrowth postembryonically, but mostly during the second half of the L1 stage following their birth up to mid-L2, with significant growth occurring during the L1-L2 transition. These are the cholinergic (VA/VB and AS neurons) and GABAergic (VD) neurons. The fact that AS neurons undergo a similar amount of outgrowth as VD neurons is informative if VD neurons are or are not susceptible to daf-18/PTEN activity. Independently, DD neurons are still quite unique on other aspects (see below), which could also bring insight into their selective response.

Finally, even adjusting the claim to "constitutes a proof-of-concept of the ability of preventing a neurodevelpmental defect with a dietary intervention" would not be completely precise, because it is unclear how much this work "constitutes a proof of concept". This is because, unless I misunderstood something, dietary interventions are already applied to prevent neurodevelopment defects, such as when folic acid supplementation is recommended to pregnant women to prevent neural tube defects in newborns.

Thank you very much for pointing out this issue and highlighting the need to further investigate the ameliorative capacity of βHB on GABAergic defects in daf-18 mutants. In the revised version, we have included experiments to address this point.

Our microscopy analyses strongly indicate that the development of DD neurons is affected, with errors observed as early as one-hour post-hatching (Main Figure 3, and Supplementary Figures  4 and 7, revised version). Additionally, based on the position of the commissures in L4s, our results strongly suggest that VD neurons are also affected (Supplementary Figure 3, revised version). Both, the frequency of animals with errors and the number of errors per animal are higher in L4s compared to L1 larvae (Main Figures 3,  and Supplementary Figure 4 and 7, revised version). It is very likely that the errors in VD neurons, which are born in the late L1 stage, are responsible for the higher frequency of defects observed in L4 animals. 

As the reviewer noted, GABAergic DD neurons, which are born embryonically, do not complete their development during the embryonic stages. Some defects in DD neurons may arise during the postembryonic period. Following the reviewer's suggestion, we analyzed L1 larvae at different times before the appearance of VDs (1 hour post-hatching and 6 hours post-hatching). We did not observe an increase in error prevalence, suggesting that DD defects in daf-18 mutants are mostly embryonic (Supplementary Fig 4B, Revised Version). 

Our findings suggest that βHB's enhancement is not due to preventive effects in DDs, as defects persist in newly hatched larvae regardless of βHB presence (Supplementary Figure 7, revised version), and postembryonic DD growth does not introduce new errors (Supplementary Figure 4, revised version). This lack of preventive effect could be due to βHB's limited penetration into the embryonic environment. Unlike early L1s, significant improvement occurs in L4s upon βHB early exposure (Supplementary Figure 7, revised version). This could be explained by a reversing effect on malformed DD neurons and/or a protective influence on VD neuron development. While we cannot rule out the first option, even if all errors in DDs in L1 were repaired (which is very unlikely), it wouldn't explain the level of improvement in L4 (Supplementary Figure 7, revised version). Therefore, we speculate that VDs may be targeted by βHB. The notion that exposure to βHB during early L1 can ameliorate defects in neurons primarily emerging in late L1s (VDs) is intriguing. We may hypothesize that residual βHB or a metabolite from prior exposure could forestall these defects in VD neurons. Notably, βHB has demonstrated a capacity for long-lasting effects through epigenetic modifications (Reviewed in He et al, 2023, https://doi.org/10.1016%2Fj.heliyon.2023.e21098). More work is needed to elucidate the underlying fundamental mechanisms regarding the ameliorating effects of βHB supplementation. We have now discussed these possibilities under discussion (Page 17, lines 369-383, revised version).

We agree with the reviewer that the term "reversal" is not accurate, and we have avoided using this terminology throughout the text. Furthermore, in the title, we have decided to change the word "rescue" to "ameliorate," as our experiments support the latter term but not the former. Additionally, the reviewer is correct that folic acid administration to pregnant women is already a metabolic intervention to prevent neural tube defects. In light of this, we have avoided claiming this as proof of concept in the revised manuscript 

(3) The data presented do not warrant the dismissal of DD remodeling as a contributing factor to the daf-18/PTEN defects.

Inhibitory GABAergic DD neurons are quite unique cells. They are well-known for their very particular property of remodeling their synaptic polarity (DD neurons switch the nature of their pre- and postsynaptic targets without changing their wiring). This process is called DD remodeling. It starts in the second half of the L1 stage and finishes during the L2 stage. Unfortunately, the fact that the authors find a specific defect in early GABAergic neurons (which are very likely these unique DD neurons) is not explored in sufficient detail and depth. The facts that these neurons are not fully developed at L1, that they still undergo limited neurite growth, and that they are poised for striking synaptic plasticity in a few hours set them apart from the other explored neurons, such as early cholinergic neurons, which show a more stable dynamics and connectivity at L1 (see Mulcahy et al., Curr Biol 2022).

The authors use their observation that daf-18/PTEN mutants present morphological defects in GABAergic neurons prior to DD remodeling to dismiss the possibility that the DAF-18/PTEN-dependent effects are "not a consequence of deficient rearrangement during the early larval stages". However, DD remodeling is just another cell-fate-determined process and as such, its timing, for instance, can be affected by mutations in genes that affect cell fates and developmental decisions, such as daf-18 and daf-16, which affect developmental fates such as those related with the dauer fate. Specifically, the authors do not exclude the possibility that the defects observed in the absence of either gene could be explained by precocious DD remodeling. Precocious DD remodeling can occur when certain pathways, such as the lin-14 heterochronic pathway, are affected. Interestingly, lin-14 has been linked with daf16/FOXO in at least two ways: during lifespan determination (Boehm and Slack, Science 2005) and in the

L1/L2 stages via the direct negative regulation of an insulin-like peptide gene ins-33 (Hristova et al., Mol Cell Bio 2005). It is likely that the prevention of DD dysfunction requires keeping insulin signaling in check (downregulated) in DD neurons in early larval stages, which seems to coincide with the critical timing and function of daf-18/PTEN. Hence, it will be interesting to test the involvement of these genes in the daf-18/daf-16 effects observed by the authors.

This is another interesting point raised by the reviewer. We have demonstrated that defects manifest in early L1 (30 min-1 hour post-hatching) which corresponds to a pre-remodeling time in wild-type worms.

We acknowledge the possibility of early remodeling in specific mutants as pointed out by the reviewer.

However, the following points suggest that the effects of these mutations may extend beyond the particularity of DD remodeling: i) Our experiments also show defects in VD neurons in daf-18 mutants (Supplementary Figure 3, revised version), as discussed in our previous response. These neurons do not undergo significant remodeling during their development. ii) DAF-18 and DAF-16 deficiencies produce neurodevelopmental alteration on other Non-Remodeling Neurons: Severe neurite defects in neurons that are nearly fully formed at larval hatching, such as AIY in daf-18 and daf-16 mutants, have been previously reported (Christensen et al., 2011). Additionally, the migration of another neuron, HSN, is severely affected in these mutants (Kennedy et al., 2013). iii) To the best of our knowledge, DD remodeling only alters synaptic polarity without forming new commissures or significant altering the trajectory of the formed ones. Thus, it is unlikely (though not impossible) for remodeling defects to cause the observed commissural branching and handedness abnormalities in DD neurons. Therefore, we think that the impact of daf-18 mutations on GABAergic neurons is not primarily linked to DD remodeling but extends to various neuron types. It is intriguing and requires further exploration in the future, the apparent resilience of cholinergic motor neurons to these mutations. This resilience is not limited to daf18/PTEN animals since mutants in certain genes expressed in both neuron types (such as neuronal integrin ina-1 or eel-1, the C. elegans ortholog of HUWE1) alter the function or morphology of GABAergic neurons but not cholinergic motor neurons (Kowalski, J. R. et al. Mol Cell Neurosci 2014; Oliver, D. et al. J Dev Biol (2019); Opperman, K. J. et al. Cell Rep 2017). These points are discussed in the manuscript (Discussion, page 15, lines 311-322, revised version) and reveal the existence of compensatory or redundant mechanisms in these excitatory neurons, rendering them much more resistant to both morphological and functional abnormalities.

Discussion on the impact of the work on the field and beyond:

The authors significantly advance the field by bringing insight into how DAF-18/PTEN affects neurodevelopment, but fall short of understanding the mechanism of selectivity towards GABAergic neurons, and most importantly, of properly contextualizing their findings within the state-of-the-art C. elegans biology.

For instance, the authors do not pinpoint which type of GABAergic neuron is affected, despite the fact that there are two very well-described populations of ventral nerve cord inhibitory GABAergic neurons with clear temporal and cell fate differences: the embryonically-born DD neurons and the postembryonically-born VD neurons. The time point of the critical period apparently defined by the authors (pending clarifications of methods, presentation of all data, and confirmation of inconsistencies between the text and figures in the submitted manuscript) could suggest that DAF-18/PTEN is required in either or both populations, which would have important and different implications. An effect on DD neurons seems more likely because an image is presented (Figure 2D) of a defect in an L1 daf-18/PTEN mutant larva with 6 neurons (which means the larva was processed at a time when VD neurons were not yet born or expressing pUnc-47, so supposedly it is an image of a larva in the first half of the L1 stage (0-~7h?)). DD neurons are also likely the critical cells here because the neurodevelopment errors are partially suppressed when the ketogenic diet is provided at an "early" L1 stage, but not later (e.g., from L2-L3, according to the text, L2-L4 according to the figure? ).

Thank you for this insightful input. As previously mentioned, we conducted experiments in this revision to clarify the specificity of GABAergic errors in daf-18/PTEN mutants, in particular, whether they affect DDs, VDs, or both. Our results suggest that commissural defects are not limited to DD neurons but also occur in VD neurons (Supplementary Figure 3). Regarding the effect of βHB, our findings suggest that VD neurons are targets of βHB action. As mentioned in the previous response and the discussion section (Page 17, lines 369-383, revised version), we might speculate that lingering βHB or a metabolite from prior exposure could mitigate these defects in VD neurons that are born in Late L1s-Early L2s. Additionally, βHB has been noted for its capacity to induce long-term epigenetic changes. Therefore, it could act on precursor cells of VD neurons, with the resulting changes manifesting during VD development independently of whether exposure has ceased. All these possibilities are now discussed in the manuscript.

Acknowledging that our work raises several questions that we aim to address in the future, we believe our manuscript provides valuable information regarding how the PI3K pathway modulates neuronal development and how dietary interventions can influence this process.

This study brings important contributions to the understanding of GABAergic neuron development in C. elegans, but unfortunately, it is justified and contextualized mostly in distantly-related fields - where the study has a dubious impact at this stage rather than in the central field of the work (post-embryonic development of C. elegans inhibitory circuits) where the study has stronger impact. This study is fundamentally about a cell fate determination event that occurs in a nutritionally-sensitive

developmental stage (post-embryonic L1 larval stage) yet the introduction and discussion are focused on more distantly related problems such as excitatory/inhibitory (E/I) balance, pathophysiology of human diseases, and treatments for them. Whereas speculation is warranted in the discussion, the reduced indepth consideration of the known biology of these neurons and organisms weakens the impact of the study as redacted. For instance, the critical role of DAF-18/PTEN seems to occur at the early L1 larval stage, a stage that is particularly sensitive to nutritional conditions. The developmental progression of L1 larvae is well-known to be sensitive to nutrition - eg, L1 larvae arrest development in the absence of food, something that is explored in nematode labs to synchronize animals at the L1 stage by allowing embryos to hatch into starvation conditions (water). Development resumes when they are exposed to food. Hence, the extensive postembryonic developmental trajectory that GABAergic neurons need to complete is expected to be highly susceptible to nutrition. Is it? The sensitivity towards the ketogenic diet intervention seems to favor this. In this sense, the attribution of the findings to issues with the nutrition-sensitive insulin-like signaling pathway seems quite plausible, yet this possibility seems insufficiently considered and discussed.

