Reviewer #1 (Public review):

The authors point out that the fitness estimates obtained from different experimental assays (monoculture, pairwise competition, or bulk competition) are not generally equivalent, not even with regard to the fitness ranking of different genotypes. Using a computational model based on experimentally measured growth phenotypes for knockout strains in yeast, as well as data from Lenski's Long Term Evolution Experiment (LTEE), they derive a set of best practice rules aimed at extracting the optimal amount of information from such experiments.

The study is very complete on a technical level and I have no suggestions for further analyses. However, I feel the readability and the conceptual focus of the manuscript could be significantly improved by rearranging the material with regard to the contents of the main text vs. the Methods and the Supplement. Detailed recommendations:

(1) Regarding readability, the large number of references to material in the Methods and Supplement fragment the main text and make it difficult to follow.

(2) Conceptually, it seems to me that the current presentation obscures the reasons why we should care about fitness in the first place. In the first paragraph of Results, the authors define fitness "as any number that is sufficient to predict the genotype's relative abundance x(t) over a short-time horizon". To me, this seems like an extremely narrow and not very interesting definition. Instead, I view fitness as an intrinsic property of a genotype that allows us to predict its performance<br /> under a range of conditions, including in particular conditions that are different from the experimental setup that was used to obtain the fitness estimates. The latter viewpoint is well expressed in Supplementary Section S1, where the authors discuss the notion of fitness potential. I would recommend to move at least part of this discussion to the main text. By comparison, the arguments in favor of the logit encoding that currently opens the Results session are rather straightforward and could be shortened significantly.

(3) Similarly, the modeling strategy used in this work is quite subtle and needs to be explained more fully in the main text. The authors use growth traits (lag time, growth rate, and yield) extracted from monoculture experiments on a yeast knockout collection and feed them into a specific mathematical model to simulate pairwise and bulk competition scenarios. Since a key claim of the work is that monoculture experiments are generally poor predictors of competitive fitness, the basis for this conclusion and the assumptions on which it is based need to be described clearly in the main text. In the current version of the manuscript, this information has<br /> been largely relegated to the Methods section.

Reviewer #2 (Public review):

Summary:

The manuscript "Quantifying microbial fitness in high-throughput experiments" provides a comprehensive analysis of the various approaches to quantifying fitness in microbial evolution, focusing on three primary factors: encoding of relative abundance, time scale of measurement, and the choice of reference subpopulation. The authors systematically explore how these choices impact fitness statistics and provide recommendations aimed at standardizing practices in the field. This manuscript aims to highlight the impact of differing fitness definitions and the methodologies utilized for analysis and how that can significantly alter interpretations of mutant fitness, affecting evolutionary predictions and the overall understanding of genetic interactions in the experiments. Although this manuscript focuses on a critical issue in the quantification of fitness in high throughput experiments, it heavily relies on only one experimental dataset (Warringer et al 2003) and one organism i.e, Yeast (Saccharomyces cerevisiae) grown in a defined medium, the environmental influence is not completely captured. While the theoretical framework is strong, more experimental examples with more organisms (i.e., more datasets) in their analysis and comparison would enhance the manuscript, especially its conclusion.

Strengths:

The choices for quantifying fitness in evolution experiments are critical and highly relevant given the increasing prevalence of high-throughput experiments in evolutionary biology. The authors methodically categorize fitness statistics and their implications, providing clarity on a complex subject. This structured approach aids in understanding the nuances of fitness measurement. The manuscript effectively highlights how different choices in fitness measurement can influence fitness rankings and the understanding of epistasis, which is important for modeling evolutionary dynamics.

Weaknesses:

The theoretical framework is robust, but the manuscript could benefit from more empirical examples to illustrate how different fitness quantification methods lead to varied conclusions in experiments. The discussion on the choice of reference subpopulation could be expanded with the influence of the environment or the condition. Different types of reference groups might yield different implications for fitness calculations, and further elaboration would enhance this section. The authors overgeneralize some findings; for instance, the implications of fitness measurement choices could vary significantly across different microbes or experimental conditions. A more detailed discussion would strengthen the conclusion.

Overall, this manuscript is a significant contribution to the field of evolutionary biology, addressing a critical issue in the quantification of fitness but lacks more experimental support to make it a wider claim. By systematically exploring the factors that influence fitness measurements, the authors provide valuable insights that can guide future research - the framework is computationally thorough but needs a more detailed explanation of concepts instead of generalizing. Further work is needed, particularly to incorporate empirical examples and expand certain discussions to include environmental variation and their impact, which would improve clarity and applicability.

Reviewer #3 (Public review):

Summary:

The authors present analyses of different fitness measures derived from empirical data from yeast knock-out mutants and the long-term evolution experiment (LTEE) with Escherichia coli to explore discrepancies and identify preferred methods to estimate relative fitness in high-throughput experiments. Their work has three components. They first discuss the different "encodings" of relative abundance data and conclude that logit transformations are preferred because they transform nonlinear abundance trajectories into linear trajectories with greater predictive power. Next, they compare per-generation with per-growth cycle relative fitness estimates inferred from simulations of pairwise competitions based on published growth traits for the yeast strains and on published pairwise competition measurements for the LTEE data. Both data sets show quantitative and qualitative (i.e. rank order) discrepancies of estimates across different time scales, which are highlighted by considering possible underlying causes (i.e. trade-offs between growth traits) and consequences (i.e. epistasis among mutations affecting different growth traits). Finally, the authors compare simulated pairwise and bulk (i.e. where many mutants compete during a growth cycle in a single environment) competition assays based on the yeast knock-out mutants and demonstrate an optimal ratio of collective mutants to wild-type strains that minimizes both sampling error and overestimation of fitness estimates when compared with pairwise competitions.

Strengths:

The study deals with a highly relevant topic. Fitness is central to general evolutionary theory, but also poorly defined and implies different traits for different organisms and conditions. For microbes, which are often used in evolution experiments, high-throughput experiments may yield different measures to quantify abundance over time, from individual growth traits to bulk competition experiments. Hence, it is relevant to consider discrepancies among those measures and identify preferred measures with respect to predicting population dynamics and evolutionary processes. The present study contributes to this aim by (i) making readers aware of differences among commonly used fitness estimates, (ii) showing that simulated (yeast) and calculated (E. coli) competitive fitness may differ across time scales, and (iii) showing that bulk competitions may yield relative fitness estimates that are systematically higher than pairwise competitions. The study is rather thorough on the theory side, with extensive derivations and analyses of various fitness measures using their resource competition model in the Supplementary Information. The study ends with a few practical recommendations for preferred methods to infer relative fitness estimates, that may be useful for experimentalists and stimulate further investigations.

Weaknesses:

The study has several limitations. Perhaps the most apparent limitation is the lack of a clear answer to the question of which fitness measure is best "in the light of first principles". The authors show clear discrepancies between fitness estimates across different time scales or using different reference genotypes in bulk competition and provide useful recommendations based on practical considerations (e.g. using pairwise competitions as the "golden standard"), but it remains unclear whether these measures provide the greatest value for the questions researchers may want to answer with them (e.g. predict shifts in genotype frequencies).

A second limitation is that the authors analyse fitness differences arising solely from resource competition, whereas microbes often interact via other mechanisms, e.g. the production of anticompetitior toxins, cross-feeding of metabolites, or lack of growth to enhance their persistence in stress conditions. Without simulations of these processes, understanding discrepancies among fitness measures is necessarily limited. In addition, the analysis of trade-offs between growth traits causing these discrepancies during resource competition seems confounded by biases in measurement error or parameter estimation, at least for growth rate and lag time (Figure 2B), where the replicate estimates for the wildtype show a similar negative correlation.

Third, the study does not validate relative fitness predictions from growth traits (as is done for the yeast mutants) with measured relative fitness estimates using competition assays, while such data are available, e.g. for the LTEE. This would strengthen their inferences about preferred fitness measures.

Fourth, the analysis of epistasis between mutations affecting different growth traits (shown in Figure 3) based on the LTEE data could be better introduced and analysed more comprehensively. Now, the examples given in panels C-F seem rather idiosyncratic and readers may wonder how general these consequences of using fitness estimates based on different time scales are.

Finally, the study is generally less accessible to experimentalists due to the extensive and principled treatment of specific population dynamic models and fitness inferences. This may distract from the overarching aim to identify fitness measures that are most accurate and useful for predictions of population dynamics and evolutionary processes. In this light, the motivation for the initial discussion of the importance of how to best encode relative abundance (Figure 1) is unclear. Also, the conclusion, that logit encoding is preferred, because it linearizes logistic growth dynamics and "improves the quality of predictions", is not further motivated. Experimentalists using non-linear models to infer fitness from growth curves or competition assays may miss the relevance of this discussion.

Author response:

We thank all three reviewers and the editors for their detailed comments on our manuscript.  The two main themes of this feedback concern the paper’s generality and its presentation.  Reviewers #2 and #3 raise questions about how the discrepancies in fitness statistics we report will be realized across organisms, environments, and in models with interactions beyond resource competition (e.g., toxicity or cross-feeding).  All reviewers and the editors have also expressed the need for the presentation to be improved, including a broader introduction to the concept of fitness (Reviewer #1), a clearer explanation of our model (Reviewer #1), better explanations of how quantifying fitness answers key biological questions (Reviewer #3), and improvements to the most technical sections to ensure accessibility to experimentalists (Reviewer #3).

In light of these comments, we wish to clarify that the goal of this paper is to provide a proof-of-principle for how different choices in quantifying fitness can lead to different analysis outcomes.  Since the focus of this paper is on the theoretical concepts, we focus on a few example data sets and a simple model to demonstrate the existence of these discrepancies.  While other organisms and environments, especially with more complex growth dynamics and interactions, could certainly have additional or different discrepancies in fitness statistics, we believe the simplicity of our approach is valuable because it demonstrates that even basic features of microbial growth (common across systems) with realistic parameter values are sufficient to cause significant differences in fitness depending on these quantification choices.  We agree with the reviewers that a systematic documentation of how these fitness discrepancies are empirically realized is important, but we believe that question is best explored in separate future works that can focus fully on this empirical rather than theoretical question.

We plan to revise the manuscript in several ways, following the suggestions of the three reviewers and the editor.  First, we will better articulate the main goal and conclusions of this manuscript, especially its generality and limitations.  Second, we will work to streamline and clarify several points in the main text identified by the reviewers to make it more accessible and useful to a broader audience, especially experimentalists who routinely measure fitness in their work.  We are grateful to the reviewers and the editor for their time and effort in assessing the manuscript, and we look forward to providing an updated version that addresses these concerns.

eLife Assessment

This study provides valuable insights into the efficacy and safety of pyrotinib as an extended adjuvant therapy following trastuzumab-based treatment in patients with high-risk HER2-positive breast cancer. The strength of evidence is solid, supported by the multicenter phase II trial design, which included a substantial number of patients across 23 centers in China. However, the single-arm study design without a control group limits the ability to draw definitive conclusions about the comparative effectiveness of pyrotinib.

Reviewer #1 (Public review):

Summary:

This study introduces a novel therapeutic strategy for patients with high-risk HER2-positive breast cancer and demonstrates that the incorporation of pyrotinib into adjuvant trastuzumab therapy can improve invasive disease-free survival.

Strengths:

The study features robust logic and high-quality data. Data from 141 patients across 23 centers were analyzed, thereby effectively mitigating regional biases and endowing the research findings with high applicability.

Weaknesses:

(1) Introduction and Discussion: Update the literature regarding the efficacy of pyrotinib combined with trastuzumab in treating HER2-positive advanced breast cancer.

(2) Did all the data have a normal distribution? Expand the description of statistical analysis.

(3) The novelty and innovative potential of your manuscript compared to the published literature should be described in more detail in the abstract and discussion section.

(4) Figure legend should provide a bit more detail about what readers should focus on.

(5) P-values should be clarified for the analysis.

(6) The order (A, B, and C) in Figure 3 should be labeled in the upper left corner of the Figure.

Reviewer #2 (Public review):

In this manuscript, Cao et al. evaluated the efficacy and safety of 12 months pyrotinib after trastuzumab-based adjuvant therapy in patients with high-risk, HER2-positive early or locally advanced breast cancer. Notably, the 2-year iDFS rate reached 94.59% (95% CI: 88.97-97.38) in all patients, and 94.90% (95% CI: 86.97-98.06) in patients who completed 1-year treatment of pyrotinib. This is an interesting and uplifting results, given that in ExteNET study, the 2-year iDFS rate was 93.9% (95% CI 92·4-95·2) in the 1-year neratinib group, and the 5-year iDFS survival was 90.2%, and 1-year treatment of neratinib in ExteNET study did not translate into OS benefit after 8-year follow-up. In this case, readers will be eagerly anticipating the long-term follow-up results of the current PERSIST study, as well as the results of the phase III clinical trial (NCT03980054).

I have the following comments:

(1) The introduction of the differences between pyrotinib and neratinib in terms of mechanism, efficacy, resistance, etc. is supposed to be included in the text so that authors could better highlight the clinical significance of the current trial.

(2) Please make sure that a total of 141 patients were enrolled in the study, 38 patients had a treatment duration of less than or equal to 6 months, and a total of 92 and 31 patients completed 1-year and 6-month treatment of extended adjuvant pyrotinib, respectively, which means 7 patients had a treatment duration of fewer than 6 months.

(3) The previous surgery history should be provided, and how many patients received lumpectomy, and mastectomy.

eLife Assessment

This useful modeling study alters a previous model of the intact cat spinal locomotor network to simulate a lateral hemi-section of the spinal cord. The modeling and experimental work described provide solid evidence that this model is capable of qualitatively predicting alterations to the swing and stance phase durations during locomotion at different speeds on intact or split-belt treadmills, but a revision of the figures to overlay the model predictions with the experimental data would facilitate the assessment of this qualitative agreement. This paper will interest neuroscientists studying vertebrate motor systems, including researchers investigating motor dysfunction after spinal cord injury.

Reviewer #1 (Public review):

Summary:

This study adapts a previously published model of the cat spinal locomotor network to make predictions of how phase durations of swing and stance at different treadmill speeds in tied-belt and split-belt conditions would be altered following a lateral hemisection. The simulations make several predictions that are replicated in experimental settings.

Strengths:

(1) Despite only altering the connections in the model, the model is able to replicate very well several experimental findings. This provides strong validation for the model and highlights its utility as a tool to investigate the operations of mammalian spinal locomotor networks.

(2) The study provides insights about interactions between the left and right sides of the spinal locomotor networks, and how these interactions depend on the mode of operation, as determined by speed and state of the nervous system.

(3) The writing is logical, clear, and easy to follow.

Weaknesses:

(1) Could the authors provide a statement in the methods or results to clarify whether there were any changes in synaptic weight or other model parameters of the intact model to ensure locomotor activity in the hemisected model?

(2) The authors should remind the reader what the main differences are between state-machine, flexor-driven, and classical half-center regimes (lines 77-79).

(3) There may be changes in the wiring of spinal locomotor networks after the hemisection. Yet, without applying any sort of plasticity, the model is able to replicate many of the experimental data. Based on what was experimentally replicated or not, what does the model tell us about possible sites of plasticity after hemisection?

(4) Why are the durations on the right hemisected (fast) side similar to results in the full spinal transected model (Rybak et al. 2024)? Is it because the left is in slow mode and so there is not much drive from the left side to the right side even though the latter is still receiving supraspinal drive, as opposed to in the full transection model? (lines 202-203).

(5) There is an error with probability (line 280).

Reviewer #2 (Public review):

This is a nice article that presents interesting findings. One main concern is that I don't think the predictions from the simulation are overlaid on the animal data at any point - I understand the match is qualitative, which is fine, but even that is hard to judge without at least one figure overlaying some of the data. Second is that it's not clear how the lateral coupling strengths of the model were trained/set, so it's hard to judge how important this hemi-split-belt paradigm is. The model's predictions match the data qualitatively, which is good; but does the comparison using the hemi-split-belt paradigm not offer any corrections to the model? The discussion points to modeling plasticity after SCI, which could be good, but does that mean the fit here is so good there's no point using the data to refine?

The manuscript is well-written and interesting. The putative neural circuit mechanisms that the model uncovers are great, if they can be tested in an animal somehow.

Page 2, lines 75-6: Perhaps it belongs in the other paper on the model, but it's surprising that in the section on how the model has been revised to have different regimes of operation as speed increases, there is no reference to a lot of past literature on this idea. Just one example would be Koditschek and Full, 1999 JEB Figure 3, where they talk about exactly this idea, or similarly Holmes et al., 2006 SIAM review Figure 7, but obviously many more have put this forward over the years (Daley and Beiwener, etc). It's neat in this model to have it tied down to a detailed neural model that can be compared with the vast cat literature, but the concept of this has been talked about for at least 25+ years. Maybe a review that discusses it should be cited?

Page 2, line 88: While it makes sense to think of the sides as supraspinal vs afferent driven, respectively, what is the added insight from having them coupled laterally in this hemisection model? What does that buy you beyond complete transection (both sides no supra) compared with intact? I can see how being able to vary cycle frequencies separately of the two limbs is a good "knob" to vary when perturbing the system in order to refine the model. But there isn't a ton of context explaining how the hemi-section with split belt paradigm is important for refining the model, and therefore the science. Is it somehow importantly related to the new "regimes" of operation versus speed idea for the model?

Page 5, line 212: For the predictions from the model, a lot depends on how strong the lateral coupling of the model is, which, in turn, depends on the data the model was trained on. Were the model parameters (especially for lateral coupling of the limbs) trained on data in a context where limbs were pushed out of phase and neuronal connectivity was likely required to bring the limbs back into the same phase relationship? Because if the model had no need for lateral coupling, then it's not so surprising that the hemisected limbs behave like separate limbs, one with surpaspinal intact and one without.

Page 8, line 360: The discussion of the mechanisms (increased influence of afferents, etc) that the model reveals could be causing the changes is exciting, though I'm not sure if there is an animal model where it can be tested in vivo in a moving animal.

Page 9, line 395: There are some interesting conclusions that rely on the hemi-split-belt paradigm here.

eLife Assessment

This fundamental article significantly advances our understanding of FGF signalling, and in particular, highlights the complex modifications affecting this pathway. The evidence for the authors' claims is convincing, combining state-of-the-art conditional gene deletion in the mouse lens with histological and molecular approaches. This work should be of great interest to molecular and developmental biologists beyond the lens community. The manuscript itself deserves minor editorial improvements, in particular, the literature on FGFR and SHC should be expanded in the introduction and discussed in more detail in the discussion.

Reviewer #1 (Public review):

Summary:

This manuscript uses the eye lens as a model to investigate basic mechanisms in the Fgf signaling pathway. Understanding Fgf signaling is of broad importance to biologists as it is involved in the regulation of various developmental processes in different tissues/organs and is often misregulated in disease states. The Fgf pathway has been studied in embryonic lens development, namely with regards to its involvement in controlling events such as tissue invagination, vesicle formation, epithelium proliferation, and cellular differentiation, thus making the lens a good system to uncover the mechanistic basis of how the modulation of this pathway drives specific outcomes. Previous work has suggested that proteins, other than the ones currently known (e.g., the adaptor protein Frs2), are likely involved in Fgfr signaling. The present study focuses on the role of Shp2 and Shc1 proteins in the recruitment of Grb2 in the events downstream of Fgfr activation.

Strengths:

The findings reveal that the juxtamembrane region of the Fgf receptor is necessary for proper control of downstream events such as facilitating key changes in transcription and cytoskeleton during tissue morphogenesis. The authors conditionally deleted all four Fgfrs in the mouse lens that resulted in molecular and morphological lens defects, most importantly, preventing the upregulation of the lens induction markers Sox2 and Foxe3 and the apical localization of F-actin, thus demonstrating the importance of Fgfrs in early lens development, i.e. during lens induction. They also examined the impact of deleting Fgfr1 and 2, on the following stage, i.e. lens vesicle development, which could be rescued by expressing constitutively active KrasG12D. By using specific mutations (e.g. Fgfr1ΔFrs lacking the Frs2 binding domain and Fgfr2LR harboring mutations that prevent binding of Frs2), it is demonstrated that the Frs2 binding site on Fgfr is necessary for specific events such as morphogenesis of lens vesicle. Further, by studying Shp2 mutations and deletions, the authors present a case for Shp2 protein to function in a context-specific manner in the role of an adaptor protein and a phosphatase enzyme. Finally, the key surprising finding from this study is that downstream of Fgfr signaling, Shc1 is an important alternative pathway - in addition to Shp2 - involved in the recruitment of Grb2 and in the subsequent activation of Ras. The methodologies, namely, mouse genetics and state-of-the-art cell/molecular/biochemical assays are appropriately used to collect the data, which are soundly interpreted to reach these important conclusions. Overall, these findings reveal the flexibility of the Fgf signaling pathway and its downstream mediators in regulating cellular events. This work is expected to be of broad interest to molecular and developmental biologists.

Weaknesses:

A weakness that needs to be discussed is that Le-Cre depends on Pax6 activation, and hence its use in specific gene deletion will not allow evaluation of the requirement of Fgfrs in the expression of Pax6 itself. But since this is the earliest Cre available for deletion in the lens, mentioning this in the discussion would make the readers aware of this issue. Referring to Jag1 among "lens-specific markers" (page 5) is debatable, suggesting changing to the lines of "the expected upregulation of Jag1 in lens vesicle". The Abstract could be modified to clearly convey the existing knowledge gap and the key findings of the present study. As it stands now, it is a bit all over the place. Some typos in the manuscript need to be fixed, e.g. "...yet its molecular mechanism remains largely resolved" - unresolved? "...in the development lens" - in the developing lens? In Figure 4 legend, "(B) Grb2 mutants Grb2 mutants displayed...", etc.

Reviewer #2 (Public review):

Summary:

I have reviewed a manuscript submitted by Wang et al., which is entitled "Shc1 cooperates with Frs2 and Shp2 to recruit Grb2 in FGF-induced lens development". In this paper, the authors first examined lens phenotypes in mice with Le-Cre-mediated knockdown (KD) of all four FGFR (FGFR1-4), and found that pERK signals, Jag1, and foxe3 expression are absent or drastically reduced, indicating that FGF signaling is essential for lens induction. Next, the authors examined lens phenotypes of FGFR1/2-KD mice and found that lens fiber differentiation is compromised and that proliferative activity and cell survival are also compromised in lens epithelium. Interestingly, Kras activation rescues defects in lens growth and lens fiber differentiation in FGFR1/2-KD mice, indicating that Ras activation is a key step for lens development. Next, the authors examined the role of Frs2, Shp2, and Grb2 in FGF signaling for lens development. They confirmed that lens fiber differentiation is compromised in FGFR1/3-KD mice combined with Frs2-dysfunctional FGFR2 mutants, which is similar to lens phenotypes of Grb2-KD mice. However, lens defects are milder in mice with Shp2YF/YF and Shp2CS mutant alleles, indicating that the involvement of Shp2 is limited for the Grb2 recruitment for lens fiber differentiation. Lastly, the authors showed new evidence on the possibility that another adapter protein, Shc1, promotes Grb2 recruitment independent of Frs2/Shp2-mediated Grb2 recruitment.

Strengths:

Overall, the manuscript provides valuable data on how FGFR activation leads to Ras activation through the adapter platform of Frs2/Shp2/Grb2, which advances our understanding of complex modification of the FGF signaling pathway. The authors applied a genetic approach using mice, whose methods and results are valid to support the conclusion. The discussion also well summarizes the significance of their findings.

Weaknesses:

The authors eventually found that the new adaptor protein Shc1 is involved in Grb2 recruitments in response to FGF receptor activation. however, the main data for Shc1 are histological sections and statistical evaluation of lens size. So, my major concern is that the authors need to provide more detailed data to support the involvement of Shc1 in Grb2 recruitment of FGF signaling for lens development.

Reviewer #3 (Public review):

Summary:

The manuscript entitled "Shc1 cooperates with Frs2 and Shp2 to recruit Grb2 in FGF-induced lens development" by Wang et al., investigates the molecular mechanism used by FGFR signaling to support lens development. The lens has long been known to depend on FGFR signaling for proper development. Previous investigations have demonstrated that FGFR signaling is required for embryonic lens cell survival and for lens fiber cell differentiation. The requirement of FGFR signaling for lens induction has remained more controversial as deletion of both Fgfr1 and Fgfr2 during lens placode formation does not prevent the induction of definitive lens markers such as FOXE3 or αA-crystallin. Here the authors have used the Le-Cre driver to delete all four FGFR genes from the developing lens placode demonstrating a definitive failure of lens induction in the absence of FGFR signaling. The authors focused on FGFR1 and FGFR2, the two primary FGFRs present during early lens development, and demonstrated that lens development could be significantly rescued in lenses lacking both FGFR1 and FGFR2 by expressing a constitutively active allele of KRAS. They also showed that the removal of pro-apoptotic genes Bax and Bak could also lead to a substantial rescue of lens development in lenses lacking both FGFR1 and FGFR2. In both cases, the lens rescue included both increased lens size and the expression of genes characteristic of lens cells.

Significantly the authors concentrated on the juxtamembrane domain, a portion of the FGFRs associated with FRS2. Previous investigations have demonstrated the importance of FRS2 activation for mediating a sustained level of ERK activation. FRS2 is known to associate both with GRB2 and SHP2 to activate RAS. The authors utilized a mutant allele of Fgfr1, lacking the entire juxtamembrane domain (Fgfr1ΔFrs), and an allele of Fgfr2 containing two-point mutations essential for Frs2 binding (Fgfr2LR). When combining three floxed alleles and leaving only one functional allele (Fgfr1ΔFrs or Fgfr2LR) the authors got strikingly different phenotypes. When only the Fgfr1ΔFrs allele was retained, the lens phenotype matched that of deleting both Fgfr1 and Fgfr2. However, when only the Fgfr2LR allele was retained the phenotype was significantly milder, primarily affecting lens fiber cell differentiation, suggesting that something other than FRS2 might be interacting with the juxtamembrane domain to support FGFR signaling in the lens. The authors also deleted Grb2 in the lens and showed that the phenotype was similar to that of the lenses only retaining the Fgfr2LR allele, resulting in a failure of lens fiber cell differentiation and decreased lens cell survival. However, mutating the major tyrosine phosphorylation site of GRB2 did not affect lens development. The author additionally investigated the role of SHP2 lens development by making by either deleting SHP2 or by making mutations in the SHP2 catalytic domain. The deletion of the SHP2 phosphatase activity did not affect lens development as severely as the total loss of SHP2 protein, suggesting a function for SHP2 outside of its catalytic activity. Although the loss of Shc1 alone has only a slight effect on lens size and pERK activation in the lens, the authors showed that the loss of Shc1 exacerbated the lens phenotype in lenses lacking both Frs2 and Shp2. The authors suggest that SHC1 binds to the FGFR juxtamembrane domain allowing for the recruitment of GRB2 independently of FRS2.

Strengths:

(1) The authors used a variety of genetic tools to carefully dissect the essential signals downstream of FGFR signaling during lens development.

(2) The authors made a convincing case that something other than FRS2 binding mediates FGFR signaling in the juxtamembrane domain.

(3) The authors demonstrated that despite the requirement of both the adaptor function and phosphatase activity of SHP2 are required for embryonic survival, neither of these activities is absolutely required for lens development.

(4) The authors provide more information as to why FGFR loss has a phenotype much more severe than the loss of FRS2 alone during lens development.

(5) The authors followed up their work analyzing various signaling molecules in the context of lens development with biochemical analyses of FGF-induced phosphorylation in murine embryonic fibroblasts (MEFs).

(6) In general, this manuscript represents a Herculean effort to dissect FGFR signaling in vivo with biochemical backing with cell culture experiments in vitro.

Weaknesses:

(1) The authors demonstrate that the loss of FGFR1 and FGFR2 can be compensated by a constitutive active KRAS allele in the lens and suggest that FGFRs largely support lens development only by driving ERK activation. However, the authors also saw that lens development was substantially rescued by preventing apoptosis through the deletion of BAK and BAX. To my knowledge, the deletion of BAK and BAX should not independently activate ERK. The authors do not show whether ERK activation is restored in the BAK/BAX deficient lenses. Do the authors suggest the FGFR3 and/or FGFR4 provide sufficient RAS and ERK activation for lens development when apoptosis is suppressed? Alternatively, is it the survival function of FGFR-signaling as much as a direct effect on lens differentiation?

(2) The authors make the argument that deleting all four FGFRs prevented lens induction but that the deletion of only FGFR1 and FGFR2 did not. Part of this argument is the retention of FOXE3 expression, αA-crystallin expression, and PROX1 expression in the FGFR1/2 double mutants. However, in Figure 1E, and Figure 1F, the staining of the double mutant lens tissue with FOXE3, αA-crystallin, and PROX1 is unconvincing. However, the retention of FOXE3 expression in the FGFR1/FGFR2 double mutants was previously demonstrated in Garcia et al 2011. Also, there needs to be an enlargement or inset to demonstrate the retention of pSMAD in the quadruple FGFR mutants in Figure 1D.

(3) Do the authors suggest that GRB2 is required for RAS activation and ultimately ERK activation? If so, do the authors suggest that ERK activation is not required for FGFR-signaling to mediate lens induction? This would follow considering that the GRB2 deficient lenses lack a problem with lens induction.

(4) The increase in p-Shc is only slightly higher in the Cre FGFR1f/f FGFR2r/LR than in the FGFR1f/Δfrs FGFR2f/f. Can the authors provide quantification?

(5) The authors have not shown directly that Shc1 binds to the juxtamembrane region of either Fgfr1 or Fgfr2.

(6) The authors have used the Le-Cre strain for all of their lens deletion experiments. Previous work has documented that the Le-Cre transgene can cause lens defects independent of any floxed alleles in both homozygous and hemizygous states on some genetic backgrounds (Dora et al., 2014 PLoS One 9:e109193 and Lam et al., Human Genomics 2019 13(1):10. Are the controls used in these experiments Le-Cre hemizygotes?

eLife Assessment

This useful study highlights the largely redundant role of the decapping activators Edc3 and Scd6 in orchestrating post-transcriptional programs to modulate metabolic responses to nutrients in yeast. The authors provide solid evidence for their conclusions, employing a variety of mutants in conjunction with a battery of transcriptome-wide analyses. This study could be further strengthened by direct biochemical validation of the functional interactions observed by systems biology approaches.

Reviewer #1 (Public review):

Summary:

mRNA decapping and decay factors play critical roles in post-transcriptionally regulating gene expression. Here, Kumar and colleagues investigate how deleting two yeast decapping enhancer proteins (Edc3 and Scd6), either alone or in tandem, influences the transcriptome. Using RNA-Seq and ribosome profiling, they come to the conclusion that these factors generally act in a redundant fashion, with a mutant lacking both proteins showing an increased abundance of select mRNAs. As these upregulated transcripts are also upregulated in mutants lacking the decapping enzyme, Dcp2, and show no increases in transcription of their cognate genes, they come to the conclusion that this is at the level of mRNA decapping and decay. Their ribosome profiling data also led them to conclude that Scd6 and Edc3 display functional redundancy and cooperativity with Dhh1/Pat1 in repressing the translation of specific transcripts. Finally, as their data suggest that Scd6 and Edc3 repress mRNAs coding for proteins involved in cellular respiration, as well as proteins involved in the catabolism of alternative carbon sources, they go on to show that these decapping activators play a role in repressing oxidative phosphorylation.

Strengths:

Overall, this manuscript is well-written and contains a large amount of high-quality data and analyses. At its core, it helps to shed light on the overlapping roles of Edc3 and Scd6 in sculpting the yeast transcriptome.

Weaknesses:

(1) While the data presented makes conclusions about mRNA stability based on corresponding ChIP-Seq analyses and analyzing other mutants (e.g. Dcp2 knockout), at no point is mRNA stability actually ever directly assessed. This direct assessment, even for select transcripts, would further strengthen their conclusions.

(2) Scd6 and Edc3 show a high level of functional redundancy, as demonstrated by the double mutant. As these proteins form complexes with other decapping factors/activators, I'm curious if depleting both proteins in the double mutant destabilizes any of these other factors. Have the authors ever assessed the levels of other key decapping factors in the double mutants (i.e. Dhh1, Pat1, Dcp2...etc)? I wonder if depleting both proteins leads to a general destabilization of key complexes. It would also be interesting to see if depleting Edc3 or Scd6 leads to a concomitant increase in the other protein as a compensatory mechanism.

(3) While not essential, it would be interesting if the authors carried out add-back experiments to determine which domain within Scd6/Edce3 plays a critical role in enforcing the regulation that they see. Their double mutant now puts them in a perfect position to carry out such experiments.

Reviewer #2 (Public review):

Summary:

This manuscript by Kumar and Zhang presents compelling evidence that Edc3 and Scd6 decapping activators present a high degree of redundancy that can only be overcome by a double mutant. In addition, the authors provide strong evidence of these complexes in regulating starvation-induced pathways as evidenced by measurements of mitochondrial membrane potential, metabolomics, and analysis of the flux of Krebs cycle intermediates.

Strengths:

Kumar and Zhang et al provide multiple sources of evidence of the direct mechanism of Edc3 and Scd6 function, by using and comparing different approaches such as mRNA-seq, ribosome occupancies, and translational efficiencies. By extensive analysis, the authors show that this complex can also regulate genes outside the Environmental Stress Response (non-iESR), which are significantly up-regulated in all three mutants. Remarkably, the gene ontology analysis of these non-iESR genes identifies enrichment for mitochondrial proteins that are implicated in the Krebs cycle. Overall, this study adds novel mechanistic insight into how nutrients control gene expression by modulating decapping and translational repression.

Weaknesses:

The authors show very nicely in Figure S1A that growth phenotypes from scd6Δedc3∆ can be rescued by transformation of EDC3 (pLfz614-7) or SCD6 (pLfz615-5). The manuscript might benefit from using these rescue strategies in the analysis performed (e.g. RNA-seq, ribosome occupancies, and translational efficiencies). Also, these rescue assays could provide a good platform to further characterise the protein-protein interactions between Edc3, Scd6, and Dhh1.

Reviewer #3 (Public review):

Summary:

In this paper, Kumar et al aimed to investigate the roles of two decapping activators, Edc3 and Scd6, in regulating mRNA decay and translation in yeast. Previous research suggested limited individual roles for these proteins in mRNA decay. The authors hypothesized that Edc3 and Scd6 act redundantly and explored how these proteins interact with two other factors involved in mRNA decapping and translational repression, with Dhh1 and Pat1, particularly in response to nutrient availability. The study aims to identify mRNAs targeted by these proteins for degradation and translation repression and assess their impact on metabolic pathways including mitochondrial function and alternative carbon source utilization.

Strengths:

The paper has several strengths including the comprehensive approach taken by the authors using multiple experimental techniques (RNA-seq, ribosome profiling, Western blotting, TMT-MS, and polysome profiling) to examine both mRNA abundance and translation efficiency, thereby providing multiple lines of evidence to support their conclusions. The authors demonstrate clear redundancy of the factors by using single and double mutants for Edc3 and Scd6 and their global approach enables an understanding of these factors' roles across the yeast transcriptome. The work connects post-transcriptional processes to nutrient-dependent gene regulation, providing insights into how cells adapt to changes in their environment. The authors demonstrate the redundant roles of Edc3 and Scd6 in mRNA decapping and translation repression. Their RNA-seq and ribosome profiling results convincingly show that many mRNAs are derepressed only in the double mutants, confirming their hypothesis of redundancy. Furthermore, the functional cooperation between Edc3/Scd6 and Dhh1/Pat1 in regulating specific metabolic pathways, like mitochondrial function and carbon source utilization, is supported by the data. The results therefore support the authors' conclusions that these decapping factors work together to fine-tune gene expression in response to nutrient availability.

Weaknesses:

The limitations of the study include the use of indirect evidence to support claims that Edc3 and Scd6 recruit Dhh1 to the Dcp2 complex, which is inferred from correlations in mRNA abundance and ribosome profiling data rather than direct biochemical evidence. Also, there is limited exploration of other signals as the study is focused on glucose availability, and it is unclear whether the findings would apply broadly across different environmental stresses or metabolic pathways.

Nonetheless, the study provides new insights into how mRNA decapping and degradation are tightly linked to metabolic regulation and nutrient responses in yeast. The RNA-seq and ribosome profiling datasets are valuable resources for the scientific community, providing quantitative information on the role of decapping activators in mRNA stability and translation control.

eLife Assessment

By exploring the conservation and functional diversity of RIPK3 and related RHIM-containing proteins across vertebrates, this important work sheds light on the evolutionary dynamics of these key immune pathways. The evidence supporting the claims is overall solid, although thorough documentation of the evolutionary analysis (e.g. in the 'Phylogenetic analysis' section), and additional work beyond human HEK293 cells, would strengthen the functional validation in support of the study's conclusions.

Reviewer #1 (Public review):

The manuscript titled "Evolutionary and Functional Analyses Reveal a Role for the RHIM in Tuning RIPK3 Activity Across Vertebrates" by Fay et al. explores the function of RIPK gene family members across a wide range of vertebrate and invertebrate species through a combination of phylogenomics and functional studies. By overexpressing these genes in human cell lines, the authors examine their capacity to activate NF-κB and induce cell death. The methods employed are appropriate, with a thorough analysis of gene loss, positive selection, and functionality. While the study is well-executed and comprehensive, its broader relevance remains limited, appealing mainly to specialists in this specific field of research. It misses the opportunity to extract broader insights that could extend the understanding of these genes beyond evolutionary conservation, particularly by employing evolutionary approaches to explore more generalizable functions.

Major comments:

The main issue I encounter is distinguishing between what is novel in this study and what has been previously demonstrated. What new insights have been gained here that are of broader relevance? The discussion, which would be a good place to do so, is very speculative and has little to do with the actual results. Throughout the manuscript, there is little explanation of the study's importance beyond the fact that it was possible to conduct it. Is the evolutionary analysis being used to advance our understanding of gene function, or is the focus merely on how these genes behave across different species? The former would be exciting, while the latter feels less impactful.

Reviewer #2 (Public review):

Summary:

By combining bioinformatical and experimental approaches, the authors address the question of why several vertebrate lineages lack specific genes of the necroptosis pathway or those that regulate the interplay between apoptosis and necroptosis. The lack of such genes was already known from previous publications, but the current manuscript provides a more in-depth analysis and also uses experiments in human cells to address the question of the functionality of the remaining genes and pathways. A particular focus is placed on RIPK3/RIPK1 and their dual roles in inducing NFkB and/or necroptosis.

Strengths:

The well-documented bioinformatical analyses provide a comprehensive data basis of the presence/absence of RIP-kinases, other RHIM proteins, apoptosis signaling proteins (FADD, CASP8, CASP10), and some other genes involved in these pathways. Several of these genes are known to be missing in certain animal lineages, which raises the question of why their canonical binding partners are present in these species. By expressing several such proteins (both wildtype and mutants destroying particular interaction regions) in human cells, the authors succeed in establishing a general role of RIPK3 and RIPK1 in NFkB activation. This function appears to be better conserved and more universal than the necroptotic function of the RHIM proteins. The authors also scrutinize the importance of the kinase function and RHIM integrity for these separate functionalities.

Weaknesses:

A major weakness of the presented study is the experimental restriction to human HEK293 cells. There are several situations where the functionality of proteins from distant organisms (like lampreys or even mussels) in human cells is not necessarily indicative of their function in the native context. In some cases, these problems are addressed by co-expressing potential interaction partners, but not all of these experiments are really informative.

A second weakness is that the manuscript addresses some interesting effects only superficially. By using host cells that are deleted for certain signaling components, a more focussed hypothesis could have been tested.

Thus, while the aim of the study is mostly met, it could have been a bit more ambitious. The limited conclusions drawn by the authors are supported by convincing evidence. I have no doubts that this study will be very useful for future studies addressing the evolution of necroptosis and its regulation by NFkB and apoptosis.

Reviewer #3 (Public review):

This important study provides insights into the functional diversification of RIP family kinase proteins in vertebrate animals. The provided results, which combine bioinformatic and experimental analyses, will be of interest to specialists in both immunology and evolutionary biology. However, the computational part of the methodology is insufficiently covered in the paper and the experimental results would benefit from including data for additional species.

(1) In the Methods section concerning gene loss analysis, the authors refer to the 'Phylogenetic analysis' section for details of RIPK sequence acquisition and alignment procedure. This section is missing from the manuscript as provided. In its absence, it is hard for the reviewer to provide relevant comments on gene presence/absence analysis.

(2) In the same section, the authors state that gene sequences were filtered and grouped based on the initial gene tree pattern (lines 448-449). How exactly did the authors filter the non-RIP kinases and other irrelevant homologs from the gene trees? Did they consider the reciprocal best (BLAST) hit approach or similar approaches for orthology inference? Did they also encounter potential pseudogenes of genes marked as missing in Figure 1C? Will the gene trees mentioned be available as supplementary files?

(3) The authors state the presence of additional RIPK2 paralog in non-therian vertebrates. The ramifications of this paralog loss in therians are not discussed in the text, although RIPK2 is also involved in NF-kB activation. In addition, the RIPK2B gene loss pattern is shunned from Figure 1C to Supplementary Figure 4, despite posing comparable interest to the reader.

(4) The authors present evidence for (repeated) positive selection in both RIPK1 and RIPK3 in bats; however, neither bat RIPK1/3 orthologs nor bat-specific RHIM tetrad variants (IQFG, IQLG) are considered in the experimental part of the work.

(5) The authors present gene presence/absence patterns for zebra mussels as an outgroup of vertebrate species analyzed. From the evolutionary perspective, adding results for a closer invertebrate group, such as lancelets, tunicates, or echinoderms, would be beneficial for reconstructing the evolutionary progression of RIPK-mediated immune functions in animals.

(6) In the broader sense, the list of non-mammalian species included in the study is not explained or substantiated in the text. What was the rationale behind selecting lizards, turtles, and lampreys for experimental assays? Why was turtle RIPK3 but not turtle RIPK1CT protein used for functional tests? Which results do the authors expect to observe if amphibian or teleost RIPK1/3 are included in the analysis, especially those with divergent tetrad variants?

(7) For lamprey RIPK3, the observed NF-kB activity levels still remain lower than those of mammalian and reptilian orthologs even after catalytic tetrad modification. In the same way, switching human RIPK3 catalytic tetrad to that of lamprey does not result in NF-kB activation. What are the potential reasons for the observed difference? Does it mean that lamprey's RIPK3 functions in NF-kB activation are, at least partially, delegated to RIPK1?

(8) In lines 386-388, the authors state that 'only non-mammalian RIPK1CT proteins required the RHIM for maximal NF-kB activation', which is corroborated by results in Figure 4B. The authors further associate this finding with a lack of ZBP1 in the respective species (lines 388-389). However, non-squamate reptiles seem to retain ZBP1, as suggested by Supplementary Table 1. Given that, do the authors expect to observe RHIM-independent (maximal) NF-kB activation in turtles and crocodilians or respective RIPK1CT-transfected cells?

eLife Assessment

This important study reports numerous attempts to replicate reports on transgenerational inheritance of a learned behavior - pathogen avoidance - in C. elegans. While the authors observe parental effects that are limited to a single generation (also called intergenerational inheritance), the authors failed to find any evidence for transmission over multiple generations, or transgenerational inheritance. The experiments presented are meticulously described, making for compelling evidence that in the authors' hands transgenerational inheritance cannot be observed. There remains the possibility that subtle differences in culture conditions or lab environment explain the failure to reproduce previous observations, with updates to the paper having further reduced the probability that this applies here. And even if this were the case, it would imply that the original results were not very robust. Given the prominence of the original reports of transgenerational inheritance, the present study is of broad interest to anyone studying genetics, epigenetics, or learned behavior.

Reviewer #1 (Public review):

Summary:

The authors report an inability to reproduce a transgenerational memory of avoidance of the pathogen PA14 in C. elegans. Instead, the authors demonstrate intergenerational inheritance for a single F1 generation, in embryos of mothers exposed to OP50 and PA14, where embryos isolated from these mothers by bleaching are capable of remembering to avoid PA14 in a manner that is dependent on systemic RNAi proteins sid-1 and sid-2. This could reflect systemic sRNAs generated by neuronal daf-7 signaling that are transmitted to F1 embryos. The authors note that transgenerational memory of PA14 was reported by the Murphy group at Princeton, but that environmental or strain variation (worms or bacteria) might explain the single generation of inheritance observed at Harvard. The Hunter group tried different bacterial growth conditions and different worm growth temperatures for independent PA14 strains, which they show to be strongly pathogenic. However, the authors could not reproduce a transgenerational effect at Harvard. This paper honestly alters expectations and indicates that the model that avoidance of PA14 is remembered for multiple generations is not robust enough to be replicated in all laboratories.<br /> Overall, this paper that demonstrates that one model for transgenerational inheritance in C. elegans not robust. The author do demonstrate an avoidance memory for F1 embryos that could be a maternal effect, and the authors confirm that this is mediated by a systemic small RNA response. There are several points in the manuscript where a more positive tone might be helpful.

Strengths:

The authors note that the high copy number daf-7::GFP transgene used by the Murphy group displayed variable expression and evidence for somatic silencing or transgene breakdown in the Hunter lab, as confirmed by the Murphy group. The authors nicely use single copy daf-7::GFP to show that neuronal daf-7::GFP is elevated in F1 but not F2 progeny with regards to memory of PA14 avoidance, speaking to an intergenerational phenotype.

The authors nicely confirm that sid-1 and sid-2 are generally required for intergenerational avoidance of F1 embryos of moms exposed to PA14. However, these small RNA proteins did not affect daf-7::GFP elevation in the F1 progeny. This result is unexpected given previous reports that daf-7::GFP is not elevated in F1 progeny of sid mutants.

The authors studied antisense small RNAs that change in Murphy data sets, identifying 116 mRNAs that might be regulated by sRNAs in response to PA14. The authors show that the maco-1 gene, putatively targeted by piRNAs according to the Kaletsky 2020 paper, displays few siRNAs that change in response to PA14. The authors conclude that the P11 ncRNA of PA14, which was proposed to promote interkingdom RNA communication by the Murphy group, may not affect maco-1 expression in C. elegans, although they did not formally demonstrate this. The authors define 8 genes based on their analysis of sRNAs and mRNAs that might promote resistance to PA14, but they do not further characterize these genes' role in pathogen avoidance. Others might wish to consider following up on these genes and their possible relationship with P11.

Weaknesses:

This very thorough and interesting manuscript is at times pugnacious.

Please explain more clearly what is High Growth media for E. coli in the text and methods, conveying why it was used by the Murphy lab, and if Normal Growth or High Growth is better for intergenerational heritability assays.

Comments on revisions:

The authors have done a reasonable job cordially revising this manuscript, and the authors have addressed most reviewer concerns. It is likely that the P11 gene was in some of the PA14 Pseudomonas strains tested, as one was kindly provided by the Murphy group

Reviewer #2 (Public review):

This paper examines the reproducibility of results reported by the Murphy lab regarding transgenerational inheritance of a learned avoidance behavior in C. elegans. It has been well established by multiple labs that worms can learn to avoid the pathogen pseudomonas aeruginosa (PA14) after a single exposure. The Murphy lab has reported that learned avoidance is transmittable to 4 generations and dependent on a small RNA expressed by PA14 that elicits the transgenerational silencing of a gene in C. elegans. The Hunter lab now reports that although they can reproduce inheritance of the learned behavior by the first generation (F1), they cannot reproduce inheritance in subsequent generations.

This is an important study that will be useful for the community. Although they fail to identify a "smoking gun", the study examine several possible sources for the discrepancy, and their findings will be useful to others interested in using these assays. The preference assay appears to work in their hands in as much as they are able to detect the learned behavior in the P0 and F1 generations, suggesting that the failure to reproduce the transgenerational effect is not due to trivial mistakes in the protocol. The authors provide a full protocol and highlight key deviations from the Murphy lab protocol. The authors provide good evidence that no single protocol modification was sufficient on its own to explain the divergent results. It remains possible that protocol differences affected the assay cumulatively or that other uncontrolled factors were responsible. Nevertheless, the authors provide good evidence that the trans-generational effect reported by the Murphy lab lacks experimental robustness, calling into question its ecological relevance in the wild.

Reviewer #3 (Public review):

Summary:

It has been previously reported in many high-profile papers, that C. elegans can learn to avoid pathogens. Moreover, this learned pathogen avoidance can be passed on to future generations - up to the F5 generation in some reports. In this paper, Gainey et al. set out to replicate these findings. They successfully replicated pathogen avoidance in the exposed animals, as well as a strong increase in daf-7 expression in ASI neurons in F1 animals, as determined by a daf-7::GFP reporter construct. However, they failed to see strong evidence for pathogen avoidance or daf-7 overexpression in the F2 generation. The failure of replication is the major focus of this work.<br /> Given their failure to replicate these findings, the authors embark on a thorough test of various experimental confounders that may have impacted their results. They also re-analyze the small RNA sequencing and mRNA sequencing data from one of the previously published papers and draw some new conclusions, extending this analysis.

Strengths:

• The authors provide a thorough description of their methods, and a marked-up version of a published protocol that describes how they adapted the protocol to their lab conditions. It should be easy to replicate the experiments.<br /> • The authors test source of bacteria, growth temperature (of both C. elegans and bacteria), and light/dark husbandry conditions. They also supply all their raw data, so that sample size for each testing plate can be easily seen (in the supplementary data). None of these variations appears to have a measurable effect on pathogen avoidance in the F2 generation, with all but one of the experiments failing to exhibit learned pathogen avoidance.<br /> • The small RNA seq and mRNA seq analysis is well performed and extends the results shown in the original paper. The original paper did not give many details of the small RNA analysis, which was an oversight. Although not a major focus of this paper, it is a worthwhile extension on the previous work.<br /> • It is rare that negative results such as these are accessible. Although the authors were unable to determine the reason that their results differ from those previously published, it is important to document these attempts in detail, as has been done here. Behavioral assays are notoriously difficult to perform and public discourse around these attempts may give clarity to the difficulties faced by a controversial field.

Weaknesses:

• Although the "standard" conditions have been tested over multiple biological replicates, many of the potential confounders that may have altered the results have been tested only once or twice. For example, changing the incubation temperature to 25{degree sign}C was tested in only two biological replicates (Exp 5.1 and 5.2) - and one of these experiments actually resulted in apparent pathogen avoidance inheritance in the F2 generation (but not in the F1). An alternative pathogen source was tested in only one biological replicate (Exp 3). Given the variability observed in the F2 generation, increasing biological replicates would have added to the strengths of the report.<br /> • A key difference between the methods used here and those published previously, is an increase in the age of the animals used for training - from mostly L4 to mostly young adults. I was unable to find a clear example of an experiment when these two conditions were compared, although the authors state that it made no difference to their results.<br /> • The original paper reports a transgenerational avoidance effect up to the F5 generation. Although in this work the authors failed to see avoidance in the F2 generation, it would have been prudent to extend their tests for more generations in at least a couple of their experiments to ensure that the F2 generation was not an aberration (although this reviewer acknowledges that this seems unlikely to be the case).

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors report an inability to reproduce a transgenerational memory of avoidance of the pathogen PA14 in C. elegans. Instead, the authors demonstrate intergenerational inheritance for a single F1 generation, in embryos of mothers exposed to OP50 and PA14, where embryos isolated from these mothers by bleaching are capable of remembering to avoid PA14 in a manner that is dependent on systemic RNAi proteins sid-1 and sid-2. This could reflect systemic sRNAs generated by neuronal daf-7 signaling that are transmitted to F1 embryos. The authors note that transgenerational memory of PA14 was reported by the Murphy group at Princeton, but that environmental or strain variation (worms or bacteria) might explain the single generation of inheritance observed at Harvard. The Hunter group tried different bacterial growth conditions and different worm growth temperatures for independent PA14 strains, which they showed to be strongly pathogenic. However, the authors could not reproduce a transgenerational effect at Harvard. This important data will allow members of the scientific community to focus on the robust and reproducible inheritance of PA14 avoidance transmitted to F1 embryos of mothers exposed to PA14, which the authors demonstrate depends on small RNAs in a manner that is downstream of or in parallel to daf-7. This paper honestly and importantly alters expectations and questions the model that avoidance of PA14 is mediated by a bacterial ncRNA whose siRNAs target a C. elegans gene. Instead, endogenous C. elegans sRNAs that affect pathogen response may be the culprit that explains sRNA-mediated avoidance.

Overall, this is an important paper that demonstrates that one model for transgenerational inheritance in C. elegans is not reproducible. This is important because it is not clear how many of the reported models of transgenerational inheritance reported in C. elegans are reproducible. The authors do demonstrate a memory for F1 embryos that could be a maternal effect, and the authors confirm that this is mediated by a systemic small RNA response. There are several points in the manuscript where a more positive tone might be helpful.

We would like to correct the statement made in the second to last sentence. The demonstration of an F1 response to PA14 was first reported by Moore et al., (2019) and then by Pereira et al., (2020) using a different behavioral assay. We merely confirmed these results in our hands, and confirmed the observation, first reported by Kaletsky et al., (2020), that sid-1 and sid-2 are required for this F1 response; although we did find that sid-1 and sid-2 are not required for the PA14-induced increase in daf-7p::gfp expression in ASI neurons in the F1 progeny of trained adults, which had not been addressed in the published work.

Yes, the intergenerational F1 response could be a maternal effect, but the in utero F1 embryos and their precursor germ cells were directly exposed to PA14 metabolites and toxins (non-maternal effect) as well as any parental response, whether mediated by small RNAs, prions, hormones, or other unknown information carriers. While the F1 aversion response does require sid-1 and sid-2, we would not presume that the substrate is therefore an RNA molecule, particularly because the systemic RNAi response supported by sid-1 and sid-2 is via long double-stranded RNA. To date, no evidence suggests that either protein transports small RNAs, particularly single-stranded RNAs.

Strengths:

The authors note that the high copy number daf-7::GFP transgene used by the Murphy group displayed variable expression and evidence for somatic silencing or transgene breakdown in the Hunter lab, as confirmed by the Murphy group. The authors nicely use single copy daf-7::GFP to show that neuronal daf-7::GFP is elevated in F1 but not F2 progeny with regards to the memory of PA14 avoidance, speaking to an intergenerational phenotype.

The authors nicely confirm that sid-1 and sid-2 are generally required for intergenerational avoidance of F1 embryos of moms exposed to PA14. However, these small RNA proteins did not affect daf-7::GFP elevation in the F1 progeny. This result is unexpected given previous reports that single copy daf-7::GFP is not elevated in F1 progeny of sid mutants. Because the Murphy group reported that daf-7 mutation abolishes avoidance for F1 progeny, this means that the sid genes function downstream of daf-7 or in parallel, rather than upstream as previously suggested.

The published report (Moore et al., 2019) shows only multicopy daf-7p::gfp results and does not address the daf-7p::gfp response in sid-1 or sid-2 mutants. Thus, our discovery that systemic RNAi, exogenous RNAi, and heritable RNAi mutants don’t disrupt elevated daf-7p::gfp in ASI neurons in the F1 progeny of PA14 trained P0’s is only unexpected with respect to the published models (Moore et al., 2019, Kaletsky et al., 2020).

The authors studied antisense small RNAs that change in Murphy data sets, identifying 116 mRNAs that might be regulated by sRNAs in response to PA14. Importantly, the authors show that the maco-1 gene, putatively targeted by piRNAs according to the Kaletsky 2020 paper, displays few siRNAs that change in response to PA14. The authors conclude that the P11 ncRNA of PA14, which was proposed to promote interkingdom RNA communication by the Murphy group, is unlikely to affect maco-1 expression by generating sRNAs that target maco-1 in C. elegans. The authors define 8 genes based on their analysis of sRNAs and mRNAs that might promote resistance to PA14, but they do not further characterize these genes' role in pathogen avoidance. The Murphy group might wish to consider following up on these genes and their possible relationship with P11.

Weaknesses:

This very thorough and interesting manuscript is at times pugnacious.

We reiterate that we never claimed that Moore et al., (2019) did not obtain their reported results. We simply stated that we could not replicate their results using the published methods and then failed in our search to identify variable(s) that might account for our results. In revising the manuscript, we have striven to make clear, unmuddied statements of facts and state that future investigations may provide independent evidence that supports the original claims and explains our divergent results.

Please explain more clearly what is High Growth media for E. coli in the text and methods, conveying why it was used by the Murphy lab, and if Normal Growth or High Growth is better for intergenerational heritability assays.

We added the standard recipes and the following explanations in the methods section to the revised text.

“NG plates minimally support OP50 growth, resulting in a thin lawn that facilitates visualization of larvae and embryos. HG plates (8X more peptone) support much higher OP50 growth, resulting in a thick bacterial lawn that supports larger worm populations.”

We have also included the following text in our presentation and discussion of the effects of growth conditions on worm choice in PA14 vs OP50 choice assays.

“Furthermore, because OP50 pathogenicity is enhanced by increased E. coli nutritive conditions (Garsin et al., 2003, Shi et al., 2006), the growth of F1-F4 progeny on High Growth (HG) plates (Moore et al., 2019; 2021b), which contain 8X more peptone than NG plates and therefore support much higher OP50 growth levels, immediately prior to the F1-F4 choice assays may further contribute to OP50 aversion among the control animals.”

We don’t know enough to claim that HG or NG media is better than the other for intergenerational assays, but they are different. Thus, switching between the two in a multigenerational experiment likely introduces unknown variability.

Reviewer #2 (Public Review):

This paper examines the reproducibility of results reported by the Murphy lab regarding transgenerational inheritance of a learned avoidance behavior in C. elegans. It has been well established by multiple labs that worms can learn to avoid the pathogen pseudomonas aeruginosa (PA14) after a single exposure. The Murphy lab has reported that learned avoidance is transmittable to 4 generations and dependent on a small RNA expressed by PA14 that elicits the transgenerational silencing of a gene in C. elegans. The Hunter lab now reports that although they can reproduce inheritance of the learned behavior by the first generation (F1), they cannot reproduce inheritance in subsequent generations.

This is an important study that will be useful for the community. Although they fail to identify a "smoking gun", the study examines several possible sources for the discrepancy, and their findings will be useful to others interested in using these assays. The preference assay appears to work in their hands in as much as they are able to detect the learned behavior in the P0 and F1 generations, suggesting that the failure to reproduce the transgenerational effect is not due to trivial mistakes in the protocol. An obvious reason, however, to account for the differing results is that the culture conditions used by the authors are not permissive for the expression of the small RNA by PA14 that the MUrphy lab identified as required for transgenerational inheritance. It would seem prudent for the authors to determine whether this small RNA is present in their cultures, or at least acknowledge this possibility.

We thank the reviewer for raising this issue and have added the following statement to this effect in the revised manuscript.

“We note that previous bacterial RNA sequence analysis identified a small non-coding RNA called P11 whose expression correlates with bacterial growth conditions that induce heritable avoidance (Kaletsky et al., 2020). Critically, C. elegans trained on a PA14 ΔP11 strain (which lacks this small RNA) still learn to avoid PA14, but their F1 and F2-F4 progeny fail to show an intergenerational or transgenerational response (Figure 3L in Kaletsky et al., 2020). The fact that we observed an intergenerational (F1) avoidance response is evidence that our PA14 growth conditions induce P11 expression.”

We believe that this addresses the concern raised here.

The authors should also note that their protocol was significantly different from the Murphy protocol (see comments below) and therefore it remains possible that protocol differences cumulatively account for the different results.

As suggested below, we have added to the supplemental documents the protocol we followed for the aversion assay. In our view, this document shows that our adjustments to the core protocol were minor. Furthermore, where possible, these adjustments were explicitly tested in side-by-side experiments for both the aversion assay and the daf-7p::gfp expression assay and presented in the manuscript.

To discover the source(s) of discrepancy between our results and the published results we subsequently introduced variations to this core protocol to exclude likely variables (worm and bacteria growth temperatures, assay conditions, worm handling methods, bacterial culture and storage conditions, and some minor developmental timing issues). Again, where possible, the effect of variations was tested in side-by-side experiments for both the aversion assay and the daf-7p::gfp expression assay and were presented in or have now been added to the manuscript.

It remains possible that we misunderstood the published Murphy lab protocols, but we were highly motivated to replicate the results so we could use these assays to investigate the reported RNAi-pathway dependent steps, thus we read every published version with extreme care.

Reviewer #3 (Public Review):

Summary:

It has been previously reported in many high-profile papers, that C. elegans can learn to avoid pathogens. Moreover, this learned pathogen avoidance can be passed on to future generations - up to the F5 generation in some reports. In this paper, Gainey et al. set out to replicate these findings. They successfully replicated pathogen avoidance in the exposed animals, as well as a strong increase in daf-7 expression in ASI neurons in F1 animals, as determined by a daf-7::GFP reporter construct. However, they failed to see strong evidence for pathogen avoidance or daf-7 overexpression in the F2 generation. The failure of replication is the major focus of this work.

Given their failure to replicate these findings, the authors embark on a thorough test of various experimental confounders that may have impacted their results. They also re-analyze the small RNA sequencing and mRNA sequencing data from one of the previously published papers and draw some new conclusions, extending this analysis.

Strengths:

(1) The authors provide a thorough description of their methods, and a marked-up version of a published protocol that describes how they adapted the protocol to their lab conditions. It should be easy to replicate the experiments.

As noted above in response to a suggestion by reviewer #2, we have replaced the annotated published protocol with the protocol that we followed. This will aid other groups' attempts to replicate our experimental conditions.

(2) The authors test the source of bacteria, growth temperature (of both C. elegans and bacteria), and light/dark husbandry conditions. They also supply all their raw data, so that the sample size for each testing plate can be easily seen (in the supplementary data). None of these variations appears to have a measurable effect on pathogen avoidance in the F2 generation, with all but one of the experiments failing to exhibit learned pathogen avoidance.

We note that the parallel analysis of daf-7p::gfp expression in ASI neurons was also tested for several of these conditions and also failed to replicate the published findings.

(3) The small RNA seq and mRNA seq analysis is well performed and extends the results shown in the original paper. The original paper did not give many details of the small RNA analysis, which was an oversight. Although not a major focus of this paper, it is a worthwhile extension of the previous work.

(4) It is rare that negative results such as these are accessible. Although the authors were unable to determine the reason that their results differ from those previously published, it is important to document these attempts in detail, as has been done here. Behavioral assays are notoriously difficult to perform and public discourse around these attempts may give clarity to the difficulties faced by a controversial field.

Thank you for your support. Choosing to pursue publication of these negative results was not an easy decision, and we thank members of the community for their support and encouragement.

Weaknesses:

(1) Although the "standard" conditions have been tested over multiple biological replicates, many of the potential confounders that may have altered the results have been tested only once or twice. For example, changing the incubation temperature to 25{degree sign}C was tested in only two biological replicates (Exp 5.1 and 5.2) - and one of these experiments actually resulted in apparent pathogen avoidance inheritance in the F2 generation (but not in the F1). An alternative pathogen source was tested in only one biological replicate (Exp 3). Given the variability observed in the F2 generation, increasing biological replicates would have added to the strengths of the report.

We agree that our study was not exhaustive in our exploration of variables that might be interfering with our ability to detect F2 avoidance. We also note that some of these variables also failed (with many more independent experiments) to induce elevated daf-7p::gfp expression in ASI neurons in F2 progeny. Our goal was not to show that variation in some growth or assay condition would generate reproducible negative results, but the exploration was designed to tweak conditions to enable detection of a robust F2 response. Given the strength of the data presented in Moore et al., (2019) we expected that adjustment of the problematic variable would produce positive results apparent in a single replicate, which could then be followed up. If we had succeeded, then we would have documented the conditions that enabled robust F2 inheritance and would have explored molecular mechanisms that support this important but mysterious process.

(2) A key difference between the methods used here and those published previously, is an increase in the age of the animals used for training - from mostly L4 to mostly young adults. I was unable to find a clear example of an experiment when these two conditions were compared, although the authors state that it made no difference to their results.

We can state firmly that the apparent time delay did not affect P0 learned avoidance (new Figure S1) or, as documented in Table S1, daf-7p::gfp expression in ASI neurons. In our experience, training mostly L4’s on PA14 frequently failed to produce sufficient F1 embryos for both F1 avoidance assays or daf-7p::gfp measurements in ASI neurons and collection of F2 progeny. Indeed, in early attempts to detect heritable PA14 aversion, trained P0 and F1 progeny were not assayed in order to obtain sufficient F2’s for a choice assay. These animals failed to display aversion, but without evidence of successful P0 training or an F1 intergenerational response this was deemed a non-fruitful trouble-shooting approach. We have added supplemental Figure S1 which presents P0 choice assay results from experiments using younger trained animals that failed to produce sufficient F1’s to continue the inheritance experiments.

The different timing at the start of training between the two protocols may reflect the age of the recovered bleached P0 embryos. It is reasonable to assume that bleaching day 1 adults vs day 2 or 3 adults from the P-1 population could shift the average age of recovered P0 embryos by several hours. The Murphy protocol only states that P0 embryos were obtained by bleaching healthy adults. Regardless, if the hypothesis entertained here is true, that a several hour difference in larval/adult age during 24 hours of training affects F2 inheritance of learned aversion but does not affect P0 learned avoidance, then we would argue that this paradigm for heritable learned avoidance, as described in Moore et al., (2019, 2021), is not sufficiently robust for mechanistic investigations.

(3) The original paper reports a transgenerational avoidance effect up to the F5 generation. Although in this work the authors failed to see avoidance in the F2 generation, it would have been prudent to extend their tests for more generations in at least a couple of their experiments to ensure that the F2 generation was not an aberration (although this reviewer acknowledges that this seems unlikely to be the case).

We would point out that we also failed to robustly replicate the F2 response in the daf-7p::gfp expression assays. An F2-specific aberration that affects two different assays seems quite unlikely, and it remains unclear how we would interpret a positive result in F3 and F4 generations without a positive result in the F2 generation. Were we to further extend these investigations, we believe that exploration of additional culture conditions would warrant higher priority than extension of our results to the F3 and F4 generations.

Reviewing Editor Comments:

The reviewers' suggestions for improving the manuscript were mostly minor, to change the wording in some places and to add some more explanation regarding the methods.

What should be highlighted in the section on OP50 growth conditions is that the initial preference for PA14 in the Murphy lab has also been observed by multiple other labs (Bargmann, Kim, Zhang, Abbalay). The fact that this preference was not observed by the Hunter lab is one of several indicators of subtle differences in the environment that might add up to explain the differences in results.

We agree that subtle known and unknown differences in OP50 and PA14 culture conditions can have measurable effects on the detection of PA14 attraction/aversion relative to OP50 attraction/aversion that could obscure or create the appearance of heritable effects between generations. We have added (see below) to the text a fuller description of the variability in the initial or naive preference observed in different laboratories using similar or variant 2-choice assays and culture conditions. It is worth emphasizing that direct comparison of the OP50 growth conditions specified in Moore et al., (2021) frequently revealed a much larger effect on the naïve choice index than is reported between labs (Figure 4).  

“Naïve (OP50 grown) worms often show a bias towards PA14 in choice assays (Zhang et al., 2005; Ha et al., 2010; Moore et al., 2019; Pereira et al., 2020; Lalsiamthara and Aballay, 2022). This response, rather than representing an innate attraction to PA14, likely reflects the context of the worm's recent growth on OP50, a mild C. elegans pathogen (Garigan et al., 2002; Garsin et al., 2003; Shi et al., 2006). Thus, the naïve worms presented with a choice between a recently experienced mild pathogen (OP50) and a novel food choice (PA14) initially choose the novel food instead of the known mild pathogen (OP50 aversion).

In line with our results, some other groups have also reported higher naïve choice index scores (Lee et al., 2017). This variability in naïve choice may reflect differences in growth conditions of either the OP50 or PA14 bacteria. In addition, we note that among the studies that show naïve worm attraction to Pseudomonas (OP50 aversion) there are extensive methodological differences from the methods in Moore et al., (2019; 2021b), including differences in bacterial growth temperature, incubation time, whether the bacteria is diluted or concentrated prior to placement on the choice plates, the concentration of peptone in the choice plates, the length of the choice assay, and the inclusion of sodium azide in the choice assays (Zhang et al., 2005; Ha et al., 2010; Moore et al., 2019; Pereira et al 2020; Lalsiamthara and Aballay, 2022). Thus, the cause of the variability across published reports is not clear.”

Overall, an emphasis on the absence of robustness of the reported results, rather than failure to reproduce them (which can always have many reasons), is appropriate.

We agree that an emphasis on robustness is appropriate and have modified the text throughout the manuscript to shift the emphasis to absence of robustness. This includes a change to the manuscript title, which is now,

“Reported transgenerational responses to Pseudomonas aeruginosa in C. elegans are not robust”

A significant experimental addition would be some attempts to determine whether the bacterial PA14 pathogen in the authors' lab produces the P11 small RNA, which has been proposed to have a causal role in initiating the previously reported transgenerational inheritance.

We acknowledge in the revised manuscript that a subsequent publication (Kaletsky et al., 2020) identified a correlation between PA14 training conditions that induced transgenerational memory and the expression of P11, a P. aeruginosa small non-coding RNA (see our response above to Reviewer #2’s similar query). While testing for the presence of P11 in Harvard culture conditions would be an important assay in any study whose purpose was to investigate the proposed P11-mediated mechanism underlying the transgenerational responses reported by the Murphy Lab, our goal was rather to replicate the robust transgenerational (F2) responses to PA14 training and then to investigate in more detail how sid-1 and sid-2 contribute to transgenerational epigenetic inheritance. Neither sid-1 nor sid-2 are predicted to transport small RNAs or single-stranded RNAs, thus testing for the presence of P11 is less relevant to our goals. Regardless, we note that Figure 3L in Kaletsky et al., (2020) showed that PA14 ΔP11 bacteria failed to induce an F1 avoidance response. Thus, the fact that we observed F1 avoidance implies that our culture conditions successfully induced P11 expression.

Reviewer #1 (Recommendations For The Authors):

The abstract could be more positive by concluding that 'We conclude that this example of transgenerational inheritance lacks robustness but instead reflects an example of small RNA-mediated intergenerational inheritance.'

As recommended, we have added additional clarifying information to the abstract and moderated the conclusion sentence.

“We did confirm that the dsRNA transport proteins SID-1 and SID-2 are required for the intergenerational (F1) inheritance of pathogen avoidance, but not for the F1 inheritance of elevated daf-7 expression. Furthermore, our reanalysis of RNA seq data provides additional evidence that this intergenerational inherited PA14 response may be mediated by small RNAs.”

“We conclude that this example of transgenerational inheritance lacks robustness, confirm that the intergenerational avoidance response, but not the elevated daf-7p::gfp expression in F1 progeny, requires sid-1 and sid-2, and identify candidate siRNAs and target genes that may mediate this intergenerational response.”

Differential expression of sRNAs or mRNAs might be better understood quantitatively by presenting data in scatterplots (Reed and Montgomery 2020) rather than in volcano plots.

We agree and have modified Figure 6A and 6B.

This statement in the main text might be unnecessary, as it affects the tenor of the conclusion of this significant manuscript. 'We note that none of the raw data for the published figures and unpublished replicate experiments . . . this hampered our ability to fully compare'.

We have rewritten this paragraph to focus on our goal: to identify the source of the discrepancy between our results and the published results. We considered discarding this statement but ultimately decided that our inability to directly compare our data to that of previously published work is a shortcoming of our study that deserves to be acknowledged and explained.

“Ideally, we would have compared our results with the published results (Moore et al., 2019), to possibly identify additional experimental parameters for further investigation; for example, a quantitative comparison of naïve choice in the P0 and F1 generations could help to determine the role of bacterial growth in the choice assay response. However, none of the raw data for the published figures and unpublished replicate experiments (Moore et al., 2019) were available on the publisher’s website or provided upon request to the corresponding author. In the absence of a quantitative comparison, it remains possible that an explanation for the discrepancies between our results and those of Moore et al., (2019) has been overlooked.”

The final sentence of the Discussion could be tempered and more positive by stating 'Thus independent reproducibility is of paramount concern, and we have tried to be completely transparent as a model for how heritability research should be conducted within the C. elegans community'.

Thank you. The suggested sentence nicely captures our intention. We now use it, almost verbatim, as our final sentence.

“Thus, independent reproducibility is of paramount concern, and we have tried to be completely transparent as a model for how heritability research should be presented within the C. elegans community.”

Reviewer #2 (Recommendations For The Authors):

Specific comments:

(1) Protocol: It is difficult to assess from the Methods the exact protocol used by the authors to assay food preference. The annotated Murphy protocol is not sufficient. The authors should provide their own protocol - a detailed lab-ready protocol where every step is outlined, and any steps that deviate from the Murphy lab protocol are called out.

Thank you for this excellent suggestion. We now include a protocol that documents the precise steps, timings, and controls that we followed (S1_aversion_protocol). We also include footnotes to both explain the reasons behind particular steps and to document known differences to the published protocol. Given the thoroughness of this suggested approach, we have thus removed the annotated version of Moore et al., (2021) from the revised submission.

(2) The authors imply in the methods that, unlike the Murphy lab, they did NOT use azide in the assay, and instead used 4oC to "freeze" the worms in place - It is not clear whether this method was used throughout all their assays and whether this could be a source of the difference. This change is NOT indicated in the annotated Murphy lab STAR Protocol they provide in the supplement.

We apologize for the lack of clarity. Concerned that azide may be interfering with our ability to detect heritable silencing we tested and then used cold-induced rigor to preserve worm choice in some choice assay results. This was not a change to the core protocol, but a variation used in some assays to determine whether azide could reduce our ability to detect heritable behavioral responses to PA14 exposure. As Moore et al., (2021) show, too much azide can affect measurement of worm choice. Too little or ineffective azide also can affect measurement of worm choice. Azide also affects bacteria (both OP50 and PA14), which could affect the production of molecules that attract or repel worms, much like performing the assay in light vs dark conditions can influence the measured choice index.

In our hands, cold-induced rigor worked well and within biological replicates was indistinguishable from azide (Figure S10). Thus, we include those results in our analysis and now indicate in Tables 2 and S2 and in Figures 1 and 3 which experiments used which method. As suggested, we now provide a detailed protocol that includes a note describing our precise method for cold-induced rigor.

Also, the number of worms used in each assay needs to be specified (same or different from Murphy protocol?), and whether any worms were "censored" as in the Murphy protocol, and if so on what basis.

While we published the exact number of worms scored in each assay (on each plate) it is unknown how this might compare to the results published in Moore et al., (2019), as the number of animals in the presented choice assays (either per plate or per choice) were not reported. Details on censoring, when to exclude data, and additional criteria to abandon an in-progress experiment are now detailed in the protocol (S1_aversion_protocol)

(3) Several instances in the text cite changes in the protocol as producing "no meaningful differences" without referring to a specific experiment that supports that statement (for example, line 399 regarding azide).

We now include data and methods comparing azide and cold-induced rigor (Supplemental document S1_aversion_protocol, Supplemental Figure S10), and data showing the P0 choice index for 48-52 hour post-bleach L4/young adults (Supplemental Figure S1), in addition to the previously noted absence of effects due to differences in embryo bleaching protocols (Figures 2, 3 and Tables 1, 2, S1, and S2).

(4) If the authors want to claim the irreproducibility of the Murphy lab results, they should use the exact protocol used by the Murphy lab in its entirety. It is not sufficient to show that individual changes do not affect the outcome, since the protocol they use appears to include SEVERAL changes which could cumulatively affect the results. If the authors do not want to do this, they should at least acknowledge and summarize in their discussion ALL their protocol changes.

We acknowledge these minor differences between the protocols we followed and the published methods but disagree that they invalidate our results. We transparently present the effect of known minimal protocol changes. We also present analysis of possible invalidating variations (number of animals in a choice assay). We emphasize that in our hands both measures of TEI, the choice assay and measurement of daf-7p::gfp in ASI neurons, failed to replicate the published transgenerational results.

If the protocol is sensitive to how animals are counted, whether bleached embryos are mixed gently or vigorously or a few hours difference in age at training, then in our view this TEI paradigm is not robust.

See also our response to reviewer #3’s public reviews above.

(5) The authors acknowledge that "non-obvious growth culture differences" could account for the different results. In this respect, the Murphy lab has proposed that the transgenerational effect requires a small RNA expressed in PA14. The authors should check that this RNA is expressed in the cultures they grow in their lab and use for their experiments. This could potentially identify where the two protocols diverge.

The bacterial culture conditions and worm training procedures described in Moore et al., (2019) successfully produced trained P0 animals that transmitted a PA14 aversion response to their F1 progeny. In a subsequent publication (Kaletsky et al., 2020), the Murphy lab showed a correlation between the culture conditions that induce heritable avoidance and the expression of P11, a P. aeruginosa small non-coding RNA. As mentioned above in response to Reviewer #2’s public review and the Reviewing Editor’s comments to authors, the Murphy lab showed that PA14 ΔP11 bacteria fail to induce an F1 avoidance response (Figure 3L in Kaletsky et al., (2020)). Thus, the fact that we observed F1 avoidance implies that our culture conditions successfully induced P11 expression. We believe that this addresses the concern raised here. Furthermore, if P11 is not reliably expressed in pathogenic PA14, then the published model is unlikely to be relevant in a natural environment. Again, we thank the reviewer for raising this issue and have added this information to the revised manuscript (see above response to Reviewer #2’s Public Reviews).

(6) Legend to Figure 1: please clarify which experiments were done with which PA14 isolates especially for A-C. What is the origin of the N2 strain used here?

These details from Tables 2 and S2 have been added to Figure 1 panels A-C and Figure 3. Bristol N2, obtained from the CGC (reference 257), was used for aversion experiments.

(7) Growth conditions: "These young adults produced comparable P0 and F1 results (Figure 1, Figure 2, and Figure 3)." It is not clear from the text what specific figure panels need to be compared to examine the effect of the variables described in the text. Please indicate which figure panels should be compared (lines 70-95).

The information for the daf-7p::gfp expression experiments displayed in Figure 1 and Figure 2 is presented in Table 1 and Table S1. The data for P0 aversion training using younger animals is now presented in Figure S1.

Reviewer #3 (Recommendations For The Authors):

While overall I found this easy to follow and well-written, I think the clarity of the figures could be improved by incorporating some of the information from S2 into Figure 3. Besides the figure label listing the experiment (Exp1, Exp2, etc) it would be helpful to add pertinent information about the experiment. For example Exp 1.1 (light, 20{degree sign}C), Exp1.2 (dark, 20{degree sign}C), Exp 5 (25{degree sign}C, light), etc.

Thank you for the suggestion. These details from Tables 2 and S2 have been added to Figures 1 A-C, and 3.

Citations

Moore, R.S., Kaletsky, R., and Murphy, C.T. (2019). Piwi/PRG-1 Argonaute and TGF-beta Mediate Transgenerational Learned Pathogenic Avoidance. Cell 177, 1827-1841 e1812.

Moore, R.S., Kaletsky, R., and Murphy, C.T. (2021). Protocol for transgenerational learned pathogen avoidance behavior assays in Caenorhabditis elegans. STAR Protoc 2, 100384.

Kaletsky, R., Moore, R.S., Vrla, G.D., Parsons, L.R., Gitai, Z., and Murphy, C.T. (2020). C. elegans interprets bacterial non-coding RNAs to learn pathogenic avoidance. Nature 586, 445-451.

Pereira, A.G., Gracida, X., Kagias, K., and Zhang, Y. (2020). C. elegans aversive olfactory learning generates diverse intergenerational effects. J Neurogenet 34, 378-388.

eLife Assessment

In this work, the authors use a Drosophila adult ventral nerve cord injury model extending and confirming previous observations; this important study reveals key aspects of adult neural plasticity. Taking advantage of several genetic reporter and fate tracing tools, the authors provide solid evidence for different forms of glial plasticity, that are increased upon injury. The data on detected plasticity under physiologic conditions and especially the extent of cell divisions and cell fate changes upon injury would benefit from validation by additional markers. The experimental part would improve if strengthened and accompanied by a more comprehensive integration of results regarding glial reactivity in the adult CNS.

