Author response:

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

eLife assessment

This work presents valuable information about the specificity and promiscuity of toxic effector and immunity protein pairs. The evidence supporting the claims of the authors is currently incomplete, as there is concern about the methodology used to analyze protein interactions, which did not take potential differences in expression levels, protein folding, and/or transient interaction into account. Other methods to measure the strength of interactions and structural predictions would improve the study. The work will be of interest to microbiologists and biochemists working with toxin-antitoxin and effector-immunity proteins.

We thank the reviewers for considering this manuscript. We agree that this manuscript provides a valuable and cross-discipline introduction to new EI pair protein families where we focus on the EI pair’s flexibility and impacts on community structure. As such, we believe we have provided a solid foundation for future studies to examine non-cognate interactions and their possible effects on microbial communities. This, by definition, leaves some areas “incomplete” and, therefore, open for further investigations. While the methods we show do consider potential differences in binding assays, we have more explicitly addressed how “expression, protein folding, and/or transient binding” may play into this expanded EI pair model. We have also tempered the discussion of the proposed model, while also clearly highlighting other published evidence of non-cognate binding interactions between effector and immunity proteins. We have responded to the reviewers’ public comments (italicized below). 

In this revised manuscript, we have updated the main text, particularly the Discussion section, to include more careful language, explain past research better, and add new references to works showing non-cognate immunity proteins protecting against effectors in other systems. We have also updated the supplemental files with more analyses; the relevant procedures are in the Materials and Methods.

Public Reviews:

Note: Reviewer 1, who appeared to focus on a subset of the manuscript rather than the whole, based their comments on several inaccuracies, which we discuss below. We found the tone in this reviewer's comments to be, at times, inappropriate, e.g., using "harsh" and "simply too drastic" to imply that common structure-function analyses were outside of the field-standard methods. We also note that the reviewer took a somewhat atypical step in reviewing this manuscript by running and analyzing the potential protein-complex data in AlphaFold2 but did not discuss areas of low confidence within that model that may contradict their conclusions. We are concerned their approach muddled valid scientific criticisms with problematic conclusions.

Reviewer #1 (Public Review):

In this manuscript, Knecht, Sirias et al describe toxin-immunity pair from Proteus mirabilis. Their observations suggest that the immunity protein could protect against non-cognate effectors from the same family. They analyze these proteins by dissecting them into domains and constructing chimeras which leads them to the conclusion that the immunity can be promiscuous and that the binding of immunity is insufficient for protective activity.

Strengths:<br />  The manuscript is well written and the data are very well presented and could be potentially interesting. The phylogenetic analysis is well done, and provides some general insights.

Weaknesses:<br /> (1) Conclusions are mostly supported by harsh deletions and double hybrid assays. The later assays might show binding, but this method is not resolutive enough to report the binding strength. Proteins could still bind, but the binding might be weaker, transient, and out-competed by the target binding.

The phrasing of structure-function analyses as “harsh” is a bit unusual, as other research groups regularly use deletions and hybrid studies. Given the known caveats to deletion and domain substitutions, we included point-mutation analyses for both the effector and immunity proteins, as found on lines 105 - 113 and 255 - 261 in the current manuscript. These caveats are also why we coupled the in vitro binding analyses with in vivo protection experiments in two distinct experimental systems (E. coli and P. mirabilis). Based on this manuscript’s introductory analysis (where we define and characterize the genes, proteins, interactions, phylogenetics, and incidences in human microbiomes), the next apparent questions are beyond the scope of this study. Future approaches would include analyzing purified proteins from the effector (E) and immunity (I) protein families using biochemical assays, such as X-ray crystallography, circular dichroism spectroscopy, among others. 

Interestingly, most papers in the EI field do not measure EI protein affinity (Jana et al., 2019, Yadav et al., 2021). Notable exceptions are earlier colicin research (Wallis et al., 1995) and a new T6SS EI paper (Bosch et al., 2023) published as we first submitted this manuscript.

(2) While the authors have modeled the structure of toxin and immunity, the toxin-immunity complex model is missing. Such a model allows alternative, more realistic interpretation of the presented data. Firstly, the immunity protein is predicted to bind contributing to the surface all over the sequence, except the last two alpha helices (very high confidence model, iPTM>0.8). The N terminus described by the authors contributes one of the toxin-binding surfaces, but this is not the sole binding site. Most importantly, other parts of the immunity protein are predicted to interact closer to the active site (D-E-K residues). Thus, based on the AlphaFold model, the predicted mechanism of immunization remains physically blocking the active site. However, removing the N terminal part, which contributes large interaction surface will directly impact the binding strength. Hence, the toxin-immunity co-folding model suggests that proper binding of immunity, contributed by different parts of the protein, is required to stabilize the toxin-immunity complex and to achieve complete neutralization. Alternative mechanisms of neutralization might not be necessary in this case and are difficult to imagine for a DNase.