We greatly appreciate the reviewer's emphasis on the sensitivity of the L1 stage to nutritional status. As the reviewer points out, C. elegans adjusts its development based on food availability, potentially arresting development in L1 in the absence of food. It is therefore reasonable that both the completion of DD neuron trajectories and the initial development steps of VD neurons are particularly sensitive to dietary modulation of the insulin pathway, in which both DAF-18 and DAF-16 play roles. This important point has also been included in the discussion (Page 18, lines 384-407, revised version).

Finally, the fact that imbalances in excitatory/inhibitory (E/I) inputs are linked to Autism Spectrum Disorders (ASD) is used to justify the relevance of the study and its findings. Maybe at this stage, the speculation would be more appropriate if restricted to the discussion. In order to be relevant to ASD, for instance, the selectivity of PTEN towards inhibitory neurons should occur in humans too. However, at present, the E/I balance alteration caused by the absence of daf-18/PTEN in C. elegans could simply be a coincidence due to the uniqueness of the post-embryonic developmental program of GABAergic neurons in C. elegans. To be relevant, human GABAergic neurons should also pass through a unique developmental stage that is critically susceptible to the PI3K-PDK1-AKT pathway in order for DAF18/PTEN to have any role in determining their function. Is this the case? Hence, even in the discussion, where the authors state that "this study provides universally relevant information on.... the mechanisms underlying the positive effects of ketogenic diets on neuronal disorders characterized by GABA dysfunction and altered E/I ratios", this claim seems unsubstantiated as written particularly without acknowledging/mentioning the criteria that would have to be fulfilled and demonstrated for this claim to be true.

Our results suggest that defects in GABAergic neurons are not limited to DDs, which, as the reviewer rightly notes, are quite unique in their post-embryonic development primarily due to the synaptic remodeling process they undergo. These defects also extend to VD neurons, which do not exhibit significant developmental peculiarities once they are born. Therefore, we think that the defects are not specific to the developmental program of DD neurons but are more related to all GABAergic motoneurons. Additionally, the observation of defects in non-GABAergic neurons in C. elegans daf-18 mutants supports the hypothesis that the role of daf-18 is not limited to DD neurons (Christensen et al., 2011; Kennedy et al., 2013).

In mammals, Pten conditional knockout (cKO) animals have been extensively studied for synaptic connectivity and plasticity, revealing an imbalance between synaptic excitation and inhibition (E/I balance) (Reviewed in Rademacher and Eickholt, 2019, Cold Spring Harbor Perspect Med, https://doi.org/10.1101%2Fcshperspect.a036780). This imbalance is now widely accepted as a key pathological mechanism linked to the development of ASD-related behavior (Lee et al, 2017; Biological Psychiatry, https://doi.org/10.1016/j.biopsych.2016.05.011) . The importance of PTEN in the development of GABAergic neurons in mammals is well-documented. For instance, embryonic PTEN deletion from inhibitory neurons impacts the establishment of appropriate numbers of parvalbumin and somatostatin-expressing interneurons, indicating a central role for PTEN in inhibitory cell development (Vogt et al, 2015, Cell Rep, https://doi.org/10.1016%2Fj.celrep.2015.04.019). Additionally, conditional PTEN knockout in GABAergic neurons is sufficient to generate mice with seizures and autism-related behavioral phenotypes (Shin et al, 2021, Molecular Brain, https://doi.org/10.1186%2Fs13041-02100731-8). Moreover, while mice in which PV GABAergic neurons lacked both copies of Pten experienced seizures and died, heterozygous animals (PV-Pten+/−) showed impaired formation of perisomatic inhibition (Baohan et al, 2016, Nature Comm, OI: 10.1038/ncomms12829). Therefore, there is substantial evidence in mammals linking PTEN mutations to neurodevelopmental disorders in general and affecting GABAergic neurons in particular. Hence, we believe that the role of daf-18/PTEN in GABAergic development could be a more widespread phenomenon across the animal kingdom rather than a specific process unique to C. elegans.

Beyond the points discussed, we have addressed the reviewer's comment regarding the last sentence of the abstract. We have revised it to more cautiously frame the relationship between our findings, ASD, and mammalian neurodevelopmental disorders.

Reviewer #2 (Public Review):

Summary:

Disruption of the excitatory/inhibitory (E/I) balance has been reported in Autism Spectrum Disorders

(ASD), with which PTEN mutations have been associated. Giunti et al choose to explore the impact of PTEN mutations on the balance between E/I signaling using as a platform the C. elegans neuromuscular system where both cholinergic (E) and GABAergic (I) motor neurons regulate muscle contraction and relaxation. Mutations in daf-18/PTEN specifically affect morphologically and functionally the GABAergic (I) system, while leaving the cholinergic (E) system unaffected. The study further reveals that the observed defects in the GABAergic system in daf-18/PTEN mutants are attributed to reduced activity of DAF-16/FOXO during development.

Moreover, ketogenic diets (KGDs), known for their effectiveness in disorders associated with E/I imbalances such as epilepsy and ASD, are found to induce DAF-16/FOXO during early development. Supplementation with β-hydroxybutyrate in the nematode at early developmental stages proves to be both necessary and sufficient to correct the effects on GABAergic signaling in daf-18/PTEN mutants.

Strengths:

The authors combined pharmacological, behavioral, and optogenetic experiments to show the

GABAergic signaling impairment at the C. elegans neuromuscular junction in DAF-18/PTEN and DAF-

16/FOXO mutants. Moreover, by studying the neuron morphology, they point towards

neurodevelopmental defects in the GABAergic motoneurons involved in locomotion. Using the same set of experiments, they demonstrate that a ketogenic diet can rescue the inhibitory defect in the daf18/PTEN mutant at an early stage.

Weaknesses:

The morphological experiments hint towards a pre-synaptic defect to explain the GABAergic signaling impairment, but it would have also been interesting to check the post-synaptic part of the inhibitory neuromuscular junctions such as the GABA receptor clusters to assess if the impairment is only presynaptic or both post and presynaptic.

Moreover, all observations done at the L4 stage and /or adult stage don't discriminate between the different GABAergic neurons of the ventral nerve cord, ie the DDs which are born embryonically and undergo remodeling at the late L1 stage, and VDs which are born post-embryonically at the end of the L1 stage. Those additional elements would provide information on the mechanism of action of the FOXO pathway and the ketone bodies.

Thank you for your insightful suggestions. 

This is an initial study that serves as a cornerstone, demonstrating the sensitivity of GABAergic neuron development to alterations in the PI3K pathway and how these alterations can be mitigated by a dietary intervention with a ketone body. While we have determined that the transcription factor DAF-16/FOXO is essential in the neurodevelopmental process and is the target of ketone bodies to alleviate defects, there are still underlying mechanisms to be elucidated. This is only the first step that opens many avenues for further investigation, including the study of post-synaptic partners.

While our current study primarily focuses on neuronal alterations without delving into potential postsynaptic effects, we do plan to investigate this aspect in future research. This includes examining GABAergic receptors as well as cholinergic receptors, as exacerbation of cholinergic signaling cannot be ruled out. To conduct a comprehensive study of post-synaptic structure and functionality, we would need strains with fluorescent markers for both pre- and post-synaptic components (such as rab-3, unc-49, unc29, acr-16 fusion to GFP or mCherry). Unfortunately, most of these strains are not currently available in our laboratory. Unlike the US or Europe, acquiring these strains from the C. elegans CGC repository in Argentina is challenging due to common customs delays, which require significant time and resources to navigate. Discussions at the Latin American C. elegans conference with CGC administrators, such as Ann Rougvie, have been initiated to address this issue, but a solution has not been reached yet.  Additionally, to analyze post-synaptic functionality in-depth, studying the response to perfusion with various agonists using electrophysiology would be beneficial. We are in the process of acquiring the capability to conduct electrophysiology experiments in our laboratory, but progress is slow due to limited funding.

While we believe these experiments are very informative, they will require a considerable amount of time due to our current circumstances. We consider them non-essential to the primary message of the paper, which focuses on neuronal developmental defects leading to functional alterations in daf-18/PTEN mutants and the novel finding that these can be mitigated by supplementing food with hydroxybutyrate. We will study the structure and functionality of the post-synapse in our future projects and also plan to extend this investigation to mutants with deficiencies in genes closely related to neurodevelopmental defects, such as neuroligin, neurexin, or shank-3, which have been implicated in synaptic architecture.

We also agree that discriminating between DD and VD neurons provides significant insights into the neurodevelopmental phenomena dependent on the FOXO pathway and the action of βHB. In this revised version, we present evidence that not only DD neurons are affected but also VD neurons (see

Supplementary Figure 3, revised version). This allows us to suggest that daf-18 affects the development of GABAergic neurons regardless of whether they are born embryonically (DDs) or post-embryonically (VDs) (see also our response to the previous reviewer). We hope to distinguish the defects observed in each type of neuron in future studies. For this, we would need to use strains specifically marked in one neuronal type or another, which, for the same reasons mentioned earlier, would take a considerable amount of time under current conditions. 

Conclusion:

Giunti et al provide fundamental insights into the connection between PTEN mutations and neurodevelopmental defects through DAF-16/FOXO and shed light on the mechanisms through which ketogenic diets positively impact neuronal disorders characterized by E/I imbalances.  

Reviewer #3 (Public Review):

Summary:

This is a conceptually appealing study by Giunti et al in which the authors identify a role for PTEN/daf-18 and daf-16/FOXO in the development of inhibitory GABA neurons, and then demonstrate that a diet rich in ketone body β-hydroxybutyrate partially suppresses the PTEN mutant phenotypes. The authors use three assays to assess their phenotypes: (1) pharmacological assays (with levamisole and aldicarb); (2) locomotory assays and (3) cell morphological assays. These assays are carefully performed and the article is clearly written. While neurodevelopmental phenotypes had been previously demonstrated for PTEN/daf-18 and daf-16/FOXO (in other neurons), and while KB β-hydroxybutyrate had been previously shown to increase daf-16/FOXO activity (in the context of aging), this study is significant because it demonstrates the importance of KB β-hydroxybutyrate and DAF-16 in the context of neurodevelopment. Conceptually, and to my knowledge, this is the first evidence I have seen of a rescue of a developmental defect with dietary metabolic intervention, linking, in an elegant way, the underpinning genetic mechanisms with novel metabolic pathways that could be used to circumvent the defects.

Strengths:

What their data clearly demonstrate, is conceptually appealing, and in my opinion, the biggest contribution of the study is the ability of reverting a neurodevelopmental defect with a dietary intervention that acts upstream or in parallel to DAF-16/FOXO.