Reviewer #1 (Public review):

Summary:

Casas-Tinto et al. present convincing data that injury of the adult Drosophila CNS triggers transdifferentiation of glial cell and even the generation of neurons from glial cells. This observation opens up the possibility to get an handle on the molecular basis of neuronal and glial generation in the vertebrate CNS after traumatic injury caused by Stroke or Crush injury. The authors use an array of sophisticated tools to follow the development of glial cells at the injury site in very young and mature adults. The results in mature adults reveal a remarkable plasticity in the fly CNS and dispels the notion that repair after injury may be only possible in nerve cords which are still developing. The observation of so called VC cells which do not express the glial marker repo could point to the generation of neurons by former glial cells.

Conclusion:

The authors present an interesting story which is technically sound and could form the basis for an in depth analysis of the molecular mechanism driving repair after brain injury in Drosophila and vertebrates.

Strengths:

The evidence for transdifferentiation of glial cells is convincing. In addition, the injury to the adult CNS shows an inherent plasticity of the mature ventral nerve cord which is unexpected.

Weaknesses:

Traumatic brain injury in Drosophila has been previously reported to trigger mitosis of glial cells and generation of neural stem cells in the larval CNS and the adult brain hemispheres. Therefore this report adds to but does not significantly change our current understanding. The origin and identity of VC cells is still unclear. The authors show that VC cells are not GABA- or glutamergic. Yet, there are many other neurotransmitter or neuropetides. It would have been nice to see a staining with another general neuronal marker such as anti-Syt1 to confirm the neuronal identity of Syt1.

Reviewer #2 (Public review):

Summary:

Casas-Tinto et al., provide new insight into glial plasticity using a crush injury paradigm in the ventral nerve cord (VNC) of adult Drosophila. The authors find that both astrocyte-like glia (ALG) and ensheating glia (EG) divide under homeostatic conditions in the adult VNC and identify ALG as the glial population that specifically ramps up proliferation in response to injury, whereas the number of EGs decreases following the insult. Using lineage-tracing tools, the authors interestingly observe interconversion of glial subtypes, especially of EGs into ALGs, which occurs independent of injury and is dependent on the availability of the transcription factor Prospero in EGs, adding to the plasticity observed in the system. Finally, when tracing the progeny of glia, Casas-Tinto and colleagues detect cells of neuronal identity and provide evidence that such glia-derived neurogenesis is specifically favored following ventral nerve cord injury, which puts forward a remarkable way in which glia can respond to neuronal damage.

Strengths:

This study highlights a new facet of adult nervous system plasticity at the level of the ventral nerve cord, supporting the view that proliferative capacity is maintained in the mature CNS and stimulated upon injury.

The injury paradigm is well chosen, as the organization of the neuromeres allows specific targeting of one segment, compared to the remaining intact and with the potential to later link observed plasticity to behavior such as locomotion.

Numerous experiments have been carried out in 7-day old flies, showing that the observed plasticity is not due to residual developmental remodeling or a still immature VNC.

By elegantly combining different methods, the authors show glial divisions including with mitotic-dependent tracing and find that the number of generated glia is refined by apoptosis later on.

The work identifies prospero in glia as an important coordinator of glial cell fate, from development to the adult context, which draws further attention to the upstream regulatory mechanisms.

Weaknesses:

The authors observe consistent inter-conversion of EG to ALG glial subtypes that is further stimulated upon injury. The authors conclude that these findings have important consequences for CNS regeneration and potentially for memory and learning. However, it remains somewhat unclear how glial transformation could contribute to regeneration and functional recovery.

The signal of the Fucci cell cycle reporter seems more complex to interpret based on the panels provided compared to the other methods employed by the authors to assess cell divisions.

Elav+ cells originating from glia do not express markers for mature neurons at the analysed time-point. If they will eventually differentiate<br /> or what type of structure is formed by them will have to be followed up in future studies.

Context/Discussion

There is some lack of connecting or later comparing the observed forms of glial plasticity in the VNC with respect to plasticity described in the fly brain.<br /> Highlighting some differences in the reactiveness of glia in the VNC compared to the brain could point to relevant differences in repair capacity in different areas of the CNS.

Based on the assays employed, the study points to a significant amount of glial "identity" changes or interconversions under homeostatic conditions. The potential significance of this rather unexpected "baseline" plasticity in adult tissues is not explicitly pointed out and could improve the understanding of the findings.<br /> Some speculations if "interconversion" of glia is driven by the needs in the tissue could enrich the discussion.

Reviewer #3 (Public review):

In this manuscript, Casas-Tintó et al. explore the role of glial cell in the response to a neurodegenerative injury in the adult brain. They used Drosophila melanogaster as a model organism, and found that glial cells are able to generate new neurons through the mechanism of transdifferentiation in response to injury. This paper provides a new mechanism in regeneration, and gives an understanding to the role of glial cells in the process.

Comments on revisions:

In the previous version of the manuscript, I had suggested several recommendations for the authors. Unfortunately, none of these were addressed in the author's revision.

Author response:

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

Public Reviews:

Reviewer #1:

Summary:

Casas-Tinto et al. present convincing data that injury of the adult Drosophila CNS triggers transdifferentiation of glial cells and even the generation of neurons from glial cells. This observation opens up the possibility of getting a handle on the molecular basis of neuronal and glial generation in the vertebrate CNS after traumatic injury caused by Stroke or Crush injury. The authors use an array of sophisticated tools to follow the development of glial cells at the injury site in very young and mature adults. The results in mature adults revealing a remarkable plasticity in the fly CNS and dispels the notion that repair after injury may be only possible in nerve cords which are still developing. The observation of so-called VC cells which do not express the glial marker repo could point to the generation of neurons by former glial cells.

Conclusion:

The authors present an interesting story that is technically sound and could form the basis for an in-depth analysis of the molecular mechanism driving repair after brain injury in Drosophila and vertebrates.

Strengths:

The evidence for transdifferentiation of glial cells is convincing. In addition, the injury to the adult CNS shows an inherent plasticity of the mature ventral nerve cord which is unexpected.

Weaknesses:

Traumatic brain injury in Drosophila has been previously reported to trigger mitosis of glial cells and generation of neural stem cells in the larval CNS and the adult brain hemispheres. Therefore this report adds to but does not significantly change our current understanding. The origin and identity of VC cells is unclear.

The Reviewer correctly points out that it has been reported that traumatic brain injury trigger generation of neural stem cells. However, according to previous reports, those cells where quiescent Dpn+ neuroblast. We now report that already differentiated adult neuropil glia transdifferentiate into neurons. Which is a new mechanism not previously reported. 

We agree with the reviewer regarding the identity of VC neurons although according to the results of G-TRACE experiments the origin is clear, they originate from neuropil glia (i.e. Astrocyte-like glia and ensheathing glia). We have used a battery of antibodies previously reported to identify specific subtypes of neurons to identify these newly generated neurons (Figure S1). We did not find any other neuronal marker rather than Elav that co-localize with VC cells

Reviewer #2:

Summary:

Casas-Tinto et al., provide new insight into glial plasticity using a crush injury paradigm in the ventral nerve cord (VNC) of adult Drosophila. The authors find that both astrocyte-like glia (ALG) and ensheating glia (EG) divide under homeostatic conditions in the adult VNC and identify ALG as the glial population that specifically ramps up proliferation in response to injury, whereas the number of EGs decreases following the insult. Using lineagetracing tools, the authors interestingly observe the interconversion of glial subtypes, especially of EGs into ALGs, which occurs independent of injury and is dependent on the availability of the transcription factor Prospero in EGs, adding to the plasticity observed in the system. Finally, when tracing the progeny of differentiated glia, Casas-Tinto and colleagues detect cells of neuronal identity and provide evidence that such glia-derived neurogenesis is specifically favored following ventral nerve cord injury, which puts forward a remarkable way in which glia can respond to neuronal damage.

Numerous experiments have been carried out in 7-day-old flies, showing that the observed plasticity is not due to residual developmental remodeling or a still immature VNC.

By elegantly combining different genetic tools, the authors show glial divisions with mitotic-dependent tracing and find that the number of generated glia is refined by apoptosis later on.

The work identifies Prospero in glia as an important coordinator of glial cell fate, from development to the adult context, which draws further attention to the upstream regulatory mechanisms.

We express our gratitude to the reviewer for their keen appreciation of our efforts and their enthusiasm for the outcomes of this research.

Weaknesses:

Although the authors do use a variety of methods to show glial proliferation, the EdU data (Figure 1B) could be more informative (Figure 1B) by displaying images of non-injured animals and providing quantifications or the mention of these numbers based on results previously acquired in the system.

We appreciate the Reviewer’s comment. We believed that adding images of non-injured animals did not add new information as we already quantified the increase of glial proliferation upon injury in Losada-Perez let al. 2021. Besides, the purpose of this experiment was to figure out if dividing cells where Astrocyte-like glia rather than the number of dividing cells. Comparing independent experiments could be tricky but if we compare the quantifications of G2-M glia (repo>fly-Fucci) done in Losada-Perez et al 2021 (fig 1C) with the quantifications of G2-M neuropil glia done in this work (fig 1C) we can see that the numbers are comparable.

The experiments relying on the FUCCI cell cycle reporter suggested considerable baseline proliferation for EGs and ALGs, but when using an independent method (Twin Spot MARCM), mitotic marking was only detected for ALGs. This discrepancy could be addressed by assessing the co-localization of the different glia subsets using the identified driver lines with mitotic markers such as PH3.

In our understanding this discrepancy could be explained by the magnitude of proliferation. The lower proliferation rate of EG (as indicate the fly-fucci experiments) combining with the incomplete efficiency of MARCM clones induction reduces considerably the chances of finding EG MARCM clones. PH3 is a mitotic marker but it is also found in apoptotic cells (Kim and Park 2012. DOI: 10.1371/journal.pone.0044307) however, we stained injured VNCs with anti-Ph3 and found ALG cells positive for PH3 (Author response image 1).

Author response image 1.

 

The data in Figure 1C would be more convincing in combination with images of the FUCCI Reporter as it can provide further information on the location and proportion of glia that enter the cell cycle versus the fraction that remains quiescent.

We added a Figure 1 V2 (version 2) with the suggested images (1-C’).

The analyses of inter-glia conversion in Figure 3 are complicated by the fact that Prospero RNAi is both used to suppress EG - to ALG conversion and as a marker to establish ALG nature. Clarifications if the GFP+ cells still expressed Pros or were classified as NP-like GFP cells are required here.

As described in the text, Pros is a marker for ALG and the results suggest that Prospero expression is required for the EG to ALG transition. We clarified these concepts in the text accordingly. In figure 3 we showed images of NP-like cells originated from EG that are prospero+, and therefore supporting the transdifferentiation from EG to ALG.  

The conclusion that ALG and EG glial cells can give rise to cells of neuronal lineage is based on glial lineage information (GFP+ cells from glial G-trace) and staining for the neuronal marker Elav. The use of other neuronal markers apart from Elav or morphological features would provide a more compelling case that GFP+ cells are mature neurons.

We completely agree with the reviewer's observation regarding the identity of VC neurons. We have used a battery of antibodies previously reported to identify specific subtypes of neurons to identify these newly generated neurons (Figure S1). We did not find any other neuronal marker rather than Elav that colocalize with VC cells

Although the text discusses in which contexts, glial plasticity is observed or increased upon injury, the figures are less clear regarding this aspect. A more systematic comparison of injured VNCs versus homeostatic conditions, combined with clear labelling of the injury area would facilitate the understanding of the panels.

We appreciate the Reviewer’s observation. We have carefully checked all figures and labelled then as “Injured” or “Not Injured”. We added a Figure 2-V2 and a figure 4-V2.

Context/Discussion

The study finds that glia in the ventral cord of flies have latent neurogenic potential. Such observations have not been made regarding glia in the fly brain, where injury is reported to drive glial divisions or the proliferation of undifferentiated progenitor cells with neurogenic potential.

Discussing this different strategy for cell replacement adopted by glia in the VNC and pointing out differences to other modes seems fascinating. Highlighting differences in the reactiveness of glia in the VNC compared to the brain also seems highly relevant as they may point to different properties to repair damage.

Based on the assays employed, the study points to a significant amount of

glial "identity" changes or interconversions, which is surprising under homeostatic conditions. The significance of this "baseline" plasticity remains undiscussed, although glia unarguably show extensive adaptations during nervous system development.

It would be interesting to know if the "interconversion" of glia is determined by the needs in the tissue or would shift in the context of selective ablation/suppression of a glial type.

We deeply appreciate the Reviewer’s enthusiasm on this subject, it is indeed fascinating. We made a reduced discussion in order to fit in the eLife Short report requirements but the specific condition that trigger glial interconversion are of great interest for us. To compromise EG or ALG viability and evaluate the behaviour of glial cells is of great interest for developmental biology and regeneration, but the precise scenario to develop these experiments is not well defined. In this report, we aim to reproduce an injury in Drosophila brain and this model should serve to analyze cellular behaviours. The scenario where we deplete on specific subpopulation of glial cells is conceptually attractive, but far away from the scope of this report.

Reviewer #3:

In this manuscript, Casas-Tintó et al. explore the role of glial cells in the response to a neurodegenerative injury in the adult brain. They used Drosophila melanogaster as a model organism and found that glial cells are able to generate new neurons through the mechanism of transdifferentiation in response to injury.

This paper provides a new mechanism in regeneration and gives an understanding of the role of glial cells in the process.

eLife Assessment

This study provides valuable new information on the role of the endoplasmic reticulum calcium pump, TgSERCA, in the human pathogen Toxoplasma gondii. It is proposed that the endoplasmic reticulum is the major calcium store in these protists and that calcium is directly transported to other organelles via membrane contact sites. While the experimental work is solid and supported by complementary approaches, direct evidence for intra-organellar calcium transport via membrane domains and specific calcium efflux transporters is lacking.

Reviewer #1 (Public review):

Li et al. investigate Ca2+ signaling in T. gondii and argue that Ca2+ tunnels through the ER to other organelles to fuel multiple aspects of T. gondii biology. They focus in particular on TgSERCA as the presumed primary mechanism for ER Ca2+ filling. Although, when TgSERCA was knocked out there was still a Ca2+ release in response to TG present. Overall the Ca2+ signaling data do not support the conclusion of Ca2+ tunneling through the ER to other organelles in fact they argue for direct Ca2+ uptake from the cytosol into the organelles as outlined in the specific points below. The authors show EM membrane contact sites between the ER and other organelles, so Ca2+ released by the ER could presumably be taken up by other organelles but that is not ER Ca2+ tunneling. They clearly show that SERCA is required for T. gondii function. Overall, the data presented to not fully support the conclusions reached.

Reviewer #2 (Public review):

The present study focuses on calcium pools and fluxes in the unicellular parasite Toxoplasma gondii, and in particular on the role of the endoplasmic reticulum (ER) calcium pump TgSERCA in sequestering and redistributing calcium to other intracellular organelles following influx at the plasma membrane. Calcium sequestration by the ER and its interactions with other intracellular organelles, including the concept of tunneling through the ER, have been extensively characterized in mammalian cells and a number of other higher eukaryotes. However, these pathways are still not well understood in many organisms, including protist pathogens such as Toxoplasma. In addition, T. gondii has unique organelles not found in most other organisms, including the apicoplast and the plant-like vacuolar compartment (PLVAC). Moreover, the fact that T. gondii transitions through life cycle stages within and exterior to the host cells, with very different exposures to calcium, adds significance to the current investigation of the role of the ER in redistributing calcium following exposure to physiological levels of extracellular calcium.

The authors have provided significant new information on the T. gondii SERCA, including its ATP- and calcium-dependence, subcellular localization, and role in taking up calcium from the cytosol when cells are exposed to high extracellular calcium. They also use a conditional knockout of TgSERCA to investigate its role in ER calcium store-filling and the ability of other subcellular organelles to sequester and release calcium. These knockout experiments provide important evidence that ER calcium uptake plays a significant role in maintaining the filling state of other intracellular compartments.

While it is clearly demonstrated, and not surprising, that the addition of 1.8 mM extracellular CaCl2 to intact T. gondii parasites preincubated with EGTA leads to an increase in cytosolic calcium and subsequent enhanced loading of the ER and other intracellular compartments, there is a caveat to the quantitation of these increases in calcium loading. The authors rely on the amplitude of cytosolic free calcium increases in response to thapsigargin, GPN, nigericin, and CCCP, all measured with fura2. This likely overestimates the changes in calcium pool sizes because the buffering of free calcium in the cytosol is nonlinear, and fura2 (with a Kd of 100-200 nM) is a substantial, if not predominant, cytosolic calcium buffer. Indeed, the increases in signal noise at higher cytosolic calcium levels (e.g. peak calcium in Figure 1C) are indicative of fura2 ratio calculations approaching saturation of the indicator dye.

Another caveat, not addressed, is that loading of fura2/AM can result in compartmentalized fura2, which might modify free calcium levels and calcium storage capacity in intracellular organelles.

The finding that the SERCA inhibitor cyclopiazonic acid (CPA) only mobilizes a fraction of the thapsigargin-sensitive calcium stores in T. gondii coincides with previously published work in another apicomplexan parasite, P. falciparum, showing that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools (Borges-Pereira et al., 2020, DOI: 10.1074/jbc.RA120.014906). It would be valuable to determine whether this reflects the off-target effects of thapsigargin or the differential sensitivity of TgSERCA to the two inhibitors.

The authors interpret the residual calcium mobilization response to Zaprinast observed after ATc knockdown of TgSERCA (Figures 4E, 4F) as indicative of a target calcium pool in addition to the ER. While this may well be correct, it appears from the description of this experiment that it was carried out using the same conditions as Figure 4A where TgSERCA activity was only reduced by about 50%.

The data in Figures 4A vs 4G and Figures 4B vs 4H indicate that the size of the response to GPN is similar to that with thapsigargin in both the presence and absence of extracellular calcium. This raises the question of whether GPN is only releasing calcium from acidic compartments or whether it acts on the ER calcium stores, as previously suggested by Atakpa et al. 2019 DOI: 10.1242/jcs.223883. Nonetheless, Figure 1H shows that there is a robust calcium response to GPN after the addition of thapsigargin.

An important advance in the current work is the use of state-of-the-art approaches with targeted genetically encoded calcium indicators (GECIs) to monitor calcium in important subcellular compartments. The authors have previously done this with the apicoplast, but now add the mitochondria to their repertoire. Despite the absence of a canonical mitochondrial calcium uniporter (MCU) in the Toxoplasma genome, the authors demonstrate the ability of T. gondii mitochondrial to accumulate calcium, albeit at high calcium concentrations. Although the calcium concentrations here are higher than needed for mammalian mitochondrial calcium uptake, there too calcium uptake requires calcium levels higher than those typically attained in the bulk cytosolic compartment. And just like in mammalian mitochondria, the current work shows that ER calcium release can elicit mitochondrial calcium loading even when other sources of elevated cytosolic calcium are ineffective, suggesting a role for ER-mitochondrial membrane contact sites. With these new tools in hand, it will be of great value to elucidate the bioenergetics and transport pathways associated with mitochondrial calcium accumulation in T. gondi.

The current studies of calcium pools and their interactions with the ER and dependence on SERCA activity in T. gondi are complemented by super-resolution microscopy and electron microscopy that do indeed demonstrate the presence of close appositions between the ER and other organelles (see also videos). Thus, the work presented provides good evidence for the ER acting as the orchestrating organelle delivering calcium to other subcellular compartments through contact sites in T. gondi, as has become increasingly clear from work in other organisms.

Reviewer #3 (Public review):

This manuscript describes an investigation of how intracellular calcium stores are regulated and provides evidence that is in line with the role of the SERCA-Ca2+-ATPase in this important homeostasis pathway. Calcium uptake by mitochondria is further investigated and the authors suggest that ER-mitochondria membrane contact sites may be involved in mediating this, as demonstrated in other organisms.

The significance of the findings is in shedding light on key elements within the mechanism of calcium storage and regulation/homeostasis in the medically important parasite Toxoplasma gondii whose ability to infect and cause disease critically relies on calcium signalling. An important strength is that despite its importance, calcium homeostasis in Toxoplasma is understudied and not well understood.

A difficulty in the field, and a weakness of the work, is that following calcium in the cell is technically challenging and thus requires reliance on artificial conditions. In this context, the main weakness of the manuscript is the extrapolation of data. The language used could be more careful, especially considering that the way to measure the ER calcium is highly artificial - for example utilising permeabilization and over-loading the experiment with calcium. Measures are also indirect - for example, when the response to ionomycin treatment was not fully in line with the suggested model the authors hypothesise that the result is likely affected by other storage, but there is no direct support for that.

Below we provide some suggestions to improve controls, however, even with those included, we would still be in favour of revising the language and trying to avoid making strong and definitive conclusions. For example, in the discussion perhaps replace "showed" with "provide evidence that are consistent with..."; replace or remove words like "efficiently" and "impressive"; revise the definitive language used in the last few lines of the abstract (lines 13-17); etc. Importantly we recommend reconsidering whether the data is sufficiently direct and unambiguous to justify the model proposed in Figure 7 (we are in favour of removing this figure at this early point of our understanding of the calcium dynamic between organelles in Toxoplasma).

Another important weakness is poor referencing of previous work in the field. Lines 248-250 read almost as if the authors originally hypothesised the idea that calcium is shuttled between ER and mitochondria via membrane contact sites (MCS) - but there is extensive literature on other eukaryotes which should be first cited and discussed in this context. Likewise, the discussion of MCS in Toxoplasma does not include the body of work already published on this parasite by several groups. It is informative to discuss observations in light of what is already known.

Author response:

Reviewer #1 (Public review):

Li et al. investigate Ca2+ signaling in T. gondii and argue that Ca2+ tunnels through the ER to other organelles to fuel multiple aspects of T. gondii biology. They focus in particular on TgSERCA as the presumed primary mechanism for ER Ca2+ filling. Although, when TgSERCA was knocked out there was still a Ca2+ release in response to TG present.

Note that we did not knockout SERCA as it is an essential gene so it would not be possible to isolate parasites that do not express SERCA. We created conditional mutants that downregulate the expression of SERCA and some activity is present in the mutant after 24 h of ATc treatment.

Overall the Ca2+ signaling data do not support the conclusion of Ca2+ tunneling through the ER to other organelles in fact they argue for direct Ca2+ uptake from the cytosol.

The authors show EM membrane contact sites between the ER and other organelles, so Ca2+ released by the ER could presumably be taken up by other organelles but that is not ER Ca2+ tunneling.

They clearly show that SERCA is required for T. gondii function.

Overall, the data presented to not fully support the conclusions reached

We agree that the data does not support Ca2+ tunneling as defined and characterized in mammalian cells. In response to this comment, we modified the title and the text accordingly.

However, we think that the study shows far more than just the role of SERCA in T. gondii functions. We argue that the study shows that the ER (through the activity of the SERCA pump) sequesters and re-distributes calcium to other organelles following influx through the PM. The experiments show that the ER is able to take calcium from the cytosol as it enters the parasite through SERCA activity, and this activity is important for the transition of the parasite between various extracellular calcium exposures. We believe that the role of the ER in redistributing calcium following exposure to physiological levels of extracellular calcium is demonstrated in the experiments shown in Figs 1H-I, 4G-H and 5G,H, I, J, K . There are no previous T. gondii studies that address the question of how intracellular stores are filled with calcium, which are essential for the continuation of the lytic cycle, meaning they are essential for the parasitism of T. gondii.

Data argue for direct Ca2+ uptake from the cytosol

The ER most likely takes up calcium from the cytosol following its entry through the PM and redistributes it to the other organelles. We will delete the word “tunneling” and replace it with transfer and re-distribution as they represent our results.

What we think is re-distribution is shown in Figure 1H and I in which the calcium released after GPN and nigericin are enhanced after TG addition. Of note is that there is no experimental evidence that supports the regulation of calcium entry by store depletion (PMID: 24867952), and we do not think that the enhanced response is due to calcium entry.

Figure 4G and H show that knocking down SERCA reduces significantly the response to GPN. Fig 5I shows that the mitochondrial calcium uptake is reduced after the addition of GPN in the knockdown mutant. Fig 2B shows that SERCA can take up calcium at 55 nM calcium while mitochondrial uptake needs higher concentrations (Fig 5B-C). However, higher calcium concentrations could be reached at the microdomains formed around MCS between the ER and mitochondrion. Figure 5E shows that the mitochondrion is not responsive to an increase of cytosolic calcium. This is also shown for the apicoplast in Fig. 7 E and F of the Li et al, Nat Commun 2021 paper.

Reviewer #2 (Public review):

The role of the endoplasmic reticulum (ER) calcium pump TgSERCA in sequestering and redistributing calcium to other intracellular organelles following influx at the plasma membrane.

T. gondii transitions through life cycle stages within and exterior to the host cells, with very different exposures to calcium, adds significance to the current investigation of the role of the ER in redistributing calcium following exposure to physiological levels of extracellular calcium.

They also use a conditional knockout of TgSERCA to investigate its role in ER calcium store-filling and the ability of other subcellular organelles to sequester and release calcium. These knockout experiments provide important evidence that ER calcium uptake plays a significant role in maintaining the filling state of other intracellular compartments.

We thank the reviewer.

While it is clearly demonstrated, and not surprising, that the addition of 1.8 mM extracellular CaCl2 to intact T. gondii parasites preincubated with EGTA leads to an increase in cytosolic calcium and subsequent enhanced loading of the ER and other intracellular compartments, there is a caveat to the quantitation of these increases in calcium loading. The authors rely on the amplitude of cytosolic free calcium increases in response to thapsigargin, GPN, nigericin, and CCCP, all measured with fura2. This likely overestimates the changes in calcium pool sizes because the buffering of free calcium in the cytosol is nonlinear, and fura2 (with a Kd of 100-200 nM) is a substantial, if not predominant, cytosolic calcium buffer. Indeed, the increases in signal noise at higher cytosolic calcium levels (e.g. peak calcium in Figure 1C) are indicative of fura2 ratio calculations approaching saturation of the indicator dye.

We agree about the limitations of using Fura2 but according to the literature (PMID:3838314, fig. 3) Fura2 is suitable for measurements between 100 nM and 1 mM calcium.  The responses in our experiments were within its linear range and the experiments with the SERCA mutant and mitochondrial GCaMPs supports the conclusions of our work.

We agree that the experiment shown in Fig 1C shows a response close to the limit of the linear range of Fura2 and we can provide a more representative trace in the final article. We can include new quantifications and comparisons.

Another caveat, not addressed, is that loading of fura2/AM can result in compartmentalized fura2, which might modify free calcium levels and calcium storage capacity in intracellular organelles.

We are aware of this issue and because of that we have modified our protocol to minimize compartmentalization. We load cells for 26 min at room temperature and keep cells in ice and do not use them for longer that 2-3 hours because we do see evidence of compartmentalization. One evidence of compartmentalization is the increase in the resting calcium concentration.

The finding that the SERCA inhibitor cyclopiazonic acid (CPA) only mobilizes a fraction of the thapsigargin-sensitive calcium stores in T. gondii coincides with previously published work in another apicomplexan parasite, P. falciparum, showing that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools (Borges-Pereira et al., 2020, DOI: 10.1074/jbc.RA120.014906). It would be valuable to determine whether this reflects the off-target effects of thapsigargin or the differential sensitivity of TgSERCA to the two inhibitors.

This is an interesting observation, and we will discuss the result considering the Plasmodium study and include the citation. We will add inhibition curves using the MagFluo protocol and compare CPA and TG.

Figure S1 suggests differential sensitivity, and it shows that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools in T. gondii. Also important is that we used 1 µM TG as we are aware that TG has shown off-target effects at higher concentrations. 

The authors interpret the residual calcium mobilization response to Zaprinast observed after ATc knockdown of TgSERCA (Figures 4E, 4F) as indicative of a target calcium pool in addition to the ER. While this may well be correct, it appears from the description of this experiment that it was carried out using the same conditions as Figure 4A where TgSERCA activity was only reduced by about 50%.

We partially agree as pointed by the reviewer knock down of TgSERCA by only 50% means that the ER still could be targeted by zaprinast and no evidence of another target calcium pool. From the MagFLuo4 experiment (although we are aware that the fluorescence of mag Fluo4 is not linear to calcium), there is SERCA activity after 24 hr of ATc treatment.  However, when adding Zaprinast after TG we see a significant release of calcium which is true for both wild type and conditional knockdowns. Because of this result we proposed that there could be another large neutral calcium pool than the one mobilized by TG. We will address these possibilities in the discussion and interpretation of the result.

The data in Figures 4A vs 4G and Figures 4B vs 4H indicate that the size of the response to GPN is similar to that with thapsigargin in both the presence and absence of extracellular calcium. This raises the question of whether GPN is only releasing calcium from acidic compartments or whether it acts on the ER calcium stores, as previously suggested by Atakpa et al. 2019 DOI: 10.1242/jcs.223883. Nonetheless, Figure 1H shows that there is a robust calcium response to GPN after the addition of thapsigargin.

The results of the experiments did not exclude the possibility that GPN can also mobilize some calcium from the ER besides acidic organelles. We don’t have any evidence to support that GPN can mobilize calcium from the ER either. Based on our unpublished work, we think GPN mainly release calcium from the PLVAC. We will include the mentioned citation and discuss the result considering the possibility that GPN may be acting on the ER.

An important advance in the current work is the use of state-of-the-art approaches with targeted genetically encoded calcium indicators (GECIs) to monitor calcium in important subcellular compartments. The authors have previously done this with the apicoplast, but now add the mitochondria to their repertoire. Despite the absence of a canonical mitochondrial calcium uniporter (MCU) in the Toxoplasma genome, the authors demonstrate the ability of T. gondii mitochondrial to accumulate calcium, albeit at high calcium concentrations. Although the calcium concentrations here are higher than needed for mammalian mitochondrial calcium uptake, there too calcium uptake requires calcium levels higher than those typically attained in the bulk cytosolic compartment. And just like in mammalian mitochondria, the current work shows that ER calcium release can elicit mitochondrial calcium loading even when other sources of elevated cytosolic calcium are ineffective, suggesting a role for ER-mitochondrial membrane contact sites. With these new tools in hand, it will be of great value to elucidate the bioenergetics and transport pathways associated with mitochondrial calcium accumulation in T. gondii.

We thank this reviewer for his/her positive comment. Studies of bioenergetics and transport pathways associated with mitochondrial calcium accumulation is part of our future plans.

The current studies of calcium pools and their interactions with the ER and dependence on SERCA activity in T. gondi are complemented by super-resolution microscopy and electron microscopy that do indeed demonstrate the presence of close appositions between the ER and other organelles (see also videos). Thus, the work presented provides good evidence for the ER acting as the orchestrating organelle delivering calcium to other subcellular compartments through contact sites in T. gondi, as has become increasingly clear from work in other organisms.

Thank you

Reviewer #3 (Public review):

This manuscript describes an investigation of how intracellular calcium stores are regulated and provides evidence that is in line with the role of the SERCA-Ca2+-ATPase in this important homeostasis pathway. Calcium uptake by mitochondria is further investigated and the authors suggest that ER-mitochondria membrane contact sites may be involved in mediating this, as demonstrated in other organisms.

The significance of the findings is in shedding light on key elements within the mechanism of calcium storage and regulation/homeostasis in the medically important parasite Toxoplasma gondii whose ability to infect and cause disease critically relies on calcium signalling. An important strength is that despite its importance, calcium homeostasis in Toxoplasma is understudied and not well understood.

We agree with the reviewer. Thank you

A difficulty in the field, and a weakness of the work, is that following calcium in the cell is technically challenging and thus requires reliance on artificial conditions. In this context, the main weakness of the manuscript is the extrapolation of data. The language used could be more careful, especially considering that the way to measure the ER calcium is highly artificial - for example utilising permeabilization and over-loading the experiment with calcium. Measures are also indirect - for example, when the response to ionomycin treatment was not fully in line with the suggested model the authors hypothesise that the result is likely affected by other storage, but there is no direct support for that.

The MagFluo protocol has been amply used in mammalian cells, DT40 cells and other cells for the characterization of the IP3 receptor response to IP3. We will include and discuss more citations in the revised article. The scheme at the top of the figure shows the protocol used. There is no overloading with calcium because the cells are permeabilized and the concentrations of calcium used are physiological and all experiments were performed at 220 nm calcium which is within the cytosolic levels tolerated by cells. The experiment was done with permeabilized cells because permeabilization allows the indicator to become diluted, the substrate MgATP to reach the membrane of the ER and in addition allows for the exposure to precise concentrations of calcium. MagFluo4 loading is intended for its compartmentalization to all intracellular compartments and the uptake stimulated by MgATP exclusively occurs in the compartment occupied by SERCA. IO is an ionophore that causes calcium release from other stores in addition to the ER and it is expected that will result in a larger release. We must clarify that the experiment shown in Fig. 2 was done to characterize the activity of SERCA and was not aimed at the characterization of the role of SERCA in the parasite. We will explain this result better in the revised version of the article.

Below we provide some suggestions to improve controls, however, even with those included, we would still be in favour of revising the language and trying to avoid making strong and definitive conclusions. For example, in the discussion perhaps replace "showed" with "provide evidence that are consistent with..."; replace or remove words like "efficiently" and "impressive"; revise the definitive language used in the last few lines of the abstract (lines 13-17); etc. Importantly we recommend reconsidering whether the data is sufficiently direct and unambiguous to justify the model proposed in Figure 7 (we are in favour of removing this figure at this early point of our understanding of the calcium dynamic between organelles in Toxoplasma).

We thank the reviewer for the suggestions and will modify the language as suggested.

Fig 7 is only a model and as all models could be incorrect. However, considering this reviewer’s criticism we will replace the model for a simpler one that is less speculative.

Another important weakness is poor referencing of previous work in the field. Lines 248-250 read almost as if the authors originally hypothesised the idea that calcium is shuttled between ER and mitochondria via membrane contact sites (MCS) - but there is extensive literature on other eukaryotes which should be first cited and discussed in this context. Likewise, the discussion of MCS in Toxoplasma does not include the body of work already published on this parasite by several groups. It is informative to discuss observations in light of what is already known.

We added a citation following the sentence mentioned by the reviewer in lines 248-250 (corrected preprint) and will include more in the revised article. We cite several pertinent articles that describe MCS in Toxoplasma (lines 378-380, very few actually). We will make sure not to miss any new articles that could have been recently published. Note that our work is not about describing the presence of MCSs. We are showing transfer of calcium between the ER and mitochondria and we present evidence that supports that it happens through MCSs.

eLife Assessment

This important study examined neuronal activity in the dentate nucleus of the cerebellum when monkeys performed a difficult perceptual decision-making task. The authors provide convincing evidence that the cerebellum represents sensory, motor, and behavioral outcome signals that are sent to the attentional system. This paper is of great general interest in that it shows the involvement of the cerebellum in cognitive processes at the neuronal level.

Reviewer #1 (Public review):

Summary:

Recordings were made from the dentate nucleus of two monkeys during a decision-making task. Correlates of stimulus position and stimulus information were found to varying degrees in the neuronal activities.

Strengths:

A difficult decision-making task was examined in two monkeys.

Weaknesses:

One of the monkeys had difficulty learning the task. The initial version of the manuscript lacked a coherent hypothesis to be tested, although the revision has improved things. In its current form, the manuscript does not provide data regarding the possibility that this part of the brain may have little to do with the task that was being studied. As noted in the response to the reviewer's comments, future studies could address this issue by providing results of additional inactivation experiments.

Reviewer #2 (Public review):

The authors trained monkeys to discriminate peripheral visual cues and associate them with planning future saccades of an indicated direction. At the same time, the authors recorded single-unit neural activity in the cerebellar dentate nucleus. They demonstrated that substantial fractions of DN cells exhibited sustained modulation of spike rates spanning task epochs and carrying information about stimulus, response, and trial outcome. Finally, tracer injections demonstrated this region of the DN projects to a large number of targets including several known to interconnect the visual attention network. The data compellingly demonstrate the authors' central claims, and the analyses are well-suited to support the conclusions. Importantly, the study demonstrates that DN cells convey many motor and nonmotor variables related to task execution, event sequencing, visual attention, and arguably decision-making/working memory.

Author response:

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

Reviewer #1:

- Summary: 

Recordings were made from the dentate nucleus of two monkeys during a decision-making task. Correlates of stimulus position and stimulus information were found to varying degrees in the neuronal activities. 

We agree with this summary.

- Strengths: 

A difficult decision-making task was examined in two monkeys.

We agree with this statement.

- Weaknesses: 

One of the monkeys did not fully learn the task. The manuscript lacked a coherent hypothesis to be tested, and no attempt was made to consider the possibility that this part of the brain may have little to do with the task that was being studied. 

We understand the reviewers concern. It is correct that one of the monkeys (Mi) did not perform at a high level, but it should be noted that both monkeys learned significantly above chance level. Therefore, we would argue that both monkeys in fact did learn the task but Mi’s performance was suboptimal. This difference in the performance levels gave us a rare opportunity to dive deeper into the reasons why some animals perform better than the others and we show that Mi (the lower performing monkey) paid more attention to the outcome of the previous trial – this is evident from our behavioural and decoding models.

We tested the overall hypothesis that neurons of the nucleus dentate can dynamically modulate their activity during a visual attention task, comprising not only sensorimotor but also cognitive attentional components. Many neurons in the dentate are multimodal (Figure 3C-D) which was something that was theorized. One of the specific hypotheses that we tested is that the dentate cells can be direction-selective for both the sensorimotor and cognitive component. Given that many of the recorded cells showed direction-selectivity in their firing rate modulation for gap directions and/or stimulus directions, we provide strong evidence that this hypothesis is correct. We have now spelled out this hypothesis more explicitly in the introduction of the revised version. We now also explain better why we tested this specific hypothesis. Indeed, earlier studies in primates such as those by Herzfeld and colleagues (2018, Nat. Neuro.) and van Es and colleagues (2019, Current Biol) have indicated that direction-selectivity of cerebellar activity may occur in various sensorimotor domains.

We also appreciate the comment of this Reviewer that in our original submission we did not show our attempt to consider the possibility that this part of the brain may have little to do with the task that was being studied. We in fact did consider this possibility in that we successfully injected 3 ml of muscimol (5 μg/ml, Sigma Aldrich) into the dentate nucleus in vivo in one of the monkeys (Mo). This application resulted in a reduction of more than 10% in correct responses of the covert attention task after 45 minutes, whereas the performance remained the same following saline injections. Unfortunately, due to the timing of the experiments and Covid19-related laboratory restrictions we were unable to perform these experiments in the other monkey or repeat them in Mo. We aim to replicate this in future experiments and publish it when we have full datasets of at least two monkeys available. For this paper we have prioritized our tracing experiments, highlighting the connections of the dentate nucleus with attention related areas in brainstem and cortex in both monkeys, following perfusion.

- Perhaps the large differences in performance between the two subjects can be used as a way to interpret the neural data's relationship to behavior, as it provided a source of variance. This is what we would hypothesize if we believed that this area of the brain is playing a significant role in the task. If one animal learns much more poorly, and this region of the brain is important for that behavior, then shouldn't there be clear, interpretable differences in the neural data? 

We thank the Reviewer for this comment. We have added a new Supplementary Figure 2, in which we present the data for both monkeys separately in the revised manuscript. Comparing the two datasets however, we see more commonalities related to the significant learning in both monkeys than differences that might be related to their different levels of learning. We have therefore decided to show the different datasets transparently in the new Supplementary Figure 2, but to stay on the conservative side in our interpretations.

- How should we look for these differences? A number of recent papers in mice have uncovered a large body of data showing that during the deliberation period, when the animal is interpreting a sensory stimulus (often using the whisker system), there is ramping activity in a principal component space among neurons that contribute to the decision. This ramping activity is present (in the PCA space) in the motor areas of the cortex, as well as in the medial and lateral cerebellar nuclei. Perhaps a similar computational approach would benefit the current manuscript. 

We also appreciate this point. We have done the principal component analysis accordingly, and we indeed do find the ramping activity in several components of the dentate activity of both monkeys (Mi and Mo). We have now added a new Supplementary Figure 3 with the first three components of both correct and incorrect trials for Mi and Mo, highlighting their potential contribution.

- What is the hypothesis that is being tested? That is, what do you think might be the function of this region of the cerebellum in this task? It seems to me that we are not entirely in the dark, as previous literature on mice decision-making tasks has produced a reasonable framework: the deliberation period coincides with ramping activity in many regions of the frontal lobe and the cerebellum. Indeed, the ramp in the cerebellum appears to be a necessary condition for the ramp to be present in the frontal lobe. Thus, we should see such ramping activity in this task in the dentate. When the monkey makes the wrong choice, the ramp should predict it. If you don't see the ramping activity, then it is possible that the hypothesis is wrong, or that you are not recording from the right place. 

It is indeed one of our specific hypotheses that the dentate cells can be direction-selective for the preparing cognitive component and/or sensorimotor response. We provide evidence that this hypothesis may be correct when we analyze the regular time response curves (see Figure 2 and the new Supplementary Figure 2 where the data of both monkeys are now presented separately). Moreover, we have now verified this by analysing the ramping curves of PCA space (new Supplementary Figure 3) and firing frequency of DN neurons that modulated upon presentation of the C-stimulus (new Supplementary Figure 4). These figures and findings are now referred to in the main text.

- As this is a difficult task that depends on the ability of the animals to understand the meaning of the cues, it is quite concerning that one of the monkeys performed poorly, particularly in the early sessions. Notably, the disparity between the two subjects is rather large: one monkey at the start of the recordings achieved a performance that was much better than the second monkey did at the end of the recording sessions. You highlighted the differences in performance in Figure 1D and mentioned that you started recording once the animals reached 60% performance. However, this did not make sense to me as the performance of Mi even after the final day of recording did not reach the performance of Mo on the first day of recording. Thus, in contrast to Mo, Mi appeared to be not ready for the task when the recording began.

We understand this point. However, please note that the learning performance of the monkeys concerned retraining sessions after they had had several weeks of vacation. So, even though it is correct that one of the two monkeys had a very good consolidation and started already at a relatively high level on the first retraining session, the other one also started and ended at a level above chance level (the y-axis starts at 0.5). We now highlight this point better in the Results section.

- One objective of having two monkeys is to illustrate that what is true in one animal is also true in the other. In some figures, you show that the neural data are significantly different, while in others you combine them into one. Thus, are you confident that the neural data across the animals should be combined, as you have done in Figure 2? Perhaps you can use the large differences in performance as a source of variance to find meaning in the neural data. 

This is a valid question; as highlighted above, we have now addressed this point in the new Supplementary Figure 2, where the data for both monkeys are presented separately. Given the sample sizes and level of variances, it is in general difficult to draw conclusions about the potential differences and contributions, but the data are sufficiently transparent to observe common trends. With regard to linking differences in the neural data to the differences in performance level, please also consider Figure 4, the new Supplementary Figure 3 (with the ramping PCA component) and new Supplementary Figure 4 (with the additional analysis of the ramping activity of DN neurons that modulated upon presentation of the C-stimulus), which suggests that the ramping stage of Mo starts before that of Mi. This difference highlights the possibility that injecting accelerations of the simple spike modulations of Purkinje cells in the cerebellar hemispheres into the complex of cerebellar nuclei may be instrumental in improving the performance of responses to covert attention, akin to what has been shown for the impact of Purkinje cells of the vestibulocerebellum on eye movement responses to vestibular stimulation (De Zeeuw et al. 1995, J Neurophysiol). This possibility is now also raised in the Discussion.

- How do we know that these neurons, or even this region of the brain, contribute to this task? When a new task is introduced, the contributions of the region of the brain that is being studied are usually established via some form of manipulation. This question is particularly relevant here because the two subjects differed markedly in their performance, yet in Figure 3 you find that a similar percentage of neurons are responding to the various elements of the task.

We appreciate this question. As highlighted above, we are refraining from showing our muscimol manipulation (3 ml of 5 μg/ml muscimol, Sigma Aldrich), as it only concerns 1 successful dataset and 1 control experiment. We hope to replicate this reversible lesion experiment in the future and publish it when we have full new datasets of at least two monkeys available. As explained above, for this paper we have sacrificed both monkeys following a timed perfusion, so as to have similar survival times for the transport of the neuro-anatomical tracer involved.  

- Behavior in both animals was better when the gap direction was up/down vs. left/right. Is this difference in behavior encoded during the time that the animal is making a decision? Are the dentate neurons better at differentiating the direction of the cue when the gap direction is up/right vs. left/right? 

These data have now been included in the new Supplementary Figure 2; we did not observe any significant differences in this respect.

Reviewer #2:

- The authors trained monkeys to discriminate peripheral visual cues and associate them with planning future saccades of an indicated direction. At the same time, the authors recorded single-unit neural activity in the cerebellar dentate nucleus. They demonstrated that substantial fractions of DN cells exhibited sustained modulation of spike rates spanning task epochs and carrying information about stimulus, response, and trial outcome. Finally, tracer injections demonstrated this region of the DN projects to a large number of targets including several known to interconnect the visual attention network. The data compellingly demonstrate the authors' central claims, and the analyses are well-suited to support the conclusions. Importantly, the study demonstrates that DN cells convey many motor and nonmotor variables related to task execution, event sequencing, visual attention, and arguably decision-making/working memory. 

We thank the Reviewer for this positive and constructive feedback.

- The study is solid and I do not have major concerns, but only points for possible improvement. 

We thank the Reviewer for this positive feedback.

- A key feature of this data is the extended changes/ramps in DN output across epochs (Figure 2). Crudely, this presents a challenge for the view that DN output mainly drives motor effectors, as the saccade itself lasts only a tiny fraction of the overall task. Some discussion of this dichotomy in thinking about the function(s) of the cerebellum, vis a vis the multifarious DN targets the authors demonstrate here, etc., would be helpful. 

We agree with the Reviewer and we have expanded our Discussion on this point, also now highlighting the outcome of the new PCA analysis recommended by Reviewer 1 (see the new Supplementary figure Figure 3).

- A high-level suggestion on the data: the presentation of the data focuses (sensibly) on the representation of the stimulus and response epochs (Figures 2-3). Yet, the authors then show that from decoding, it is, in fact, a trial outcome that is best represented in the population (Figure 4). While there is nothing 'wrong' with this, it reads slightly incongruously, and the reader does a bit of a "double take" back to the previous figures to see if they missed examples of the trial-outcome signals, but the previous presentations only show correct trials. Consider adding somewhere in the first 3 main figures some neural data showing comparisons with incorrect trials. This way, the reader develops prior expectations for the outcome decoding result and frame of reference for interpreting it. On a related note, the text contains an earlier introduction of this issue (p24 last sentence) and p25 paragraph 1 cites Figure 3D and 3E for signals "related to the absence of reward" - but the caption says this includes only correct trials? 

We thank the Reviewer for bringing up these points. We have addressed the textual suggestions. Moreover, we have done the PCA analysis suggested by Reviewer 1 for both the correct and incorrect trials (see Supplementary material).

- P29: The discrepancy in retrograde labeling between monkeys (2 orders of magnitude): I realize the authors can't really do anything about this, but the difference is large enough to warrant concerns in the interpretation (how did the tracer spread over the drastically larger area? Isotropically? Could it cross more "hard boundaries" and incorporate qualitatively different inputs/outputs?). A small discussion of possible caveats in interpreting the outcomes would be helpful. 

We fully agree with this comment. As highlighted in the text, in both monkeys we first identified the optimal points for injection in the dentate nucleus electrophysiologically and we used the same pump with the same settings to carry out the injections, but even so the differences are substantial. We suspect that the larger injection might have been caused by an air bubble trapped in the syringe or a deviation in the stock solution, but we can never be sure of that. We have added a potential explanation for the caveat that might have played a role.

- And a list of quick points: 

We have addressed all points listed below; we want to thank the Reviewer for bringing them up.

P3 paragraph 2 needs comma "in daily life,". 

P4 paragraph 2 "C-gap" terminology not previously defined. 

P4 paragraph 2 "animals employed different behavioral strategies". Grammatically, you should probably say "each animal employed a different behavioral strategy," but also scientifically the paragraph doesn't connect this claim to anything about the DN (whereas, e.g., the abstract does make this connection clear). 

P5 paragraph 1 "theca" should be "the". 

P6 paragraph 1 problem with ignashenkova citation insert. 

P10 paragraph 1 I think the spike rate "difference between highest and lowest" is not exactly the same as "variance," you might want to change the terminology. 

P10 paragraph 1 should probably say "To determine if a cell preferentially modulated". 

P10 paragraph 1 last sentence the last clause could be clearer. 

P17 paragraph 2 should be something like "as well as those by Carpenter and..."? 

P20 caption: consider "...directionality in the task: only one C-stim...". 

P20 caption: consider "to the left and right in the [L/R] task...to the top/bottom in the [U/D] task". 

Fig1E and S1 - is there a physical meaning of the "weight" unit, and if none, can this be transformed into a more meaningful unit? 

P21 paragraph 1 consider "activity was recorded for 304 DN neurons...". 

P21 paragraph 1 "correlations with the temporal windows" it's not clear how activity can "correlate" with a time window, consider rephrasing (activity levels changed during these time epochs, depending on stimulus identity). 

P21 paragraph 1 should be "by comparing the number of spikes in a bin...". 

P22 paragraph 2 "when we aligned the neurons to the time of maximum change" needs clarification. The maximum change of what? And per neuron? Across the population? 

P22 paragraph 2 "than that of the facilitating" should be "than did the facilitating units". 

P24 paragraph 1 needs a comma and rewording "Within each direction, trials are sorted by the time of saccade onset". 

P24 paragraph 1 should probably say "Same as in G, but for suppressed cells". 

P24 paragraph 2 should say "more than one task event" not "events". 

P24 paragraph 2 needs a comma "To fully characterize the neural responses, we fitted". 

P25 paragraph 1 should probably say "we sampled from similar populations of DN". 

P34 paragraph 3 consider rephrasing the sentence that contains both "dissociation" and "dissociate". 

P37 last line: consider "coordination of cerebellum and cerebral cortex *in* higher order mental..."? 

P38 paragraph 1 citation needed for "kinematics of goal-directed hand actions of others"? 

P38 paragraph 1 commas probably not needed "map visual input, from high-level visual regions, onto..." 

References

- Herzfeld D.J., Kojima Y, Soetedjo R, Shadmehr R (2018) Encoding of error and learning to correct that error by the Purkinje cells of the cerebellum. Nat Neurosci 21:736–743.

- van Es, D.M., van der Zwaag W., and Knapen T. (2019) Topographic Maps of Visual Space in the Human Cerebellum. Current Biol Volume 29, Issue 10p1689-1694.e3May 20.

- De Zeeuw CI, Wylie DR, Stahl JS, Simpson JI. (1995) Phase relations of Purkinje cells in the rabbit flocculus during compensatory eye movements. J Neurophysiol. Nov;74(5):2051-64. doi: 10.1152/jn.1995.74.5.2051.

Author response:

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

Reviewer #1 (Public review):

From the Reviewing Editor:

Four reviewers have assessed your manuscript on valence and salience signaling in the central amygdala. There was universal agreement that the question being asked by the experiment is important. There was consensus that the neural population being examined (GABA neurons) was important and the circular shift method for identifying task-responsive neurons was rigorous. Indeed, observing valenced outcome signaling in GABA neurons would considerably increase the role the central amygdala in valence. However, each reviewer brought up significant concerns about the design, analysis and interpretation of the results. Overall, these concerns limit the conclusions that can be drawn from the results. Addressing the concerns (described below) would work towards better answering the question at the outset of the experiment: how does the central amygdala represent salience vs valence.

A weakness noted by all reviewers was the use of the terms 'valence' and 'salience' as well as the experimental design used to reveal these signals. The two outcomes used emphasized non-overlapping sensory modalities and produced unrelated behavioral responses. Within each modality there are no manipulations that would scale either the value of the valenced outcomes or the intensity of the salient outcomes. While the food outcomes were presented many times (20 times per session over 10 sessions of appetitive conditioning) the shock outcomes were presented many fewer times (10 times in a single session). The large difference in presentations is likely to further distinguish the two outcomes. Collectively, these experimental design decisions meant that any observed differences in central amygdala GABA neuron responding are unlikely to reflect valence, but likely to reflect one or more of the above features.

We appreciate the reviewers’ comments regarding the experimental design. When assessing fear versus reward, we chose stimuli that elicit known behavioral responses, freezing versus consumption. The use of stimuli of the same modality is unlikely to elicit easily definable fear or reward responses or to be precisely matched for sensory intensity. For example, sweet or bitter tastes can be used, but even these activate different taste receptors and vary in the duration of the activation of taste-specific signaling (e.g. how long the taste lingers in the mouth). The approach we employed is similar to that of Yang et al., 2023 (doi: 10.1038/s41586-023-05910-2) that used water reward and shock to characterize the response profiles of somatostatin neurons of the central amygdala. Similar to what was reported by Yang and colleagues we observed that the majority of CeA GABA neurons responded selectively to one unconditioned stimulus (~52%). We observed that 15% of neurons responded in the same direction, either activated or inhibited, by the food or shock US. These were defined as salience based on the definitions of Lin and Nicolelis, 2008 (doi: 10.1016/j.neuron.2008.04.031) in which basal forebrain neurons responded similarly to reward or punishment irrespective of valence. The designation of valence encoding based opposite responses to the food or shock is straightforward (~10% of cells); however, we agree that the designation of modality-specific encoding neurons as valence encoding is less straightforward.

A second weakness noted by a majority of reviewers was a lack of cue-responsive unit and a lack of exploration of the diversity of response types, and the relationship cue and outcome firing. The lack of large numbers of neurons increasing firing to one or both cues is particularly surprising given the critical contribution of central amygdala GABA neurons to the acquisition of conditioned fear (which the authors measured) as well as to conditioned orienting (which the authors did not measure). Regression-like analyses would be a straightforward means of identifying neurons varying their firing in accordance with these or other behaviors. It was also noted that appetitive behavior was not measured in a rigorous way. Instead of measuring time near hopper, measures of licking would have been better. Further, measures of orienting behaviors such as startle were missing.

The authors also missed an opportunity for clustering-like analyses which could have been used to reveal neurons uniquely signaling cues, outcomes or combinations of cues and outcomes. If the authors calcium imaging approach is not able to detect expected central amygdala cue responding, might it be missing other critical aspects of responding?

As stated in the manuscript, we were surprised by the relatively low number of cue responsive cells; however, when using a less stringent statistical method (Figure 5 - Supplement 2), we observed 13% of neurons responded to the food associated cue and 23% responded to the shock associated cue. The differences are therefore likely a reflection of the rigor of the statistical measure to define the responsive units. The number of CS responsive units is less than reported in the CeAl by Ciocchi et al., 2010 (doi: 10.1038/nature09559 ) who observed 30% activated by the CS and 25% inhibited, but is not that dissimilar from the results of Duvarci et al., 2011 (doi: 10.1523/JNEUROSCI.4985-10.2011 ) who observed 11% activated in the CeAl and 25% inhibited by the CS. These numbers are also consistent with previous single cell calcium imaging of cell types in the CeA. For example, Yang et al., 2023 (doi: 10.1038/s41586-023-05910-2) observed that 13% of somatostatin neurons responded to a reward CS and 8% responded to a shock CS. Yu et al., 2017 (doi: 10.1038/s41593-017-0009-9) observed 26.5% of PKCdelta neurons responded to the shock CS. It should also be noted that our analysis was not restricted to the CeAl. Finally, Food learning was assessed in an operant chamber in freely moving mice with reward pellet delivery. Because liquids were not used for the reward US, licking is not a metric that can be used.

All reviewers point out that the evidence for salience encoding is even more limited than the evidence for valence. Although the specific concern for each reviewer varied, they all centered on an oversimplistic definition of salience. Salience ought to scale with the absolute value and intensity of the stimulus. Salience cannot simply be responding in the same direction. Further, even though the authors observed subsets of central amygdala neurons increasing or decreasing activity to both outcomes - the outcomes can readily be distinguished based on the temporal profile of responding.

We thank the reviewers for their comments relating to the definition of salience and valence encoding by central amygdala neurons. We have addressed each of the concerns below.

Additional concerns are raised by each reviewer. Our consensus is that this study sought to answer an important question - whether central amygdala signal salience or valence in cue-outcome learning. However, the experimental design, analyses, and interpretations do not permit a rigorous and definitive answer to that question. Such an answer would require additional experiments whose designs would address the significant concerns described here. Fully addressing the concerns of each reviewer would result in a re-evaluation of the findings. For example, experimental design better revealing valence and salience, and analyses describing diversity of neuronal responding and relationship to behavior would likely make the results Important or even Fundamental.

We appreciate the reviewers’ comments and have addressed each concern below.

Reviewer #2 (Public review):

In this article, Kong and authors sought to determine the encoding properties of central amygdala (CeA) neurons in response to oppositely valenced stimuli and cues predicting those stimuli. The amygdala and its subregional components have historically been understood to be regions that encode associative information, including valence stimuli. The authors performed calcium imaging of GABA-ergic CeA neurons in freely-moving mice conditioned in Pavlovian appetitive and fear paradigms, and showed that CeA neurons are responsive to both appetitive and aversive unconditioned and conditioned stimuli. They used a variant of a previously published 'circular shifting' technique (Harris, 2021), which allowed them to delineate between excited/non-responsive/inhibited neurons. While there is considerable overlap of CeA neurons responding to both unconditioned stimuli (in this case, food and shock, deemed "salience-encoding" neurons), there are considerably fewer CeA neurons that respond to both conditioned stimuli that predict the food and shock. The authors finally demonstrated that there are no differences in the order of Pavlovian paradigms (fear - shock vs. shock - fear), which is an interesting result, and convincingly presented given their counterbalanced experimental design.

In total, I find the presented study useful in understanding the dynamics of CeA neurons during a Pavlovian learning paradigm. There are many strengths of this study, including the important question and clear presentation, the circular shifting analysis was convincing to me, and the manuscript was well written. We hope the authors will find our comments constructive if they choose to revise their manuscript.

While the experiments and data are of value, I do not agree with the authors interpretation of their data, and take issue with the way they used the terms "salience" and "valence" (and would encourage them to check out Namburi et al., NPP, 2016) regarding the operational definitions of salience and valence which differ from my reading of the literature. To be fair, a recent study from another group that reports experiments/findings which are very similar to the ones in the present study (Yang et al., 2023, describing valence coding in the CeA using a similar approach) also uses the terms valence and salience in a rather liberal way that I would also have issues with (see below). Either new experiments or revised claims would be needed here, and more balanced discussion on this topic would be nice to see, and I felt that there were some aspects of novelty in this study that could be better highlighted (see below).

One noteworthy point of alarm is that it seems as if two data panels including heatmaps are duplicated (perhaps that panel G of Figure 5-figure supplement 2 is a cut and paste error? It is duplicated from panel E and does not match the associated histogram).

We thank the reviewer for their insightful comments and assessment of the manuscript.

Major concerns:

(1) The authors wish to make claims about salience and valence. This is my biggest gripe, so I will start here.

(1a) Valence scales for positive and negative stimuli and as stated in Namburi et al., NPP, 2016 where we operationalize "valence" as having different responses for positive and negative values and no response for stimuli that are not motivational significant (neutral cues that do not predict an outcome). The threshold for claiming salience, which we define as scaling with the absolute value of the stimulus, and not responding to a neutral stimulus (Namburi et al., NPP, 2016; Tye, Neuron, 2018; Li et al., Nature, 2022) would require the lack of response to a neutral cue.

We appreciate the reviewer’s comment on the definitions of salience and valence and agree that there is not a consistent classification of these response types in the field. As stated above, we used the designation of salience encoding if the cells respond in the same direction to different stimuli regardless of the valence of the stimulus similar to what was described previously (Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031). Similar definitions of salience have also been reported elsewhere (for examples see: Stephenson-Jones et al., 2020, doi: 10.1016/j.neuron.2019.12.006,  Zhu et al., 2018 doi: 10.1126/science.aat0481, and  Comoli et al., 2003, doi: 10.1038/nn1113P). Per the suggestion of the reviewer, we longitudinally tracked cells on the first day of Pavlovian reward conditioning the fear conditioning day. Although there were considerably fewer head entries on the first day of reward conditioning, we were able to identify 10 cells that were activated by both the food US and shock US. We compared the responses to the first five head entries and last head entries and the first 5 shocks and last five shocks. Consistent with what has been reported for salience encoding neurons in the basal forebrain (Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031), we observed that the responses were highest when the US was most unexpected and decreased in later trials.

Author response image 1.

(1b) The other major issue is that the authors choose to make claims about the neural responses to the USs rather than the CSs. However, being shocked and receiving sucrose also would have very different sensorimotor representations, and any differences in responses could be attributed to those confounds rather than valence or salience. They could make claims regarding salience or valence with respect to the differences in the CSs but they should restrict analysis to the period prior to the US delivery.

Perhaps the reviewer missed this, but analysis of valence and salience encoding to the different CSs are presented in Figure 5G, Figure 5 -Supplement 1 C-D, and Figure 5 -Supplement 2 N-O. Analysis of CS responsiveness to CSFood and CSShock were analyzed during the conditioning sessions Figure 3E-F, Figure 4B-C, Figure 5 – Supplement 2J-O and Figure 5 – Supplement 3K-L, and during recall probe tests for both CSFood and CSShock, Figure 5 – Supplement 1C-J.

(1c) The third obstacle to using the terms "salience" or "valence" is the lack of scaling, which is perhaps a bigger ask. At minimum either the scaling or the neutral cue would be needed to make claims about valence or salience encoding. Perhaps the authors disagree - that is fine. But they should at least acknowledge that there is literature that would say otherwise.<br /> (1d) In order to make claims about valence, the authors must take into account the sensory confound of the modality of the US (also mentioned in Namburi et al., 2016). The claim that these CeA neurons are indeed valence-encoding (based on their responses to the unconditioned stimuli) is confounded by the fact that the appetitive US (food) is a gustatory stimulus while the aversive US (shock) is a tactile stimulus.

We provided the same analysis for the US and CS. The US responses were larger and more prevalent, but similar types of encoding were observed for the CS. We agree that the food reward and the shock are very different sensory modalities. As stated above, the use of stimuli of the same modality is unlikely to elicit easily definable fear or reward responses or to be precisely matched for sensory intensity. We agree that the definition of cells that respond to only one stimulus is difficult to define in terms of valence encoding, as opposed to being specific for the sensory modality and without scaling of the stimulus it is difficult to fully address this issue. It should be noted however, that if the cells in the CeA were exclusively tuned to stimuli of different sensory modalities, we would expect to see a similar number of cells responding to the CS tones (auditory) as respond to the food (taste) and shock (somatosensory) but we do not. Of the cells tracked longitudinally 80% responded to the USs, with 65% of cells responding to food (activated or inhibited) and 44% responding to shock (activated or inhibited).

(2) Much of the central findings in this manuscript have been previously described in the literature. Yang et al., 2023 for instance shows that the CeA encodes salience (as demonstrated by the scaled responses to the increased value of unconditioned stimuli, Figure 1 j-m), and that learning amplifies responsiveness to unconditioned stimuli (Figure 2). It is nice to see a reproduction of the finding that learning amplifies CeA responses, though one study is in SST::Cre and this one in VGAT::cre - perhaps highlighting this difference could maximize the collective utility for the scientific community?

We agree that the analysis performed here is similar to what was conducted by Yang et al., 2023. With the major difference being the types of neurons sampled. Yang et al., imaged only somatostatin neurons were as we recorded all GABAergic cell types within the CeA. Moreover, because we imaged from 10 mice, we sampled neurons that ostensibly covered the entire dorsal to ventral extent of the CeA (Figure 1 – Supplement 1). Remarkably, we found that the vast majority of CeA neurons (80%) are responsive to food or shock. Within this 80% there are 8 distinct response profiles consistent with the heterogeneity of cell types within the CeA based on connectivity, electrophysiological properties, and gene expression. Moreover, we did not find any spatial distinction between food or shock responsive cells, with the responsive cell types being intermingled throughout the dorsal to ventral axis (Figure 5 – Supplement 3).

(3) There is at least one instance of copy-paste error in the figures that raised alarm. In the supplementary information (Figure 5- figure supplement 2 E;G), the heat maps for food-responsive neurons and shock-responsive neurons are identical. While this almost certainly is a clerical error, the authors would benefit from carefully reviewing each figure to ensure that no data is incorrectly duplicated.

We thank the reviewer for catching this error. It has been corrected.

(4) The authors describe experiments to compare shock and reward learning; however, there are temporal differences in what they compare in Figure 5. The authors compare the 10th day of reward learning with the 1st day of fear conditioning, which effectively represent different points of learning and retrieval. At the end of reward conditioning, animals are utilizing a learned association to the cue, which demonstrates retrieval. On the day of fear conditioning, animals are still learning the cue at the beginning of the session, but they are not necessarily retrieving an association to a learned cue. The authors would benefit from recording at a later timepoint (to be consistent with reward learning- 10 days after fear conditioning), to more accurately compare these two timepoints. Or perhaps, it might be easier to just make the comparison between Day 1 of reward learning and Day 1 of fear learning, since they must already have these data.

We agree that there are temporal differences between the food and shock US deliveries. This is likely a reflection of the fact that the shock delivery is passive and easily resolved based on the time of the US delivery, whereas the food responses are variable because they are dependent upon the consumption of the sucrose pellet. Because of these differences the kinetics of the responses cannot be accurately compared. This is why we restricted our analysis to whether the cells were food or shock responsive. Aside from reporting the temporal differences in the signals did not draw major conclusions about the differences in kinetics. In our experimental design we counterbalanced the animals that received fear conditioning firs then food conditioning, or food conditioning then fear conditioning to ensure that order effects did not influence the outcome of the study. It is widely known that Pavlovian fear conditioning can facilitate the acquisition of conditioned stimulus responses with just a single day of conditioning. In contrast, Pavlovian reward conditioning generally progresses more slowly. Because of this we restricted our analysis to the last day of reward conditioning to the first and only day of fear conditioning. However, as stated above, we compared the responses of neurons defined as salience during day 1 of reward conditioning and fear conditioning. As would be predicted based on previous definitions of salience encoding (Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031), we observed that the responses were highest when the US was most unexpected

(5) The authors make a claim of valence encoding in their title and throughout the paper, which is not possible to make given their experimental design. However, they would greatly benefit from actually using a decoder to demonstrate their encoding claim (decoding performance for shock-food versus shuffled labels) and simply make claims about decoding food-predictive cues and shock-predictive cues. Interestingly, it seems like relatively few CeA neurons actually show differential responses to the food and shock CSs, and that is interesting in itself.

As stated above, valence and salience encoding were defined similar to what has been previously reported (Li et al., 2019, doi: 10.7554/eLife.41223; Yang et al., 2023, doi: 10.1038/s41586-023-05910-2; Huang et al., 2024, doi: 10.1038/s41586-024-07819; Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031; Stephenson-Jones et al., 2020, doi: 10.1016/j.neuron.2019.12.006; Zhu et al., 2018, doi: 10.1126/science.aat0481; and Comoli et al., 2003, doi: 10.1038/nn1113P). Interestingly, many of these studies did not vary the US intensity.

Reviewer #3 (Public review):

Summary:

In their manuscript entitled Kong and colleagues investigate the role of distinct populations of neurons in the central amygdala (CeA) in encoding valence and salience during both appetitive and aversive conditioning. The study expands on the work of Yang et al. (2023), which specifically focused on somatostatin (SST) neurons of the CeA. Thus, this study broadens the scope to other neuronal subtypes, demonstrating that CeA neurons in general are predominantly tuned to valence representations rather than salience.

We thank the reviewer for their insightful comments and assessment of the manuscript.

Strengths:

One of the key strengths of the study is its rigorous quantitative approach based on the "circular-shift method", which carefully assesses correlations between neural activity and behavior-related variables. The authors' findings that neuronal responses to the unconditioned stimulus (US) change with learning are consistent with previous studies (Yang et al., 2023). They also show that the encoding of positive and negative valence is not influenced by prior training order, indicating that prior experience does not affect how these neurons process valence.

Weaknesses:

However, there are limitations to the analysis, including the lack of population-based analyses, such as clustering approaches. The authors do not employ hierarchical clustering or other methods to extract meaning from the diversity of neuronal responses they recorded. Clustering-based approaches could provide deeper insights into how different subpopulations of neurons contribute to emotional processing. Without these methods, the study may miss patterns of functional specialization within the neuronal populations that could be crucial for understanding how valence and salience are encoded at the population level.

We appreciate the reviewer’s comments regarding clustering-based approaches. In order to classify cells as responsive to the US or CS we chose to develop a statistically rigorous method for classifying cell response types. Using this approach, we were able to define cell responses to the US and CS. Importantly, we identified 8 distinct response types to the USs. It is not clear how additional clustering analysis would improve cell classifications.

Furthermore, while salience encoding is inferred based on responses to stimuli of opposite valence, the study does not test whether these neuronal responses scale with stimulus intensity-a hallmark of classical salience encoding. This limits the conclusions that can be drawn about salience encoding specifically.

As stated above, we used salience classifications similar to those previously described (Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031; Stephenson-Jones et al., 2020, doi: 10.1016/j.neuron.2019.12.006; Zhu et al., 2018, doi: 10.1126/science.aat0481; and Comoli et al., 2003, doi: 10.1038/nn1113P). We agree that varying the stimulus intensity would provide a more rigorous assessment of salience encoding; however, several of the studies mentioned above classify cells as salience encoding without varying stimulus intensity. Additionally, the inclusion of recordings with varying US intensities on top of the Pavlovian reward and fear conditioning would further decrease the number of cells that can be longitudinally tracked and would likely decrease the number of cells that could be classified.

In sum, while the study makes valuable contributions to our understanding of CeA function, the lack of clustering-based population analyses and the absence of intensity scaling in the assessment of salience encoding are notable limitations.

Reviewer #4 (Public review):

Summary:

The authors have performed endoscopic calcium recordings of individual CeA neuron responses to food and shock, as well as to cues predicting food and shock. They claim that a majority of neurons encode valence, with a substantial minority encoding salience.

Strengths:

The use of endoscopic imaging is valuable, as it provides the ability to resolve signals from single cells, while also being able to track these cells across time. The recordings appear well-executed, and employ a sophisticated circular shifting analysis to avoid statistical errors caused by correlations between neighboring image pixels.

Weaknesses:

My main critique is that the authors didn't fully test whether neurons encode valence. While it is true that they found CeA neurons responding to stimuli that have positive or negative value, this by itself doesn't indicate that valence is the primary driver of neural activity. For example, they report that a majority of CeA neurons respond selectively to either the positive or negative US, and that this is evidence for "type I" valence encoding. However, it could also be the case that these neurons simply discriminate between motivationally relevant stimuli in a manner unrelated to valence per se. A simple test of this would be to check if neural responses generalize across more than one type of appetitive or aversive stimulus, but this was not done. The closest the authors came was to note that a small number of neurons respond to CS cues, of which some respond to the corresponding US in the same direction. This is relegated to the supplemental figures (3 and 4), and it is not noted whether the the same-direction CS-US neurons are also valence-encoding with respect to different USs. For example, are the neurons excited by CS-food and US-food also inhibited by shock? If so, that would go a long way toward classifying at least a few neurons as truly encoding valence in a generalizable way.

As stated above, valence and salience encoding were defined similar to what has been previously reported (Li et al., 2019, doi: 10.7554/eLife.41223; Yang et al., 2023, doi: 10.1038/s41586-023-05910-2; Huang et al., 2024, doi: 10.1038/s41586-024-07819; Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031; Stephenson-Jones et al., 2020, doi: 10.1016/j.neuron.2019.12.006; Zhu et al., 2018, doi: 10.1126/science.aat0481; and Comoli et al., 2003, doi: 10.1038/nn1113P). As reported in Figure 5 and Figure 5 – Supplement 3, ~29% of CeA neurons responded to both food and shock USs (15% in the same direction and 13.5% in the opposite direction). In contrast, only 6 of 303 cells responded to both the CSfood and CSshock, all in the same direction.

A second and related critique is that, although the authors correctly point out that definitions of salience and valence are sometimes confused in the existing literature, they then go on themselves to use the terms very loosely. For example, the authors define these terms in such a way that every neuron that responds to at least one stimulus is either salience or valence-encoding. This seems far too broad, as it makes essentially unfalsifiable their assertion that the CeA encodes some mixture of salience and valence. I already noted above that simply having different responses to food and shock does not qualify as valence-encoding. It also seems to me that having same-direction responses to these two stimuli similarly does not quality a neuron as encoding salience. Many authors define salience as being related to the ability of a stimulus to attract attention (which is itself a complex topic). However, the current paper does not acknowledge whether they are using this, or any other definition of salience, nor is this explicitly tested, e.g. by comparing neural response magnitudes to any measure of attention.

As stated in response to reviewer 2, we longitudinally tracked cells on the first day of Pavlovian reward conditioning the fear conditioning day. Although there were considerably fewer head entries on the first day of reward conditioning, we were able to identify 10 cells that were activated by both the food US and shock US. We compared the responses to the first five head entries and last head entries and the first 5 shocks and last five shocks. Consistent with what has been reported for salience encoding neurons in the basal forebrain (Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031), we observed that the responses were highest when the US was most unexpected and decreased in later trials.

The impression I get from the authors' data is that CeA neurons respond to motivationally relevant stimuli, but in a way that is possibly more complex than what the authors currently imply. At the same time, they appear to have collected a large and high-quality dataset that could profitably be made available for additional analyses by themselves and/or others.

Lastly, the use of 10 daily sessions of training with 20 trials each seems rather low to me. In our hands, Pavlovian training in mice requires considerably more trials in order to effectively elicit responses to the CS. I wonder if the relatively sparse training might explain the relative lack of CS responses?

It is possible that learning would have occurred more quickly if we had used greater than 20 trials per session. However, we routinely used 20-25 trials for Pavlovian reward conditioning (doi: 10.1073/pnas.1007827107; doi: 10.1523/JNEUROSCI.5532-12.2013; doi: 10.1016/j.neuron.2013.07.044; and doi: 10.1016/j.neuron.2019.11.024).

eLife Assessment

This useful work reveals differential activity to food and shock outcomes in central amygdala GABAergic neurons. Evidence supports claims of unconditioned stimulus activity that changes with learning. Compelling evidence that the circular shift method rigorously identifies functional neuron types is also presented. However, the evidence regarding claims related to valence or salience signaling in these neurons is incomplete. This work will be of interest to neuroscientists studying sensory processing and learning in the amygdala.

Reviewer #2 (Public review):

This study presents valuable insight on how neurons within the central amygdala may broadly encode the valence of emotional stimuli. The evidence supporting most of the authors' conclusion is solid, although some of the claims should be treated with caution due to potential alternative interpretation of the data.

In this revised manuscript the authors have addressed the reviewers' critiques in a way that acknowledges the feedback but does not fully embrace or rigorously address the reviewers' core concerns. Here are the main observations that support this impression:

(1) The authors repeatedly acknowledge the ambiguity in defining "valence" and "salience" in the literature, but their responses don't clarify how they address these terms more rigorously. They seem to justify their operational definitions by citing previous studies but do not address how their definitions impact the clarity and robustness of their findings.

(2) The reviewers highlighted that using stimuli from different sensory modalities without scaling them or including neutral cues limits the ability to distinguish between valence and salience. The authors acknowledge this but argue that using same-modality stimuli would not produce distinct responses. This response doesn't address the reviewers' point about how these design limitations could weaken the conclusions. They seem to rely on citations of similar experimental designs instead of addressing the core critique or proposing additional experiments.

(3) In response to the low number of cue-responsive units and the call for more rigorous behavioral measures (like licking or orienting), the authors provide some data but emphasize statistical rigor over behavioral insights, which was questioned during the initial review. They don't propose any methodological adjustments or consider alternative explanations.

(4) The reviewers suggested clustering or other population-level analyses to understand functional diversity within the central amygdala. The authors argue that their statistical approach was sufficient and don't believe additional clustering analyses would add value. This response seems dismissive, as they don't consider whether population-level insights might reveal patterns that single-cell responses overlook.

Overall, while the authors have responded to each concern, their rebuttals often reference other studies to justify their choices rather than addressing the specific limitations highlighted by the reviewers.

Reviewer #3 (Public review):

Summary:

The authors have performed endoscopic calcium recordings of individual CeA neuron responses to food and shock, as well as to cues predicting food and shock. They claim that a majority of neurons encode valence, with a substantial minority encoding salience.

Strengths:

The use of endoscopic imaging is valuable, as it provides the ability to resolve signals from single cells, while also being able to track these cells across time (though the latter capability was not extensively utilized). Another strength is the use of a sophisticated circular shifting analysis to avoid statistical errors caused by correlations between neighboring image pixels.

Weaknesses:

In the first version of this manuscript, my main critique was that the authors didn't fully test whether neurons encode valence. In their rebuttal, the authors justify their use of the terms valence and salience by citing prior works from different labs:

(1) Li et al., 2019, doi: 10.7554/eLife.41223<br /> (2) Yang et al., 2023, doi: 10.1038/s41586-023-05910-2<br /> (3) Huang et al., 2024, doi: 10.1038/s41586-024-07819<br /> (4) Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031<br /> (5) Stephenson-Jones et al., 2020, doi: 10.1016/j.neuron.2019.12.006<br /> (6) Zhu et al., 2018, doi: 10.1126/science.aat0481<br /> (7) Comoli et al., 2003, doi: 10.1038/nn1113P

Among these, items #1 and #3 primarily discuss valence, while #2, #4, #6, and #7 discuss salience, and #5 discusses both.

Upon reviewing these references, the authors' identification of valence encoding patterns is still problematic, and indeed studies cited above show several lines of evidence for valence encoding that are absent here. For example, item #3 ranked behavioral responses to five different odors in drosophila, from most attractive to most repulsive, and saw neuronal responses correlated with the degree of attraction versus repulsion across all five odors. This is robust evidence for valence encoding that is absent here. Items #1 and #5 above are the other two valence-addressing studies cited, and although those only used one rewarding and one aversive stimulus (in rodents), both also added a neutral cue, and most critically, identified substantial subsets of neurons showing a rank-order response, e.g. either aversion > neutral > reward or aversion < neutral < reward. Again, that level of demonstration of valence encoding is not shown in the current study.

Finally, two of the valence studies above tested responses to omission of reward/punishment, providing yet more evidence of valence encoding that is absent in the current study.

While there is much to like about the current study, the claims of valence encoding appear hard to justify, and should be toned down.

eLife Assessment

This is a valuable study describing an implementation of awake mouse fMRI with implanted head coils at high fields. The evidence presented is convincing, combining technical advances with interesting neuroscience applications showing that mice anticipate stimuli given at regular (but at irregular) intervals.

Reviewer #1 (Public review):

Summary:

The authors bring together implanted radiofrequency coils, high-field MRI imaging, awake animal imaging, and sensory stimulation methods in a technological demonstration. The results are very detailed descriptions of the sensory systems under investigation.

Strengths:

The maps are qualitatively excellent for rodent whole-brain imaging.<br /> The design of the holder and the coil is pretty clever.

Weaknesses:

Some unexpected regions appear on the whole brain maps, and the discussion of these regions is succinct.<br /> The authors do not make the work and effort to train the animals and average the data from several hundred trials apparent enough. This is important for any reader who would like to consider implementing this technology.<br /> The data is not available. This does not let the readers make their own assessment of the results.

Comments on revisions:

All good, I can but only congratulate the authors on a study well done.

Reviewer #2 (Public review):

This work explores the advancement of awake mouse BOLD-fMRI at 14 Tesla. The study introduces custom-implanted RF coils aimed at improving signal-to-noise ratio (SNR) and assesses their performance in detecting responses to stimuli in awake mice. The coils show significant SNR improvements and are a noteworthy innovation. Detailed descriptions of the coil design, including parts lists and diagrams, enhance the reproducibility of the methods. A thorough 5-week acclimation protocol was used to minimize stress and motion during imaging. Stress was primarily evaluated using eye tracking which, in an fMRI setting, is novel and could help move the field forward with further validation (within the context of fMRI experiments). Overall, the authors successfully demonstrate high-resolution awake mouse fMRI with enhanced SNR; thus achieving their primary aim.

This work is likely to significantly impact the field by demonstrating the feasibility of high-quality awake mouse fMRI, potentially leading to more accurate and artifact-free studies of brain function. The detailed methods shared will facilitate replication and adoption by other researchers, promoting standardized practices. The methods and data provided serve as valuable resources for the neuroscience community.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors bring together implanted radiofrequency coils, high-field MRI imaging, awake animal imaging, and sensory stimulation methods in a technological demonstration. The results are very detailed descriptions of the sensory systems under investigation.