In response to the reviewer’s comment, we again reviewed the RdnE-RdnI AlphaFold2 complex predictions with the most updated version of ColabFold (1.5.2-patch with PDB100 and MMseq2) and have included them at the end of these responses [1].

However, the literature reports that computational predictions of E-I complexes often do not match experimental structural results (Hespanhol et al., 2022, Bosch et al., 2023). As such, we chose not to include the predicted cognate and non-cognate RdnE-I complexes from ColabFold (which uses AlphaFold2) and have not included this data in the revised manuscript. (It is notable that reviewer 1 found the proposed expanded model and research so interesting as to directly input and examine the AI-predicted RdnE-RdnI protein interactions in AlphaFold2.)

Discussion of the prevailing toxin-immunity complex model is in the introduction (lines 45-48) and Figure 5E. Further, there are various known mechanisms for neutralizing nucleases and other T6SS effectors, which we briefly state in the discussion (lines 359 - 361). More in-depth, these molecular mechanisms include active-site blocking (Benz et al., 2012), allosteric-site binding (Kleanthous et al., 1999 and Lu et al., 2014), enzymatic neutralization of the target (Ting et al., 2021), and structural disruption of both the active and binding sites (Bosch et al., 2023). Given this diversity of mechanisms, we did not presume to speculate on the as-of-yet unknown mechanism of RdnI protection. We have expanded discussion of these items in the revised manuscript.

(3) Dissection of a toxin into two domains is also not justified from a structural point of view, it is probably based on initial sequence analyses. The N terminus (actually previously reported as Pone domain in ref 21) is actually not a separate domain, but an integral part of the protein that is encased from both sides by the C terminal part. These parts might indeed evolve faster since they are located further from the active site and the central core of the protein. I am happy to see that the chimeric toxins are active, but regarding the conservation and neutralization, I am not surprised, that the central core of the protein fold is highly conserved. However, "deletion 2" is quite irrelevant - it deletes the central core of the protein, which is simply too drastic to draw any conclusions from such a construct - it will not fold into anything similar to an original protein, if it will fold properly at all.

The reviewer’s comment highlights why we turned to the chimera proteins to dissect the regions of RdnE (formerly IdrD-CT), as the deletions could result in misfolded proteins. (We initially examined RdnE in the years before the launch of AlphaFold2.) However, the reviewer is incorrect regarding the N-terminus of RdnE. The PoNe domain, while also a subfamily of the PD-(D/E)XK superfamily, forms a distinct clade of effectors from the PD-(D/E)XK domain in RdnE (formally IdrD-CT) as seen in Hespanhol et al., 2022; this is true for other DNase effectors as well. Many studies analyzing effectors within the PD-(D/E)XK superfamily only focus on the PD-(D/E)XK domain, removing just this domain from the context of the whole protein (Hespanhol et al., 2022; Jana et al., 2019). Of note, in RdnE, this region alone (containing the DNA-binding domain) is insufficient for DNase activity (unlike in PoNe). We have clarified this distinction in the results section of the current manuscript, visible in figure 2 .

(4) Regarding the "promiscuity" there is always a limit to how similar proteins are, hence when cross-neutralization is claimed authors should always provide sequence similarities. This similarity could also be further compared in terms of the predicted interaction surface between toxin and immunity.

Reviewer 1 points out a fundamental property of protein-protein interactions that has been isolated away from the impacts of such interactions on bacterial community structure. We have provided the whole protein alignments in figure 3 supplemental figure 3, the summary images in Figure 3D, and the protein phylogenetic trees in Figure 3C. We encourage others to consider the protein alignments as percent amino acid sequence similarity is not necessarily a good gauge for protein function and interactions. These data are publicly available on the OSF website associated with this manuscript https://osf.io/scb7z/, and we hope the community explores the data there.

In consideration of the enthusiasm to deeply dive into the primary research data, we have included the pairwise sequence identities across the entire proteins here: Proteus RdnI vs. Rothia RdnI: 23.6%; Proteus RdnI vs. Prevotella RdnI: 16.3%, Proteus RdnI vs. Pseudomonas RdnI: 14.6%; Rothia RdnI vs. Prevotella RdnI: 22.4%, Rothia RdnI vs. Pseudomonas RdnI: 17.6%; Prevotella RdnI vs. Pseudomonas RdnI: 19.5%. (As stated in response to reviewer 1 comment 2, we did not find it appropriate to make inferences based on AlphaFold2-predicted protein complexes.)