Weaknesses:

The model shows AKT-1 as an inhibitor of DAF-16, yet their studies show no differences from wildtype in akt-1 and akt-2 mutants. AKT is not a major protein studied in this paper, and it can be removed from the model to avoid confusion, or the result can be discussed in the context of the model to clarify interpretation.

Thank you very much for the suggestion. We agree with the reviewer's appreciation that the study of AKT's action itself is too limited in this study to draw conclusions that would allow its inclusion in the proposed model. Therefore, following the reviewer's suggestion, we have removed this protein from our model

When testing additional genes in the DAF-18/FOXO pathway, there were no significant differences from wild-type in most cases. This should be discussed. Could there be an alternate pathway via DAF-18/DAF16, excluding the PI3K pathway or are there variations in activity of PI3K genes during a ketogenic diet that are hard to detect with current assays?

Thank you for bringing up this point. Our pharmacological experiments indeed demonstrate that all mutants associated with an exacerbation of the PI3K pathway, which typically inhibits nuclear translocation and activity of the transcription factor DAF-16, lead to imbalances in E/I

(excitation/inhibition) that manifest as hypersensitivity to cholinergic drugs. This includes the gain of function of pdk-1 and the loss of function of daf-18 and daf-16 itself. In our subsequent experiments, we demonstrate that this exacerbation of the PI3K pathway leads to errors in the neurodevelopment of GABAergic neurons, which explains the hypersensitivity to aldicarb and levamisole.

As the reviewer remarks, it is intriguing why mutants inhibiting this pathway do not show differences in their sensitivity to cholinergic drugs compared to wild-type animals. We can speculate, for instance, that during neurodevelopment, there is a critical period where the PI3K pathway must remain with very low activity (or even deactivated) for proper development of GABAergic neurons. This could explain why there are no differences in sensitivity to cholinergic drugs between mutants that inhibit the PI3K pathway and the wild type. The PI3K pathway depends on insulin-like signals, which are in turn positively modulated by molecules associated with the presence of food. Interestingly, larval stage 1 is particularly sensitive to nutritional status, being able to completely arrest development in the absence of food. Therefore, dietary intervention with BHB may generate a signal of dietary restriction (as seen in mammals) and, as a consequence of this dietary restriction, the PI3K pathway is inhibited, resulting in increased DAF-16 activity. This could restore the proper neurodevelopment of GABAergic neurons. However, this is mere speculation, and further deeper experiments (than the pharmacology ones we performed here) with mutants in different genes within the PI3K pathway may shed light on this point.

Following the reviewer's suggestion, this point has been discussed in the revised version of the manuscript. (Discussion Page 18, Lines 384-407).

The consequence of SOD-3 expression in the broader context of GABA neurons was not discussed. SOD3 was also measured in the pharynx but measuring it in neurons would bolster the claims.

SOD-3 is a known target of DAF-16. Previous studies have shown that βHB induces SOD-3 expression through the induction of DAF-16 (Edwards et al, 2014, Aging,

https://doi.org/10.18632%2Faging.100683). The highest levels of SOD-3 expression are typically observed in the pharynx or intestine (DeRosa et al, 2019 https://doi.org/10.1038/s41586-019-1524-5;  Zheng et al., 2021, PNAS, https://doi.org/10.1073/pnas.2021063118), and it is often used as a measure of general upregulation of DAF-16. Therefore, we used this parameter as a measure of βHB upregulating systemic DAF-16 activity.  While we agree with the reviewer that observing variations in SOD-3 expression in neurons would further support our conclusions, unfortunately, we did not detect measurable signals of SOD-3 in motor neurons in either the control condition or the daf-18 background even upon stress or BHB-exposure. This may be because SOD-3 is a minor target of DAF-16 in these neurons, or its modulation may not correspond to the timing of fluorescence measurements (L4-adults).

Despite this, our genetic experiments and neuron-specific rescue experiments lead us to conclude that DAF-16 must act autonomously in GABAergic neurons to ensure proper neurodevelopment.

If they want to include AKT-1, seeing its effect on SOD-3 expression could be meaningful to the model.

Thank you for this suggestion. We believe that even measuring SOD-3 levels in akt mutant backgrounds would still provide limited information to give it a predominant value in our work. Additionally, to have a complete understanding of the total role of AKT, it would be necessary to measure it in a double mutant background of akt-1; akt-2, and these double mutants generate 100 % dauers even at 15C (Oh et al., PNAS 2005, https://doi.org/10.1073/pnas.0500749102; Quevedo et al., Current Biology 2007, http://dx.doi.org/10.1016/j.cub.2006.12.038; Gatzi et al., PLOS ONE 2014,

https://doi.org/10.1371/journal.pone.0107671), greatly complicating the execution of these experiments. Therefore, following the first advice of this reviewer, we have decided to modify our model by excluding AKT.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

⁃ Please include earlier in the main text the rationale for using unc-25 as a control/reference already when mentioning Figure 1A.

Thank you for pointing out the need to reference this control earlier. We have included the following paragraph in the description of Figure 1 (Page 5, line 71, revised version):

“Hypersensitivity to cholinergic drugs is typical of animals with an increased E/I ratio in the neuromuscular system, such as mutants in unc-25 (the C. elegans orthologue for glutamic acid decarboxylase, an essential enzyme for synthesizing GABA). While daf-18/PTEN mutants become paralyzed earlier than wild-type animals, their hypersensitivity to cholinergic drugs is not as severe as that observed in animals completely deficient in GABA synthesis, such unc-25 null mutants (Figures 1B and 1C) indicating a less pronounced imbalance between excitatory and inhibitory signals.”

⁃ Please discuss the greater sensitivity of pdk-1(gf) animals to levamisole than to aldicarb.

Thank you for bringing up this subtle point.  We understand that the reviewer is referring to the paralysis curve in response to aldicarb in pdk-1(gf), which is closer to unc-25 than the curve for levamisole (in both cases, they are more sensitive than the wild type). Therefore, pdk-1(gf) animals seem to be more sensitive to aldicarb than to levamisole. These results are now shown in Figure 1D (revised version).

The PI3K pathway does not only act in neurons but also in muscles. Gain of function in pdk-1 has been shown to modulate muscle protein degradation (Szewczyk et al, EMBO Journal, 2008. https://doi.org/10.1038/sj.emboj.7601540). In contrast,  no effect on protein degradation has been reported for null mutants in this gene. Several studies have demonstrated that protein degradation levels can differentially affect receptor subunits, particularly acetylcholine receptors (Reviewed in Crespi et al, Br J Pharmacol, 2018). C. elegans is characterized by a wide repertoire of AChR subunits, and there are at least two subtypes of ACh receptors in muscles (one multimeric sensitive to levamisole and one homomeric (ACR-16) insensitive to levamisole) (Richmond et al, 1999 Nature Neuroscience http://dx.doi.org/10.1038/12160; Touroutine D, JBC 2005 https://doi.org/10.1074/jbc.M502818200).

Interestingly, acr-16 null mutants are hypersensitive to aldicarb (Zeng et al, JCB, 2023, https://doi.org/10.1083/jcb.202301117) while the electrophysiological response to levamisole in this mutant remains similar to that of wild-type (Tourorutine et al, 2005). Therefore, it may be that the gain of function in pdk-1 induces a change in the expression of AChR subtypes in muscle that differentially affect sensitivity to levamisole and ACh. This is purely speculative, and there may be many other explanations. While it would be interesting to explore this difference further, it goes far beyond the scope of this study. The cholinergic drug sensitivity assay is purely exploratory and allowed us to delve into the GABAergic and cholinergic signals in daf-18 mutants. In this sense, the hypersensitivity of pdk-1(gf) to both drugs supports the idea that an increase in PI3K signaling leads to an increased E/I ratio.

⁃ Please explain the rationale to perform akt-1 and akt-2 assays separated. Why not test doublemutants? Has their lack of redundancy been determined?.  

Our pharmacological assays are conducted at the L4 larval stage, making it impossible to analyze the potential redundancy of akt-1 and akt-2 in sensitivity to levamisole and aldicarb. This impossibility arises because the akt-1;akt-2 double mutant exhibits nearly 100% arrest as dauer even at 15°C, as reported in several prior studies (Oh et al., PNAS 2005, https://doi.org/10.1073/pnas.0500749102; Quevedo et al., Current Biology 2007, http://dx.doi.org/10.1016/j.cub.2006.12.038; Gatzi et al., PLOS ONE 2014, https://doi.org/10.1371/journal.pone.0107671). While the increased dauer arrest in the double mutant compared to the single mutants might suggest redundant functions in dauer entry, there are also reports indicating the absence of redundancy in other processes, such as vulval development (Nakdimon et al., PLOS Genetics 2012, https://doi.org/10.1371%2Fjournal.pgen.1002881).

The complete Dauer arrest likely underlies why other studies focusing on the role of the PI3K pathway in neurodevelopment utilize both mutants separately (Christensen et al, Development 2011,

https://doi.org/10.1242/dev.069062). While determining the potential redundancy of these genes is not feasible for this assay, we utilized various mutants of the pathway (age-1, pdk-1, daf-18, daf-16 and daf16;daf-18 in addition to the akt-s) that support the conclusion, which is that exacerbating the PI3K pathway activity makes animals hypersensitive to cholinergic drugs.

In response to the reviewer's concern, we have added a sentence in the text explaining the impossibility of performing the assay in the akt-1;akt-2 double mutant (Page 6, lines90-92) 

Figure 1C and D (This applies to all similarly presented bar figures). Please show data points and dispersion (preferably data, median+- 25-75% or average+-SD). 

Thank you. Done

⁃ Line 112 -maybe "and resumes"? 

Thank you. Done (Line 126, revised version)

⁃ Figure 1E and F. Please present mean +-SD (not SEM) of fluctuations. Please change slightly the tones so that the dispersion is easier to distinguish on the "blue light on" box.

Thank you for the suggestion. We have adjusted the tones as recommended to enhance the visualization of the "blue light on" box. For visualization purposes, we present the shading of the standard error of the mean (SEM), as is usual in these types of optogenetic experiments where traces of animal length variations are measured (Liewald et al, Nature Methods, 2008, doi: 10.1038/nmeth.1252; Schulstheis et al, J. Neurophysiology, 2011, doi: 10.1152/jn.00578.2010; Koopman et al, BMC Biology 2021, https://doi.org/10.1186/s12915-021-01085-2; Seidhenthal et al, Micro Publication Biology, 2022, https://doi.org/10.17912%2Fmicropub.biology.000607 ).

For the revised version, we have also included bar graphs for each optogenetic experiment, representing the mean of the length average of each worm measured from the first second after the blue light was turned on until the second before the light was turned off (in the graph, this corresponds to the period between seconds 6 and 9 of the traces). These graphs include the standard deviation and the corresponding significance levels. All of this has been included in the new legend (Figure 2D, 2E, 4E-J).

⁃ Figure 1A&1B & Supplementary Figure 1D x Supplementary Figure 1E&1F. What is the difference between these experiments? Whereas the unc-25 mutants paralyze in the same amount of time, the WT animals paralyze ~1 h later in Supplementary Figure 1E-1F in response to either drug. Please revise experimental conditions to see if anything can be learned eg, maybe this is a nutritional response from experiments done at different timepoints? Maybe different food recipes affected sensitivity to paralysis?