Strengths:

- The maps are qualitatively excellent for rodent whole-brain imaging. - The design of the holder and the coil is pretty clever.

Weaknesses:

- Some unexpected regions appear on the whole brain maps, and the discussion of these regions is succinct.

- The authors do not make the work and e ort to train the animals and average the data from several hundred trials apparent enough. This is important for any reader who would like to consider implementing this technology.

- The data is not available. This does not let the readers make their own assessment of the results.

Thank you for the comments on this manuscript. We have provided more detailed discussion of the unexpected regions(page 18 – line 491-494) and training procedures(page7-9 – line 172-236). We also uploaded the datasets to OpenNeuro 

Whisker (https://doi.org/10.18112/openneuro.ds005496.v1.0.1),  Visual (https://doi.org/10.18112/openneuro.ds005497.v1.0.0) and Zenodo:

SNR Line Profile Data & Data Processing Scripts:  (https://zenodo.org/doi/10.5281/zenodo.13821455). 

Reviewer #2 (Public Review):

Summary:

The manuscript by Hike et al. entitled 'High-resolution awake mouse fMRI at 14 Tesla' describes the implementation of awake mouse BOLD-fMRI at high field. This work is timely as the field of mouse fMRI is working toward collecting high-quality data from awake animals. Imaging awake subjects o ers opportunities to study brain function that are otherwise not possible under the more common anesthetized conditions. Not to mention the confounding e  ects that anesthesia has on neurovascular coupling. What has made progress in this area slow (relative to other imaging approaches like optical imaging) is the environment within the MRI scanner (high acoustic noise) - as well as the intolerance of head and body motion. This work adds to a relatively small, but quickly growing literature on awake mouse fMRI. The findings in the study include testing of an implanted head-coil (for MRI data reception). Two designs are described and the SNR of these units at 9.4T and 14T are reported. Further, responses to visual as well as whisker stimulation recorded in acclimated awake mice are shown. The most interesting finding, and most novel, is the observation that mice seem to learn to anticipate the presentation of the stimulus - as demonstrated by activations evident ~6 seconds prior to the presentation of the stimulus when stimuli are delivered at regular intervals (but not when stimuli are presented at random intervals). These kinds of studies are very challenging to do. The surgical preparation and length of time invested into training animals are grueling. I also see this work as a step in the right direction and evidence of the foundations for lots of interesting future work. However, I also found a few shortcomings listed below.

Weaknesses:

(1) The surface coil, although o ering a great SNR boost at the surface, ultimately comes at a cost of lower SNR in deeper more removed brain regions in comparison to commercially available Bruker coils (at room temperature). This should be quantified. A rough comparison in SNR is drawn between the implanted coils and the Bruker Cryoprobe - this should be a quantitative comparison (if possible) - including any di erences in SNR in deeper brain structures. There are drawbacks to the Cryoprobe, which can be discussed, but a more thorough comparison between the implanted coils, and other existing options should be provided (the Cryoprobe has been used previously in awake mouse experiments(Sensory evoked fMRI paradigms in awake mice - Chen, Physiological e ects of a habituation procedure for functional MRI in awake mice using a cryogenic radiofrequency probe – Yoshida, PREVIOUS REFERENCE). Further, the details of how to build the implanted coils should be provided (shared) - this should include a parts list as well as detailed instructions on how to build the units. Also, how expensive are they? And can they be reused?

Thank you for the comment. We did not use a Bruker Cryoprobe for this work but rather a Bruker 4array surface coil. We are unable to compare to a cryoprobe since we do not have access to one for our system. A comparison to previously published data using different scanners could be possible but would require the sequence contain identical parameters to avoid introducing an uncontrollable variable, we are planning to recruit different laboratories to test the implanted RF coils with their existing cryoprobes in the future study. 

We have included an updated figure comparing SNR at different depths across the Bruker 4-array coil and the implanted RF coils. As shown in Supplementary Figure 7B, there is significant SNR enhancement up to 4 mm cortical depth for both single loop and Figure 8 implanted RF coils in comparison to the Bruker 4-array coil.

Author response image 1.

Comparison between implanted and commercial coils. A shows representative coils in the single loop (left) and figure 8 styles (right). Supplementary Table 1 provides a parts list and cost for making these coils and Supplementary Figure 1 provides a circuit diagram to assemble. B presents the SNR line profile values as a function of distance from Pia Matter for each coil tested at 9.4T: commercial phased array surface coil (4 Array), implanted single loop, and implanted figure 8. SNR values were calculated by dividing the signal by the standard deviation of the noise. C-E shows a representative FLASH image with line profile of SNR measurements from each of the coils used to create the graph seen in B. Clear visual improvement in SNR can be seen in figures C-E. C – Commercial phased array. D – Single loop at 9.4T. E – Figure 8 at 9.4T. (N4 array = 6, Nsingle loop = 5, Nfigure 8 = 5)

Additionally, we have added a supplementary figure (supp fig 1) of a circuit diagram, in an effort to disseminate the prototype design of the coils to other laboratories. We have included a detailed parts list with the cost for construction of the coils configured for our scanner(supp table 1). These specifics though would need to be adjusted to the precise field strength/bore size/animal the coil was being built for. As for reusability, the copper wire is cemented to the animal skull and this implantable coil should be considered as consumables for the awake mouse experiments, though the PCB parts can be retrieved.  

(2) In the introduction, the authors state that "Awake mouse fMRI has been well investigated". I disagree with this statement and others in the manuscript that gives the reader the impression that awake experiments are not a challenging and unresolved approach to fMRI experiments in mice (or rodents). Although there are multiple labs (maybe 15 worldwide) that have conducted awake mouse experiments (with varying degrees of success/thoroughness), we are far from a standardized approach. This is a strength of the current work and should be highlighted as such. I encourage the authors to read the recent systematic review that was published on this topic in Cerebral Cortex by Mandino et al. There are several elements in there that should influence the tone of this piece including awake mouse implementations with the Bruker Cryoprobe, prevalence of surgical preparations, and evaluations of stress.

Thank you for the comment. We agree with the reviewer that the current stage of awake mouse fMRI studies remains to be improved.  And, we have revised the Introduction to highlight the state-of-theart of awake mouse fMRI (Page 4 – line 81-88). 

(3) The authors also comment on implanted coils reducing animal stress - I don't know where this comment is coming from, as this has not been reported in the literature (to my knowledge) and the authors don't appear to have evaluated stress in their mice. 

Since question 3 and 4 are highly related to the acclimation procedures, we will answer the two questions together.   

(4) Following on the above point, measures of motion, stress, and more details on the acclimation procedure that was implemented in this study should be included.

We thank the reviewer to raise the animal training issues.  

During the animal training, we have measured both pupil dynamic and eye motion features from training sessions, of which the detailed procedure is described in Methods (page 7-9 – line 172236). 

The training procedure is carried out over a total of 5 weeks with four phases of training: i. Holding animal in hands, ii. Head-fixation and pupillometry, iii. Head-fixation and pupillometry with mockMRI acoustic exposure, iv. Head-fixation and pupillometry with Echo-Planar-Imaging (EPI) in the MR scanner.

Author response table 1.

As shown in Supp Fig 2B, the spectral power of pupil dynamics (<0.02Hz) and eye movements gradually increased as a function of the training time for head-fixed mice exposed to the mock MRI acoustic environment during phase 3.  In phase 4, when head-fixed mice were put into the scanner for the first time, both eye movements and pupil dynamics were initially reduced during scanning but recovered to an acclimated state on Day 2, similar to the level on Day 8 of phase 3.  These behavioral outputs would provide an alternative way to monitor the stress levels of the mice. 

Author response image 2.

The eye movements (A) and power spectra of pupil dynamics (<0.02Hz) (B) change during different training phases.

It should be noted that stress may be related to increased frequency of eye blinking or twitching movements in human subjects(1–3). Whereas, the eyeblink of head-fixed mice has been used for behavioral conditioning to investigate motor learning in normal behaving mice(4–6). Importantly, head-fixed mouse studies have shown that eye movements are significantly reduced compared to the free-moving mice(7). The increased eye movement during acclimation process would indicate an alleviated stress level of the head-fixed mice in our cases. Meanwhile, stress-related pupillary dilation could dominate the pupil dynamics at the early phase of training(8). We have observed a gradually increased pupil dynamic power spectrum at the ultra-slow frequency during phase 3, presenting the alleviated stress-related pupil dilation but recovered pupil dynamics to other factors, including arousal, locomotion, startles, etc. in normal behaving mice.  Despite the extensive training procedure of the present work in comparison to the existing awake mouse fMRI studies (training strategies for awake mice fMRI have been reviewed by Mandino et al. to show the overall training duration of existing studies(9)), the stress remains a confounding factor for the brain functional mapping in head-fixed mice. In particular, a recent study(10) shows that the corticosterone concentration in the blood samples of head-fixed mice is significantly reduced on Day 25 following the training but remains higher than in the control mice. In the discussion section, we have discussed the potential issues of stress-related confounding factors for awake mouse fMRI studies (Page 16 – lines 436-458). 

(1) A. Marcos-Ramiro, D. Pizarro-Perez, M. Marron-Romera, D. Gatica-Perez, Automatic blinking detection towards stress discovery. ICMI 2014 - Proceedings of the 2014 International Conference on Multimodal Interaction 307–310 (2014). https://doi.org/10.1145/2663204.2663239/SUPPL_FILE/ICMI1520.MP4.

(2) M. Haak, S. Bos, S. Panic, L. Rothkrantz, DETECTING STRESS USING EYE BLINKS AND BRAIN ACTIVITY FROM EEG SIGNALS. Lance 21, 76 (2009).

(3) E. Del Carretto Di Ponti E Sessam, Exploring the impact of Stress and Cognitive Workload on Eye Movements: A Preliminary Study. (2023).

(4) S. A. Heiney, M. P. Wohl, S. N. Chettih, L. I. Ru olo, J. F. Medina, Cerebellar-dependent expression of motor learning during eyeblink conditioning in head-fixed mice. J Neurosci 34, 14845–14853 (2014).

(5) S. N. Chettih, S. D. Mcdougle, L. I. Ruffolo, J. F. Medina, Adaptive timing of motor output in the mouse: The role of movement oscillations in eyelid conditioning. Front Integr Neurosci 5, 12996 (2011).

(6) J. J. Siegel, et al., Trace Eyeblink Conditioning in Mice Is Dependent upon the Dorsal Medial Prefrontal Cortex, Cerebellum, and Amygdala: Behavioral Characterization and Functional Circuitry. eNeuro 2, 51–65 (2015).

(7) A. F. Meyer, J. O’Keefe, J. Poort, Two Distinct Types of Eye-Head Coupling in Freely Moving Mice. Current Biology 30, 2116-2130.e6 (2020).

(8) H. Zeng, Y. Jiang, S. Beer-Hammer, X. Yu, Awake Mouse fMRI and Pupillary Recordings in the UltraHigh Magnetic Field. Front Neurosci 16, 886709 (2022).

(9) F. Mandino, S. Vujic, J. Grandjean, E. M. R. Lake, Where do we stand on fMRI in awake mice? Cereb Cortex 34 (2024).

(10) K. Juczewski, J. A. Koussa, A. J. Kesner, J. O. Lee, D. M. Lovinger, Stress and behavioral correlates in the head-fixed method: stress measurements, habituation dynamics, locomotion, and motor-skill learning in mice. Scientific Reports 2020 10:1 10, 1–19 (2020).

(5) It wasn't clear to me at what times the loop versus "Figure 8" coil was being used, nor how many mice (or how much data) were included in each experiment/plot. There is also no mention of biological sex.

Thank you for the comment. We have clarified sex and number. The figure 8 coil was only used as part of development to show the improvement of the coil design for cortical measurements. The detailed information is described in Method (Page 6 – line 127-129 & Page 10 – line 269-270). Additionally animal numbers have been included in the figure captions.

(6) Building on the points above, the manuscript overall lacks experimental detail (especially since the format has the results prior to the methods).

Thank you for the comment. We have modified the manuscript to increase the experimental detail and moved the methods section before the results.

(7) An observation is made in the manuscript that there is an appreciable amount of negative BOLD signal. The authors speculate that this may come from astrocyte-mediated BOLD during brain state changes (and cite anesthetized rat and non-human primate experiments). This is very strange to me. First, the negative BOLD signal is not plotted (please do this), further, there are studies in awake mice that measure astrocyte activation eliciting positive BOLD responses (see Takata et al. in Glia, 2017).

We thank the reviewer to raise the negative BOLD fMRI observation issue.  We added a subplot of the negative BOLD signal changes in the revised Figure 4. This negative BOLD signals across cortical areas could be coupled with brain state changes upon air-pu -induced startle responses. Our future studies are focusing on elucidating the brain-wide activity changes of awake mice with fMRI.  We also provide a detailed discussion of the potential mechanism underlying the negative BOLD fMRI signals. First, as reported in the paper (suggested  by the reviewer),  astrocytic Ca2+ transients coincide with positive BOLD responses in the activated cortical areas, which is aligning with the neurovascular coupling (NVC) mechanism. However, there is emerging evidence to show that astrocytic Ca2+ transients are coupled with both positive and negative BOLD responses in anesthetized rats(11) and awake mice(12). An intriguing observation is that cortex-wide negative BOLD signals coupled with the spontaneous astrocytic Ca2+ transients could co-exist with the positive BOLD signal detected at the activated cortex.  Studies have shown that astrocytes are involved in regulating brain state changes(13), in particular, during locomotion(14) and startle responses(15). These brain state-dependent global negative BOLD responses are also related to the arousal changes of both non-human primates(16) and human subjects(17).  The established awake mouse fMRI platform with ultra-high spatial resolution will enable the brain-wide activity mapping of the functional nuclei contributing to the brain state changes of head-fixed awake mice in future studies. (Page 17-18 – Line 478-490)

(11) M. Wang, Y. He, T. J. Sejnowski, X. Yu, Brain-state dependent astrocytic Ca2+ signals are coupled to both positive and negative BOLD-fMRI signals. Proc Natl Acad Sci U S A 115, E1647–E1656 (2018).

(12) C. Tong, Y. Zou, Y. Xia, W. Li, Z. Liang, Astrocytic calcium signal bidirectionally regulated BOLD-fMRI signals in awake mice in Proc. Intl. Soc. Mag. Reson. Med. 32, (2024).

(13) K. E. Poskanzer, R. Yuste, Astrocytes regulate cortical state switching in vivo. Proc Natl Acad Sci U S A 113, E2675–E2684 (2016).

(14) M. Paukert, et al., Norepinephrine controls astroglial responsiveness to local circuit activity. Neuron 82, 1263–1270 (2014).

(15) R. Srinivasan, et al., Ca2+ signaling in astrocytes from IP3R2−/− mice in brain slices and during startle responses in vivo. Nat Neurosci 18, 708 (2015).

(16) C. Chang, et al., Tracking brain arousal fluctuations with fMRI. Proc Natl Acad Sci U S A 113, 4518– 4523 (2016).

(17) B. Setzer, et al., A temporal sequence of thalamic activity unfolds at transitions in behavioral arousal state. Nat Commun 13 (2022).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I really enjoyed this work. The maps shown are among the best-quality maps out there. Here are suggestions to the authors.

(1) Both the ACA and VRA are rather unexpected. The authors explain these briefly as being part of the associative cortical areas. Both the ACA and VRA are not canonical associative areas (or at least not to us). This warrants a stronger discussion.

To verify both ACA and VRA as associate areas, we provide the  connectivity map projections from the Allen Brain Atlas (seen below). These projections are derived from a Cre-dependent AAV tracing of axonal projections. We have included an explanation of this in the introduction. 

Author response image 3.

Representative images are shown indicating connections between the barrel cortex and retrosplenial area from an injection in the barrel cortex (Left panel) as well as the visual cortex and cingulate connection from an injection in the visual cortex (Right panel). Images are of connectivity map projections from the Allen Brain Atlas derived from a Cre-dependent AAV tracing of axonal projections

(2) This is a lot of work. But looking at the figures, this is not obvious. We read in the caption that several hundred trials were used. It would be good to also specify how many mice. It would be clearer to represent this info in the figure as well to support the fact that this is not a trivial acquisition.

Thank the reviewer to raise the e ort issue. We have edited the figure to include this information and included the numbers in the text as well

(3) The training protocol is seemingly extensive, but this is only visible by following another reference. Including a description in this work would help the reader make sense of the effort that went into this work.

We thank the reviewer to raise the training protocol issue. We have more thoroughly discussed the training method used for this study (page 7-9 – line 172-236)

(4) I really would love to see that dataset made freely available - this should be the norm.

The datasets have been uploaded to OpenNeuro 

Whisker (https://doi.org/10.18112/openneuro.ds005496.v1.0.1),  Visual (https://doi.org/10.18112/openneuro.ds005497.v1.0.0) and Zenodo:

SNR Line Profile Data & Data Processing Scripts: 

(https://zenodo.org/doi/10.5281/zenodo.13821455). 

(page 21 – line 573-579)

Reviewer #2 (Recommendations For The Authors):

(1) I'm a little confused about the stimulation paradigm and the effect of it causing an effective 2second TR (which is on the long side) - please elaborate (a figure might be helpful). The paradigm for visual stimulation also seems elaborate, can you please explain the logic and how it was developed?

Thank you for raising the detailed stimulation paradigm issues. The stimulation paradigm is independent and does not interfere with the setup of the effective 2-second TR. The 2-second TR is based on the usage of 2-segment EPI, each with a TR of 1-second. The application of 2-segment paradigm enables the echo spacing with 0.52 ms with effective image bandwidth with 3858Hz, assuring less image distortion.  The stimulation paradigm was defined by an “8s on, 32s o ” epoch such to elicit a strong BOLD response and could be used for any reasonable TR duration. 

We have included a figure outlining the stimulation paradigm (Supp Fig. 3)

(2) I had difficulties viewing the movies (on my MAC).

Thank you for this note. We have re-upload the videos in .mov format

eLife Assessment

This study presents valuable findings on the role of the satiety hormone cholecystokinin typically associated with feeding in the control of a pituitary hormone, FSH, which is a critical regulator of reproductive physiology. The authors provide solid pharmacological evidence that cholecystokinin is sufficient to regulate FSH and compelling genetic evidence that one of its receptors is required for gonadal development, with uncertainties remaining about the physiological regulation and necessity of the peptide. The work will be of interest to reproductive biologists, especially those with an interest in the endocrine control of fertility.

Reviewer #2 (Public review):

Summary:

This manuscript builds on previous work suggesting that the CCK peptide is the releasing hormone for FSH in fishes, which is different than that observed in mammals where both LH and FSH release are under the control of GnRH. Based on data using calcium imaging as a readout for stimulation of the gonadotrophs, the researchers present data supporting the hypothesis that CCK stimulates FSH-containing cells in the pituitary. In contrast LH containing cells show a weak and variable response to CCK, but are highly responsive to GnRH. Data are presented that support the role of CCK in release of FSH. Researchers also state the functional overlap exists in the potency of GnRH to activate FSH cells, thus the two signalling pathways are not separate.<br /> The results are of interest to the field because for many years the assumption has been that fishes use the same signalling mechanism. These data present an intriguing variation where a hormone involved in satiation acts in the control of reproduction.

Strengths:

The strengths of the manuscript are that researchers have shed light on different pathways controlling reproduction in fishes.

Weaknesses:

Weaknesses are that it is not clear if multiple ligand/receptors are involved (more than one CCK and more than one receptor?). The imaging of the CCK terminals and CCK receptors needs to be reinforced.

Comments on revisions:

The authors have responded to the comments with clarity and have made the important requested changes such as clarifying the CCK receptors (their expression and exactly which receptor was targeted), and emphasizing the interactions of CCK, namely that CCK induces LH secretion, but not to the same extent as FSH. All minor comments directed to the layout of the figures and text have been addressed. In summary, comments have been addressed satisfactorily.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The pituitary gonadotropins, FSH and LH, are critical regulators of reproduction. In mammals, synthesis and secretion of FSH and LH by gonadotrope cells are controlled by the hypothalamic peptide, GnRH. As FSH and LH are made in the same cells in mammals, variation in the nature of GnRH secretion is thought to contribute to the differential regulation of the two hormones. In contrast, in fish, FSH and LH are produced in distinct gonadotrope populations and may be less (or differently) dependent on GnRH than in mammals. In the present manuscript, the authors endeavored to determine whether FSH may be independently controlled by a distinct peptide, cholecystokinin (CCK), in zebrafish.

Strengths:

The authors demonstrated that the CCK receptor is enriched in FSH-producing relative to LH-producing gonadotropes, and that genetic deletion of the receptor leads to dramatic decreases in gonadotropin production and gonadal development in zebrafish. Also, using innovative in vivo and ex vivo calcium imaging approaches, they show that LH- and FSH-producing gonadotropes preferentially respond to GnRH and CCK, respectively. Exogenous CCK also preferentially stimulated FSH secretion ex vivo and in vivo.

Weaknesses:

The concept that there may be a distinct FSH-releasing hormone (FSHRH) has been debated for decades. As the authors suggest that CCK is the long-sought FSHRH (at least in fish), they must provide data that convincingly leads to such a conclusion. In my estimation, they have not yet met this burden. In particular, they show that CCK is sufficient to activate FSH-producing cells, but have not yet demonstrated its necessity. Their one attempt to do so was using fish in which they inactivated the CCK receptor using CRISPR-Cas9. While this manipulation led to a reduction in FSH, LH was affected to a similar extent. As a result, they have not shown that CCK is a selective regulator of FSH.

Our conclusion regarding the necessity of CCK signaling for FSH secretion is based on the following evidence:

(1) CCK-like receptors are expressed in the pituitary gland predominantly on FSH cells.

(2) Application of CCK to pituitaries elicits FSH cell activation and to a much lesser degree activation of LH cells.  (calcium imaging assays)

(3) Application of CCK to pituitaries and by injections in-vivo significantly increased only FSH release.

(4) Mutating the FSH-specific CCK receptor in a different species of fish (medaka) also causes a complete shutdown of FSH production and phenocopies a fsh-mutant phenotype (Uehara, Nishiike et al. 2023).

Taken together, we believe that this data strongly supports the conclusion that CCK is necessary for FSH production and release from the fish pituitary. Admittedly, the overlapping effects of CCK on both FSH and LH cells in zebrafish (evident in both our calcium imaging experiments and especially in the KO phenotype) complicates the interpretation of the phenotype. We speculate that the effect of CCK on LH cells in zebrafish can be caused either by paracrine signaling within the gland or by the effects of CCK on GnRH neurons that were shown to express CCK receptors .

In the current version, we emphasize that CCK also induces LH secretion. Although it does not affect LH to the same extent as FSH, an overlap does exist. This is mentioned in the abstract and discussion.

Moreover, they do not yet demonstrate that the effects observed reflect the loss of the receptor's function in gonadotropes, as opposed to other cell types.

Although there is evidence for the expression of CCK receptor in other tissues, we do show a direct decrease of FSH and LH expression in the gonadotrophs of the pituitary of the mutant fish; taken together with its significant expression in FSH cells compared to the rest of the cells of the pituitary in the cell specific transcriptomic, it is the most reasonable explanation for the mutant phenotype.

Unfortunately, unlike in mice, technologies for conditional knockout of genes in specific cell types are not yet available for our model and cell types. Additional tissue distribution of the three receptors types of CCK was added in supplementary figure 1, from this tissue distribution it can be appreciated how in the pituitary only CCKBRA (our identified CCK receptor) is expressed, while in other tissues it is either not expressed or expressed with the additional CCK receptors that can compensate its activity.

It also is not clear whether the phenotypes of the fish reflect perturbations in pituitary development vs. a loss of CCK receptor function in the pituitary later in life. Ideally, the authors would attempt to block CCK signaling in adult fish that develop normally. For example, if CCK receptor antagonists are available, they could be used to treat fish and see whether and how this affects FSH vs. LH secretion.

While the observed gonadal phenotype of the KO (sex inversed fish) should have a developmental origin since it requires a long time to manifest, the effect of the KO on FSH and LH cells is probably more acute. Unfortunately a specific antagonist that affect only CCKRBA and not the other CCK receptors wasn’t identified yet.

In the Discussion, the authors suggest that CCK, as a satiety factor, may provide a link between metabolism and reproduction. This is an interesting idea, but it is not supported by the data presented. That is, none of the results shown link metabolic state to CCK regulation of FSH and fertility. Absent such data, the lengthy Discussion of the link is speculative and not fully merited.

In the revised manuscript, we provided data to link cck with metabolic status in supplementary figure 1 and modified the discussion to tone down the link between metabolic status to and reproductive state.

Also in the Discussion, the authors argue that "CCK directly controls FSH cells by innervating the pituitary gland and binding to specific receptors that are particularly abundant in FSH gonadotrophs." However, their imaging does not demonstrate innervation of FSH cells by CCK terminals (e.g., at the EM level).

Innervation of the fish pituitary does not imply a synaptic-like connection between axon terminals and endocrine cells. In fact, such connections are extremely rare, and their functionality is unclear. Instead, the mode of regulation between hypothalamic terminals and endocrine cells in the fish pituitary is more similar to "volume transmission" in the CNS, i.e. peptides are released into the tissue and carried to their endocrine cell targets by the circulation or via diffusion. A short explanation was added in lines 395-398 in the discussion

Moreover, they have not demonstrated the binding of CCK to these cells. Indeed, no CCK receptor protein data are shown.

Our revised manuscript  includes detailed experiments showing the activation of the receptor by its homologous ligand, supplementary Figure 1 includes a transactivation  assay of CCK to its receptor and the effect of the different mutants on the activation of the receptor. Unfortunately, no antibody is available against this fish specific receptor (one of the caveats of working with fish models); therefore, we cannot present receptor protein data.

The calcium responses of FSH cells to exogenous CCK certainly suggest the presence of functional CCK receptors therein; but, the nature of the preparations (with all pituitary cell types present) does not demonstrate that CCK is acting directly in these cells.

We agree with the reviewer that there are some disadvantages in choosing to work with a whole-tissue preparation. However, we believe that the advantages of working in a more physiological context far outweigh the drawbacks as it reflects the natural dynamics more precisely. Since our transcriptome data, as well as our ISH staining, show that the CCK receptor is exclusively expressed in FSH cells, it is improbable that the observed calcium response is mediated via a different pituitary cell type.

Indeed, the asynchrony in responses of individual FSH cells to CCK (Figure 4) suggests that not all cells may be activated in the same way. Contrast the response of LH cells to GnRH, where the onset of calcium signaling is similar across cells (Figure 3).

The difference between the synchronization levels of LH and FSH cells activity stems from the gap-junction mediated coupling between LH cells that does not exist between FSH cells(Golan, Martin et al. 2016). Therefore, the onset of calcium response in FSH cells is dependent on the irregular diffusion rate of the peptide within the preparation, whereas the tight homotypic coupling between LH cells generates a strong and synchronized calcium rise that propagates quickly throughout the entire population

The differences in connectivity between LH and FSH cells is mentioned in lines 194-195

Finally, as the authors note in the Discussion, the data presented do not enable them to conclude that the endogenous CCK regulating FSH (assuming it does) is from the brain as opposed to other sources (e.g., the gut).

We agree with the reviewer that, for now, we are unable to determine whether hypothalamic or peripheral CCK are the main drivers of FSH cells. While the strong innervation of the gland by CCK-secreting hypothalamic neurons strengthens the notion of a hypothalamic-releasing hormone and also fits with the dogma of the neural control of the pituitary gland in fish (Ball 1981), more experiments are required to resolve this question.

Reviewer #2 (Public Review):

Summary:

This manuscript builds on previous work suggesting that the CCK peptide is the releasing hormone for FSH in fishes, which is different than that observed in mammals where both LH and FSH release are under the control of GnRH. Based on data using calcium imaging as a readout for stimulation of the gonadotrophs, the researchers present data supporting the hypothesis that CCK stimulates FSH-containing cells in the pituitary. In contrast, LH-containing cells show a weak and variable response to CCK but are highly responsive to GnRH. Data are presented that support the role of CCK in the release of FSH. Researchers also state that functional overlap exists in the potency of GnRH to activate FSH cells, thus the two signalling pathways are not separate. The results are of interest to the field because for many years the assumption has been that fishes use the same signalling mechanism. These data present an intriguing variation where a hormone involved in satiation acts in the control of reproduction.

Strengths:

The strengths of the manuscript are that researchers have shed light on different pathways controlling reproduction in fishes.

Weaknesses:

Weaknesses are that it is not clear if multiple ligand/receptors are involved (more than one CCK and more than one receptor?). The imaging of the CCK terminals and CCK receptors needs to be reinforced.

Reviewer consultation summary: 

The data presented establish sufficiency, but not necessity of CCK in FSH regulation. The paper did not show that CCK endogenously regulates FSH in fish. This has not been established yet.

This is a very important comment, also raised by reviewer 1. To avoid repetition, please see our detailed response to the comment above.

The paper presents the pharmacological effects of CCK on ex vivo preparations but does not establish the in vivo physiological function of the peptide. The current evidence for a novel physiological regulatory mechanism is incomplete and would require further physiological experiments. These could include the use of a CCK receptor antagonist in adult fish to see the effects on FSH and LH release, the generation of a CCK knockout, or cell-specific genetic manipulations.

As detailed in the responses to the first reviewer, we cannot conduct conditional, cellspecific gene knockout in our model. However we did conducted KO and show the direct effect on FSH and LH secretion together with physiological characterisation of the mutant.

Zebrafish have two CCK ligands: ccka, cckb and also multiple receptors: cckar, cckbra and cckbrb. There is ambiguity about which CCK receptor and ligand are expressed and which gene was knocked out.

In the revised manuscript, we clarified which of the receptors are expressed (CCKRBA) and which receptor is targeted. We also provided data showing the specificity of the receptors (both WT and mutant) to the ligands. Supplementary 1 shows receptor cross-activation. The method also specifies the exact NCBI ID numbers of the targeted receptor and the antibody used for the immunostaining.

Blocking CCK action in fish (with receptor KO) affects FSH and LH. Therefore, the work did not demonstrate a selective role for CCK in FSH regulation in vivo and any claims to have discovered FSHRH need to be more conservative.

We agree with the reviewer that the overlap in the effect of CCK measured in the calcium activation of cells and in the KO model does not allow us to conclude selectivity. In this context, it is crucial to highlight that CCKRBA exhibits high expression on FSH cells but not on LH cells. Therefore, the effect of CCK on LH cells is likely paracrine or through GnRH neurons that were shown to express CCK receptors. In the current version, we emphasize that CCK also induces LH secretion. Although it does not affect LH to the same extent as FSH, an overlap does exist. This is mentioned in the abstract and discussion.

The labelling of the terminals with anti-CCK looks a lot like the background and the authors did not show a specificity control (e.g. anti-CCK antibody pre-absorbed with the peptide or anti-CCK in morphant/KO animals).

Figures colours had been updated to better visualise the specific staining of the antibody. Also, The same antibody had been previously used to mark CCK-positive cells in the gut of the red drum fish(Webb, Khan et al. 2010) , where a control (pre-absorbed with the peptide) experiment had been conducted.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Abstract:

The authors have not yet established that CCK is the primary regulator of FSH in vivo.

In the new version, we highlight the leading effect of CCK on the reproductive axis, which includes FSH and LH.

Introduction:

The authors need to make clear earlier in the Introduction that fish have two types of gonadotropes. This information comes too late (last paragraph) currently.

Added in line 42

They should discuss relevant data on the differential regulation of FSH and LH in fish, as a rationale for looking for different releasing factors.

This has been discussed in the first paragraph of the introduction

In the last sentence of the penultimate paragraph, the authors assume that it must be a hypothalamic factor that regulates FSH. Why is this necessarily the case? Are there data indicating that a hypothalamic factor is required for FSH production in fish?

This has been mentioned in the discussion, we do not deny that circulating CCK or CCK from other brain areas might affect FSH secretion in the pituitary (line 402-404). However, as the hypothalamus serves as the main gateway from the brain to the pituitary and contains hypophysiotropic CCK neurons it is the most reasonable assumption.

Results:

In the first paragraph, the authors reference three types of CCK receptors, only one of which is expressed in the pituitary. The specific receptor should be named here.

The receptor name and NCBI id had been added in this paragraph.

Figure 1: What specificity controls were used for the ISH in Figure 1?

HCR- The method used to identify RNA expression and developed by Molecular Instruments (https://www.molecularinstruments.com/hcr-rnafish-protocols), do not require specific control as had been previously done with older ISH methods. The use of multiple short probes assure the specificity to the RNA.More over the expression is specific to the targeted cells.

In Figure 1D, the red square is missing in the KO fish (at low magnification).

This was fixed in the updated version.

In Figure 1G, the number of dots does not correspond to the number of animals described in the figure legend. Does each point represent an animal?

Each dot represent a fish. The order of the numbers in the legend didn’t match the order in the graph, this had been fixed in the last version

Figure 2A: It is not clear that all FSH (GFP) cells are double-labeled. Should all double-labeled cells appear white? Many appear as green. Some quantification of the proportion of co-labeling is needed. Also, the scale bars are too small to read. Perhaps add the size of the scale bars to the legend.

They are all double-labeled, as can be seen by the single-color images, since GFP fluorescence is stronger than RCaMP fluorescence, the double-labelling might be seen a green cells; a scale bar was added.

Figure 2C: Is the synchronous activity of LH cells here dependent on endogenous GnRH? Can these events be blocked with a GnRH receptor antagonist?

We currently do not have enough data to support this hypothesis and the in vivo 2 photon system is not optimal to answer these questions since these are spontaneous events which are difficult to predict. This is the main reason we moved to an ex vivo system. The similar response we receive when applying GnRH in the ex vivo system support it is GnRH activation.

Figure 4C: As some LH cells respond to CCK, can the authors really claim that CCK is a selective regulator of FSH? What explains the heterogeneity in the response of LH cells to CCK?

In this version, we highlight that CCK directly activates FSH but it is also affecting LH to some extent. However it is clear that the effect on FSH cells is more significant.

Figures 5A and B: With larger Ns, some of the trends might be significant (e.g., GnRH stimulated FSH release and CCK stimulated LH release).

Though there is a trend, the values in the Y axis reveal that the trend of response of FSH to GnRH and LH to CCK is lower then the distribution of the basal response (the before) in all of the graphs. Hence we do not believe a larger N will affect those results. We added the range of the secreted hormones concentrations in the result description to emphasize the difference in values,

Figures 5C and D: What explains the lack of an increase in LH secretion following GnRH treatment?

We did not measure LH Secretion in the plasma as we didn’t have enough blood, we do see an increase in LH transcription (see supplementary figure 5 – figure supplement 1)

Also, as mRNA levels were measured (in C), reference should be made to expression rather than transcription. Not all changes in mRNA levels reflect changes in transcription.Also, remove transcription from the legend. Reference to supplementary Figure 4 in the legend should be supplementary Figure 6. Finally, in C and D, distinguish males from females (as in 5A and B).

Modifications had been done according to the reviewer suggestions.

Figure legends:

The figure legends are very long. One way to shorten them is to remove descriptions of the results. The legends should indicate what is in each figure, not the results of the experiments.

Modifications had been done according to the reviewer suggestions.

Sample sizes should be spelled out in the legends, as they are not in the M&M.

We made sure all sample sizes are mentioned in the legend

Materials and Methods:

Section 1.1 can be removed as it repeats content presented elsewhere.

This section was removed

Section 1.5: It is unclear what this means: "blinding was not applied to ensure tractability" Please clarify.

This section was removed

Reviewer #2 (Recommendations For The Authors):

It appears that zebrafish have two ligands: ccka, cckb. Also multiple receptors: cckar, cckbra and cckbrb. Authors need to discuss this and clearly state which ligand and which receptor they are referring to in the manuscript.

We discussed the receptor type in the first paragraph of the results, the exact synthetic peptide used is described in the methods. The 8 amino acids of the mature CCK peptide are the same between CCKa and CCKb. A sentence regarding the specificity of the antibody to the mature CCK peptide was added in line 101.

"to GnRH puff application (300 μl of 30 μg/μl)"; (250 μl of 30 μg/ml CCK)

Please give the final concentration to make it easy on the readers of the data.

The molarity of the final concentration was added.

(2.4) Differential calcium response underlies differential hormone. This section is a bit confusing to read, for example:

"For that, we collected the medium perfused through our ex vivo system (Fig. 2a) and measured LH and FSH levels using a specific ELISA validated for zebrafish [31] while monitoring the calcium activity of the cells."

So the authors did the ELISA while monitoring the activity (?). This sentence does not make sense: please rewrite it.

We modified this sentence  in line 308-311

To functionally validate the importance of CCK signalling we used CRISPR-cas9 to generate loss-of-function (LOF) mutations in the pituitary- CCK receptor gene.

The authors need to clearly state WHICH gene they inactivated: Zebrafish have three CCK-receptors, so "the pituitary receptor gene" needs to be defined.

Was added again in line 107, and is mentioned in the methods

Figure 3 is a crucial figure!

Figure 3B: The data are not very convincing. Please state how thick the sections are in the figure legend (assuming these are adult pituitaries),

Added in the legend (figure 1C in the new version), slice thickness and adult fish.

Please show at least the merged image a high magnification view of the co-localization of the receptor with the cells.

This is figure 1 in the new revision, a magnified figure was added

Please give the scale bar size for 3B.

Scales for all images were added

Figure 3C: the co-localization of the terminals of the CCK and FSH cells shows very few cells expressing close to terminals.

Important: Because the labelling of the terminals with anti-CCK looks a lot like the background, it is very important to show the control (anti-CCK antibody pre-absorbed with the peptide). The authors should have these data. The photo needs to have been taken at the same gain (contrast) and the photo showing the terminals.

This is  a commercial antibody that had been previously validated for CCK in fish. The co-localization pattern resembles GnRH innervation in the pituitary. In fish when hypothalamic neurons innervate the pituitary they do not innervate all the cells, as this is an endocrine system, the peptide can travel to neighbouring cells via diffusion or aided blood flow (Golan, Zelinger et al. 2015) ).  The images reveal the direct innervation of CCK in the pituitary and its proximity to FSH cells.

Figure 4c, on right. The text seems to be stretched as if the photo was adjusted without locking the aspect ratio. Please check the original images.

This has been fixed

Can the authors use different pseudo colours? Differentiating a double label of white versus yellow is very difficult, and thus the photo is not very convincing.

This had been changed to green and magenta

What is meant by "CCK-AB" antibody? Perhaps anti-CCK would be a better label

This has been fixed

Figure 5A: increase the magnification of the insets; the structure of the gonads is very difficult to see with clarity in these low mag images. The most obvious way to improve this figure is to reduce or eliminate the pie graph (not really necessary) and show a high magnification (and larger) image of the gonadal structure.

This is figure 1 in the new version, with magnification of the gonad next to each body section.

Discussion:

" Moreover, in the zebrafish, as well as in other species, the functional overlap in gonadotropin signalling pathways is not limited to the pituitary but is also present in the gonad, through the promiscuity of the two gonadotropin receptors"<br /> The reasoning of this sentence is not clear: zebrafish do not use GnRH to control reproduction: they lack GnRH1 through genomic rearrangement (see Whitlock, Postlethwait and Ewer 2019) and KO of GnRH2/GnRH3 does not affect reproduction.

While GnRH KO model indicate a redundancy of GnRH in this axis in zebrafish, there is also ample evidence for its importance in regulating reproduction such as its effect on gonadotropin (Golan, Martin et al. 2016) and its use in spawning inductions in fish (Mizrahi and Levavi-Sivan 2023). We believe it is currently too soon to conclude that GnRH signalling is completely non relevant to reproduction in cyprinids.  

Reviewing Editor (Recommendations For The Authors):

It would be interesting to see calcium imaging experiments in the CCKR receptor mutants to establish a more direct connection between peptide action and activity.

We added a receptor assay that reflect the non-activation of the mutated receptors by CCK (supplementary figure 1) , and compared it to the wild type that is activated. This show that: 1) CCK directly activate our identified receptor in FSH cells. 2) the mutated receptors are non-active.

"all homozygous fish (CCKR+12/+7/-1/ CCKR+12/+7/-1, n=12)"

It may be better to write the genotype of fish separately as CCKR+12/+12, CCKR+7/+7 and CCKR-1/-1, n=12) otherwise it seems as if all alleles occurred together in the same fish.

Modified according to the reviewer request

In Figure 1 scale bar legends are very small. 

Description of the scale bars were added to the all the legends

Figure 1 legend "On the top right of each panel is the gender distribution" - fish have no gender but sex.

Modified according to the reviewer request

The authors should endeavour to improve the presentation of the figures. They should use a sans-serif font and check that text is not cut at the edge of figure panels, that scale bars are uniform and clearly labelled and fonts are of similar size and clearly legible. E.g. labels of the fish brain of Fig3A are very small.

We modified all the figures to adapt the font and the scales, we increased the size of the image in Figure 3a to make the labels clearer.

Please use the elife format to name supplementary figures, as Figure X - Figure Supplement Y (each supplement associated with one of the main figures).

Fixed

Peptide concentrations in the ex vivo experiments should also be given as molar concentrations not only as '250 μl of 30 μg/ml CCK'.

Fixed

"In contrast, FSH cells responded with a very low calcium rise in hormonal secretion in response to GnRH" - a very low rise in hormonal secretion

Fixed

Please clarify why you used a GnRH synthetic agonist and not the native peptide.

It is commonly used for spawning induction in fish (line 245); it has also been shown to directly affect the secretion of LH and FSH (Biran, Golan et al. 2014, Biran, Golan et al. 2014, Mizrahi, Gilon et al. 2019) , added to line 245.

References

Ball, J. (1981). "Hypothalamic control of the pars distalis in fishes, amphibians, and reptiles." General and comparative endocrinology 44(2): 135-170.

Biran, J., M. Golan, N. Mizrahi, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2014). "Direct regulation of gonadotropin release by neurokinin B in tilapia (Oreochromis niloticus)." Endocrinology 155(12): 4831-4842.

Biran, J., M. Golan, N. Mizrahi, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2014). "LPXRFa, the Piscine Ortholog of GnIH, and LPXRF Receptor Positively Regulate Gonadotropin Secretion in Tilapia (Oreochromis niloticus)." Endocrinology 155(11): 4391-4401.

Golan, M., A. O. Martin, P. Mollard and B. Levavi-Sivan (2016). "Anatomical and functional gonadotrope networks in the teleost pituitary." Scientific Reports 6: 23777.

Golan, M., E. Zelinger, Y. Zohar and B. Levavi-Sivan (2015). "Architecture of GnRH-Gonadotrope-Vasculature Reveals a Dual Mode of Gonadotropin Regulation in Fish." Endocrinology 156(11): 4163-4173.

Mizrahi, N., C. Gilon, I. Atre, S. Ogawa, I. S. Parhar and B. Levavi-Sivan (2019). "Deciphering Direct and Indirect Effects of Neurokinin B and GnRH in the Brain-Pituitary Axis of Tilapia." Front Endocrinol (Lausanne) 10: 469.

Mizrahi, N. and B. Levavi-Sivan (2023). "A novel agent for induced spawning using a combination of GnRH analog and an FDA-approved dopamine receptor antagonist." Aquaculture 565: 739095.

Uehara, S. K., Y. Nishiike, K. Maeda, T. Karigo, S. Kuraku, K. Okubo and S. Kanda (2023). "Cholecystokinin is the follicle-stimulating hormone (FSH)-releasing hormone." bioRxiv: 2023.2005.2026.542428.

Webb, K. A., Jr., I. A. Khan, B. S. Nunez, I. Rønnestad and G. J. Holt (2010). "Cholecystokinin: molecular cloning and immunohistochemical localization in the gastrointestinal tract of larval red drum, Sciaenops ocellatus (L.)." Gen Comp Endocrinol 166(1): 152-159.

eLife Assessment

This important work investigates how two distinct processes, morphological changes and synaptic plasticity, contribute to the final shape of neuronal dendrites and the spatial structure of their synaptic inputs. The modelling is convincing and could be broadly applied to other similar questions. The work will be of interest to neuroscientists studying dendritic development and connectivity at a single-cell level.

Reviewer #2 (Public review):

This work combines a model of two-dimensional dendritic growth with attraction and stabilisation by synaptic activity. The authors find that constraining growth models with competition for synaptic inputs produces artificial dendrites that match some key features of real neurons both over development and in terms of final structure. In particular, incorporating distance-dependent competition between synapses of the same dendrite naturally produces distinct phases of dendritic growth (overshoot, pruning, and stabilisation) that are observed biologically and leads to local synaptic organisation with functional relevance. The approach is elegant and well-explained but makes some significant modelling assumptions that might impact the biological relevance of the results.

The main strength of the work is the general concept of combining morphological models of growth with synaptic plasticity and stabilisation. This is an interesting way to bridge two distinct areas of neuroscience in a manner that leads to findings that could be significant for both. The modelling of both dendritic growth and distance-dependent synaptic competition is carefully done, constrained by reasonable biological mechanisms, and well-described in the text. The paper also links its findings, for example in terms of phases of dendritic growth or final morphological structure, to known data well.

The authors have managed to address my previous comments on the paper well by considering axonal dynamics, spatial correlations, and the effects of changing ratios of BDNF-proBDNF. The modelling has now been validated over a wider range of confounding factors and looks to be a solid basis for future work in this direction.

Reviewer #3 (Public review):

The authors propose a mechanistic model of how the interplay between activity-independent growth and an activity-dependent synaptic strengthening/weakening model influences the dendrite shape, complexity, and distribution of synapses. The authors focus on a model for stellate cells with multiple dendrites emerging from a soma. The activity-independent component is provided by a random pool of presynaptic sites representing potential synapses and releasing a diffusible signal promoting dendritic growth. Then, a spontaneous activity pattern with some correlation structure is imposed at those presynaptic sites. The strength of these synapses follows a learning rule previously proposed by the lab: synapses strengthen when there is correlated firing across multiple sites, and synapses weaken if there is uncorrelated firing with the relative strength of these processes controlled by available levels of BDNF/proBDNF. Once a synapse is weakened below a threshold, the dendrite branch at that site retracts and loses its sensitivity to the growth signal.

This revised version of the manuscripts contains clarifications and additional experiments that better reflect the robustness of the model. I continue to maintain my favorable review. I am glad the research persevered the long delays with changing trainees.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review):

The authors introduce a computational model that simulates the dendrites of developing neurons in a 2D plane, subject to constraints inspired by known biological mechanisms such as diffusing trophic factors, trafficked resources, and an activity-dependent pruning rule. The resulting arbors are analyzed in terms of their structure, dynamics, and responses to certain manipulations. The authors conclude that 1) their model recapitulates a stereotyped timecourse of neuronal development: outgrowth, overshoot, and pruning 2) Neurons achieve near-optimal wiring lengths, and Such models can be useful to test proposed biological mechanisms- for example, to ask whether a given set of growth rules can explain a given observed phenomenon - as developmental neuroscientists are working to understand the factors that give rise to the intricate structures and functions of the many cell types of our nervous system. 

Overall, my reaction to this work is that this is just one instantiation of many models that the author could have built, given their stated goals. Would other models behave similarly? This question is not well explored, and as a result, claims about interpreting these models and using them to make experimental predictions should be taken warily. I give more detailed and specific comments below.  

We thank the reviewer for the summary of the work. But the criticism “that this is one instantiation of many models [we] could have built” is unfair as it can apply to any model. We chose one of the most minimalistic models which implements known biological mechanisms including activity-independent and -dependent phases of dendritic growth, and constrained parameters based on experimental data. We compare the proposed model to other alternatives in the Discussion section. In the revised manuscript, we additionally investigate the sensitivity of model output to variations of specific parameters, as explained below.

Point 1.1. Line 109. After reading the rest of the manuscript, I worry about the conclusion voiced here, which implies that the model will extrapolate well to manipulations of all the model components. How were the values of model parameters selected? The text implies that these were selected to be biologically plausible, but many seem far off. The density of potential synapses, for example, seems very low in the simulations compared to the density of axons/boutons in the cortex; what constitutes a potential synapse? The perfect correlations between synapses in the activity groups is flawed, even for synapses belonging to the same presynaptic cell. The density of postsynaptic cells is also orders of magnitude of, etc. Ideally, every claim made about the model's output should be supported by a parameter sensitivity study. The authors performed few explorations of parameter sensitivity and many of the choices made seem ad hoc.  

We have performed detailed sensitivity analysis on the model parameters mentioned by the reviewer, including (I) the density of postsynaptic cells (somatas), (II) the density of potential synapses, and (III) the level of correlations between synapses. 

(I) While the density of postsynaptic cells in our baseline model seems a bit low, at least when compared to densities observed in adulthood (Keller et al., 2018), we explored how altering this value affects the model dynamics. We found that the postsynaptic cell density does not affect the timing of dendritic outgrowth, overshoot and synaptic pruning. It only changes the final size of the dendritic arbor and the resulting number of connected synapses. This analysis is now included in Supplementary Figure 3-2.

(II) The density of potential synapses and the density of connected synapses that we used in the manuscript are already in the range of densities that can be found in the literature (Leighton et al., 2024; Ultanir et al., 2007; Glynn et al., 2011; Yang et al., 2014), some of which we already cited in the original submission.

A potential concern might be that the rapid slowing down of growth in the model could be due to a depletion of potential synapses. To illustrate that this is not the case, we showed that the number of available potential synapses over the time course of the simulations remains high (Figure 3, new panel e). Therefore, the initial density of potential synapses is sufficient and does not affect the final density of connected synapses.

To further illustrate the robustness of our model dynamics to longer simulation times, we added a new supplementary figure (Supplementary Figure 3-1).

These new figure additions (Figure 3e, Supplementary Figure 3-1, and Supplementary Figure 3-2) and their implications for the model dynamics are discussed in the Results section of the revised paper:

p.9 line 198, “After the initial overshoot and pruning, dendritic branches in the model stay stable, with mainly small subbranches continuing to be refined (Figure 3-Figure Supplement 1). This stability in the model is achieved despite the number of potential synaptic partners remaining high (Figure 3e), indicating a balance between activity-independent and activitydependent mechanisms. The dendritic growth and synaptic refinement dynamics are independent of the postsynaptic somata densities used in our simulations (Figure 3-Figure Supplement 2). Only the final arbor size and the number of connected synapses decrease with an increase in the density of the somata, while the timing of synaptic growth, overshoot and pruning remains the same (Figure 3-Figure Supplement 2).”

We also added more details to the description of our model in the Methods section:

p.24 line 615, “For all simulations in this study, we distributed nine postsynaptic somata at regular distances in a grid formation on a 2-dimensional 185 × 185 pixel area, representing a cortical sheet (where 1 pixel = 1 micron, Figure 4). This yields a density of around 300 neurons per 𝑚𝑚2 (translating to around 5,000 per 𝑚𝑚3, where for 25 neurons in Figure 3Figure Supplement 2 this would be around 750 neurons per 𝑚𝑚2 or 20,000 per 𝑚𝑚3). The explored densities are a bit lower than compared to neuron densities observed in adulthood (Keller et al., 2018). In the same grid, we randomly distributed 1,500 potential synapses, yielding an initial density of 0.044 potential synapses per 𝜇𝑚2 (Figure 3e). At the end of the simulation time, around 1,000 potential synapses remain, showing that the density of potential synapses is sufficient and does not significantly affect the final density of connected synapses. Thus, the rapid slowing down of growth in our model is not due to a depletion of potential synaptic partners. The resulting density of stably connected synapses is approximately 0.015 synapses per 𝜇𝑚2 (around 60 synapses stabilized per dendritic tree, Figure 3b). This density compares well to experimental findings, where, especially during early development, synaptic densities are described to be within a range similar to the one observed in our model (Leighton et al., 2024; Ultanir et al., 2007; Glynn et al., 2011; Yang et al., 2014; Koshimizu et al., 2009; Tyler and Pozzo-Miller, 2001).”

(III) Lastly, we investigated how the correlation between synapses of the same activity group might affect our conclusions. As correlations in our model mainly arise from patterns of spontaneous activity which are abundant in early postnatal development (retinal waves (Ackman et al., 2012) or endogenous activity in the form of highly synchronized events involving a large fraction of the cells (Siegel et al., 2012), we explored varying the correlations within each activity group, across activity groups and combinations of both. While this analysis supported our previously described intuition on how competition between synaptic activities should drive activity-dependent refinement, recently a study found direct evidence for such subcellular refinement of synaptic inputs specifically dependent on spontaneous activity between retinal ganglion cell axons and retinal waves in the superior colliculus (Matsumoto et al., 2024). The new analysis confirmed our earlier results that the competition between activity groups leads to activity-dependent refinement and yielded further insight into how the studied activity correlations can affect the competition. Those results are presented in a completely new figure (new Figure 5, supported by the Supplementary Figure 5-1 and 5-2) and discussed in the Results section:

p.11 line 249, “Group activity correlations shape synaptic overshoot and selectivity competition across synaptic groups.

Since correlations between synapses emerge from correlated patterns of spontaneous activity abundant during postnatal development (Ackman et al., 2012; Siegel et al., 2012), we explored a wide range of within-group correlations in our model (Figure 5a). Although a change in correlations within the group has only a minor effect on the resulting dendritic lengths (Figure 5b) and overall dynamics, it can change the density of connected synapses and thus also affect the number of connected synapses to which each dendrite converges throughout the simulations (Figure 5c,e). This is due to the change in specific selectivity of each dendrite which is a result of the change in within-group correlations (Figure 5d). While it is easier for perfectly correlated activity groups to coexist within one dendrite (Figure 5-Figure Supplement 1a, 100%), decreasing within-group correlations increases the competition between groups, producing dendrites that are selective for one specific activity group (60%, Figure 5d, Figure 5-Figure Supplement 1a). This selectivity for a particular activity group is maximized at intermediate (approximately 60%) within-group correlations, while the contribution of the second most abundant group generally remains just above random chance levels (Figure 5-Figure Supplement 1a). Further reducing within-group correlations (20%, Figure 5a) causes dendrites to lose their selectivity for specific activity groups due to the increased noise in the activity patterns (20%, Figure 5a). Overall, reducing within-group correlations increases synapse pruning (Figure 5f, bottom), also found experimentally (Matsumoto et al., 2024) as dendrites require an extended period to fine-tune connections aligned with their selectivity biases. This phenomenon accounts for the observed reduction in both the density and number of synapses connected to each dendrite.

In addition to the within-group correlations, developmental spontaneous activity patterns can also change correlations between groups as for example retinal waves propagated in different domains (Feller et al., 1997) (Figure 5-Figure Supplement 2). An increase in between-group correlations in our model intuitively decreases competition between the groups since fully correlated global events synchronize the activity of all groups (Figure 5-Figure Supplement 2). The reduction in competition reduces pruning in the model, which can be recovered by combining cross-group correlations with decreased within-group correlations (Figure 5-Figure Supplement 2). Our simulations show that altering the correlations within activity groups increases competition (by lowering the within-group correlations) or decreases competition (by raising the across-group correlations). Hence, in our model, competition between activity groups due to non-trivially structured correlations is necessary to generate realistic dynamics between activity-independent growth and activity-dependent refinement or pruning.

In sum, our simulations demonstrate that our model can operate under various correlations in the spike trains. We find that the level of competition between synaptic groups is crucial for the activity-dependent mechanisms to either potentiate or depress synapses and is fully consistent with recent experimental evidence showing that the correlation between spontaneous activity in retinal ganglion cells axons and retinal waves in the superior colliculus governs branch addition vs. elimination (Matsumoto et al., 2024)."

Precise details on the implementation of the changed activity correlations were added to the Methods section:

p. 25 line 638, “Within-group and across-group activity correlations. For the decreased withingroup correlations, we generated parent spike trains for each individual group with the firing rate 𝑟𝑖𝑛 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ 𝑃𝑖𝑛 (e.g., 𝑃𝑖𝑛 = 100%; 60%; 20%, Figure 5). All the synapses of the same group share the same parent spike train and the remaining spikes for each synapse are uniquely generated with the firing rate 𝑟𝑟𝑒𝑠𝑡 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ (1 − 𝑃𝑖𝑛) (e.g., (1 − 𝑃𝑖𝑛) = 0%; 40%; 80%), resulting in the desired firing rate 𝑟𝑡𝑜𝑡𝑎𝑙 (see Table 1). For the increase in across-group correlations, we generated one master spike train with the firing rate 𝑟𝑐𝑟𝑜𝑠𝑠 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ 𝑃𝑐𝑟𝑜𝑠𝑠 for all the synapses of all groups (e.g., 𝑃𝑐𝑟𝑜𝑠𝑠 = 5%; 10%; 20%, Figure 5-Figure Supplement 2). This master spike train is shared across all groups and then filled up according to the within-group correlation (if not specified differently 𝑃𝑖𝑛 = 1 − 𝑃𝑐𝑟𝑜𝑠𝑠 to maintain the rate 𝑟𝑡𝑜𝑡𝑎𝑙). In all the cases, also in those where the change in across-group correlations is combined with the change in within-group correlations, the remaining spikes for each synapse are generated with a firing rate 𝑟𝑟𝑒𝑠𝑡 = 𝑟𝑡𝑜𝑡𝑎𝑙 ∗ (1 − 𝑃𝑖𝑛 − 𝑃𝑐𝑟𝑜𝑠𝑠) to obtain an overall desired firing rate of 𝑟𝑡𝑜𝑡𝑎𝑙.”

Point 1.2. Many potentially important phenomena seem to be excluded. I realize that no model can be complete, but the choice of which phenomena to include or exclude from this model could bias studies that make use of it and is worth serious discussion. The development of axons is concurrent with dendrite outgrowth, is highly dynamic, and perhaps better understood mechanistically. In this model, the inputs are essentially static. Growing dendrites acquire and lose growth cones that are associated with rapid extension, but these do not seem to be modeled. Postsynaptic firing does not appear to be modeled, which may be critical to activity-dependent plasticity. For example, changes in firing are a potential explanation for the global changes in dendritic pruning that occur following the outgrowth phase.  

Thanks to the reviewer for bringing up these important considerations. We do indeed write in the Introduction (e.g. lines 36-76) which phenomena we include in the model and why. The Discussion also compares our model to others (lines 433-490), pointing out that most models either focus on activity-independent or activity-dependent phases. We include both, combining the influence of both molecular gradients and growth factors as well as activity-dependent connectivity refinements instructed by spontaneous activity. We consider our model a tractable, minimalist mechanistic model which includes both activity-independent and activity-dependent aspects. 

Regarding postsynaptic firing, this is indeed super relevant and an important point to consider. In one of our recent publications (Kirchner and Gjorgjieva, 2021), we studied only an activity-dependent model for the organization of synaptic inputs on non-growing dendrites which have a fixed length. There, we considered the effect of postsynaptic firing (via a back-propagating action potential) and demonstrated that it plays an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron. For example, we showed that it could lead to the emergence of retinotopic maps on the dendritic tree which have been found experimentally (Iacaruso et al., 2017). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree. This is now also discussed in the Discussion section of the revised manuscript:

p. 21 line 491, “Although we did not explicitly model postsynaptic firing, our previous work with static dendrites has shown that it can play an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron (Kirchner and Gjorgjieva, 2021). For example, we showed that it could lead to the emergence of retinotopic maps on the dendritic tree which have been found experimentally (Iacaruso et al., 2017). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree.”

Including the concurrent development of axons in the model is indeed very interesting. In fact, a recent tour-de-force techniques paper found similar to what we assume. Hebbian activity-dependent dynamics of axonal branches of retinal ganglion cells experiencing spontaneous activity in relation to retinal waves in the superior colliculus (Matsumoto et al., 2024). New branches tend to be added at the locations where spontaneous activity of individual branches is more correlated with retinal waves, whereas asynchronous activity is associated with branch elimination. We suspect the same Hebbian activity-dependent dynamics to apply also to dendritic growth. 

To address simultaneous dynamic axons to our growing dendrites, in the revised version of the manuscript, we included a simplified form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, which come from axons of presynaptic partners. We explored different median lifetimes of synapses in combination with several distances with which a synapse can move in the simulated space (new Supplementary Figure 3-3). Our results show that dynamically moving synapses only affect the dynamics and stability of our model when the rate of moving synapses combined with the distance of moving synapses is faster than the dendritic growth. In scenarios in which synapses can move across large distances, dendrites get further destabilized due to synapses transferring from one dendrite to another, perturbing the attractor fields of the potential synapses even in late phases of the simulations. Besides such non-biological scenarios, dynamically moving synapses do not affect the model dynamics too much. Thus, they mostly add additional noise and variability to the growth and pruning without changing the timing and amplitude of the dynamics. These results are discussed in the results section of the revised manuscript:

p.9 line 207, “The development of axons is concurrent with dendritic growth and highly dynamic Matsumoto et al. (2024). To address the impact of simultaneously growing axons, we implemented a simple form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, originating from the axons of presynaptic partners (Figure 3-Figure Supplement 3). When potential synapses can move rapidly (median lifetime of 1.8 hours), the model dynamics are perturbed quite substantially, making it difficult for the dendrites to stabilize completely (Figure 3–Figure Supplement 3c). However, slowly moving potential synapses (median lifetime of 18 hours) still yield comparable results (Figure 3-Figure Supplement 3). The distance of movement significantly influenced results only when potential synaptic lifetimes were short. For extended lifetimes, the moving distance had a minor impact on the dynamics, predominantly affecting the time required for dendrites to stabilize. This was the result of synapses being able to transfer from one dendrite to another, potentially forming new long-lasting connections even at advanced stages of synaptic refinement. In sum, our results show that potential axonal dynamics only affect the stability of our model when these dynamics are much faster than dendritic growth.”

Precise details on the implementation of the dynamically moving synapses and their synaptic lifetimes are now in the Methods section:

p. 25 line 650, “Dynamically moving synapses. For the moving synapses we introduced lifetimes for each synapse, randomly sampled from a log-normal distribution with median 1.8h (for when they move frequently), 4.5h or 18h (for when they move rarely) and variance equal to 1 (Figure 3-Figure Supplement 3b). The lifetime of a synapse decreases only when the synapse is not connected to any of the dendrites (i.e., is a potential synapse). When the lifetime of a synapse expires, the synapse moves to a new location with a new lifetime sampled from the same log-normal distribution. This enables synapses to move multiple times throughout a simulation. The exact locations and distances to which each synapse can move are determined by a binary matrix (dimensions: 𝑝𝑖𝑥𝑒𝑙𝑑𝑖𝑠𝑡𝑎𝑛𝑐𝑒 × 𝑝𝑖𝑥𝑒𝑙𝑑𝑖𝑠𝑡𝑎𝑛𝑐𝑒) representing a ring (annulus) with the inner radius 𝑑/4 and outer radius 𝑑/2 , where the synapse location is at the center of the matrix. All the locations of the matrix within the ring boundaries (between the inner radius and outer radius) are potential locations to which the synapse can move. The synapse then moves randomly to one of the possible locations where no other synapse or dendrite is located. For the movement distances, we chose the ring dimensions 3 × 3, 25 × 25 and 101 × 101, yielding the moving distances (radii) of 1 pixel per movement, 12 pixels per movement and 50 pixels per movement (𝑟 = (𝑑−1)/2). These pixel distances represent small movements, as much as a dendrite can grow in one step (1 micron), and larger movements which are far enough so that the synapse will not attract the same branches again (12 microns) or far enough so that it might attract a completely different dendrite (50 microns, Figure 3-Figure Supplement 3a).”

Point 1.3. Line 167. There are many ways to include activity -independent and -dependent components into a model and not every such model shows stability. A key feature seems to be that larger arbors result in reduced growth and/or increased retraction, but this could be achieved in many ways (whether activity dependent or not). It's not clear that this result is due to the combination of activity-dependent and independent components in the model, or conceptually why that should be the case.

We never argued for model uniqueness. There are always going to be many different models (at different spatial and temporal scales, at different levels of abstraction). We can never study all of them and like any modeling study in systems neuroscience we have chosen one model approach and investigated this approach. We do compare the current model to others in the Discussion. If the reviewers have a specific implementation that we should compare our model to as an alternative, we could try, but not if this means doing a completely separate project.

Point 1.4. Line 183. The explanation of overshoot in terms of the different timescales of synaptic additions versus activity-dependent retractions was not something I had previously encountered and is an interesting proposal. Have these timescales been measured experimentally? To what extent is this a result of fine-tuning of simulation parameters?  

We found that varying the amount of BDNF controls the timescale of the activity-dependent plasticity (see our Figure 6c). Hence, changing the balance between synaptic additions vs. retractions is already explored in Figure 6e and f. Here we show that the overshoot and retraction does not have to be fine-tuned but may be abolished if there is too much activity-dependent plasticity. 

Regarding the relative timescales of synaptic additions vs. retractions: since the first is mainly due to activity-independent factors, and the second due to activity-dependent plasticity, the questions is really about the timescales of the latter two. As we write in the Introduction (lines 61-63), manipulating activity-dependent synaptic transmission has been found to not affect morphology but rather the density and specificity of synaptic connections (Ultanir et al. 2007), supporting the sequential model we have (although we do not impose the sequence, as both activity-independent and activitydependent mechanisms are always “on”; but note that activity-dependent plasticity can only operate on synapses that have already formed).

The described results are robust to parameter variations (performed on the postsynaptic density, potential synapse density, and within- and across-group correlations) as described in the reply to reviewer #1 point 1.1.

Point 1.5. Line 203. This result seems at odds with results that show only a very weak bias in the tuning distribution of inputs to strongly tuned cortical neurons (e.g. work by Arthur Konnerth's group). This discrepancy should be discussed.  

First, we note that the correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter, but is rather a property of correlated spontaneous activity. 

Nonetheless, there is some variability in what the experimental data show. Many studies have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al., 2011; Takahashi et al., 2012; Winnubst et al., 2015; Gökçe et al., 2016; Wilson et al., 2016; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al., 2018; Kerlin et al., 2019; Ju et al., 2020, Hedrick et al., 2022, Hedrick et al., 2024). Interestingly, some in vivo studies have reported lack of fine-scale synaptic organization (Varga et al., 2011; X. Chen et al., 2011; T.-W. Chen et al., 2013; Jia et al., 2010; Jia et al., 2014), while others reported clustering for different stimulus features in different species. For example, dendritic branches in the ferret visual cortex exhibit local clustering of orientation selectivity but do not exhibit global organization of inputs according to spatial location and receptive field properties (Wilson et al. 2016; Scholl et al., 2017). In contrast, synaptic inputs in mouse visual cortex do not cluster locally by orientation, but only by receptive field overlap, and exhibit a global retinotopic organization along the proximal-distal axis (Iacaruso et al., 2017). We proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity similar to the BDNF-proBDNF model that we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021). This is now also discussed in the Discussion section of the revised manuscript:

p. 20 line 471, “The correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter, but is rather a property of spontaneous activity. Nonetheless, there is some variability in what the experimental data show. Many have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al., 2011; Winnubst et al., 2015; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al., 2018; Takahashi et al., 2012; Gökçe et al., 2016; Wilson et al., 2016; Kerlin et al., 2019; Ju et al., 2020; Hedrick et al., 2022, 2024). Other studies have reported lack of fine-scale synaptic organization (Chen et al., 2013; Varga et al., 2011; Chen et al., 2011; Jia et al., 2010, 2014). Interestingly, some of these discrepancies might be explained by different species showing clustering with respect to different stimulus features (orientation or receptive field overlap) (Scholl et al., 2017; Wilson et al., 2016; Iacaruso et al., 2017). Our prior work proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity as we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021).”

Point 1.6. Line 268. How does the large variability in the size of the simulated arbors relate to the relatively consistent size of arbors of cortical cells of a given cell type? This variability suggests to me that these simulations could be sensitive to small changes in parameters (e.g. to the density or layout of presynapses).  

We again thank the reviewer for the detailed explanation and feedback on parameters that should be tested in more detail. We have explored several of the suggested model parameters and believe that we have managed to explain and illustrate their effects on the model's dynamics clearly. The precise changes are explained in the reply to point 1.1 and are now available in the revised version of the manuscript.

Point 1.7. The modeling of dendrites as two-dimensional will likely limit the usefulness of this model. Many phenomena- such as diffusion, random walks, topological properties, etc - fundamentally differ between two and three dimensions.  

Indeed, there are many differences between two and three dimensions. We have ongoing work that extends the current model to 3D but is beyond the scope of the current paper. In systems neuroscience, people have found very interesting results making such simplified geometric assumptions about networks, for instance the one-dimensional ring model has been used to uncover fundamental insights about computations even though highly simplified and abstracted. We are convinced that our model, especially with the new sensitivity analysis, makes interesting and novel contributions and predictions.

Point 1.8. The description of wiring lengths as 'approximately optimal' in this text is problematic. The plotted data show that the wiring lengths are several deviations away from optimal, and the random model is not a valid instantiation of the 2D non-overlapping constraints the authors imposed. A more appropriate null should be considered.  

We appreciate the reviewer’s feedback regarding the use of the term “approximately optimal” in describing wiring lengths. We acknowledge that our initial terminology was imprecise and could be misleading. We had previously referred to the minimal wiring length as the optimal wiring length, which does not fully capture the nuances of neuronal wiring optimization. As noted in prior literature, such as the work by Hermann Cuntz (Cuntz et al., 2010 & 2012), neurons can optimize their wiring beyond simply minimizing dendritic length.

To address this issue, to better capture the balance between wiring minimization and functional constraints, such as conduction delays, we have developed a new modeling approach based on minimum spanning trees with a balancing factor (Cuntz et al., 2010 & 2012). This factor modulates the trade-off between minimizing wiring length and accounting for conduction delays from synapses to the soma. Specifically, the model assumes a balance between minimizing the total dendritic length and minimizing the tree distance between synapses and the site of input integration, typically the soma. This balance is illustrated in Figure 8 (Figure 7 in the original manuscript), where we demonstrate that the deviation from the theoretical minimum length arises because direct paths to synapses often require longer dendrites in our models.

Together with the new result, which we added as the new panels f, g and h to Figure 8 (originally Figure 7), we also adjusted panel a of Figure 8, to now illustrate the difference between random wiring, minimal wiring and minimal conductance delay. The updated Figure 8 and its new findings are discussed in the results section of the revised manuscript:

p.17 line 387, “This deviation is expected given that real dendrites need to balance their growth processes between minimizing wire while reducing conduction delays. The interplay between these two factors emerges from the need to reduce conduction delays, which requires a direct path length from a given synapse to the soma, consequently increasing the total length of the dendritic cable. (Cuntz et al., 2010, 2012; Ferreira Castro et al., 2020).

To investigate this further, we compared the scaling relations of the final morphologies of our models with other synthetic dendritic morphologies generated using a previously described minimum spanning tree (MST) based model. The MST model balances the minimization of total dendritic length and the minimization of conduction delays between synapses and the soma. This balance results in deviations from the theoretical minimum length because direct paths to synapses often require longer dendrites (Cuntz et al., 2008, 2010). The balance in the model is modulated by a balancing factor (𝑏𝑓 ). If 𝑏𝑓 is zero, dendritic trees minimize the cable only, and if 𝑏𝑓 is one, they will try to minimize the conduction delays as much as possible. It is important to note that the MST model does not simulate the developmental process of dendritic growth; it is a phenomenological model designed to generate static morphologies that resemble real cells.

To facilitate the comparison of total lengths between our simulated and MST morphologies, we generated MST models under the same initial conditions (synaptic spatial distribution) as our models and simulated them to match several morphometrics (total length, number of terminals, and surface area) of our grown morphologies. This allowed us to create a corresponding MST tree for each of our synthetic trees. Consequently, we could evaluate whether the branching structures of our models were accurately predicted by minimum spanning trees based on optimal wiring constraints. We found that the best match occurred with a trade-off parameter 𝑏𝑓 = 0.9250 (Figure 8f). Using the morphologies generated by the MST model with the specified trade-off parameter (𝑏𝑓 ), we showed that the square root of the synapse count and the total length (𝐿) in both our model generated trees and the MST trees exhibit a linear scaling relationship (Figure 8g; 𝑅2 = 0.65). The same linear relationship can be observed for the square root of the surface area and the total length 𝐿 of our model trees and the MST trees (Figure 8h; 𝑅2 = 0.73). Overall, these results indicate that our model generate trees are wellfitted by the MST model and follow wire optimization constraints.

We acknowledge that the value of the balancing factor 𝑏𝑓 in our model is higher than the range of balancing factors that is typically observed in the biological dendritic counterparts, which generally ranges between 0.2 and 0.4 (Cuntz et al., 2012; Ferreira Castro et al., 2020; Baltruschat et al., 2020). However, it is still remarkable that our model, which does not explicitly address these two conservation laws, achieves approximately optimal wiring. Why do we observe such a high 𝑏𝑓 value? We reason that two factors may contribute to this. First, in our models, local branches grow directly to the nearest potential synapse, potentially taking longer routes instead of optimally branching to minimize wiring length (Wen and Chklovskii, 2008). Second, the growth process in our models does not explicitly address the tortuosity of the branches, which can increase the total length of the branches used to connect synapses. In the future, it will be interesting to add constraints that take these factors into account. Taken together, combining activity-independent and -dependent dendrite growth produces morphologies that approximate optimal wiring.”

Further details on the fitted MST model and the corresponding analysis were added to the methods section:

p.26 line 669, “Comparison with wiring optimization MST models. To evaluate the wire minimization properties of our model morphologies (n=288), we examined whether the number of connected synapses (N), total length (L), and surface area of the spanning field (S) conformed to the scaling law 𝐿 ≈ 𝜋−1/2 ⋅ 𝑆1/2 ⋅ 𝑁1/2 (Cuntz et al., 2012). Furthermore, to validate that our model dendritic morphologies scale according to optimal wiring principles, we created simplified models of dendritic trees using the MST algorithm with a balancing factor (bf). This balancing factor adjusts between minimizing the total dendritic length and minimizing the tree distance between synapses and the soma (Cost = 𝐿 + 𝑏𝑓 ⋅ 𝑃 𝐿) (MST_tree; best bf = 0.925) (Cuntz et al., 2010); TREES Toolbox http://www.treestoolbox.org).

Initially, we generated MSTs to connect the same distributed synapses as our models. We performed MST simulations that vary the balancing factor between 𝑏𝑓 = 0 and 𝑏𝑓 = 1 in steps of 0.025 while calculating the morphometric agreement by computing the error (Euclidean distance) between the morphologies of our models and those generated by the MST models. The morphometrics used were total length, number of terminals, and surface area occupied by the synthetic morphologies.”

Point 1.9. It's not clear to me what the authors are trying to convey by repeatedly labeling this model as 'mechanistic'. The mechanisms implemented in the model are inspired by biological phenomena, but the implementations have little resemblance to the underlying biophysical mechanisms. Overall my impression is that this is a phenomenological model intended to show under what conditions particular patterns are possible. Line 363, describing another model as computational but not mechanistic, was especially unclear to me in this context.  

What we mean by mechanistic is that we implement equations that model specific mechanisms i.e. we have a set of equations that implement the activity-independent attraction to potential synapses (with parameters such as the density of synapses, their spatial influence, etc) and the activitydependent refinement of synapses (with parameters such as the ratio of BDNF and proBDNF to induce potentiation vs depression, the activity-dependent conversion of one factor to the other, etc). This is a bottom-up approach where we combine multiple elements together to get to neuronal growth and synaptic organization. This approach is in stark contrast to the so-called top-down or normative approaches where the method would involve defining an objective function (e.g. minimal dendritic length) which depends on a set of parameters and then applying a gradient descent or other mathematical optimization technique to get at the parameters that optimize the objective function. This latter approach we would not call mechanistic because it involves an abstract objective function (who could say what a neuron or a circuit should be trying to optimize?) and a mathematical technique for how to optimize the function (we don’t know if neurons can compute gradients of abstract objective functions). 

Hence our model is mechanistic, but it does operate at a particular level of abstraction/simplification. We don’t model individual ion channels, or biophysics of synaptic plasticity (opening and closing of NMDA channels, accumulation of proteins at synapses, protein synthesis). We do, however, provide a biophysical implementation of the plasticity mechanism through the BDNF/proBDNF model which is more than most models of plasticity achieve, because they typically model a phenomenological STDP or Hebbian rule that just uses activity patterns to potentiate or depress synaptic weights, disregarding how it could be implemented. To the best of our understanding, this is what is normally considered mechanistic in the field (in contrast to, for example, biophysical).

Reviewer #2 (Public Review): 

This work combines a model of two-dimensional dendritic growth with attraction and stabilisation by synaptic activity. The authors find that constraining growth models with competition for synaptic inputs produces artificial dendrites that match some key features of real neurons both over development and in terms of final structure. In particular, incorporating distance-dependent competition between synapses of the same dendrite naturally produces distinct phases of dendritic growth (overshoot, pruning, and stabilisation) that are observed biologically and leads to local synaptic organisation with functional relevance. The approach is elegant and well-explained, but makes some significant modelling assumptions that might impact the biological relevance of the results. 

Strengths: 

The main strength of the work is the general concept of combining morphological models of growth with synaptic plasticity and stabilisation. This is an interesting way to bridge two distinct areas of neuroscience in a manner that leads to findings that could be significant for both. The modelling of both dendritic growth and distance-dependent synaptic competition is carefully done, constrained by reasonable biological mechanisms, and well-described in the text. The paper also links its findings, for example in terms of phases of dendritic growth or final morphological structure, to known data well. 

Weaknesses: 

The major weaknesses of the paper are the simplifying modelling assumptions that are likely to have an impact on the results. These assumptions are not discussed in enough detail in the current version of the paper. 

(1) Axonal dynamics. 

A major, and lightly acknowledged, assumption of this paper is that potential synapses, which must come from axons, are fixed in space. This is not realistic for many neural systems, as multiple undifferentiated neurites typically grow from the soma before an axon is specified (Polleux & Snider, 2010). Further, axons are also dynamic structures in early development and, at least in some systems, undergo activity-dependent morphological changes too (O'Leary, 1987; Hall 2000). This paper does not consider the implications of joint pre- and post-synaptic growth and stabilisation.  

We thank the reviewer for the summary of the strengths and weaknesses of the work. While we feel that including a full model of axonal dynamics is beyond the scope of the current manuscript, some aspects of axonal dynamics can be included and are now implemented and tested in the revised manuscript. Since this feedback covers similar aspects of the model that were also pointed out by reviewer #1, we refer here to our detailed reply to their comments 1.1 and 1.2, where we list and discuss all the analyses performed to address the raised issues.

(2) Activity correlations 

On a related note, the synapses in the manuscript display correlated activity, but there is no relationship between the distance between synapses and their correlation. In reality, nearby synapses are far more likely to share the same axon and so display correlated activity. If the input activity is spatially correlated and synaptic plasticity displays distance-dependent competition in the dendrites, there is likely to be a non-trivial interaction between these two features with a major impact on the organisation of synaptic contacts onto each neuron.  

We have explored the amount of correlation (between and within correlated groups) in the revised manuscript (see also our reply to reviewer comment 1.1).

However, previous experimental work, (e.g. Kleindienst et al., 2011) has provided anatomical and functional analyses that it is unlikely that the functional synaptic clustering on dendritic branches is the result of individual axons making more than one synapse (see pg. 1019).

(3) BDNF dynamics 

The models are quite sensitive to the ratio of BDNF to proBDNF (eg Figure 5c). This ratio is also activity-dependent as synaptic activation converts proBDNF into BDNF. The models assume a fixed ratio that is not affected by synaptic activity. There should at least be more justification for this assumption, as there is likely to be a positive feedback relationship between levels of BDNF and synaptic activation.  

The reviewer is correct. We used the BDNF-proBDNF model for synaptic plasticity based on our previous work (Kirchner and Gjorgjieva, 2021).  

There, we explored only the emergence of functionally clustered synapses on static dendrites which do not grow. In the Methods section (Parameters and data fitting) we justify the choice of the ratio of BDNF to proBDNF from published experimental work. We also performed sensitivity analysis (Supplementary Fig. 1) and perturbation simulations (Supplementary Fig. 3), which showed that the ratio is crucial in regulating the overall amount of potentiation and depression of synaptic efficacy, and therefore has a strong impact on the emergence and maintenance of synaptic organization. Since we already performed all this analysis, we expect that the same results will also apply to the current model which includes dendritic growth, as it involves the same activity-dependent mechanism.