Overall, it looks more like a regular toxin-immunity couple, where some cross-reactions with homologues are possible, depending on how far the sequences have deviated. Nevertheless, taking all of the above into account, these results do not challenge toxin-immunity specificity dogma.

In this manuscript, we did not intend to dismiss the E-I specificity model but rather point out its limitations and propose an important expansion of that model that accounts for cross-protection and survival against attacks from other genera. We agree that it is commonly considered that deviations in amino acid sequence over time could result in cross-binding and protection (see lines 364-368). However, the impacts of such cross-binding on community structure, bacterial survival, and strain evolution were rarely addressed in prior literature, with exceptions such as in Zhang et al., 2013 and Bosch et al., 2023 among others. One key insight we propose and show in this manuscript is that cross-binding can be a fitness benefit in mixed communities; therefore, it could be selected for evolutionarily (lines 378-380), even potentially in host microbiomes.

Reviewer #2 (Public Review):

Summary:

The manuscript by Knecht et al entitled "Non-cognate immunity proteins provide broader defenses against interbacterial effectors in microbial communities" aims at characterizing a new type VI secretion system (T6SS) effector immunity pair using genetic and biochemical studies primarily focused on Proteus mirabilis and metagenomic analysis of human-derived data focused on Rothia and Prevotella sequences. The authors provide evidence that RdnE and RdnI of Proteus constitute an E-I pair and that the effector likely degrades nucleic acids. Further, they provide evidence that expression of non-cognate immunity derived from diverse species can provide protection against RdnE intoxication. Overall, this general line of investigation is underdeveloped in the T6SS field and conceptually appropriate for a broad audience journal. The paper is well-written and, aside from a few cases, well-cited. As detailed below however, there are several aspects of this paper where the evidence provided is somewhat insufficient to support the claims. Further, there are now at least two examples in the literature of non-cognate immunity providing protection against intoxication, one of which is not cited here (Bosch et al PMID 37345922 - the other being Ting et al 2018). In general therefore I think that the motivating concept here in this paper of overturning the predominant model of interbacterial effector-immunity cognate interactions is oversold and should be dialed back.

We agree that analyses focusing on flexible non-cognate interactions and protection are underdeveloped within the T6SS field and are not fully explored within a community structure. These ideas are rapidly growing in the field, as evidenced by the references provided by the reviewer. As stated earlier, we did not intend to overturn the prevailing model but rather have proposed an expanded model that accounts for protection against attacks from foreign genera.

Strengths:

One of the major strengths of this paper is the combination of diverse techniques including competition assays, biochemistry, and metagenomics surveys. The metagenomic analysis in particular has great potential for understanding T6SS biology in natural communities. Finally, it is clear that much new biology remains to be discovered in the realm of T6SS effectors and immunity.

Weaknesses:

The authors have not formally shown that RdnE is delivered by the T6SS. Is it the case that there are not available genetics tools for gene deletion for the BB2000 strain? If there are genetic tools available, standard assays to demonstrate T6SS-dependency would be to interrogate function via inactivation of the T6SS (e.g. by deleting tssC).

Our research group showed that the T6SS secretes RdnE (previously IdrD) in Wenren et al., 2013 (cited in lines 71-73). We later confirmed T6SS-dependent secretion by LC-MS/MS (Saak et al., 2017).  

For swarm cross-phyla competition assays (Figure 4), at what level compared to cognate immunity are the non-cognate immunity proteins being expressed? This is unclear from the methods and Figure 4 legend and should be elaborated upon. Presumably these non-cognate immunity proteins are being overexpressed. Expression level and effector-to-immunity protein stoichiometry likely matters for interpretation of function, both in vitro as well as in relevant settings in nature. It is important to assess if native expression levels of non-cognate cross-phyla immunity (e.g. Rothia and Prevotella) protect similarly as the endogenously produced cognate immunity. This experiment could be performed in several ways, for example by deleting the RdnE-I pair and complementing back the Rothia or Prevotella RdnI at the same chromosomal locus, then performing the swarm assay. Alternatively, if there are inducible expression systems available for Proteus, examination of protection under varying levels of immunity induction could be an alternate way to address this question. Western blot analysis comparing cognate to non-cognate immunity protein levels expressed in Proteus could also be important. If the authors were interested in deriving physical binding constants between E and various cognate and non-cognate I (e.g. through isothermal titration calorimetry) that would be a strong set of data to support the claims made. The co-IP data presented in supplemental Figure 6 are nice but are from E. coli cells overexpressing each protein and do not fully address the question of in vivo (in Proteus) native expression.