Thank you for pointing this out. While the experiments with daf-18 (in both alleles) and daf-16 were conducted at the beginning of this project (2019-2020), the assays with the other mutants in the PI3K and mTOR pathways were performed years later. Changes in the reagents used (agar, peptone, cholesterol, etc.) to grow the worms have occurred, potentially altering the animals' response directly or through the nutritional quality of the bacteria they grow on. In addition, the difference may be attributed to the fact that experiments at the project's outset were conducted by one author, while more recent experiments were carried out by another. The goal is to quantify paralysis in non-responsive worms after touch stimulation. The force of this probing or the thickness of the hair used for touching can be slightly operator-dependent and can lead to variable responses. In addition, always the presence of wild-type and unc-25 strain is included as internal control in every experiment. Nevertheless, despite this userdependent variation, the experiments were always conducted blindly (except for unc-25, whose uncoordinated phenotype is easily identifiable), thus we trust in the outcomes.

⁃ Supplementary Figure 1G - Length and Width appear to be switched in both left and right panels - please revise and include a description of N and of statistics depicted. 

Unfortunately, we don't see the switching error that the reviewer mentioned. In the left panel, we demonstrate that optogenetic activation of GABAergic neurons leads to an increase in length without modifying the width of the animal. Therefore, we conclude that the increase in area, as observed in our Fiji macro for optogenetic response analysis, is due to an increase in the animal's length. In the cholinergic activation shown in the right panel, the animal shortens (decreasing length) without modifying the width, resulting in the reduction of the total body area. 

We have included information about N (sample size) and the statistical test used in the legends as suggested. These graphs are now shown as Figures 2F and G, revised version.

⁃ Supplementary Figure 1G legend lines 779-780. Please describe the post-hoc test applied following ANOVA to obtain the denoted p values. This applies to all datasets where ANOVA or Krusal-Wallis tests were applied.

Following reviewer´s suggestion, all the post-hoc tests applied after ANOVA or Kruskal-Wallis analysis were included in the legend of each figure and Materials and Methods (statistical analysis section).

⁃ Line 174 maybe "arises *from* the hyperactivation" instead of *for*?.

Corrected. Thank you. Line 190, revised version.

⁃ Supplementary Figure 4. On line 816 it says n=40-90, but please check the n of the daf-18, daf-16 samples, which seem to have less than 40 animals.

We understand that the reviewer is referring to Supplementary Figure 3 from the original version (now Supplementary Figure 5 in the revised version). We have now included the number of observations below each data point cloud to clearly indicate the sample size for each condition

⁃ Supplementary Figure 4 - please state what are the bars on the graphs. Please state which post-hoc test was performed after Kruskal-Wallis and present at least the p values obtained between treated controls and each genotype. Alternatively, present the whole truth table in supplementary daita.

We understand that the reviewer is referring to Supplementary Figure 3 from the original version (now Supplementary Figure 5 in the revised version). There was an error in the original legend (thank you for bringing this to our attention) since the statistics were not performed using Kruskall-Wallis in this case, but rather each treated condition was compared to its own untreated control using Mann-Whitney test. We have now added the p-values to the graph. All raw data for this figure, as well as for all other figures, are available in Open Science Framework (https://osf.io/mdpgc/?view_only=3edb6edf2298421e94982268d9802050).

⁃ Please cite the figure panels in order: eg, Figure 3E is mentioned in the text after panels Figure 3F-K.

Done. We have rearranged the figures to adapt them to the text order (Figure 4, revised version)

⁃ Figure 4 - line 610 please revise "(n=20-30 (n: 20-25 animals per genotype/trial)."

Thank you. Corrected.

⁃ Figure 4 - there appears to be an inconsistency in the figure with the text (lines 223-225). In figures it says E-L1, but in the text, it says "solely in L1". Does E-L1 include the whole L1 stage? If not- E-L1 can be interpreted only as during the embryonic stage, hence, no exposure to betaHB due to the impermeable chitin eggshell. Then there is L1-L2, which should cover the L1 stage and the L2 or something else. Please revise. The text mentions L2-L3 or L3-L4 and these categories are not in the figures. This clarification is key for the interpretation of the results. The precise developmental time of the exposures is not defined either in the methods or in the figures. Please provide precise times relative to hours and/or molts and revise the text/figure for consistency.

The reviewer is entirely correct in pointing out the lack of relevant data regarding the exposure time to βHB. We have now clarified the information For the revised version, we have adjusted the nomenclature of each exposure period to precisely reflect the developmental stages involved.

For the experiments involving continuous exposure to βHB throughout development, the NGM plate contained the ketone body. Therefore, the exposure encompassed, in principle, the ex-utero embryonic development period up to L4-Young adults (E-L4/YA, in Figure 5A) when the experiments were conducted. Since it could be a restriction to drug penetration through the chitin shell of the eggs (see Supplementary Figure 7), we can ensure βHB exposure from hatching.

In experiments involving exposure at different developmental stages as those depicted in Figure 4 of the original version, (now Figure 5), animals were transferred between plates with and without βHB as required. We exposed daf-18/PTEN mutant animals to βHB-supplemented diets for 18-hour periods at different developmental stages (Figure 5A). The earliest exposure occurred during the 18 hours following egg laying, covering ex-utero embryonic development and the first 8-9 hours of the L1 stage (This period is called E-L1, in figure 5 revised version). The second exposure period encompassed the latter part of the L1 stage, the entire L2 stage, and most of the L3 stage (L1-L3). The third exposure spanned the latter part of the L3 stage (~1-2 hours), the entire L4 stage, and the first 6-7 hours of the adult stage (L3-YA).

All this information has been conveniently included in Figure 5 (and its legend), text (Page 13, lines 259276), and Material and Methods of the revised manuscript.

⁃ Some methods are not sufficiently well described. Specifically, how the animals were exposed to treatments and how stages were obtained for each experiment. Was synchronization involved? If so, in which experiments and how exactly was it performed?

As mentioned in previous responses all the experiments were performed in age-synchronized animals. We include the following sentence in Materials and Methods (C. elegans culture and maintenance section): “All experiments were conducted on age-synchronized animals. This was achieved by placing gravid worms on NGM plates and removing them after two hours. The assays were performed on the animals hatched from the eggs laid in these two hours”.

Reviewer #2 (Recommendations For The Authors):

Major points

(1) To complete the study on the GABAergic signaling at the NMJs, it would be interesting to assess the status of the post-synaptic part of the synapse such as the GABAR clustering. It would also tell if the impairment is only presynaptic or both post and presynaptic.

Thank you for your insightful suggestion. We agree that exploring post-synaptic elements can shed light on whether the impairment is solely presynaptic or involves both pre and post-synaptic components.

While our current study primarily focuses on neuronal alterations without delving into potential postsynaptic effects, we do plan to investigate this aspect in the future. This includes not only examining GABAergic receptors but also exploring cholinergic receptors, as exacerbation of cholinergic signaling cannot be ruled out. To conduct a comprehensive study of post-synaptic structure and functionality, we would need strains with fluorescent markers for both pre and post-synaptic components (rab-3, unc-49, unc-29, acr-16 driving GFP or mCherry). However, most of these strains are not currently available in our laboratory. Unlike the US or Europe, acquiring these strains from the C. elegans CGC repository in Argentina is challenging due to common customs delays, requiring significant time and resources to navigate. Discussions at the Latin American C. elegans conference with CGC administrators, such as Ann Rougvie, have been initiated to address this issue, but a solution has not been reached yet. 

Additionally, to analyze post-synaptic functionality in-depth, studying the response to perfusion with various agonists using electrophysiology would be beneficial. We are in the process of acquiring the capability to conduct electrophysiology experiments in our laboratory, but progress is slow due to limited funding.

While we believe these experiments are very informative, they will require a considerable amount of time due to our current circumstances. We consider them non-essential to the primary message of the paper, which focuses on neuronal morphological defects leading to functional alterations in daf-18/PTEN mutants.

We will include these experiments in our future projects, also planning to extend this investigation to mutants with deficiencies in genes closely related to neurodevelopmental defects, such as neuroligin, neurexin, or shank-3, which have been implicated in synaptic architecture.

(2) The author always referred to unc-47 promoter or unc-17 promoter, never specifying where those promoters are driving the expression (and in the Materials & Methods, no information on the corresponding sequence). Depending on the promoters they may not only be expressed in the motoneurons involved in locomotion (VA, VB, DA, DB, VD, and DD), but they could also be expressed in other neurons which could be of importance for the conclusions of the optogenetic assays but also the daf-18 expression in GABAergic neurons.

We appreciate the reviewer's insight regarding the broader expression patterns of the unc-17 and unc-47 promoters in all cholinergic and GABAergic neurons, respectively. The strains expressing constructs with these promoters were obtained from the CGC or other labs and have been widely used in previous papers (Liewald et al, Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008); Byrne, A. B. et al. Neuron 81, 561-573, doi:10.1016/j.neuron.2013.11.019 (2014).

Regarding the optogenetic assays, the readout utilized (body length elongation or contraction) is primarily associated with the activity of cholinergic and GABAergic motor neurons and has been used in numerous studies to measure motor neuron functionality (Liewald et al, Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008);Hwang, H. et al. Sci Rep 6, 19900, doi:10.1038/srep19900 (2016); Schultheis et al,  . J Neurophysiol 106, 817-827, doi:10.1152/jn.00578.2010 (2011); Koopman, M., Janssen, L. & Nollen, E. A. BMC Biol 19, 170, doi:10.1186/s12915-021-01085-2 (2021);). It has previously been established that the shortening observed after optogenetic activation of the unc-17 promoter, while active in various interneurons, depends on the activity of cholinergic motor neurons (Liewald et al., Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008)). This was demonstrated by examining transgenic worms expressing ChR2-YFP from another cholinergic, motoneuronspecific but weaker promoter, Punc-4. They observed contraction and coiling upon illumination, albeit to a milder degree.

In terms of GABAergic neurons, only 3 do not directly synapse to body wall muscles (AVL, PDV, and RIS) and are primarily involved in defecation. Of the 23 GABAergic motor neurons, 19 are Dtype motoneurons, while the remaining 4 innervate head muscles (Pereira et al, eLife 2015, https://doi.org/10.7554/eLife.12432). It is therefore expected that while there may be some contribution from these latter neurons to the elongation after optogenetic activation in animals containing punc-47::ChR2, the main contribution should be from the D-type neurons. Additionally, while there may be some influence on D-type neuron development due to daf-18 rescue in neurons like RME, DVB or AVL, the most direct explanation for the rescue is that daf-18 acts autonomously in D-type cells.  Additionally, we have pharmacological and behavioral assays that support the findings of optogenetics and enable us to reach final conclusions.

(3) DD neurons are born during embryogenesis and newborn L1s have neurites even though less than at a later stage. If possible, it would be interesting to take a look at them to see if βHB has an effect or not. It will corroborate the hypothesis that βHB action is prevented by the impermeable eggshell on a system that can respond at a later stage. Moreover, using a specific DD, DA, and DB promoter, it would be possible to check if there is a difference in the morphological defects between embryonic and post-embryonic neurons.