A further weakness is in the discussion of how the final morphologies conform to principles of optimal wiring, which is quite imprecise. 'Optimal wiring' in the sense of dendrites and axons (Cajal, 1895; Chklovskii, 2004; Cuntz et al, 2007, Budd et al, 2010) is not usually synonymous with 'shortest wiring' as implied here. Instead, there is assumed to be a balance between minimising total dendritic length and minimising the tree distance (ie Figure 4c here) between synapses and the site of input integration, typically the soma. The level of this balance gives the deviation from the theoretical minimum length as direct paths to synapses typically require longer dendrites. In the model this is generated by the guidance of dendritic growth directly towards the synaptic targets. The interpretation of the deviation in this results section discussing optimal wiring, with hampered diffusion of signalling molecules, does not seem to be correct. 

We agree with this comment. We had wrongly used the term “optimal wiring” as neurons can optimize their wiring not only by minimizing their dendritic length but other factors as noted by the reviewer. In the revised manuscript we replaced the term “optimal wiring” with “minimal wiring” wherever it was incorrectly used. On top of that, we performed further analysis and discussed these differences, as pointed out in the reply to reviewer #1 point 1.8.

To summarize, we want to again thank the reviewer for their in-depth review and all the suggestions that helped us improve the analysis and implementation of our model.

Reviewer #3 (Public Review): 

The authors propose a mechanistic model of how the interplay between activity-independent growth and an activity-dependent synaptic strengthening/weaken model influences the dendrite shape, complexity and distribution of synapses. The authors focus on a model for stellate cells, which have multiple dendrites emerging from a soma. The activity independent component is provided by a random pool of presynaptic sites that represent potential synapses and that release a diffusible signal that promotes dendritic growth. Then a spontaneous activity pattern with some correlation structure is imposed at those presynaptic sites. The strength of these synapses follow a learning rule previously proposed by the lab: synapses strengthen when there is correlated firing across multiple sites, and synapses weaken if there is uncorrelated firing with the relative strength of these processes controlled by available levels of BDNF/proBDNF. Once a synapse is weakened below a threshold, the dendrite branch at that site retracts and loses its sensitivity to the growth signal 

The authors run the simulation and map out how dendrites and synapses evolve and stabilize. They show that dendritic trees growing rapidly and then stabilize by balancing growth and retraction (Figure 2). They also that there is an initial bout of synaptogenesis followed by loss of synapses, reflecting the longer amount of time it takes to weaken a synapse (Figure 3). They analyze how this evolution of dendrites and synapses depends on the correlated firing of synapses (i.e. defined as being in the same "activity group"). They show that in the stabilized phase, synapses that remain connected to a given dendritic branch are likely to be from same activity group (Figure 4). The authors systemically alter the learning rule by changing the available concentration of BDNF, which alters the relative amount of synaptic strengthening, which in turn affects stabilization, density of synapses and interestingly how selective for an activity group one dendrite is (Figure 5). In addition the authors look at how altering the activity-independent factors influences outgrowth (Figure 6). Finally, one of the interesting outcomes is that the resulting dendritic trees represent "optimal wiring" solutions in the sense that dendrites use the shortest distance given the distribution of synapses. They compare this distribute to one published data to see how the model compared to what has been observed experimentally.  

There are many strengths to this study. The consequence of adding the activity-dependent contribution to models of synapto- and dendritogenesis is novel. There is some exploration of parameters space with the motivation of keeping the parameters as well as the generated outcomes close to anatomical data of real dendrites. The paper is also scholarly in its comparison of this approach to previous generative models. This work represented an important advance to our understanding of how learning rules can contribute to dendrite morphogenesis.

We thank the reviewer for the positive evaluation of the work and the suggestions below.

To improve the clarity of the manuscript, we adjusted and fixed some figures and corresponding paragraphs as follows:

(1) We increased the number of ticks and their corresponding numbers in all the figures to make them easier to read and interpret.

(2) In Figure 3 panel d, showing the evolution of synaptic weight, we corrected the upper limit at the yaxis to 1 (from previously 2).

(3) Due to a typo in the implementation of the BDNF concentration, we had to correct the used BDNF concentrations from 49%, 45% and 40%, to 49%, 46.5% and 43% respectively.

(4) The y-axis labels of Figure 6 (old Figure 5) panel e and f were changed to make the plots clearer (e: “morphology change explained (%)” to "effect on morphology (%)", and f: “synapse connection explained (%)” to "effect on connected synapses (%)").

(5) The values for the eta and tau-w in the supplementary Table were corrected. Previously tau-w was falsely 6000 time steps which was corrected to 3000 time steps, and eta was 45% and is now 46.5%.

We believe that all the changes to the manuscript will address the reviewer’s concerns and enhance the clarity and accuracy of the findings described in the manuscript.

eLife Assessment

This valuable study gives new insight into decision-making during C. elegans foraging, providing evidence that animals can make accept-reject decisions upon encountering a food patch. Using rigorous behavioral analysis and quantitative modeling, the authors provide evidence that nematodes integrate sensory information with prior experience and internal state when making this decision. While some of the evidence is compelling, some key claims are only incompletely supported and would benefit from further validation.

Reviewer #1 (Public review):

Summary:

This work uses a novel, ethologically relevant behavioral task to explore decision-making paradigms in C. elegans foraging behavior. By rigorously quantifying multiple features of animal behavior as they navigate in a patch food environment, the authors provide strong evidence that worms exhibit one of three qualitatively distinct behavioral responses upon encountering a patch:<br /> (1) "search", in which the encountered patch is below the detection threshold;<br /> (2) "sample", in which animals detect a patch encounter and reduce their motor speed, but do not stay to exploit the resource and are therefore considered to have "rejected" it; and<br /> (3) "exploit", in which animals "accept" the patch and exploit the resource for tens of minutes.<br /> Interestingly, the probability of these outcomes varies with the density of the patch as well as the prior experience of the animal. Together, these experiments provide an interesting new framework for understanding the ability of the C. elegans nervous system to use sensory information and internal state to implement behavioral state decisions.

Strengths:

(1) The work uses a novel, neuroethologically-inspired approach to studying foraging behavior.

(2) The studies are carried out with an exceptional level of quantitative rigor and attention to detail.

(3) Powerful quantitative modeling approaches including GLMs are used to study the behavioral states that worms enter upon encountering food, and the parameters that govern the decision about which state to enter.

(4) The work provides strong evidence that C. elegans can make 'accept-reject' decisions upon encountering a food resource.

(5) Accept-reject decisions depend on the quality of the food resource encountered as well as on internally represented features that provide measurements of multiple dimensions of internal state, including feeding status and time.

Weaknesses:

(1) The authors repeatedly assert that an individual's behavior in the foraging assay depends on its prior history (particularly cultivation conditions). While this seems like a reasonable expectation, it is not fully fleshed out. The work would benefit from studies in which animals are raised on more or less abundant food before the behavioral task.

(2) The authors convincingly show that the probability of particular behavioral outcomes occurring upon patch encounter depends on time-associated parameters (time since last patch encounter, time since last patch exploitation). There are two concerns here. First, it is not clear how these values are initialized - i.e., what values are used for the first occurrence of each behavioral state? More importantly, the authors don't seem to consider the simplest time parameter, the time since the start of the assay (or time since worm transfer). Transferring animals to a new environment can be associated with significant mechanical stimulus, and it seems quite possible that transferring animals causes them to enter a state of arousal. This arousal, which certainly could alter sensory function or decision-making, would likely decay with time. It would be interesting to know how well the model performs using time since assay starts as the only time-dependent parameter.

(3) Similarly, Figures 2L and M clearly show that the probability of a search event occurring upon a patch encounter decreases markedly with time. Because search events are interpreted as a failure to detect a patch, this implies that the detection of (dilute) patches becomes more efficient with time. It would be useful for the authors to consider this possibility as well as potential explanations, which might be related to the point above.

(4) Based on their results with mec-4 and osm-6 mutants, the authors assert that chemosensation, rather than mechanosensation, likely accounts for animals' ability to measure patch density. This argument is not well-supported: mec-4 is required only for the function of the six non-ciliated light-touch neurons (AVM, PVM, ALML/R, PLML/R). In contrast, osm-6 is expected to disrupt the function of the ciliated dopaminergic mechanosensory neurons CEP, ADE, and PDE, which have previously been shown to detect the presence of bacteria (Sawin et al 2000). Thus, the paper's results are entirely consistent with an important role of mechanosensation in detecting bacterial abundance. Along these lines, it would be useful for the authors to speculate on why osm-6 mutants are more, rather than less, likely to "accept" when encountering a patch.

(5) While the evidence for the accept-reject framework is strong, it would be useful for the authors to provide a bit more discussion about the null hypothesis and associated expectations. In other words, what would worm behavior in this assay look like if animals were not able to make accept-reject decisions, relying only on exploit-explore decisions that depend on modulation of food-leaving probability?

Reviewer #2 (Public review):

This study provides an experimental and computational framework to behavioral biology that helps examine and understand how C. elegans make decisions while foraging in environments with patches of food. The authors show that worms actively reject or accept food patches depending on a number of internal and external factors.

The key novelty and strength of this paper is the explicit demonstration of behavior analysis and quantitative modeling to elucidate the decision-making process. In particular, the description of the exploring vs. exploiting phases, and sensing vs. non-sensing categories of C. elegans foraging behavior based on the clustering of behavioral states defined in a multi-dimensional behavior-metrics space, and the implementation of a generalized linear model (GLM) whose parameters can provide quantitative biological interpretations.

While the concept is interesting, there are many flaws in the experimental, analysis, and models that weaken what one can conclude from the work.

Reviewer #3 (Public review):

Summary:

In this study by Haley et al, the authors investigated explore-exploit foraging using C. elegans as a model system. Through an elegant set of patchy environment assays, the authors built a GLM based on past experience that predicts whether an animal will decide to stay on a patch to feed and exploit that resource, instead of choosing to leave and explore other patches.

Strengths:

I really enjoyed reading this paper. The experiments are simple and elegant, and address fundamental questions of foraging theory in a well-defined system. The experimental design is thoroughly vetted, and the authors provide a considerable volume of data to prove their points. My only criticisms have to do with the data interpretation, which I think is easily addressable.

Weaknesses:

(1) Sensing vs. non-sensing

The authors claim that when animals encounter dilute food patches, they do not sense them, as evidenced by the shallow deceleration that occurs when animals encounter these patches. This seems ethologically inaccurate. There is a critical difference between not sensing a stimulus, and not reacting to it. Animals sense numerous stimuli from their environment, but often only behaviorally respond to a fraction of them, depending on their attention and arousal state. With regard to C. elegans, it is well-established that their amphid chemosensory neurons are capable of detecting very dilute concentrations of odors. In addition, the authors provide evidence that osm-6 animals have altered exploit behaviors, further supporting the importance of amphid chemosensory neurons in this behavior.

(2) Search vs. sample & sensing vs. non-sensing

In Figures 2H and 2I, the authors claim that there are three behavioral states based on quantifying average velocity, encounter duration, and acceleration, but I only see three. Based on density distributions alone, there really only seem to be 2 distributions, not 3. The authors claim there are three, but to come to this conclusion, they used a QDA, which inherently is based on the authors training the model to detect three states based on prior annotations. Did the authors perform a model test, such as the Bayesian Information Criterion, to confirm whether 2 vs. 3 Gaussians is statistically significant? It seems like the authors are trying to impose two states on a phenomenon with a broad distribution. This seems very similar to the results observed for roaming vs. dwelling experiments, which again, are essentially two behavioral states.

(4) History-dependence of the GLM

The logistic GLM seems like a logical way to model a binary choice, and I think the parameters you chose are certainly important. However, the framing of them seems odd to me. I do not doubt the animals are assessing the current state of the patch with an assessment of past experience; that makes perfect logical sense. However, it seems odd to reduce past experience to the categories of recently exploited patch, recently encountered patch, and time since last exploitation. This implies the animals have some way of discriminating these past patch experiences and committing them to memory. Also, it seems logical that the time on these patches, not just their density, should also matter, just as the time without food matters. Time is inherent to memory. This model also imposes a prior categorization in trying to distinguish between sensed vs. not-sensed patches, which I criticized earlier. Only "sensed" patches are used in the model, but it is questionable whether worms genuinely do not "sense" these patches.

(5) osm-6

The osm-6 results are interesting. This seems to indicate that the worms are still sensing the food, but are unable to assess quality, therefore the default response is to exploit. How do you think the worms are sensing the food? Clearly, they sense it, but without the amphid sensory neurons, and not mechanosensation. Perhaps feeding is important? Could you speculate on this?

(7) Impact:

I think this work will have a solid impact on the field, as it provides tangible variables to test how animals assess their environment and decide to exploit resources. I think the strength of this research could be strengthened by a reassessment of their model that would both simplify it and provide testable timescales of satiety/starvation memory.

Author response:

We thank the reviewers for their thoughtful comments. We are working to revise our manuscript and address each of the reviewers comments. A summary of our planned revisions and responses to some of the reviewers’ major concerns are included below.

Cultivation Density: Reviewers #1 and #2 suggested that additional studies testing the effects of varying bacterial density during animal development (cultivation) would strengthen our findings. While we agree with the reviewers that this is a very interesting experiment, it is not feasible. Indeed, we attempted this experiment but found it nontrivial to maintain stable bacterial density conditions over long timescales as this requires matching the rate of bacterial growth with the rate of bacterial consumption. Despite our best efforts, we have not been able to identify conditions that satisfy these requirements. We will focus our revised manuscript to include only assertions about the effects of recent experiences.

Transfer Method: Reviewers #1 and #2 expressed concern that the stress of transferring animals to a new plate may have resulted in an increased arousal state and thus a greater probability of rejecting patches. We thank the reviewers for this thoughtful remark and plan to conduct additional analyses to address this hypothesis. We did, however, anticipate this possibility and, to mitigate the stress of moving, we used an agar plug method where animals were transferred using the flat surface of small cylinders of agar. Importantly, the use of agar as a medium to transfer animals provides minimal disruption to their environment as all physical properties (e.g. temperature, humidity, surface tension) are maintained. Qualitatively, we observe no marked change in behavior from before to after transfer with the agar plug method, especially as compared to the often drastic changes observed when using a metal or eyelash pick.

Time Parameter: Related to the transfer method, Reviewer #1 expressed concern that the simplest time parameter (time since start of the assay) might better predict animal behavior. We thank the reviewer for pointing out the need to specifically test whether the time-dependent change in explore-exploit decision-making corresponds better with satiety (time off patch) or arousal (time since transfer/start of assay) state. We will conduct additional analyses to address these alternative hypotheses.

Parameter Initialization: Reviewer #1 pointed out an oversight in our methods section regarding the model parameter values used for the first encounter. We plan to clarify the initialization of parameters in the manuscript. In short, for the first patch encounter where k = 1:

● ρk is the relative density of the first patch.

● τs is the duration of time spent off food since the beginning of the recorded experiment. For the first patch, this is equivalent to the total time elapsed.

● ρh is the approximated relative density of the bacterial patch on the acclimation plates (see Assay preparation and recording in Methods). Acclimation plates contained one large 200 µL patch seeded with OD600 = 1 and grown for a total of ~48 hours. As with all patches, the relative density was estimated from experiments using fluorescent bacteria OP50-GFP as described in Bacterial patch density estimation in Methods.

● ρe is equivalent to ρh.

Sensing vs. non-sensing: Reviewer #3 suggested that the term “non-sensing” may not be ethologically accurate. We thank the reviewer for their comment and agree that we do not know for certain whether the animals sensed these patches or were merely non-responsive to them. We are, however, confident that these encounters lack evidence of sensing. Specifically, we note that our analyses used to classify events as sensing or non-sensing examined whether an animal’s slow-down upon patch entry could be distinguished from either that of events where animals exploited or that of encounters with patches lacking bacteria. We found that  “non-sensing” encounters are indeed indistinguishable from encounters with bacteria-free patches where there are no bacteria to be sensed (see Figure 2 - Supplement 7C-D and Patch encounter classification as sensing or non-sensing in Methods). Regardless, we agree with the reviewer that all that can be asserted for certain about these events is that animals do not respond to the bacterial patch in any way that we measured. Therefore, we will replace the term “non-sensing” with “non-responding” to better indicate the ethological interpretation of these events.

Time-dependent changes in sensing vs. non-sensing: Reviewer #1 remarked that the sensation of dilute patches increases with time. We agree with the reviewer that we observe increased responsiveness to dilute patches with time. Although this is interesting, our primary focus was on what decision an animal made given that they clearly sensed the presence of the bacterial patch. Nonetheless, we will add this observation to the discussion as an area of future work to investigate the sensory mechanisms behind this effect.

Classification of sensing vs. non-sensing: Reviewers #2 and #3 expressed concerns about the validity of the two clusters identified using the semi-supervised QDA approach described. We are grateful to the reviewers for pointing out the difficulty in visualizing the clusters and the need for additional clarity in explaining the supervised labeling. We will use additional visualizations and methods to validate the clusters we have discovered. Specifically, we aim to provide additional evidence that the sensing vs. nonsensing data is bi-modal (i.e. a two-cluster classification method fits best). Further, it seems that there may be some confusion as to how we arrived at 3 encounter types (i.e. search, sample, exploit) that we plan to clarify in the manuscript. Specifically, it’s important to note that two methods were used on two different (albeit related) sets of parameters. We first used a two-cluster GMM to classify encounters as explore or exploit. We then used a two-cluster semi-supervised QDA to classify encounters as sensing or non-sensing (to be changed to “non-responding”, see above response) using a different set of parameters. We thus separated the explore cluster into two (sensing and non-sensing exploratory events) resulting in three total encounter types: exploit, sample (explore/sensing), and search (explore/non-sensing). We will clarify this in the text. Additionally, we will clarify the labelling used for “supervising” QDA. Specifically, we made two simple assumptions: 1) animals must have sensed the patch if they exploited it and 2) animals must not have sensed the patch if there were no bacteria to sense. Thus, we labeled encounters as sensing if they were found to be exploitatory as we assume that sensation is prerequisite to exploitation; and we labeled encounters as non-sensing for events where animals encountered patches lacking bacteria (OD600 = 0). All other points were non-labeled prior to learning the model. In this way, our labels were based on the experimental design and results of the GMM, an unsupervised method; rather than any expectations we had about what sensing should look like. The semi-supervised QDA method then used these initial labels to iteratively fit a paraboloid that best separated these clusters, by minimizing the posterior variance of classification.

Accept-reject vs. stay-switch: Reviewers #1 and #2 ask for additional discussion on how the accept-reject decision-making framework differs from the stay-switch framework. We thank the reviewers for alerting us to this gap in our discussion. We intend to clarify that these frameworks ask two different types of questions (i.e. “Do you want to eat it?” versus “If so, how long do you want to eat it for?”). These concepts are well described in canonical foraging theory literature (see Pyke, Pulliam & Charnov 1977 for a review on the subject) and are easily distinguishable for animals that forage using the following framework: 1) search for prey, 2) encounter prey from a distance, 3) identify prey type, 4) decide to pursue (accept-reject decision), 5) pursue and capture the prey, 6) exploit prey, and 7) decide to stop exploiting and start searching again (stay-switch decision). In this case, it is easy to see the distinction between accept-reject and stay-switch decisions. However, in some scenarios, animals must physically encounter prey prior to identification and then must make an accept-reject decision. In these cases where pursuit and capture are not visualized, it is harder to distinguish between accept-reject and stay-switch decisions. In our experiments, we find significant bimodality in encounter duration (see Figure 2H) where short duration (exploratory) encounters appear to represent a lower bound where animals spend the minimum amount of time possible on a patch (less than 2 minutes), which we interpret as a rejection of the patch. On the other hand, exploitatory encounters span a large range of durations from 2 to 60+ minutes which we interpret as an initial acceptance of the patch followed by a series of stay-switch decisions which determine the overall duration of the encounter. While one could certainly model our data using only stay-switch decision-making, we ascertain that an encounter of minimal duration is better interpreted ethologically as a rejection than as an immediate switch decision. We will revise the text to further extrapolate upon our point of view on this somewhat philosophical distinction and what it predicts about C. elegans behavior.

Sensory mutant behavior: Reviewers #1 and #3 ask for further speculation on the observed behavior of osm-6 and mec-4 animals. We will further elaborate on our findings, how they relate to previous studies, and what they suggest about the mechanisms behind these foraging decisions.

Model design: Reviewer #3 suggested several alterations to the behavioral model. While the proposed model seems entirely reasonable and could aid in elucidating the time component of how prior experience affects decision-making, we chose the present model based on our experience with model selection using these data. Indeed, as the reviewer suggested, we did a great number of analyses involving model selection including model selection criteria (AIC, BIC) and optimization with regularization techniques (LASSO and elastic nets). We found that the problem of model selection was compounded by the enormous array of highly correlated variables we had to choose from. Additionally, we found that both interaction terms and non-linear terms of our task variables could be predictive of accept-reject decisions but that the precise set of terms selected depended sensitively on which model selection technique was used and generally made rather small contributions to prediction. The diverse array of results and combinatorial number of predictors to possibly include failed to add anything of interpretable value. We therefore chose to take a different approach to this problem. Rather than trying to determine what the “best” model was we instead asked whether a minimal model could be used to answer a set of core questions. Indeed, our goal was not maximal predictive performance but rather to distinguish between the effects of different influences enough to determine if encounter history had a significant, independent effect on decision making. We thus chose to only include task variables that spanned the most basic components of behavioral mechanisms to ask very specific questions. For example, we selected a time variable that we thought best encapsulated satiety. While we could have included many additional terms, or made different choices about which terms to include, based on our analyses these choices would not have qualitatively changed our results. Further, we sought to validate the parameters we chose with additional studies (i.e. food-deprived and sensory mutant animals). We regard our study as an initial foray into demonstrating accept-reject decision-making in nematodes. The exact mechanisms and, consequently, the best model design is therefore beyond the scope of this study. Lastly, Reviewer #3 criticized the use of only sensed patches in the model. While we acknowledge that we are not certain as to whether the “non-sensing” encounters are truly not sensed, we find qualitatively similar results when including all exploratory patches in our analyses. In fact, when all encounters are used, we find stronger correlations between our task variables and the accept-reject decision. However, we take the position that sensation is necessary for decision-making and thus believe that while our model’s predictive performance may be better using all encounters, the interpretation of our findings is stronger when we only include sensing events.

eLife Assessment

This study provides important insights into the role of the Mid1 gene in hippocampal development and its implications in Opitz G/BBB syndrome, with much evidence supporting its impact on synaptic plasticity, neural rhythms, and cognitive functions. The methods, data, and analyses are solid, supporting the claims, presenting several minor weaknesses, and establishing Mid1 as a potential therapeutic target for neurological deficits associated with OS. The conclusions are largely supported by the results, but additional data are needed.

Reviewer #1 (Public review):

Summary:

The authors demonstrated that a mouse model of Opitz syndrome induced by Mid1 gene knockout exhibited a significant decrease in α rhythm in HPC and abnormal synchronization of γ rhythm in the prefrontal cortex and hippocampus, showing decreased synaptic plasticity and learning and memory dysfunction. All these effects were attributed to the inhibition of p Creb by PP2Ac.

Strengths:

The authors used Mid1 gene knockout mice as a mouse model of Opitz syndrome. They carried out RNA seq analysis and found cAMP signaling pathway, calcium signaling pathway, and 100 other pathways have changed significantly.

Weaknesses:

(1) A Mid1 supplementation experiment in Mid1 knockout mice was lacking in this study.

(2) Enzymes that regulate Creb phosphorylation include not only phosphatases such as PP2A, but also kinases such as CaMKII, PKA, and ERK1/2. These protein kinases should be detected, especially CaMKII, their bioinformatics data show calcium signaling pathways have significantly changed.

Reviewer #2 (Public review):

Summary:

The manuscript investigates the role of the Mid1 gene in hippocampal (HPC) development and its contribution to Opitz G/BBB syndrome (OS), which is characterized by neurological deficits and structural abnormalities. The authors use a knockout mouse model (Mid1-/y) to elucidate the underlying molecular mechanisms that contribute to learning and memory impairments. They demonstrate that Mid1 gene deletion leads to reduced synaptic plasticity, abnormal neural rhythms, and decreased cognitive functions, providing a mechanistic explanation for the neurological deficits seen in OS patients. This study addresses an important gap in understanding the neural mechanisms underlying Opitz G/BBB syndrome and provides substantial evidence that the Mid1 gene plays a critical role in hippocampal function and cognition.

Strengths:

Understanding the role of Mid1 in HPC development could have broader implications for neurodevelopmental disorders beyond OS, particularly in conditions associated with synaptic dysfunction or memory impairments. The study's focus on the impact of Mid1 on the cAMP signaling pathway, BDNF expression, and synaptic plasticity offers novel mechanisms relevant to both neurodevelopment and neurodegeneration. Moreover, the combination of RNA-seq, electrophysiological measurements, and histological staining provides a multidimensional approach to understanding how Mid1 influences neuronal function and structure.

Weaknesses:

(1) The introduction is insufficient, and the number of references is too low. With only nine references, there isn't enough context to adequately explain the background and previous evidence.

(2) The specificity of behavioral deficits is lacking. The authors indicate learning and memory dysfunction, yet the Y-maze and Morris water maze primarily assess spatial memory. Additional behavioral tests, such as the novel object recognition test for recognition memory or fear conditioning for associative learning, should be included to provide a more comprehensive assessment.

(3) The manuscript mentions decreased synaptic plasticity but lacks thorough investigation; a more detailed analysis of long-term potentiation (LTP) or depression (LTD) would strengthen the claims. Additionally, while spine morphology is analyzed, incorporating electrophysiological measurements of synaptic strength would better correlate structural changes with functional outcomes.

(4) The authors performed H&E staining to count the number of hippocampal pyramidal neurons; however, H&E lacks specificity for identifying pyramidal neurons. Neuronal-specific IHC staining would be more appropriate for this quantification. Additionally, the manuscript does not mention the counting method used, which should be clarified.

(5) Information on the knockout mice used in the study is missing from the Methods section. Additionally, the sex of the mice should be specified, as exploring potential sex-specific differences in the impact of Mid1 deletion could significantly enhance the study's findings.

Reviewer #3 (Public review):

Summary:

The authors tried to characterize the neuronal deficiency in Mid1 knockout mice. They performed behavioral, neuroelectrophysiological, and pathological experiments to show that Mid1 knockout mice have cognitive function, impaired synaptic plasticity, and changes in gene expression.

Strengths:

The evidence provides insight into the mechanisms of cognitive impairments in Opitz syndrome. Overall, the manuscript is well-organized.

Weaknesses:

(1) The major weakness is that the proposed molecular mechanism is not fully supported by the current data. The data presented here only show that changes in gene expression levels, cognitive impairments, and electrophysiological impairments are correlated with each other, but do not support causality.

(2) The main conclusion is that "The main reason is that the deletion of Mid1 gene will increase the accumulation of Pp2ac protein, inhibit the activity of p-Creb, affect the downstream cAMP pathway, lead to the decrease of synaptic density and plasticity, and ultimately affect the learning and memory ability". This should be toned down, since causality is not supported here.

(3) The description of the results should be improved. Only one figure is presented in the manuscript. Some key information in the supplementary figures should be moved to the main figures. This is very strange since four display items are allowed even for a short report.

Author response:

First of all, I'd like to express my heartfelt thanks to you for your meticulous and professional review comments. Your feedback is very important to our work. It not only helps us identify the shortcomings in the paper, but also provides valuable guidance for improving the quality of the paper.

We carefully read every suggestion you made and were deeply inspired. Please rest assured that we will carefully consider and revise each opinion to ensure that our research work is more rigorous and clear. We promise to revise the manuscript accordingly to meet the standards of the journal and enhance the credibility and influence of the research.

The main modifications include the experiment of A Mid1 supplementation experiment in Mid1 knockout micesupplementing Mid1 in Mid1 knockout mice; Detection of kinases such as CaMKII, PKA and ERK1/2; Supplementary references; Supplement the behavioral experiment of new object recognition; Electrophysiological measurement experiment of supplementing LTP; Supplementary neuron-specific immunohistochemical staining experiment; Supplementing the information of knockout mice used in the study; Modify the language expression of the article and the problem of too few pictures.

Thank you again for your valuable time and professional advice. We look forward to submitting the revised manuscript to you for further review.

eLife Assessment

This study makes a valuable advance in our understanding of defensive symbionts in insects. It uses a meta-analysis to quantify the magnitude of change in host fitness components when symbionts are present in hosts exposed to natural enemies. The evidence supporting the study conclusions is solid, with analyses confirming common assumptions that symbionts generally provide defence at low cost to hosts.

Reviewer #1 (Public review):

Summary:

Cesar, Santos & Cogni use a meta-analysis to report on the direction and magnitude of three fundamental fitness components in defensive symbioses. Specifically, the work focuses on interactions between three arthropod host families (Aphididae, Culicidae, Drosophilidae, and others) and common bacterial endosymbionts (Wolbachia, Serratia, Hamiltonella, Spiroplasma, Rickettsia, Regiella X-type and Arsenophonus). The results of the overall analysis confirm common assumptions and previous work on such fitness components, showing that defensive symbionts provide strong protection to hosts and cause detectable costs to both hosts and the enemy. The analysis provides insight into the extent of the cost/benefit tradeoff for hosts, reporting that the cost is six times lower than the protective effect. The confirmation that natural enemies attacking hosts infected with symbionts have a reduction in their fitness is also an interesting one, as this shows that the majority of defensive symbionts provide protection by resisting enemy infection, as opposed to tolerating it. This finding has important consequences for evolutionary counter-responses in the enemy species. Of course, this result has less relevance for certain types of enemies (such as parasitoids) where successful infection is dependent upon host killing.

Interesting results also emerge from the subgroup analysis. For the full dataset, both natural and introduced symbionts were similarly effective in positively influencing the fitness of hosts. However, in the Wolbachia-specific analysis, the artificially introduced symbionts caused costs to the hosts where the natural strain did not. These findings have potentially important ramifications for schemes that use endosymbionts for biocontrol or vector competence, suggesting that (in some cases) natural strains may be the more stable choice for deploying (as they are associated with lower costs).

The analysis draws from an impressively large dataset, but the interpretation of the full impact of the results would be helped by greater detail on the species/strain level systems included, the data extraction approach, and inclusion criteria. Accounting for phylogenetic nonindependence and alternative coding of one of the moderator variables could also strengthen the biological relevance of the models. Suggestions and thoughts are outlined below.

Strengths & Potential Improvements:

An impressively large number of effect sizes (3000) from only 226 studies is collected, robustly confirming common assumptions on the magnitude of fundamental fitness components. However the paper would benefit from a clear breakdown in the main text of the specificities of each system included (e.g. a table at the host species/symbiont strain level, where it is possible). Currently, there is not enough detail for those who want a deep dive to understand what data was extracted for the analysis from these 226 studies, or those who want to understand the underlying diversity in the dataset.

Currently, when the 'natural enemy group' is tested as a moderator it is coded broadly by type of organism (e.g. virus, bacterium, fungi, parasitoid). But this doesn't adequately capture the mode of killing/fitness reduction by the enemy, which would be the much more biologically relevant categorisation for your questions. For example, parasitoid infection is dependent upon host death (thus host fecundity is not relevant, because the host either survived or did not). Among bacterial and viral pathogens antagonists there is scope for both fecundity and survival to be affected. This in turn may be a very influential factor for the outcome. You could consider recoding this enemy moderator.

The analysis is restricted to arthropod hosts and defensive symbionts that are also classed as endosymbionts. This focus should be made clear early on in the paper, as there are many systems (that are classed by many as defensive symbioses) that are not part of the analysis.

There is fairly minimalistic testing of moderators/sub-groups (which probably has its statistical strengths) but perhaps there are also some missed opportunities for testing other ecological contributors to variance, including coinfection (although perhaps limited by power) and other approaches to coding enemy group (as detail above).

Looking at the overview of systems included, there's likely a high degree of phylogenetic non-independence in the dataset. Where it is possible, using phylogenetically controlled models could strengthen this analysis.

Looking at your included systems (Table S5), you might be able to test the effect of coinfection on the 3 variables of interest. For example, it would be particularly important to see if the effects of two symbionts are additive or not.

No code for the analysis is provided for review at this stage and full details of the dataset are also not available. This slightly limits the ability to assess the full scope and robustness of the study. It would be helpful to have an extensive table in the supplementary detailing (minimum) the reference, study, experiment, host species, symbiont strain, and a description of the exact data extraction source (e.g.table/figure/in text), and method of extraction.

Reviewer #2 (Public review):

Summary:

In this exciting study, Cesar and co-authors perform a meta-analysis on the influence of arthropod symbionts on the fitness of their hosts when they are exposed or not to natural enemies. These so-called defensive symbionts are increasingly recognized as key elements in arthropod survival against natural enemies, with effects that ripple through entire terrestrial ecosystems. The topic is timely, the approach is sound, and the manuscript is well-written. I believe this manuscript will attract the attention of entomologists and of microbiologists interested in symbiosis. This study builds on a previous meta-analysis that I was involved in, which was based on phloem-feeding insects. This novel data set is much larger and includes flies (including the model system Drosophila) and mosquitoes (a group of high medical interest). While the previous meta-analysis considered only parasitoids as natural enemies, this study also includes fungi, bacteria, and viruses.

Strengths:

The authors compile a very large dataset and provide a broad quantitative overview of the effects of defensive symbionts in insects. By measuring symbiont effects in the presence and absence of natural enemies, the authors are able to infer whether a trade-off between defense and the costs of mutualism in the absence of enemy pressure exists. Defensive symbioses are an important research topic that had its initial "momentum" a decade ago, so the timing for such a systematic review is very appropriate.

Weaknesses:

I think the manuscript could be improved by clarifying several sections, particularly the introduction and methods. The introduction section is too specific and heavily reliant on particular examples. In my view, the theoretical background of the study could be made clearer, and the knowledge gap identified more explicitly. A focus on how widespread defensive symbioses are, along with a brief, up-to-date review of the groups possessing such symbionts, would help. This lack of focus is also observed in the methods section, where more details are needed in many instances to better understand how data was collected and analyzed. Regarding the analyses, the multi-level analysis contains many moderators, but it's unclear why these moderators were included. While this may seem a minor issue, it highlights a disconnection between the analyses, the conceptual background, and the hypotheses tested. Another important weakness is that the analyses are too general, and much-hidden information is not immediately apparent. For instance, readers cannot easily identify which species of symbionts are studied (and the effects they have), or which natural enemies are involved. Although this information is found in the supplementary material, including it in the main body would significantly improve the manuscript.

Author response:

Reviewer #1 (Public review):

Summary:

Cesar, Santos & Cogni use a meta-analysis to report on the direction and magnitude of three fundamental fitness components in defensive symbioses. Specifically, the work focuses on interactions between three arthropod host families (Aphididae, Culicidae, Drosophilidae, and others) and common bacterial endosymbionts (Wolbachia, Serratia, Hamiltonella, Spiroplasma, Rickettsia, Regiella X-type and Arsenophonus). The results of the overall analysis confirm common assumptions and previous work on such fitness components, showing that defensive symbionts provide strong protection to hosts and cause detectable costs to both hosts and the enemy. The analysis provides insight into the extent of the cost/benefit tradeoff for hosts, reporting that the cost is six times lower than the protective effect. The confirmation that natural enemies attacking hosts infected with symbionts have a reduction in their fitness is also an interesting one, as this shows that the majority of defensive symbionts provide protection by resisting enemy infection, as opposed to tolerating it. This finding has important consequences for evolutionary counter-responses in the enemy species. Of course, this result has less relevance for certain types of enemies (such as parasitoids) where successful infection is dependent upon host killing.

Interesting results also emerge from the subgroup analysis. For the full dataset, both natural and introduced symbionts were similarly effective in positively influencing the fitness of hosts. However, in the Wolbachia-specific analysis, the artificially introduced symbionts caused costs to the hosts where the natural strain did not. These findings have potentially important ramifications for schemes that use endosymbionts for biocontrol or vector competence, suggesting that (in some cases) natural strains may be the more stable choice for deploying (as they are associated with lower costs).

The analysis draws from an impressively large dataset, but the interpretation of the full impact of the results would be helped by greater detail on the species/strain level systems included, the data extraction approach, and inclusion criteria. Accounting for phylogenetic nonindependence and alternative coding of one of the moderator variables could also strengthen the biological relevance of the models. Suggestions and thoughts are outlined below.

We sincerely thank Reviewer #1 for the time and effort dedicated to reviewing our manuscript. The suggestions provided are highly constructive and will greatly assist us in improving both our analyses and the manuscript overall.

Strengths & Potential Improvements:

An impressively large number of effect sizes (3000) from only 226 studies is collected, robustly confirming common assumptions on the magnitude of fundamental fitness components. However the paper would benefit from a clear breakdown in the main text of the specificities of each system included (e.g. a table at the host species/symbiont strain level, where it is possible). Currently, there is not enough detail for those who want a deep dive to understand what data was extracted for the analysis from these 226 studies, or those who want to understand the underlying diversity in the dataset.

We thank the reviewer for the suggestion, and we will add this information to our revised manuscript.

Currently, when the 'natural enemy group' is tested as a moderator it is coded broadly by type of organism (e.g. virus, bacterium, fungi, parasitoid). But this doesn't adequately capture the mode of killing/fitness reduction by the enemy, which would be the much more biologically relevant categorisation for your questions. For example, parasitoid infection is dependent upon host death (thus host fecundity is not relevant, because the host either survived or did not). Among bacterial and viral pathogens antagonists there is scope for both fecundity and survival to be affected. This in turn may be a very influential factor for the outcome. You could consider recoding this enemy moderator.

We agree, and we will implement this in the analysis to our revised manuscript.

The analysis is restricted to arthropod hosts and defensive symbionts that are also classed as endosymbionts. This focus should be made clear early on in the paper, as there are many systems (that are classed by many as defensive symbioses) that are not part of the analysis.

We agree, and we will implement this to our revised manuscript.

There is fairly minimalistic testing of moderators/sub-groups (which probably has its statistical strengths) but perhaps there are also some missed opportunities for testing other ecological contributors to variance, including coinfection (although perhaps limited by power) and other approaches to coding enemy group (as detail above).

We agree, and we will implement this in the analysis to our revised manuscript.

Looking at the overview of systems included, there's likely a high degree of phylogenetic non-independence in the dataset. Where it is possible, using phylogenetically controlled models could strengthen this analysis.

We thank the reviewer for the suggestion. We will explore the possibility of using phylogenetically controlled models in our analyses, although we recognize the challenges associated with their implementation, particularly in the case of the natural enemies, given the great diversity of distant related groups included in our study - viruses, bacteria, fungi, protozoans, nematodes and parasitoids wasps.

Looking at your included systems (Table S5), you might be able to test the effect of coinfection on the 3 variables of interest. For example, it would be particularly important to see if the effects of two symbionts are additive or not.

We agree, and we will implement this in the analysis to our revised manuscript.

No code for the analysis is provided for review at this stage and full details of the dataset are also not available. This slightly limits the ability to assess the full scope and robustness of the study. It would be helpful to have an extensive table in the supplementary detailing (minimum) the reference, study, experiment, host species, symbiont strain, and a description of the exact data extraction source (e.g.table/figure/in text), and method of extraction.

The code for the analysis and the full raw data with the suggested information are available at https://github.com/cassiasqr/MetaSymbiont (The link is available at the end of the manuscript).

Reviewer #2 (Public review):

Summary:

In this exciting study, Cesar and co-authors perform a meta-analysis on the influence of arthropod symbionts on the fitness of their hosts when they are exposed or not to natural enemies. These so-called defensive symbionts are increasingly recognized as key elements in arthropod survival against natural enemies, with effects that ripple through entire terrestrial ecosystems. The topic is timely, the approach is sound, and the manuscript is well-written. I believe this manuscript will attract the attention of entomologists and of microbiologists interested in symbiosis. This study builds on a previous meta-analysis that I was involved in, which was based on phloem-feeding insects. This novel data set is much larger and includes flies (including the model system Drosophila) and mosquitoes (a group of high medical interest). While the previous metaanalysis considered only parasitoids as natural enemies, this study also includes fungi, bacteria, and viruses.

Strengths:

The authors compile a very large dataset and provide a broad quantitative overview of the effects of defensive symbionts in insects. By measuring symbiont effects in the presence and absence of natural enemies, the authors are able to infer whether a trade-off between defense and the costs of mutualism in the absence of enemy pressure exists. Defensive symbioses are an important research topic that had its initial "momentum" a decade ago, so the timing for such a systematic review is very appropriate.

We sincerely thank Reviewer #2 for dedicating their time and effort to reviewing our manuscript. The suggestions are very insightful and will significantly contribute to improving our manuscript.

Weaknesses:

I think the manuscript could be improved by clarifying several sections, particularly the introduction and methods. The introduction section is too specific and heavily reliant on particular examples. In my view, the theoretical background of the study could be made clearer, and the knowledge gap identified more explicitly. A focus on how widespread defensive symbioses are, along with a brief, up-to-date review of the groups possessing such symbionts, would help. This lack of focus is also observed in the methods section, where more details are needed in many instances to better understand how data was collected and analyzed. Regarding the analyses, the multi-level analysis contains many moderators, but it's unclear why these moderators were included. While this may seem a minor issue, it highlights a disconnection between the analyses, the conceptual background, and the hypotheses tested. 

We thank the reviewer for the suggestions, and we will try to make the introduction and the methods section clearer. 

Another important weakness is that the analyses are too general, and much-hidden information is not immediately apparent. For instance, readers cannot easily identify which species of symbionts are studied (and the effects they have), or which natural enemies are involved. Although this information is found in the supplementary material, including it in the main body would significantly improve the manuscript.

We agree, and we will implement this to our   revised manuscript.

eLife Assessment

This valuable study provides new insights into the role of the conserved protein FLWR-1/Flower in synaptic transmission using C. elegans. The authors employ a range of techniques, including calcium imaging, ultrastructural analysis, and electrophysiology, providing evidence that challenges previous assumptions about FLWR-1 function. While some findings are solid, several conclusions remain incomplete and require further study to substantiate the proposed mechanisms.

Reviewer #1 (Public review):

Summary:

In this study, Seidenthal et al. investigated the role of the C. elegans Flower protein, FLWR-1, in synaptic transmission, vesicle recycling, and neuronal excitability. They confirmed that FLWR-1 localizes to synaptic vesicles and the plasma membrane and facilitates synaptic vesicle recycling at neuromuscular junctions, albeit in an unexpected manner. The authors observed that hyperstimulation results in endosome accumulation in flwr-1 mutant synapses, suggesting that FLWR-1 facilitates the breakdown of endocytic endosomes, which differs from earlier studies in flies that suggested the Flower protein promotes the formation of bulk endosomes. This is a valuable finding. Using tissue-specific rescue experiments, the authors showed that expressing FLWR-1 in GABAergic neurons restored the aldicarb-resistant phenotype seen in flwr-1 mutants to wild-type levels. In contrast, FLWR-1 expression in cholinergic neurons in flwr-1 mutants did not restore aldicarb sensitivity, yet muscle expression of FLWR-1 partially but significantly recovered the aldicarb-resistant defects. The study also revealed that removing FLWR-1 leads to increased Ca2+ signaling in motor neurons upon photo-stimulation. Further, the authors conclude that FLWR-1 contributes to the maintenance of the excitation/inhibition (E/I) balance by preferentially regulating the excitability of GABAergic neurons. Finally, SNG-1::pHluorin data imply that FLWR-1 removal enhances synaptic transmission, however, the electrophysiological recordings do not corroborate this finding.

Strengths:

This study by Seidenthal et al. offers valuable insights into the role of the Flower protein, FLWR-1, in C. elegans. Their findings suggest that FLWR-1 facilitates the breakdown of endocytic endosomes, which marks a departure from its previously suggested role in forming endosomes through bulk endocytosis. This observation could be important for understanding how Flower proteins function across species. In addition, the study proposes that FLWR-1 plays a role in maintaining the excitation/inhibition balance, which has potential impacts on neuronal activity.

Weaknesses:

One issue is the lack of follow-up tests regarding the relative contributions of muscle and GABAergic FLWR-1 to aldicarb sensitivity. The findings that muscle expression of FLWR-1 can significantly rescue aldicarb sensitivity are intriguing and may influence both experimental design and data interpretation. Have the authors examined aldicarb sensitivity when FLWR-1 is expressed in both muscles and GABAergic neurons, or possibly in muscles and cholinergic neurons? Given that muscles could influence neuronal activity through retrograde signaling, a thorough examination of FLWR-1's role in muscle is necessary, in my opinion.

Would the results from electrophysiological recordings and GCaMP measurements be altered with muscle expression of FLWR-1? Most experiments presented in the manuscript compare wild-type and flwr-1 mutant animals. However, without tissue-specific knockout, knockdown, or rescue experiments, it is difficult to separate cell-autonomous roles from non-cell-autonomous effects, in particular in the context of aldicarb assay results. Also, relying solely on levamisole paralysis experiments is not sufficient to rule out changes in muscle AChRs, particularly due to the presence of levamisole-resistant receptors.

This issue regarding the muscle role of FLWR-1 also complicates the interpretation of results from coelomocyte uptake experiments, where GFP secreted from muscles and coelomocyte fluorescence were used to estimate endocytosis levels. A decrease in coelomocyte GFP could result from either reduced endocytosis in coelomocytes or decreased secretion from muscles. Therefore, coelomocyte-specific rescue experiments seem necessary to distinguish between these possibilities.

The manuscript states that GCaMP was used to estimate Ca2+ levels at presynaptic sites. However, due to the rapid diffusion of both Ca2+ and GCaMP, it is unclear how this assay distinguishes Ca2+ levels specifically at presynaptic sites versus those in axons. What are the relative contributions of VGCCs and ER calcium stores here? This raises a question about whether the authors are measuring the local impact of FLWR-1 specifically at presynaptic sites or more general changes in cytoplasmic calcium levels.

The experiments showing FLWR-1's presynaptic localization need clarification/improvement. For example, data shown in Fig. 3B represent GFP::FLWR-1 is expressed under its own promoter, and TagRFP::ELKS-1 is expressed exclusively in GABAergic neurons. Given that the pflwr-1 drives expression in both cholinergic and GABAergic neurons, and there are more cholinergic synapses outnumbering GABAergic ones in the nerve cord, it would be expected that many green FLWR-1 puncta do not associate with TagRFP::ELKS-1. However, several images in Figure 3B suggest an almost perfect correlation between FLWR-1 and ELKS-1 puncta. It would be helpful for the readers to understand the exact location in the nerve cord where these images were collected to avoid confusion.

The SNG-1::pHluorin data in Figure 5C is significant, as they suggest increased synaptic transmission at flwr-1 mutant synapses. However, to draw conclusions, it is necessary to verify whether the total amount of SNG-1::pHluorin present on synaptic vesicles remains the same between flwr-1 mutant and wild-type synapses. Without this comparison, a conclusion on levels of synaptic vesicle release based on changes in fluorescence might be premature, in particular given the results of electrophysiological recordings.

Finally, the interpretation of the E74Q mutation results needs reconsideration. Figure 8B indicates that the E74Q variant of FLWR-1 partially loses its rescuing ability, which suggests that the E74Q mutation adversely affects the function of FLWR-1. Why did the authors expect that the role of FLWR-1 should have been completely abolished by E74Q? Given that FLWR-1 appears to work in multiple tissues, might FLWR-1's function in neurons requires its calcium channel activity, whereas its role in muscles might be independent of this feature? While I understand there is ongoing debate about whether FLWR-1 is a calcium channel, the experiments in this study do not definitively resolve local Ca2+ dynamics at synapses. Thus, in my opinion, it may be premature to draw firm conclusions about calcium influx through FLWR-1.

Also, the aldicarb data presented in Figures 8B and 8D show notable inconsistencies that require clarification. While Figure 8B indicates that the 50% paralysis time for flwr-1 mutant worms occurs at 3.5-4 hours, Figure 8D shows that 50% paralysis takes approximately 2.5 hours for the same flwr-1 mutants. This discrepancy should be addressed. In addition, the manuscript mentions that the E74Q mutation impairs FLWR-1 folding, which could significantly affect its function. Can the authors show empirical data supporting this claim?

Reviewer #2 (Public review):

Summary:

The Flower protein is expressed in various cell types, including neurons. Previous studies in flies have proposed that Flower plays a role in neuronal endocytosis by functioning as a Ca2+ channel. However, its precise physiological roles and molecular mechanisms in neurons remain largely unclear. This study employs C. elegans as a model to explore the function and mechanism of FLWR-1, the C. elegans homolog of Flower. This study offers intriguing observations that could potentially challenge or expand our current understanding of the Flower protein. Nevertheless, further clarification or additional experiments are required to substantiate the study's conclusions.

Strengths:

A range of approaches was employed, including the use of a flwr-1 knockout strain, assessment of cholinergic synaptic activity via analyzing aldicarb (a cholinesterase inhibitor) sensitivity, imaging Ca2+ dynamics with GCaMP3, analyzing pHluorin fluorescence, examination of presynaptic ultrastructure by EM, and recording postsynaptic currents at the neuromuscular junction. The findings include notable observations on the effects of flwr-1 knockout, such as increased Ca2+ levels in motor neurons, changes in endosome numbers in motor neurons, altered aldicarb sensitivity, and potential involvement of a Ca2+-ATPase and PIP2 binding in FLWR-1's function.

Weaknesses:

(1) The observation that flwr-1 knockout increases Ca2+ levels in motor neurons is notable, especially as it contrasts with prior findings in flies. The authors propose that elevated Ca2+ levels in flwr-1 knockout motor neurons may stem from "deregulation of MCA-3" (a Ca2+ ATPase in the plasma membrane) due to FLWR-1 loss. However, this conclusion relies on limited and somewhat inconclusive data (Figure 7). Additional experiments could clarify FLWR-1's role in MCA-3 regulation. For instance, it would be informative to investigate whether mutations in other genes that cause elevated cytosolic Ca2+ produce similar effects, whether MCA-3 physically interacts with FLWR-1, and whether MCA-3 expression is reduced in the flwr-1 knockout.

(2) In silico analysis identified residues R27 and K31 as potential PIP2 binding sites in FLWR-1. The authors observed that FLWR-1(R27A/K31A) was less effective than wild-type FLWR-1 in rescuing the aldicarb sensitivity phenotype of the flwr-1 knockout, suggesting that FLWR-1 function may depend on PIP2 binding at these two residues. Given that mutations in various residues can impair protein function non-specifically, additional studies may be needed to confirm the significance of these residues for PIP2 binding and FLWR-1 function. In addition, the authors might consider explicitly discussing how this finding aligns or contrasts with the results of a previous study in flies, where alanine substitutions at K29 and R33 impaired a Flower-related function (Li et al., eLife 2020).

(3) A primary conclusion from the EM data was that FLWR-1 participates in the breakdown, rather than the formation, of bulk endosomes (lines 20-22). However, the reasoning behind this conclusion is somewhat unclear. Adding more explicit explanations in the Results section would help clarify and strengthen this interpretation.

(4) The aldicarb assay results in Figure 3 are intriguing, indicating that reduced GABAergic neuron activity alone accounts for the flwr-1 mutant's hyposensitivity to aldicarb. Given that cholinergic motor neurons also showed increased activity in the flwr-1 mutant, one might expect the flwr-1 mutant to display hypersensitivity to aldicarb in the unc-47 knockout background. However, this was not observed. The authors might consider validating their conclusion with an alternative approach or, at the minimum, providing a plausible explanation for the unexpected result. Since aldicarb-induced paralysis can be influenced by factors beyond acetylcholine release from cholinergic motor neurons, interpreting aldicarb assay results with caution may be advisable. This is especially relevant here, as FLWR-1 function in muscle cells also impacts aldicarb sensitivity (Figure S3B). Previous electrophysiological studies have suggested that aldicarb sensitivity assays may sometimes yield misleading conclusions regarding protein roles in acetylcholine release.

(5) Previous studies have suggested that the Flower protein functions as a Ca²⁺ channel, with a conserved glutamate residue at the putative selectivity filter being essential for this role. However, mutating this conserved residue (E74Q) in C. elegans FLWR-1 altered aldicarb sensitivity in a direction opposite to what would be expected for a Ca²⁺ channel function. Moreover, the authors observed that E74 of FLWR-1 is not located near a potential conduction pathway in the FLWR-1 tetramer, as predicted by Alphafold3. These findings raise the possibility that Flower may not function as a Ca2+ channel. While this is a potentially significant discovery, further experiments are needed to confirm and expand upon these results.

(6) Phrases like "increased excitability" and "increased Ca2+ influx" are used throughout the manuscript. However, there is no direct evidence that motor neurons exhibit increased excitability or Ca2+ influx. The authors appear to interpret the elevated Ca2+ signal in motor neurons as indicative of both increased excitability and Ca2+ influx. However, this elevated Ca2+ signal in the flwr-1 mutant could occur independently of changes in excitability or Ca2+ influx, such as in cases of reduced MCA-3 activity. The authors may wish to consider alternative terminology that more accurately reflects their findings.

Reviewer #3 (Public review):

Summary:

Seidenthal et al. investigated the role of the Flower protein, FLWR-1, in C. elegans and confirmed its involvement in endocytosis within both synaptic and non-neuronal cells, possibly by contributing to the fission of bulk endosomes. They also uncovered that FLWR-1 has a novel inhibitory effect on neuronal excitability at GABAergic and cholinergic synapses in neuromuscular junctions.

Strengths:

This study not only reinforces the conserved role of the Flower protein in endocytosis across species but also provides valuable ultrastructural data to support its function in the bulk endosome fission process. Additionally, the discovery of FLWR-1's role in modulating neuronal excitability broadens our understanding of its functions and opens new avenues for research into synaptic regulation.

Weaknesses:

The study does not address the ongoing debate about the Flower protein's proposed Ca2+ channel activity, leaving an important aspect of its function unexplored. Furthermore, the evidence supporting the mechanism by which FLWR-1 inhibits neuronal excitability is limited. The suggested involvement of MCA-3 as a mediator of this inhibition lacks conclusive evidence, and a more detailed exploration of this pathway would strengthen the findings.

eLife Assessment

This important study introduces rationally designed, genetically encoded tools for the selective and reversible ablation of excitatory and inhibitory synapses. The evidence is convincing, supported by robust experiments and clear results that validate the effectiveness of each tool. This work will be of particular interest to researchers exploring the roles of specific synapses within neural circuitry.

Reviewer #1 (Public review):

Summary:

This work is a continuation of a previous paper from the Arnold group, where they engineered GFE3, which allows to specifically ablate inhibitory synapses. Here, the authors generate 3 different actuators:

(1) An excitatory synapse ablator.

(2) A photoactivatable inhibitory synapse ablator.

(3) A chemically inhibitory synapse ablator.

Following initial engineering, the authors present characterization and optimization data to showcase that these new tools allow one to specifically ablate synapses, without toxicity and with specificity. Furthermore, they showcase that these manipulations are reversible.

Altogether, these new tools would be important for the neuroscience community.

Strengths:

The authors convincingly demonstrate the engineering, optimization, and characterization of these new probes. The main novelty here is the new excitatory synapse ablator, which has not been shown yet and thus could be a valuable tool for neuroscientists.

Weaknesses:

There are a few specific issues with regard to these probes that are unclear to me, which require some explanation or potentially new analysis and experiments.

The biggest concern in this regard is: that almost all the characterization is performed in cultured dissociated neurons. I wonder if, for the typical neuroscience user, it would be trivial to characterize how well these tools express and operate in vivo. This could be substantially different and present some limitations as to the utility of these tools.

Reviewer #2 (Public review):

Summary:

This study introduces a set of genetically encoded tools for the selective and reversible ablation of excitatory and inhibitory synapses. Previously, the authors developed GFE3, a tool that efficiently ablates inhibitory synapses by targeting an E3 ligase to the inhibitory scaffolding protein Gephyrin via GPHN.FingR, a recombinant, antibody-like protein (Gross et al., 2016). Building on this work, they now present three new ablation tools: PFE3, which targets excitatory synapses, and two new versions of GFE3-paGFE3 and chGFE3-that are photoactivatable and chemically inducible, respectively. These tools enable selective and efficient synapse ablation in specific cell types, providing valuable methods for disrupting neural circuits. This approach holds broad potential for investigating the roles of specific synaptic input onto genetically determined cells.

Strengths:

The primary strength of this study lies in the rational design and robust validation of each tool's effectiveness, building on previous work by the authors' group (Gross et al., 2016). Each tool serves distinct research needs: PFE3 enables efficient degradation of PSD-95 at excitatory synapses, while paGFE3 and chGFE3 allow for targeted degradation of Gephyrin, offering spatiotemporal control over inhibitory synapses via light or chemical activation. These tools are efficiently validated through robust experiments demonstrating reductions in synaptic markers (PSD-95 and Gephyrin) and confirming reversibility, which is crucial for transient ablation. By providing tools with both optogenetic and chemical control options, this study broadens the applicability of synapse manipulation across varied experimental conditions, enhancing the utility of E3 ligase-based approaches for synapse ablation.

Weaknesses:

While this study provides valuable tools and addresses many critical points for validation, examining potential issues with specificity and background effects in further detail could strengthen the paper. For instance, PFE3 results in reductions in both PSD-95 and GluA1. In previous work, GFE3 selectively reduced Gephyrin without affecting major Gephyrin interactors or other PSD proteins. Clarifying whether PFE3 affects additional PSD proteins beyond GluA1 would be important for accurately interpreting results in experiments using PFE3. Additionally, further insight into PFE3's impact on inhibitory synapses would be valuable.

For paGFE3 and chGFE3, the E3 ligase (RING domain of Mdm2) is overexpressed throughout cells as a separate construct. Although the authors show that Gephyrin is not significantly reduced without light or chemical activation, it remains possible that other proteins could be ubiquitinated due to the overexpressed E3 domain. Addressing these points would clarify the strengths and limitations of tools, providing users with valuable information.

eLife Assessment

This paper is an important overview of the currently published literature on low-intensity focussed ultrasound stimulation (TUS) in humans, with a meta-analysis of this literature that explores which stimulation parameters might predict the directionality of the physiological stimulation effects. Whilst currently incomplete, the database proposed by the paper has the potential to become a key community resource if carefully curated and developed.

Reviewer #1 (Public review):

Summary:

This paper is a relevant overview of the currently published literature on low-intensity focussed ultrasound stimulation (TUS) in humans, with a meta-analysis of this literature that explores which stimulation parameters might predict the directionality of the physiological stimulation effects.

The pool of papers to draw from is small, which is not surprising given the nascent technology. It seems nevertheless relevant to summarize the current field in the way done here, not least to mitigate and prevent some of the mistakes that other non-invasive brain stimulation techniques have suffered from, most notably the theory- and data-free permutation of the parameter space.<br /> The meta-analysis concludes that there are, at best, weak trends toward specific parameters predicting the direction of the stimulation effects. The data have been incorporated into an open database, that will ideally continue to be populated by the community and thereby become a helpful resource as the field moves forward.

Strengths:

The current state of human TUS is concisely and well summarized. The methods of the meta-analysis are appropriate. The database is a valuable resource.

Weaknesses:

These are not so much weaknesses but rather comments and suggestions that the authors may want to consider.

(1) I may have missed this, but how will the database be curated going forward? The resource will only be as useful as the quality of data entry, which, given the complexity of TUS can easily be done incorrectly.

(2) It would be helpful to report the full statistics and effect sizes for all analyses. At times, only p-values are given. The meta-analysis only provides weak evidence (judged by the p-values) for two parameters having a predictive effect on the direction of neuromodulation. This reviewer thinks a stronger statement is warranted that there is currently no good evidence for duty cycle or sonication direction predicting outcome (though I caveat this given the full stats aren't reported). The concern here is that some readers may gallop away with the impression that the evidence is compelling because the p-value is on the correct side of 0.05.

(3) This reviewer thinks the issue of (independent) replication should be more forcefully discussed and highlighted. The overall motivation for the present paper is clearly and thoughtfully articulated, but perhaps the authors agree that the role that replication has to play in a nascent field such as TUS is worth considering.

(4) A related point is that many of the results come from the same groups (the so-called theta-TUS protocol being a clear example). The analysis could factor this in, but it may be helpful to either signpost independent replications, which studies come from the same groups, or both.

(5) The recent study by Bao et al 2024 J Phys might be worth including, not least because it fails to replicate the results on theta TUS that had been limited to the same group so far (by reporting, in essence, the opposite result).

(6) The summary of TUS effects is useful and concise. Two aspects may warrant highlighting, if anything to safeguard against overly simplistic heuristics for the application of TUS from less experienced users. First, could the effects of sonication (enhancing vs suppressing) depend on the targeted structure? Across the cortex, this may be similar, but for subcortical structures such as the basal ganglia, thalamus, etc, the idiosyncratic anatomy, connectivity, and composition of neurons may well lead to different net outcomes. Do the models mentioned in this paper account for that or allow for exploring this? And is it worth highlighting that simple heuristics that assume the effects of a given TUS protocol are uniform across the entire brain risk oversimplification or could be plain wrong? Second, and related, there seems to be the implicit assumption (not necessarily made by the authors) that the effects of a given protocol in a healthy population transfer like for like to a patient population (if TUS protocol X is enhancing in healthy subjects, I can use it for enhancement in patient group Y). This reviewer does not know to which degree this is valid or not, but it seems simplistic or risky. Many neurological and psychiatric disorders alter neurotransmission, and/or lead to morphological and structural changes that would seem capable of influencing the impact of TUS. If the authors agree, this issue might be worth highlighting.

Reviewer #2 (Public review):

Summary:

This paper describes a number of aspects of transcranial ultrasound stimulation (TUS) including a generic review of what TUS might be used for; a meta-analysis of human studies to identify ultrasound parameters that affect directionality; a comparison between one postulated mechanistic model and results in humans; and a description of a database for collecting information on studies.

Strengths:

The main strength was a meta-analysis of human studies to identify which ultrasonic parameters might result in enhancement or suppression of modulation effects. The meta-analysis suggests that none of the US parameters correlate significantly with effects. This is a useful result for researchers in the field in trying to determine how the parameter space should be further investigated to identify whether it is possible to indeed enhance or suppress brain activity with ultrasound.

The database is a good idea in principle but would be best done in collaboration with ITRUSST, an international consortium, and perhaps should be its own paper.

Weaknesses:

The paper tries to cover too many topics and some of the technical descriptions are a bit loose. The review section does not add to the current literature. The comparison with a mechanistic model is limited to comparing data with a single model at a time when there is no general agreement in the field as to how ultrasound might produce a neuromodulation effect. The comparison is therefore of limited value.

eLife Assessment

This important study includes convincing evidence to show that behavioral measures and hippocampal representations of cognitive control are not dependent upon the medial prefrontal cortex. Whilst overall the study is of importance, it is possible that the conceptual framework used to interpret and discuss the findings could be strengthened in a revised version. The results are expected to be of interest to those studying neural mechanisms of cognitive control and functions of associational brain regions.

Reviewer #1 (Public review):

Summary:

The authors examine the role of the medial prefrontal cortex (mPFC) in cognitive control, i.e. the ability to use task-relevant information and ignore irrelevant information, in the rat. According to the central-computation hypothesis, cognitive control in the brain is centralized in the mPFC and according to the local hypothesis, cognitive control is performed in task-related local neural circuits. Using the place avoidance task which involves cognitive control, it is predicted that if mPFC lesions affect learning, this would support the central computation hypothesis whereas no effect of lesions would rather support the local hypothesis. The authors thus examine the effect of mPFC lesions in learning and retention of the place avoidance task. They also look at functional interconnectivity within a large network of areas that could be activated during the task by using cytochrome oxydase, a metabolic marker. In addition, electrophysiological unit recordings of CA1 hippocampal cells are made in a subset of (lesioned or intact) animals to evaluate overdispersion, a firing property that reflects cognitive control in the hippocampus. The results indicate that mPFC lesions do not impair place avoidance learning and retention (though flexibility is altered during conflict training), do not affect cognitive control seen in hippocampal place cell activity (alternation of frame-specific firing), a measure of location-specific firing variability, in pretraining. It nevertheless has some effect on functional interconnections. The results overall support the local hypothesis.

Strengths:

(1) Straightforward hypothesis: clarification of the involvement of the mPFC in the brain is expected and achieved. Appropriate use of fully mastered methods (behavioral task, electrophysiological recordings, measure of metabolic marker cytochrome oxidase) and rigorous analysis of the data. The conclusion is strongly supported by the data.

(2) Weaknesses: No notable weaknesses in the conception, making of the study, and data analysis. The introduction does not mention important aspects of the work, i.e. cytochrome oxidase measure and electrophysiological recordings. The study is actually richer than expected from the introduction.

Reviewer #2 (Public review):

Park et al. set out to test two competing hypotheses about the role of the medial prefrontal cortex (PFC) in cognitive control, the ability to use task-relevant cues and ignore task-irrelevant cues to guide behavior. The "central computation" hypothesis assumes that cognitive control relies on computations performed by the PFC, which then interacts with other brain regions to accomplish the task. Alternatively, the "local computation" hypothesis suggests that computations necessary for cognitive control are carried out by other brain regions that have been shown to be essential for cognitive control tasks, such as the dorsal hippocampus and the thalamus. If the central computation hypothesis is correct, PFC lesions should disrupt cognitive control. Alternatively, if the local computation hypothesis is correct, cognitive control would be spared after PFC lesions. The task used to assess cognitive control is the active place avoidance task in which rats must avoid a section of a rotating arena using the stationary room cues and ignoring the local olfactory cues on the rotating platform. Performance on this task has previously been shown to be disrupted by hippocampal lesions and hippocampal ensembles dynamically represent the room and arena depending on the animal's proximity to the shock zone. They found no group (lesion vs. sham) differences in the three behavioral parameters tested: distance traveled, latency to enter the shock zone, and number of shock zone entries for both the standard task and the "conflict" task in which the shock zone was rotated by 180 degrees. The only significant difference was the savings index; the lesion group entered the new shock zone more often than the sham group during the first 5 minutes of the second conflict session. This deficit was interpreted as a cognitive flexibility deficit rather than a cognitive control failure. Next, the authors compared cytochrome oxidase activity between sham and lesion groups in 14 brain regions and found that only the amygdala showed significant elevation in the lesion vs. sham group. Pairwise correlation analysis revealed a striking difference between groups, with many correlations between regions lost in the lesion group (between reuniens and hippocampus, reuniens and amygdala and a correlation between dorsal CA1 and central amygdala that appeared in the lesion group and were absent in the sham group. Finally, the authors assessed dorsal hippocampal representations of the spatial frame (arena vs. room) and found no differences between lesion and sham groups. The only difference in hippocampal activity was reduced overdispersion in the lesion group compared to the sham group on the pretraining session only and this difference disappeared after the task began. Collectively, the authors interpret their findings as supporting the local computation hypothesis; computations necessary for cognitive control occur in brain regions other than the PFC.

Strengths:

(1) The data were collected in a rigorous way with experimental blinding and appropriate statistical analyses.

(2) Multiple approaches were used to assess differences between lesion and sham groups, including behavior, metabolic activity in multiple brain regions, and hippocampal single-unit recording.

Weaknesses:

(1) Only male rats were used with no justification provided for excluding females from the sample.

(2) The conceptual framework used to interpret the findings was to present two competing hypotheses with mutually exclusive predictions about the impact of PFC lesions on cognitive control. The authors then use mainly null findings as evidence in support of the local computation hypothesis. They acknowledge that some people may question the notion that the active place avoidance task indeed requires cognitive control, but then call the argument "circular" because PFC has to be involved in cognitive control. This assertion does not address the possibility that the active place avoidance task simply does not require cognitive control.

(3) The authors did not link the CO activity with the behavioral parameters even though the CO imaging was done on a subset of the animals that ran the behavioral task nor did they make any attempt to interpret these findings in light of the two competing hypotheses posed in the introduction. Moreover, the discussion lacks any mechanistic interpretations of the findings. For example, there are no attempts to explain why amygdala activity and its correlation with dCA1 activity might be higher in the PFC lesioned group.

(4) Publishing null results is important to avoid wasting animals, time, and money. This study's results will have a significant impact on how the field views the role of the PFC in cognitive control. Whether or not some people reject the notion that the active place avoidance task measures cognitive control, the findings are solid and can serve as a starting point for generating hypotheses about how brain networks change when deprived of PFC input.

Reviewer #3 (Public review):

Summary:

This study by Park and colleagues investigated how the medial prefrontal cortex (mPFC) influences behavior and hippocampal place cell activity during a two-frame active place avoidance task in rats. Rats learned to avoid the location of mild shock within a rotating arena, with the shock zone being defined relative to distal cues in the room. Permanent chemical lesions of the mPFC did not impair the ability to avoid the shock zone by using distal cues and ignoring proximal cues in the arena. In parallel, hippocampal place cells alternated between two spatial tuning patterns, one anchored to the distal cues and the other to the proximal cues, and this alteration was not affected by the mPFC lesion. Based on these findings, the authors argue that the mPFC is not essential for differentiating between task-relevant and irrelevant information.

Strengths:

This study was built on substantial work by the Fenton lab that validated their two-frame active place avoidance task and provided sound theoretical and analytical foundations. Additionally, the effectiveness of mPFC lesions was validated by several measures, enabling the authors to base their argument on the lack of lesion effects on behavior and place cell dynamics.

Weaknesses:

The authors define cognitive control as "the ability to judiciously use task-relevant information while ignoring salient concurrent information that is currently irrelevant for the task." (Lines 77-78). This definition is much simpler than the one by Miller and Cohen: "the ability to orchestrate thought and action in accordance with internal goals (Ref. 1)" and by Robbins: "processes necessary for optimal scheduling of complex sequence of behaviour." (Dalley et al., 2004, PMID: 15555683). Differentiating between task-relevant and irrelevant information is required in various behavioral tasks, such as differential learning, reversal learning, and set-shifting tasks. Previous rodent behavioral studies have shown that the integrity of the mPFC is necessary for set-shifting but not for differential or reversal learning (e.g., Enomoto et al., 2011, PMID: 21146155; Cho et al., 2015, PMID: 25754826). In the present task design, the initial training is a form of differential learning between proximal and distal cues, and the conflict training is akin to reversal learning. Therefore, the lack of lesion effects is somewhat expected. It would be interesting to test whether mPFC lesions impair set-shifting in their paradigm (e.g., the shock zone initially defined by distal cues and later by proximal cues). If the mPFC lesions do not impair this ability and associated hippocampal place dynamics, it will provide strong support for the authors' local-computation hypothesis.

eLife Assessment

This manuscript represents a fundamental contribution demonstrating that fentanyl-induced respiratory depression can be reversed with a peripherally-restricted mu opioid receptor antagonist. The paper reports compelling and rigorous physiological, pharmacokinetic, and behavioral evidence supporting this major claim, and furthers mechanistic understanding of how peripheral opioid receptors contribute to respiratory depression. These findings reshape our understanding of opioid-related effects on respiration and have significant therapeutic implications given that medications currently used to reverse opioid overdose (such as naloxone) produce severe aversive and withdrawal effects via actions within the central nervous system.

Reviewer #1 (Public review):

Summary:

This paper shows that the synthetic opioid fentanyl induces respiratory depression in rodents. This effect is revised by the opioid receptor antagonist naloxone, as expected. Unexpectedly, the peripherally restricted opioid receptor antagonist naloxone methiodide also blocks fentanyl-induced respiratory depression.

Strengths:

The paper reports compelling physiology data supporting the induction of respiratory distress in fentanyl-treated animals. Evidence suggesting that naloxone methiodide reverses this respiratory depression is compelling. This is further supported by pharmacokinetic data suggesting that naloxone methiodide does not penetrate into the brain, nor is it metabolized into brain-penetrant naloxone.

Weaknesses:

A weakness of the study is the fact that the functional significance of opioid-induced changes in neural activity in the nTS (as measured by cFos and GcAMP/photometry) is not established. Does the nTS regulate fentanyl-induced respiratory depression, and are changes in nTS activity induced by naloxone and naloxone methiodide relevant to their ability to reverse respiratory depression?

Reviewer #2 (Public review):

Summary:

In this article, Ruyle and colleagues assessed the contribution of central and peripheral mu opioid receptors in mediating fentanyl-induced respiratory depression using both naloxone and naloxone methiodide, which does not cross the blood-brain barrier. Both compounds prevented and reversed fentanyl-induced respiratory depression to a comparable degree. The advantage of peripheral treatments is that they circumvent the withdrawal-like effects of naloxone. Moreover, neurons located in the nucleus of the solitary tract are no longer activated by fentanyl when nalaxone methiodide is administered, suggesting that these responses are mediated by peripheral mu opioid receptors. The results delineate a role for peripheral mu opioid receptors in fentanyl-derived respiratory depression and identify a potentially advantageous approach to treating overdoses without inflicting withdrawal on the patients.

Strengths:

The strengths of the article include the intravenous delivery of all compounds, which increase the translational value of the article. The authors address both the prevention and reversal of fentanyl-derived respiratory depression. The experimental design and data interpretation are rigorous and appropriate controls were used in the study. Multiple doses were screened in the study and the approaches were multipronged. The authors demonstrated the activation of NTS cells using multiple techniques and the study links peripheral activation of mu opioid receptors to central activation of NTS cells. Both males and females were used in the experiments. The authors demonstrate the peripheral restriction of naloxone methiodide.

Weaknesses:

Nalaxone is already broadly used to prevent overdoses from opioids so in some respects, the effects reported here are somewhat incremental.

Reviewer #3 (Public review):

Summary:

This manuscript outlines a series of very exciting and game-changing experiments examining the role of peripheral MORs in OIRD. The authors outline experiments that demonstrate a peripherally restricted MOR antagonist (NLX Methiodide) can rescue fentanyl-induced respiratory depression and this effect coincides with a lack of conditioned place aversion. This approach would be a massive boon to the OUD community, as there are a multitude of clinical reports showing that naloxone rescue post fentanyl over-intoxication is more aversive than the potential loss-of-life to the individuals involved. This important study reframes our understanding of successful overdose rescue with potential for reduced aversive withdrawal effects.

Strengths:

Strengths include the plethora of approaches arriving at the same general conclusion, the inclusion of both sexes and the result that a peripheral approach for OIRD rescue may side-step severe negative withdrawal symptoms of traditional NLX rescue.

Weaknesses:

The major weakness of this version relates to the data analysis assessed sex-specific contributors to the results.

eLife Assessment

Aging reduces tissue regeneration capacity, posing challenges for an aging population. In this fundamental study, Reeves et al. show that by combining Wnt-mediated osteoprogenitor expansion (using a special bandage) with intermittent fasting, bone healing can be restored in aged animals. By employing rigorous histological, transcriptomic, and imaging analyses in a clinically relevant model, the authors provide compelling evidence supporting the conclusions. The therapeutic approach presented in this study shows promise for rejuvenating tissue repair, not only in bones but potentially across other tissues.

Reviewer #1 (Public review):

Summary:

Aging reduces tissue regeneration capacity, posing challenges for an aging population. In this study, the authors investigate impaired bone healing in aging, focusing on calvarial bones, and introduce a two-part rejuvenation strategy. Aging depletes osteoprogenitor cells and reduces their function, which hinders bone repair. Simply increasing the number of these cells does not restore their regenerative capacity in aged mice, highlighting intrinsic cellular deficits. The authors' strategy combines Wnt-mediated osteoprogenitor expansion with intermittent fasting, which remarkably restores bone healing. Intermittent fasting enhances osteoprogenitor function by targeting NAD+ pathways and gut microbiota, addressing mitochondrial dysfunction - an essential factor in aging. This approach shows promise for rejuvenating tissue repair, not only in bones but potentially across other tissues.

Strengths:

This study is exciting, impressive, and novel. The data presented is robust and supports the findings well.

Weaknesses:

As mentioned above the data is robust and supports the findings well. I have minor comments only.

Reviewer #2 (Public review):

Summary:

Reeves et al explore a model of bone healing in the context of aging. They show that intermittent fasting can improve bone healing, even in aged animals. Their study combines a 'bone bandage' which delivers a canonical Wnt signal with intermittent fasting and shows impacts on the CD90 progenitor cell population and the healing of a critical-sized defect in the calvarium. They also explore potential regulators of this process and identify mitochondrial dysfunction in the age-related decline of stem cells. In this context, by modulating NAD+ pathways or the gut microbiota, they can also enhance healing, hinting at an effect mediated by complex impacts on multiple pathways associated with cellular metabolism.

Strengths:

The study shows a remarkable finding: that age-related decreases in bone healing can be restored by intermittent fasting. There is ample evidence that intermittent fasting can delay aging, but here the authors provide evidence that in an already-aged animal, intermittent fasting can restore healing to levels seen in younger animals. This is an important finding as it may hint at the potential benefits of intermittent fasting in tissue repair.

Weaknesses:

The authors explore potential mechanisms by which the intermittent fasting protocol might impact bone healing. However, they do not identify a magic bullet here that controls this effect. Indeed, the fact that their results with intermittent fasting can be replicated by changing the gut microbiota or modulating fundamental pathways associated with NAD, suggests that there is no single mechanism that drives this effect, but rather an overall complex impact on metabolic processes, which may be very difficult to untangle.

Reviewer #3 (Public review):

Summary:

This study aims to address the significant challenge of age-related decline in bone healing by developing a dual therapeutic strategy that rejuvenates osteogenic function in aged calvarial bone tissue. Specifically, the authors investigate the efficacy of combining local Wnt3a-mediated osteoprogenitor stimulation with systemic intermittent fasting (IF) to restore bone repair capacity in aged mice. The highlights are:

(1) Novel Approach with Aged Models:<br /> This pioneering study is among the first to demonstrate the rejuvenation of osteoblasts in significantly aged animals through intermitted fasting, showcasing a new avenue for regenerative therapies.

(2) Rejuvenation Potential in Aged Tissues:<br /> The findings reveal that even aged tissues retain the capacity for rejuvenation, highlighting the potential for targeted interventions to restore youthful cellular function.

(3) Enhanced Vascular Health:<br /> The study also shows that vascular structure and function can be significantly improved in aged tissues, further supporting tissue regeneration and overall health.<br /> Through this innovative approach, the authors seek to overcome intrinsic cellular deficits and environmental changes within aged osteogenic compartments, ultimately achieving bone healing levels comparable to those seen in young mice.

Strengths:

The study is a strong example of translational research, employing robust methodologies across molecular, cellular, and tissue-level analyses. The authors leverage a clinically relevant, immunocompetent mouse model and apply advanced histological, transcriptomic, and functional assays to characterise age-related changes in bone structure and function. Major strengths include the use of single-cell RNA sequencing (scRNA-seq) to profile osteoprogenitor populations within the calvarial periosteum and suture mesenchyme, as well as quantitative assessments of mitochondrial health, vascular density, and osteogenic function. Another important point is the use of very old animals (up to 88 weeks, almost 2 years) modelling the human bone aging that usually starts >65 yo. This comprehensive approach enables the authors to identify critical age-related deficits in osteoprogenitor number, function, and microenvironment, thereby justifying the combined Wnt3a and IF intervention.

Weaknesses:

One limitation is the use of female subjects only and the limited exploration of immune cell involvement in bone healing. Given the known role of the immune system in tissue repair, future studies including a deeper examination of immune cell dynamics within aged osteogenic compartments could provide further insights into the mechanisms of action of IF.

eLife Assessment

The findings of this study are valuable, as they address a critical methodological gap in decision-making research by demonstrating how heuristic strategies can confound interpretations of uncertainty-driven behaviour and provide a clearer framework for distinguishing between uncertainty-seeking and heuristic-driven exploration. While the evidence is solid, with strong methodological rigour in task design and computational modelling, some claims, such as the stability of uncertainty parameters and correlations with psychopathology measures, require refinement. Overall, the data broadly support the study's claims, but interpretational ambiguities limit the impact of certain findings.

Reviewer #1 (Public review):

Summary:

The study investigates how uncertainty and heuristic strategies influence reward-based decision-making, using a novel two-armed bandit task combined with computational modeling. It aims to disentangle uncertainty-driven behavior from heuristic strategies such as repetition bias and win-stay-lose-shift tendencies, while also exploring individual differences in these processes.

Strengths:

The paper is methodologically sound, and the inclusion of subjective reports enhances the validity of the model testing. The findings on the use of heuristics under specific uncertainty conditions are particularly intriguing.

Weaknesses:

(1) Unclear how the findings significantly diverge from previous work:

At the start of the introduction, the authors propose a working hypothesis of "heterogeneity in the uncertainty effects." However, this concept is already well-established in the field. Foundational work by Yu and Dayan (2005) and more recent studies by Gershman and colleagues on total and relative uncertainty have provided substantial evidence supporting this idea. Additionally, the notion that such heterogeneity could explain mixed findings has been discussed in studies like Wilson (2014). What specific problem are the authors addressing here, and how does their work significantly differ from previous research?

Later on, however, it seems that the authors' hypothesis is to test the role of multiple factors in driving participants' decisions in the context considered by the authors. First, why is it important to solve such a puzzle? Second, this too has been investigated previously, see for example Dubois (2022), eLife. Therefore, what novel things is this paper bringing to the table? I do see that the task is novel - mostly combining different experimental strategies previously adopted - and that the model includes both heuristics and uncertainty-based strategies, which can account for their shared variance ... but are the authors really answering a novel question? Also, it is not very clear which question the authors are answering see point C below.

(2) The sample size appears to be quite small, and the results would be more convincing if supported by a replication study.

(3) The results section can be somewhat unclear at times, as it introduces novel aspects (e.g., the fMRI session) or questions that were not previously explained within the framework outlined in the introduction. While the findings related to psychopathology are interesting, their relevance to the research question posed in the introduction is not immediately clear. If these findings have significant added value, it would be helpful for the authors to highlight this earlier in the manuscript. Similarly, the results on individual differences in uncertainty (Section 3.6), though intriguing, appear tangential to the primary research question regarding the role of multiple factors in driving participants' decisions. Overall, it would strengthen the manuscript to clarify the main research question and ensure the results are more directly aligned with it.

Reviewer #2 (Public review):

Summary:

This paper addresses mixed findings regarding levels of uncertainty-seeking/avoidance in past reinforcement learning studies. Using computational modelling and a novel variant of a bandit task performed across two sessions, the authors investigate the extent to which uncertainty-driven behaviour can be distinguished from heuristic-like behaviours (e.g., repetition, win-stay/lose-switch). They demonstrate that heuristics account for a significant and stable portion of the variance in choice behaviour, which might otherwise be misattributed to uncertainty-driven parameters. Additionally, they find that relative uncertainty explains additional variance and provides some evidence of stability across sessions.

Strengths:

The task is well-designed to tease apart multiple different factors contributing to choice during a bandit task, including separating those tied to uncertainty per se versus other policies. They validate a Bayesian model to account for learning and choice behaviour, as well as subjective estimates of learned value and confidence in these values. The work employs comprehensive model comparison to characterise behaviour in this task, and points to important risks within research on uncertainty preferences using bandit-like tasks when failing to fully account for heuristic-like drivers of such behaviour.

Weaknesses:

Part of this work seeks to relate individual differences in various choice parameters across sessions and to relate those to self-report scales. The estimates of cross-session reliability are valuable, particularly when comparing across the different parameters (e.g., heuristic ones being most robust), but the uncertainty-related parameters are interpreted too liberally (i.e., as being stable across sessions when both were weak and one was not significant). Moreover, the correlations with external scales are very hard to interpret given the number of comparisons that were run without correction. The findings overall will have value to people interested in modelling uncertainty preferences in learning tasks -- some of whom have considered heuristic factors less than others -- but perhaps be of more moderate impact beyond this group.

Reviewer #3 (Public review):

Summary:

This work investigated how uncertainty, repetition bias, and win-stay-lose-shift processes influence reward-based decision-making. Using a modified two-armed bandit task and computational models, the authors provide evidence for individual variation in the integration of uncertainty on choice behaviour that remains somewhat stable across two experiment sessions. The authors also find a number of interesting results due to their ability to disentangle components of this decision-making process using their novel task and models. Specifically, they find that higher total uncertainty leads people to use more heuristic-based strategies like making repetitive choices or engaging in win-stay-lose-shift behaviour. However, they also find that there are individual differences in how people use uncertainty to guide their choices, and that these differences are consistent within individuals across multiple experiment sessions. This finding can help explain prior inconsistencies in the literature, where researchers have found evidence for both uncertainty-seeking and uncertainty-avoidance tendencies. Overall, this research adds to our understanding of the mechanisms of uncertainty-modulated learning and decision-making.

Strengths:

One of the primary strengths of this research is that it helps provide support for the idea that mixed and null results in the prior literature could be due to individual differences in uncertainty preferences and that this individual variation is somewhat stable within subjects across multiple experiment sessions. The authors cleverly disentangle expected reward and uncertainty by interleaving free and forced choice trials in their behavioural task, illuminating the novel impact of reward and uncertainty on this particular decision process. However, it should be noted that this behavioural decorrelation does not persist beyond the first few trials after a forced choice period, so whether or not the decorrelation is truly robust remains unclear.

The authors also use computational modelling to further probe the influence of uncertainty on reward-based choices. Specifically, they compare a Bayesian ideal observer learning model and a variation on a standard Rescorla-Wagner model, finding that a version of the Bayesian model fits the participants' behaviour best. The model descriptions and analyses are clearly explained and methodologically rigorous.

Interestingly, the authors find that both repetition bias and model parameters that capture a win-stay-lose-shift strategy (signed and unsigned previous prediction error) significantly improve their model fits. They also make an important point that if win-stay-lose-shift behaviour is not controlled for, then switch behaviour (for example, switching to a lower expected reward option after receiving a large loss) may appear to be uncertainty-seeking when it is not. This idea speaks to a larger point that future research should be careful to not conflate "exploration" with "uncertainty-seeking."

Weaknesses:

This research has some weaknesses regarding the correlations between the psychopathology measures and the computational model parameters. First, the choice of self-report measures is not well supported by any specific hypotheses. Relatedly, the authors do not include sufficient rationale for their choice to include only results from the anxiety and impulsivity measures in the main text while leaving out significant findings for a number of correlations between other measures and parameter coefficients. It is also not clear how the model parameters are being derived for use in each of these correlational analyses. In sum, the manuscript as-is contains inconsistent and/or confusing reporting of correlation results that require further clarification.

eLife Assessment

This valuable study investigates the mechanisms that contribute to nerve-injury-induced allodynia by studying the role of the estrogen receptor GPR30 in a population of CCK+ neurons in the dorsal horn of the spinal cord that receive direct inputs from primary somatosensory cortex and modulate nociceptive sensitivity. The authors provide convincing evidence, using a variety of complementary approaches, ranging from the cellular to physiology level; however, conclusions that descending corticospinal projections modulate nociceptive behaviors through GPR30 are incompletely supported. With some additional analyses, the findings will be better positioned within the context of spinal circuitry literature.

Reviewer #1 (Public review):

In this manuscript, Chen et al. investigate the role of the membrane estrogen receptor GPR30 in spinal mechanisms of neuropathic pain. Using a wide variety of techniques, they first provide convincing evidence that GPR30 expression is restricted to neurons within the spinal cord, and that GPR30 neurons are well-positioned to receive descending input from the primary sensory cortex (S1). In addition, the authors put their findings in the context of the previous knowledge in the field, presenting evidence demonstrating that GRP30 is expressed in the majority of CCK-expressing spinal neurons. Overall, this manuscript furthers our understanding of neural circuity that underlies neuropathic pain and will be of broad interest to neuroscientists, especially those interested in somatosensation. Nevertheless, the manuscript would be strengthened by additional analyses and clarification of data that is currently presented.

Strengths:

The authors present convincing evidence for the expression of GPR30 in the spinal cord that is specific to spinal neurons. Similarly, complementary approaches including pharmacological inhibition and knockdown of GPR30 are used to demonstrate the role of the receptor in driving nerve injury-induced pain in rodent models.

Weaknesses:

Although steps were taken to put their data into the broader context of what is already known about the spinal circuitry of pain, more considerations and analyses would help the authors better achieve their goal. For instance, to determine whether GPR30 is expressed in excitatory or inhibitory neurons, more selective markers for these subtypes should be used over CamK2. Moreover, quantitative analysis of the extent of overlap between GRP30+ and CCK+ spinal neurons is needed to understand the potential heterogeneity of the GRP30 spinal neuron population, and to interpret experiments characterizing descending SI inputs onto GRP30 and CCK spinal neurons. Filling these gaps in knowledge would make their findings more solid.

Reviewer #2 (Public review):

Using a variety of experimental manipulations, the authors show that the membrane estrogen receptor G protein-coupled estrogen receptor (GPER/GPR30) expressed in CCK+ excitatory spinal interneurons plays a major role in the pain symptoms observed in the chronic constriction injury (CCI) model of neuropathic pain. Intrathecal application of selective GPR30 agonist G 1induced mechanical allodynia and thermal hyperalgesia in male and female mice. Downregulation of GPR30 in CCK+ interneurons prevented the development of mechanical and thermal hypersensitivity during CCI. They also show the up modulation of AMPA receptor expression by GPR30.

Generally, the conclusions are supported by the experimental results. I also would like to see significant improvements in the writing and the description of results.

Methodological details for some of the techniques are rather sparse. For example, when examining the co-localization of various markers, the authors do not indicate the number of animals/sections examined. Similarly, when examining the effect of shGper1, it is unclear how many cells/sections/animals were counted and analyzed.

In other sections, there is no description of the concentration of drugs used (for example, Figure 4H). In Figures 4C-E, there is no indication of the duration of the recordings, the ionic conditions, the effect of glutamate receptor blockers, etc

Some results appear anecdotal in the way they are described. For example, in Figure 5, it is unclear how many times this experiment was repeated.

Reviewer #3 (Public review):

Summary:

The authors convincingly demonstrate that a population of CCK+ spinal neurons in the deep dorsal horn express the G protein-coupled estrogen receptor GPR30 to modulate pain sensitivity in the chronic constriction injury (CCI) model of neuropathic pain in mice. Using complementary pharmacological and genetic knockdown experiments they convincingly show that GPR30 inhibition or knockdown reverses mechanical, tactile, and thermal hypersensitivity, conditioned place aversion, and c-fos staining in the spinal dorsal horn after CCI. They propose that GPR30 mediates an increase in postsynaptic AMPA receptors after CCI using slice electrophysiology which may underlie the increased behavioral sensitivity. They then use anterograde tracing approaches to show that CCK and GPR30 positive neurons in the deep dorsal horn may receive direct connections from the primary somatosensory cortex. Chemogenetic activation of these dorsal horn neurons proposed to be connected to S1 increased nociceptive sensitivity in a GPR30-dependent manner. Overall, the data are very convincing and the experiments are well conducted and adequately controlled. However, the proposed model of descending corticospinal facilitation of nociceptive sensitivity through GPR30 in a population of CCK+ neurons in the dorsal horn is not fully supported.

Strengths:

The experiments are very well executed and adequately controlled throughout the manuscript. The data are nicely presented and supportive of a role for GPR30 signaling in the spinal dorsal horn influencing nociceptive sensitivity following CCI. The authors also did an excellent job of using complementary approaches to rigorously test their hypothesis.

Weaknesses:

The primary weakness in this manuscript involves overextending the interpretations of the data to propose a direct link between corticospinal projections signaling through GPR30 on this CCK+ population of spinal dorsal horn neurons. For example, even in the cropped images presented, GPR30 is present in many other CCK-negative neurons. Only about a quarter of the cells labeled by the anterograde viral tracing experiment from S1 are CCK+. Since no direct evidence is provided for S1 signaling through GPR30, this conclusion should be revised.

eLife Assessment

This valuable study by Xu and colleagues investigates brainstem circuits mediating evoked respiratory reflexes that they define as cough-like in a freely behaving mouse model. They have applied multiple circuit mapping and manipulation approaches to suggest that the caudal spinal trigeminal nucleus (SP5C) nucleus can play a novel role in generating a reflex cough-like behavior in mice. The authors give incomplete evidence that the reflex behavior produced in their mouse model is definitively cough, limiting functional interpretation of the putative circuit identified and requiring more thorough experimental interrogation of the behavior studied.

Reviewer #1 (Public review):

Summary:

The study by Xu and colleagues provides a useful study of brainstem circuits involved in evoked respiratory reflexes that they define to be cough or cough-like in nature. The study is conducted in mice which has the benefit of allowing for the use of modern transgenic tools, although many of the experiments end up using viral vector-based approaches that could be deployed in any species. The disadvantage of the mouse model is understanding the true identity of the respiratory event that is defined as cough. This limitation requires careful interrogation in order to understand the biology of the circuit under investigation. In this respect, the authors provide an incomplete description of a putative cough pathway linking the caudal spinal trigeminal nucleus with the ventral respiratory group. Neurons assigned as CaMKII+ with putative inputs from the paratrigeminal nucleus are central to this circuit, although the evidence for each of these claims is relatively weak or non-existent. Overall, the study employs interesting methods but limitations in methods and details of methods reduce interpretation of the study outcomes.

Strengths:

The use of modern methods to investigate brainstem circuits involved in an essential respiratory reflex.

Weaknesses:

(1) The most significant issue that needs careful consideration is the exact respiratory response, which is called a cough. The authors show a trace from their plethysmography recordings and superimpose the 3 phases of cough (inspiration, compression, expiration) with confidence, yet the parameters used to delineate these phases are unclear. Of more concern, an identical respiratory trace was reported recently as a sneeze in Jiang et al Cell 2024 (PMID 39243765). Comparing Figure 1 in the Xu study with Figure 5 in the Jiang study, it is impossible to see any difference in the respiratory trace that would allow the assignment of one as cough and the other as sneeze. The audio signals also look remarkably similar and the purported cough signal in the Jiang study is quite different. Gannot et al Nat Neurosci 2024 (PMID 38977887) seems to agree with Xu in the identity of a cough signal, but Li et al Cell 2021 (PMID 34133943) again labels these as sneezes. One of the older studies that tried to classify respiratory signals in mice (Chen et al PlosONE 2013) labeled the Jiang cough trace as a deep inspiration, while sneeze looks different again. To add further confusion, Zhang et al AJP 2017 (PMID 28228416 ) provide yet another respiratory plethysmography trace that they define as a cough, and label responses discussed above as expiration reflexes. This begs the question - who, if anyone, is correct? Interpreting the circuits underlying these peculiar mouse responses depends on accuracy in defining the response in the first instance.

(2) The involvement of the causal nSp5 in cough is an unexpected finding. Some understanding of if and how vagal afferent inputs reach this location would help strengthen the manuscript. The authors claim in the discussion that the nucleus of the solitary tract is not the source of inputs, but rather they may arise from the paratrigeminal nucleus (although no data is presented to support this claim). This could fit with the known jugular vagal afferent pathway, which is embryologically distinct and terminates in trigeminal regions, rather than the NTS. But if this is correct, what does this finding then say about the purported involvement of NTS neurons in cough in mice, for example, the recent study by Gannot et al Nat Neurosci where Tac1-expressing NTS neurons were integral for what they call cough in mice? Xu and colleagues are encouraged to resolve their input circuitry so that we can better understand the pathway under investigation and how it relates to the NTS pathway. Related to this, and the issues differentiating cough-like responses from sneeze, the authors will need to consider how to differentiate their cough-like circuitry from the sneeze pathway from the caudal nSp5 to the cVRG as reported by Li et al Cell 2021. It seems highly possible that the two groups are studying the same circuitry, yet the interpretation is confounded by an inability to agree on the identity of the evoked response.

(3) Injection volumes and titres for AAV transductions are not stated anywhere. The methods (line 484) indicate that different volumes were used for different purposes, but nowhere is this information stated properly. Looking at representative images suggests that volumes were very large, with most of the brainstem often transduced. As single slices are only ever shown it becomes a concern as to how extensive transductions truly are. The authors need to provide complete maps of viral transduction so that readers can understand exactly what regions could contribute to responses, thereby confounding interpretation.

(4) The authors do not provide any data to explore the impacts of manipulations on basal breathing. This is important as impacts on the respiratory patterning will likely have profound effects on evoked responses that are not related to the specific pathway under investigation. For example, in Figure 2b. breathing looks to be severely compromised in the TKO animals and disrupted in the M4 DREADD animals. Figure 3 also shows the effects of optical stimulation on breathing patterns, which appear like apnea with several breakthrough augmented breaths (some labeled as cough?), although hard to see properly in the traces provided. Figure 5, one would expect VRG inhibition to have impacts on breathing, and the traces supplied appear to suggest this is the case. Please include data showing breathing effects and consider how these may confound your study interpretation.

Reviewer #2 (Public review):

Summary:

This study employs a combination of state-of-the-art experimental approaches in mice to identify components of the brainstem circuits involved in the cough reflex in a freely behaving mouse model. The cough reflex is an important respiratory airway defense mechanism, and there has been longstanding interest in defining the neural circuits involved in the mammalian brainstem. Consistent with other recent studies, the present results provide multiple lines of evidence indicating that mice are a suitable model for studying neural mechanisms generating cough behavior. The main novel finding of this study is the authors' results indicating that the caudal spinal trigeminal nucleus (SP5C) nucleus plays a role in generating cough-like behaviors in response to inhaled tussigen. The supporting data presented for this role includes the authors' findings that: (1) neural activity in the SP5C is strongly correlated with tussigen-evoked cough-like behaviors, (2) impairing synaptic outputs or chemogenetic inhibition of SP5C neurons effectively abolished these cough-like reflexes, (3) optogenetically activating a specific subpopulation of excitatory neurons in the SP5C triggers cough-like behaviors, (4) SP5C neurons project monosynaptically to ventral medullary regions containing respiratory circuits that exhibit cough-related neural activity, and (5) specific activation of the SP5C-ventral respiratory circuitry induces robust cough-like behavior without tussive stimuli. This study will be valuable to respiratory neurobiologists studying mechanosensory control of breathing in mammals.

Strengths:

(1) The authors developed an experimental paradigm in mice that combines whole-body plethysmography (WBP), audio, and video tracking to assess breathing and putative cough-like behaviors in conscious animals.

(2) The mouse model enables optogenetic, chemogenetic, virus-based circuit tracing and manipulation, and in vivo fiber photometry to analyze neural activity and define circuity in the medulla-producing cough-like behavior.

(3) Multiple lines of evidence from these experimental approaches support the conclusion that the SP5C nucleus plays a role in the respiratory reflex behaviors studied in mice, but there is uncertainty that these behaviors are definitively cough.

Weaknesses:

(1) This paper lacks essential quantitative details about the number of animals studied explicitly for many of the experimental paradigms presented and for statistical analyses as well as to verify replication of the neuroanatomical data presented.

(2) The authors' evidence is incomplete that the reflex behavior produced in their mouse model is definitively cough, limiting functional interpretation of the putative circuit identified and requiring more thorough experimental interrogation of the behavior studied.

(3) The medullary circuit described conveys afferent sensorimotor signals to downstream respiratory circuits to coordinate cough-like motor behavior, but how the circuits that typically mediate the cough reflex, which involve airway-related vagal sensory neurons, operate in conjunction or parallel with the SP5C circuit described has not been determined, which is a significant gap in understanding how the present results fit into the neural control of the cough reflex.

Reviewer #3 (Public review):

Summary:

The authors have submitted a comprehensive manuscript on the production and central pathways that they propose mediate cough-like behaviors in a TRAP2 transgenic mouse model. While the central pathway data are good, there is significant uncertainty regarding the identity of the presumptive cough-like behavior that has been produced in their model which reduces enthusiasm for the manuscript.

Strengths:

(1) The use of the TRAP2 model in the investigation of coughing is strong.

(2) The implication of SP5 in the production of coughing in response to ammonia inhalation is a novel finding. Further, this area can be activated by AAV-CaMKII to induce coughing in the absence of coincident afferent activation is an important observation.

Weaknesses:

(1) A fundamental aspect of this investigation is the unequivocal identification of the behavior that has been evoked. In this case, the authors have not established that they are actually studying cough. The evidence that they present (especially Figure 1 - Supplement 1) clearly shows that the citric acid (2nd example), capsaicin (2nd example), and ammonia (2nd example) box flows lack a large inspiratory component which is a requirement of cough. The referenced behaviors appear to be expulsion/inspiration which is not cough. The only way these behaviors could be cough is if the conventional polarity of presentation of the flow signals are reversed. However, inspection of the flows during breathing strongly indicates that inspiration is down in your records. Again, this makes these behaviors expulsion/inspiration.

An additional issue is that there are compression phases marked when the flow is occurring. The compression phase is a period of no flow so this is not accurate. There also is no evidence that the mouse has a compression phase at all. In cough flow records in humans, the compression phase can clearly be seen when it happens but not all coughs have one. You must show that a compression phase happens according to the actual description of what this segment of cough actually is.

It may be that you are evoking behaviors that primarily occur in the mouse. As such, they would be novel airway protective behaviors that are worthy of description and study. Ironically, another manuscript in the journal Cell (Jiang et al, 2024, Cell 187:5981-5997) shows similar box flow polarities as your own and clear cough airflows (Fig. 5B). However, they also show other airflow patterns that resemble what you call cough (Figure 5A) but they call them sneeze. Those airflows are expulsion/inspiration and are clearly not sneezing as the expulsion in this behavior also is preceded not followed by inspiration.

The definitive manuscript on cough in the mouse is Zhang et al Am J Physiol Reg Integr Comp 312:R718-R726, 2017. In this manuscript, Figure 2 clearly shows both box pressures and intrapleural pressures during airway protective behaviors in the awake mouse. Note that both cough and a behavior known as expiration reflex were recorded. The key element here is that the cough elicited a tri-phasic box flow. The last excursion was associated with a sound. When compared to the pressure it is clear that this last flow excursion is mechanical chest wall recoil from residual volume. The fact that this segment of the flow record was associated with sound strongly suggests that the vocal folds were adducting at the time to "brake" the chest wall recoil. In other words, the airway resistance went up to slow inspiratory airflow as the chest returned to its resting position. As such, this observation suggests that the chest wall mechanics of cough in the mouse are different than that of larger animals.

(2) Roger Shannon and coworkers have published a number of papers on the detailed brainstem circuits that are responsible for coughing. I recommend that the authors assimilate this knowledge in the context of their results.

eLife Assessment

The authors present a biologically plausible framework for action selection and learning in the striatum that is a fundamental advance in our understanding of possible neural implementations of reinforcement learning in the basal ganglia. They provide compelling evidence that their model can reconcile realistic neural plasticity rules with the distinct functional roles of the direct and indirect spiny projection neurons of the striatum, recapitulating experimental findings regarding the activity profiles of these distinct neural populations and explaining a key aspect of striatal function.

Reviewer #1 (Public review):

Summary:

The authors propose a new model of biologically realistic reinforcement learning in the direct and indirect pathway spiny projection neurons in the striatum. These pathways are widely considered to provide a neural substrate for reinforcement learning in the brain. However, we do not yet have a full understanding of mechanistic learning rules that would allow successful reinforcement learning like computations in these circuits. The authors outline some key limitations of current models and propose an interesting solution by leveraging learning with efferent inputs of selected actions. They show that the model simulations are able to recapitulate experimental findings about the activity profile in these populations of mice during spontaneous behavior. They also show how their model is able to implement off-policy reinforcement learning.

Strengths:

The manuscript has been very clearly written and the results have been presented in a readily digestible manner. The limitations of existing models, that motivate the presented work, have been clearly presented and the proposed solution seems very interesting. The novel contribution of the proposed model is the idea that different patterns of activity drive current action selection and learning. Not only does this allow the model is able to implement reinforcement learning computations well, but this suggestion may have interesting implications regarding why some processes selectively affect ongoing behavior and others affect learning. The model is able to recapitulate some interesting experimental findings about various activity characteristics of dSPN and iSPN pathway neuronal populations in spontaneously behaving mice. The authors also show that their proposed model can implement off-policy reinforcement learning algorithms with biologically realistic learning rules. This is interesting since off-policy learning provides some unique computational benefits and it is very likely that learning in neural circuits may, at least to some extent, implement such computations.

Weaknesses:

A weakness in this work is that it isn't clear how a key component in the model - an efferent copy of selected actions - would be accessible to these striatal populations. The authors propose several plausible candidates, but future work may clarify the feasibility of this proposal.

Reviewer #2 (Public review):

Summary:

The basal ganglia is often understood within a reinforcement learning (RL) framework, where dopamine neurons convey a reward prediction error that modulates cortico-striatal connections onto spiny projection neurons (SPNS) in the striatum. However, current models of plasticity rules are inconsistent with learning in a reinforcement learning framework.

This paper proposes a new model that describes how distinct learning rules in direct and indirect pathway striatal neurons allow them to implement reinforcement learning models. It proposes that two distinct components of striatal activity affect action selection and learning. They show that the proposed implementation allows learning in simple tasks and is consistent with experimental data from calcium imaging data in direct and indirect SPNs in freely moving mice.

Strengths:

Despite the success of reward prediction errors at characterizing the responses of dopamine neurons as the temporal difference error within an RL framework, the implementation of RL algorithms in the rest of the basal ganglia has been unclear. A key missing aspect has been the lack of a RL implementation that is consistent with the distinction of direct- and indirect SPNs. This paper proposes a new model that is able to learn successfully in simple RL tasks and explains recent experimental results.

The author shows that their proposed model, unlike previous implementations, this model can perform well in RL tasks. The new model allows them to make experimental predictions. They test some of these predictions and show that the dynamics of dSPNs and iSPNs correspond to model predictions.

More generally, this new model can be used to understand striatal dynamics across direct and indirect SPNs in future experiments.

Weaknesses:

The authors could characterize better the reliability of their experimental predictions and the description of the parameters of some of the simulations

The authors propose some ideas about how the specificity of the striatal efferent inputs but should highlight better that this is a key feature of the model whose anatomical implementation has yet to be resolved.

Reviewer #3 (Public review):

Summary:

This paper points out an inconsistency of the roles of the striatal spiny neurons projecting to the indirect pathway (iSPN) and the synaptic plasticity rule of those neurons expressing dopamine D2 receptors and proposes a novel, intriguing mechanisms that iSPNs are activated by the efference copy of the chosen action that they are supposed to inhibit.

The proposed model was supported by simulations and analysis of the neural recording data during spontaneous behaviors.

Strengths:

Previous models suggested that the striatal neurons learn action-value functions, but how the information about the chosen action is fed back to the striatum for learning was not clear. The author pointed out that this is a fundamental problem for iSPNs that are supposed to inhibit specific actions and its synaptic inputs are potentiated with dopamine dips.

The authors propose a novel hypothesis that iSPNs are activated by efference copy of the selected action which they are supposed to inhibit during action selection. Even though intriguing and seemingly unnatural, the authors demonstrated that the model based on the hypothesis can circumvent the problem of iSPNs learning to disinhibit the actions associated with negative reward errors. They further showed by analyzing the cell-type specific neural recording data by Markowitz et al. (2018) that iSPN activities tend to be anti-correlated before and after action selection.

Weaknesses:

(1) It is not correct to call the action value learning using the externally-selected action as "off-policy." Both off-policy algorithm Q-learning and on-policy algorithm SARSA update the action value of the chosen action, which can be different from the greedy action implicated by the present action values. In standard reinforcement learning terminology, on-policy or off-policy is regarding the actions in the subsequent state, whether to use the next action value of (to be) chosen action or that of greedy choice as in equation (7).

It is worth noting that this paper suggested that dopamine neurons encode on-policy TD errors:<br /> Morris G, Nevet A, Arkadir D, Vaadia E, Bergman H (2006). Midbrain dopamine neurons encode decisions for future action. Nat Neurosci, 9, 1057-63. https://doi.org/10.1038/nn1743

(2) It is also confusing to contract TD learning and Q-learning, as the latter is considered as one type of TD learning. In the TD error signal by state value function (6) is dependent on the chosen action a_{t-1} implicitly in r_t and s_t based on the reward and state transition function.

(3) It is not clear why interferences of the activities for action selection and learning can be avoided, especially when actions are taken with short intervals or even temporal overlaps. How can the efference copy activation for the previous action be dissociated with the sensory cued activation for the next action selection?

(4) Although it may be difficult to single out the neural pathway that carries the efference copy signal to the striatum, it is desired to consider their requirements and difference possibilities. A major issue is that the time delay from actions to reward feedback can be highly variable.

An interesting candidate is the long-latency neurons in the CM thalamus projecting to striatal cholinergic interneurons, which are activated following low-reward actions:<br /> Minamimoto T, Hori Y, Kimura M (2005). Complementary process to response bias in the centromedian nucleus of the thalamus. Science, 308, 1798-801. https://doi.org/10.1126/science.1109154

(5) In the paragraph before Eq. (3), Eq. (1) should be Eq. (2) for the iSPN.

eLife Assessment

This study presents a valuable study of early brain development using advanced MRI methods. In particular, the study investigates the relationship between the maturation of diffusion MRI tissue properties and suggests that they may precede and guide the emergence of brain folding patterns. The data is solid, however, the evidence supporting the precedence of tissue changes over brain folding appears incomplete.

Reviewer #1 (Public review):

Summary:

This manuscript describes the analysis of fetal MRI and diffusion-weighted images of the fetal brain in utero, which reveals correlations between spatial and temporal patterns in diffusion behavior (associated with tissue microstructure) with local geometry of the brain surface (describing cortical folding). The authors use advanced imaging and image analysis pipelines, notably high angular resolution multi-shell diffusion imaging (HARDI) and multi-shell, multi-tissue constrained spherical deconvolution (MSMT-CSD) analysis of the resulting data to analyze. The key metric of tissue microstructure is "tissue fraction" which describes the relative contribution of organized anisotropic diffusion to overall diffusion, and the key geometry parameter is sulcal depth.

The major observation is that tissue fraction, which generally increases with gestational age, is lower in sulcal fundi, and importantly that the relative difference in tissue fraction emerges *before* folding occurs. The relatively low values of tissue fraction in regions of incipient sulci may be important to the physical mechanism of cortical folding.

Strengths:

Strengths of the manuscript include the application of advanced, highly technical imaging and image analysis methods to extract high-resolution data on both surface geometry and diffusion from a unique fetal cohort. The comparison of local features of surface and microstructure in both age-matched and age-mismatched analyses reveals a clear negative correlation between tissue fraction and sulcal depth.

Weaknesses:

The authors could improve the manuscript by (i) expanding their effort to place their current findings in the context of mechanistic models of folding and (ii) explaining more clearly how the diffusion measurements reflect tissue fraction. The relationship between the tissue fraction metric, the diffusion measurements, and the tissue microstructure is quite opaque.

Reviewer #2 (Public review):

Summary:

The authors analyze parameters related to anisotropy and gyrification in the developing human brain and describe an increase in tissue fraction (TF) across development. They correlate TF and sulcal depth in the CP and SP across local neighborhoods, describing a negative correlation. Also, they perform age-mismatched correlation of tissue fraction at early stages with sulcal depth at later ones and show correlation inside sulci, which they interpret as indicating the presence of minor structural changes in the brain that precede the development of sulci.

Strengths:

The study compiles a large cohort of cases through different developmental ages and performs sophisticated data analysis. Overall, the work is interesting.

Weaknesses:

I have some questions. What is the potential meaning of TF? It seems to be an estimator of anisotropy highly related to fractional anisotropy (FA), but it behaves in a complementary manner, increasing along gestation, in sharp contrast with the decrease observed in FA in this study (suppl. fig 3) and by others. Please clarify how it is calculated, what is the potential biological meaning of TF and how it differs from FA.

The correlations between TF and sulcal depth do not seem to provide much novelty, since as mentioned by the authors, previous evidence has pointed in that direction. The other concept in the paper relates to detecting structural changes in prospective sulcal areas in the cortex, which the authors analyze through the age-mismatched correlation of TF and subsequent sulcation. However, the results do not show a robust correlation as detailed below and do not seem particularly useful, as they require the inclusion of post-hoc information in the model, limiting the strength of the relationship and the predictive value. My main point of criticism is that if TF is a good marker of the structural modifications that will favor the development of sulci later in development, TF should show a map predictive of those sulci (e.g. at GW 25), that is however not the case. It is not necessary to correlate with future sulcal depth, as we know exactly where the primary sulci will develop. Conversely, it seems that TF decreases along the gyrification process, and it might just be a measure of the structural changes accompanying it.

In Figure 2 it illustrates the increase in TF across GA, but no R values or significance values are provided. Please add them to evaluate the robustness of the correlation.

In previous work of the authors, the subplate is not clearly distinguished from the subcortical white matter after 31 GW, as it starts to disintegrate (Kostovic et al., 2002; Calixto et al., 2024). However, in this manuscript, the SP is differentiated at those later ages. The methods section describes a 2 mm thick compartment below the cortical plate. However, if that is the case, it seems quite arbitrary (to coincide with the resolution of the diffusion imaging) and risks analyzing a compartment that is no longer present. Please explain the criteria followed for such distinction and more importantly, how such distinction is reliable considering the low detectability described in previous studies. In this regard, the discussion described that a rapid increase in TF was only seen in the SP after 30 GW, but maybe this increase would reflect the dissipation of the SP and the transformation of that space in subcortical white matter, with a much more expected anisotropy. The authors should review this.

The analysis describes a negative correlation between tissue fraction and sulcal depth when gyrification proceeds and the authors find that an age-mismatched correlation between tissue fraction in young embryos and sulcal depth in older embryos also shows a negative correlation in future sites of sulcation. However, for the correlation to exist, the tissue fraction in young individuals should already show low values in the prospective sulci, but no clear changes can be seen at GW 25 or 27 in lissencephalic areas that will bear sulci later on, as is the case of the central sulcus at GW 25 or the STS at GW 27, the latter showing very high tissue fraction (instead of the expected low).

Another question refers to Figures 3b and c. The graphs represent specific neighborhoods in the central sulcus at 27 and 35 GW. It can be argued that those neighborhoods might not be representative of the brain or of the whole sulcus. Please show the graph with all neighborhoods, which will provide more definitive evidence of the existence of the correlation. In this regard, the average graphs represented in Figure 3F seem to show a clear correlation at 27 GW in the subplate, but the correlation seems to fade at later stages (in both SP and CP), with both sulci and gyri exhibiting a negative correlation while other sulcal areas do not exhibit correlation. I think all points should be included in the correlation to better support the hypothesis.

Figure 4 shows the age-mismatched correlations, but they do not seem convincing particularly when they should be more useful, at 25 GW. Indeed, as seen in both Figures A and C, the central sulcus shows a negative correlation only in a few spots on one hemisphere, while (in C) most of the prospective sulcus shows a positive correlation, contrary to the hypothesis.

Lastly, the authors performed an age-mismatched correlation between TF at different ages and the sulcal depth at 35W, when it is maximal. This maximal depth might be "pushing" the correlation to significant territory. The authors should provide correlation also with the sulcal depth at other GAs, such as P29, P31, or P33, and analyze how the correlations hold.

eLife Assessment

This study presents valuable quantitative insights into the prevalence of functionally clustered synaptic inputs on neuronal dendrites. The simple analytical calculations and computer simulations provide solid support for the main arguments. The findings can lead to a more detailed understanding of how dendrites contribute to the computation of neuronal networks.

Joint Public Review:

Summary:

If synaptic input is functionally clustered on dendrites, nonlinear integration could increase the computational power of neural networks. But this requires the right synapses to be located in the right places. This paper aims to address the question of whether such synaptic arrangements could arise by chance (i.e. without special rules for axon guidance or structural plasticity), and could therefore be exploited even in randomly connected networks. This is important, particularly for the dendrites and biological computation communities, where there is a pressing need to integrate decades of work at the single-neuron level with contemporary ideas about network function.

Using an abstract model where ensembles of neurons project randomly to a postsynaptic population, back-of-envelope calculations are presented that predict the probability of finding clustered synapses and spatiotemporal sequences. Using data-constrained parameters, the authors conclude that clustering and sequences are indeed likely to occur by chance (for large enough ensembles), but require strong dendritic nonlinearities and low background noise to be useful.

Strengths:

- The back-of-envelope reasoning presented can provide fast and valuable intuition. The authors have also made the effort to connect the model parameters with measured values. Even an approximate understanding of cluster probability can direct theory and experiments towards promising directions, or away from lost causes.

- I found the general approach to be refreshingly transparent and objective. Assumptions are stated clearly about the model and statistics of different circuits. Along with some positive results, many of the computed cluster probabilities are vanishingly small, and noise is found to be quite detrimental in several cases. This is important to know, and I was happy to see the authors take a balanced look at conditions that help/hinder clustering, rather than just focus on a particular regime that works.

- This paper is also a timely reminder that synaptic clusters and sequences can exist on multiple spatial and temporal scales. The authors present results pertaining to the standard `electrical' regime (~50-100 µm, <50 ms), as well as two modes of chemical signaling (~10 µm, 100-1000 ms). The senior author is indeed an authority on the latter, and the simulations in Figure 5, extending those from Bhalla (2017), are unique in this area. In my view, the role of chemical signaling in neural computation is understudied theoretically, but research will be increasingly important as experimental technologies continue to develop.

(Editors' note: the paper has been through two rounds of revisions and the authors are encouraged to finalise this as the Version of Record. The earlier reviews are here: https://elifesciences.org/reviewed-preprints/100664v2/reviews#tab-content)

Author response:

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

Reviewer #1 (Public Review):

In this revision, the authors significantly improved the manuscript. They now address some of my concerns. Specifically, they show the contribution of end-effects on spreading the inputs between dendrites. This analysis reveals greater applicability of their findings to cortical cells, with long, unbranching dendrites than other neuronal types, such as Purkinje cells in the cerebellum.

They now explain better the interactions between calcium and voltage signals, which I believe improve the take-away message of their manuscript. They modified and added new figures that helped to provide more information about their simulations.

However, some of my points remain valid. Figure 6 shows depolarization of ~5mV from -75. This weak depolarization would not effectively recruit nonlinear activation of NMDARs. In their paper, Branco and Hausser (2010) showed depolarizations of ~10-15mV.

More importantly, the signature of NMDAR activation is the prolonged plateau potential and activation at more depolarized resting membrane potentials (their Figure 4). Thus, despite including NMDARs in the simulation, the authors do not model functional recruitment of these channels. Their simulation is thus equivalent to AMPA only drive, which can indeed summate somewhat nonlinearly.

In the current study, we used short sequences of 5 inputs, since the convergence of longer sequences is extremely unlikely in the network configurations we have examined. This resulted in smaller EPSP amplitudes of ~5mV (Figure 6 - Supplement 2A, B). Longer sequences containing 9 inputs resulted in larger somatic depolarizations of ~10mV (Figure 6 - Supplement 2E, F). Although we had modified the (Branco, Clark, and Häusser 2010) model to remove the jitter in the timing of arrival of inputs and made slight modifications to the location of stimulus delivery on the dendrite, we saw similar amplitudes when we tested a 9-length sequence using (Branco, Clark, and Häusser 2010)’s published code (Figure 6 - Supplement 2I, J). In all the cases we tested (5 input sequence, 9 input sequence, 9 input sequence with (Branco, Clark, and Häusser 2010) code repository), removal of NMDA synapses lowered both the somatic EPSPs (Figure 6 - Supplement 2C,D,G,H,K,L) as well as the selectivity (measured as the difference between the EPSPs generated for inward and outward stimulus delivery) (Figure 6 Supplement 2M,N,O). Further, monitoring the voltage along the dendrite for a sequence of 5 inputs showed dendritic EPSPs in the range of 20-45 mV (Figure 6 - Supplement 2P, Q), which came down notably (10-25mV) when NMDA synapses were abolished (Figure 6 - Supplement 2R, S). Thus, even sequences containing as few as 5 inputs were capable of engaging the NMDA-mediated nonlinearity to show sequence selectivity, although the selectivity was not as strong as in the case of 9 inputs.

Reviewer #1 (Recommendations for the authors):

Minor points:

Figure 8, what does the scale in A represent? I assume it is voltage, but there are no units. Figure 8, C, E, G, these are unconventional units for synaptic weights, usually, these are given in nS / per input.

We have corrected these. The scalebar in 8A represents membrane potential in mV. The units of 8C,E,G are now in nS.

Reviewer #2 (Public Review):

Summary:

If synaptic input is functionally clustered on dendrites, nonlinear integration could increase the computational power of neural networks. But this requires the right synapses to be located in the right places. This paper aims to address the question of whether such synaptic arrangements could arise by chance (i.e. without special rules for axon guidance or structural plasticity), and could therefore be exploited even in randomly connected networks. This is important, particularly for the dendrites and biological computation communities, where there is a pressing need to integrate decades of work at the single-neuron level with contemporary ideas about network function.

Using an abstract model where ensembles of neurons project randomly to a postsynaptic population, back-of-envelope calculations are presented that predict the probability of finding clustered synapses and spatiotemporal sequences. Using data-constrained parameters, the authors conclude that clustering and sequences are indeed likely to occur by chance (for large enough ensembles), but require strong dendritic nonlinearities and low background noise to be useful.

Strengths:

(1) The back-of-envelope reasoning presented can provide fast and valuable intuition. The authors have also made the effort to connect the model parameters with measured values. Even an approximate understanding of cluster probability can direct theory and experiments towards promising directions, or away from lost causes.

(2) I found the general approach to be refreshingly transparent and objective. Assumptions are stated clearly about the model and statistics of different circuits. Along with some positive results, many of the computed cluster probabilities are vanishingly small, and noise is found to be quite detrimental in several cases. This is important to know, and I was happy to see the authors take a balanced look at conditions that help/hinder clustering, rather than to just focus on a particular regime that works.

(3) This paper is also a timely reminder that synaptic clusters and sequences can exist on multiple spatial and temporal scales. The authors present results pertaining to the standard `electrical' regime (~50-100 µm, <50 ms), as well as two modes of chemical signaling (~10 µm, 100-1000 ms). The senior author is indeed an authority on the latter, and the simulations in Figure 5, extending those from Bhalla (2017), are unique in this area. In my view, the role of chemical signaling in neural computation is understudied theoretically, but research will be increasingly important as experimental technologies continue to develop.

Weaknesses:

(1) The paper is mostly let down by the presentation. In the current form, some patience is needed to grasp the main questions and results, and it is hard to keep track of the many abbreviations and definitions. A paper like this can be impactful, but the writing needs to be crisp, and the logic of the derivation accessible to non-experts. See, for instance, Stepanyants, Hof & Chklovskii (2002) for a relevant example.

It would be good to see a restructure that communicates the main points clearly and concisely, perhaps leaving other observations to an optional appendix. For the interested but time-pressed reader, I recommend starting with the last paragraph of the introduction, working through the main derivation on page 7, and writing out the full expression with key parameters exposed. Next, look at Table 1 and Figure 2J to see where different circuits and mechanisms fit in this scheme. Beyond this, the sequence derivation on page 15 and biophysical simulations in Figures 5 and 6 are also highlights.

We appreciate the reviewers' suggestions. We have tightened the flow of the introduction. We understand that the abbreviations and definitions are challenging and have therefore provided intuitions and summaries of the equations discussed in the main text.

Clusters calculations

Our approach is to ask how likely it is that a given set of inputs lands on a short segment of dendrite, and then scale it up to all segments on the entire dendritic length of the cell.

Thus, the probability of occurrence of groups that receive connections from each of the M ensembles (PcFMG) is a function of the connection probability (p) between the two layers, the number of neurons in an ensemble (N), the relative zone-length with respect to the total dendritic arbor (Z/L) and the number of ensembles (M).

Sequence calculations

Here we estimate the likelihood of the first ensemble input arriving anywhere on the dendrite, and ask how likely it is that succeeding inputs of the sequence would arrive within a set spacing.

Thus, the probability of occurrence of sequences that receive sequential connections (PcPOSS) from each of the M ensembles is a function of the connection probability (p) between the two layers, the number of neurons in an ensemble (N), the relative window size with respect to the total dendritic arbor (Δ/L) and the number of ensembles (M).

(2) I wonder if the authors are being overly conservative at times. The result highlighted in the abstract is that 10/100000 postsynaptic neurons are expected to exhibit synaptic clustering. This seems like a very small number, especially if circuits are to rely on such a mechanism. However, this figure assumes the convergence of 3-5 distinct ensembles. Convergence of inputs from just 2 ense mbles would be much more prevalent, but still advantageous computationally. There has been excitement in the field about experiments showing the clustering of synapses encoding even a single feature.

We agree that short clusters of two inputs would be far more likely. We focused our analysis on clusters with three of more ensembles because of the following reasons:

(1) The signal to noise in these clusters was very poor as the likelihood of noise clusters is high.

(2) It is difficult to trigger nonlinearities with very few synaptic inputs.

(3) At the ensemble sizes we considered (100 for clusters, 1000 for sequences), clusters arising from just two ensembles would result in high probability of occurrence on all neurons in a network (~50% in cortex, see p_CMFG in figures below.). These dense neural representations make it difficult for downstream networks to decode (Foldiak 2003).

However, in the presence of ensembles containing fewer neurons or when the connection probability between the layers is low, short clusters can result in sparse representations (Figure 2 - Supplement 2). Arguments 1 and 2 hold for short sequences as well.

(3) The analysis supporting the claim that strong nonlinearities are needed for cluster/sequence detection is unconvincing. In the analysis, different synapse distributions on a single long dendrite are convolved with a sigmoid function and then the sum is taken to reflect the somatic response. In reality, dendritic nonlinearities influence the soma in a complex and dynamic manner. It may be that the abstract approach the authors use captures some of this, but it needs to be validated with simulations to be trusted (in line with previous work, e.g. Poirazi, Brannon & Mel, (2003)).

We agree that multiple factors might affect the influence of nonlinearities on the soma. The key goal of our study was to understand the role played by random connectivity in giving rise to clustered computation. Since simulating a wide range of connectivity and activity patterns in a detailed biophysical model was computationally expensive, we analyzed the exemplar detailed models for nonlinearity separately (Figures 5, 6, and new figure 8), and then used our abstract models as a proxy for understanding population dynamics. A complete analysis of the role played by morphology, channel kinetics and the effect of branching requires an in-depth study of its own, and some of these questions have already been tackled by (Poirazi, Brannon, and Mel 2003; Branco, Clark, and Häusser 2010; Bhalla 2017). However, in the revision, we have implemented a single model which incorporates the range of ion-channel, synaptic and biochemical signaling nonlinearities which we discuss in the paper (Figure 8, and Figure 8 Supplement 1, 2,3). We use this to demonstrate all three forms of sequence and grouped computation we use in the study, where the only difference is in the stimulus pattern and the separation of time-scales inherent in the stimuli.

(4) It is unclear whether some of the conclusions would hold in the presence of learning. In the signal-to-noise analysis, all synaptic strengths are assumed equal. But if synapses involved in salient clusters or sequences were potentiated, presumably detection would become easier? Similarly, if presynaptic tuning and/or timing were reorganized through learning, the conditions for synaptic arrangements to be useful could be relaxed. Answering these questions is beyond the scope of the study, but there is a caveat there nonetheless.

We agree with the reviewer. If synapses receiving connectivity from ensembles had stronger weights, this would make detection easier. Dendritic spikes arising from clustered inputs have been implicated in local cooperative plasticity (Golding, Staff, and Spruston 2002; Losonczy, Makara, and Magee 2008). Further, plasticity related proteins synthesized at a synapse undergoing L-LTP can diffuse to neighboring weakly co-active synapses, and thereby mediate cooperative plasticity (Harvey et al. 2008; Govindarajan, Kelleher, and Tonegawa 2006; Govindarajan et al. 2011). Thus if clusters of synapses were likely to be co-active, they could further engage these local plasticity mechanisms which could potentiate them while not potentiating synapses that are activated by background activity. This would depend on the activity correlation between synapses receiving ensemble inputs within a cluster vs those activated by background activity. We have mentioned some of these ideas in a published opinion paper (Pulikkottil, Somashekar, and Bhalla 2021). In the current study, we wanted to understand whether even in the absence of specialized connection rules, interesting computations could still emerge. Thus, we focused on asking whether clustered or sequential convergence could arise even in a purely randomly connected network, with the most basic set of assumptions. We agree that an analysis of how selectivity evolves with learning would be an interesting topic for further work.

References

Bhalla, Upinder S. 2017. “Synaptic Input Sequence Discrimination on Behavioral Timescales Mediated by Reaction-Diffusion Chemistry in Dendrites.” Edited by Frances K Skinner. eLife 6 (April):e25827. https://doi.org/10.7554/eLife.25827.

Branco, Tiago, Beverley A. Clark, and Michael Häusser. 2010. “Dendritic Discrimination of Temporal Input Sequences in Cortical Neurons.” Science (New York, N.Y.) 329 (5999): 1671–75. https://doi.org/10.1126/science.1189664.

Foldiak, Peter. 2003. “Sparse Coding in the Primate Cortex.” The Handbook of Brain Theory and Neural Networks. https://research-repository.st-andrews.ac.uk/bitstream/handle/10023/2994/FoldiakSparse HBTNN2e02.pdf?sequence=1.

Golding, Nace L., Nathan P. Staff, and Nelson Spruston. 2002. “Dendritic Spikes as a Mechanism for Cooperative Long-Term Potentiation.” Nature 418 (6895): 326–31. https://doi.org/10.1038/nature00854.

Govindarajan, Arvind, Inbal Israely, Shu-Ying Huang, and Susumu Tonegawa. 2011. “The Dendritic Branch Is the Preferred Integrative Unit for Protein Synthesis-Dependent LTP.” Neuron 69 (1): 132–46. https://doi.org/10.1016/j.neuron.2010.12.008.

Govindarajan, Arvind, Raymond J. Kelleher, and Susumu Tonegawa. 2006. “A Clustered Plasticity Model of Long-Term Memory Engrams.” Nature Reviews Neuroscience 7 (7): 575–83. https://doi.org/10.1038/nrn1937.

Harvey, Christopher D., Ryohei Yasuda, Haining Zhong, and Karel Svoboda. 2008. “The Spread of Ras Activity Triggered by Activation of a Single Dendritic Spine.” Science (New York, N.Y.) 321 (5885): 136–40. https://doi.org/10.1126/science.1159675.

Losonczy, Attila, Judit K. Makara, and Jeffrey C. Magee. 2008. “Compartmentalized Dendritic Plasticity and Input Feature Storage in Neurons.” Nature 452 (7186): 436–41. https://doi.org/10.1038/nature06725.

Poirazi, Panayiota, Terrence Brannon, and Bartlett W. Mel. 2003. “Pyramidal Neuron as Two-Layer Neural Network.” Neuron 37 (6): 989–99. https://doi.org/10.1016/S0896-6273(03)00149-1.

Pulikkottil, Vinu Varghese, Bhanu Priya Somashekar, and Upinder S. Bhalla. 2021. “Computation, Wiring, and Plasticity in Synaptic Clusters.” Current Opinion in Neurobiology, Computational Neuroscience, 70 (October):101–12. https://doi.org/10.1016/j.conb.2021.08.001.

eLife Assessment

The study presents important findings that reveal SEPHS2 and VPS37C as new potential drug targets for dasatinib and hydroxychloroquine respectively in addition to confirming known targets of these drugs. The evidence provided is compelling as observed in the methods, data and analyses. This article will be of great interest to chemical biologists, biochemists, and scientists in drug discovery and diagnostics.

Reviewer #2 (Public review):

Summary:

The study by Sun et al. introduces a useful system utilizing the proteasomal accessory factor A (PafA) and HaloTag for investigating drug-protein interactions in both in vitro (cell culture) and in vivo (zebrafish) settings. The authors presented the development and optimization of the system, as well as examples of its application and the identification of potential novel drug targets. However, the manuscript requires considerable improvements, particularly in writing and justification of experimental design. There are several inaccuracies in data description and a lack of statistics in some figures, undermining the conclusions drawn in the manuscript. Additionally, the authors introduced variants of the ligands and its cognate substrates, yet their use in different experiments appears random and lacks justification. It is challenging for readers to remember and track the specific properties of each variant, further complicating the interpretation of the results.

The conclusions of this paper are mostly backed by data, but certain aspects of data analysis and description require further clarification and expansion.

Comments on revisions:

We would like thank authors for submitting this revised version. We appreciate their inclusion of additional experiments, which convincingly demonstrate the absence of significant toxicity for in vivo applications. All our concerns and questions have been fully addressed. The clarity and quality of the writing have been substantially improved. We believe this innovative proximity labeling tool would be inspiring and valuable for the field.

Reviewer #3 (Public review):

Summary:

This manuscript introduces POST-IT (Pup-On-target for Small molecule Target Identification Technology), a novel non-diffusive proximity tagging system for identifying target proteins in live cells and organisms. This technology preserves cellular context essential for capturing specific drug-protein interactions, including transient complexes and membrane-associated proteins. Using an engineered fusion of proteasomal accessory factor A (PafA) and HaloTag, POST-IT specifically labels proximal proteins upon binding to a small molecule, with extensive optimization to enhance specificity and efficiency.

Strengths:

The study successfully identifies known targets and discovers new binders, such as SEPHS2 for dasatinib and VPS37C for hydroxychloroquine, advancing our understanding of their mechanisms. Additionally, its application in live zebrafish embryos demonstrates POST-IT's potential for widespread use in biological research and drug development.

Comments on revisions:

The authors have addressed most of the issues I raised in my review. I have no further comments.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) The technology requires a halo-tagged derivation of the active compound, and the linked position will have a huge impact on the potential "target hits" of the molecules. Given the fact that most of the active molecules lack of structure-activity relationship information, it is very challenging to identify the optimal position of the halo tag linkage.

We appreciate your insightful comment. While finding the optimal position to attach a chemical linker to a small molecule of interest is indeed a challenging but necessary step, this is a common difficulty across all target-ID methods, except for those that are modification-free, as we described in Discussion. However, modification-free approaches such as DARTS, CETSA, and TPP have their own limitations, such as low sensitivity and a high false-positive rate. Additionally, DARTS and SPROX are limited to use with cell lysates. Please refer to the introduction in our manuscript for more details on these approaches. On the other hand, synthesizing HTL derivatives is relatively straightforward compared to other modifications, and we provide helpful guidelines for chemical linker design, provided the optimal chemical moiety has been identified, which is crucial for target identification. We selected dasatinib and HCQ/CQ as model compounds because previous studies offered insights into their derivative synthesis. Our data also show that DH5 retains strong kinase inhibitory activity (Figure 4—figure supplement 2), and DC661-H1 demonstrates potent inhibition of autophagy (Figure 6—figure supplement 1). For novel compounds, conducting a thorough structure-activity relationship (SAR) study is essential to determine the optimal position for HTL derivative synthesis.

(2) Although POST-IT works in zebrafish embryos, there is still a long way to go for the broad application of the technology in other animal models.

Thank you for your constructive comment. Yes, there is still a long way to go in developing the POST-IT system for broader applications in other animal models, especially in mice. However, we hope that our study provides valuable insights and inspiration to scientists and experts for applying the POST-IT system in various models. We are also committed to further improving its applicability.

(3) The authors identified SEPHS2 as a new potential target of dasatinib and further validated the direct binding of dasatinib with this protein. However, considering the super strong activity of dasatinib against c-Src (sub nanomolar IC50 value), it is hard to conclude the contribution of SEPHS2 binding (micromolar potency) to its antitumor activity.

Thank you for your insightful comment. We agree that the anticancer activity of dasatinib primarily results from inhibiting tyrosine kinases such as SRC and ABL. However, SEPHS2 contains an “opal" termination codon, UGA, at the 60th amino acid residue, which codes for selenocysteine. Due to the technical challenge of expressing selenoproteins in E. coli, we mutated it to cysteine for expression in E. coli to avoid premature translation termination, as described in the Materials and Methods section. Although the purified recombinant SEPHS2 shows a Kd of about 10 µM for dasatinib, the binding affinity to endogenous SEPHS2 may be higher since selenocysteine is larger and more electronegative than cysteine. This presents an interesting area for future investigation. Furthermore, our study of dasatinib’s binding to SEPHS2 could help facilitate the development of new SEPHS2 inhibitors, potentially targeting the active site of SEPHS2.

Reviewer #3 (Public review):

(1) Target Specificity: It is crucial for the authors to differentiate between the primary targets of the POST-IT system and those identified as side effects. This distinction is essential for assessing the specificity and utility of the technology.

Thank you for your insightful comment. Drugs inevitably bind to various proteins with differing affinities, which can contribute to both side effects and beneficial outcomes. Typically, the primary targets exhibit high affinities. In this manuscript, we ranked the identified protein targets of DH5 based on affinity from mass spectrometry and p-values (Fig. 5A), and for DC661-H1, we used the SILAC ratio (Fig. 6A). We also individually assessed many drug-protein binding affinities using the MST assay, as well as in vitro and in cellulo assays, demonstrating their specificity. Moreover, we believe it is essential to identify as many protein targets as possible at physiological drug concentrations to better understand the drug’s side effects. Of course, further investigation is required to assess the roles and effects of these target proteins.

(2) In Vivo Target Identification: The manuscript lacks detailed clarity on which specific targets were successfully identified in the in vivo experiments. Expanding on this information would provide a clearer view of the system's effectiveness and scope in complex biological settings.

Thank you for your insightful comment regarding in vivo target identification. In this manuscript, we utilized a cell line as the primary method for in vivo target identification and validation after optimizing our system in test tubes. We successfully validated many of the targets identified using our POST-IT system (Figure 6—figure supplement 3). To demonstrate the proof of principle for in vivo application, we employed zebrafish embryos as an in vivo model, showing that endogenous SRC can be effectively pulled down by DH5 treatment (Fig. 7). While we could have explored the entire proteome to identify endogenous target proteins in zebrafish that bind to DH5 or dasatinib, we felt this would extend beyond our original scope, given that we have already demonstrated POST-IT’s ability to identify target proteins for dasatinib. Specific target identification and validation are crucial when using zebrafish for drug discovery. Additionally, we acknowledge that drugs likely interact with a range of protein targets in living organisms and may undergo metabolism and interactions within the circulatory system, which we address in our discussion.

(3) Reproducibility and Scalability: Discussion on the reproducibility of the POST-IT system across various experimental setups and biological models, as well as its scalability for larger-scale drug discovery programs, would be beneficial.

Thank you for the suggestion. While our system has shown  high reproducibility in our experiments, further improving both reproducibility and scalability would be advantageous. One potential approach to address this is through the generation of stable-expressing cell lines and transgenic zebrafish lines, which we have discussed in the revised manuscript. Establishing stable cell lines with robust POST-IT expression could enhance scalability for drug discovery applications.

(4) Quantitative Analysis: A more detailed quantitative analysis of the protein interactions identified by POST-IT, including statistical significance and comparative data against other technologies, would enhance the manuscript.

Thank you for your suggestion. In our assessment of drug-protein affinity, we included Kd values as quantitative measures using MST assays. The protein targets of dasatinib identified through mass spectrometry are also accompanied by p-values for quantitative analysis (Fig. 5A), and the detailed procedures are described in the Material and methods section. While it is challenging to provide direct comparative data against other technologies, our system successfully identified many known target proteins for dasatinib, as well as SEPHS2 and VPS37C as new targets for dasatinib and for HCQ/CQ, respectively, which were not detected by other methods.

(5) Technological Limitations: The authors should discuss any limitations or potential pitfalls of the POST-IT system, which would be crucial for future users and for guiding subsequent improvements.

Thank you for your insightful suggestion We agree that clearly defining the technological limitations is important. Therefore, we have expanded our original discussion on the limitations of our POST-IT system (Discussion section, paragraph 6).

(6) Long-Term Stability and Activity: Information on the long-term stability and activity of the POST-IT components in different biological environments would ensure the reliability of the system in prolonged experiments.

Yes, this is an important question. We did not notice any stability or toxicity issues with Halo-PafA and Pup substrates in HEK293T cells or zebrafish, which is an important factor for stable cell lines and transgenic zebrafish lines. However, HTL derivatives of the drug could be toxic or unstable due to the nature of the drug or its metabolism, which needs to be taken into account when designing experiments, and we have included this in the Discussion.

(7) Comparison with Existing Technologies: A detailed comparison with existing proximity tagging and target identification technologies would help position POST-IT within the current landscape, highlighting its unique advantages and potential drawbacks.

We appreciate your valuable feedback and agree that such comparisons are crucial. We have included a detailed overview and comparison of existing proximity-tagging systems and their related target identification technologies in the Introduction (lines 78-100) and Discussion (lines 391-412), highlighting their respective pros and cons. Additionally, we have expanded the discussion to further compare these technologies with our POST-IT system, addressing its advantages and limitations (lines 378-390, lines 448-467). We hope this provides sufficient context and information to effectively position POST-IT among the landscape of proximity-tagging target identification technologies.

(8) Concerns Regarding Overexposed Bands: Several figures in the manuscript, specifically Figure 3A, 3B, 3C, 3F, 3G, Figure 4D, and the second panels in Figure 7C as well as some figures in the supplementary file, exhibit overexposed bands.

We appreciate your astute observation regarding the overexposed bands and apologize for any confusion. The “overexposed” bands represent the unpupylated proteins, while the bands above them correspond to the pupylated proteins. We intended to clearly show both pupylated and unpupylated bands, although the latter are generally much weaker. We are currently working on further improving our POST-IT system to enhance pupylation efficiency.

(9) Innovation Concern: There is a previous paper describing a similar approach: Liu Q, Zheng J, Sun W, Huo Y, Zhang L, Hao P, Wang H, Zhuang M. A proximity-tagging system to identify membrane protein-protein interactions. Nat Methods. 2018 Sep;15(9):715-722. doi: 10.1038/s41592-018-0100-5. Epub 2018 Aug 13. PMID: 30104635. It is crucial to explicitly address the novel aspects of POST-IT in contrast to this earlier work.

Thank you for bringing this to our attention. Proximity-tagging systems like BioID, TurboID, NEDDylator, and PafA (Lui Q et al., Nat Methods 2018) were initially developed to study protein-protein interactions or identify protein interactomes, as these applications are of broader interest and generally easier to implement. However, applying proximity-tagging systems for small molecule target identification requires significant optimization. As described in the introduction (lines 78-100), target protein identification systems have since been developed using TurboID and NEDDylator (Tao AJ et al., Nat Commun 2023; Hill ZB et al., J Am Chem Soc 2016). It is conceivable that a PafA-based proximity-tagging system could also be adapted for target-ID, and other groups may pursue this approach in the future. Although the PafA-Pup system shows great promise for target-ID applications, extensive optimization was needed to enable its use for this purpose. Finally, we demonstrate that POST-IT offers distinct advantages over other proximity-tagging-based target-ID systems. For more details, please refer to the introduction and discussion sections.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Figure 1- Figure Supplement 1A: The Pup substrate "HB-Pup" is mentioned, but the main text or figure legend provides no introduction or description.

We appreciate your astute observation. We have added a description in the main text and figure legend as follows: “…and used HB-Pup as a control, which contains 6´His and BCCP at the N terminus of Pup” in the main text (line 142) and “HB, TS, and SBP refer to 6´His and BCCP, twin-STII (Strep-tag II), and streptavidin binding peptide, respectively.” in the Figure 1-figure supplement 1A.

(2) Figure 1 - Figure Supplement 3B: The authors used TS-sPupK61R as a substrate but did not explain why. The main text mentions that mutating sPup alone did not affect polypupylation, raising the question of why TS-sPupK61R was used in this figure. Furthermore, while the authors state that polypupylation becomes evident after 1 hour of incubation (more pronounced after 2 or 3 hours), the reactions here were conducted for only 30 minutes.

Thank you for your question. Figure 1 - Figure Supplement 3B was conducted to test self-pupylation levels in the different Halo-PafA derivatives. For this purpose, we could use any Pup substrate such as SBP-sPup and SBPK4R-sPupK61R, instead of Ts-sPup and TS-sPupK61R, as they do not show any differences in pupylation activity. We chose Ts-sPup and TS-sPupK61R simply because any Pup substrates could be used for this purpose. Similarly, we did not need to incubate the reaction for a longer time to detect polypupylation, as our intention was to test “self-pupylation”. We demonstrated in Figure 1 – figure supplement 2 that polypupylation is dependent on the number or position of lysine residues in Pup substrate or tags. The results clearly showed that self-pupylation was almost completely abolished by the Halo8KR mutation. To clarify this, we added the following description in lines 168-169: “Ts-sPup and TS-sPupK61R were chosen as sPup substrates for this experiment, although any Pup substrates could have been used. The levels of self-pupylation were assessed.”

(3) Line 156: The statement that "the TS-tag completely abolished polypupylation in TS-sPup" is inaccurate. Using TSK8R-sPupK61R as the substrate, several bands appear, which likely represent Halo-PafA with varying degrees of polypupylation. Some bands also appear to correspond to those seen when using TS-sPup as a substrate. The authors should clarify how they distinguish between multipupylation and polypupylation in this case.

We sincerely appreciate your insight into clarifying the distinction between multipupylation and polypupylation. Polypupylation refers to the addition of a new Pup onto a previously linked Pup on the target protein, akin to polyubiquitination. In contrast, multipupylation involves multiple single pupylations at different positions on the target proteins. Since pupylation occurs exclusively at lysine residues in tag-Pup substrates, mutating all lysine residues to arginine, as in TSK48R-sPupK61R, prevents the mutant tag-Pup from linking to another Pup. This means that only single pupylation can proceed with this type of mutant Pup substrate. If multiple pupylated bands are observed with this mutant substrate, it indicates “multipupylation” rather than “polypupylation”, as shown in Figure 1-figure supplement 2D. The same applies to the pupylation bands in Figure 1-figure supplement 2E and F, as sSBP-sPupK61R and SBPK4R-sPupK61R lack lysine residues. By comparing these multipupylation bands, it is also possible to distinguish them from polypupylation bands, which are marked by yellow arrows. However, after 2-3 pupylation bands, higher-order bands become increasingly difficult to distinguish.

To clarify the mutation in the TS-tag, we revised the sentence in line 156 from “However, further mutations within the TS-tag completely abolished polypupylation in TS-sPup” to “However, further mutations of two lysine residues within the TS-tag, creating TSK8R-sPupK61R, completely abolished polypupylation in TS-sPup”. Additionally, we have inserted sentences in line 152 to define polypupylation and multipupylation, as described here.

(4) Line 160: Similar to the above concern about line 156, the claim that SBPK4R and sSBP completely prevented polypupylation is unconvincing and requires more supporting evidence.

Thank you for raising this concern. As mentioned above, both SBPK4R and sSBP lack lysine residues required for pupylation. As a result, these mutants can only undergo multiple single pupylations on the lysine residues of the target protein, which leads to “multipupylation”. In Figure 1-figure supplement 2E and F, pupylation bands by sSBP-sPupK61R or SBPK4R-sPupK61R do not display doublet bands (one from multipupylation and the other from polypupylation), as seen with SBP-sPup, marked by yellow arrows. Notably, Halo-PafA containing polypupylated branches migrates more slowly than one with an equal number of multipupylation events. To clarify this point, we have added the phrase “as shown in sSBP-sPupK61R and SBP4KR-sPupK61R” at the end of the sentence in line 160.

(5) Lines 176-177: The authors claim that PafAS126A exhibited reduced polypupylation compared to PafA, but given that PafAS126A may reduce depupylase activity, how could it reduce polypupylation levels? Moreover, it is hard to find any data supporting this conclusion in Figure 1 - Figure Supplement 3B.

We appreciate your insightful comment. At this point, we do not fully understand how the mutation that reduces depupylase activity also decreases polypupylation. It is possible that PafAS126A has a lower preference for pupylated Pup as a prey, which is required for polypupylation, since depupylase activity depends on recognizing pupylated Pup as a prey to remove it. Nonetheless, Halo-PafAS126A shows reduced levels of higher molecular weight bands compared to Halo-PafA, as shown in Figure 1-figure supplement 3B, while exhibiting increased pupylation in lower molecular weight bands, which represent either multipupylation or low-degree polypupylation. Since higher molecular weight bands (> 150 kD) are likely due to polypupylation, this result suggests reduced polypupylation and increased multipupylation in Halo-PafAS126A. To clarify this in the main text, we have added the following description in line 177: “as evidenced by the decreased levels of high molecular weight bands and an increase in low molecular weight bands”

(6) POST-IT system in cellulo validation: The system was developed using the Halo-tag, yet the in-cell validation uses FRB and FKBP instead, without explaining this switch. This inconsistency makes the logic of the experiment unclear.

We appreciate your insightful comment. The interaction between rapamycin and FRB or FKBP is known to be highly specific and robust, making this system useful in various biological contexts. Due to this property, rapamycin can induce interaction between two proteins when one is fused with FRB and the other with FKBP. Before testing or optimizing the POST-IT system in cells, we hypothesized that using the rapamycin-induced interaction between FRB and FKBP could introduce pupylation of the target protein, provided that PafA is fused with FRB or FKBP and the target protein is fused with the other. The results demonstrate that PafA can introduce pupylation of the target protein in a proximity-dependent manner via this chemically induced interaction. To further clarify this in the main text, we modified the original sentence in lines 214-216 as follows: “To mimic drug-target interaction-induced pupylation in live cells and assess the potential of PafA as a proximity-tagging system for target-ID, we incorporated the rapamycin-induced interaction between FRB and FKBP into our PL system, as this interaction between a small molecule and a protein is known to be highly specific and robust (Figure 3—figure supplement 1A).”

(7) Line 209: The authors decided to use the SBP-tag for further studies due to better performance, but in Figure 3 - Figure supplement 1, they still used the unintroduced HB-Pup as the substrate, which is confusing and lacks explanation.

Thank you for raising your question. The SBP-tag is not superior to the TS-tag in terms of pupylation activity. However, the TSK8R mutant cannot bind to Strep-Tactin beads, while the SBP mutants, SBPK4R and sSBP, can bind to streptavidin. Therefore, we chose the SBP-tag instead of the TS-tag for further studies as a Pup substrate in POST-IT system, as we needed to pull down the target proteins. HB-Pup is consistently used as a control throughout various experiments, as it is the original Pup substrate. In Figure 3-figure supplement 1B and C, HB-Pup was used to test chemically induced pupylation by PafA. In these cases, it was not so critical which Pup substrate was chosen. Furthermore, we compared HB-Pup and different SBP-sPup substrates in Figure 3-figure supplement 1D, where HB-Pup was used as a control or for comparison. Although pupylation bands with HB-Pup appear more robust, this substrate contains multiple lysine residues, leading to high levels of polypupylation. To make it clear, we modified the sentence in line 209 to “Therefore, we decided to use the SBP-tag as a Pup substrate in the POST-IT system for further studies.”.

(8) Line 220: Both SBP-sPup and SBPK4R-sPupK61R are described as exhibiting efficient pupylation, but the data show mostly self-pupylation and little to no pupylation of the target protein.

Thank you for your concern. However, pupylation of the target protein is actually quite substantial, as the intensities of the free form and pupylated proteins are relatively similar, as shown in the upper panel of Figure 3-figure supplement 1D. Self-pupylation is always much higher than target pupylation, because PafA constantly pupylates itself, whereas pupylation of the target protein occurs only through interaction. Furthermore, V5-FRB-mKate2-PafA contains many lysine residues, which increases the levels of self-pupylation.

(9) Lines 222-224: The authors chose SBPK4R-sPupK61R to avoid polypupylation, although SBP-sPup did not cause detectable polypupylation. Neither substrate caused pupylation of the target protein, so the rationale behind this choice is unclear.

Thank you for raising your question. Similar to the above comment (#8), please refer to the pupylation bands of the target protein, as shown in the upper panel of Figure 3-figure supplement 1D. The pupylation band of the target protein is quite remarkable, as the intensities of the free form and pupylated proteins are comparable. Additionally, there are no multiple pupylation bands in either case, except for one additional weak multipupylation band, indicating no polypupylation by SBP-sPup, which does not have K-to-R mutations. Of course, SBPK4R-sPupK61R can only undergo single pupylation, as it does not contain lysine residues. Although we did not observe polypupylation by SBP-sPup in this experimental condition, it is possible that SBP-sPup may cause polypupylation under different experimental conditions or with other target proteins. Since SBPK4R-sPupK61R exhibits comparable pupylation of the target protein at least in this experiment setting as SBP-sPup, we selected SBPK4R-sPupK61R as the Pup substrate for POST-IT system to avoid any potential polypupylation that could be caused by SBP-sPup in other cases. We believe that polypupylation can introduce bias into the analysis and hinder the comprehensive discovery of additional target proteins for small molecules.

(10) Line 224: The authors conclude that rapamycin greatly reduced self-pupylation, but the supporting data are unclear.

Thank you for your constructive comments on our manuscript. Please refer to the lower panel of Figure 3-figure supplement 1D. When using either SBPK4R-sPupK61R or SBP-sPup, rapamycin treatment results in reduced levels of self-pupylation compared to the no-treatment control. However, we did not observe this reduction with HB-Pup and do not know the reason. To clarify this in the main text, we added the following description to the end of the sentence: “when using either SBPK4R-sPupK61R or SBP-sPup, as shown in the lower panel of Figure 3—figure supplement 1D”

(11) Line 234: The authors selected an 18-amino acid linker, but given that linkers longer than 10 amino acids enhance labeling, this choice should be explained.

Thank you for raising your question. In fact, a linker of 10 amino acids (aa) or longer is likely to behave similarly. We chose an 18 aa linker instead of a 40 aa linker primarily for the convenience of cloning and to reduce the potential for DNA sequence recombination associated with longer repeats. Additionally, a longer, flexible linker may behave like an intrinsically disordered protein (Harmon et al., 2017), which can lead to unwanted protein-protein interactions or phase separation. To elaborate on this, we added the following sentences after the sentence in line 233-235: “We chose the 18-amino acid linker instead of the 40-amino acid linker for easier cloning and to lower the risk of DNA recombination from longer repeats. Additionally, a longer, flexible linker may behave like an intrinsically disordered protein (Harmon et al., 2017), an unwanted feature for target-ID.”

(12) S126A and K172R mutations: The authors claim that these mutations additively enhanced pupylation under cellular conditions, but in Figure 3B, the band intensities appear similar for the wild-type and mutant versions.

Thank you for raising your concern. Although a single pupylation band appears similar among the three different Halo-PafA proteins, multipupylation bands are slightly but noticeably increased by the S126A and K172R mutations compared to Halo8KR-PafA. Since we used SBPK4R-sPupK61R as a Pup substrate, all higher molecular weight bands result from multipupylation rather than polypupylation. This illustrates why it is preferable to use SBPK4R-sPupK61R over SBP-sPup, as the pupylation bands with SBP-sPup are mixtures of poly- and multipupylation, making it difficult to assess levels of target labeling. To clarify this in the main text, we added the following description after the sentence in line 236: “as the higher molecular weight multipupylation bands are slightly but noticeably increased with these mutations compared to Halo8KR-PafA”

(13) Line 263: The authors selected DH5 for further experiments due to its efficiency, but the data suggest that the performance of DH1 to DH5 is similar.

We appreciate your question about the different dasatinib HTL derivatives. However, our data clearly show that DH2-5 derivatives bind significantly more effectively to Halo-PafA in vitro and in live cells compared to DH1 (Figure 4A and B). Additionally, the DH2-5 derivatives result in dramatically increased pupylation of the target protein in vitro and noticeable enhancement in live cells (Figure 4C and D). Among DH2 to DH5, there is no obvious difference in binding to Halo-PafA or pupylation of the target protein. Therefore, we chose DH5, as we believe that the longer linker in DH5 may facilitate the binding of a more diverse range of target proteins to dasatinib, enabling the discovery of additional target proteins.

(14) Line 309: The authors introduce HCQ and CQ as important drugs but then investigate the mechanism using DC661 without introducing or justifying the choice of this compound.

Thank you for your point. We explained the reason to choose DC661, a dimer form of CQ, instead of CQ for the synthesis of an HTL derivative in line 310. “assuming that a dimer would enhance binding affinity as previously described.” As the dimer forms of a drug or a small molecule such as testosterone dimers, estrogen dimers, and numerous anticancer drug dimers have been often developed to enhance drug effects (Paquin A et., Molecules 2021). Similarly, dimer forms of HCQ/CQ have been introduced and shown to be more potent (Hrycyna CA et al., ACS Chem Biol 2014; Rebecca VW et al., Cancer Discovery 2019). We expected that using a dimer form might offer higher probability to identify target proteins for HCQ/CQ.

(15) The authors suggest that multipupylation levels were enhanced but do not explain whether this might benefit the system or introduce other issues. Clarifying this point would provide valuable insight for potential users of this system.

Thank you for your thoughtful suggestion. Polypupylation likely leads to biased enrichment of a limited set of target proteins, and its levels may not correlate with the binding affinity of target proteins to the small molecule of interest, features that can negatively impact target-ID. In contrast, multipupylation may be correlated with binding affinity or interaction frequency, as we observed increased levels of multipupylation with higher Pup concentrations and longer incubation times. This suggests that target proteins with multiple lysines in proximity to PafA can be sequentially pupylated, starting with the most accessible lysine. However, if a target protein has only one accessible lysine, pupylation will occur only once, regardless of the protein’s affinity to the small molecule. In summary, while polypupylation may be a drawback for target-ID, multipupylation could be useful for both target-ID and understanding binding mode. To elaborate on this, we added the following additional explanation after the sentence in line 152: “, whereas multipupylation is more likely correlated with binding affinity or interaction frequency.”

(16) The author should address whether the Halotag ligand modification of the drug alters the binding properties between the drug and targets. That may be causing artifact binding of the drug and other proteins.

Thank you for your insightful comment. Yes, it is true that chemical modifications of the small molecule of interest, such as linker derivatization (e.g., HTL) or photo-affinity labeling, generally lead to reduced activity or affinity compared to the original molecule. Synthesizing a derivative is a common challenge across all target-ID methods, except for modification-free approaches, as we mentioned in the Discussion. However, modification-free methods like DARTS, CETSA, and TPP have their own limitations, including low sensitivity or high false positive rates. Identifying the optimal position for chemical modification on the small molecule of interest is critical. We chose dasatinib and HCQ/CQ as model compounds, because previous studies provided insights into their derivative synthesis. In addition, our data show that DH5 retains robust kinase inhibitory activity (Figure 4-figure supplement 2), and DC661-H1 exhibits potent autophagy inhibition (Figure 6-figure supplement 1). For novel compounds, a thorough structure-activity relationship study is essential to identify the optimal position for HTL derivative synthesis.

(17) The author stated there is no observable toxicity in zebrafish without providing a detailed analysis or enough data. Further analysis of the expression of Halo-PafA and its substrate sPup influence on toxicity or side effects to the living cells or animals would be needed. It is important for in vivo applications.

Thank you for your constructive suggestion. We have now included additional experimental data in Figure 7-figure supplement 1, showing no toxicity in zebrafish embryos expressing the POST-IT system. We assessed toxicity in two ways: by injecting the POST-IT DNA plasmid into one-cell-stage embryos for acute expression, and by using embryos from transgenic zebrafish expressing POST-IT under a heat-shock inducible promoter. Neither the injection nor the heat-shock activation of POST-IT expression resulted in any noticeable toxicity.

eLife Assessment

This important work presents two studies on predictive processing in subjects with and without tinnitus, matched for age, sex and hearing loss. These studies together provide compelling evidence for an enhanced predictability of upcoming sounds in regular sequences in EEG data recorded from tinnitus subjects. This work will be of interest to researchers, especially neuroscientists, in the tinnitus field and beyond.

Reviewer #1 (Public Review):

This work presents a replicable difference in predictive processing between subjects with and without tinnitus. In two independent MEG studies and using a passive listening paradigm, the authors identify an enhanced prediction score in tinnitus subjects compared to control subjects. In the second study, individuals with and without tinnitus were carefully matched for hearing levels (next to age and sex), increasing the probability that the identified differences could truly be attributed to the presence of tinnitus. Results from the first study could successfully be replicated in the second, although the effect size was notably smaller.

Throughout the manuscript, the authors provide a thoughtful interpretation of their key findings and offer several interesting directions for future studies. Their conclusions are fully supported by their findings. Moreover, the authors are sufficiently aware of the inherent limitations of cross-sectional studies.

Strengths:

The robustness of the identified differences in prediction scores between individuals with and without tinnitus is remarkable, especially as successful replication studies are rare in the tinnitus field. Moreover, the authors provide several plausible explanations for the decline of the effect size observed in the second study.