This is a very interesting point raised by the reviewer. We conducted experiments to analyze the morphology of GABAergic neurons in animals exposed to βHB only during the ex-utero embryonic development (in their laid egg state). We observed that this incubation was not sufficient to rescue the defects in GABAergic neurons (Supplementary Figure 7, revised version). As reported by other authors and discussed in our paper, the chitinous eggshell might act as an impermeable barrier to most drugs. However, we cannot rule out that incubation during this period is necessary but not sufficient to mitigate the defects. We have included these experiments in Supplementary Figure 7 and in the text (Page 13, lines 272-276)

Additionally, we analyzed confocal images where, based on their position, we could identify and assess errors in DD (embryonic) and VD (Post-embryonic) neurons (Supplementary Figure 3, revised version). These experiments show that the effects are observed in both types of neurons, and we did not observe any differential alterations in neuronal morphology between the two types of neurons.

Minor points

(1)   Expression of daf-18/PTEN in muscle or hypodermis, could it ensure a proper development? It could give insights into the action mechanism of βHB.

The reviewer's observation is indeed very intriguing. Previous studies from the Grishok lab (Kennedy et al, 2013) have demonstrated that the expression of daf-18 or daf-16 in extraneuronal tissues, specifically in the hypodermis, can rescue migratory defects in the serotoninergic neuron HSN in daf-18 or daf-16 null mutants of C. elegans. Clearly, this could also be an option for rescuing the morphological and functional defects of GABAergic motoneurons.

However, the fact that the expression of daf-18 in GABAergic neurons rescues these defects strongly suggests an autonomous effect. In this regard, autonomous effects of DAF-18 or DAF-16 on neurodevelopmental defects have also been reported in interneurons in C. elegans (Christensen et al, 2011). This is included in the discussion (Page 15, lines 330-335)

(2) Re-organise the introduction. The paragraph on ketogenic diets (lines 35-38) is not logically linked.

Following reviewer´s suggestion we have reorganized the introduction and changed the order of explanation regarding the significance of ketogenic diets, linking it with their proven effectiveness in alleviating symptoms of diseases with E/I imbalance (Lines 23-60, revised version)

(3) Incorporate titles in the result section to guide the reader.

Done. Thank you

(4) Systematically add PTEN or FOXO when daf-18 or daf-16 are mentioned (for example lines 69, 84, 85).

Done. Thank you  

(5) Strain lists: lines 646 to 653: some information is missing on the different transgenes used in this study (integrated (Is) or extrachromosomal (Ex) with their numbers).

Thank you for bringing this to our attention. We have now included all the information regarding the different transgenes used in this study, including whether they are integrated (Is) or extrachromosomal (Ex) and their respective numbers. This information can be found in the revised version of the manuscript (Materials and Methods, C. elegans culture and maintenance section highlighted in yellow).

Reviewer #3 (Recommendations For The Authors):

In Figure 1, some experiments were done with the unc-25 control while others, such as the optogenetic experiments, were done without those controls.

Thank you for pointing this out. In the optogenetic experiments, we waited for the worm to move forward for 5 seconds at a sustained speed before exposing it to blue light to standardize the experiment, as the response can vary if the animal is in reverse, going forward, or stationary. Due to the severity of the uncoordinated movement in unc-25 mutants, achieving this forward movement before exposure is very difficult. Additionally, this lack of coordination prevents these animals from performing the escape response tests, as they barely move. Therefore, we limited the use of this severe GABAergic-deficient control to pharmacological or post-prodding shortening experiments.

eLife assessment

The authors are interested in the developmental origin of the neurons of the cerebellar nuclei. In this valuable study, they identify a population of neurons with a specific complement of markers that originate in a distinct location from where cerebellar nuclear precursor cells have been thought to originate that show distinct developmental properties. The discovery of a new germinal zone giving rise to a new population of neurons is an exciting finding, and it enriches our understanding of cerebellar development. The claims are reasonably well supported by the solid evidence because the authors use a wide range of technical approaches, including transgenic mice that allow them to disentangle the influence of distinct developmental organisers.

Reviewer #1 (Public Review):

Summary:

The authors are interested in the developmental origin of the neurons of the cerebellar nuclei. They identify a population of neurons with a specific complement of markers originating in a distinct location from where cerebellar nuclear precursor cells have been thought to originate that show distinct developmental properties. The cerebellar nuclei have been well studied in recent years to understand their development through an evolutionary lens, which supports the importance of this study. The discovery of a new germinal zone giving rise to a new population of CN neurons is an exciting finding, and it enriches our understanding of cerebellar development, which has previously been quite straightforward, where cerebellar inhibitory cells arise from the ventricular zone and the excitatory cells arise from the rhombic lip.

Strengths:

One of the strengths of the manuscript is that the authors use a wide range of technical approaches, including transgenic mice that allow them to disentangle the influence of distinct developmental organizers such at ATOH.<br /> Their finding of a novel germinal zone and a novel population of CN neurons is important for developmental neuroscientists, cerebellar neuroscientists.

Weaknesses:

One important question raised by this work is what do these newly identified cells eventually become in the adult cerebellum. Are they excitatory or inhibitory? Do they correspond to a novel cell type or perhaps one of the cell classes that have been recently identified in the cerebellum (e.g. Fujita et al., eLife, 2020)? Understanding this would significantly bolster the impact of this manuscript.

The major weakness of the manuscript is that it is written for a very specialized reader who has a strong background in cerebellar development, making it hard to read for eLife's general audience. It's challenging to follow the logic of some of the experiments as well as to contextualize these findings in the field of cerebellar development.

Reviewer #2 (Public Review):

Summary:

Canonically cerebellar neurons are derived from 2 primary germinal zones within the anterior hindbrain (dorsal rhombomere 1). This manuscript identifies an important, previously underappreciated origin for a subset of early cerebellar nuclei neurons - likely the mesencephalon. This is an exciting finding.

Strengths:

The authors have identified a novel early population of cerebellar neurons with likely novel origin in the midbrain. They have used multiple assays to support their conclusions, including immunohistochemistry and in situ analyses of a number of markers of this population which appear to stream from the midbrain into the dorsal anterior cerebellar anlage.

The inclusion of Otx2-GFP short term lineage analyses and analysis of Atoh1 -/- animals also provide considerable support for the midbrain origin of these neurons as streams of cells seem to emanate from the midbrain. However, without live imaging there remains the possibility that these streams of cells are not actually migrating and rather, gene expression is changing in static cells. Hence the authors have conducted midbrain diI labelling experiments of short term and long term cultured embryos showing di-labelled cells in the developing cerebellum. These studies confirm migration of cells from the midbrain into the early cerebellum.

The authors have appropriately responded to review issues, replacing panels in figures and updating legends and text. They have also appropriately noted the limitations of their work.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Recommendations For The Authors):

Additional experiments to characterize what this novel cell type becomes in older animals would be ideal to strengthen the manuscript, but the authors should at least address this in the Discussion.

The manuscript could be significantly improved if the authors included, for example, a timeline and/or cartoon contextualizing these cells relative to the formation of other CN neurons and their locations, perhaps as a summary figure at the end. Furthermore, the logic of each figure could be enhanced if the authors graphically show - again, perhaps with a schematic/cartoon - the question being tested for each figure. Furthermore, making the figure titles less descriptive and more explanatory would also help a reader follow the logic of the experiments.

These are indeed valid and important questions for our research, and understanding the distribution, fate, and connectivity of this new cell type in the cerebellar nuclei postnatally is a focus of ongoing investigation in our lab. To address these questions, we are currently utilizing SNCA-GFP mice, a project led by a PhD student in my lab. While this work will be the subject of a full-length research paper, we do add a sentence to the paper concerning a recent report about the presence of SNCA neurons in the adult CN.  We have included a reference to the postnatal expression of SNCA (“In adult mice, postnatal expression of SNCA has been reported in medial CN neurons. PMID: 32639229”.) on page 8 of our manuscript (highlighted in yellow). In addition, we have included a cartoon as a summary figure (Fig. 9) illustrating the origin of cerebellar nuclei from the caudal and rostral ends in both Atoh1+/+ and Atoh1-/- mice. Thank you once again, we have revised and improved the Fig. titles accordingly.

Reviewer #2 (Recommendations For The Authors):

Figure 3:

(1) If most SNCA+ cells are OTX2+ based on the IHCs, why are there so many SNCA+ Otx2- cells in the sort?

In each group, 350,000 cells were sorted. Due to the relatively small population size of this subset of cerebellar nuclei neurons, the sorting procedure could not perfectly mirror our immunohistochemistry results. In each group, 350,000 cells were sorted. Due to the relatively small population size of this subset of cerebellar nuclei neurons, the sorting procedure could not perfectly mirror our immunohistochemistry results. However, it is noteworthy that a portion of sorted cells expressed SNCA or Otx2 while a smaller population co-expressed both Otx2 and SNCA in the cerebellar primordium.

(2) Panel 3F: FACS graphs - the resolution of the figures is too poor on the PDF to read any of the text of these graphs. What are the axes?

We thank the reviewer for this comment. In the revision a high resolution of the FACS graph has replaced the lower quality graph in panel 3F. This clearly identifies the axes and text for this panel.

Figure 4:

(1) Arrowheads are making a subset of + cerebellar cells -Why? Not defined in the legend.

The population of cells indicated by the arrowheads are now defined in the legend. We have added the statement “Examples of Otx2 expressing cells are indicated by arrowheads in panels B, D, E, and F.”

(2) The orientation of panels E and F is unclear - please provide low mag panel insets.

An orientation marker (ie, (r-c and d-v; rostral caudal and dorsal ventral, respectively)) has been added to panel A, which applies to all panels, including panels E and F. Furthermore, the isthmus is noted with an “i” to provide further orientation.

(3) G - and throughout the paper - whisker plots (not simple box plots) are required. Also, it is unclear from the methods how Otx2+ cells were counted - how many embryos/age? The description of 10 sections across 3 slides is incomplete. Are these cells distributed equally across the mediolateral axis of the anlage? Where are comparable M/L sections compared across ages? Is the increase in # across time because these cells are proliferative or are more migrating into the anlage?

The plot has been replaced with whisker plots. A more detailed description of the Method used has been on page 15; “To assess the number of OTX2-positive cells, we conducted immunohistochemistry (IHC) labeling on slides containing serial sections from embryonic days 12, 13, 14, and 15 (n=3 at each timepoint). Under the microscope, we systematically counted OTX2-positive cells within the cerebellar primordium. This analysis encompassed a minimum of 10 sections, spread across at least 3 slides, ensuring comprehensive coverage of OTX2 expression along the mediolateral axis of the cerebellar primordium. For each slide, the counts of OTX2-positive cells from all sections were cumulatively calculated to determine the total number of positive cells per slide. Subsequently, statistical analysis was employed to compare the results obtained different developmental time points.”

Figure 5:

The use of confocal microscopy creates clear data re Otx2-GFP expression, but I cannot understand the origin of the panels. How do they relate to E/F and H/I? Different sections?

In Figure 5, panels A-D display Otx2 expressing cells in the cerebellar primordium of Otx2-GFP transgenic mice, whereas panels E-J depict RNAscope fluorescence in situ hybridization (FISH) for the Otx2 probe in wild type mice. These represent complementary approaches to map Otx2+ cells in the developing cerebellum. This is made clear in a revised legend in Fig 5.

Figure 6:

The justification for the in-culture experiments, particularly the long (4 and 21DIV) times is unclear and needs to be strengthened or the in vitro data should be removed.

Thank you for the respected reviewer’s comment. The E-H panels, show the co-expression of SNCA and p75NTR, highlight a significant role in the differentiation of specific neuronal populations during development. These findings validate our previous results (PMID: 31509576) and are consistent with the results of our current study. Therefore, we have chosen to keep these panels. However, in line with the suggestion from the reviewer, we have removed panels I-L from Fig. 6.

Figure 7:

SNCA expression in panels A and G is not specific nor is the Otx2 staining in panel B making the data in panels C and I uninterpretable and these panels need to be replaced. The Meis2 data however is much better and I agree this data shows that the dorsal RL-derived cells are deleted in Atoh1-/- while the SNCA+ cells remain. This is strong data supporting the dual origins of NTZ.

Thank you for the points, Panel A and G have been replaced with high-resolution images. In addition, panels A-C have been carefully cropped to enhance focus on the NTZ area, to improve the quality and visibility of panels.  To enhance clarity, we have included a summary fig. 9 for clarification.

Figure 8:

The diI experiments are a key addition to this paper and clearly show the direct movement of some cells from the mesencephalon into the developing cerebellum, but data presentation must be considerably strengthened.

(1) What is the inset in panel A? Low mag of embryo? Perhaps conversion of image to PDF degraded resolution - add a description in the legend. Arrowhead and arrow identities are reversed in the legend. The arrow points to the isthmus.

Thank you for the comment, for clarification we have included information in the Fig. legend (highlighted in yellow). In addition, the issues with the arrows have been addressed and corrected.

(2) Panels B and C are also shown in Supplementary Figure 2 with arrows indicating rostral and caudal movement - these arrows need to be added here. There is no need to replicate these same panels in the supplement.

Thanks, arrows have been added in panels B, C of Fig. 8.

(3) The text states that "almost all DiI cells migrated caudally into the cerebellum" and refers to Figure 8E and Suppementl 3 but there is no evidence/support shown for this, just a few + cells in 8E and some very difficult-to-see positive cells in sections in Supplement E-F. Given the importance of this data, I am surprised that the authors chose bright field/phase microscopy to show this. This section's data is not convincing data at all. I find it very difficult to see specific staining. These panels must be improved. This is key data for paper conclusions.

These are valid points, and we acknowledge that this experiment alone may not provide conclusive evidence regarding the subset of CN originating from mesencephalon. At this stage of the study, we do not claim definitively that the SNCA/OTX2/MEIS2 positive cells originate from the mesencephalon. As stated in our manuscript, "In conclusion, our study indicates that the SNCA+/ OTX2+/ MEIS2+/ p75NTR+/ LMX1A- rostroventral subset of CN neurons do not originate from the well-known distinct germinative zones of the cerebellar primordium. Instead, our findings suggest the existence of a previously unidentified extrinsic germinal zone, potentially the mesencephalon."  We have also discussed embryonic culture approaches in the manuscript, which could involve the use of other agents such as plasmid/viral vectors, hinting at the possibility of origin from the mesencephalon. While tracing the origin from the mesencephalon in vivo and in vitro is promising and on our to-do list, the data will not be available for this manuscript. To prevent confusion, we have eliminated redundant panels of Fig. 8 with Supplementary Fig. 2 and 3. However, if the reviewer deems it necessary to remove these panels, we are prepared to do so.

Reviewer #2 (Public Review):

Summary:

Complexin (Cplx) is expressed at nearly all chemical synapses. Mammalian Cplx comes in four different paralogs which are differentially expressed in different neurons or secretory cell types, either selectively or in combination with one or two other Cplx isoforms. Cplx binds with high affinity to assembled SNARE complexes and promotes evoked synchronous release. Cplx is assumed to preclude premature SV fusion by preventing full SNARE assembly, thereby arresting subsequent SNARE-driven fusion ("fusion-clamp" theory). The protein has multiple domains, the functions of which are controversially discussed. Cplx's function has been studied in a variety of model organisms including mouse, fly, worm, and fish with seemingly conflicting results which led to partly contradicting conclusions.<br /> Makee et al. study the function of mammalian Cplx2 in chromaffin cells by making use of Cplx2 ko mice to overexpress and functionally characterize mutant Cplx2 forms in cultured chromaffin cells. The main conclusion of the present study are:

The hydrophobic character of the amphipathic helix in Cplx's C-terminal domain is essential for inhibiting premature vesicle fusion at a [Ca2+]i of several hundreds of nM (pre-flash [Ca2+]i). The Cplx-mediated inhibition of fusion under these conditions does not rely on expression of either Syt1 or Syt7.

Slow-down of exocytosis by N-terminally truncated Cplx mutants in response to a [Ca2+]i of several µM (peak flash [Ca2+]i) occurs regardless of the presence or absence of Syt7 demonstrating that Cplx2 does not act as a switch favoring preferential assembly of the release machinery with Syt1,2 rather than the "slow" sensor Syt7.

Cplx's N-terminal domain is required for the Cplx2-mediated increase in the speed of exocytosis and faster onset of exocytosis which likely reflect an increased apparent Ca2+ sensitivity and faster Ca2+ binding of the release machinery.

Strengths:

The authors perform systematic truncation/mutational analyses of Cplx2. They analyze the impact of single and combined deficiencies for Cplx2 and Syt1 to establish interactions of both proteins.<br /> State-of-the-art methods are employed: Vesicle exocytosis is assayed directly and with high resolution using capacitance measurements. Intracellular [Ca2+] is controlled by loading via the patch-pipette and by UV-light induced flash-photolysis of caged [Ca2+]. The achieved [Ca2+ ] is measured with Ca2+ -sensitive dyes.<br /> The data is of high quality and the results are compelling.

Weaknesses:

With the exception of mammalian retinal ribbon synapses (and some earlier RNAi knock down studies which had off-target effects), there is little experimental evidence for a "fusion-clamp"-like function of Cplxs at mammalian synapses. At conventional mammalian synapses, genetic loss of Cplx (i.e. KO) consistently decreases AP-evoked release, and generally either also decreases spontaneous release rates or does not affect spontaneous release, which is inconsistent with a "fusion-clamp" theory. This is in stark contrast to invertebrate (D. m. and C. e.) synapses where genetic Cplx loss is generally associated with a strong upregulation of spontaneous release.

There are alternative scenarios explaining how Cplx may phenomenological "clamp" vesicle fusion rates without mechanistically assigning a "clamping" function to Cplx (Neher 2010, Neuron). In fact, changes in asynchronous release kinetics following conditioning AP trains observed at Cplx1 ko calyx of Held synapses do not favor a "fusion clamp" model (Chang et al., 2015, J.Neurosci.), while an alternative model, assigning Cplx the role of a "checkpoint" protein in SNARE assembly, quantitatively reproduces all experimental observations (Lopez et al., 2024, PNAS). It might be helpful for a reader to mention such alternative scenarios.

eLife assessment

This important work shows compelling data that significantly advances our understanding of the regulation of neurotransmitter and hormone secretion by exploring the mechanisms of how the protein complexin 2 (Cplx2) interacts with the calcium sensor synaptotagmin. The function of mammalian Cplx2 is studied using chromaffin cells derived from Cplx2 knock out mice as a system to overexpress and functionally characterize mutant Cplx2 forms and the interaction between Cplx2 and synaptotagmin. The authors identify structural requirements within the protein for Cplx's dual role in preventing premature vesicle exocytosis and enhancing evoked exocytosis. The findings are of broad interest to neuroscientists and cell biologists.

Reviewer #1 (Public Review):

Summary:

Using chromaffin cells as a powerful model system for studying secretion, the authors study the regulatory role of complexin in secretion. Complexin is still enigmatic in its regulatory role, as it both provides inhibitory and facilitatory functions in release. The authors perform an extensive structure-function analysis of both the C- and N-terminal regions of complexin. There are several interesting findings that significantly advances our understanding of cpx/SNARe interactions in regulating release. C-terminal amphipathic helix interferes with SNARE complex assembly and thus clamps fusion. There are acidic residues in the C-term that may be seen as putative interaction partners for Synaptotagmin. The N-terminus of Complexin promoting role may be associated with an interaction with Syt1. In particular the putative interaction with Syt1 is of high interest and supported by quite strong functional and biochemical evidence. The experimental approaches are state of the art, and the results are of the highest quality and convincing throughout. They are adequate and intelligently discussed in the rich context of the standing literature. Whilst there are some concerns about whether the facilitatory actions of complexion have to be tightly linked to Syt1 interactions, the proposed model will significantly advance the field by providing new directions in future research.

Author response:

The following is the authors’ response to the previous reviews.

Reviewer #1 (Recommendations For The Authors):

The revised manuscript addressed my minor concerns adequately, and the manuscript is now further improved. I have no remaining criticisms.

Reviewer #2 (Recommendations For The Authors):

Abstract:

line 45 The abbreviation "SytI" should perhaps be introduced above.

done

Results:

line 139 "RRP kinetics" should perhaps read "RRP depletion kinetics" or "secretion kinetics".

We replaced “RRP kinetics” with “RRP secretion kinetics”

line 325ff and Figure 8

As far as I understand, SytI 875 R233Q ki cells shown in violet express wt CplxII. Perhaps this should be explicitly stated?

To accommodate this suggestion: We now state on page 13 line 302: “Overexpression of the CpxII DN mutant in SytI R233Q ki cells, which is expected to outcompete the function of endogenous CpxII in these cells (Dhara et al., 2014), further slowed down the rate of synchronized release and restored the EB size to the wt level (Figure 7C, D)”

line 332ff and Figure 8

What is plotted in Figure 8B bottom and in Figure 8D is not a "rate" but rather a "unitary rate", more commonly referred to as a "rate constant".

The y-axis label of Figures 8B and 8D should therefore better be changed to "rate constant". See also line 528 of the Discussion.

Figure (y-axis label) and text were changed accordingly

eLife assessment

The ExA-SPIM methodology developed will be important to the field of light sheet microscopy as the new technology provides an impressive field of view making it possible to image the entire expanded mouse brain at cellular and subcellular resolution. The authors provide solid evidence that mostly supports the conclusions.

Reviewer #1 (Public Review):

Summary:

Glaser et al present ExA-SPIM, a light-sheet microscope platform with large volumetric coverage (Field of view 85mm^2, working distance 35mm ), designed to image expanded mouse brains in their entirety. The authors also present an expansion method optimized for whole mouse brains, and an acquisition software suite. The microscope is employed in imaging an expanded mouse brain, the macaque motor cortex and human brain slices of white matter.<br /> This is impressive work, and represents a leap over existing light-sheet microscopes. As an example, it offers a ~ fivefold higher resolution than mesoSPIM (https://mesospim.org/), a popular platform for imaging large cleared samples. Thus while this work is rooted in optical engineering, it manifests a huge step forward and has the potential to become an important tool in the neurosciences.

Strengths:

-ExA-SPIM features an exceptional combination of field of view, working distance, resolution and throughput.

-An expanded mouse brain can be acquired with only 15 tiles, lowering the burden on computational stitching. That the brain does not need to be mechanically sectioned is also seen as an important capability.

-The image data is compelling, and tracing of neurons has been performed. This demonstrates the potential of the microscope platform.