The rigorous matching for hearing loss, in addition to age and sex, in the second study is an important strength. This ensures that the identified differences cannot be attributed to differences in hearing levels between the groups.

The used methodology is explained clearly and in detail, ensuring that the used paradigms may be employed by other researchers in future studies. Moreover, the registering of the data collection and analysis methods for Study 2 as a Registered Report should be commended, as the authors have clearly adhered to the methods as registered.

Reviewer #2 (Public review):

Summary:

This study aimed to test experimentally a theoretical framework that aims to explain the perception of tinnitus, i.e., the perception of a phantom sound in the absence of external stimuli, through differences in auditory predictive coding patterns. To this aim, the researchers compared the neural activity preceding and following the perception of a sound using MEG in two different studies. The sounds could be highly predictable or random, depending on the experimental condition. They revealed that individuals with tinnitus and controls had different anticipatory predictions. This finding is a major step in characterizing the top-down mechanisms underlying sound perception in individuals with tinnitus.

Strengths:

This article uses an elegant, well-constructed paradigm to assess the neural dynamics underlying auditory prediction. The findings presented in the first experiment were partially replicated in the second experiment, which included 80 participants. This large number of participants for an MEG study ensures very good statistical power and a strong level of evidence. The authors used advanced analysis techniques - Multivariate Pattern Analysis (MVPA) and classifier weights projection - to determine the neural patterns underlying the anticipation and perception of a sound for individuals with or without tinnitus. The authors evidenced different auditory prediction patterns associated with tinnitus. Overall, the conclusions of this paper are well supported, and the limitations of the study are clearly addressed and discussed.

Author response:

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

eLife Assessment

This important work presents two studies on predictive processes in subjects with and without tinnitus. The evidence supporting the authors' claims is compelling, as their second study serves as an independent replication of the first. Rigorous matching between study groups was performed, especially in the second study, increasing the probability that the identified differences in predictive processing can truly be attributed to the presence of tinnitus. This work will be of interest to researchers, especially neuroscientists, in the tinnitus field.

We thank the editors at elife very much for their favorable assessment of our manuscript. Based upon the comments of the reviewer, we aimed to further improve our manuscript to be a valuable addition to the tinnitus research field.

Public Reviews:

Reviewer #2 (Public review):

Summary:

This study aimed to test experimentally a theoretical framework that aims to explain the perception of tinnitus, i.e., the perception of a phantom sound in the absence of external stimuli, through differences in auditory predictive coding patterns. To this aim, the researchers compared the neural activity preceding and following the perception of a sound using MEG in two different studies. The sounds could be highly predictable or random, depending on the experimental condition. They revealed that individuals with tinnitus and controls had different anticipatory predictions. This finding is a major step in characterizing the top-down mechanisms underlying sound perception in individuals with tinnitus.

Strengths:

This article uses an elegant, well-constructed paradigm to assess the neural dynamics underlying auditory prediction. The findings presented in the first experiment were partially replicated in the second experiment, which included 80 participants. This large number of participants for an MEG study ensures very good statistical power and a strong level of evidence. The authors used advanced analysis techniques - Multivariate Pattern Analysis (MVPA) and classifier weights projection - to determine the neural patterns underlying the anticipation and perception of a sound for individuals with or without tinnitus. The authors evidenced different auditory prediction patterns associated with tinnitus. Overall, the conclusions of this paper are well supported, and the limitations of the study are clearly addressed and discussed.

Weaknesses:

Even though the authors took care of matching the participants in age and sex, the control could be more precise. Tinnitus is associated with various comorbidities, such as hearing loss, anxiety, depression, or sleep disorders. The authors assessed individuals' hearing thresholds with a pure tone audiogram, but they did not take into account the high frequencies (6 kHz to 16 kHz) in the patient/control matching. Moreover, other hearing dysfunctions, such as speech-in-noise deficits or hyperacusis, could have been taken into account to reinforce their claim that the observed predictive pattern was not linked to hearing deficits. Mental health and sleep disorders could also have been considered more precisely, as they were accounted for only indirectly with the score of the 10-item mini-TQ questionnaire evaluating tinnitus distress. Lastly, testing the links between the individuals' scores in auditory prediction and tinnitus characteristics, such as pitch, loudness, duration, and occurrence (how often it is perceived during the day), would have been highly informative.

Thank you very much for your careful evaluation of our manuscript. We agree with you that our study design has some limitations such as the assessment of higher frequencies, comorbidities, and tinnitus characteristics. In our discussion, we aimed to acknowledge these issues for future research to improve this study design and gain more insights into neural tinnitus processes.

See e.g.:

Line 946-949:

“Additionally, we rigorously controlled for hearing loss in Study 2, however, pure-tone audiometric testing was solely performed up to 8kHz and we were therefore not able to draw conclusions regarding hearing impairments in higher frequencies and their influence on the effects.”

Line 949-954:

“Moreover, we did not screen our participants for hyperacusis. This hypersensitivity to mild sounds is widely correlated with the sensation of tinnitus and underlying neural mechanisms are potentially intertwined with tinnitus processes (Schilling et al., 2023; Yukhnovich et al., 2023; Zheng, 2020). Screening for hyperacusis in future work can therefore reveal more details on participant characteristics influencing predictive processing.”

Line 955-958:

“In both studies, tinnitus distress was not correlated with the reported prediction effects. Nevertheless, tinnitus can also be characterized by other features such as its loudness, pitch or duration which were not included in the experimental assessment.”

Line 958-963:

“Additionally, we solely used a short version of the Mini-TQ (Goebel and Hiller, 1992) in Study 2, which did not allow us to relate prediction scores to subscales like sleep disturbances which potentially influence cognitive functioning and thus predictive processing. Next to sleeping disorders and distress, tinnitus is often also accompanied by psychological comorbidities such as depression or anxiety (Langguth, 2011) which are potential confounds of the results.”

Comments on revisions:

Thank you for your responses. There are a few remaining points that, if addressed, could further enhance the manuscript:

- While the manuscript acknowledges the limitation of not matching groups on hearing thresholds in Study 1, a deeper analysis of participants' hearing abilities and their impact on MEG results, similar to that conducted in Study 2, would be valuable. Specifically, including a linear model that considers all frequencies, group membership, and their interactions could highlight differences across groups. Additionally, examining the effect of high-frequency hearing loss on prediction scores, as performed in Study 2, would strengthen the analysis, particularly given the trend noted (line 719). Such an addition could make a significant contribution to the literature by exploring how hearing abilities may influence prediction patterns.

We appreciate your feedback and agree with you that it is a crucial question how hearing abilities influence prediction patterns in tinnitus. However, as hearing status was not assessed in the control group in study 1, we are unfortunately not able to include linear models to investigate differences across groups in this sample. This led us to the implementation of study 2 with a comprehensive hearing assessment to investigate group differences. We highlighted this issue in our methods section.

Line 170-172:

“As pure-tone audiometric testing was not included for the control subjects, group comparisons between hearing thresholds were not feasible.”

- The connection with the hippocampal regions (line 864) remains somewhat unclear. While the inclusion of the Paquette reference appropriately links temporal region activity with tinnitus, it does not fully support the statement: "An increased focus on hippocampal regions, e.g., in fMRI, patient, or animal studies, could be a worthwhile complement to our MEG work, given the outstanding relevance of medial temporal areas in the formation of associations in statistical learning paradigms"

Thank you for your constructive input. This section is purely speculative, and we do not aim to provide strong claims or expected results but solely point out potential future research directions.

- Authors should add a comparison of participants mini-TQ scores on both studies

We appreciate your input and added a comparison of mini TQ-scores between samples. For study 1, all subscales were included, however, we computed the comparison solely based on the items of the mini-TQ to increase comparability. The results were not significant, i.e., tinnitus distress values did not differ between studies.

Line 629-632:

“We additionally compared tinnitus distress values assessed by the mini-TQ (Goebel and Hiller, 1992) between study 1 and study 2 to detect potential differences between the samples, however, results of the Welch’s t-test were not significant with t(30.7)=1.27, p\=.214.”

- Authors should add significant level on Fig 6.B as in Fig 3.C, and a n.s on Fig 6.D

Thank you very much for your input, we added significance levels and a n.s. to the Figures 6B and 6D.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary of the work: In this work, Fruchard et. al. study the enzyme Tgt and how it modifies guanine in tRNAs to queuosine (Q), essential for Vibrio cholerae's growth under aminoglycoside stress. Q's role in codon decoding efficiency and its proteomic effects during antibiotic exposure is examined, revealing Q modification impacts tyrosine codon decoding and influences RsxA translation, affecting the SoxR oxidative stress response. The research proposes Q modification's regulation under environmental cues reprograms the translation of genes with tyrosine codon bias, including DNA repair factors, crucial for bacterial antibiotic response.

The experiments are well-designed and conducted and the conclusions, for the most part, are well supported by the data. However, a few clarifications will significantly strengthen the manuscript.

Thank you.

Major:

Figure S4 A-D. These growth curves are important data and should be presented in the main figures. Moreover, given that it is not possible to make a rsxA mutant, I wonder if it would be possible to connect rsx and tgt using the following experiment: expression of tgt results in resistance to TOB (in B), while expression of only rsx lower resistance to TOB (in D). Then simultaneous overexpression of both tgt/rsx in the WT strain should have either no effect on TOB resistance or increased resistance, relative to the WT. Perhaps the authors have done this, and if so, the data should be included as it will significantly strengthen their model.

We thank the reviewer for this suggestion, we have tried to overexpress both tgt and rsxA simultaneously. However, this appears to be toxic as cells form small colonies and cannot grow well in liquid. We think that the presence of 2 plasmids and corresponding selection antibiotics amplify the toxicity of overexpressing rsxA, and even tgt. In fact, it can be seen that tgt overexpression in WT is already slightly deleterious, in the absence of tobramycin (figure 1B).

Figure S4 - Is there a rationale for why it is possible to make rsx mutants in E. coli, but not in V. cholerae? For example, does E. coli have a second gene/protein that is redundant in function to rsxA, while V. cholerae does not? I think your data hint at this, since in the right panel growth data, your double mutant does not fully rescue back to rsx single mutant levels, suggesting another factor in tgt mutant also acts to lower resistance to TOB. If so, perhaps a line or two in text will be helpful for readers.

This point raised by the referee is an interesting one that we have also asked ourselves at multiple occasions. In fact, the Rsx operon is linked with oxidative stress and respiration. Vibrio cholerae and E. coli show differences on genes involved in these pathways. V. cholerae lacks the cyo/nuo respiratory complex genes, and does not encode a Suf operon. Moreover, deletion of the anaerobic respiration Frd pathway leads to strong decrease of V. cholerae growth even in aerobic conditions. (10.1128/spectrum.01730-23). We have previously also generally seen differences between the 2 species in response to stress (10.1128/AAC.01549-10) and the way they deal with ROS (10.1371/journal.pgen.1003421). Therefore, we think that the fact that rsx is essential in V. cholerae and not E. coli could either be due to the presence of an additional redundant pathway in E. coli as suggested by the referee, or to more general differences in respiration and treatment of ROS. We thank the referee for highlighting this and we have now included a comment about this in the manuscript.

- For growth curves in Figure 2 and relative comparisons like in Figure 5D and Figure S4 (and others in the paper), statistics and error bars, along with replicate information should be provided.

We had mentioned this in the methods section, we have now added the specific information also on figure legends.

- Figure 6A - Is the transcript fold change in linear or log? If linear, then tgt expression should not be classified as being upregulated in TOB. It is barely up by ~2-fold with TOB- 0.6....which is a mild phenotype, at best.

We think that 2-fold change of tgt expression can be sufficient to lead to changes in tRNA modification levels. We agree that this is a mild induction, we have thus changed “increase” to “mildly increase” in the results.  

- Line 779- 780: "This indicates that sub-MIC TOB possibly induces tgt expression through the stringent response activation." To me, the data presented in this figure, do not support this statement. The experiment is indirect.

We agree, we rephrased: “Tobramycin may induces tgt expression through stringent response activation or through an independent pathway. “

- Figure 3B and D. - These samples only have tobramycin, correct? The legend says both carbenicillin and tobramycin.

The legend is correct, samples also have carbenicillin because we are testing here the growth with 2 synonymous beta-lactamase genes in presence of beta-lactams.

- Figure 5. The color schemes in bars do not match up with the color scheme in cartoons below panels B and C. That makes it confusing to read. Please fix.

Fixed.

- A lot of abbreviations have been used. This makes reading a bit cumbersome. Ideally, less abbreviations will be used.

Fixed

Reviewer #2 (Public Review):

Fruchard et al. investigate the role of the queuosine (Q) modification of the tRNA (Q-tRNA) in the human pathogen Vibrio cholerae. First, the authors state that the absence of Q-modified tRNAs (tgt mutant) increases the translation of TAT codons and proteins with a high TAT codon bias. Second, the absence of Q increases rsxA translation, because rsxA gene has a high TAT codon bias. Third, increased RsxA in the absence of Q inhibits SoxR response, reducing resistance towards the antibiotic tobramycin (TOB). Authors also predict in silico which genes harbor a higher TAT bias and found that among them are some involved in DNA repair, experimentally observing that a tgt mutant is more resistant to UV than the wt strain. It is worth noting that authors employ a wide variety of techniques, both experimental and bioinformatic. However, some aspects of the work need to be clarified or reevaluated.

(1) The statement that the absence of Q increases the translation of TAT codons and proteins encoded by TAT-enriched genes presents the following problems that should be addressed:

(1.1) The increase in TAT codon translation in the absence of Q is not supported by proteomics, since there was no detected statistical difference for TAT codon usage in proteins differentially expressed. Furthermore, there are some problems regarding the statistics of proteomics. Some proteins shown in Table S1 have adjusted p-values higher than their pvalues, which makes no sense. Maybe there is a mistake in the adjusted p-value calculation.

We appreciate the reviewer’s thorough examination of our findings. In our study, we employed an adaptive Benjamini-Hochberg (BH) procedure to control the false discovery rate in our list of selected proteins, as explained in the Data Analysis part of the Proteomics MS and analysis part of our material and methods. The classical BH procedure (10.1111/j.2517-6161.1995.tb02031.x) calculates the 𝑚×𝑝(𝑗) adjusted p-value for the i-th ranked p-value as min where 𝑝(𝑗) is the j-th ranked pvalue and 𝑚 is the number of tests (e.g. number of proteins) (see 10.1021/acs.jproteome.7b00170 for details). Since m/j > 1 and 𝑝(𝑗) > 𝑝(𝑖) for 𝑗≥𝑚, it follows that for 𝑗≥i, resulting in adjusted p-values being higher or equal than the original p-values. Therefore, contrary to the reviewer's comment, it is a mathematical property that the adjusted p-value is greater than the original p-value when using the classical Benjamini-Hochberg procedure. 

However, we want to underline that we used an « adaptive » BH procedure, which calculates the adjusted p-value for the i-th ranked p-value as min , where 𝜋0 is an estimate of the proportion of true null hypotheses (see 10.1021/acs.jproteome.7b00170 for details). Indeed, the classical BH procedure makes the assumption that 𝜋0 \= 1, which is a strong assumption in MS-based proteomics context.  Consequently, the mathematical property that the adjusted p-value is greater than the original p-value does not always hold true in our approach (that depends also on the 𝜋0 parameter).

In addition, it is not common to assume that proteins that are quantitatively present in one condition and absent in another are differentially abundant proteins. Proteomics data software typically addresses this issue and applies some corrections. It would be advisable to review that.

We thank the reviewer for highlighting this point. Indeed, some software impute a random small value to replace missing values and then produces statistics based on this imputed data (10.1038/nmeth.3901). However, the validity and relevance of generating statistics in the absence of actual data is questionable. 

There are no universally accepted guidelines for handling this situation, and we believe it is more logical to set these values aside as potential interesting proteins. It is well-established that intensity values are often missing due to the detection limits of the spectrometer, suggesting that the missing values observed in several replicates of a condition are actually due to low values (see 10.1093/bioinformatics/btp362 and 10.1093/bioinformatics/bts193 for instance). It is thus logical to consider the associated proteins as potentially differentially abundant when comparing their complete absence in all replicates of one condition to their presence in several replicates of another condition.

(1.2) Problems with the interpretation of Ribo-seq data (Figure 4D). On the one hand, the Ribo-seq data should be corrected (normalized) with the RNA-seq data in each of the conditions to obtain ribosome profiling data, since some genes could have more transcription in some of the conditions studied. In other articles in which this technique is used (such as in Tuorto et al., EMBO J. 2018; doi: 10.15252/embj.201899777), it is interpreted that those positions in which the ribosome moves most slowly and therefore less efficiently translated), are the most abundant. Assuming this interpretation, according to the hypothesis proposed in this work, the fragments enriched in TAT codons should have been less abundant in the absence of Q-tRNA (tgt mutant) in the Rib-seq experiment. However, what is observed is that TAT-enriched fragments are more abundant in the tgt mutant, and yet the Ribo-seq results are interpreted as RNA-seq, stating that this is because the genes corresponding to those sequences have greater expression in the absence of Q. 

As recommended by the reviewer, we normalized the RiboSeq data with the RNAseq data to account for potential RNA variations. The updated Figure 4 demonstrates that this normalization does not alter our findings, confirming that variations at the RNAseq level do not contradict changes at the translational level. 

The reviewer's observation that pauses at TAT codons would lead to ribosome accumulation and subsequent categorization as "up" genes is accurate. We must emphasize, however, that this category of “up genes” is probably quite diverse. The effect of ribosome stalling at TAT codons on total mRNA ribosome occupancy is likely highly variable, depending on the location of the TAT codon(s) within the CDS and the gene's expression level. We therefore think that genes in the "Up" category mainly correspond to genes that are more translated because the impact of pausing at TAT codons is probably not strong enough. Note that unlike what is usually done in bacterial riboseq experiments, we did not use any antibiotics to artificially freeze the ribosomes.

On the other hand, it would be interesting to calculate the mean of the protein levels encoded by the transcripts with high and low ribosome profiling data.

While this is a common request, we believe that comparing RiboSeq and proteomics data is not particularly informative. RiboSeq data directly measures translation, while proteomics provides information about protein abundance at steady state, reflecting the balance between protein synthesis and degradation. Furthermore, the number of proteins detectable by mass spectrometry is significantly smaller than the number of genes quantified by RiboSeq. Given these factors, there is often a low correlation between translation and protein abundance, making a direct comparison less relevant 

(1.3) This statement is contrary to most previously reported studies on this topic in eukaryotes and bacteria, in which ribosome profiling experiments, among others, indicate that translation of TAT codons is slower (or unaffected) than translation of the TAC codons, and the same phenomenon is observed for the rest of the NAC/T codons. This is completely opposed to the results showed in Figure 4. However, the results of these studies are either not mentioned or not discussed in this work. Some examples of articles that should be discussed in this work:

- "Queuosine-modified tRNAs confer nutritional control of protein translation" (Tuorto et al., 2018; 10.15252/embj.201899777)

- "Preferential import of queuosine-modified tRNAs into Trypanosoma brucei mitochondrion is critical for organellar protein synthesis" (Kulkarni et al., 2021; doi:10.1093/nar/gkab567.

- "Queuosine-tRNA promotes sex-dependent learning and memory formation by maintaining codonbiased translation elongation speed" (Cirzi et al., 2023; 10.15252/embj.2022112507)

- "Glycosylated queuosines in tRNAs optimize translational rate and post-embryonic growth" (Zhao et al., 2023; 10.1016/j.cell.2023.10.026)

- "tRNA queuosine modification is involved in biofilm formation and virulence in bacteria" (Diaz-Rullo and Gonzalez-Pastor, 2023; doi: 10.1093/nar/gkad667). In this work, the authors indicate that QtRNA increases NAT codon translation in most bacterial species. Could the regulation of TAT codonenriched proteins by Q-tRNAs in V. cholerae an exception? In addition, authors use a bioinformatic method to identify genes enriched in NAT codons similar to the one used in this work, and to find in which biological process are involved the genes whose expression is affected by Q-tRNAs (as discussed for the phenotype of UV resistance). It will be worth discussing all of this.

Thank you for detailed suggestions, we agree that this discussion was missing and this comment gives us a chance to address that in the revised version of the manuscript.

About the references above suggested by the referee, 4 of these papers were not mentioned in our manuscript, these were published while our manuscript was previously in review and we realize we have not cited them in the latest version of our manuscript. We thank the referee for highlighting this. We have now included a discussion about this. 

We included the following in the discussion:

“However, the opposite codon preference was shown in E. coli {Diaz-Rullo, 2023 #1888}. In eukaryotes also, several recent studies indicate slower translation of U-ending codons in the absence of Q34 {Cirzi, 2023 #1887;Kulkarni, 2021 #1886;Tuorto, 2018 #1268}. It’s important to note here, that in V. cholerae ∆tgt, increased decoding of U-ending codons is observed only with tyrosine, and not with the other three NAC/U codons (Histidine, Aspartate, Asparagine). This is interesting because it suggests that what we observe with tyrosine may not adhere to a general rule about the decoding efficiency of U- or C-ending codons, but instead seems to be specific to Tyr tRNAs, at least in the context of V. cholerae. Exceptions may also exist in other organisms. For example, in human cells, queuosine increases efficiency of decoding for U- ending codons and slows decoding of C- ending codons except for AAC {Zhao, 2023 #1889}. In this case, the exception is for tRNA Asparagine. Moreover, in mammalian cells {Tuorto, 2018 #1268}, ribosome pausing at U-ending codons is strongly seen for Asp, His and Asn, but less with Tyr. In Trypanosoma {Kulkarni, 2021 #1886}, reporters with a combination of the 4 NAC/NAU codons for Asp, Asn, Tyr, His have been tested, showing slow translation at U- ending version of the reporter in the absence of Q, but the effect on individual codons (e.g. Tyr only) is not tested. In mice {Cirzi, 2023 #1887}, ribosome slowdown is seen for the Asn, Asp, His U-ending codons but not for the Tyr U-ending codon. In summary, Q generally increases efficiency of U- ending codons in multiple organisms, but there appears to be additional unknown parameters which affect tyrosine UAU decoding, at least in V. cholerae. Additional factors such as mRNA secondary structures or mistranslation may also contribute to the better translation of UAU versions of tested genes. Mistranslation could be an important factor. If codon decoding fidelity impacts decoding speed, then mistranslation could also contribute to decoding efficiency of Tyr UAU/UAC codons and proteome composition.”

(1.4) It is proposed that the stress produced by the TOB antibiotic causes greater translation of genes enriched in TAT codons. 

Actually, it’s the opposite because in presence of TOB, in the wt, tgt would be induced leading to more Q on tRNA-Tyr and less translation of TAT.

On the one hand, it is shown that the GFP-TAT version (gene enriched in TAT codons) and the RsxATAT-GFP protein (native gene naturally enriched in TAT) are expressed more, compared to their versions enriched in TAC in a tgt mutant than in a wt, in the presence of TBO (Fig. 5C). 

Figure 5C shows relative fluorescence, ie changes of fluorescence in delta-tgt compared to WT. So it’s not necessarily more expressed but “more increased”

However, in the absence of TOB, and in a wt context, although the two versions of GFP have a similar expression level (Fig. 3SD), the same does not occur with RsxA, whose RsxA-TAT form (the native one) is expressed significantly more than the RsxA-TAC version (Fig. 3SA). How can it be explained that in a wt context, in which there are also tRNA Q-modification, a gene naturally enriched in TAT is translated better than the same gene enriched in TAC?

We thank the referee for this question based on careful assessment of our data. We agree, there appears to be significantly more RsxA-TAT in WT than RsxA-TAC. This could be due to other effects such as secondary structure formation on mRNA when the wt RsxA is recoded with TAC codons. This does not hinder the conclusion that the translation of the TAT version is increased in delta-tgt compared to WT.  

It would be expected that in the presence of Q-tRNAs the two versions would be translated equally (as happens with GFP) or even the TAT version would be less translated. On the other hand, in the presence of TOB the fluorescence of WT GFP(TAT) is higher than the fluorescence of WT GFP(TAC) (Figure S3E) (mean fluorescence data for RsxA-GFP version in the presence of TOB is not shown). These results may indicate that the apparent better translation of TAT versions could be due to indirect effects rather from TAT codon translation.

This is now mentioned in the manuscript

“We cannot exclude, however, that additional factors such as mRNA secondary structures also contributes to the better translation of UAU versions of tested genes. “

(2) Another problem is related to the already known role of Q in prevention of stop codon readthrough, which is not discuss at all in the work. In the absence of Q, stop codon readthrough is increased. In addition, it is known that aminoglycosides (such as tobramycin) also increase stop codon readthrough ("Stop codon context influences genome-wide stimulation of termination codon readthrough by aminoglycosides"; Wanger and Green, 2023; 10.7554/eLife.52611). Absence of Q and presence of aminoglycosides can be synergic, producing devastating increases in stop codon readthrough and a large alteration of global gene expression. All of these needs to be discussed in the work. Moreover, it is known that stop codon readthrough can alter gene expression and mRNA sequence context all influence the likelihood of stop codon readthrough. Thus, this process could also affect to the expression of recoded GFP and RsxA versions.

We included the following in the revised version of the manuscript (results):

“Q modification impacts decoding fidelity in V. cholerae.

To test whether a defect in Q34 modification influences the fidelity of translation in the presence and absence of tobramycin, previously developed reporter tools were used (Fabret & Namy, 2021), to measure stop codons readthrough in V. cholerae ∆tgt and wild-type strains. The system consists of vectors containing readthrough promoting signals inserted between the lacZ and luc sequences, encoding β-galactosidase and luciferase, respectively. Luciferase activity reflects the readthrough efficiency, while β-galactosidase activity serves as an internal control of expression level, integrating a number of possible sources of variability (plasmid copy number, transcriptional activity, mRNA stability, and translation rate).  We found increased readthrough at stop codons UAA and to a lesser extent at UAG for ∆tgt, and this increase was amplified for UAG in presence of tobramycin (Fig. S2, stop readthrough). In the case of UAA, tobramycin appears to decrease readthrough, this may be artefactual, due to the toxic effect of tobramycin on ∆tgt.

Mistranslation at specific codons can also impact protein synthesis. To further investigate mistranslation levels by tRNATyr in WT and ∆tgt, we designed a set of gfp mutants where the codon for the catalytic tyrosine required for fluorescence (TAT at position 66) was substituted by nearcognate codons (Fig. S2). Results suggest that in this sequence context, particularly in the presence of tobramycin, non-modified tRNATyr mistakenly decodes Asp GAC, His CAC and also Ser UCC, Ala GCU, Gly GGU, Leu CUU and Val GUC codons, suggesting that Q34 increases the fidelity of tRNATyr. 

In parallel, we replaced Tyr103 of the β-lactamase described above, with Asp codons GAT or GAC. The expression of the resulting mutant β-lactamase is expected to yield a carbenicillin sensitive phenotype. In this system, increased tyrosine misincorporation (more mistakes) by tRNATyr at the mutated Asp codon, will lead to increased synthesis of active β-lactamase, which can be evaluated by carbenicillin tolerance tests. As such, amino-acid misincorporation leads here to phenotypic (transient) tolerance, while genetic reversion mutations result in resistance (growth on carbenicillin). The rationale is summarized in Fig. 3C. When the Tyr103 codon was replaced with either Asp codons, we observe increased β-lactamase tolerance (Fig. 3D, left), suggesting increased misincorporation of tyrosine by tRNATyr at Asp codons in the absence of Q, again suggesting that Q34 prevents misdecoding of Asp codons by tRNATyr.

In order to test any effect on an additional tRNA modified by Tgt, namely tRNAAsp, we mutated the Asp129 (GAT) codon of the β-lactamase. When Asp129 was mutated to Tyr TAT (Fig. 3D, right), we observe reduced tolerance in ∆tgt, but not when it was mutated to Tyr TAC, suggesting less misincorporation of aspartate by tRNAAsp at the Tyr UAU codon in the absence of Q. In summary, absence of Q34 increases misdecoding by tRNATyr at Asp codons, but decreases misdecoding by tRNAAsp at Tyr UAU. 

This supports the fact that tRNA Q34 modification is involved in translation fidelity during antibiotic stress, and that the effects can be different on different tRNAs, e.g. tRNATyr and tRNAAsp tested here.”

Added figures: Figure S2, Figure 3CD

(3) The statement about that the TOB resistance depends on RsxA translation, which is related to the presence of Q, also presents some problems:

(3.1) It is observed that the absence of tgt produces a growth defect in V. cholerae when exposed to TOB (Figure 1A), and it is stated that this is mediated by an increase in the translation of RsxA, because its gene is TAT enriched. However, in Figure S4F, it is shown that the same phenotype is observed in E. coli, but its rsxA gene is not enriched in TAT codons. Therefore, the growth defect observed in the tgt mutant in the presence of TOB may not be due to the increase in the translation of TAT codons of the rsxA gene in the absence of Q. This phenotype is very interesting, but it may be related to another molecular process regulated by Q. Maybe the role of Q in preventing stop codon readthrough is important in this process, reducing cellular stress in the presence of TOB and growing better.

FigS4F (now figure 5D) shows that rsxA can be toxic during growth in presence of tobramycin, but it does not show that rsxA translation is increased in E. coli in delta-tgt. However, we agree with the referee that there are probably additional processes regulated by Q which are also involved in the response to TOB stress. We already had mentioned this briefly in the discussion (“Note that, our results do not exclude the involvement of additional Q-regulated MoTTs in the response to sub-MIC TOB, since Q modification leads to reprogramming of the whole proteome. “), we further discussed it as follows:

“As a consequence, transcripts with tyrosine codon usage bias are differentially translated. One such transcript codes for RsxA, an anti-SoxR factor. SoxR controls a regulon involved in oxidative stress response and sub-MIC aminoglycosides trigger oxidative stress in V. cholerae{Baharoglu, 2013 #720}, pointing to an involvement of oxidative stress response in the response to sub-MIC tobramycin stress.

A link between Q34 and oxidative stress has also been previously found in eukaryotic organisms {Nagaraja, 2021 #1466}. Note that our results do not exclude the involvement of additional Qregulated translation of other transcripts in the response to tobramycin. Q34 modification leads to reprogramming of the whole proteome, not only for other transcripts with codon usage bias, but also through an impact on the levels of stop codon readthrough and mistranslation at specific codons, as supported by our data.”

(3.2) All experiments related to the effect of Q on the translation of TAT codons have been performed with the tgt mutant strain. Considering that the authors have a pSEVA-tgt plasmid to overexpress this gene, they would have to show whether tgt overexpression in a wt strain produces a decrease in the translation of proteins encoded by TAT-enriched genes such as RsxA. This experiment would allow them to conclude that Q reduces RsxA levels, increasing resistance to TOB.

We agree that this would be interesting to test, however, as it can be seen in figure 1B, delta-tgt pSEVAtgt (complemented strain) grows better than WT pSEVA-tgt (tgt overexpression). In fact, overexpression of tgt negatively impacts cell growth and yield smaller colonies, especially when cells carry a second plasmid (e.g with gfp constructs). We have also seen this with other RNA modification gene overexpressions in the lab (unpublished). We believe that the expression of tgt is tuned and since overexpression affects fitness, it is generally difficult to conduct experiments with overexpression plasmid for RNA modifications.  Nevertheless, we have done the experiment (with slow growing bacteria) and when we normalize expression of gfp in the presence of tgt overexpressing plasmid to the condition with no plasmid, we see little (1.5 fold) or no effect of tgt overexpression on fluorescence (see graph below). This is probably due to a toxic effect of ooverexpression and we do not believe these results are biologically relevant. 

Author response image 1.

(3.3) On the other hand, Fig. 1B shows that when the wt and tgt strains compete, both overexpressing tgt, the tgt mutant strain grows better in the presence of TOB. This result is not very well understood, since according to the hypothesis proposed, the absence of modification by Q of the tRNA would increase the translation of genes enriched in TAT, therefore, a strain with a higher proportion of Q-modified tRNAs as in the case of the wt strain overexpressing tgt would express the rsxA gene less than the tgt strain overexpressing tgt and would therefore grow better in the presence of TOB. For all these reasons, it would be necessary to evaluate the effect of tgt overexpression on the translation of RsxA.

See our answer above about negative effect of tgt overexpression.

(3.4) According to Figure 1I, the overexpression of tRNA-Tyr(GUA) caused a better growth of tgt mutant in comparison to WT. If the growth defect observed in tgt mutant in the presence of TOB is due to a better translation of the TAT codons of rsxA gene, the overexpression of tRNA-Tyr(GUA) in the tgt mutant should have resulted in even better RsxA translation a worse growth, but not the opposite result.

We agree, we think that rsxA is not the only factor responsible for growth defect of tgt in presence of TOB (as now further discussed in the discussion). Overexpression of tRNAtyr possibly changes the equilibrium between the decoding of TAC vs TAT and may restore translation of TAC enriched genes. As also suggested by rev3, we have measured decoding reporters for TAT/TAC while overexpressing tTNA-tyr. This is now added to the results in fig S2C and the following:

“We also tested decoding reporters for TAT/TAC in WT and ∆tgt overexpressing tRNATyr in trans (Fig. S1C). The presence of the plasmid (empty p0) amplified differences between the two strains with decreased decoding of TAC (and increased TAT, as expected) in ∆tgt compared to WT. Overexpression of tRNATyrGUA did not significantly impact decoding of TAT and increased decoding of TAC, as expected. Since overexpression of tRNATyrGUA rescues ∆tgt in tobramycin (Fig. 1I) and facilitates TAC decoding, this suggests that issues with TAC codon decoding contribute to the fitness defect observed in ∆tgt upon growth with tobramycin. Overexpression of tRNATyrAUA increased decoding of TAT in WT but did not change it in ∆tgt where it is already high. Unexpectedly, overexpression of tRNATyrAUA also increased decoding of TAC in WT. Thus, overexpression of tRNATyrAUA possibly changes the equilibrium between the decoding of TAC vs TAT and may restore translation of TAC enriched transcripts.” 

Added figure: figure S1C

(4) It cannot be stated that DNA repair is more efficient in the tgt mutant of V. cholerae, as indicated in the text of the article and in Fig 7. The authors only observe that the tgt mutant is more resistant to UV radiation and it is suggested that the reason may be TAT bias of DNA repair genes. To validate the hypothesis that UV resistance is increased because DNA repair genes are TAT biased, it would be necessary to check if DNA repair is affected by Q. UV not only produces DNA damage, but also oxidative stress. Therefore, maybe this phenotype is due to the increase in proteins related to oxidative stress controlled by RsxA, such as the superoxide dismutase encoded by sodA. It is also stated that these repair genes were found up for the tgt mutant in the Ribo-seq data, with unchanged transcription levels. Again, it is necessary to clarify this interpretation of the Ribo-seq data, since the fact that they are more represented in a tgt mutant perhaps means that translation is slower in those transcripts. Has it been observed in proteomics (wt vs tgt in the absence of TOB) whether these proteins involved in repair are more expressed in a tgt mutant?

We agree that our results do not directly show that DNA repair is more efficient, but that delta-tgt responds better to UV. This has been modified in the manuscript. About oxidative stress, we did not see a better or worse response to H202 of delta-tgt. Moreover, since we see better response of deltatgt  to UV only in V. cholerae and not in E. coli, we did not favor the hypothesesi of response to stressox. In proteomics, we do not detect changes for DNA repair genes except for RuvA which is more abundant in delta-tgt. We have toned down the statement about DNA repair in the paper.

(5) The authors demonstrate that in E. coli the tgt mutant does not show greater resistance to UV radiation (Fig. 7D), unlike what happens in V. cholerae. It should be discussed that in previous works it has been observed that overexpression in E. coli of the tgt gene or the queF gene (Q biosynthesis) is involved in greater resistance to UV radiation (Morgante et al., Environ Microbiol, 2015 doi: 10.1111/1462-2920.12505; and Díaz-Rullo et al., Front Microbiol. 2021 doi: 10.3389/fmicb.2021.723874). As an explanation, it was proposed (Diaz-Rullo and Gonzalez-Pastor, NAR 2023 doi: 10.1093/nar/gkad667) that the observed increase in the capacity to form biofilms in strains that overexpress genes related to Q modification of tRNA would be related to this greater resistance to UV radiation.

We now mention the previous observations suggesting a link between tgt and UV. We thank the referee for the reference which we had overlooked. Note that in the case of our experiments, all cultures are in planktonic form and are not allowed to form biofilms. We thus prefer not to biofilmlinked processes in this study.

Reviewer #3 (Public Review):

Summary:

In this manuscript the authors begin with the interesting phenotype of sub-inhibitory concentrations of the aminoglycoside tobramycin proving toxic to a knockout of the tRNA-guanine transglycosylase (Tgt) of the important human pathogen, Vibrio cholerae. Tgt is important for incorporating queuosine (Q) in place of guanosine at the wobble position of GUN codons. The authors go on to define a mechanism of action where environmental stressors control expression of tgt to control translational decoding of particularly tyrosine codons, skewing the balance from TAC towards TAT decoding in the absence of the enzyme. The authors use advanced proteomics and ribosome profiling to reveal that the loss of tgt results in increased translation of proteins like RsxA and a cohort of DNA repair factors, whose genes harbor an excess of TAT codons in many cases. These findings are bolstered by a series of molecular reporters, mass spectrometry, and tRNA overexpression strains to provide support for a model where Tgt serves as a molecular pivot point to reprogram translational output in response to stress.

Strengths:

The manuscript has many strengths. The authors use a variety of strains, assays, and advanced techniques to discover a mechanism of action for Tgt in mediating tolerance to sub-inhibitory concentrations of tobramycin. They observe a clear phenotype for a tRNA modification in facilitating reprogramming of the translational response, and the manuscript certainly has value in defining how microbes tolerate antibiotics.

We thank the referee for their time and comments. 

Weaknesses:

The conclusions of the manuscript are mostly very well-supported by the data, but in some places control experiments or peripheral findings cloud precise conclusions. Some additional clarification, discussion, or even experimental extension could be useful in strengthening these areas.

(1) The authors have created and used a variety of relevant molecular tools. In some cases, using these tools in additional assays as controls would be helpful. For example, testing for compensation of the observed phenotypes by overexpression of the Tyrosine tRNA(GUA) in Figure 2A with the 6xTAT strain, Figure 5C with the rxsA-GFP fusion, and/or Figure 7B with UV stress would provide additional information of the ability of tRNA overexpression to compensate for the defect in these situations.

Thank you for the suggestions. Since overexpression of tRNA tyr is not expected to decrease decoding of TAT, we do not necessarily expect any effect for UV and rsxA expression. Overexpression of tRNA_GUA restores fitness of delta-tgt in TOB, but this is probably independent of RsxA. As ref2 also suggested above, we included in the discussion that the effect seen in delta-tgt with TOB is not only due to RsxA expression but also additional processes. However, these suggestions are interesting and we performed the following experiments in order to have an answer for these questions: 

- “testing for compensation of the observed phenotypes by overexpression of the Tyrosine tRNA(GUA) in Figure 2A with the 6xTAT strain”: 

This is now included in figure S2C and results as follows: 

“We also tested decoding reporters for TAT/TAC in WT and ∆tgt overexpressing tRNA-Tyr in trans (Fig. S1C). The presence of the plasmid amplified differences between the two strains with decreased decoding of TAC (and increased TAT, as expected) in ∆tgt with empty plasmid compared to WT. Overexpression of tRNA_TyrGUA did not significantly impact decoding of TAT and increased decoding of TAC as expected. Since overexpression of tRNA_TyrGUA rescues ∆tgt in tobramycin (Fig. 1I) and facilitates TAC decoding, this suggests that issues with TAC codon decoding contribute to the fitness defect observed in ∆tgt upon growth with tobramycin. Overexpression of tRNA_TyrAUA increased decoding of TAT in WT but did not change it in ∆tgt where it is already high. Interestingly, overexpression of TyrAUA also increased decoding of TAC in WT. Thus, overexpression of tRNA_TyrAUA possibly changes the equilibrium between the decoding of TAC vs TAT and may restore translation of TAC enriched transcripts. “  

-  Figure 5C with the rxsA-GFP fusion: 

When we overexpress tRNA_GUA, rsxA fluorescence is 2-fold higher in delta-tgt compared to wt. However, the fluorescence is highly decreased compared to the condition with no tRNA overexpression. While we are not sure whether this apparent decrease is a technical issue or not (e.g. due to the presence of additional plasmid), we prefer not to further explore this in this manuscript. Note that we could not obtain delta-tgt strain carrying both plasmids expressing tRNA_GUA and rsxA, suggesting toxic overproduction of rsxA in this context.

Author response image 2.

- Figure 7B with UV stress: 

Here again, delta-tgt overexpressing tRNA_GUA is still more UV resistant than WT overexpressing tRNA_GUA.

Author response image 3.

(2) The authors present a clear story with a reprogramming towards TAT codons in the knockout strain, particularly regarding tobramycin treatment. The control experiments often hint at other codons also contributing to the observed phenotypes (e.g., His or Asp), yet these effects are mostly ignored in the discussion. It would be helpful to discuss these findings at a minimum in the discussion section, or possibly experimentally address the role of His or Asp by overexpression of these tRNAs together with Tyrosine tRNA(GUA) in an experiment like that of Figure 1I to see if a more "wild type" phenotype would present. In fact, the synergy of Tyr, His, and/or Asp codons likely helps to explain the effects observed with the DNA repair genes in later experiments.

We thank the referee for the suggestion. We agree that there could be synergies between these codons, and that’s probably why proteomics data does not clearly reflect tyrosine codons usage bias. This is now further discussed in the ideas and speculation section. 

Moreover, we have added Figure S3G and the following result:

“Since not all TAT biased proteins are found to be enriched in ∆tgt proteomics data, the sequence context surrounding TAT codons could affect their decoding. To illustrate this, we inserted after the gfp start codon, various tyrosine containing sequences displayed by rsxA (Fig. S3G). The native tyrosines were all TAT codons, our synthetic constructs were either TAT or TAC, while keeping the remaining sequence unchanged.  We observe that the production of GFP carrying the TEYTATLLL sequence from RsxA is increased in Δtgt compared to WT, while it is unchanged with TEYTACLLL. However, production of the GFP with the sequences LYTATRLL/LYTACRLL and EYTATLR/ EYTACLR was not unaffected (or even decreased for the latter) by the absence of tgt. Overall, our results demonstrate that RsxA is upregulated in the ∆tgt strain at the translational level, and that proteins with a codon usage bias towards tyrosine TAT are prone to be more efficiently translated in the absence of Q modification, but this is also dependent on the sequence context. “

(3) Regarding Figure 6D, the APB northern blot feels like an afterthought. It was loaded with different amounts of RNA as input and some samples are repeated three times, but Δcrp only once. Collectively, it makes this experiment very difficult to assess.

A different amount of RNA was used only for ∆tgt in which we have only one band because of the absence of modification. For all the other conditions, the same amount of RNA was used (0.9 µg). Additional replicates of crp were in an additional gel but only a representative gel was shown in the manuscript. This is now specified in the legend.

We also attach below the picture of the gel with total RNA (syber Gold labelling of total RNA), where it can be seen that the lanes contain an equivalent quantity of RNA, except for ∆tgt.

Author response image 4.

Minor Points:

(3) Fig S2B, do the authors have a hypothesis why the Asp and Phe tRNAs lead to a growth decrease in the untreated samples? It appears like Phe(GAA) partially compensates for the defect.

Yes we agree, at this stage we do not have any satisfactory answer for this unfortunately. This would be interesting to study further but this is beyond the scope of the present study.

(5) Lines 655 to 660 seem more appropriate as speculation in the discussion rather than as a conclusion in the results, where no direct experiments are performed. The authors might take advantage of the "Ideas and Speculation" section that eLife allows.

Thank you very much for this suggestion, we added this section to the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor.

- Figure 6 - Fonts on several mutants is different size/type. fixed

- What is the Pm promoter. Please expand and give enough details so reader can follow. Especially as it is less used in V. cholerae (typical being pBAD or pTAC promoters). done

- Spacing where references are inserted should be checked. done

- Line 860-863 - "V. cholerae's response to sub-MIC antibiotic stress is transposable to other Gramnegative pathogens" . This reads awkard. Consider rephrasing. done

- Figure 7 - Text in A and C is very small and is very hard to read. Font for tgt is different.

Fixed. Tgt is in italics.

Reviewer #2 (Recommendations For The Authors):

As specified in the public review, more evidence would be necessary to affirm that tRNAs not modified by Q have a greater preference for translating TAT codons, since there are several previous studies in which it is shown that Q-tRNAs have a greater preference for NAT codons (including TAT). For example, it is suggested to explore what happens with other recoded genes (enriched in TAT or TAC) if there is a high level of Q-tRNAs (overexpression of tgt in a wt context). It is also necessary to clarify how to interpret the Ribo-seq results, which apparently is different from how they have been interpreted in other studies.

Please see above our responses and changes made to the manuscript.

Minor corrections

In Figure 8, replace "Epitranscriptomic adapation to stress" with "Epitranscriptomic adaptation to stress".

Fixed, thank you for noticing!

Reviewer #3 (Recommendations For The Authors):

(1) Lines 48-50, and 110 to 112, the authors have a nice mechanism and story, yet the lines mentioned feel very qualified (e.g., "possibly", "plausibly") and lead to the abstract hiding the value and major conclusions of the study. The authors could consider to revise or even remove these lines to focus on the take-home message in the abstract and end of introduction/discussion. 

Thank you for this comment, we modified the text.  

(2) Additional description for the samples in the results section for Figure 1 would be helpful to the reader.

Done

(3) Figure S1, the line of experiments with rluF is interesting, but in the end the choice seems a little random. Have the authors assessed knockouts of other modifications on the ASL for effects? Since the modification is not well characterized in V. cholerae according to the authors, it might make sense to save this for a future paper.

We removed S1, as we agree that this experiment does not really add something to the paper.

(4) Line 334 and 353 are redundant.

Fixed

(5) It is likely beyond the scope of the study, but it would strengthen the paper to repeat Figure 3 with His and/or Asp based on the findings of 2C and 4E to better understand the contribution of His and Asp to Q biology.

We repeated figure 3 with Asp. Based on Fig 2C (less efficient decoding of GAC in deta-tgt in TOB) and 4E (positive GAT codon bias in proteins up in riboseq in delta-tgt TOB), we would expect that beta-lactamase with asp GAC would be less efficiently decoded than GAT in delta-tgt. 

This was added to the manuscript

“Like Tyr103, Asp129 was shown to be important for resistance to β-lactams (Doucet et al., 2004; Escobar et al., 1994; Jacob et al., 1990). When we replaced the native Asp129 GAT with the synonymous codon Asp129 GAC, the GAC version did not appear to produce functional β-lactamase in ∆tgt (Fig. 3B), suggesting increased mistranslation or inefficient decoding of the GAC codon by tRNAAsp in the absence of Q. Decoding of GAT codon was also affected in ∆tgt in the presence of tobramycin.”

Added figure: Figure 3B

(6) The authors could consider replacing 5D with S4A-D, which is easier to understand in our opinion.

Done

eLife Assessment

This study investigates the role of queuosine (Q) tRNA modification in aminoglycoside tolerance in Vibrio cholerae and presents convincing evidence to conclude that Q is essential for the efficient translation of TAT codons, although this depends on the context. The absence of Q reduces aminoglycoside tolerance potentially by reprogramming the translation of an oxidative stress response gene, rxsA. Overall, the findings point to an important mechanism whereby changes in Q modification levels control the decoding of mRNAs enriched in TAT codons under antibiotic stress.

Reviewer #1 (Public review):

Summary of the work:

In this work Fruchard et. al. study the enzyme Tgt and how it modifies guanine in tRNAs to queuosine (Q), essential for Vibrio cholerae's growth under aminoglycoside stress. Q's role in codon decoding efficiency and its proteomic effects during antibiotic exposure is examined, revealing Q modification impacts tyrosine codon decoding and influences RsxA translation, affecting the SoxR oxidative stress response. The research proposes Q modification's regulation under environmental cues reprograms the translation of genes with tyrosine codon bias, including DNA repair factors, crucial for bacterial antibiotic response.

The experiments are well-designed and conducted and the conclusions, for the most part, are well-supported by the data.

Comments on revisions:

The authors have answered my queries

Reviewer #2 (Public review):

Fruchard et al. investigate the role of the queuosine (Q) modification of the tRNA (Q-tRNA) in the human pathogen Vibrio cholerae. First, the authors state that the absence of Q-modified tRNAs (tgt mutant) increases the translation of TAT codons and proteins with a high TAT codon bias. Second, the absence of Q increases rsxA translation, because rsxA gene has a high TAT codon bias. Third, increased RsxA in the absence of Q inhibits SoxR response, reducing resistance towards the antibiotic tobramycin (TOB). Authors also predict in silico which genes harbor a higher TAT bias and found that among them are some involved in DNA repair, experimentally observing that a tgt mutant is more resistant to UV than the wt strain. It is worth noting that authors employ a wide variety of techniques, both experimental and bioinformatics.

The authors have satisfactorily responded to most of the comments that needed clarification. Particularly interesting was the addition of the new results section "Q modification impacts decoding fidelity in V. cholerae", after the suggestion to explore the role of Q in prevention of stop codon readthrough. Although it is not a major problem, since the article is very complete and interesting, the interpretation of the results of RiboSeq data carried out in this work remains controversial. This technique, at least when it has been used in eukaryotes to investigate whether there is a bias in the translation of certain codons affected by Q (Tuorto et al., EMBO J. 2018; doi: 10.15252/embj.201899777), has been interpreted as meaning that ribosomes spend less time in the optimal codons and therefore there is an increase in occupancy at codons where translation slows down. On the other hand, it has been observed that "in ribosome profiling experiments conducted without cycloheximide pretreatment, there is a clear inverse relationship between tRNA abundance and ribosome occupancy, showing that ribosomes spend less time at optimal codons and specifically this has been observed in experiments in which a translation inhibitor such as cycloheximide is not used (see review: Hanson G & Coller J. Nat Rev Mol Cell Biol. doi: 10.1038/nrm.2017.91, and experiments in yeast: Hussmann JA et al. PLoS Genet. doi: 10.1371/journal.pgen.1005732). On the other hand, we believe that the comparison between RiboSeq and proteomic data would be interesting to check whether this interpretation of the RiboSeq data is correct. It should not be a problem that the proteomics data could be incomplete, it would just be a more limited study. If the correct interpretation of the RiboSeq results is as proposed by the authors, a correlation should be observed between the abundance of TAT-enriched RNA fragments and the most abundant proteins. Therefore, it would be interesting to perform this comparison and see if significant results are obtained that help to understand the correct interpretation of the RiboSeq experiments.

Reviewer #3 (Public review):

Summary:

In this manuscript the authors begin with the interesting phenotype of sub inhibitory concentrations of the aminoglycoside tobramycin proving toxic to a knockout of the tRNA-guanine transglycosylase (Tgt) of the important human pathogen, Vibrio cholerae. Tgt is important for incorporating queuosine (Q) in place of guanosine at the wobble position of GUN codons. The authors go on to define a mechanism of action where environmental stressors control expression of tgt to control translational decoding of particularly tyrosine codons, skewing the balance from TAC towards TAT decoding in the absence of the enzyme. The authors use advanced proteomics and ribosome profiling to reveal that the loss of tgt results in increased translation of proteins like RsxA and a cohort of DNA repair factors, whose genes harbor an excess of TAT codons in many cases. These findings are bolstered by a series of molecular reporters, mass spectrometry, and tRNA overexpression strains to provide support for a model where Tgt serves as a molecular pivot point to reprogram translational output in response to stress. The manuscript therefore improves our understanding of the phenotype of focus and will prove useful for the field in our understanding of Modification Tunable Transcripts.

Strengths:

The manuscript has many strengths. The authors use a variety of strains, assays, and advanced techniques to discover a mechanism of action for Tgt in mediating tolerance to sub inhibitory concentrations of tobramycin. They observe a clear phenotype for a tRNA modification in facilitating reprogramming of the translational response, and the manuscript certainly has value in defining how microbes tolerate antibiotics.

Weaknesses:

The conclusions of the manuscript are mostly very well-supported by the data, but a few experimental directions remain inconclusive. The finding linking Tgt and UV damage susceptibility is one example where the phenotype is striking, but the mechanism remains somewhat unclear. Future work in this direction will likely be required to fully understand how Tgt influences the repair of DNA after UV.

eLife Assessment

The study highlights adhesion G-protein-coupled receptor A3 (ADGRA3) as a potential target for activating adaptive thermogenesis in both white and brown adipose tissue. This finding offers valuable insights for researchers in the field of adipose tissue biology and metabolism. The authors have presented additional evidence to address the reviewers' comments, including experiments conducted on primary stromal vascular fractions from adipose tissues. However, the revised manuscript fails to address several reviewer concerns, such as the measurement of whole-body energy expenditure through indirect calorimetry and the assessment of food intake. Furthermore, the nanoparticle-mediated knockdown of Adgra3 did not adequately address the tissue selectivity of ADGRA in mice. As a result, the primary claims of the study are only partially supported by the available data, leading to the conclusion that the research is deemed incomplete.

Joint Public Review:

Based on bioinformatics and expression analysis using mouse and human samples, the authors claim that the adhesion G-protein coupled receptor ADGRA3 may be a valuable target for increasing thermogenic activity and metabolic health. Genetic approaches to deplete ADGRA3 expression in vitro resulted in reduced expression of thermogenic genes including Ucp1, reduced basal respiration and metabolic activity as reflected by reduced glucose uptake and triglyceride accumulation. In line, nanoparticle delivery of shAdgra3 constructs is associated with increased body weight, reduced thermogenic gene expression in white and brown adipose tissue (WAT, BAT), and impaired glucose and insulin tolerance. On the other hand, ADGRA3 overexpression is associated with an improved metabolic profile in vitro and in vivo, which can be explained by increasing the activity of the well-established Gs-PKA-CREB axis. Notably, a computational screen suggested that ADGRA3 is activated by hesperetin. This metabolite is a derivative of the major citrus flavonoid hesperidin and has been described to promote metabolic health. Using appropriate in vitro and in vivo studies, the authors show that hesperitin supplementation is associated with increased thermogenesis, UCP1 levels in WAT and BAT, and improved glucose tolerance, an effect that was attenuated in the absence of ADGRA3 expression.

The revised manuscript fails to address several reviewer concerns, such as the measurement of whole-body energy expenditure through indirect calorimetry and the assessment of food intake.

The previous reviews are here: https://elifesciences.org/reviewed-preprints/100205v2/reviews#tab-content

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This article identifies ADGR3 as a candidate GPCR for mediating beige fat development. The authors use human expression data from Human Protein Atlas and Gtex databases and combine this with experiments performed in mice and a murine cell line. They refer to a GPCR bioactivity screening tool PRESTO-Salsa, with which it was found that Hesperetin activates ADGR3. From their experiments, authors conclude that Hesperetin activates ADGR3, inducing a Gs-PKA-CREB axis resulting in adipose thermogenesis.

Strengths:

The authors analyze human data from public databases and perform functional studies in mouse models. They identify a new GPCR with a role in thermogenic activation of adipocytes.

Considerations:

Selection of ADGRA3 as a candidate GPCR relevant for mediating beiging in humans:

The authors identify GPCRs that are expressed more highly in murine iBAT compared to iWAT in response to cold and assess which of these GPCRs are expressed in human subcutaneous or visceral adipocytes. Although this strategy will identify GPCRs that are expressed at higher levels in brown fat compared to beige and thus possibly more active in thermogenic function, the relevance in choosing GPCRs that also are expressed in unstimulated human white adipocytes should be considered. Thermogenic activity is not normally present in human white adipocytes. It would have strengthened the GPCR selection if the authors instead had assessed the intersection with human brown adipocytes that were activated with norepinephrine.

We appreciate your constructive feedback and believe that by adopting this refined strategy, we will strengthen our selection of GPCRs related to adipose thermogenesis in other ongoing studies. We look forward to continuing our research in this area and contributing to the understanding of adipose thermogenesis and its potential therapeutic applications. Thank you once again for your valuable input. 

Strategy to investigate the role of ADGRA3 in WAT beiging:

Having identified ADGRA3 as their candidate receptor, the authors investigated the receptor in mouse models, the murine inguinal adipocyte cell line 3T3 and in human subcutaneous adipose progenitors (HAdsc) differentiated in vitro. Calling the human cells "beige" is a stretch as these cells are derived from a white adipose depot. The authors do observe regulation in UCP1 and abundance of mitochondria following modification of ADGRA3 in the cells. However, in future studies, it should be considered if the receptor rather plays a role in differentiation per se, and perhaps not specifically in thermogenic differentiation/activity.

Regarding the reviewer's suggestion to consider whether ADGRA3 plays a role in differentiation per se, rather than specifically in thermogenic differentiation/activity, we acknowledge that this is an important consideration. Our current studies have focused on the role of ADGRA3 in regulating UCP1 expression and mitochondrial abundance, which are hallmarks of adipose thermogenic activity. However, we recognize that ADGRA3 may also have broader roles in adipocyte differentiation and function that are not limited to thermogenesis.

To address this point, in future studies, we plan to conduct additional experiments to investigate the potential role of ADGRA3 in adipocyte differentiation, including its effects on the expression of markers of adipocyte differentiation and its impact on adipocyte metabolism and function. These studies will provide further insights into the mechanisms by which ADGRA3 regulates adipocyte biology.

According to the Human Protein Atlas and Gtex databases, ADGRA3 is not only expressed in adipocytes, but also in other tissues and cell types. The authors address this by measuring the expression in a panel of these tissues, demonstrating a knockdown not only in the adipose tissue, but also in the liver and less pronounced in the muscle (Figure S2). It should thus be emphasized that the decreased TG levels in serum and liver in the mice might in fact depend on Adgra3 overexpression in the liver. Even though this might not have been the purpose of the experiment, it is important to highlight this as it could serve as hypothesis building for future studies of the function of this receptor.

Thank you for your thoughtful comments and feedback. We appreciate the insight provided by the Human Protein Atlas and Gtex databases regarding the tissue distribution of ADGRA3. We fully acknowledge that the decreased TG levels observed in both the serum and liver of the mice might be linked to the overexpression of Adgra3 in the liver.

Although this was not the primary objective of our experiment, we agree that this observation is worth highlighting as it could serve as a basis for future hypothesis-driven research on the functional role of ADGRA3 in different tissues. In light of your comments, we emphasized this potential link between Adgra3 overexpression in the liver and reduced TG levels in discussion, as follows.

“…the precise mechanisms underlying the influence of on adipose thermogenesis. Furthermore, it is crucial to highlight that the observed decrease in TG levels in both serum and liver (Figure 4-figure supplement 2C-D) might be attributed to the significant increase in Adgra3 expression in the liver, which is a consequence of the nanoparticle-mediated overexpression of Adgra3. While the exact mechanism remains to be fully elucidated, this correlation suggests a potential link between Adgra3 overexpression in the liver and reduced TG levels in the serum. We will employ more sophisticated models in subsequent studies to further…”

Reviewer #3 (Public Review):

Summary:

The manuscript by Zhao et al. explored the function of adhesion G protein-coupled receptor A3 (ADGRA3) in thermogenic fat biology.

Strengths:

Through both in vivo and in vitro studies, the authors found that the gain function of ADGRA3 leads to browning of white fat and ameliorates insulin resistance.

Weaknesses:

There are several lines of weak methodologies such as using 3T3-L1 adipocytes and intraperitoneal(i.p.) injection of virus. Moreover, as the authors stated that ADGRA3 is constitutively active, how could the authors then identify a chemical ligand?

Comments on revised version:

The revised manuscript by Zhao et al. has limited improvement. The authors refused to perform revised experiments using primary cultures even though two reviewers pointed out the same weakness (3T3-L1 adipocytes are unsuitable). Using infrared thermography to measure body temperature is also problematic.

Thanks for your comments. We regret that human adipocytes induced from human adipose-derived stem cells (hADSCs) were not recognized as primary cultures by multiple reviewers. Therefore, we have included relevant experimental results of mouse primary adipocytes induced from stromal vascular fraction (SVF) in Figure 8E-H as a supplement. The thermal imaging device was used to measure the temperature of BAT, while the body temperature was measured at 9:00 using a rectal probe connected to a digital thermometer.

eLife Assessment

This important study represents a data processing pipeline to discover causal interactions from time-lapse imaging data, and convincingly illustrates it on a challenging application for the analysis of tumor-on-chip ecosystem data. The authors describe the raw data they used (imaging data), go through a step-by-step description on how to extract the features they are interested in from the raw data, and how to perform the causal discovery process. This paper tackles the problem of learning causal interactions from temporal data, which is applicable to many biological applications.

Reviewer #1 (Public review):

Summary:

This paper presents a data processing pipeline to discover causal interactions from time-lapse imaging data and convincingly illustrates it on a challenging application for the analysis of tumor-on-chip ecosystem data.

The core of the discovery module is the original tMIIC method of the authors, which is shown in supplementary material to compare favourably to two state-of-the-art methods on synthetic temporal data on a 15 nodes network.

Strengths:

This paper tackles the problem of learning causal interactions from temporal data which is an open problem in presence of latent variables.

The core of the method tMIIC of the authors is nicely presented in connection to Granger-Schreiber causality and to the novel graphical conditions used to infer latent variables and based on a theorem about transfer entropy.

tMIIC compares favourably to PC and PCMCI+ methods using different kernels on synthetic datasets generated from a network of 15 nodes.

A full application to tumor-on-chip cellular ecosystems data including cancer cells, immune cells, cancer-associated fibroblasts, endothelial cells and anti cancer drugs, with convincing inference results with respect to both known and novel effects between those components and their contact.

The code and dataset are available online for the reproducibility of the results.

Weaknesses:

The references to "state-of-the-art methods" concerning the inference of causal networks should be more precise by giving citations in the main text, and better discussed in general terms, both in the first section and in the section of presentation of CausalXtract. It is only in the legend of the figures of the supplementary material that we get information.

Of course, comparison on our own synthetic datasets can always be criticized but this is rather due to the absence of a common benchmark in this domain compared to other domains. I recommend the authors to explicitly propose their datasets made accessible in supplementary material as benchmark for the community.

Comments on revisions:

This is a very nice paper.

Reviewer #2 (Public review):

Summary:

The authors propose a methodology to perform causal (temporal) discovery. The approach appears to be robust and is tested in the different scenarios: one related to live-cell imaging data, and another one using synthetic (mathematically defined) time series data. They compare the performance of their findings against another well-known method by using metrics like F-score, precision and recall,

Strengths:

--Performance, robustness, the text is clear and concise, The authors provide the code to review.

Comments on revisions:

The authors have addressed my concerns properly providing the needed explanations.

Author response:

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

Reviewer #1 (Public review):

Summary:

This paper presents a data processing pipeline to discover causal interactions from time-lapse imaging data, and convicingly illustrates it on a challenging application for the analysis of tumor-on-chip ecosystem data. The core of the discovery module is the original tMIIC method of the authors, which is shown in supplementary material to compare favourably to two state-of-the-art methods on synthetic temporal data on a 15 nodes network.

Strengths:

This paper tackles the problem of learning causal interactions from temporal data which is an open problem in presence of latent variables. The core of the method tMIIC of the authors is nicely presented in connection to Granger- Schreiber causality and to the novel graphical conditions used to infer latent variables and based on a theorem about transfer entropy. tMIIC compares favourably to PC and PCMCI+ methods using different kernels on synthetic datasets generated from a network of 15 nodes. A full application to tumor-onchip cellular ecosystems data including cancer cells, immune cells, cancer-associated fibroblasts, endothelial cells and anti cancer drugs, with convincing inference results with respect to both known and novel effects between those components and their contact.

The code and dataset are available online for the reproducibility of the results.

We thank Reviewer #1 for highlighting the main results and strengths of our paper, as well as, for his/her recommendations below to further improve the manuscript.

Weaknesses:

The references to ”state-of-the-art methods” concerning the inference of causal networks should be more precise by giving citations in the main text, and better discussed in general terms, both in the first section and in the section of presentation of CausalXtract. It is only in the legend of the figures of the supplementary material that we get information. Of course, comparison on our own synthetic datasets can always be criticized but this is rather due to the absence of common benchmark and I would recommend the authors to explicitly propose their datasets as benchmark to the community.

Following Reviewer #1’s suggestion, we now compare tMIIC’s performance to other state-of-the-art causal discovery methods for time series data in the main text and in a new Figure 2. This Figure 2 also highlights the relation between graph-based causal discovery methods for time series data and Granger-Schreiber temporal causality, as discussed in more details in Methods (Theorem 1).

We also agree about the importance of sharing benchmark datasets with the community. This is the reason why we provide the dynamical equations of the 15-node benchmarks in Supplementary Tables 1 & 2, so that anyone can generate equivalent time series datasets of any desired length.

Reviewer #2 (Public review):

Summary:

The authors propose a methodology to perform causal (temporal) discovery. The approach appears to be robust and is tested in the different scenarios: one related with live-cell imaging data, and another one using synthetic (mathematically defined) time series data. They compare the performance of their findings against another well-know method by using metrics like F-score, precision and recall,

Strengths:

Performance, robustness, the text is clear and concise, The authors provide the code to review.

We thank Reviewer #2 for his/her positive assessment of our work and the suggestions below to improve the manuscript.

Weaknesses:

One concern could be the applicability of the method in other areas like climate, economy. For those areas, public data are available and might be interesting to test how the method performs with this kind of data.

While our main expertise concerns the analysis of biological and biomedical data, we agree that tMIIC (which is included in MIIC R package) could in principle be applied to other areas, like climate, economy.

We have not included benchmarks on such diverse types of datasets in the present manuscript, which focuses on CausalXtract’s pipeline for the analysis and causal interpretation of live-cell time-lapse imaging data from complex cellular systems.

Author response:

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

Reviewer 1:

We thank Reviewer 1 for their helpful comments and hope that the changes made to the revised manuscript have addressed their points.

This study presents a novel application of the inverted encoding (i.e., decoding) approach to detect the correlates of crossmodal integration in the human EEG (electrophysiological) signal. The method is successfully applied to data from a group of 41 participants, performing a spatial localization task on auditory, visual, and audiovisual events. The analyses clearly show a behavioural superiority for audio-visual localization. Like previous studies, the results when using traditional univariate ERP analyses were inconclusive, showing once more the need for alternative, more sophisticated approaches. Instead, the principal approach of this study, harnessing the multivariate nature of the signal, captured clear signs of super-additive responses, considered by many as the hallmark of multisensory integration. Unfortunately, the manuscript lacks many important details in the descriptions of the methodology and analytical pipeline. Although some of these details can eventually be retrieved from the scripts that accompany this paper, the main text should be self-contained and sufficient to gain a clear understanding of what was done. (A list of some of these is included in the comments to the authors). Nevertheless, I believe the main weakness of this work is that the positive results obtained and reported in the results section are conditioned upon eye movements. When artifacts due to eye movements are removed, then the outcomes are no longer significant. 

Therefore, whether the authors finally achieved the aims and showed that this method of analysis is truly a reliable way to assess crossmodal integration, does not stand on firm ground. The worst-case scenario is that the results are entirely accounted for by patterns of eye movements in the different conditions. In the best-case scenario, the method might truly work, but further experiments (and/or analyses) would be required to confirm the claims in a conclusive fashion.

One first step toward this goal would be, perhaps, to facilitate the understanding of results in context by reporting both the uncorrected and corrected analyses in the main results section. Second, one could try to support the argument given in the discussion, pointing out the origin of the super-additive effects in posterior electrode sites, by also modelling frontal electrode clusters and showing they aren't informative as to the effect of interest.

We performed several additional analyses to address concerns that our main result was caused by different eye movement patterns between conditions. We re-ran our key analyses using activity exclusively from frontal electrodes, which revealed poorer decoding performance than that from posterior electrodes. If eye movements were driving the non-linear enhancement in the audiovisual condition, we would expect stronger decoding using sensors closer to the source, i.e., the extraocular muscles. We also computed the correlations between average eye position and stimulus position for each condition to evaluate whether participants made larger eye movements in the audiovisual condition, which might have contributed to better decoding results. Though we did find evidence for eye movements toward stimuli, the degree of movement did not significantly differ between conditions.

Furthermore, we note that the analysis using a stricter eye movement criterion, acknowledged in the Discussion section of the original manuscript, resulted in very similar results to the original analysis. There was significantly better decoding in the AV condition (as measured by d') than the MLE prediction, but this difference did not survive cluster correction. The most likely explanation for this is that the strict eye movement criterion combined with our conservative measure of (mass-based) cluster correction led to reduced power to detect true differences between conditions. Taken together with the additional analyses described in the revised manuscript and supplementary materials, the results show that eye movements are unlikely to account for differences between the multisensory and unisensory conditions. Instead, our decoding results likely reflect nonlinear neural integration between audio and visual sensory information.

“Any experimental design that varies stimulus location needs to consider the potential contribution of eye movements. We computed correlations between participants’ average eye position and each stimulus position between the three sensory conditions (auditory, visual and audiovisual; Figure S1) and found evidence that participants made eye movements toward stimuli. A re-analysis of the data with a very strict eye-movement criterion (i.e., removing trials with eye movements >1.875º) revealed that the super-additive enhancement in decoding accuracy no longer survived cluster correction, suggesting that our results may be impacted by the consistent motor activity of saccades towards presented stimuli. Further investigation, however, suggests this is unlikely. Though the correlations were significantly different from 0, they were not significantly different from each other. If consistent saccades to audiovisual stimuli were responsible for the nonlinear multisensory benefit we observed, we would expect to find a higher positive correlation between horizontal eye position and stimulus location in the audiovisual condition than in the auditory or visual conditions. Interestingly, eye movements corresponded more to stimulus location in the auditory and audiovisual conditions than in the visual condition, indicating that it was the presence of a sound, rather than a visual stimulus, that drove small eye movements. This could indicate that participants inadvertently moved their eyes when localising the origin of sounds. We also re-ran our analyses using the activity measured from the frontal electrodes alone (Figure S2). If the source of the nonlinear decoding accuracy in the audiovisual condition was due to muscular activity produced by eye movements, there should be better decoding accuracy from sensors closer to the source. Instead, we found that decoding accuracy of stimulus location from the frontal electrodes (peak d' = 0.08) was less than half that of decoding accuracy from the more posterior electrodes (peak d' = 0.18). These results suggest that the source of neural activity containing information about stimulus position was located over occipito-parietal areas, consistent with our topographical analyses (inset of Figure 3).” 

The univariate ERP analyses an outdated contrast, AV <> A + V to capture multisensory integration. A number of authors have pointed out the potential problem of double baseline subtraction when using this contrast, and have recommended a number of solutions, experimental and analytical. See for example: [1] and [2]. 

(1) Teder-Salejarvi, W. A., McDonald, J. J., Di Russo, F., & Hillyard, S. A. (2002). Cognitive Brain Research, 14, 106-114. 

(2) Talsma, D., & Woldorff, M. G. (2005). Journal of cognitive neuroscience, 17(7), 1098-1114.

We thank the reviewer for raising this point. Comparing ERPs across different sensory conditions requires careful analytic choices to discern genuine sensory interactions within the signal. The AV <> (A +V) contrast has often been used to detect multisensory integration, though any non-signal related activity (i.e. anticipatory waves; Taslma & Woldorff, 2005) or pre-processing manipulation (e.g. baseline subtraction; Teder-Sälejärvi et al., 2002) will be doubled in (A + V) but not in AV. Critically, we did not apply a baseline correction during preprocessing and thus our results are not at risk of double-baseline subtraction in (A + V). Additionally, we temporally jittered the presentation of our stimuli to mitigate the potential influence of consistent overlapping ERP waves (Talsma & Woldorff, 2005). 

The results section should provide the neurometric curve/s used to extract the slopes of the sensitivity plot (Figure 2B). 

We thank the reviewer for raising this point of clarification. The sensitivity plots for Figures 2B and 2C were extracted from the behavioural performance of the behavioural and EEG tasks, respectively. The sensitivity plot for Figure 2B was extracted from individual psychometric curves, whereas the d’ values for Figure 2C were calculated from the behavioural data for the EEG task. This information has been clarified in the manuscript.

“Figure 1. Behavioural performance is improved for audiovisual stimuli. A) Average accuracy of responses across participants in the behavioural session at each stimulus location for each stimulus condition, fitted to a psychometric curve. Steeper curves indicate greater sensitivity in identifying stimulus location. B) Average sensitivity across participants in the behavioural task, estimated from psychometric curves, for each stimulus condition. The red cross indicates estimated performance assuming optimal (MLE) integration of unisensory cues. C) Average behavioural sensitivity across participants in the EEG session for each stimulus condition. Error bars indicate ±1 SEM.”

The encoding model was fitted for each electrode individually; I wonder if important information contained as combinations of (individually non-significant) electrodes was then lost in this process and if the authors consider that this is relevant. 

Although the encoding model was fitted for each electrode individually for the topographic maps (Figure 4B), in all other analyses the encoding model was fitted across a selection of electrodes (see final inset of Figure 3). As this electrode set was used for all other neural analyses, our model would allow for the detection of important information contained in the neural patterns across electrodes. This information has been clarified in the manuscript.

“Thus, for all subsequent analyses we only included signals from the central-temporal, parietal-occipital, occipital and inion sensors for computing the inverse model (see final inset of Figure 2). As the model was fitted for multiple electrodes, subtle patterns of neural information contained within combinations of sensors could be detected.”

Neurobehavioral correlations could benefit from outlier rejection and the use of robust correlation statistics. 

We thank the reviewer for raising this issue. Note, however, that the correlations we report are resistant to the influence of outliers because we used Spearman’s rho1 (as opposed to Pearson’s). This information has been communicated in the manuscript.

(1) Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069

“Neurobehavioural correlations. As behavioural and neural data violated assumptions of normality, we calculated rank-order correlations (Spearman’s rho) between the average decoding sensitivity for each participant from 150-250 ms poststimulus onset and behavioural performance on the EEG task. As Spearman’s rho is resistant to outliers (Wilcox, 2016), we did not perform outlier rejection.”

“Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069”

Many details that are important for the reader to evaluate the evidence and to understand the methods and analyses aren't given; this is a non-exhaustive list:  

We thank the reviewer for highlighting these missing details. We have updated the manuscript where necessary to ensure the methods and analyses are fully detailed and replicable.

- specific parameters of the stimuli and performance levels. Just saying "similarly difficult" or "marginally higher volume" is not enough to understand exactly what was done.  

“The perceived source location of auditory stimuli was manipulated via changes to interaural level and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992). The precise timing of when each speaker delivered an auditory stimulus was calculated from the following formula:

where x and z are the horizontal and forward distances in metres between the ears and the source of the sound on the display, respectively, r is the head radius, and s is the speed of sound. We used a constant approximate head radius of 8 cm for all participants. r was added to x for the left speaker and subtracted for the right speaker to produce the interaural time difference. For ±15° source locations, interaural timing difference was 1.7 ms. To simulate the decrease in sound intensity as a function of distance, we calculated interaural level differences for the left and right speakers by dividing the sounds by the left and right distance vectors. Finally, we resampled the sound using linear interpolation based on the calculations of the interaural level and timing differences. This process was used to calculate the soundwaves played by the left and right speakers for each of the possible stimulus locations on the display. The maximum interaural level difference between speakers was 0.14 A for ±15° auditory locations, and 0.07 A for ±7.5°.”

- where are stimulus parameters adjusted individually or as a group? Which method was followed?  

To clarify, stimulus parameters (frequency, size, luminance, volume, location, etc.) were manipulated throughout pilot testing only. Parameters were adjusted to achieve similar pilot behavioural results between the auditory and visual conditions. For the experiment proper, parameters remained constant for both tasks and were the same for all participants.

“During pilot testing, stimulus features (size, luminance, volume, frequency etc.) were manipulated to make visual and auditory stimuli similarly difficult to spatially localize. These values were held constant in the main experiment.”

- specify which response buttons were used.

“Participants were presented with two consecutive stimuli and tasked with indicating, via button press, whether the first (‘1’ number-pad key) or second (‘2’ number-pad key) interval contained the more leftward stimulus.”

“At the end of each sequence, participants were tasked with indicating, via button press, whether more presentations appeared on the right (‘right’ arrow key) or the left (‘left’ arrow key) of the display.”

- no information is given as to how many trials per condition remained on average, for analysis.  

The average number of remaining trials per condition after eye-movement analysis is now included in the Methods section of the revised manuscript.

“We removed trials with substantial eye movements (>3.75 away from fixation) from the analyses. After the removal of eye movements, on average 2365 (SD \= 56.94), 2346 (SD \= 152.87) and 2350 (SD \= 132.47) trials remained for auditory, visual and audiovisual conditions, respectively, from the original 2400 per condition.”

- no information is given on the specifics of participant exclusion criteria. (even if the attrition rate was surprisingly high, for such an easy task).  

The behavioural session also served as a screening task. Although the task instructions were straightforward, perceptual discrimination was not easy due to the ambiguity of the stimuli. Auditory localization is not very precise, and the visual stimuli were brief, dim, and diffuse. The behavioural results reflect the difficulty of the task. Attrition rate was high as participants who scored below 60% correct in any condition were deemed unable to accurately perform the task, were not invited to complete the subsequent EEG session, and omitted from the analyses. We have included the specific criteria in the manuscript.

“Participants were first required to complete a behavioural session with above 60% accuracy in all conditions to qualify for the EEG session (see Behavioural session for details).”

- EEG pre-processing: what filter was used? How was artifact rejection done? (no parameters are reported); How were bad channels interpolated?  

We used a 0.25 Hz high-pass filter to remove baseline drifts, but no low-pass filter. In line with recent studies on the undesirable influence of EEG preprocessing on ERPs1, we opted to avoid channel interpolation and artifact rejection. This was erroneously reported in the manuscript and has now been clarified. For the sake of clarity, here we demonstrate that a reanalysis of data using channel interpolation and artifact rejection returned the same pattern of results. 

(1) Delorme, A. (2023). EEG is better left alone. Scientific Reports, 13, 2372. https://doi.org/10.1038/s41598-023-27528-0

- specific electrode locations must be given or shown in a plot (just "primarily represented in posterior electrodes" is not sufficiently informative).  

A diagram of the electrodes used in all analyses is included within Figure 3, and we have drawn readers’ attention to this in the revised manuscript.

“Thus, for all subsequent analyses we only included signals from the central-temporal, parietal-occipital, occipital and inion sensors for computing the inverse model (see final inset of Figure 2).” 

- ERP analysis: which channels were used? What is the specific cluster correction method?

We used a conservative mass-based cluster correction from Pernet et al. (2015) - this information has been clarified in the manuscript.

“A conservative mass-based cluster correction was applied to account for spurious differences across time (Pernet et al., 2015).” 

“Pernet, C. R., Latinus, M., Nichols, T. E., & Rousselet, G. A. (2015). Cluster-based computational methods for mass univariate analyses of event-related brain potentials/fields: A simulation study. Journal of Neuroscience Methods, 250, 85-93. https://doi.org/https://doi.org/10.1016/j.jneumeth.2014.08.003” 

- results: descriptive stats on performance must be given (instead of saying "participants performed well").  

The mean and standard deviation of participants’ performance for each condition in the behavioural and EEG experiments are now explicitly mentioned in the manuscript.

“A quantification of the behavioural sensitivity (i.e., steepness of the curves) revealed significantly higher sensitivity for the audiovisual stimuli (M = .04, SD = .02) than for the auditory stimuli alone (M = .03, SD = .01; Z = -3.09, p = .002), and than for the visual stimuli alone (M = .02, SD = .01; Z = -5.28, p = 1.288e-7; Figure 1B). Sensitivity for auditory stimuli was also significantly higher than sensitivity for visual stimuli (Z = 2.02, p = .044).” 

“We found a similar pattern of results to those in the behavioural session; sensitivity for audiovisual stimuli (M = .85, SD = .33) was significantly higher than for auditory (M = .69, SD = .41; Z = -2.27, p = .023) and visual stimuli alone (M = .61, SD = .29; Z = -3.52, p = 4.345e-4), but not significantly different from the MLE prediction (Z = -1.07, p = .285).” 

- sensitivity in the behavioural and EEG sessions is said to be different, but no comparison is given. It is not even the same stimulus set across the two tasks...  