Weaknesses:

-There is a general question about the scaling laws of lenses, and expansion microscopy, which in my opinion remained unanswered: In the context of whole brain imaging, a larger expansion factor requires a microscope system with larger volumetric coverage, which in turn will have lower resolution (Figure 1B). So what is optimal? Could one alternatively image a cleared (non-expanded) brain with a high resolution ASLM system (Chakraborty, Tonmoy, Nature Methods 2019, potentially upgraded with custom objectives) and get similar effective resolution as the authors get with expansion? This is not meant to diminish the achievement, but it was unclear if the gains in resolution from the expansion factor are traded off by the scaling laws of current optical systems.

-It was unclear if 300 nm lateral and 800 nm axial resolution is enough for many questions in neuroscience. Segmenting spines, distinguishing pre- and postsynaptic densities, or tracing densely labeled neurons might be challenging. A discussion about the necessary resolution levels in neuroscience would be appreciated.

-Would it be possible to characterize the aberrations that might be still present after whole brain expansion? One approach could be to image small fluorescent nanospheres behind the expanded brain, and recover the pupil function via phase retrieval. But even full width half maximum (FWHM) measurements of the nanospheres' images would give some idea of the magnitude of the aberrations.

Review of the revised manuscript:

The authors have carefully addressed my concerns and suggestions.

I appreciate the extended discussion on tissue clearing compared to expansion. I would recommend substantiating some of the statements though with references, or in other instances expanding a little further. I would encourage the authors to consider the points below. But there is also another path to actually reduce that specific discussion, if the conclusion is that it opened more questions than answers.

Specifically, here are some points in the paragraph that discusses tissue clearing and expansion that could be improved:<br /> -The statement "Spherical aberration increases with NA" reads nonspecific to me. I think a more precise formulation would be "The effect of spherical aberration (e.g. loss of Strehl ratio) increases with NA. The stated third power law would also benefit from a reference.<br /> -The statement "the index of refraction gradients in tissue decreases with the third power of the expansion factor..." reads a bit odd. "Gradients in refractive index" would be more consistent with the usage of r.i. throughout the manuscript.<br /> For the third power law, it might be important to know what drives the remaining refractive index variation in expansion microscopy. If it is the labels and their linkers, then indeed, they get increasingly diluted as their amount remains constant. However, if the aberrations are caused by the polymer gel, I would assume you would need more monomer material for higher expansion factors? Thus, I was not fully sure about the scaling law in this case. If there is a reference where this was explored in detail, that would resolve this issue.

-The statement that aberrations scale with gradients in refractive index also needs either a reference, or an explanation for the reader. I think figure S4 was supposed to illustrate this, but was not referenced in the discussion (and could be clarified, see comment below).

To me, the discussion focused strongly on tissue clearing vs expansion. What was left out in the discussion was if larger expansion factors would be favorable (i.e. whole brain imaging with 10-20X expansion instead of 4-5X). Some arguments implicitly seemed to stipulate that a larger expansion factor would optically be favorable. But Figure S7 highlights another tradeoff with the decay in sensitivity and Figure 1b provides the technological constraints on lens design. So as a reader, I was not fully sure if the next frontier should be 10-20X expansion brain imaging, or if 4-5X is currently a sweet spot.

Further comments:

Please explain the variables in Figure S4, such as F, WD and d. It was unclear to me what the RI profile should mean in the bottom row. Naively, the figure of merit would be the optical path length that is integrated along the different rays, as this leads to a variation in the wavefront.

Figure S5: I would caution to say the SNR was quantified, but rather say it was estimated (in the shot noise limit). Was the background subtracted for the SNR measurements?<br /> Squaring the SNR estimates, it looks like the photon counts went down ~10-fold from z=2mm to z=25mm. That is a larger reduction in signal than I had expected. If it was based solely on aberrations, a 10-fold drop in Strehl ratio seems significant (potentially smaller if we assume the light-sheet also underwent aberrations). Are there other factors that could explain the signal reduction (maybe from the labeling side)?<br /> Further on Figure S5: Fourier transforms (power spectrum) and single line profiles are in my opinion not the best way to quantify resolution. Could the authors perform image decorrelation analysis on the region of interest (Descloux, A., Kristin Stefanie Grußmayer, and Aleksandra Radenovic. "Parameter-free image resolution estimation based on decorrelation analysis." Nature methods 2019) or Fourier ring correlation? This would give in some sense an average resolving power in that depth, and would remove the bias from picking a line profile.

Reviewer #2 (Public Review):

Summary:

In this revised manuscript, Glaser et al. have responded to the reviewer comments by removing some of the overstated claims from the prior manuscript and editing portions of the manuscript text to enhance the clarity. Although the manuscript would be stronger if the authors had been able to provide data that justified the original high-impact claims from the initial publication (e.g. that the images could be used for robust and automated neuronal tracing across large volumes), the amended manuscript text now more closely matches the supporting data. As with the initial submission, I believe that the microscope design and characterization is a useful contribution to the field and the data are quite stunning. However, I still feel like there are some overstated claims in this revision that should be addressed so as not to mislead readers.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Glaser et al present ExA-SPIM, a light-sheet microscope platform with large volumetric coverage (Field of view 85mm^2, working distance 35mm), designed to image expanded mouse brains in their entirety. The authors also present an expansion method optimized for whole mouse brains and an acquisition software suite. The microscope is employed in imaging an expanded mouse brain, the macaque motor cortex, and human brain slices of white matter. 

This is impressive work and represents a leap over existing light-sheet microscopes. As an example, it offers a fivefold higher resolution than mesoSPIM (https://mesospim.org/), a popular platform for imaging large cleared samples. Thus while this work is rooted in optical engineering, it manifests a huge step forward and has the potential to become an important tool in the neurosciences. 

Strengths: 

- ExA-SPIM features an exceptional combination of field of view, working distance, resolution, and throughput. 

- An expanded mouse brain can be acquired with only 15 tiles, lowering the burden on computational stitching. That the brain does not need to be mechanically sectioned is also seen as an important capability. 

- The image data is compelling, and tracing of neurons has been performed. This demonstrates the potential of the microscope platform. 

Weaknesses: 

- There is a general question about the scaling laws of lenses, and expansion microscopy, which in my opinion remained unanswered: In the context of whole brain imaging, a larger expansion factor requires a microscope system with larger volumetric coverage, which in turn will have lower resolution (Figure 1B). So what is optimal? Could one alternatively image a cleared (non-expanded) brain with a high-resolution ASLM system (Chakraborty, Tonmoy, Nature Methods 2019, potentially upgraded with custom objectives) and get a similar effective resolution as the authors get with expansion? This is not meant to diminish the achievement, but it was unclear if the gains in resolution from the expansion factor are traded off by the scaling laws of current optical systems. 

Paraphrasing the reviewer: Expanding the tissue requires imaging larger volumes and allows lower optical resolution. What has been gained?

The answer to the reviewer’s question is nuanced and contains four parts. 

First, optical engineering requirements are more forgiving for lenses with lower resolution. Lower resolution lenses can have much larger fields of view (in real terms: the number of resolvable elements, proportional to ‘etendue’) and much longer working distances. In other words, it is currently more feasible to engineer lower resolution lenses with larger volumetric coverage, even when accounting for the expansion factor. 

Second, these lenses are also much better corrected compared to higher resolution (NA) lenses. They have a flat field of view, negligible pincushion distortions, and constant resolution across the field of view. We are not aware of comparable performance for high NA objectives, even when correcting for expansion.

Third, although clearing and expansion render tissues ‘transparent’, there still exist refractive index inhomogeneities which deteriorate image quality, especially at larger imaging depths. These effects are more severe for higher optical resolutions (NA), because the rays entering the objective at higher angles have longer paths in the tissue and will see more aberrations. For lower NA systems, such as ExaSPIM, the differences in paths between the extreme and axial rays are relatively small and image formation is less sensitive to aberrations. 

Fourth, aberrations are proportional to the index of refraction inhomogeneities (dn/dx). Since the index of refraction is roughly proportional to density, scattering and aberration of light decreases as M^3, where M is the expansion factor. In contrast, the imaging path length through the tissue only increases as M. This produces a huge win for imaging larger samples with lower resolutions. 

To our knowledge there are no convincing demonstrations in the literature of diffraction-limited ASLM imaging at a depth of 1 cm in cleared mouse brain tissue, which would be equivalent to the ExA-SPIM imaging results presented in this manuscript.  

In the discussion of the revised manuscript we discuss these factors in more depth. 

- It was unclear if 300 nm lateral and 800 nm axial resolution is enough for many questions in neuroscience. Segmenting spines, distinguishing pre- and postsynaptic densities, or tracing densely labeled neurons might be challenging. A discussion about the necessary resolution levels in neuroscience would be appreciated. 

We have previously shown good results in tracing the thinnest (100 nm thick) axons over cm scales with 1.5 um axial resolution. It is the contrast (SNR) that matters, and the ExaSPIM contrast exceeds the block-face 2-photon contrast, not to mention imaging speed (> 10x).  

Indeed, for some questions, like distinguishing fluorescence in pre- and postsynaptic structures, higher resolutions will be required (0.2 um isotropic; Rah et al Frontiers Neurosci, 2013). This could be achieved with higher expansion factors.

This is not within the intended scope of the current manuscript. As mentioned in the discussion section, we are working towards ExA-SPIM-based concepts to achieve better resolution through the design and fabrication of a customized imaging lens that maintains a high volumetric coverage with increased numerical aperture.  

- Would it be possible to characterize the aberrations that might be still present after whole brain expansion? One approach could be to image small fluorescent nanospheres behind the expanded brain and recover the pupil function via phase retrieval. But even full width half maximum (FWHM) measurements of the nanospheres' images would give some idea of the magnitude of the aberrations. 

We now included a supplementary figure highlighting images of small axon segments within distal regions of the brain.  

Reviewer #2 (Public Review): 

Summary: 

In this manuscript, Glaser et al. describe a new selective plane illumination microscope designed to image a large field of view that is optimized for expanded and cleared tissue samples. For the most part, the microscope design follows a standard formula that is common among many systems (e.g. Keller PJ et al Science 2008, Pitrone PG et al. Nature Methods 2013, Dean KM et al. Biophys J 2015, and Voigt FF et al. Nature Methods 2019). The primary conceptual and technical novelty is to use a detection objective from the metrology industry that has a large field of view and a large area camera. The authors characterize the system resolution, field curvature, and chromatic focal shift by measuring fluorescent beads in a hydrogel and then show example images of expanded samples from mouse, macaque, and human brain tissue. 

Strengths: 

I commend the authors for making all of the documentation, models, and acquisition software openly accessible and believe that this will help assist others who would like to replicate the instrument. I anticipate that the protocols for imaging large expanded tissues (such as an entire mouse brain) will also be useful to the community. 

Weaknesses: 

The characterization of the instrument needs to be improved to validate the claims. If the manuscript claims that the instrument allows for robust automated neuronal tracing, then this should be included in the data. 

The reviewer raises a valid concern. Our assertion that the resolution and contrast is sufficient for robust automated neuronal tracing is overstated based on the data in the paper. We are hard at work on automated tracing of datasets from the ExA-SPIM microscope. We have demonstrated full reconstruction of axonal arbors encompassing >20 cm of axonal length.  But including these methods and results is out of the scope of the current manuscript. 

The claims of robust automated neuronal tracing have been appropriately modified.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Smaller questions to the authors: 

- Would a multi-directional illumination and detection architecture help? Was there a particular reason the authors did not go that route?

Despite the clarity of the expanded tissue, and the lower numerical aperture of the ExA-SPIM microscope, image quality still degrades slightly towards the distal regions of the brain relative to both the excitation and detection objective. Therefore, multi-directional illumination and detection would be advantageous. Since the initial submission of the manuscript, we have undertaken re-designing the optics and mechanics of the system. This includes provisions for multi-directional illumination and detection. However, this new design is beyond the scope of this manuscript. We now mention this in L254-255 of the Discussion section.

- Why did the authors not use the same objective for illumination and detection, which would allow isotropic resolution in ASLM? 

The current implementation of ASLM requires an infinity corrected objective (i.e. conjugating the axial sweeping mechanism to the back focal plane). This is not possible due to the finite conjugate design of the ExA-SPIM detection lens.

More fundamentally, pushing the excitation NA higher would result in a shorter light sheet Rayleigh length, which would require a smaller detection slit (shorter exposure time, lower signal to noise ratio). For our purposes an excitation NA of 0.1 is an excellent compromise between axial resolution, signal to noise ratio, and imaging speed. 

For other potentially brighter biological structures, it may be possible to design a custom infinity corrected objective that enables ASLM with NA > 0.1.

- Have the authors made any attempt to characterize distortions of the brain tissue that can occur due to expansion? 

We have not systematically characterized the distortions of the brain tissue pre and post expansion. Imaged mouse brain volumes are registered to the Allen CCF regardless of whether or not the tissue was expanded. It is beyond the scope of this manuscript to include these results and processing methods, but we have confirmed that the ExA-SPIM mouse brain volumes contain only modest deformation that is easily accounted for during registration to the Allen CCF. 

- The authors state that a custom lens with NA 0.5-0.6 lens can be designed, featuring similar specifications. Is there a practical design? Wouldn't such a lens be more prone to Field curvature? 

This custom lens has already been designed and is currently being fabricated. The lens maintains a similar space bandwidth product as the current lens (increased numerical aperture but over a proportionally smaller field of view). Over the designed field of view, field curvature is <1 µm. However, including additional discussion or results of this customized lens is beyond the scope of this manuscript.

Reviewer #2 (Recommendations For The Authors): 

• System characterization: 

- Please state what wavelength was used for the resolution measurements in Figure 2.

An excitation wavelength of 561 nm was used. This has been added to the manuscript text.

- The manuscript highlights that a key advance for the microscope is the ability to image over a very large 13 mm diameter field of view. Can the authors clarify why they chose to characterize resolution over an 8diameter mm field rather than the full area? 

The 13 mm diameter field of view refers to the diagonal of the 10.6 x 8.0 mm field of view. The results presented in Figure 1c are with respect to the horizontal x direction and vertical y direction. A note indicating that the 13 mm is with respect to the diagonal of the rectangular imaging field has been added to the manuscript text. The results were presented in this way to present the axial and lateral resolution as a function of y (the axial sweeping direction).

- The resolution estimates seem lower than I would expect for a 0.30 NA lens (which should be closer to ~850 nm for 515 nm emission). Could the authors clarify the discrepancy? Is this predicted by the Zemax model and due to using the lens in immersion media, related to sampling size on the camera, or something else? It would be helpful if the authors could overlay the expected diffraction-limited performance together with the plots in Figure 2C. 

As mentioned previously, the resolution measurements were performed with 561 nm excitation and an emission bandpass of ~573 – 616 nm (595 nm average). Based on this we would expect the full width half maximum resolution to be ~975 nm. The resolution is in fact limited by sampling on the camera. The 3.76 µm pixel size, combined with the 5.0X magnification results in a sampling of 752 nm. Based on the Nyquist the resolution is limited to ~1.5 µm. We have added clarifying statements to the text.

- I'm confused about the characterization of light sheet thickness and how it relates to the measured detection field curvature. The authors state that they "deliver a light sheet with NA = 0.10 which has a width of 12.5 mm (FWHM)." If we estimate that light fills the 0.10 NA, it should have a beam waist (2wo) of ~3 microns (assuming Gaussian beam approximations). Although field curvature is described as "minimal" in the text, it is still ~10-15 microns at the edge of the field for the emission bands for GFP and RFP proteins. Given that this is 5X larger than the light sheet thickness, how do the authors deal with this? 

The generated light sheet is flat, with a thickness of ~ 3 µm. This flat light sheet will be captured in focus over the depth of focus of the detection objective. The stated field curvature is within 2.5X the depth of focus of the detection lens, which is equivalent to the “Plan” specification of standard microscope objectives.

- In Figure 2E, it would be helpful if the authors could list the exposure times as well as the total voxels/second for the two-camera comparison. It's also worth noting that the Sony chip used in the VP151MX camera was released last year whereas the Orca Flash V3 chosen for comparison is over a decade old now. I'm confused as to why the authors chose this camera for comparison when they appear to have a more recent Orca BT-Fusion that they show in a picture in the supplement (indicated as Figure S2 in the text, but I believe this is a typo and should be Figure S3). 

This is a useful addition, and we have added exposure times to the plot. We have also added a note that the Orca Flash V3 is an older generation sCMOS camera and that newer variants exist. Including the Orca BT-Fusion. The BT-Fusion has a read noise of 1.0 e- rms versus 1.6 e- rms, and a peak quantum efficiency of ~95% vs. 85%. Based on the discussion in Supplementary Note S1, we do not expect that these differences in specifications would dramatically change the data presented in the plot. In addition, the typo in Figure S2 has been corrected to Figure S3.

- In Table S1, the authors note that they only compare their work to prior modalities that are capable of providing <= 1 micron resolution. I'm a bit confused by this choice given that Figure 2 seems to show the resolution of ExA-SPIM as ~1.5 microns at 4 mm off center (1/2 their stated radial field of view). It also excludes a comparison with the mesoSPIM project which at least to me seems to be the most relevant prior to this manuscript. This system is designed for imaging large cleared tissues like the ones shown here. While the original publication in 2019 had a substantially lower lateral resolution, a newer variant, Nikita et al bioRxiv (which is cited in general terms in this manuscript, but not explicitly discussed) also provides 1.5-micron lateral resolution over a comparable field of view. 

We have updated the table to include the benchtop mesoSPIM from Nikita et al., Nature Communications, 2024. Based on this published version of the manuscript, the lateral resolution is 1.5 µm and axial resolution is 3.3 µm. Assuming the Iris 15 camera sensor, with the stated 2.5 fps, the volumetric rate (megavoxels/sec) is 37.41.

- The authors state that, "We systematically evaluated dehydration agents, including methanol, ethanol, and tetrahydrofuran (THF), followed by delipidation with commonly used protocols on 1 mm thick brain slices. Slices were expanded and examined for clarity under a macroscope." It would be useful to include some data from this evaluation in the manuscript to make it clear how the authors arrived at their final protocol. 

Additional details on the expansion protocol may be included in another manuscript.

General comments: 

• There is a tendency in the manuscript to use negative qualitative terms when describing prior work and positive qualitative terms when describing the work here. Examples include: 

- "Throughput is limited in part by cumbersome and error-prone microscopy methods". While I agree that performing single neuron reconstructions at a large scale is a difficult challenge, the terms cumbersome and error-prone are qualitative and lacking objective metrics.

We have revised this statement to be more precise, stating that throughput is limited in part by the speed and image quality of existing microscopy methods.

- The resolution of the system is described in several places as "near-isotropic" whereas prior methods were described as "highly anisotropic". I agree that the ~1:3 lateral to axial ratio here is more isotropic than the 1:6 ratio of the other cited publications. However, I'm not sure I'd consider 3-fold worse axial resolution than lateral to be considered "near" isotropic.

We agree that the term near-isotropic is ambiguous. We have modified the text accordingly, removing the term near-isotropic and where appropriate stating that the resolution is more isotropic than that of other cited publications.

- exposures (which in the caption is described as "modest"). I'd suggest removing these qualitative terms and just stating the values.

We agree and have changed the text accordingly.

• The results section for Figure 5 is titled "Tracing axons in human neocortex and white matter". Although this section states "larger axons (>1 um) are well separated... allowing for robust automated and manual tracing" there is no data for any tracing in the manuscript. Although I agree that the images are visually impressive, I'm not sure that this claim is backed by data.

We have now removed the text in this section referring to automated and manual tracing.

eLife assessment

The paper investigates a potential cause of a type of severe epilepsy that develops in early life because of a defect in a gene called KCNQ2. The significance is fundamental because it substantially advances our understanding of a major research question. The strength of the evidence is convincing because appropriate methods are used that are in line with the state-of-the art.

Reviewer #1 (Public Review):

Abreo et al., performed a detailed multidisciplinary analysis of a pathogenic variant of the KCNQ2 ion channel subunit identified in a child with neonatal-onset epilepsy and neurodevelopmental disorders. These analyses revealed multiple molecular and cellular mechanisms associated with this variant, and providing important insights into what distinguishes distinct pathogenic variants of KCNQ2 associated with self-limited familial neonatal epilepsy versus those leading to developmental and epileptic encephalopathy, and how they may mechanistically differ, to result in different extents of developmental impairment. The authors first provide a detailed clinical description of the patient heterozygous for a novel pathogenic variant encoding KCNQ2 G256W. They then model the structure of the G256W variant based on recent cryo-EM structures of KCNQ2 and other ion channel subunits and find that while the affected position is quite distinct from the channel pore, it participates in a novel, evolutionarily conserved set of amino acids that form a network of hydrogen bonds that stabilize the structure of the pore domain. They then undertake a series of rigorous and quantitative laboratory experiments in which the KCNQ2 G256W variant is coexpressed exogenously with WT KCNQ2 and KCNQ3 subunits in heterologous cells, and endogenously in novel gene edited mice generated for this study. This includes detailed electrophysiological analyses in the transfected heterologous cells revealing the dominant-negative phenotype of KCNQ2 G256W. They find altered firing properties in hippocampal CA1 neurons in brain slices from the heterozygous KCNQ2 G256W mice. They next show that the expression and localization of KCNQ channels is altered in brain neurons from heterozygous KCNQ2 G256W mice, suggesting that this variant impacts KCNQ2 trafficking and stability. Together, these laboratory studies reveal that the molecular and cellular mechanisms shaping KCNQ channel expression, localization and function are impacted at multiple levels by the variant encoding KCNQ2 G256W, likely contributing to the clinical features of the child heterozygous for this variant relative to patients harboring distinct KCNQ2 pathogenic variants.

Reviewer #3 (Public Review):

Summary:

This manuscript describes the symptoms of patients harboring KCNQ2 mutation G256W, functional changes of the mutant channel in exogenous expression, and phenotypes of G256W/+ mice. The patients presented seizures, the mutation reduced currents of the channel, and the G256W/+ mice show seizures, increased firing frequency in neurons, and reduced KCNQ2 expression and altered subcellular distribution.

Strengths:

This is a large amount of work and all results corroborated the pathogenicity of the mutation in KCNQ2, providing an interesting example of KCNQ2-associated neurological disorder's impact on functions at all levels including molecular, cellular, tissue, animal model and patients.