This relationship was noted as a potential explanation for the higher sensitivities obtained in the EEG task, and was not intended to stand up to statistical scrutiny. We agree it makes little sense to compare statistically between the EEG and behavioural results as they were obtained from different tasks. We would like to clarify, however, that the stimuli used in the two tasks were the same, with the exception that in the EEG task the stimuli were presented from 5 locations versus 8 in the behavioural task. To avoid potential confusion, we have removed the offending sentence from the manuscript:

Reviewer 2:

Their measure of neural responses is derived from the decoder responses, and this takes account of the reliability of the sensory representations - the d' statistics - which is an excellent thing. It also means if I understand their analysis correctly (it could bear clarifying - see below), that they can generate from it a prediction of the performance expected if an optimal decision is made combining the neural signals from the individual modalities. I believe this is the familiar root sum of squares d' calculation (or very similar). Their decoding of the audiovisual responses comfortably exceeds this prediction and forms part of the evidence for their claims. 

Yet, superadditivity - including that in evidence in the principle of inverse effectiveness more typically quantifies the excess over the sum of proportions correct in each modality. Their MLE d' statistic can already predict this form of superadditivity. Therefore, the superadditivity they report here is not the same form of superadditivity that is usually referred to in behavioural studies. It is in fact a stiffer definition. What their analysis tests is that decoding performance exceeds what would be expected from an optimally weighted linear integration of the unisensory information. As this is not the common definition it is difficult to relate to behavioral superadditivity reported in much literature (of percentage correct). This distinction is not at all clear from the manuscript. 

But the real puzzle is here: The behavioural data or this task do not exceed the optimal statistical decision predicted by signal detection theory (the MLE d'). Yet, the EEG data would suggest that the neural processing is exceeding it. So why, if the neural processing is there to yield better performance is it not reflected in the behaviour? I cannot explain this, but it strikes me that the behaviour and neural signals are for some reason not reflecting the same processing. 

Be explicit and discuss this mismatch they observe between behaviour and neural responses. 

Thank you, we agree that it is worth expanding on the observed disconnect between MSI in behaviour and neural signals. We have included an additional paragraph in the Discussion of the revised manuscript. Despite the mismatch, we believe the behavioural and neural responses still reflect the same underlying processing, but at different levels of sensitivity. The behavioural result likely reflects a coarse down-sampling of the precision in location representation, and thus less likely to reflect subtle MSI enhancements.

“An interesting aspect of our results is the apparent mismatch between the behavioural and neural responses. While the behavioural results meet the optimal statistical threshold predicted by MLE, the decoding analyses suggest that the neural response exceeds it. Though non-linear neural responses and statistically optimal behavioural responses are reliable phenomena in multisensory integration (Alais & Burr, 2004; Ernst & Banks, 2002; Stanford & Stein, 2007), the question remains – if neural super-additivity exists to improve behavioural performance, why is it not reflected in behavioural responses? A possible explanation for this neurobehavioural discrepancy is the large difference in timing between sensory processing and behavioural responses. A motor response would typically occur some time after the neural response to a sensory stimulus (e.g., 70-200 ms), with subsequent neural processes between perception and action that introduce noise (Heekeren et al., 2008) and may obscure super-additive perceptual sensitivity. In the current experiment, participants reported either the distribution of 20 serially presented stimuli (EEG session) or compared the positions of two stimuli (behavioural session), whereas the decoder attempts to recover the location of every presented stimulus. While stimulus location could be represented with higher fidelity in multisensory relative to unisensory conditions, this would not necessarily result in better performance on a binary behavioural task in which multiple temporally separated stimuli are compared. One must also consider the inherent differences in how super-additivity is measured at the neural and behavioural levels. Neural super-additivity should manifest in responses to each individual stimulus. In contrast, behavioural super-additivity is often reported as proportion correct, which can only emerge between conditions after being averaged across multiple trials. The former is a biological phenomenon, while the latter is an analytical construct. In our experiment, we recorded neural responses for every presentation of a stimulus, but behavioural responses were only obtained after multiple stimulus presentations. Thus, the failure to find super-additivity in behavioural responses might be due to their operationalisation, with between-condition comparisons lacking sufficient sensitivity to detect super-additive sensory improvements. Future work should focus on experimental designs that can reveal super-additive responses in behaviour.”

Re-work the introduction to explain more clearly the relationship between the behavioural superadditivities they review, the MLE model, and the superadditivity it actually tests. 

We agree it is worth discussing how super-additivity is operationalised across neural and behavioural measures. However, we do not believe the behavioural studies we reviewed claimed super-additive behavioural enhancements. While MLE is often used as a behavioural marker of successful integration, it is not necessarily used as evidence for super-additivity within the behavioural response, as it relies on linear operations. 

“It is important to consider the differences in how super-additivity is classified between neural and behavioural measures. At the level of single neurons, superadditivity is defined as a non-linear response enhancement, with the multisensory response exceeding the sum of the unisensory responses. In behaviour, meanwhile, it has been observed that the performance improvement from combining two senses is close to what is expected from optimal integration of information across the senses (Alais & Burr, 2004; Stanford & Stein, 2007). Critically, behavioural enhancement of this kind does not require non-linearity in the neural response, but can arise from a reliability-weighted average of sensory information. In short, behavioural performance that conforms to MLE is not necessarily indicative of neural super-additivity, and the MLE model can be considered a linear baseline for multisensory integration.”

Regarding the auditory stimulus, this reviewer notes that interaural time differences are unlikely to survive free field presentation.

Despite the free field presentation, in both the pilot test and the study proper participants were able to localize auditory stimuli significantly above chance. 

"However, other studies have found super-additive enhancements to the amplitude of sensory event-related potentials (ERPs) for audiovisual stimuli (Molholm et al., 2002; Talsma et al., 2007), especially when considering the influence of stimulus intensity (Senkowski et al., 2011)." - this makes it obvious that there are some studies which show superadditivity. It would have been good to provide a little more depth here - as to what distinguished those studies that reported positive effects from those that did not.

We have provided further detail on how super-additivity appears to manifest in neural measures.

“In EEG, meanwhile, the evoked response to an audiovisual stimulus typically conforms to a sub-additive principle (Cappe et al., 2010; Fort et al., 2002; Giard & Peronnet, 1999; Murray et al., 2016; Puce et al., 2007; Stekelenburg & Vroomen, 2007; Teder- Sälejärvi et al., 2002; Vroomen & Stekelenburg, 2010). However, when the principle of inverse effectiveness is considered and relatively weak stimuli are presented together, there has been some evidence for super-additive responses (Senkowski et al., 2011).”

“While behavioural outcomes for multisensory stimuli can be predicted by MLE, and single neuron responses follow the principles of inverse effectiveness and super- additivity, among others (Rideaux et al., 2021), how audiovisual super-additivity manifests within populations of neurons is comparatively unclear given the mixed findings from relevant fMRI and EEG studies. This uncertainty may be due to biophysical limitations of human neuroimaging techniques, but it may also be related to the analytic approaches used to study these recordings. For instance, superadditive responses to audiovisual stimuli in EEG studies are often reported from very small electrode clusters (Molholm et al., 2002; Senkowski et al., 2011; Talsma et al., 2007), suggesting that neural super-additivity in humans may be highly specific. However, information encoded by the brain can be represented as increased activity in some areas, accompanied by decreased activity in others, so simplifying complex neural responses to the average rise and fall of activity in specific sensors may obscure relevant multivariate patterns of activity evoked by a stimulus.”

P9. "(25-75 W, 6 Ω)." This is not important, but it is a strange way to cite the power handling of a loudspeaker. 

“The loudspeakers had a power handling capacity of 25-75 W and a nominal impedance of 6 Ω.” 

I am struggling to understand the auditory stimulus: 

"Auditory stimuli were 100 ms clicks". Is this a 100-ms long train of clicks? A single pulse which is 100ms long would not sound like a click, but two clicks once filtered by the loudspeaker. Perhaps they mean 100us. 

"..with a flat 850 Hz tone embedded within a decay envelope". Does this mean the tone is gated - i.e. turns on and off slowly? Or is it constant?

We thank the reviewer for catching this. ‘Click’ may not be the most apt way of defining the auditory stimulus. It was a 100 ms square wave tone with decay, i.e., with an onset at maximal volume before fading gradually. Given that the length of the stimulus was 100 ms, the decay occurs quickly and provides a more ‘click-like’ percept than a pure tone. We have provided a representation of the sound below for further clarification. This represents the amplitude from the L and R speakers for maximally-left and maximally-right stimuli. We have added this clarification in the revised manuscript. 

Author response image 1.

“Auditory stimuli were 100 ms, 850 Hz tones with a decay function (sample rate = 44, 100 Hz; volume = 60 dBA SPL, as measured at the ears).”

P10. "Stimulus modality was either auditory, visual, or audiovisual. Trials were blocked with short (~2 min) breaks between conditions".

Presumably the blocks were randomised across participants.

Condition order was not randomised across participants, but counterbalanced. This has been clarified in the manuscript.

“Stimulus modality was auditory, visual or audiovisual, presented in separate blocks with short breaks (~2 min) between conditions (see Figure 6A for an example trial). The order of conditions was counterbalanced across participants.” 

P15. Feels like there is a step not described here: "The d' of the auditory and visual conditions can be used to estimate the predicted 'optimal' sensitivity of audiovisual signals as calculated through MLE." Do they mean sqrt[ (d'A)^2 + (d'V)^2] ? If it is so simple then it may as well be made explicit here. A quick calculation from eyeballing Figures 2B and 2C suggests this is the case.

We thank the reviewer for raising this point of clarification. Yes, the ‘optimal’ audiovisual sensitivity was calculated as the hypotenuse of the auditory and visual sensitivities. This calculation has been made explicit in the revised manuscript.

The d’ from the auditory and visual conditions can be used to estimate the predicted ‘optimal’ sensitivity to audiovisual signals as calculated through the following formula:

"The perceived source location of auditory stimuli was manipulated via changes to interaural intensity and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992)." The stimuli were delivered by a pair of loudspeakers, and the incident sound at each ear would be a product of both speakers. And - if there were a time delay between the two speakers, then both ears could potentially receive separate pulses one after the other at different delays. Did they record this audio stimulus with manikin? If not, it would be very difficult to know what it was at the ears. I don't doubt that if they altered the relative volume of the loudspeakers then some directionality would be perceived but I cannot see how the interaural level and timing differences could be matched - as if the sound were from a single source. I doubt that this invalidates their results, but to present this as if it provided matched spatial and timing cues is wrong, and I cannot work out how they can attribute an azimuthal location to the sound. For replication purposes, it would be useful to know how far apart the loudspeakers were and what the timing and level differences actually were.

The behavioural tasks each had evenly distributed ‘source locations’ on the horizontal azimuth of the computer display (8 for the behavioural session, 5 for the EEG session). We manipulated the perceived location of auditory stimuli through interaural time delays and interaural level differences. By first measuring the forward (z) and horizontal (x) distance of each source location to each ear, the method worked by calculating what the time-course of a sound wave should be at the location of the ear given the sound wave at the source. Then, for each source location, we can calculate the time delay between speakers given the vectors of x and z, the speed of sound and the width of the head.  As the intensity of sound drops inversely with the square of the distance, we can divide the sound wave by the distance for each source location to provide the interaural level difference. Though we did not record the auditory stimulus with a manikin, our behavioural analyses show that participants were able to detect the directions of auditory stimuli from our manipulations, even to a degree that significantly exceeded the localisation accuracy for visual stimuli (for the behavioural session task). This information has been clarified in the manuscript.

“Auditory stimuli were played through two loudspeakers placed either side of the display (80 cm apart for the behavioural session, 58 cm apart for the EEG session).” 

“The perceived source location of auditory stimuli was manipulated via changes to interaural level and timing (Whitworth & Jeffress, 1961; Wightman & Kistler, 1992). The precise timing of when each speaker delivered an auditory stimulus was calculated from the following formula:

where x and z are the horizontal and forward distances in metres between the ears and the source of the sound on the display, respectively, r is the head radius, and s is the speed of sound. We used a constant approximate head radius of 8 cm for all participants. r was added to x for the left speaker and subtracted for the right speaker to produce the interaural time difference. For ±15° source locations, interaural timing difference was 1.7 ms. To simulate the decrease in sound intensity as a function of distance, we calculated interaural level differences for the left and right speakers by dividing the sounds by the left and right distance vectors. Finally, we resampled the sound using linear interpolation based on the calculations of the interaural level and timing differences. This process was used to calculate the soundwaves played by the left and right speakers for each of the possible stimulus locations on the display. The maximum interaural level difference between speakers was 0.14 A for ±15° auditory locations, and 0.07 A for ±7.5°.

I am confused about this statement: "A quantification of the behavioural sensitivity (i.e., steepness of the curves) revealed significantly greater sensitivity for the audiovisual stimuli than for the auditory stimuli alone (Z = -3.09, p = .002)," It is not clear from the methods how they attributed sound source angle to the sounds. Conceivably they know the angle of the loudspeakers, and this would provide an outer bound on the perceived location of the sound for extreme interaural level differences (although free field interaural timing cues can create a wider sound field). 

Our analysis of behavioural sensitivity was dependent on the set ‘source locations’ that were used to calculate the position of auditory and audiovisual stimuli.  In the behavioural task, participants judged the position of the target stimulus relative to a central stimulus. Thus, for each source location, we recorded how often participants correctly discriminated between presentations. The quoted analysis acknowledges that participants were more sensitive to audiovisual stimuli than auditory stimuli in the context of this task. A full explanation of how source location was implemented for auditory stimuli has been clarified in the manuscript. 

It would be very nice to see some of the "channel" activity - to get a feel for the representation used by the decoder. 

We have included responses for the five channels as a Supplemental Figure.

Figure 6 appears to show that there is some agreement between behaviour and neural responses - for the audiovisual case alone. The positive correlation of behavioural and decoding sensitivity appears to be driven by one outlier - who could not perform the audiovisual task (and indeed presumably any of them). Furthermore, if we were simply Bonferonni correct for the three comparisons, this would become non-significant. It is also puzzling why the unisensory behaviour and EEG do not correlate - which seems to again suggest a poor correspondence between them. Opposite to the claim made.

We understand the reviewer’s concern here. We would like to note, however, that each correlation used unique data sets – that is, the behavioural and neural data for each separate condition. In this case, we believe a Bonferroni correction for multiple comparisons is too conservative, as no data set was compared more than once. Neither the behavioural nor the neural data were normally distributed, and both contained outliers. Rather than reduce power through outlier rejection, we opted to test correlations using Spearman’s rho, which is resistant to outliers1. It is also worth noting that, without outlier rejection, the audiovisual correlation (p \= .003) would survive a Bonferroni correction for 3 comparisons. The nonsignificant correlation in the auditory and visual conditions might be due to the weaker responses elicited by unisensory stimuli, with the reduced signal-to-noise ratio obscuring potential correlations. Audiovisual stimuli elicited more precise responses both behaviourally and neurally, increasing the power to detect a correlation. 

(1) Wilcox, R.R. (2016), Comparing dependent robust correlations. British Journal of Mathematical & Statistical Psychology, 69(3), 215-224. https://doi.org/10.1111/bmsp.12069

“We also found a significant positive correlation between participants’ behavioural judgements in the EEG session and decoding sensitivity for audiovisual stimuli. This result suggests that participants who were better at identifying stimulus location also had more reliably distinct patterns of neural activity. The lack of neurobehavioural correlation in the unisensory conditions might suggest a poor correspondence between the different tasks, perhaps indicative of the differences between behavioural and neural measures explained previously. However, multisensory stimuli have consistently been found to elicit stronger neural responses than unisensory stimuli (Meredith & Stein, 1983; Puce et al., 2007; Senkowski et al., 2011; Vroomen & Stekelenburg, 2010), which has been associated with behavioural performance (Frens & Van Opstal, 1998; Wang et al., 2008). Thus, the weaker signalto-noise ratio in unisensory conditions may prevent correlations from being detected.”

Further changes:

(1)   To improve clarity, we shifted the Methods section to after the Discussion. This change included updating the figure numbers to match the new order (Figure 1 becomes Figure 6, Figure 2 becomes Figure 1, and so on).

(2)   We also resolved an error on Figure 2 (previously Figure 3). The final graph (Difference between AV and A + V) displayed incorrect values on the Y axis.

This has now been remedied.

eLife Assessment

Despite the well-established facilitatory effects of multisensory integration on behavioural measures, standard neuroimaging approaches have yet to reliably and precisely identify the corresponding neural correlates. In this valuable paper, Buhmann et al. leverage EEG decoding methods, moving beyond traditional univariate analyses, to capture these correlates. They present solid evidence that this approach can effectively estimate multisensory integration in humans across a broad range of contexts.

Reviewer #1 (Public review):

This study presents a novel application of inverted encoding (i.e., decoding) to detect non-linear correlates of crossmodal integration in human neural activity, using EEG (electroencephalography). The method is successfully applied to data from a group of 41 participants, performing a spatial localization task on auditory, visual, and audio-visual events. The analyses clearly show a behavioural superiority for audio-visual localization. Like previous studies, the results when using traditional univariate ERP analyses were inconclusive, showing once more the need for alternative, more sophisticated approaches. The inverted encoding approach of this study, harnessing on the multivariate nature of the signal, captured clear signs of super-additive responses, considered by many as the hallmark of multisensory integration. Despite the removal of eye-movement artefacts from the signal eliminated the significant decoding effect, the author's control analyses showed that decoding is more effective from parietal, compared to frontal electrodes, thereby ruling out ocular contamination as the sole origin of the relevant signal.

This significant finding can bear important advances in the many fields where multisensory integration has been shown to play an important role, by providing a way to bring much needed coherence across levels of analysis, from behaviour to single-cell electrophysiology. To achieve this, it would be ideal to contrast whether the pattern of super-additive effects in other scenarios where clear behavioural signs of multisensory integration are also observed. One could also try to further support the posterior origin of the super-additive effects by source localization.

Comments on revised version:

All my previous concerns have been addressed. I congratulate the authors on a very nice paper.

Reviewer #2 (Public review):

Summary:

This manuscript seeks to reconcile observations in multisensory perception - from behavior and from neural responses. It is intuitively obvious that perceiving a stimulus via two senses results in better performance than one alone. However, the nature of this interaction is complicated and relating different measures (behavioural, neural) is challenging.

It is not uncommon to observe that for a perceptual task the percentage of correct responses seen with two senses is higher than the sum of the percentage correct obtained with each modality individually. i.e. the gains are "superadditive". The gains of adding a second sense are typically larger when the performance with the first sense is relatively poor - this effect is often called the principle inverse effectiveness. More generally, what this tells us is that performance in a multisensory perceptual task is a non-linear sum of performance for each sensory modality alone. In invasive recordings from single neurons, a wide range of non-linear interactions is observed - some superadditive, and some sub-additive.

Despite this abundance evidence of non-linearity in some measures of multisensory integration, evoked responses (EEG) to such sensory stimuli often show little evidence of it - and this is the problem this manuscript tackles. The key assertion made is that a univariate analysis of the EEG signal is likely to average out non-linear effects of integration. This is a reasonable assertion, and their analysis does indeed provide evidence that a multivariate approach can reveal non-linear interactions in the evoked responses.

Strengths:

It is of great value to understand how the process of multisensory integration occurs, and despite a wealth of observations of the benefits of perceiving the world with multiple senses, we still lack a reasonable understanding of how the brain integrates information. For example - what underlies the large individual differences in the benefits of two senses over one? One way to tackle this is via brain imaging, but this is problematic if important features of the processing - such as non-linear interactions are obscured by the lack of specificity of the measurements. The approach they take to analysis of the EEG data allows the authors to look in more detail at the variation in activity across EEG electrodes, which averaging across electrodes cannot.

This version of the manuscript is well written and for the most part clear and the report of non-linear summation of neural responses is convincing. A particular strength of the paper is their use of a statistical model of multisensory integration as their "null" model of neural responses, and the "inverted-encoder" which infers an internal representation of the stimulus which can explain the EEG responses. This encoder generates a prediction of decoding performance, which can be used to generate predictions of multisensory decoding from unisensory decoding, or from a sum of the unisensory internal representations.

In behavioural performance, it is frequently observed that the performance increase from two senses is close to what is expected from the optimal integration of information across the senses, in a statistical sense. It can be plausibly explained by assuming that people are able to weight sensory inputs according to their reliability - and somewhat optimally. Critically the apparent "superadditive" effect on performance described above does not require any non-linearity in the sum of information across the senses, but can arise from correctly weighting the information according to reliability.

The authors apply a similar model to predict the neural responses expected to audiovisual stimuli from the neural responses to audio and visual stimuli alone, assuming optimal statistical integration of information. The neural responses to audiovisual stimuli exceed the predictions of this model and this is the main evidence supporting their conclusion, and it is convincing.

Weaknesses:

The main weakness of the manuscript is that their behavioural data show no evidence of performance that exceeds the predictions of these statistical models. In fact, the models predict multisensory performance from unisensory performance pretty well. This makes it hard to interpret their results, as surely if these nonlinear neural interactions underlie the behaviour, then we should be able to see evidence of it in the behaviour. I cannot offer an easy explanation for this.

Overall, therefore, I applaud the motivation and the sophistication of the analysis method and think it shows great promise for tackling these problems.

eLife Assessment

This valuable research contributes to our understanding of marine plankton diversity and gene expression by employing robust methodologies for sample collection and analysis. However, it lacks a comprehensive comparison with existing single-cell transcriptomics techniques in microbial ecology, and some terminology requires clarification for consistency with field standards. The downstream data analysis therefore provides only incomplete support for the claims made by the authors.

Reviewer #1 (Public review):

Summary:

The authors aim to elucidate the diversity and gene expression patterns of marine plankton using innovative collection and sequencing methodologies. Their work investigates the taxonomic and functional profiles of planktonic communities, providing insights into their ecological roles and responses to environmental changes.

Strengths:

The methodology utilized in this study, particularly the combination of single-cell sequencing and advanced bioinformatics techniques, represents a significant advancement in the field of plankton research. The application of the Smart-seq2 protocol for cDNA synthesis, followed by rigorous quality control measures, ensures high-quality data generation. This comprehensive approach not only enhances the resolution of the obtained genetic information but also allows for a more detailed exploration of the diversity and functional potential of the phytoplankton community.

One of the major strengths of this study is the rigorous methodological approach, including precise sampling techniques and robust data analysis protocols, which enhance the reliability of the results. The use of advanced sequencing technologies allows for a comprehensive assessment of gene expression, significantly contributing to our understanding of plankton diversity and its implications for marine ecosystems.

Weaknesses:

While the evidence presented is solid, there are areas where the analysis could be expanded. The authors could further explore the ecological interactions within plankton communities, which would provide a more holistic view of their functional roles. Additionally, a broader discussion of the implications of their findings for marine conservation efforts could enhance the manuscript's impact.

The choice of both the plankton net and filter pore size during the plankton collection process is critical, as these factors directly impact the types of phytoplankton collected. The use of a 25 μm filter paper, in particular, may result in the omission of many eukaryotic phytoplankton species. This limitation, combined with the characteristics of the plankton net, could affect the comprehensiveness and accuracy of the results, potentially influencing the study's conclusions regarding phytoplankton diversity.

The timing of fixation is crucial, as it directly affects whether the measured transcriptome accurately represents the organisms' actual transcriptional state in their native water environment. If fixation occurred a significant time after sample collection, the transcriptomic data may not reflect their true in situ transcriptional activity, which greatly reduces the relevance of this method.

Reviewer #2 (Public review):

Summary:

The paper introduces Ukiyo-e-Seq, a novel method integrating microscopy with single-cell transcriptomics to study individual, uncultured eukaryotic plankton cells. By combining microscopic imaging with transcriptomic analysis, the approach links plankton morphology to gene expression, enabling taxonomic identification and functional protein exploration. Ukiyo-e-Seq was tested on 66 microbial eukaryotic cells, revealing taxonomic diversity across four superkingdoms and allowing analysis of protein complexes and developmental genes in individual species. According to the authors, this method has the potential to advance single-cell marine biodiversity studies by addressing limitations in traditional taxonomy and metatranscriptomics, especially for rare or uncultured organisms.

However, the study's conclusions are often weakly supported by data, particularly given that this is not the first study to combine microscopy and single-cell transcriptomics of eukaryotic plankton using Smart-seq2.

Strengths:

A notable strength is the authors' generation of several single-cell transcriptomes for the diatom Chaetoceros, which could benefit from greater focus rather than broadly addressing eukaryotic single cells.

Weaknesses:

The study lacks comparison with other single-cell transcriptomics studies and it was presented as the first study that combines imaging and single-cell transcriptomics (smart-seq2) of eukaryotic plankton while in fact it is not. The sampling methodology is not replicable as the authors used a tea strainer instead of standard plankton collection equipment to filter larger cells. Terminology throughout the paper is unconventional, such as "public and private contigs," "single-organism genomics," "highly expressed contigs," and "optical methods." Additionally, the authors did not specify which database was used for taxonomic assignments. These issues may stem from the authors' limited background in microbial ecology. Overall, the study has many drawbacks and it could benefit from complete rewriting and focusing mainly on single-cell transcriptomics of diatoms.

Reviewer #3 (Public review):

Gatt et al. present a novel take on single-cell RNA-sequencing from complex planktonic samples, introducing an approach they aptly named Ukiyo-e-Seq. This work combines environmental sampling with cell picking, microscopic imaging, and Smart-seq2 single-cell RNA sequencing to profile uncultured eukaryotic plankton. Developing single-cell approaches for such ecosystems is critical, given the poor representation of many planktonic species in cultures and reference databases. This work could help bridge existing technological gaps between morphological and molecular studies of aquatic microeukaryotes

The authors argue that microscopy does not provide information on the biochemistry of species under consideration. At best, it provides taxonomic labeling of species within a sample, yet imaging fails to assess their metabolic state or to disentangle cryptic species. In a standard metatranscriptomic setup, the sequence pool is described by aligning assembled contigs with reference databases to obtain functional and taxonomic information. This complex community-level data is impossible to parse at the single-organism level. Moreover, by relying on reference datasets, a lot of potential information can be missed. The aim of the approach is to combine the strengths of both methods, generating single-cell transcriptomic data linked to individual plankton images.

Strengths:

Ukiyo-e-Seq generated a valuable dataset by combining imaging and transcriptomics for individual planktonic organisms from environmental samples. This multimodal approach has the potential to improve taxonomic predictions and functional insights at the single-organism level. This manuscript demonstrates the technical feasibility of such an approach. Data of this type is rare and thus represents a valuable resource to further advance single-cell sequencing of planktonic species from environmental samples.

Weaknesses:

(1) The merge-split strategy, where single-cell reads are pooled prior to assembly, is counterintuitive. Pooling obscures the single-organism resolution that single-cell methods aim to achieve. The approach might be useful for assembling low-coverage contigs, but risks masking unique expression profiles for transcripts unique to a given well. As an alternative, the authors could assemble each well independently to obtain well-specific transcriptomic bins. Assemblies could then be clustered based on sequence similarity, thereby imposing strict clustering parameters to maintain resolution, to create a common reference for downstream analysis if needed. In my opinion, better results would be obtained by implementing a per-well assembly and read mapping.

(2) The focus on the top five most expressed contigs throughout the manuscripts' data analysis is a limiting choice, as it excludes most contigs. In the preprint, we are presented with a very narrow view of the data. Visualising the entire range of assembled contigs would provide a better picture of the transcriptomic composition and diversity per well. It would be interesting to assess if the full information could be used to preliminary bin transcriptomic sequences from individual wells, for example, by gathering all 'private' contigs with high read coverage in a single well. Does such a set represent a single complete eukaryotic transcriptome?

(3) I missed a verification with (broad-scale) taxonomic assessments based on the associated microscopic images. In their goals, the authors state that a joint approach has the potential to discover new taxonomic biodiversity. I agree, and to me, this is what is exciting about the preprint, yet I miss an example or the right bioinformatic implementation to drive home this claim. Are there organisms in wells where poor taxonomic annotations, based on alignment to a reference database or the LCA approach implemented in Kraken2, would usually result in ignoring the species in classic metatranscriptomics? Can you advance the taxonomic annotation by referring back to the organisms' picture? Can manual assessment of taxonomy advance the results from the LCA approach?

(4) The current use of AlphaFold to predict protein structures does not convincingly add to the study's core objectives.

Overall, Ukiyo-e-Seq presents a promising method for studying single-cell diversity in environmental samples, though the bioinformatic pipeline requires refinement to support some of the claims made by the authors. Additionally, the manuscript would benefit from clarity and additional details in its methods and a more consistent approach to presenting results and summary statistics across all assembled contigs and all sampled wells, rather than focusing on selected wells.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to elucidate the diversity and gene expression patterns of marine plankton using innovative collection and sequencing methodologies. Their work investigates the taxonomic and functional profiles of planktonic communities, providing insights into their ecological roles and responses to environmental changes.

Strengths:

The methodology utilized in this study, particularly the combination of single-cell sequencing and advanced bioinformatics techniques, represents a significant advancement in the field of plankton research. The application of the Smart-seq2 protocol for cDNA synthesis, followed by rigorous quality control measures, ensures high-quality data generation. This comprehensive approach not only enhances the resolution of the obtained genetic information but also allows for a more detailed exploration of the diversity and functional potential of the phytoplankton community.

One of the major strengths of this study is the rigorous methodological approach, including precise sampling techniques and robust data analysis protocols, which enhance the reliability of the results. The use of advanced sequencing technologies allows for a comprehensive assessment of gene expression, significantly contributing to our understanding of plankton diversity and its implications for marine ecosystems.

Weaknesses:

While the evidence presented is solid, there are areas where the analysis could be expanded. The authors could further explore the ecological interactions within plankton communities, which would provide a more holistic view of their functional roles. Additionally, a broader discussion of the implications of their findings for marine conservation efforts could enhance the manuscript's impact.

The choice of both the plankton net and filter pore size during the plankton collection process is critical, as these factors directly impact the types of phytoplankton collected. The use of a 25 μm filter paper, in particular, may result in the omission of many eukaryotic phytoplankton species. This limitation, combined with the characteristics of the plankton net, could affect the comprehensiveness and accuracy of the results, potentially influencing the study's conclusions regarding phytoplankton diversity.

The timing of fixation is crucial, as it directly affects whether the measured transcriptome accurately represents the organisms' actual transcriptional state in their native water environment. If fixation occurred a significant time after sample collection, the transcriptomic data may not reflect their true in situ transcriptional activity, which greatly reduces the relevance of this method.

Thank you for your time, effort, and expertise.

We agree that additional analyses could improve our understanding of the plankton communities sampled. We have conducted an array of alternative analyses that were not included in the current manuscript and plan to perform new analyses over the next few months as part of a deeper revision of the manuscript. We are especially interested in “providing a more holistic view of the functions” of individual plankton within the community.

As for the protocol details, the pore size of the filter paper was chosen to focus on ~100 micron-sized organisms as a starting point: they are likely to contain more RNA than smaller organisms, making them well suited for an initial proof of concept of the methodology. That choice, however, is not particularly tightly constrained, therefore smaller plankton could be captured. This is supported by the lack of correlation, in our data, between organismal size and number of detected sequencing reads.

Timing to cell death/fixation is a common question we receive not just in this manuscript but any RNA-Seq from primary samples. In this case, plankton were seen swimming until picking, and after picking each organism was deposited within two seconds into a lysis buffer for fixation. Therefore, we do not have reason to believe that the transcriptional activity sampled in the sequencing reads differs in any major way from the one in living plankton. Nonetheless, a study specifically testing the effect of time between ocean sampling and reverse transcription would provide more quantitative information on this point.

Reviewer #2 (Public review):

Summary:

The paper introduces Ukiyo-e-Seq, a novel method integrating microscopy with single-cell transcriptomics to study individual, uncultured eukaryotic plankton cells. By combining microscopic imaging with transcriptomic analysis, the approach links plankton morphology to gene expression, enabling taxonomic identification and functional protein exploration. Ukiyo-e-Seq was tested on 66 microbial eukaryotic cells, revealing taxonomic diversity across four superkingdoms and allowing analysis of protein complexes and developmental genes in individual species. According to the authors, this method has the potential to advance single-cell marine biodiversity studies by addressing limitations in traditional taxonomy and metatranscriptomics, especially for rare or uncultured organisms.

However, the study's conclusions are often weakly supported by data, particularly given that this is not the first study to combine microscopy and single-cell transcriptomics of eukaryotic plankton using Smart-seq2.

Strengths:

A notable strength is the authors' generation of several single-cell transcriptomes for the diatom Chaetoceros, which could benefit from greater focus rather than broadly addressing eukaryotic single cells.

Weaknesses:

The study lacks comparison with other single-cell transcriptomics studies and it was presented as the first study that combines imaging and single-cell transcriptomics (smart-seq2) of eukaryotic plankton while in fact it is not. The sampling methodology is not replicable as the authors used a tea strainer instead of standard plankton collection equipment to filter larger cells. Terminology throughout the paper is unconventional, such as "public and private contigs," "single-organism genomics," "highly expressed contigs," and "optical methods." Additionally, the authors did not specify which database was used for taxonomic assignments. These issues may stem from the authors' limited background in microbial ecology. Overall, the study has many drawbacks and it could benefit from complete rewriting and focusing mainly on single-cell transcriptomics of diatoms.

Thank you for your time, effort, and expertise.

There might be a bit of confusion between single-cell and single-organism sequencing, likely due to lack of clarity in our initial submission. In particular, in this manuscript no effort was spent trying to dissociate oligocellular plankton into individual cells before sequencing. While probably feasible, we expect that to be technically much harder than single-organism sequencing as performed here. The reviewer does not reference a published paper where combined imaging and RNA-Seq of individual uncultured plankton has been achieved, and we were unable to find one in the scientific literature. As stated in the manuscript, others have already performed some work on cultured plankton and single-organism sequencing (without matching images) of uncultured environmental microorganisms.

The suggestion to focus on a smaller biological niche such as diatoms and adopt language more familiar to that specific community is well received. Indeed, given that organisms as diverse as fish larvae and diatoms could be profiled with Ukiyo-e-Seq, future studies could use the same method to address specific questions with a deeper and more narrow scope. However, this manuscript is demonstrating the feasibility of Ukiyo-e-Seq and its ability to produce usable data for a broad spectrum of organisms: part of the scientific audience might not have a specific interest in diatoms.

The tea strainer was used for coarse pre-filtering: the exact pore size, geometry and factory tolerance on those measurements are inconsequential because each organism is later chosen (or not) based on a high-resolution microscopy image (or multiple, if fluorescence is considered). This really is a strength of Ukiyo-e-Seq over FACS or droplet-based sorters, which can only collect coarse optical information from each organism for (typically) less than 1 millisecond. In Ukiyo-q-Seq, while the actual decision to pick an individual is currently manual (by the operator of the picker), it can be automated in principle. For instance, one could build a machine learning model of plankton taxonomy based on a large collection of labelled images and use predictions from such a model to automatically drive the picker (e.g. focussing on diatoms), increasing throughput. Even in that case, however, the initial filtering stages using tea strainers, plankton nets, filter paper etc. would not be critical for the final selection of individuals as long as they are not too restrictive.

The database used for taxonomic assignment was the NCBI non-redundant nucleotide database, accessed through the reference library provided by Kraken2 (nt).

Reviewer #3 (Public review):

Gatt et al. present a novel take on single-cell RNA-sequencing from complex planktonic samples, introducing an approach they aptly named Ukiyo-e-Seq. This work combines environmental sampling with cell picking, microscopic imaging, and Smart-seq2 single-cell RNA sequencing to profile uncultured eukaryotic plankton. Developing single-cell approaches for such ecosystems is critical, given the poor representation of many planktonic species in cultures and reference databases. This work could help bridge existing technological gaps between morphological and molecular studies of aquatic microeukaryotes

The authors argue that microscopy does not provide information on the biochemistry of species under consideration. At best, it provides taxonomic labeling of species within a sample, yet imaging fails to assess their metabolic state or to disentangle cryptic species. In a standard metatranscriptomic setup, the sequence pool is described by aligning assembled contigs with reference databases to obtain functional and taxonomic information. This complex community-level data is impossible to parse at the single-organism level. Moreover, by relying on reference datasets, a lot of potential information can be missed. The aim of the approach is to combine the strengths of both methods, generating single-cell transcriptomic data linked to individual plankton images.

Strengths:

Ukiyo-e-Seq generated a valuable dataset by combining imaging and transcriptomics for individual planktonic organisms from environmental samples. This multimodal approach has the potential to improve taxonomic predictions and functional insights at the single-organism level. This manuscript demonstrates the technical feasibility of such an approach. Data of this type is rare and thus represents a valuable resource to further advance single-cell sequencing of planktonic species from environmental samples.

Weaknesses:

(1) The merge-split strategy, where single-cell reads are pooled prior to assembly, is counterintuitive. Pooling obscures the single-organism resolution that single-cell methods aim to achieve. The approach might be useful for assembling low-coverage contigs, but risks masking unique expression profiles for transcripts unique to a given well. As an alternative, the authors could assemble each well independently to obtain well-specific transcriptomic bins. Assemblies could then be clustered based on sequence similarity, thereby imposing strict clustering parameters to maintain resolution, to create a common reference for downstream analysis if needed. In my opinion, better results would be obtained by implementing a per-well assembly and read mapping.

(2) The focus on the top five most expressed contigs throughout the manuscripts' data analysis is a limiting choice, as it excludes most contigs. In the preprint, we are presented with a very narrow view of the data. Visualising the entire range of assembled contigs would provide a better picture of the transcriptomic composition and diversity per well. It would be interesting to assess if the full information could be used to preliminary bin transcriptomic sequences from individual wells, for example, by gathering all 'private' contigs with high read coverage in a single well. Does such a set represent a single complete eukaryotic transcriptome?

(3) I missed a verification with (broad-scale) taxonomic assessments based on the associated microscopic images. In their goals, the authors state that a joint approach has the potential to discover new taxonomic biodiversity. I agree, and to me, this is what is exciting about the preprint, yet I miss an example or the right bioinformatic implementation to drive home this claim. Are there organisms in wells where poor taxonomic annotations, based on alignment to a reference database or the LCA approach implemented in Kraken2, would usually result in ignoring the species in classic metatranscriptomics? Can you advance the taxonomic annotation by referring back to the organisms' picture? Can manual assessment of taxonomy advance the results from the LCA approach?

(4) The current use of AlphaFold to predict protein structures does not convincingly add to the study's core objectives.

Overall, Ukiyo-e-Seq presents a promising method for studying single-cell diversity in environmental samples, though the bioinformatic pipeline requires refinement to support some of the claims made by the authors. Additionally, the manuscript would benefit from clarity and additional details in its methods and a more consistent approach to presenting results and summary statistics across all assembled contigs and all sampled wells, rather than focusing on selected wells.

Thank you for your time and effort, and for your expertise on the matter.

The suggestions to conduct additional bioinformatic analyses to explore more fully the criticality and potential of various design choices (e.g. meta-assembly) are well received. We have tried some of those ideas already (e.g. assembling individual wells) and we have considered but not yet conducted or polished others (e.g. a more thorough taxonomic verification). We will endeavour to carry out as many of those analyses as possible during the deeper revision process in the coming months.

AlphaFold 3’s use was designed to demonstrate the ability to investigate protein-protein interactions from individual species. When two peptide sequences are detected within the same well, they are more likely to be potential interacting partners than in a metatranscriptomic study, because the compartmentalisation of reads into tens or hundreds of wells greatly reduces the search space of potential interaction partners (which has a baseline runtime complexity of n squared, where n is the number of peptide sequences identified).

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eLife Assessment

This important study explores the relationship between the sequence of prokaryotic promoter elements and their activity using mutagenesis to generate thousands of mutant sequences. The evidence supporting these findings is convincing. This work will appeal to those interested in bacterial genetics, genome evolution, and gene regulation.

Reviewer #1 (Public review):

Summary:

This study by Fuqua et al. studies the emergence of sigma70 promoters in bacterial genomes. While there have been several studies to explore how mutations lead to promoter activity, this is the first to explore this phenomena in a wide variety of backgrounds, which notably contain a diverse assortment of local sigma70 motifs in variable configurations. By exploring how mutations affect promoter activity in such diverse backgrounds, they are able to identify a variety of anecdotal examples of gain/loss of promoter activity and propose several mechanisms for how these mutations are interacting within the local motif landscape. Ultimately, they show how different sequences have different probabilities of gaining/losing promoter activity and may do so through a variety of mechanisms.

Major strengths and weaknesses of the methods and results:

This study uses Sort-Seq to characterize promoter activity, which has been adopted by multiple groups and shown to be robust. Furthermore, they use a slightly altered protocol which allows measurements of bi-directional promoter activity. This combined with their pooling strategy allows them to characterize expression of many different backgrounds in both directions in extremely high-throughput which is impressive! A second key approach this study relies on is the identification of promoter motifs using position weight matrices (PWMs). While these methods are prone to false positives, the authors implement a systematic approach which is standard in the field. However, drawing these types of binary definitions (is this a motif? yes/no) should always come with the caveat that gene expression is quantitative traits that we oversimplify when drawing boundaries.

Their approach to randomly mutagenize promoters allowed them to find many examples of different types of evolutions that may occur to increase or decrease promoter activity. They have supported these with validations in more controlled backgrounds which convincingly support their proposed mechanisms for promoter evolution.

An appraisal of whether the authors achieved their aims, and whether the results support their conclusions:

The authors express a key finding that the specific landscape of promoter motifs in a sequence affect the likelihood that local mutations create or destroy regulatory elements. The authors have described many examples, including several that are non-obvious, and show convincingly that different sequence backgrounds have different probabilities for gaining or losing promoter activity. This overarching conclusion is supported by trend and mechanistic data which show differences in probabilities of evolving promoters, as well as the mechanisms underlying these evolutions. Furthermore, these mutations are well described and presented, showing the strength of emergent promoter motifs and their specific spacings from existing motifs within the sequence.

Impact of the work on the field, and the utility of the methods and data to the community:

This study enhances our understanding of the diverse mechanisms by which promoters can evolve or devolve, potentially improving models that predict mutational outcomes. While this study reveals complex mutational patterns, modeling them could significantly advance our ability to predict bacterial evolutionary trajectories and interpret genomes, bringing us closer to that goal.

Recent work in the field of bacterial gene regulation has raised interest in bidirectional promoter regions. While the authors do not discuss how mutations that raise expression in one direction may affect another, they have created an expansive dataset which may enable other groups to study this interesting phenomenon. Also, their variation of the Sort-Seq protocol will be a valuable example for other groups who may be interested in studying bidirectional expression. Lastly, this study may be of interests to groups studying eukaryotic regulation as it can inform how the evolution of transcription factor binding sites influences short-range interactions with local regulator elements.

Any additional context to understand the significance of the work:

Predicting whether a sequence drives promoter activity is a challenging task. By learning the types of mutations that create or destroy promoters, this study provides valuable insights for computational models aimed at predicting promoter activity.

Comments on revised version:

I am satisfied with the extensive changes made by the author. This manuscript is excellent.

I very much like the change in figures to incorporate the sequence information. It is great to see clear representations of the emergent sigma70 motifs and their spacing relative to existing motifs. This addition significantly improves the clarity of the findings.

The validation of mutations on a clean background is well-executed, and the results are convincing. I appreciate the effort put into validating their results. The additional analyses that include TGn and UP-element motifs are also well done and highly relevant, as these elements are known to compensate for weaker or absent -35 sequences.

Most or all perceived inconsistencies from the previous version have been resolved. While I don't think the fluorescence threshold of 1.5 a.u. for promoter activity is justified, the authors do acknowledge this shortcoming, and even empirically-derived thresholds are still technically arbitrary.

I particularly enjoyed Figure 1E, thank you for entertaining my analysis request! Also, the H-NS story is a nice addition showing how transcription factors influence this evolution

Overall, this revised manuscript is an excellent contribution to the field, and I have no further recommendations for improvement.

Reviewer #2 (Public review):

Summary:

Fuqua et al investigated the relationship between prokaryotic box motifs and the activation of promoter activity using a mutagenesis sequencing approach. From generating thousands of mutant daughter sequences from both active and non-active promoter sequences they were able to produce a fantastic dataset to investigate potential mechanisms for promoter activation. From these large numbers of mutated sequences, they were able to generate mutual information with gene expression to identify key mutations relating to the activation of promoter island sequences.

Strengths:

The data generated from this paper is an important resource to address this question of promoter activation. Being able to link promoter modulated gene expression to mutational changes in previously nonactive promoter regions is exciting. This approach allows future large-scale studies to investigate evolutionary processes relating to changes in gene regulation in a statistically robust manner. Here there is a focus on the -10 and -35 boxes but other elements and interactions were explored including; H-NS binding, UP-element and TGn. Alongside this, the method of identifying key mutations using mutual information in this paper is well done and should be a standard in future studies for identifying regions of interest.

Weaknesses:

While the generation of the data is superb, as the authors have stated clearly themselves, there is a lot of scope for future studies to understand both causal relationships and utilise the data more effectively. The authors look at changes in regulatory expression based on a few observations that are treated independently but occur concurrently. While this study has backed up findings experimentally this may not always be possible. Previously this reviewer had suggested addressing this using complementary approaches such as analysis focusing on identifying important motifs, using something like a glm lasso regression to identify significant motifs, and then combining with mutational hotspot information would be more robust. The authors tried to implement such an approach in response to the review, but its complexity became beyond the scope. I look forward to the development of such methods that allow more complete exploration of similar datasets.

Comments on revised version:

The authors addressed all my previous comments. I believe the study is much improved and thank them for the time and effort they put into addressing the comments.

Reviewer #3 (Public review):

This work brings a computational approach to the study of promoters and transcription. The paper is improved but there are still factual errors and implausible explanations. I am not convinced by the response from the authors, concerning the promoter -35 element, in their rebuttal.

Comments on author rebuttal:

- We respectfully but strongly disagree that our analysis has misrepresented the true nature of -35 boxes. First, accounting for more A's at position 5 in the PWM is not going to lead to a "critical error." This is because positions 4-6 of the motif barely have any information content (bits) compared to positions 1-3 (see Fig 1A).

The analysis does misrepresent the consensus -35 element, which is, unequivocally, TTGACA. I agree that positions 4-6 of the element are less well-conserved.

- This assertion is not just based on our own PWM, but based on ample precedent in the literature. In PMID 14529615, TTG is present in 38% of all -35 boxes, but ACA only in 8%.

This does not mean that TTGACA is not the consensus, or that "ACA" is not important at promoters where it's present.

- In PMID 29388765, with the -10 instance TATAAT, the -35 instance TTGCAA yields stronger promoters compared to the -35 instance TTGACA (See their Figure 3B).

This is a known phenomenon and results from "perfect" promoters being limited at the point of RNA polymerase promoter escape (because the RNAP struggles to "let go" of perfect promoters). This does not mean the TTGACA is not the consensus. Indeed, and this is a key point, it is evident in the figure the authors refer to that TTGACA stimulates more transcription than alternative -35 sequences when -10 elements are not perfect.

- In PMID 29745856 (Figure 2), the most information content lies in positions 1-3, with the A and C at position 5 both nearly equally represented, as in our PWM.

The motif shown in this paper suffers from exactly the same issue as the paper under review; the variable spacing between the -35 hexamer and -10 element isn't taken into account by MEME.

- In PMID 33958766 (Figure 1) an experimentally-derived -35 box is even reduced to a "partial" -35 box which only includes positions 1 and 2, with consensus: TTnnnn.

This paper does not show an "experimentally-derived -35 box" in Figure 1 (or anywhere else, as far as I can see).

- In addition, we did not derive the PWMs as the reviewer describes. The PWMs we use are based on computational predictions that are in excellent agreement with experimental results. Specifically, the PWMs we use are from PMID 29728462, which acquired 145 -10 and -35 box sequences from the top 3.3% of computationally predicted boxes from Regulon DB.

The paper mentioned states "for the genomic RNAP logo, sequences were taken from computationally predicted RNAP binding sites on RegulonDB" so these are not experimentally defined promoters? It's not obvious from the paper, or regulon DB, which sequences these are or how they were predicted.

- Thank you for pointing out that our original submission was incomplete in this regard. We address these concerns by new analyses, including some new experiments. First, Rho dependent termination is associated with the RUT motif, which is very rich in Cytosines (PMID: 30845912). Given that our sequences confer between 65%-78% of AT-content, canonical rho dependent termination is unlikely. However, we computationally searched for rho-dependent terminators using the available code from PMID: 30845912, but the algorithm did not identify any putative RUTs. Because this analysis was not informative, we did not include it in the paper.

I don't believe it is the case that Rho absolutely requires a RUT sequence. My understanding is that, if an RNA is not translated, Rho will intervene (e.g. see PMID: 18487194).

- We respectfully disagree that the reviewer's point is pertinent because what the reviewer is referring to is the likelihood that the sequence is a promoter, which indeed increases with AT content, but we are focused on the likelihood that a sequence becomes a promoter through DNA mutation

I disagree that this distinction is relevant. An AT-rich sequence will much more closely resemble a promoter by chance than a GC rich sequence. As an extreme example, the sequence TTTTTT can be converted into a reasonable -10 element by one change (to TATTTT) but the sequence GGGGGG can't.

Author response:

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

We performed multiple new experiments and analyses in response to the reviewers concerns, and incorporated the results of these analyses in the main text, and in multiple substantially revised or new figures. Before embarking on a point-by-point reply to the reviewers’ concerns, we here briefly summarize our most important revisions.

First, we addressed a concern shared by Reviewers #1-3 about a lack of information about our DNA sequences. To this end, we redesigned multiple figures (Figures 3, 4, 5, S8, S9, S10, S11, and S12) to include the DNA sequences of each tested promoter, the specific mutations that occurred in it, the resulting changes in position-weight-matrix (PWM) scores, and the spacing between promoter motifs. Second, Reviewers #1 and #2 raised concerns about a lack of validation of our computational predictions and the resulting incompleteness of the manuscript. To address this issue, we engineered 27 reporter constructs harboring specific mutations, and experimentally validated our computational predictions with them. Third, we expanded our analysis to study how a more complete repertoire of other sigma 70 promoter motifs such as the UP-element and the extended -10 / TGn motif affects gene expression driven by the promoters we study. Fourth, we addressed concerns by Reviewer #3 about the role of the Histone-like nucleoid-structuring protein (H-NS) in promoter emergence and evolution. We did this by performing both experiments and computational analyses, which are now shown in the newly added Figure 5. Fifth, to satisfy Reviewer #3’s concerns about missing details in the Discussion, we have rewritten this section, adding additional details and references. 

We next describe these and many other changes in a point-by-point reply to each reviewer’s comments. In addition, we append a detailed list of changes to each section and figure to the end of this document.

Reviewer #1 (Public Review):

Summary:

This study by Fuqua et al. studies the emergence of sigma70 promoters in bacterial genomes. While there have been several studies to explore how mutations lead to promoter activity, this is the first to explore this phenomenon in a wide variety of backgrounds, which notably contain a diverse assortment of local sigma70 motifs in variable configurations. By exploring how mutations affect promoter activity in such diverse backgrounds, they are able to identify a variety of anecdotal examples of gain/loss of promoter activity and propose several mechanisms for how these mutations interact within the local motif landscape. Ultimately, they show how different sequences have different probabilities of gaining/losing promoter activity and may do so through a variety of mechanisms.

We thank Reviewer #1 for taking the time to read and provide critical feedback on our manuscript. Their summary is fundamentally correct.

Major strengths and weaknesses of the methods and results:

This study uses Sort-Seq to characterize promoter activity, which has been adopted by multiple groups and shown to be robust. Furthermore, they use a slightly altered protocol that allows measurements of bi-directional promoter activity. This combined with their pooling strategy allows them to characterize expressions of many different backgrounds in both directions in extremely high throughput which is impressive! A second key approach this study relies on is the identification of promoter motifs using position weight matrices (PWMs). While these methods are prone to false positives, the authors implement a systematic approach which is standard in the field. However, drawing these types of binary definitions (is this a motif? yes/no) should always come with the caveat that gene expression is a quantitative trait that we oversimplify when drawing boundaries.

The point is well-taken. To clarify this and other issues, we have added a section on the limitations of our work to the Discussion. Within this section we include the following sentences (lines 675-680):

“Additionally, future studies will be necessary to address the limitations of our own work. First, we use binary thresholding to determine i) the presence or absence of a motif, ii) whether a sequence has promoter activity or not, and iii) whether a part of a sequence is a hotspot or not. While chosen systematically, the thresholds we use for these decisions may cause us to miss subtle but important aspects of promoter evolution and emergence.”

Their approach to randomly mutagenizing promoters allowed them to find many anecdotal examples of different types of evolutions that may occur to increase or decrease promoter activity. However, the lack of validation of these phenomena in more controlled backgrounds may require us to further scrutinize their results. That is, their explanations for why certain mutations lead or obviate promoter activity may be due to interactions with other elements in the 'messy' backgrounds, rather than what is proposed.

Thank you for raising this important point. To address it, we have conducted extensive new validation experiments for the newest version of this manuscript. For the “anecdotal” examples you described, we created 27 reporter constructs harboring the precise mutation that leads to the loss or gain of gene expression, and validated its ability to drive gene expression. The results from these experiments are in Figures 3, 4, 5, and Supplemental Figures S8-S11, and are labeled with a ′ (prime) symbol.

These experiments not only confirm the increases and decreases in fluorescence that our analysis had predicted. They also demonstrate, with the exception of two (out of 27) falsepositive discoveries, that background mutations do not confound our analysis. We mention these two exceptions (lines 364-367):

“In two of these hotspots, our validation experiments revealed no substantial difference in gene expression as a result of the hotspot mutation (Fig S8F′ and Fig S8J′). In both of these false positives, new -10 boxes emerge in locations without an upstream -35 box.”

An appraisal of whether the authors achieved their aims, and whether the results support their conclusions:

The authors express a key finding that the specific landscape of promoter motifs in a sequence affects the likelihood that local mutations create or destroy regulatory elements. The authors have described many examples, including several that are non-obvious, and show convincingly that different sequence backgrounds have different probabilities for gaining or losing promoter activity. While this overarching conclusion is supported by the manuscript, the proposed mechanisms for explaining changes in promoter activity are not sufficiently validated to be taken for absolute truth. There is not sufficient description of the strength of emergent promoter motifs or their specific spacings from existing motifs within the sequence. Furthermore, they do not define a systematic process by which mutations are assigned to different categories (e.g. box shifting, tandem motifs, etc.) which may imply that the specific examples are assigned based on which is most convenient for the narrative.

To summarize, Reviewer #1 criticizes the following three aspects of our work in this comment. 1) The mechanisms we proposed are not sufficiently validated. 2) The description of motifs, spacing, and PWM scores are not shown. 3) How mutations are classified into different categories (i.e. box-shifting, tandem motifs, etc.) is not systematically defined. 

These are all valid criticisms. In response, we performed an extensive set of follow-up experiments and analyses, and redesigned the majority of the figures. Here is a more detailed response to each criticism:

(1) Proposed mechanisms for explaining changes in promoter activity are not sufficiently validated. We engineered 27 reporter constructs harboring the specific mutations in the parents that we had predicted to change promoter activity. For each, we compared their fluorescence levels with their wild-type counterpart. The results from these experiments are in Figures 3 and 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12, and are labeled with a ′ (prime) symbol.

(2) No sufficient description of the strength of emergent promoter motifs or their specific spacings. We redesigned the figures to include the DNA sequences of the parent sequences, as well as the degenerate consensus sequences for each mutation. We additionally now highlight the specific motif sequences, their respective PWM scores, and by how much the score changes upon mutation. Finally, we annotated the spacing of motifs. These changes are in Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12.

We note that in many cases, high-scoring PWM hits for the same motif can overlap (i.e. two -10 motifs or two -35 motifs overlap). Additionally, the proximity of a -35 and -10 box does not guarantee that the two boxes are interacting. Together, these two facts can result in an ambiguity of the spacer size between two boxes. To avoid any reporting bias, we thus often report spacer sizes as a range (see Figure panels 4F, S8D, S8F-L, S9A, S9H, S10A, and S10E). The smallest spacer we annotate is in Figure 4F with 10 bp, and the largest is in Figure S8D with 26 bp. Any more “extreme” distances are not annotated and for the reader to decide if an interaction is present or not.

(3) No systematic process by which mutations are assigned to different categories such as box shifting, tandem motifs, etc. We opted to reformulate these categories completely, because the phenotypic effects of a previously mentioned “tandem motif” was actually a byproduct of H-NS repression (see the newly added Figure S12). 

We also agree that the categories were ambiguous. We now introduce two terms: homo-gain and hetero-gain of -10 and -35 boxes. The manuscript now clearly defines these terms, and the relevant passage now reads as follows (lines 430-435): 

“We found that these mutations frequently create new boxes overlapping those we had identified as part of a promoter

(Fig S9). This occurs when mutations create a -10 box overlapping a -10 box, a -35 box overlapping a -35 box, a -10 box overlapping a -35 box, or a -35 box overlapping a -10 box. We call the resulting event a “homo-gain” when the new box is of the same type as the one it overlaps, and otherwise a “hetero-gain”. In either case, the creation of the new box does not always destroy the original box.”

Impact of the work on the field, and the utility of the methods and data to the community: From this study, we are more aware of different types of ways promoters can evolve and devolve, but do not have a better ability to predict when mutations will lead to these effects. Recent work in the field of bacterial gene regulation has raised interest in bidirectional promoter regions. While the authors do not discuss how mutations that raise expression in one direction may affect another, they have created an expansive dataset that may enable other groups to study this interesting phenomenon. Also, their variation of the Sort-Seq protocol will be a valuable example for other groups who may be interested in studying bidirectional expression. Lastly, this study may be of interest to groups studying eukaryotic regulation as it can inform how the evolution of transcription factor binding sites influences short-range interactions with local regulator elements. Any additional context to understand the significance of the work:

The task of computationally predicting whether a sequence drives promoter activity is difficult. By learning what types of mutations create or destroy promoters from this study, we are better equipped for this task.

We thank Reviewer #1 again for their time and their thoughtful comments.

Reviewer #2 (Public Review):

Summary:

Fuqua et al investigated the relationship between prokaryotic box motifs and the activation of promoter activity using a mutagenesis sequencing approach. From generating thousands of mutant daughter sequences from both active and non-active promoter sequences they were able to produce a fantastic dataset to investigate potential mechanisms for promoter activation. From these large numbers of mutated sequences, they were able to generate mutual information with gene expression to identify key mutations relating to the activation of promoter island sequences.

We thank Reviewer #2 for reading and providing a thorough review of our manuscript. 

Strengths:

The data generated from this paper is an important resource to address this question of promoter activation. Being able to link the activation of gene expression to mutational changes in previously nonactive promoter regions is exciting and allows the potential to investigate evolutionary processes relating to gene regulation in a statistically robust manner. Alongside this, the method of identifying key mutations using mutual information in this paper is well done and should be standard in future studies for identifying regions of interest.

Thank you for your kind words.

Weaknesses:

While the generation of the data is superb the focus only on these mutational hotspots removes a lot of the information available to the authors to generate robust conclusions. For instance.

(1) The linear regression in S5 used to demonstrate that the number of mutational hotspots correlates with the likelihood of a mutation causing promoter activation is driven by three extreme points.

A fair criticism. In response, we have chosen to remove the analysis of this trend from the manuscript entirely. (Additionally, Pnew and mutual information calculations both relied on the fluorescence scores of daughter sequences, so the finding was circular in its logic.)

(2) Many of the arguments also rely on the number of mutational hotspots being located near box motifs. The context-dependent likelihood of this occurring is not taken into account given that these sequences are inherently box motif rich. So, something like an enrichment test to identify how likely these hot spots are to form in or next to motifs.

Another good point. To address it, we carried out a computational analysis where we randomly scrambled the nucleotides of each parent sequence while maintaining the coordinates for each mutual information “hotspot.” This scrambling results in significantly less overlap with hotspots and boxes. This analysis is now depicted in Figure 2C and described in lines 272-296.

(3) The link between changes in expression and mutations in surrounding motifs is assessed with two-sided Mann Whitney U tests. This method assumes that the sequence motifs are independent of one another, but the hotspots of interest occur either in 0, 3, 4, or 5s in sequences. There is therefore no sequence where these hotspots can be independent and the correlation causation argument for motif change on expression is weakened.

This is a fair criticism and a limitation of the MWU test. To better support our reasoning, we engineered 27 reporter constructs harboring the specific mutations in the parents that we had predicted to change promoter activity. For each, we compared their fluorescence levels with their wild-type counterpart. The results from these experiments are in Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12 and are labeled with a ′ (prime) symbol.

These experiments not only confirm the increases and decreases in fluorescence that our analysis had predicted. They also demonstrate, with the exception of two (out of 27) falsepositive discoveries, that background mutations do not confound our analysis. We mention these two exceptions (lines 364-367):

“In two of these hotspots, our validation experiments revealed no substantial difference in gene expression as a result of the hotspot mutation (Fig S8F′ and Fig S8J′). In both of these false positives, new -10 boxes emerge in locations without an upstream -35 box.”

(4) The distance between -10 and -35 was mentioned briefly but not taken into account in the analysis.

We have now included these spacer distances where appropriate. These changes are in Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12.

We note that in many cases, high-scoring PWM hits for the same motif can overlap (i.e. two -10 motifs or two -35 motifs overlap). Additionally, the proximity of a -35 and -10 box does not guarantee that the two boxes are interacting. Together, these two facts can result in an ambiguity of the spacer size between two boxes. To avoid any reporting bias, we thus often report spacer sizes as a range (see Figure panels 4F, S8D, S8F-L, S9A, S9H, S10A, and S10E). The smallest spacer we annotate is in Figure 4F with 10 bp, and the largest is in Figure S8D with 26 bp. More “extreme” distances are not annotated, and for the reader to decide if an interaction is present or not.

The authors propose mechanisms of promoter activation based on a few observations that are treated independently but occur concurrently. To address this using complementary approaches such as analysis focusing on identifying important motifs, using something like a glm lasso regression to identify significant motifs, and then combining with mutational hotspot information would be more robust.

This is a great idea, and we pursued it as part of the revision. For each parent sequence, we mapped the locations of all -10 and -35 box motifs in the daughters, then reduced each sequence to a binary representation, either encoding or not encoding these motifs, also referred to as a “hot-encoded matrix.” We subsequently performed a Lasso regression between the hot-encoded matrices and the fluorescence scores of each daughter sequence. The regression then outputs “weights” to each of the motifs in the daughters. The larger a motif’s weight is, the more the motif influences promoter activity. The Author response image 1 describes our workflow.

Author response image 1.

We really wanted this analysis to work, but unfortunately, the computational model does not act robustly, even when testing multiple values for the hyperparameter lambda (λ), which accounts for differences in model biases vs variance.

The regression assigns strong weights almost exclusively to -10 boxes, and assigns weak to even negative weights to -35 boxes. While initially exciting, these weights do not consistently align with the results from the 27 constructs with individual mutations that we tested experimentally. This ultimately suggests that the regression is overfitting the data.

We do think a LASSO-regression approach can be applied to explore how individual motifs contribute to promoter activity. However, effectively implementing such a method would require a substantially more complex analysis. We respectfully believe that such an approach would distract from the current narrative, and would be more appropriate for a computational journal in a future study. 

Because this analysis was inconclusive, we have not made it part of the revised manuscript. However, we hope that our 27 experimentally validated new constructs with individual mutations are sufficient to address the reviewer’s concerns regarding independent verification of our computational predictions.

Other elements known to be involved in promoter activation including TGn or UP elements were not investigated or discussed.

Thank you for highlighting this potentially important oversight. In response, we have performed two independent analyses to explore the role of TGn in promoter emergence in evolution. First, we computationally searched for -10 boxes with the bases TGn immediately upstream of them in the parent sequences, and found 18 of these “extended -10 boxes” in the parents (lines 143145):

“On average, each parent sequence contains ~5.32 -10 boxes and ~7.04 -35 boxes (Fig S1). 18 of these -10 boxes also include the TGn motif upstream of the hexamer.”

However, only 20% of these boxes were found in parents with promoter activity (lines 182-185):

“We also note that 30% (15/50) of parents have the TGn motif upstream of a -10 box, but only 20% (3/15) of these parents have promoter activity (underlined with promoter activity: P4-RFP, P6-RFP, P8-RFP, P9-RFP, P10-RFP, P11GFP, P12-GFP, P17-GFP, P18-GFP, P18-RFP, P19-RFP, P22-RFP, P24-GFP, P25-GFP, P25-RFP). “

Second, we computationally searched through all of the daughter sequences to identify new -10 boxes with TGn immediately upstream. We found 114 -10 boxes with the bases TGn upstream. However, only 5 new -10 boxes (2 with TGn) were associated with increasing fluorescence (lines 338-345):

“On average, 39.5 and 39.4 new -10 and -35 boxes emerged at unique positions within the daughter sequences of each mutagenized parent (Fig 3A,B), with 1’562 and 1’576 new locations for -10 boxes and -35 boxes, respectively. ~22% (684/3’138) of these new boxes are spaced 15-20 bp away from their cognate box, and ~7.3% (114/1’562) of the new -10 boxes have the TGn motif upstream of them. However, only a mere five of the new -10 boxes and four of the new 35 boxes are significantly associated with increasing fluorescence by more than +0.5 a.u. (Fig 3C,D).”

In addition, we now study the role of UP elements. This analysis showed that the UP element plays a negligible role in promoter emergence within our dataset.  It is discussed in a new subsection of the results (lines 591-608).

Collectively, these additional analyses suggest that the presence of TGn plus a -10 box is insufficient to create promoter activity, and that the UP element does not play a significant role in promoter emergence or evolution.

Reviewer #3 (Public Review):

Summary:

Like many papers in the last 5-10 years, this work brings a computational approach to the study of promoters and transcription, but unfortunately disregards or misrepresents much of the existing literature and makes unwarranted claims of novelty. My main concerns with the current paper are outlined below although the problems are deeply embedded.

We thank Reviewer #3 for taking the time to review this manuscript. We have made extensive changes to address their concerns about our work.

Strengths:

The data could be useful if interpreted properly, taking into account i) the role of translation ii) other promoter elements, and iii) the relevant literature.

Weaknesses:

(1) Incorrect assumptions and oversimplification of promoters.

- There is a critical error on line 68 and Figure 1A. It is well established that the -35 element consensus is TTGACA but the authors state TTGAAA, which is also the sequence represented by the sequence logo shown and so presumably the PWM used. It is essential that the authors use the correct -35 motif/PWM/consensus. Likely, the authors have made this mistake because they have looked at DNA sequence logos generated from promoter alignments anchored by either the position of the -10 element or transcription start site (TSS), most likely the latter. The distance between the TSS and -10 varies. Fewer than half of E. coli promoters have the optimal 7 bp separation with distances of 8, 6, and 5 bp not being uncommon (PMID: 35241653). Furthermore, the distance between the -10 and -35 elements is also variable (16,17, and 18 bp spacings are all frequently found, PMID: 6310517). This means that alignments, used to generate sequence logos, have misaligned -35 hexamers. Consequently, the true consensus is not represented. If the alignment discrepancies are corrected, the true consensus emerges. This problem seems to permeate the whole study since this obviously incorrect consensus/motif has been used throughout to identify sequences that resemble -35 hexamers.

We respectfully but strongly disagree that our analysis has misrepresented the true nature of -35 boxes. First, accounting for more A’s at position 5 in the PWM is not going to lead to a “critical error.” This is because positions 4-6 of the motif barely have any information content (bits) compared to positions 1-3 (see Fig 1A). This assertion is not just based on our own PWM, but based on ample precedent in the literature. In PMID 14529615, TTG is present in 38% of all -35 boxes, but ACA only in 8%. In PMID 29388765, with the -10 instance TATAAT, the -35 instance TTGCAA yields stronger promoters compared to the -35 instance TTGACA (See their Figure 3B).

In PMID 29745856 (Figure 2), the most information content lies in positions 1-3, with the A and C at position 5 both nearly equally represented, as in our PWM. In PMID 33958766 (Figure 1) an experimentally-derived -35 box is even reduced to a “partial” -35 box which only includes positions 1 and 2, with consensus: TTnnnn.

In addition, we did not derive the PWMs as the reviewer describes. The PWMs we use are based on computational predictions that are in excellent agreement with experimental results. Specifically, the PWMs we use are from PMID 29728462, which acquired 145 -10 and -35 box sequences from the top 3.3% of computationally predicted boxes from Regulon DB. See PMID 14529615 for the computational pipeline that was used to derive the PWMs, which independently aligns the -10 and -35 boxes to create the consensus sequences. The -35 PWMs significantly and strongly correlates with an experimentally derived -35 box (see Supporting Information from Figure S4 of Belliveau et al., PNAS 2017. Pearson correlation coefficient = 0.89). Within the 145 -35 boxes, the exact consensus sequence (TTGACA) that Reviewer #3 is concerned about is present 6 times in our matrix, and has a PWM score above the significance threshold. In other words, TTGACA, is classified to be a -35 box in our dataset.

We now provide DNA sequences for each of the figures to improve accessibility and reproducibility. A reader can now use any PWM or method they wish to interpret the data.

- An uninformed person reading this paper would be led to believe that prokaryotic promoters have only two sequence elements: the -10 and -35 hexamers. This is because the authors completely ignore the role of the TG motif, UP element, and spacer region sequence. All of these can compensate for the lack of a strong -35 hexamer and it's known that appending such elements to a lone -10 sequence can create an active promoter (e.g. PMIDs 15118087, 21398630, 12907708, 16626282, 32297955). Very likely, some of the mutations, classified as not corresponding to a -10 or -35 element in Figure 2, target some of these other promoter motifs.

Thank you for bringing this oversight to our attention. We have performed two independent analyses to explore the role of TGn in promoter emergence in evolution. First, we computationally searched for -10 boxes with the bases TGn immediately upstream of them in the parent sequences, and found 18 of these “extended -10 boxes” in the parents (lines 143145):

“On average, each parent sequence contains ~5.32 -10 boxes and ~7.04 -35 boxes (Fig S1). 18 of these -10 boxes also include the TGn motif upstream of the hexamer.”

However, only 20% of these boxes were found in parents with promoter activity (lines 182-185):

“We also note that 30% (15/50) of parents have the TGn motif upstream of a -10 box, but only 20% (3/15) of these parents have promoter activity (underlined with promoter activity: P4-RFP, P6-RFP, P8-RFP, P9-RFP, P10-RFP, P11GFP, P12-GFP, P17-GFP, P18-GFP, P18-RFP, P19-RFP, P22-RFP, P24-GFP, P25-GFP, P25-RFP).”

Second, we computationally searched through all of the daughter sequences to identify new -10 boxes with TGn immediately upstream. We found 114 -10 boxes with the bases TGn upstream. However, only 5 new -10 boxes (2 with TGn) were associated with increasing fluorescence (lines 338-345):

“On average, 39.5 and 39.4 new -10 and -35 boxes emerged at unique positions within the daughter sequences of each mutagenized parent (Fig 3A,B), with 1’562 and 1’576 new locations for -10 boxes and -35 boxes, respectively. ~22% (684/3’138) of these new boxes are spaced 15-20 bp away from their cognate box, and ~7.3% (114/1’562) of the new -10 boxes have the TGn motif upstream of them. However, only a mere five of the new -10 boxes and four of the new 35 boxes are significantly associated with increasing fluorescence by more than +0.5 a.u. (Fig 3C,D).”

In addition, we now study the role of UP elements. This analysis showed that the UP element plays a negligible role in promoter emergence within our dataset.  It is discussed in a new subsection of the results (lines 591-608) and in the newly added Figure S13.

Collectively, these additional analyses suggest that the presence of TGn plus a -10 box is insufficient to create promoter activity, and that the UP element does not play a significant role in promoter emergence or evolution.

- The model in Figure 4C is highly unlikely. There is no evidence in the literature that RNAP can hang on with one "arm" in this way. In particular, structural work has shown that sequencespecific interactions with the -10 element can only occur after the DNA has been unwound (PMID: 22136875). Further, -10 elements alone, even if a perfect match to the consensus, are non-functional for transcription. This is because RNAP needs to be directed to the -10 by other promoter elements, or transcription factors. Only once correctly positioned, can RNAP stabilise DNA opening and make sequence-specific contacts with the -10 hexamer. This makes the notion that RNAP may interact with the -10 alone, using only domain 2 of sigma, extremely unlikely.

This is a valid criticism, and we thank the reviewer for catching this problem. In response, we have removed the model and pertinent figures throughout the entire manuscript.

(2) Reinventing the language used to describe promoters and binding sites for regulators.

- The authors needlessly complicate the narrative by using non-standard language. For example, On page 1 they define a motif as "a DNA sequence computationally predicted to be compatible with TF binding". They distinguish this from a binding site "because binding sites refer to a location where a TF binds the genome, rather than a DNA sequence". First, these definitions are needlessly complicated, why not just say "putative binding sites" and "known binding sites" respectively? Second, there is an obvious problem with the definitions; many "motifs" with also be "bindings sites". In fact, by the time the authors state their definitions, they have already fallen foul of this conflation; in the prior paragraph they stated: "controlled by DNA sequences that encode motifs for TFs to bind". The same issue reappears throughout the paper.

We agree that this was needlessly complicated. We now just refer to every sequence we study as a motif. A -10 box is a motif, a -35 box is a motif, a putative H-NS binding site is an H-NS motif, etc. The word “binding site” no longer occurs in the manuscript.

- The authors also use the terms "regulatory" and non-regulatory" DNA. These terms are not defined by the authors and make little sense. For instance, I assume the authors would describe promoter islands lacking transcriptional activity (itself an incorrect assumption, see below)as non-regulatory. However, as horizontally acquired sections of AT-rich DNA these will all be bound by H-NS and subject to gene silencing, both promoters for mRNA synthesis and spurious promoters inside genes that create untranslated RNAs. Hence, regulation is occurring.

Another fair point. We have thus changed the terminology throughout to “promoter” and “nonpromoter.”

- Line 63: "In prokaryotes, the primary regulatory sequences are called promoters". Promoters are not generally considered regulatory. Rather, it is adjacent or overlapping sites for TFs that are regulatory. There is a good discussion of the topic here (PMID: 32665585). 

We have rewritten this. The sentence now reads (lines 67-69):

“A canonical prokaryotic promoter recruits the RNA polymerase subunit σ70 to transcribe downstream sequences (Burgess et al., 1969; Huerta and Collado-Vides, 2003; Paget and Helmann, 2003; van Hijum et al., 2009).”

(3) The authors ignore the role of translation.

- The authors' assay does not measure promoter activity alone, this can only be tested by measuring the amount of RNA produced. Rather, the assay used measures the combined outputs of transcription and translation. If the DNA fragments they have cloned contain promoters with no appropriately positioned Shine-Dalgarno sequence then the authors will not detect GFP or RFP production, even though the promoter could be making an RNA (likely to be prematurely terminated by Rho, due to a lack of translation). This is known for promoters in promoter islands (e.g. Figure 1 in PMID: 33958766).

We agree that this is definitely a limitation of our study, which we had not discussed sufficiently. In response, we now discuss this limitation in a new section of the discussion (lines 680-686):

“Second, we measure protein expression through fluorescence as a readout for promoter activity. This readout combines transcription and translation. This means that we cannot differentiate between transcriptional and post-transcriptional regulation, including phenomena such as premature RNA termination (Song et al., 2022; Uptain and Chamberlin, 1997), post-transcriptional modifications (Mohanty and Kushner, 2006), and RNA-folding from riboswitch-like sequences (Mandal and Breaker, 2004).”

- In Figure S6 it appears that the is a strong bias for mutations resulting in RFP expression to be close to the 3' end of the fragment. Very likely, this occurs because this places the promoter closer to RFP and there are fewer opportunities for premature termination by Rho.

The reviewer raises a very interesting possibility. To validate it, we have performed the following analysis. We took the RFP expression values from the 9’934 daughters with single mutations in all 25 parent sequences (P1-RFP, P2-RFP, … P25-RFP), and plotted the location of the single mutation (horizontal axis) against RFP expression (vertical axis) in Author response image 2. 

Author response image 2.

The distribution is uniform across the sequences, showing that distance from the RBS is not likely the reason for this observation. Since this analysis was uninformative with respect to distance from the RBS, we chose not to include it in the manuscript.

(4) Ignoring or misrepresenting the literature.

- As eluded to above, promoter islands are large sections of horizontally acquired, high ATcontent, DNA. It is well known that such sequences are i) packed with promoters driving the expression on RNAs that aren't translated ii) silenced, albeit incompletely, by H-NS and iii) targeted by Rho which terminates untranslated RNA synthesis (PMIDs: 24449106, 28067866, 18487194). None of this is taken into account anywhere in the paper and it is highly likely that most, if not all, of the DNA sequences the authors have used contain promoters generating untranslated RNAs.

Thank you for pointing out that our original submission was incomplete in this regard. We address these concerns by new analyses, including some new experiments. First, Rhodependent termination is associated with the RUT motif, which is very rich in Cytosines (PMID: 30845912). Given that our sequences confer between 65%-78% of AT-content, canonical rhodependent termination is unlikely. However, we computationally searched for rho-dependent terminators using the available code from PMID: 30845912, but the algorithm did not identify any putative RUTs. Because this analysis was not informative, we did not include it in the paper.

We analyzed the role of H-NS on promoter emergence and evolution within our dataset using both experimental and computational approaches. These additional analyses are now shown in the newly-added Figure 5 and the newly-added Figure S12. We found that H-NS represses P22-GFP and P12-RFP and affects the bidirectionality of P20. More specifically, to analyze the effects of H-NS, we first compared the fluorescence levels of parent sequences in a Δhns background vs the wild-type (dh5α) background in Figure 5A. We found 6 candidate H-NS targets, with P22-GFP and P12-RFP exhibiting the largest changes in fluorescence (lines 496506):

“We plot the fluorescence changes in Fig 5A as distributions for the 50 parents, where positive and negative values correspond to an increase or decrease in fluorescence in the Δhns background, respectively. Based on the null hypothesis that the parents are not regulated by H-NS, we classified outliers in these distributions (1.5 × the interquartile range) as H-NS-target candidates. We refer to these outliers as “candidates” because the fluorescence changes could also result from indirect trans-effects from the knockout (Mattioli et al., 2020; Metzger et al., 2016). This approach identified 6 candidates for H-NS targets (P2-GFP, P19-GFP, P20-GFP, P22-GFP, P12-RFP, and P20-RFP). For GFP, the largest change occurs in P22-GFP, increasing fluorescence ~1.6-fold in the mutant background (two-tailed t-test, p=1.16×10-8) (Fig 5B). For RFP, the largest change occurs in P12-RFP, increasing fluorescence ~0.5-fold in the mutant background (two-tailed t-test, p=4.33×10-10) (Fig 5B).” 

We also observed that the Δhns background affected the bidirectionality of P20 (lines 507-511):

“We note that for template P20, which is a bidirectional promoter, GFP expression increases ~2.6-fold in the Δhns background (two-tailed t-test, p=1.59×10-6). Simultaneously, RFP expression decreases ~0.42-fold in the Δhns background (two-tailed t-test, p=4.77×10-4) (Fig S12A). These findings suggest that H-NS also modulates the directionality of P20’s bidirectional promoter through either cis- or trans-effects.”

We then searched for regions where losing H-NS motifs in hotspots significantly changed fluorescence. We identified 3 motifs in P12-RFP and P22-GFP (lines 522-528):

“For P22-GFP, a H-NS motif lies 77 bp upstream of the mapped promoter. Mutations which destroy this motif significantly increase fluorescence by +0.52 a.u. (two-tailed MWU test, q=1.07×10-3) (Fig 5E). For P12-RFP, one H-NS motif lies upstream of the mapped promoter’s -35 box, and the other upstream of the mapped promoter’s -10 box. Mutations that destroy these H-NS motifs significantly increase fluorescence by +0.53 and +0.51 a.u., respectively (two-tailed MWU test, q=3.28×10-40 and q=4.42 ×10-50) (Fig 5F,G). Based on these findings, we conclude that these motifs are bound by H-NS.”

We are grateful for the suggestion to look at the role of H-NS in our dataset. Our analysis revealed a more plausible explanation to what we formerly referred to as a “Tandem Motif” in the original submission. Previously, we had shown that in P12-RFP, when a -35 box is created next to the promoter’s -35 box, or a -10 box next to the promoter’s -10 box, that expression decreases. These new -10 and -35 boxes, however, also overlap with the two H-NS motifs in P12-RFP. We tested these exact point mutations in reporter plasmids and in the Δhns background, and found that the Δhns background rescues this loss in expression (see Figure S12). This analysis is in the newly added subsection: “The binding of H-NS changes when new 10 and -35 boxes are gained” and can be found at lines 529-563. We summarize the findings in a final paragraph of the section (lines 556-563):

“To summarize, we present evidence that H-NS represses both P22-GFP and P12-RFP in cis. H-NS also modulates the bidirectionality of P20-GFP/RFP in cis or trans. In P22-GFP, the strongest H-NS motif lies upstream of the promoter. In P12-RFP, the strongest H-NS motifs lie  upstream of the -10 and -35 boxes of the promoter. We note that there are 16 additional H-NS motifs surrounding the promoter in P12-RFP that may also regulate P12-RFP (Fig S12G). Mutations in two of these two H-NS motifs can create additional -10 and -35 boxes that appear to lower expression. However, the effects of these mutations are insignificant in the absence of H-NS, suggesting that these mutations actually modulate H-NS binding.”

We also agree that the majority of these sequences are likely driving the expression of many untranslated RNAs (see Purtov et al., 2014). We thus now define a promoter more carefully as follows (lines 113-119):

“In this study, we define a promoter as a DNA sequence that drives the expression of a (fluorescent) protein whose expression level, measured by its fluorescence, is greater than a defined threshold. We use a threshold of 1.5 arbitrary units (a.u.) of fluorescence. This definition does not distinguish between transcription and translation. We chose it because protein expression is usually more important than RNA expression whenever natural selection acts on gene expression, because it is the primary phenotype visible to natural selection (Jiang et al., 2023).” 

We also state this as a limitation of our study in the Discussion (lines 680-686):

“Second, we measure protein expression through fluorescence as a readout for promoter activity. This readout combines transcription and translation. This means that we cannot differentiate between transcriptional and post-transcriptional regulation, including phenomena such as premature RNA termination (Song et al., 2022; Uptain and Chamberlin, 1997), post-transcriptional modifications (Mohanty and Kushner, 2006), and RNA-folding from riboswitch-like sequences (Mandal and Breaker, 2004).”

- The authors state that GC content does not correlate with the emergence of new promoters. It is known that GC content does correlate to the emergence of new promoters because promoters are themselves AT-rich DNA sequences (e.g. see Figure 1 of PMID: 32297955). There are two reasons the authors see no correlation in this work. First, the DNA sequences they have used are already very AT-rich (between 65 % and 78 % AT-content). Second, they have only examined a small range of different AT-content DNA (i.e. between 65 % and 78 %). The effect of AT-content on promoter emerge is most clearly seen between AT-content of between around 40 % and 60 %. Above that level, the strong positive correlation plateaus.

We respectfully disagree that the reviewer’s point is pertinent because what the reviewer is referring to is the likelihood that the sequence is a promoter, which indeed increases with AT content, but we are focused on the likelihood that a sequence becomes a promoter through DNA mutation. We note that if a DNA sequence is more AT-rich, then it is more likely to have -10 and -35 boxes, because their consensus sequences are also AT-rich. However, H-NS and other transcriptional repressors also bind to AT-rich sequences. This could also explain the saturation observed above 60% AT-content in PMID 32297955. Perhaps we can address this trend in future works.

- Once these authors better include and connect their results to the previous literature, they can also add some discussion of how previous papers in recent years may have also missed some of this important context.

We apologize for this oversight. We have rewritten the Discussion section to include the following points below. Many of the newly added references come from the group of David Grainger, who works on H-NS repression, bidirectional promoters, promoter emergence, promoter motifs, and spurious transcription in E. coli. More specifically:

(1) The role of pervasive transcription and the likelihood of promoter emergence (lines 614-621):

“Instead, we present evidence that promoter emergence is best predicted by the level of background transcription each non-promoter parent produces, a phenomenon also referred to as “pervasive transcription” (Kapranov et al., 2007).

From an evolutionary perspective, this would suggest that sequences that produce such pervasive transcripts – including the promoter islands (Panyukov and Ozoline, 2013) and the antisense strand of existing promoters (Dornenburg et al., 2010; Warman et al., 2021), may have a proclivity for evolving de-novo promoters compared to other sequences (Kapranov et al., 2007; Wade and Grainger, 2014).”

(2) How our results contradict the findings from Bykov et al., 2020 (lines 622-640):

“A previous study randomly mutagenized the appY promoter island upstream of a GFP reporter, and isolated variants with increased and decreased GFP expression. The authors found that variants with higher GFP expression acquired mutations that 1) improve a -10 box to better match its consensus, and simultaneously 2) destroy other -10 and -35 boxes (Bykov et al., 2020). The authors concluded that additional -10 and -35 boxes repress expression driven by promoter islands. Our data challenge this conclusion in several ways. 

First, we find that only ~13% of -10 and -35 boxes in promoter islands actually contribute to promoter activity. Extrapolating this percentage to the appY promoter island, ~87% (100% - 13%) of the motifs would not be contributing to its activity. Assuming the appY promoter island is not an outlier, this would insinuate that during random mutagenesis, these inert motifs might have accumulated mutations that do not change fluorescence. Indeed, Bykov et al. (Bykov et al., 2020) also found that a similar frequency of -10 and -35 boxes were destroyed in variants selected for lower GFP expression, which supports this argument. Second, we find no evidence that creating a -10 or -35 box lowers promoter activity in any of our 50 parent sequences. Third, we also find no evidence that destruction of a -10 or -35 box increases promoter activity without plausible alternative explanations, i.e. overlap of the destroyed box with a H-NS site, destruction of the promoter, or simultaneous creation of another motif as a result of the destruction. In sum, -10 and 35 boxes are not likely to repress promoter activity.”

(3) How other sequence features besides the -10 and -35 boxes may influence promoter emergence and activity (lines 661-671):

“These findings suggest that we are still underestimating the complexity of promoters. For instance, the -10 and -35 boxes, extended -10, and the UP-element may be one of many components underlying promoter architecture. Other components may include flanking sequences (Mitchell et al., 2003), which have been observed to play an important role in eukaryotic transcriptional regulation (Afek et al., 2014; Chiu et al., 2022; Farley et al., 2015; Gordân et al., 2013). Recent studies on E. coli promoters even characterize an AT-rich motif within the spacer sequence (Warman et al., 2020), and other studies use longer -10 and -35 box consensus sequences (Lagator et al., 2022). Another possibility is that there is much more transcriptional repression in the genome than anticipated (Singh et al., 2014). This would also coincide with the observed repression of H-NS in P22-GFP and P12-RFP, and accounts of H-NSrepression in the full promoter island sequences (Purtov et al., 2014).”

(4) The limits of our experimental methodology (lines 675-686):

“Additionally, future studies will be necessary to address the limitations of our own work. First, we use binary thresholding to determine i) the presence or absence of a motif, ii) whether a sequence has promoter activity or not, and iii) whether a part of a sequence is a hotspot or not. While chosen systematically, the thresholds we use for these decisions may cause us to miss subtle but important aspects of promoter evolution and emergence. Second, we measure protein expression through fluorescence as a readout for promoter activity. This readout combines transcription and translation. This means that we cannot differentiate between transcriptional and post-transcriptional regulation, including phenomena such as premature RNA termination (Song et al., 2022; Uptain and Chamberlin, 1997), posttranscriptional modifications (Mohanty and Kushner, 2006), and RNA-folding from riboswitch-like sequences (Mandal and Breaker, 2004) “

(5) An updated take-home message (lines 687-694):

“Overall, our study demonstrates that -10 and -35 boxes neither prevent existing promoters from driving expression, nor do they prevent new promoters from emerging by mutation. It shows how mutations can create new -10 and -35 boxes near or on top of preexisting ones to modulate expression. However, randomly creating a new -10 or -35 box will rarely create a new promoter, even if the new box is appropriately spaced upstream or downstream of a cognate box. Ultimately our study demonstrates that promoter models need to be further scrutinized, and that using mutagenesis to create de-novo promoters can provide new insights into promoter regulatory logic.”

(5) Lack of information about sequences used and mutations.

- To properly assess the work any reader will need access to the sequences cloned at the start of the work, where known TSSs are within these sequences (ideally +/- H-NS, which will silence transcription in the chromosomal context but may not when the sequences are removed from their natural context and placed in a plasmid). Without this information, it is impossible to assess the validity of the authors' work.

Thank you for raising this point. Please see Data S1 for the 25 template sequences (P1-P25) used in this study, and Data S2 for all of the daughter sequences.

For brevity, we have addressed the reviewer’s request to look at the role of H-NS in their comment (4) “Ignoring or misrepresenting the literature.”

We do not have information about the predicted transcription start sites (TSS) for the parent sequences because the program which identified them (Platprom) is no longer available. Regardless, having TSS coordinates would not validate or invalidate our findings, since we already know that the promoter islands produce short transcripts throughout their sequences, and we are primarily interested in promoters which can produce complete transcripts.

- The authors do not account for the possibility that DNA sequences in the plasmid, on either side of the cloned DNA fragment, could resemble promoter elements. If this is the case, then mutations in the cloned DNA will create promoters by "pairing up" with the plasmid sequences. There is insufficient information about the DNA sequences cloned, the mutations identified, or the plasmid, to determine if this is the case. It is possible that this also accounts for mutational hotspots described in the paper.

We agree that these are important points. To address the criticism that we provided insufficient information, we now redesigned all our figures to provide this information. Specifically, the figures now include the DNA sequences, their PWM predictions, and the exact mutations that lead to promoter activity. The figures with these changes are Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12. We now also provide more details about pMR1 in a new section of the methods (lines 740-748):

“Plasmid MR1 (pMR1)

The plasmid MR1 (pMR1) is a variant of the plasmid RV2 (pRV2) in which the kan resistance gene has been swapped with the cm resistance gene (Guazzaroni and Silva-Rocha, 2014). Plasmid pMR1 encodes the BBa_J34801 ribosomal binding site (RBS, AAAGAGGAGAAA) 6 bp upstream of the start codon for GFP(LVA). The plasmid also encodes a putative RBS (AAGGGAGG) (Cazemier et al., 1999) 5 bp upstream of the start codon for mCherry on the opposite strand.

The plasmid additionally contains the low-to-medium copy number origin of replication p15A (Westmann et al., 2018).

A map of the plasmid is available on the Github repository: https://github.com/tfuqua95/promoter_islands “

The reviewer also makes a valid point about promoter elements of the plasmid itself. We addressed it with the following new analyses. First we re-examined each of the examples where new -10 and -35 boxes are gained or lost, to see if any of these hotspots occur on the flanking ends of the parent sequences. We looked specifically at the ends because they could potentially interact with -10 and -35 box-like sequences on the plasmid to form a promoter. 

Only one of these hotspots (out of 27) occurred at the end of the cloned sequences, and is thus a candidate for the phenomenon the reviewer hypothesized. This hotspot occurs in P9-GFP, where gaining a -10 box at the left flank increases expression (see Figure S8E-F’). There is indeed a -35 box 22-23 bp upstream of this -10 box on the plasmid, which could potentially affect promoter activity. 

We tested the GFP expression of a construct harboring the point mutation which creates this -10 box on the left flank of P9-GFP. However, there was no significant difference in fluorescence between this construct and the wile-type P9-GFP (see Figure S8E-F’). Thus, this -35 box on pMR1 is not likely creating a new promoter.

(6) Overselling the conclusions.

Line 420: The paper claims to have generated important new insights into promoters. At the same time, the main conclusion is that "Our study demonstrates that mutations to -10 and -35 boxes motifs are the primary paths to create new promoters and to modulate the activity of existing promoters". This isn't new or unexpected. People have been doing experiments showing this for decades. Of course, mutations that make or destroy promoter elements create and destroy promoters. How could it be any other way?

In hindsight, we agree that the original conclusion was not very novel. Our new conclusion is that -10 and -35 boxes do not repress transcription, and that our current promoter models, even with the additional motifs like the UP-element and the extended -10, are insufficient to understand promoters (lines 687-694):

“Overall, our study demonstrates that -10 and -35 boxes neither prevent existing promoters from driving expression, nor do they prevent new promoters from emerging by mutation. It shows how mutations can create new -10 and -35 boxes near or on top of preexisting ones to modulate expression. However, randomly creating a new -10 or -35 box will rarely create a new promoter, even if the new box is appropriately spaced upstream or downstream of a cognate box. Ultimately our study demonstrates that promoter models need to be further scrutinized, and that using mutagenesis to create de-novo promoters can provide new insights into promoter regulatory logic.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I would like to start by thanking the authors for presenting an interesting and well-written article for review. This paper is a welcome addition to the field, addressing modern questions in the longstanding area of bacterial gene regulation. It is both enlightening and inspiring. While I do have suggestions, I hope these are not perceived as a lack of optimism for the work.

Thank you for your kind words and suggestions, and for providing an astute and constructive review. We feel that manuscript has greatly improved with your suggested changes.

ABSTRACT:

Line 11: The sentence, "It is possible that these motifs influence..." Could be rewritten to be clearer as it is the most important point of the manuscript. It is not obvious that you're talking about how the local landscape of motifs affects the probability of promoters evolving/devolving in this location.

We have changed the sentence to read, “Here, we ask whether the presence of such motifs in different genetic sequences influences promoter evolution and emergence.”

INTRODUCTION:

Line 68: Is the -35 consensus motif not TTGACA? Here it is listed as TTGAAA.

Corrected from TTGAAA to TTGACA

RESULTS:

Line 92-94. In finding that the. The main takeaway from this work is that different sequences have different likelihoods of mutations creating promoters and so I believe this claim could be explored deeper with more quantitative information. Could the authors supplement this claim by including? Could you look at whether there is a correlation between the baseline expression of a parent sequence and Pnew? I expect even the inactive sequences to have some variability in measured expression.

Thank you for this great idea. We followed up on it by plotting the baseline parent sequence fluorescence scores against Pnew. You are indeed correct, i.e., Pnew increases with baseline expression following a sigmoid function, and is now shown in Figure 1D. To report our new observations, we have added the following section to the Results (lines 219-232):

“Although mutating each of the 40 non-promoter parent sequences could create promoter activity, the likelihood Pnew that a mutant has promoter activity, varies dramatically among parents. For each non-promoter parent, Fig 1D shows the percentage of active daughter sequences. The median Pnew is 0.046 (std. ± 0.078), meaning that ~4.6% of all mutants have promoter activity. The lowest Pnew is 0.002 (P25-GFP) and the highest 0.41 (P8-RFP), a 205-fold difference.

We hypothesized that these large differences in Pnew could be explained by minute differences in the fluorescence scores of each parent, particularly if its score was below 1.5 a.u. Plotting the fluorescence scores of each parent (N=50) and their respective Pnew values as a scatterplot (Fig 1E), we can fit these values to a sigmoid curve (see methods). This finding helps to explain why P8-RFP has a high Pnew (0.41) and P25-GFP a low Pnew (0.002), as their fluorescence scores are 1.380 and 1.009 a.u., respectively. The fact that the inflection point of the fitted curve is at 1.51 a.u. further justifies our use of 1.5 a.u. as a cutoff for promoter and non-promoter activity.”

Another potentially interesting analysis would be to see if k-mer content is correlated with Pnew. That is, determine the abundance of all hexamers in the sequence and see if Pnew is correlated with the number of hexamers present that is one nucleotide distance away from the consensus motifs (such as TcGACA or TAcAAT).

We performed the suggested analysis by searching for k-mers that correlate with Pnew and found that no k-mer significantly correlates with Pnew (lines 240-248):

“We then asked whether any k-mers ranging from 1-6 bp correlated with the non-promoter Pnew values (5,460 possible k-mers). 718 of these 1-6 bp k-mers are present 3 or more times in at least one non-promoter parent. We calculated a linear regression between the frequency of these 718 k-mers and each Pnew value, and adjusted the p-values to respective q-values (Benjamini-Hochberg correction, FDR=0.05). This analysis revealed six k-mers: CTTC, GTTG,

ACTTC, GTTGA, AACTTC, TAACTT which correlate with Pnew. However, these correlations are heavily influenced by an outlying Pnew value of 0.41 (P8-RFP) (Fig S5C-H), and upon removing P8-RFP from the analysis, no k-mer significantly correlates with Pnew (data not shown)”

Line 152-157: How did you define the thresholds for 'active' or 'inactive'? It is not clear in the methods how this distinction was made.

We have more clearly defined these thresholds in the text. A sequence with promoter activity has a fluorescence score greater than 1.5 a.u. (lines 168-172):

“We declared a daughter sequence to have promoter activity or to be a promoter if its score was greater than or equal to 1.5 a.u., as this score lies at the boundary between no fluorescence and weak fluorescence based on the sort-seq bins (methods). Otherwise, we refer to a daughter sequence as having no promoter activity or being a non-promoter.”

Lines: 152-157: In trying to find the parent expression levels, no figure was available showing the distribution of parent expression levels. Furthermore, In looking at Data S2 & filtering out for sequences with distance 0 from the parent, I found the most active sequences did not match up with the sequences described as active in this section (e.g. p19 and p20 have a higher topstrand mean over P22, yet are not listed as active top strand sequences).

We really appreciate you taking the time to examine the supplemental data. We previously listed the parents that had only GFP activity but no RFP activity (P22), and only RFP activity but no GFP activity (P6, P12, P13, P18, P21). We then said that P19 and P20 were bidirectional promoters, because they showed both GFP and RFP activity. In hindsight, we realize that our wording was confusing. We thus rewrote the affected paragraph, such that the bidirectional promoters are now in both lists of GFP/RFP active parents. We also now make the distinction between “templates” which comprise our 25 promoter island fragments, and “parents”, where we treat both strands separately (50 parents total). The paragraph in question now reads (lines 173-187):

“Because some sequences in our library are unmutated parent sequences, we determined that 10/50 of the parent sequences already encode promoter activity before mutagenesis. Specifically, three parents drove expression on the top strand (P19-GFP, P20-GFP, P22-GFP), and five did on the bottom strand (P6-RFP, P12-RFP, P13-RFP, P18-RFP, P19-RFP, P20-RFP, P21-RFP). Two parents harbor bidirectional promoters (P19 and P20). The remaining 40 parent sequences are non-promoters, with an average fluorescence score of 1.39 a.u. We note that some of these parents have a fluorescence score higher than 1.39 a.u., but less than 1.50 a.u. such as P8-RFP (1.38 a.u.), P16-RFP (1.39 a.u.), P9-GFP (1.49 a.u.), and P1-GFP (1.47 a.u.). Whether these are truly “promoters” or not, is based solely on our threshold value of 1.5 a.u. We also note that 30% (15/50) of parents have the TGn motif upstream of a -10 box, but only 20% (3/15) of these parents have promoter activity (underlined with promoter activity: P4-RFP, P6-RFP, P8-RFP, P9RFP, P10-RFP, P11-GFP, P12-GFP, P17-GFP, P18-GFP, P18-RFP, P19-RFP, P22-RFP, P24-GFP, P25-GFP, P25RFP). See Fig S4 for fluorescence score distributions for each parent and its daughters, and Data S2 for all daughter sequence fluorescence scores.”

Please include a supplementary figure showing the different parent expression levels (GFP mean +/- sd). Also, please explain the discrepancy in the 'active sequences' compared to Data S2 or correct my misunderstanding.

We have added this plot to Figure S4B. The discrepancy arose because we listed the parents that had only GFP activity but no RFP activity (P22), and only RFP activity but no GFP activity (P6, P12, P13, P18, P21). We then said that P19 and P20 were bidirectional promoters, because they showed both GFP and RFP activity. previous response regarding the ambiguity.

Line 182: I do not see 'Fuqua and Wagner 2023' in the references (though I am familiar with the preprint).

We have added Fuqua and Wagner, BiorXiv 2023 to the references.

Lines 197 - 200: The distribution of hotspot locations should be compared to the distribution of mutations in the library. e.g. It is not notable that 17% of mutations are in -10 motifs if 17% of all mutations are in -10 motifs.

Thank you for raising this point. To address it, we carried out a computational analysis where we randomly scrambled the nucleotides of each parent sequence while maintaining the coordinates for each mutual information “hotspot.” This scrambling results in significantly less overlap with hotspots and boxes. This analysis is now depicted in Figure 2C and written in lines 272-296.

Lines 253-264: Examples 3B, 3D, and 3F should indicate the spacing between the new and existing motifs. Are these close to the 15-19 bp spacer lengths preferred by sigma70?

Point well taken. We now annotate the spacing of motifs in Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, and S11. We note that in many cases, high-scoring PWM hits for the same motif can overlap (i.e. two -10 motifs or two -35 motifs overlap). Additionally, the proximity of a 35 and -10 box does not guarantee that the two boxes are interacting. Together, these two facts can result in an ambiguity of the spacer size between two boxes. To avoid any reporting bias, we thus often report spacer sizes as a range (see Figure panels 4F, S8D, S8F-L, S9A, S9H, S10A, and S10E). The smallest spacer we annotate is in Figure 4F with 10 bp, and the largest is in Figure S8D with 26 bp. Any more “extreme” distances are not annotated, and for the reader to decide if an interaction is present or not.

Line 255: While fun, I am concerned about the 'Shiko' analogy. My understanding is the prevailing theory is that -35 recognition occurs before -10 recognition (https://doi.org/10.1073/pnas.94.17.9022, 10.1101/sqb.1998.63.141). Given this, the 'Shiko -35' concept in 3H is a bit awkward as it suggests that sigma70 stops at -10 motifs before planting down on the -35. Considering the cited paper is still in the preprint stages (and did not observe these Shiko -35 emergences), I am concerned about how this particular example will be received by the community. Perhaps more care could be done to verify that this example is consistent with generally accepted mechanisms of promoter recognition or a short clarification could be added to clarify the extent of the analogy.

Thank you for raising this point. We decided to remove the Shiko analogy, because several readers assumed that it relates to the physical binding of RNA polymerase, rather than being an evolutionary mechanism of mutations forming complementary motifs in a stepwise manner.

Lines 323-326: It would be helpful to describe a more systematic approach to defining emergence events into different categories. A clear definition of each category in the methods or main text would help others consistently refer to these concepts in the future. This could be helped by showing the actual parent vs daughter sequences as a supplementary figure to figures 4B, 4D, & 4G.

We agree this could have been more clearly communicated. We have addressed this by 1) simplifying the nomenclatures of these categories and  2) clearly defining these categories, and 3) showing the actual parent vs daughter sequences in Figure 4, and Supplemental Figures S9, S10, S11, and S12. More specifically:

(1) Simplifying the nomenclature. We highlight events where gaining new -10 and -35 boxes can modify the promoter activity of parent sequences with promoter activity. This occurs when a new -10 or -35 box appears that partially overlaps with the -10 or -35 box of the actual promoter. Thus, we rename two terms: hetero-gain and homo-gain, shown in Figure 4B:

(2) We clearly define these categories (lines 430-435):

“We found that these mutations frequently create new boxes overlapping those we had identified as part of a promoter (Fig S9). This occurs when mutations create a -10 box overlapping a -10 box, a -35 box overlapping a 35 box, a -10 box overlapping a -35 box, or a -35 box overlapping a -10 box. We call the resulting event a “homogain” when the new box is of the same type as the one it overlaps, and otherwise a “hetero-gain”. In either case, the creation of the new box does not always destroy the original box.”

In the original manuscript, there was an additional third category, where gaining a -35 box upstream of the promoter’s -35 box, and gaining a -10 box upstream of the promoter’s -10 box decreased expression. We referred to this as a “tandem motif” and it can be found in Figure S12C,D. However, in response to comment “(4) Ignoring or misrepresenting the literature” from Reviewer #3, we carried out an analysis of the binding of H-NS (see Figure 5 and Figure S12). This analysis revealed that this “tandem motif” phenomenon was actually the result of changing the affinity of H-NS to these regions. Thus, the “tandem motif” is probably spurious.

DISCUSSION:

Line 378-379: Since hotspots are essentially areas where promoters appear, wouldn't it be obvious that having more hotspots (i.e. areas where more promoters appear) would equate to a higher probability of new promoters? It would be helpful to clarify why this isn't obvious. This could be resolved by adding more complexity to the statement, such as showing that the level of mutual information found in a hotspot or across all hotspots in a sequence is correlated with Pnew.

A fair criticism. In response, we have chosen to remove the analysis of this trend from the manuscript entirely. (Additionally, Pnew and mutual information calculations both relied on the fluorescence scores of daughter sequences, so the finding was circular in its logic.)

Line 394-396: This comparison of findings to Bykov et al should include a bit more justification for the proposed mechanism and how it specifically was observed in this paper. What did they observe and how do these findings relate?

We gladly followed this suggestion, and added the following two paragraphs to the discussion (lines 622-640).

“A previous study randomly mutagenized the appY promoter island upstream of a GFP reporter, and isolated variants with increased and decreased GFP expression. The authors found that variants with higher GFP expression acquired mutations that 1) improve a -10 box to better match its consensus, and simultaneously 2) destroy other -10 and -35 boxes (Bykov et al., 2020). The authors concluded that additional -10 and -35 boxes repress expression driven by promoter islands. Our data challenge this conclusion in several ways. 

First, we find that only ~13% of -10 and -35 boxes in promoter islands actually contribute to promoter activity. Extrapolating this percentage to the appY promoter island, ~87% (100% - 13%) of the motifs would not be contributing to its activity. Assuming the appY promoter island is not an outlier, this would insinuate that during random mutagenesis, these inert motifs might have accumulated mutations that do not change fluorescence. Indeed, Bykov et al. (Bykov et al., 2020) also found that a similar frequency of -10 and -35 boxes were destroyed in variants selected for lower GFP expression, which supports this argument. Second, we find no evidence that creating a -10 or -35 box lowers promoter activity in any of our 50 parent sequences. Third, we also find no evidence that destruction of a -10 or -35 box increases promoter activity without plausible alternative explanations, i.e. overlap of the destroyed box with a H-NS site, destruction of the promoter, or simultaneous creation of another motif as a result of the destruction. In sum, -10 and 35 boxes are not likely to repress promoter activity. “

METHODS:

Line 500: Could you provide more details on PMR1 (e.g. size, copy number, RBS strength) or a reference? I could not find this easily.

Thank you for pointing out this oversight. In response, we have added the following subsection to the methods (lines 740-748):

“Plasmid MR1 (pMR1)

The plasmid MR1 (pMR1) is a variant of the plasmid RV2 (pRV2) in which the kan resistance gene has been swapped with the cm resistance gene (Guazzaroni and Silva-Rocha, 2014). Plasmid pMR1 encodes the BBa_J34801 ribosomal binding site (RBS, AAAGAGGAGAAA) 6 bp upstream of the start codon for GFP(LVA). The plasmid also encodes a putative RBS (AAGGGAGG) (Cazemier et al., 1999) 5 bp upstream of the start codon for mCherry on the opposite strand.

The plasmid additionally contains the low-to-medium copy number origin of replication p15A (Westmann et al., 2018).

A map of the plasmid is available on the Github repository: https://github.com/tfuqua95/promoter_islands.”

Line 581: What was the sequencing instrument &/or depth?

We now report this information as follows (Methods, lines 918-922):

“Illumina sequencing

The amplicon pool was sequenced by Eurofins Genomics (Eurofins GmbH, Germany) using a NovaSeq 6000 (Illumina, USA) sequencer, with an S4 flow cell, and a PE150 (Paired-end 150 bp) run. In total, 282’843’000 reads and 84’852’900’000 bases were sequenced. Raw sequencing reads can be found here: https://www.ncbi.nlm.nih.gov/bioproject/1071572.”

SUPPLEMENT:

Supplementary Figure 2: Why does the GFP control produce a bimodal distribution?

The GFP+ culture was inoculated directly from a glycerol stock. The bimodal distribution probably results from a subset of the bacteria having lost the GFP-coding insert, because the left-most peak coincides with the negative control.

Reviewer #2 (Recommendations For The Authors):

This paper would benefit from a clear definition of what constitutes an active promoter as this is only mentioned as justification for the use of arbitrary values for fluorescence.

Good point. To clarify, we now include this new paragraph in the introduction (lines 112-119):

“In this study, we define a promoter as a DNA sequence that drives the expression of a (fluorescent) protein whose expression level, measured by its fluorescence, is greater than a defined threshold. We use a threshold of 1.5 arbitrary units (a.u.) of fluorescence. This definition does not distinguish between transcription and translation. We chose it because protein expression is usually more important than RNA expression whenever natural selection acts on gene expression, because it is the primary phenotype visible to natural selection (Jiang et al., 2023).”

There needs to be a clear distinction in the use of the word sequences as often interchange sequences when meaning the 25 parent sequences and then the 50 possible sequences directions the promoter can act. It is confusing going from one to the other.

We agree that this distinction is important. To make it clearer, we now introduce an additional term (lines 119-130). Our experiments start from 25 promoter island fragments (P1-P25), which we now call template sequences. Each template sequence comprises both DNA strands. The parent sequences are the top and bottom strands of each template sequence. Therefore, there are now 50 parent sequences (P1-GFP, P1-RFP, P2-GFP…, P25-RFP). By treating each strand as its own sequence, we no longer have to refer to the strand, avoiding the earlier confusion.

The description of the hotspots is often unclear and trying to determine if 3 out of 9 hotspots come from one parent sequence or multiple is not possible. A table denoting this information would be most helpful.

We agree, and now provide this information in Data S3.

Finally, the description of the proposed mechanism of promoter activation via mutation of motifs should not be in the results but in the discussion, as it has insufficient evidence and would require further experimental validation.

We remedied this problem by providing experimental validation of the proposed mechanisms. Specifically, we created the precise mutations that caused a loss or gain of a -10 or a -35 box, and measured the level of gene expression they drive with a plate reader. Because we chose to provide this experimental validation, we opted to leave the mechanisms of promoter activation in the results section.

The (Fuqua and Wagner 20023) paper is not in the references.

We have added Fuqua and Wagner, BiorXiv 2023 to the references.

I enjoyed the paper and wish the authors the best for their future work.

Thank you for taking the time to review our manuscript!

Reviewer #3 (Recommendations For The Authors):

The paper has major flaws. For example:

The data need to be analysed with correct promoter sequence element sequences (TTGACA for the -35 element).

The discrepancy lies in the frequency of A’s vs C’s at position #5 of the PWM. Our PWM was built with more A’s than C’s at this position, but also includes C’s in this position. However, we respectfully disagree that using a different -35 box PWM is going to change the outcomes of our study. First, positions 4-6 of the PWM barely have any information content (bits) compared to positions 1-3 (see Fig 1A). This assertion is not just based on our own PWM, but based on ample precedent in the literature. In PMID 14529615, TTG is present in 38% of all -35 boxes, but ACA only 8%. In PMID 29388765, with the -10 instance TATAAT, the -35 instance TTGCAA yields stronger promoters compared to the -35 instance TTGACA (See their Figure 3B). In PMID 29745856 (Figure 2), the most information content lies in positions 1-3, with the A and C at position 5 both nearly equally represented, as in our PWM. In PMID 33958766 (Figure 1) an experimentally-derived -35 box is even reduced to a “partial” -35 box which only includes positions 1 and 2, with consensus: TTnnnn. Additionally, the -35 box PWM that we used significantly and strongly correlates with an experimentally derived -35 box (see Supporting Information from Figure S4 of Belliveau et al., PNAS 2017. Pearson correlation coefficient = 0.89). We now provide DNA sequences for each of the figures to improve accessibility and reproducibility. A reader can now use any PWM or method they wish to interpret the data.

The data need to be analysed taking into account the role of other promoter elements and sequences for translation.

Point well taken. 

Thank you for bringing this oversight to our attention. We have performed two independent analyses to explore the role of TGn in promoter emergence in evolution. First, we computationally searched for -10 boxes with the bases TGn immediately upstream of them in the parent sequences, and found 18 of these “extended -10 boxes” in the parents (lines 143145):

“On average, each parent sequence contains ~5.32 -10 boxes and ~7.04 -35 boxes (Fig S1). 18 of these -10 boxes also include the TGn motif upstream of the hexamer.”

However, only 20% of these boxes were found in parents with promoter activity (lines 182-185):

“We also note that 30% (15/50) of parents have the TGn motif upstream of a -10 box, but only 20% (3/15) of these parents have promoter activity (underlined with promoter activity: P4-RFP, P6-RFP, P8-RFP, P9-RFP, P10-RFP, P11GFP, P12-GFP, P17-GFP, P18-GFP, P18-RFP, P19-RFP, P22-RFP, P24-GFP, P25-GFP, P25-RFP).” 

Second, we computationally searched through all of the daughter sequences to identify new -10 boxes with TGn immediately upstream. We found 114 -10 boxes with the bases TGn upstream. However, only 5 new -10 boxes (2 with TGn) were associated with increasing fluorescence (lines 338-345):

“Mutations indeed created many new -10 and -35 boxes in our daughter sequences. On average, 39.5 and 39.4 new 10 and -35 boxes emerged at unique positions within the daughter sequences of each mutagenized parent (Fig 3A,B), with 1’562 and 1’576 new locations for -10 boxes and -35 boxes, respectively. ~22% (684/3’138) of these new boxes are spaced 15-20 bp away from their cognate box, and ~7.3% (114/1’562) of the new -10 boxes have the TGn motif upstream of them. However, only a mere five of the new -10 boxes and four of the new -35 boxes are significantly associated with increasing fluorescence by more than +0.5 a.u. (Fig 3C,D).”

In addition, we now study the role of UP elements. This analysis showed that the UP element plays a negligible role in promoter emergence within our dataset.  It is discussed in a new subsection of the results (lines 591-608).

“The UP-element does not strongly influence promoter activity in our dataset.

The UP element is an additional AT-rich promoter motif that can lie stream of a -35 box in a promoter sequence (Estrem et al., 1998; Ross et al., 1993). We asked whether the creation of UP-elements also creates or modulates promoter activity in our dataset. To this end, we first identified a previously characterized position-weight matrix for the UP element (NNAAAWWTWTTTTNNWAAASYM, PWM threshold score = 19.2 bits) (Estrem et al., 1998) (Fig S13A). We then computationally searched for UP-element-specific hotspots within the parent sequences, i.e., locations in which mutations that gain or lose UP-elements lead to significant fluorescence increases (Mann-Whitney U-test, Fig S7 and methods. See Data S8 for the coordinates, fluorescence changes, and significance). The analysis did not identify any UP elements whose mutation significantly changes fluorescence. 

We then repeated the analysis with a less stringent PWM threshold of 4.8 bits (1/4th of the PWM threshold score). This time, we identified 74 “UP-like” elements that are created or destroyed at unique positions within the parents. 23 of these motifs significantly change fluorescence when created or destroyed. However, even with this liberal threshold, none of these UP-like elements increase fluorescence by more than 0.5 a.u. when gained, or decrease fluorescence by more than 0.5 a.u. when lost (Fig S13B). This finding ultimately suggests that the UP element plays a negligible role in promoter emergence within our dataset.”

Collectively, these additional analyses suggest that the presence of TGn plus a -10 box is insufficient to create promoter activity, and that the UP element does not play a significant role in promoter emergence or evolution.

The full sequences used need to be provided and mutations resulting in new promoters need to be shown.

To Figures 3, 4, 5, and Supplemental Figures S8, S9, S10, S11, and S12, we have added the sequences which created or the destroyed the promoters, and their PWM scores.

The paper needs to be rewritten to take into account the relevant literature on i) promoter islands (i.e. sections of horizontally acquired AT-rich DNA) ii) generation and loss of promoters by mutation.

We have rewritten the introduction. The majority of these points are now addressed in the following two new paragraphs (lines 92-112):

“Recent work shows that mutations can help new promoters to emerge from promoter motifs or from sequences adjacent to such motifs (Bykov et al., 2020; Fuqua and Wagner, 2023; Yona et al., 2018). However, encoding -10 and -35 boxes is insufficient to drive complete transcription of a gene coding sequence. For instance, the E. coli genome contains clusters of -10 and -35 boxes that are bound by RNA polymerase and produce short oligonucleotide fragments, but rarely create complete transcripts. Such clusters are called promoter islands, and are strongly associated with horizontally-transferred DNA (Bykov et al., 2020; Panyukov and Ozoline, 2013; Purtov et al., 2014; Shavkunov et al., 2009). 

There are two proposed explanations for why promoter islands do not create full transcripts. First, the TF H-NS may repress promoter activity in promoter islands. This is because in a Δhns background, transcript levels from the promoter islands increases (Purtov et al., 2014). However, mutagenizing a specific promoter island (appY) until it transcribes a GFP reporter, reveals that in-vitro H-NS binding does not significantly change when GFP levels increase (Bykov et al., 2020). Thus, it is not clear whether H-NS actually represses the complete transcription of these sequences. The second proposed explanation is that excessive promoter motifs silence transcription. The aforementioned study found that promoter activity increases when mutations improve a -10 box to better match its consensus (TAAAAAT→TATACT), while simultaneously destroying surrounding -10 and -35 boxes (Bykov et al., 2020). However, we note that if these surrounding motifs never contributed to GFP fluorescence to begin with, then mutations could also simply have accumulated in them during random mutagenesis without affecting promoter activity.”

In closing, we would like to thank all three reviewers again for your time to engage with this manuscript.

Summary of specific changes that we have made to each section of the manuscript 

• Abstract

- We updated the abstract to include the finding that more than 1’500 new -10s and 35s are created in our dataset, but only ~0.3% of them actually create de-novo promoter activity.

- We no longer highlight the conclusion that the majority of promoters emerge and evolve from -10 and -35 boxes.

• Introduction

- We have added more background information about the UP-element and the TGn motif.

- We better describe the promoter islands and the results identified by Bykov et al., 2020.

• Results: Promoter island sequences are enriched with motifs for -10 and -35 boxes.

- We clarify how the -10 and -35 PWMs we use were derived.

- We refer to the 25 promoter island fragments as “Template sequences” (P1-P25). The “parent sequences” now correspond to the top and bottom strands of each template (N=50, P1-GFP, P1-RFP, P2-GFP, …, P25-RFP).

- We elaborate that ~7% of the -10 boxes in the template sequences have the TGn motif.

- In the previous version of the manuscript, if there were overlapping -10 boxes or overlapping -35 box, we counted these to be a single -10 box or a single -35 box, respectively. In the new version of the manuscript, we now treat each motif as an independent box. Because of this, the number of -10 and -35 boxes per parent have slightly increased.  

•Results: Non-promoters vary widely in their potential to become promoters.

- We make a clear distinction between promoters and non-promoters, and define the parent sequences.

- We note that only 20% of parents with an “extended -10 box” have promoter activity.

• Results: Promoter emergence correlates with minute differences in background promoter levels.

- We added an analysis where we compare Pnew to the parent fluorescence levels, even if they are below 1.5 a.u. We find that the distribution of Pnew matches a sigmoid function.

• Results: Promoter emergence does not correlate with simple sequence features

- We added an analysis comparing k-mer counts to Pnew.

- We updated the way we count -10 and -35 boxes, and recalculated the correlation with Pnew. The P and R2 values have changed, but Pnew still does not significantly correlate with -10 or -35 box counts.

• Results: Promoters emerge and evolve only from specific subsets of -10 and -35 boxes

- We have added an analysis where we computationally scramble the wild-type parent sequences while maintaining the coordinates of the mutual information hotspots. This reveals that the overlap with -10 and -35 motifs is not a coincidence of dense promoter motif encoding.

We found a computational error in our analysis and updated the percent overlap between -10 boxes and -35 boxes with mutual information hotspots. The results are similar. o 14% of -10 boxes overlap with hotspots with our new way of defining -10 and -35 boxes.

• Results: New -10 and -35 boxes readily emerge, but rarely lead to de-novo promoter activity

- We quantify how often a new -10 and -35 box is created at a unique position within our collection of promoter fragments, and how often this results in a -10 and -35 box being appropriately spaced, and how often this actually leads to de-novo promoter activity. o We quantify how often a TGn sequence lies upstream of a new -10 box.

• Results: Promoters can emerge when mutations create motifs but not by destroying them.

- For each example, we added the DNA sequences of the wild-type region of interest and the mutant region of interest that results in the gain of promoter activity, and their respective PWM scores. 

- We created constructs to validate each example by testing their fluorescence on a plate reader.

- We removed the P1-GFP example from the main figure, as it was a false-positive in the dataset. It is now in Fig S8.

- We removed the Shiko Emergence metaphor because it could be confused with a binding mechanism for RNA polymerase.

• Results – Gaining new motifs over existing motifs increases and decreases promoter activity.

- We removed the “Tandem motif” because it is more likely caused by H-NS binding.

- We renamed the mechanisms to be “hetero-gain” and “homo-gain” for simplicity, and clearly define how we classified each sequence into each category.

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the predicted point mutations.

• Results – Histone-like nucleoid-structuring protein (H-NS) represses P12-RFP and P22-GFP.

- This is a new analysis, which explores the role of the TF H-NS in repressing the parent sequences. 

- We identified putative H-NS motifs in P12-RFP and P22-GFP.

- We show experimentally that in a H-NS null background, a bidirectional promoter (P20) becomes unidirectional, even though P20 does not contain an obvious H-NS motif.

- In the original version of the manuscript, we describe a phenomenon where gaining a -35 box upstream of a promoter’s -35 box, or a -10 box upstream of a promoter’s -10 box significantly decreases expression. We called this phenomenon a “tandem motif.” However, in the newest version of the manuscript, we find that these fluorescence decreases are rescued in a H-NS null background, suggesting the finding was actually due to H-NS binding modulation and not -10 and -35 boxes.

• Results – The UP-element does not strongly influence promoter activity in our dataset.

We used a PWM for the UP element to see if gaining or losing UP motifs was significantly correlated with increasing or decreasing expression. Even with a liberal PWM threshold, the analysis did not find any UP elements.

• Discussion

- We rewrote the discussion to account for the new analyses and the results on H-NS, the UP-element, and the extended -10.

- We better explain how our results clash with the results from the Bykov paper.

- We fit our results into the context of David Grainger’s papers.

• Methods

- Added an explanation about pMR1.

- Added methods describing how we created the point mutation constructs.

- Added the methods for the plate reader.

- Added the methods for Illumina sequencing.

- Added the methods for the sigmoid curve-fitting.

• Figure 1

- Panel E compares how Pnew (the probability of a daughter sequence having a fluorescence score greater than 1.5 a.u.) associates with the fluorescence scores of each parent sequence.

- Panel F was originally in Figure S5. In the originally submitted version of the manuscript, if there were overlapping -10s or overlapping -35s, we counted these to be a single -10 or a single -35, respectively. In the new version of the manuscript, we now treat each motif as an independent box. Because of this, the r2 and p values have changed, but the conclusions have not (Pnew still does not significantly correlate with -10 or -35 box counts).

• Figure 2

- Panel C now includes a stacked barplot showing the percentage of -10 and -35 boxes that overlap with mutual information hotspots when the parent sequences are randomly scrambled computationally.

• Figure 3

- Panels A-C were added to explain how we define a new -10/-35 box, how many such new boxes each parent has. These panels also illustrate how we associate the presence or absence of a motif with significant changes in fluorescence scores of the daughter sequences.

- We moved the example of P1-GFP to Figure S8 because when we tested the specific mutation which leads to gaining the -10 box, fluorescence did not change.

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from reporter constructs harboring the point mutations predicted by our computational analyses.

- Cartoons of RNA polymerase have been removed.

• Figure 4

- The tandem-motif has been removed from the figure.

- Cartoons of RNA polymerase have been removed.

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the point mutations predicted by our computational analyses.

• Figure 5

- This is a new figure analyzing the role of H-NS in promoter evolution and emergence.

• Figure S4

- Panel B now shows the wild-type parent scores and their standard deviations from the sort-seq experiment.

• Figure S5

- Panels with -10 and -35 box counts moved to Figure 1.

- The panel comparing Pnew to hotspot counts was removed.

- Correlations between different k-mers and Pnew are added to panels C-H.

• Figure S8

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the point mutations predicted by our computational analyses.

• Figure S9

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the point mutations predicted by our computational analyses.

• Figure S10

- We now include the DNA sequences, the PWM scores, the spacer lengths, and the fluorescence values from constructs harboring the point mutations predicted by our computational analyses.

• Figure S11

- Added DNA sequences and PWM scores.

• Figure S12

- A new figure with further insights about H-NS.

• Figure S13

- A new figure regarding the UP-element analysis.

• Figure S14

- Added Panel D to show how we created mutant reporter constructs for validation.

eLife Assessment

This study presents a new quantitative method, CROWN-seq, to map the cap-adjacent RNA modification N6,2'-O-dimethyladenosine (m6Am) with single nucleotide resolution. Using thoughtful controls and well-validated reagents, the authors provide compelling evidence that the method is reliable and reproducible. Additionally, the study provides important evidence that m6Am may increase transcription in modified mRNAs, however, the data only demonstrates a correlation between m6Am and transcriptional regulation rather than causality. Overall, this study is poised to advance m6Am research, being of broad interest to the RNA biology and gene regulation fields.

Reviewer #1 (Public review):

Summary:

In this manuscript, Liu et al. present CROWN-seq, a technique that simultaneously identifies transcription-start nucleotides and quantifies N6,2'-O-dimethyladenosine (m6Am) stoichiometry. This method is derived from ReCappable-seq and GLORI, a chemical deamination approach that differentiates A and N6-methylated A. Using ReCappable-seq and CROWN-seq, the authors found that genes frequently utilize multiple transcription start sites, and isoforms beginning with an Am are almost always N6-methylated. These findings are consistently observed across nine cell lines. Unlike prior reports that associated m6Am with mRNA stability and expression, the authors suggest here that m6Am may increase transcription when combined with specific promoter sequences and initiation mechanisms. Additionally, they report intriguing insights on m6Am in snRNA and snoRNA and its regulation by FTO. Overall, the manuscript presents a strong body of work that will significantly advance m6Am research.

Strengths:

The technology development part of the work is exceptionally strong, with thoughtful controls and well-supported conclusions.

Weaknesses:

Given the high stoichiometry of m6Am, further association with upstream and downstream sequences (or promoter sequences) does not appear to yield strong signals. As such, transcription initiation regulation by m6Am, suggested by the current work, warrants further investigation.

Reviewer #2 (Public review):

Summary:

In the manuscript "Decoding m6Am by simultaneous transcription-start mapping and methylation quantification" Liu and co-workers describe the development and application of CROWN-Seq, a new specialized library preparation and sequencing technique designed to detect the presence of cap-adjacent N6,2'-O-dimethyladenosine (m6Am) with single nucleotide resolution. Such a technique was a key need in the field since prior attempts to get accurate positional or quantitative measurements of m6Am positioning yielded starkly different results and failed to generate a consistent set of targets. As noted in the strengths section below the authors have developed a robust assay that moves the field forward.

Furthermore, their results show that most mRNAs whose transcription start nucleotide (TSN) is an 'A' are in fact m6Am (85%+ for most cell lines). They also show that snRNAs and snoRNAs have a substantially lower prevalence of m6Am TSNs.

Strengths:

Critically, the authors spent substantial time and effort to validate and benchmark the new technique with spike-in standards during development, cross-comparison with prior techniques, and validation of the technique's performance using a genetic PCIF1 knockout. Finally, they assayed nine different cell lines to cross-validate their results. The outcome of their work (a reliable and accurate method to catalog cap-adjacent m6Am) is a particularly notable achievement and is a needed advance for the field.

Weaknesses:

No major concerns were identified by this reviewer.

Mid-level Concerns:

(1) In Lines 625 and 626, the authors state that "our data suggest that mRNAs initate (mis-spelled by authors) with either Gm, Cm, Um, or m6Am." This reviewer took those words to mean that for A-initiated mRNAs, m6Am was the 'default' TSN. This contradicts their later premise that promoter sequences play a role in whether m6Am is deposited.

(2) Further, the following paragraph (lines 633-641) uses fairly definitive language that is unsupported by their data. For example in lines 637 and 638 they state "We found that these differences are often due to the specific TSS motif." Simply, using 'due to' implies a causative relationship between the promoter sequences and m6Am has been demonstrated. The authors do not show causation, rather they demonstrate a correlation between the promoter sequences and an m6Am TSN. Finally, despite claiming a causal relationship, the authors do not put forth any conceptual framework or possible mechanism to explain the link between the promoter sequences and transcripts initiating with an m6Am.

(3) The authors need to soften the language concerning these data and their interpretation to reflect the correlative nature of the data presented to link m6Am and transcription initiation.

Reviewer #3 (Public review):

Summary:

m6Am is an abundant mRNA modification present on the TSN. Unlike the structurally similar and abundant internal mRNA modification m6A, m6Am's function has been controversial. One way to resolve controversies surrounding mRNA modification functions has been to develop new ways to better profile said mRNA modification. Here, Liu et al. developed a new method (based on GLORI-seq for m6A-sequencing), for antibody-independent sequencing of m6Am (CROWN-seq). Using appropriate spike-in controls and knockout cell lines, Liu et al. clearly demonstrated CROWN-seq's precision and quantitative accuracy for profiling transcriptome-wide m6Am. Subsequently, the authors used CROWN-seq to greatly expand the number of known m6Am sites in various cell lines and also determine m6Am stoichiometry to generally be high for most genes. CROWN-seq identified gene promoter motifs that correlate best with high stoichiometry m6Am sites, thereby identifying new determinants of m6Am stoichiometry. CROWN-seq also helped reveal that m6Am does not regulate mRNA stability or translation (as opposed to past reported functions). Rather, m6Am stoichiometry correlates well with transcription levels. Finally, Liu et al. reaffirmed that FTO mainly demethylates m6Am, not of mRNA but of snRNAs and snoRNAs.

Strengths:

This is a well-written manuscript that describes and validates a new m6Am-sequencing method: CROWN-seq as the first m6Am-sequencing method that can both quantify m6Am stoichiometry and profile m6Am at single-base resolution. These advantages facilitated Liu et al. to uncover new potential findings related to m6Am regulation and function. I am confident that CROWN-seq will likely be the gold standard for m6Am-sequencing henceforth.

Weaknesses:

Though the authors have uncovered a potentially new function for m6Am, they need to be clear that without identifying a mechanism, their data might only be demonstrating a correlation between the presence of m6Am and transcriptional regulation rather than causality.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Liu et al. present CROWN-seq, a technique that simultaneously identifies transcription-start nucleotides and quantifies N6,2'-O-dimethyladenosine (m6Am) stoichiometry. This method is derived from ReCappable-seq and GLORI, a chemical deamination approach that differentiates A and N6-methylated A. Using ReCappable-seq and CROWN-seq, the authors found that genes frequently utilize multiple transcription start sites, and isoforms beginning with an Am are almost always N6-methylated. These findings are consistently observed across nine cell lines. Unlike prior reports that associated m6Am with mRNA stability and expression, the authors suggest here that m6Am may increase transcription when combined with specific promoter sequences and initiation mechanisms. Additionally, they report intriguing insights on m6Am in snRNA and snoRNA and its regulation by FTO. Overall, the manuscript presents a strong body of work that will significantly advance m6Am research.

Strengths:

The technology development part of the work is exceptionally strong, with thoughtful controls and well-supported conclusions.

We appreciate the reviewer for the very positive assessment of the study. We have addressed the concerns below.

Weaknesses:

Given the high stoichiometry of m6Am, further association with upstream and downstream sequences (or promoter sequences) does not appear to yield strong signals. As such, transcription initiation regulation by m6Am, suggested by the current work, warrants further investigation.

We thank the reviewer for the insightful comments. We have softened the language related to m6Am and transcription regulation. We totally agree with the reviewer that future investigation is required to determine the molecular mechanism behind m6Am and transcription regulation.

Reviewer #2 (Public review):

Summary:

In the manuscript "Decoding m6Am by simultaneous transcription-start mapping and methylation quantification" Liu and co-workers describe the development and application of CROWN-Seq, a new specialized library preparation and sequencing technique designed to detect the presence of cap-adjacent N6,2'-O-dimethyladenosine (m6Am) with single nucleotide resolution. Such a technique was a key need in the field since prior attempts to get accurate positional or quantitative measurements of m6Am positioning yielded starkly different results and failed to generate a consistent set of targets. As noted in the strengths section below the authors have developed a robust assay that moves the field forward.

Furthermore, their results show that most mRNAs whose transcription start nucleotide (TSN) is an 'A' are in fact m6Am (85%+ for most cell lines). They also show that snRNAs and snoRNAs have a substantially lower prevalence of m6Am TSNs.

Strengths:

Critically, the authors spent substantial time and effort to validate and benchmark the new technique with spike-in standards during development, cross-comparison with prior techniques, and validation of the technique's performance using a genetic PCIF1 knockout. Finally, they assayed nine different cell lines to cross-validate their results. The outcome of their work (a reliable and accurate method to catalog cap-adjacent m6Am) is a particularly notable achievement and is a needed advance for the field.

Weaknesses:

No major concerns were identified by this reviewer.

We thank the reviewer for the positive assessment of the method and dataset. We have addressed the concerns below.

Mid-level Concerns:

(1) In Lines 625 and 626, the authors state that “our data suggest that mRNAs initate (mis-spelled by authors) with either Gm, Cm, Um, or m6Am.” This reviewer took those words to mean that for A-initiated mRNAs, m6Am was the ‘default’ TSN. This contradicts their later premise that promoter sequences play a role in whether m6Am is deposited.

We thank the reviewer for the comment. We have changed this sentence into “Instead, our data suggest that mRNAs initiate with either Gm, Cm, Um, or Am, where Am are mostly m6Am modified.” The revised sentence separates the processes of transcription initiation and m6Am deposition, which will not confuse the reader.

(2) Further, the following paragraph (lines 633-641) uses fairly definitive language that is unsupported by their data. For example in lines 637 and 638 they state “We found that these differences are often due to the specific TSS motif.” Simply, using ‘due to’ implies a causative relationship between the promoter sequences and m6Am has been demonstrated. The authors do not show causation, rather they demonstrate a correlation between the promoter sequences and an m6Am TSN. Finally, despite claiming a causal relationship, the authors do not put forth any conceptual framework or possible mechanism to explain the link between the promoter sequences and transcripts initiating with an m6Am.

(3) The authors need to soften the language concerning these data and their interpretation to reflect the correlative nature of the data presented to link m6Am and transcription initiation.

For (2) and (3). We have softened the language in the revised manuscript. Specifically, for lines 633-641 in the original manuscript, we have changed “are often due to” into “are often related to” in the revised manuscript, which claims a correlation rather than a causation.

Reviewer #3 (Public review):

Summary:

m6Am is an abundant mRNA modification present on the TSN. Unlike the structurally similar and abundant internal mRNA modification m6A, m6Am’s function has been controversial. One way to resolve controversies surrounding mRNA modification functions has been to develop new ways to better profile said mRNA modification. Here, Liu et al. developed a new method (based on GLORI-seq for m6A-sequencing), for antibody-independent sequencing of m6Am (CROWN-seq). Using appropriate spike-in controls and knockout cell lines, Liu et al. clearly demonstrated CROWN-seq’s precision and quantitative accuracy for profiling transcriptome-wide m6Am. Subsequently, the authors used CROWN-seq to greatly expand the number of known m6Am sites in various cell lines and also determine m6Am stoichiometry to generally be high for most genes. CROWN-seq identified gene promoter motifs that correlate best with high stoichiometry m6Am sites, thereby identifying new determinants of m6Am stoichiometry. CROWN-seq also helped reveal that m6Am does not regulate mRNA stability or translation (as opposed to past reported functions). Rather, m6Am stoichiometry correlates well with transcription levels. Finally, Liu et al. reaffirmed that FTO mainly demethylates m6Am, not of mRNA but of snRNAs and snoRNAs.

Strengths:

This is a well-written manuscript that describes and validates a new m6Am-sequencing method: CROWN-seq as the first m6Am-sequencing method that can both quantify m6Am stoichiometry and profile m6Am at single-base resolution. These advantages facilitated Liu et al. to uncover new potential findings related to m6Am regulation and function. I am confident that CROWN-seq will likely be the gold standard for m6Am-sequencing henceforth.

Weaknesses:

Though the authors have uncovered a potentially new function for m6Am, they need to be clear that without identifying a mechanism, their data might only be demonstrating a correlation between the presence of m6Am and transcriptional regulation rather than causality.

We thank the reviewer for the very positive assessment of the CROWN-seq method. We have softened the language which is related to the correlation between m6Am and transcription regulation.

eLife Assessment

This valuable study combined multiple approaches to gain insight into why rising estradiol levels, by influencing hypothalamic neurons, ultimately lead to ovulation. The experimental data were solid, but evidence for the conclusion that the findings explain how estradiol acts in the intact female were incomplete because they lacked experimental conditions that better approximate physiological conditions. Nevertheless the work will be of interest to reproductive biologists working on ovarian biology and female fertility.

Reviewer #1 (Public review):

Summary:

In this work, Qiu and colleagues examined the effects of preovulatory (i.e., proestrous or late follicular phase) levels of circulating estradiol on multiple calcium and potassium channel conductances in arcuate nucleus kisspeptin neurons. Although these cells are strongly linked to a role as the "GnRH pulse generator," the goal here was to examine the physiological properties of these cells in a hormonal milieu mimicking late proestrus, the time of the preovulatory GnRH-LH surge. Computational modeling is used to manipulate multiple conductances simultaneously and support a role for certain calcium channels in facilitating a switch in firing mode from tonic to bursting. CRISPR knockdown of the TRPC5 channel reduced overall excitability, but this was only examined in cells from ovariectomized mice without estradiol treatment.

Comments to address most recent author response:

The concern regarding the CRISPR experiments being confined to OVX mice is that the results can only suggest that CRISPR-mediated knockdown of TRPC5 can, at best, phenocopy the OVX+E condition. A reciprocal experiment in the opposite direction (for example, that returning TRPC5 to OVX levels in OVX+E mice prevents the changes in firing activity and pattern typical of the OVX+E2 condition) would strengthen the indication that E2-sensitive changes in TRPC5 expression and function are critically important to surge function. Acknowledging this as a limitation of the studies would help to better contextualize the value of the CRISPR experiments to an understanding of surge mechanisms when done only in OVX conditions.

The nature of the confusion regarding the consideration of OVX+E2 conditions in the computational model primarily arises from the methods description in the supplemental file: "The effect of E2 on ionic currents is modelled as a change in the maximum conductance parameter. For currents IM,IT, ICa and ITRPC5 this change is inferred from the qPCR data assuming that the conductance is directly proportional to the mRNA expression." If these were instead based on the whole-cell recordings as the authors now indicate in their response, then this description needs to be edited and clarified accordingly. Furthermore, the section states, "For ISK, IBK, Ileak, the OVX and OVX+E2 conductances are obtained from current-voltage relationships recorded from Kiss1ARH neurons in the absence/presence of iberiotoxin (BK blocker) and apamin (SK blocker). All other currents were assumed to be unaffected by E2." This section thus does not directly indicate that the recordings in the stated figures were used in the model, and moreover suggests that currents besides ISK, IBK, and Ileak were not different in OVX+E2 conditions.

The prior evidence stated for correlation of mRNA and channel conductance is not explicitly cited in the manuscript. It is well known that post-translational modifications, physiological modulation of individual channel biophysical properties, and many other factors can influence the end output of a membrane conductance. Therefore, the authors should, at minimum, provide a literature citation supporting the assumption used here.

Reviewer #2 (Public review):

Summary:

Kisspeptin neurons of the arcuate nucleus (ARC) are thought to be responsible for the pulsatile GnRH secretory pattern and to mediate feedback regulation of GnRH secretion by estradiol (E2). Evidence in the literature, including the work of the authors, indicates that ARC kisspeptin coordinate their activity through reciprocal synaptic interactions and the release of glutamate and of neuropeptide neurokinin B (NKB), which they co-express. The authors show here that E2 regulates the expression of genes encoding different voltage-dependent calcium channels, calcium-dependent potassium channels and canonical transient receptor potential (TRPC5) channels and of the corresponding ionic currents in ARC kisspeptin neurons. Using computer simulations of the electrical activity of ARC kisspeptin neurons, the authors also provide evidence of what these changes translate into in terms of these cells' firing patterns. The experiments reveal that E2 upregulates various voltage-gated calcium currents as well as 2 subtypes of calcium-dependent potassium currents, while decreasing TRPC5 expression (an ion channel downstream of NKB receptor activation), the slow excitatory synaptic potentials (slow EPSP) elicited in ARC kisspeptin neurons by NKB release and expression of the G protein-associated inward-rectifying potassium channel (GIRK). Based on these results, and on those of computer simulations, the authors propose that E2 promotes a functional transition of ARC kisspeptin neurons from neuropeptide-mediated sustained firing that supports coordinated activity for pulsatile GnRH secretion to a less intense burst-like firing pattern that could favor glutamate release from ARC kisspeptin. The authors suggest that the latter might be important for the generation of the preovulatory surge in females.

Strengths:

The authors combined multiple approaches in vitro and in silico to gain insights into the impact of E2 on the electrical activity of ARC kisspeptin neurons. These include patch-clamp electrophysiology combined with selective optogenetic stimulation of ARC kisspeptin neurons, reverse transcriptase quantitative PCR, pharmacology and CRISPR-Cas9-mediated knockdown of the Trpc5 gene. The addition of computer simulations for understanding the impact of E2 on the electrical activity of ARC kisspeptin cells is also a strength.

The authors add interesting information on the complement of ionic currents in ARC kisspeptin neurons and on their regulation by E2 to what was already known in the literature. Pharmacological and electrophysiological experiments appear of the highest standards and robust statistical analyses are provided throughout. The impact of E2 replacement on calcium and potassium currents is compelling. Likewise, the results of Trpc5 gene knockdown do provide good evidence that the TRPC5 channel plays a key role in mediating the NKB-mediated slow EPSP. Surprisingly, this also revealed an unsuspected role for this channel in regulating the membrane potential and excitability of ARC kisspeptin neurons.

Weaknesses:

The manuscript also has weaknesses that obscure some of the conclusions drawn by the authors.

One is that the authors compare here two conditions, OVX versus OVX replaced with high E2, that may not reflect the physiological conditions under which the proposed transition between neuropeptide-dependent sustained firing and less intense burst firing might take place (i.e. the diestrous [low E2] and proestrous [high E2] stages of the estrous cycle). This is an important caveat to keep in mind when interpreting the authors' findings. Indeed, that E2 alters certain ionic currents when added back to OVX females, does not mean that the magnitude of all of these ionic currents will vary during the estrous cycle.<br /> In addition, although the computational modeling indicates a role of the various E2-modulated conductances in causing a transition in ARC kisspeptin neuron firing pattern, their role is not directly tested in physiological recordings, weakening the link between these changes and the shift in firing patterns.

Overall, the manuscript provides interesting information about the effects of E2 on specific ionic currents in ARC kisspeptin neurons and some insights into the functional impact of these changes. However, some of the conclusions of the work, with regard, in particular, to the role of these changes in ion channels and to their implications for the LH surge, are not fully supported by the findings.

Author response:

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

Reviewer #1 (Public review):

Summary:

In this work, Qiu and colleagues examined the effects of preovulatory (i.e., proestrous or late follicular phase) levels of circulating estradiol on multiple calcium and potassium channel conductances in arcuate nucleus kisspeptin neurons. Although these cells are strongly linked to a role as the "GnRH pulse generator," the goal here was to examine the physiological properties of these cells in a hormonal milieu mimicking late proestrus, the time of the preovulatory GnRH-LH surge. Computational modeling is used to manipulate multiple conductances simultaneously and support a role for certain calcium channels in facilitating a switch in firing mode from tonic to bursting. CRISPR knockdown of the TRPC5 channel reduced overall excitability, but this was only examined in cells from ovariectomized mice without estradiol treatment.

Comments to address most recent author response:

The concern regarding the CRISPR experiments being confined to OVX mice is that the results can only suggest that CRISPR-mediated knockdown of TRPC5 can, at best, phenocopy the OVX+E condition. A reciprocal experiment in the opposite direction (for example, that returning TRPC5 to OVX levels in OVX+E mice prevents the changes in firing activity and pattern typical of the OVX+E2 condition) would strengthen the indication that E2-sensitive changes in TRPC5 expression and function are critically important to surge function. Acknowledging this as a limitation of the studies would help to better contextualize the value of the CRISPR experiments to an understanding of surge mechanisms when done only in OVX conditions.

We have noted in the manuscript that “It would be of interest in future experiments to do the reciprocal experiment to see if overexpressing Trpc5 channels in Kiss1ARH neurons from OVX + E2 females restores the RMP and  “rescues” the synchronization phenotype.”

The nature of the confusion regarding the consideration of OVX+E2 conditions in the computational model primarily arises from the methods description in the supplemental file: "The effect of E2 on ionic currents is modelled as a change in the maximum conductance parameter. For currents IM,IT, ICa and ITRPC5 this change is inferred from the qPCR data assuming that the conductance is directly proportional to the mRNA expression." If these were instead based on the whole-cell recordings as the authors now indicate in their response, then this description needs to be edited and clarified accordingly. Furthermore, the section states, "For ISK, IBK, Ileak, the OVX and OVX+E2 conductances are obtained from current-voltage relationships recorded from Kiss1ARH neurons in the absence/presence of iberiotoxin (BK blocker) and apamin (SK blocker). All other currents were assumed to be unaffected by E2." This section thus does not directly indicate that the recordings in the stated figures were used in the model, and moreover suggests that currents besides ISK, IBK, and Ileak were not different in OVX+E2 conditions.

The prior evidence stated for correlation of mRNA and channel conductance is not explicitly cited in the manuscript. It is well known that post-translational modifications, physiological modulation of individual channel biophysical properties, and many other factors can influence the end output of a membrane conductance. Therefore, the authors should, at minimum, provide a literature citation supporting the assumption used here.

We have re-written the paragraph on “Modelling the effects of E2” in the Supplemental Information (now Appendix 1)  to clarify the that the modeling was based on a combination of electrophysiological recordings and the qPCR data presented in this and previous publications. The statement that “all other currents were assumed to be unaffected by E2” was a misstatement and has been deleted. As per the reviewer’s request, we have listed seven publications that document the correlation between the mRNA expression and channel conductance for the various channels. We thank the reviewer for the suggestion.

Reviewer #2 (Public review):

Summary:

Kisspeptin neurons of the arcuate nucleus (ARC) are thought to be responsible for the pulsatile GnRH secretory pattern and to mediate feedback regulation of GnRH secretion by estradiol (E2). Evidence in the literature, including the work of the authors, indicates that ARC kisspeptin coordinate their activity through reciprocal synaptic interactions and the release of glutamate and of neuropeptide neurokinin B (NKB), which they co-express. The authors show here that E2 regulates the expression of genes encoding different voltage-dependent calcium channels, calcium-dependent potassium channels and canonical transient receptor potential (TRPC5) channels and of the corresponding ionic currents in ARC kisspeptin neurons. Using computer simulations of the electrical activity of ARC kisspeptin neurons, the authors also provide evidence of what these changes translate into in terms of these cells' firing patterns. The experiments reveal that E2 upregulates various voltage-gated calcium currents as well as 2 subtypes of calcium-dependent potassium currents, while decreasing TRPC5 expression (an ion channel downstream of NKB receptor activation), the slow excitatory synaptic potentials (slow EPSP) elicited in ARC kisspeptin neurons by NKB release and expression of the G protein-associated inward-rectifying potassium channel (GIRK). Based on these results, and on those of computer simulations, the authors propose that E2 promotes a functional transition of ARC kisspeptin neurons from neuropeptide-mediated sustained firing that supports coordinated activity for pulsatile GnRH secretion to a less intense burst-like firing pattern that could favor glutamate release from ARC kisspeptin. The authors suggest that the latter might be important for the generation of the preovulatory surge in females.

Strengths:

The authors combined multiple approaches in vitro and in silico to gain insights into the impact of E2 on the electrical activity of ARC kisspeptin neurons. These include patch-clamp electrophysiology combined with selective optogenetic stimulation of ARC kisspeptin neurons, reverse transcriptase quantitative PCR, pharmacology and CRISPR-Cas9-mediated knockdown of the Trpc5 gene. The addition of computer simulations for understanding the impact of E2 on the electrical activity of ARC kisspeptin cells is also a strength.

The authors add interesting information on the complement of ionic currents in ARC kisspeptin neurons and on their regulation by E2 to what was already known in the literature. Pharmacological and electrophysiological experiments appear of the highest standards and robust statistical analyses are provided throughout. The impact of E2 replacement on calcium and potassium currents is compelling. Likewise, the results of Trpc5 gene knockdown do provide good evidence that the TRPC5 channel plays a key role in mediating the NKB-mediated slow EPSP. Surprisingly, this also revealed an unsuspected role for this channel in regulating the membrane potential and excitability of ARC kisspeptin neurons.

Weaknesses:

The manuscript also has weaknesses that obscure some of the conclusions drawn by the authors.

One is that the authors compare here two conditions, OVX versus OVX replaced with high E2, that may not reflect the physiological conditions under which the proposed transition between neuropeptide-dependent sustained firing and less intense burst firing might take place (i.e. the diestrous [low E2] and proestrous [high E2] stages of the estrous cycle). This is an important caveat to keep in mind when interpreting the authors' findings. Indeed, that E2 alters certain ionic currents when added back to OVX females, does not mean that the magnitude of all of these ionic currents will vary during the estrous cycle.

We do know that the slow EPSP, which is generated by TRPC5 channels, tracks beautifully with the steroid state of female mice.  Using our E2 treatment paradigm that generates a LH surge in OVX females (left panel in Author response image 1), there is no difference in the amplitude of the slow EPSP in proestrous versus OVX + E2 females (right panel in Author response image 1).    

Author response image 1.

In addition, although the computational modeling indicates a role of the various E2-modulated conductances in causing a transition in ARC kisspeptin neuron firing pattern, their role is not directly tested in physiological recordings, weakening the link between these changes and the shift in firing patterns.

In future experiments we will test directly the physiological contribution of the other E2-modulated conductances in causing the transition in the firing pattern of arcuate Kiss1 neurons using CRISPR/SaCas9 technology as we have documented for the TRPC5 channel (e.g., Figures 11 and 12).

Overall, the manuscript provides interesting information about the effects of E2 on specific ionic currents in ARC kisspeptin neurons and some insights into the functional impact of these changes. However, some of the conclusions of the work, with regard, in particular, to the role of these changes in ion channels and to their implications for the LH surge, are not fully supported by the findings.

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this work, Qiu and colleagues examined the effects of preovulatory (i.e., proestrous or late follicular phase) levels of circulating estradiol on multiple calcium and potassium channel conductances in arcuate nucleus kisspeptin neurons. Although these cells are strongly linked to a role as the "GnRH pulse generator," the goal here was to examine the physiological properties of these cells in a hormonal milieu mimicking late proestrus, the time of the preovulatory GnRH-LH surge. Computational modeling is used to manipulate multiple conductances simultaneously and support a role for certain calcium channels in facilitating a switch in firing mode from tonic to bursting. CRISPR knockdown of the TRPC5 channel reduced overall excitability, but this was only examined in cells from ovariectomized mice without estradiol treatment. The manuscript has been substantially improved from the initial version by the addition of new experiments and clarification of important figures. Importantly, the overlap of data with previous reports from the same group has been corrected.

Strengths:

(1) Examination of multiple types of calcium and potassium currents, both through electrophysiology and molecular biology.

(2) Focus on arcuate kisspeptin neurons during the surge is relatively conceptually novel as the anteroventral periventricular nucleus (AVPV) kisspeptin neurons have received much more attention as the "surge generator" population.

(3) The modeling studies allow for direct examination of manipulation of single and multiple conductances, whereas the electrophysiology studies necessarily require examination of each current in isolation. Construction of an arcuate kisspeptin neuron model promises to be of value to the reproductive neuroendocrinology field.

Weaknesses:

A remaining weakness in this revised version of the manuscript is that the relevance of the CRISPR experiments is still rather tenuous given that the goal is to understand what happens in the estrogen-treatment condition, and these experiments were performed only in OVX mice. Similar concerns reflect that the computational model examining the effect of E2 infers multiple conductances based on qPCR data and an assumption that the conductances are directionally proportional to the level of gene expression, and then tunes these to the current recordings obtained from OVX mice, without a direct confirmation in OVX+E2 conditions that the model parameters accurately reflect the properties of these currents in the presence of estrogen.

We are still puzzled by Reviewer’s concerns about doing the CRISPRing of Trpc5 in the OVX+E2 females.  The Trpc5 channel expression is significantly reduced with the E2 treatment (Figure 10E) which we know translates into a minimal slow EPSP (Figure 2, Qiu eLife 2016) and is essentially equivalent to the slow EPSP amplitude in the Trpc5 mutagenesis in the ovariectomized females (Figure 12).  TRPC5 channel conductance is already at “rock bottom.”  The modeling informs us that such a low TRPC5 conductance will not support a long lasting slow EPSP and sustained firing (Figure 13A).

Also, we respectively point out that we have published a score of papers over the past 20 years showing that the channel conductance does correlate with the mRNA expression (e.g., Qiu et al., eLife 2018).  Secondly, the model does take into consideration the OVX + E2 conditions (Figure 13B,C) which is based on the extensive whole-cell recordings presented in Figures 4,5,6,7,8 and 9.

Reviewer #2 (Public Review):

Summary:

Kisspeptin neurons of the arcuate nucleus (ARC) are thought to be responsible for the pulsatile GnRH secretory pattern and to mediate feedback regulation of GnRH secretion by estradiol (E2). Evidence in the literature, including the work of the authors, indicates that ARC kisspeptin coordinate their activity through reciprocal synaptic interactions and the release of glutamate and of neuropeptide neurokinin B (NKB), which they co-express. The authors show here that E2 regulates the expression of genes encoding different voltage-dependent calcium channels, calcium-dependent potassium channels and canonical transient receptor potential (TRPC5) channels and of the corresponding ionic currents in ARC kisspeptin neurons. Using computer simulations of the electrical activity of ARC kisspeptin neurons, the authors also provide evidence of what these changes translate into in terms of these cells' firing patterns. The experiments reveal that E2 upregulates various voltage-gated calcium currents as well as 2 subtypes of calcium-dependent potassium currents while decreasing TRPC5 expression (an ion channel downstream of NKB receptor activation), the slow excitatory synaptic potentials (slow EPSP) elicited in ARC kisspeptin neurons by NKB release and expression of the G protein-associated inward-rectifying potassium channel (GIRK). Based on these results, and on those of computer simulations, the authors propose that E2 promotes a functional transition of ARC kisspeptin neurons from neuropeptide-mediated sustained firing that supports coordinated activity for pulsatile GnRH secretion to a less intense burst-like firing pattern that could favor glutamate release from ARC kisspeptin. The authors suggest that the latter might be important for the generation of the preovulatory surge in females.

Strengths:

The authors combined multiple approaches in vitro and in silico to gain insights into the impact of E2 on the electrical activity of ARC kisspeptin neurons. These include patch-clamp electrophysiology combined with selective optogenetic stimulation of ARC kisspeptin neurons, reverse transcriptase quantitative PCR, pharmacology and CRISPR-Cas9-mediated knockdown of the Trpc5 gene. The addition of computer simulations for understanding the impact of E2 on the electrical activity of ARC kisspeptin cells is also a strength.

The authors add interesting information on the complement of ionic currents in ARC kisspeptin neurons and on their regulation by E2 to what was already known in the literature. Pharmacological and electrophysiological experiments appear of the highest standards and robust statistical analyses are provided throughout. The impact of E2 replacement on calcium and potassium currents is compelling. Likewise, the results of Trpc5 gene knockdown do provide good evidence that the TRPC5 channel plays a key role in mediating the NKB-mediated slow EPSP. Surprisingly, this also revealed an unsuspected role for this channel in regulating the membrane potential and excitability of ARC kisspeptin neurons.

Weaknesses:

The manuscript also has weaknesses that obscure some of the conclusions drawn by the authors.

One is that the authors compare here two conditions, OVX versus OVX replaced with high E2, that may not reflect the physiological conditions under which the proposed transition between neuropeptide-dependent sustained firing and less intense burst firing might take place (i.e. the diestrous [low E2] and proestrous [high E2] stages of the estrous cycle). This is an important caveat to keep in mind when interpreting the authors' findings. Indeed, that E2 alters certain ionic currents when added back to OVX females, does not mean that the magnitude of all of these ionic currents will vary during the estrous cycle.

Unfortunately, mice are a poor reproductive model since female mice do not have a clear follicular (estradiol-driven) phase distinctive from the luteal (progesterone-driven) phase.  Had we utilized a “proestrous” female, we could not with certainty distinguish between the effects of estradiol versus progesterone on the expression of the calcium and potassium channels that were the focus of this study.  Therefore, using our physiological model we can state with confidence that “estradiol elicits distinct firing patterns in arcuate nucleus kisspeptin neurons….”

Overall, the manuscript provides interesting information about the effects of E2 on specific ionic currents in ARC kisspeptin neurons and some insights into the functional impact of these changes. However, some of the conclusions of the work, with regard, in particular, to the role of these changes in ion channels and their implications for the LH surge, are not fully supported by the findings.

As we pointed out in the Discussion, the O’Byrne lab has clearly shown the relevance of Kiss1ARH neuronal burst firing and the release of glutamate to its effects on the LH surge:

“Rather, we postulate that glutamate neurotransmission is more important for excitation of Kiss1AVPV/PeN neurons and facilitating the GnRH (LH) surge with high circulating levels of E2 when peptide neurotransmitters are at a nadir and glutamate levels are high in female Kiss1ARH neurons. Indeed, low frequency (5 Hz) optogenetic stimulation of Kiss1ARH neurons, which only releases glutamate in E2-treated, ovariectomized females (Qiu J. et al., 2016), generates a surge-like increase in LH release during periods of optical stimulation (Lin et al., 2021; Voliotis et al., 2021).  In a subsequent study optical stimulation of Kiss1ARH neuron terminals in the AVPV at 20 Hz, a frequency commonly used for terminal stimulation in vivo, generated a similar surge of LH (Shen et al., 2022).  Additionally, intra-AVPV infusion of glutamate antagonists, AP5+CNQX, completely blocked the LH surge induced by Kiss1ARH terminal photostimulation in the AVPV (Shen et al., 2022).”

Recommendations for the authors:

Reviewer #2 (Recommendations for The Authors):

The reviewer noted the following in the revised manuscript:

- page 6, the authors may consider adding that presynaptic effects of blocking calcium channels on the slow EPSP cannot be fully ruled out. Indeed, the added experiments do indicate that some of the effects can be explained by impaired regulation of TRPC5 channels by calcium influx through calcium channels; however, the senktide-induced current is not fully blocked by the broad-spectrum calcium channel inhibitor cadmium, suggesting that the effect of blocking these channels on the slow EPSP may involve other mechanisms, such as presynaptic effects.

Optogenetic stimulation of all Kiss1ARH neurons induces the release of NKB at “physiological” concentrations, which in turn generates a slow EPSP in the recorded Kiss1ARH neuron. Blocking voltage-gated calcium channels can inhibit the NKB release from presynaptic  Kiss1ARH neurons, thereby reducing the amplitude of the slow EPSP. However, in whole-cell recordings of synaptically isolated Kiss1ARH neurons,  senktide directly induces a large inward current (Figure 3F), which is generated by the opening of TRPC5 channels (Qiu et al. J. Neurosci 2021). Voltage-gated calcium channels are coupled to the activation of TRPC5 channels (Blair, Kaczmarek and Clapham, J. Gen Physiol 2009), so by blocking voltage-gated calcium channels, cadmium effectively abrogates the facilitating effects of these channels on TRPC5 channel activation and significantly reduces but does not abolish the inward (excitatory) current (Figures 3F-H). We have clarified in the Results (page 6) that the Kiss1ARH neurons were synaptically isolated as depicted in Figures 3F,G.

- page 8, bottom, the mean value given for the apamin-sensitive current amplitude in E2 treated females does not match that plotted on the I/V graph in Figure 7F.

Thank you for pointing out this typographical error, which we have corrected.