P. mirabilis strain ATCC29906 does not encode the rdnE and rdnI genes on the chromosome (NCBI BioSample: SAMN00001486) (line 151). Production of the RdnI proteins, including the cognate Proteus RdnI, comes from equivalent transgenic expression vectors. Specifically, the rdnI genes were expressed under the flaA promoter in P. mirabilis strain ATCC29906 (Table 1) for the swarm competition assays found in Figure 2C and Figure 4. This promoter results in constitutive expression in swarming cells (Belas et al., 1991; Jansen et al., 2003). In the revised manuscript, figure 4 Supplement Figure 2 shows the relative RdnI protein levels in these strains; we also clarified the expression constructs in the text (see reviewer 3, comment 1).

Lines 321-324, the authors infer differences between E and I in terms of read recruitment (greater abundance of I) to indicate the presence of orphan immunity genes in metagenomic samples (Figure 5A-D). It seems equally or perhaps more likely that there is substantial sequence divergence in E compared to the reference sequence. In fact, metagenomes analyzed were required only to have "half of the bases on reference E-I sequence receiving coverage". Variation in coverage again could reflect divergent sequence dipping below 90% identity cutoff. I recommend performing metagenomic assemblies on these samples to assess and curate the E-I sequences present in each sample and then recalculating coverage based on the exact inferred sequences from each sample.

This comment raises the challenges with metagenomic analyses. It was difficult to balance specificity to a particular species’ DNA sequence with the prevalence of any homologous sequence in the sample. Given the distinction in binding interactions among the examined four species, we opted to prioritize specificity, accepting that we were losing access to some rdnE and rdnI sequences in that decision. We chose a 90% identity cutoff, which, through several in silica controls, ensured that each sequence we identified was the rdnE or rdnI gene from that specific species. For the Version of Record, we have included analysis with a 70% cutoff in the supplemental information to try to account for sequence divergence by lowering the identity cutoffs as suggested. The data from the 70% identity cutoff was consistent with the original data from the 90% identity cutoff.

A description of gene-level read recruitment in the methods section relating to metagenomic analysis is lacking and should be provided.

Noted. We included the raw code and sequences on the OSF website associated with this manuscript https://osf.io/scb7z/.

Reviewer #3 (Public Review):

Summary:<br /> The authors discovered that the RdnE effector possesses DNase activity, and in competition, P. mirabilis having RdnE outcompetes the null strain. Additionally, they presented evidence that the RdnI immunity protein binds to RdnE, suppressing its toxicity. Interestingly, the authors demonstrated that the RdnI homolog from a different phylum (i.e., Actinomycetota) provides cross-species protection against RdnE injected from P. mirabilis, despite the limited identity between the immunity sequences. Finally, using metagenomic data from human-associated microbiomes, the authors provided bioinformatic evidence that the rdnE/rdnI gene pair is widespread and present in individual microbiomes. Overall, the discovery of broad protection by non-cognate immunity is intriguing, although not necessarily surprising in retrospect, considering the prolonged period during which Earth was a microbial battlefield/paradise.

Strengths:<br /> The authors presented a strong rationale in the manuscript and characterized the molecular mechanism of the RdnE effector both in vitro and in the heterologous expression model. The utilization of the bacterial two-hybrid system, along with the competition assays, to study the protective action of RdnI immunity is informative. Furthermore, the authors conducted bioinformatic analyses throughout the manuscript, examining the primary sequence, predicted structural, and metagenomic levels, which significantly underscore the significance and importance of the EI pair. 

Weaknesses:<br /> (1) The interaction between RdnI and RdnE appears to be complex and requires further investigation. The manuscript's data does not conclusively explain how RdnI provides a "promiscuous" immunity function, particularly concerning the RdnI mutant/chimera derivatives. The lack of protection observed in these cases might be attributed to other factors, such as a decrease in protein expression levels or misfolding of the proteins. Additionally, the transient nature of the binding interaction could be insufficient to offer effective defenses.

Yes, we agree with the reviewer and hope that grant reviewers’ share this colleague’s enthusiasm for understanding the detailed molecular mechanisms of RdnE-RdnI binding across genera. In the revised manuscript, we have continued to emphasize such caveats as the next frontier is clearly understanding the molecular mechanisms for RdnI cognate or non-cognate protection. In the revised manuscript, figure 4 Supplement Figure 2 shows the RdnI protein levels; we also clarified the expression constructs in the text (see reviewer 2, comment 2).

(2) The results from the mixed population competition lack quantitative analysis. The swarm competition assays only yield binary outcomes (Yes or No), limiting the ability to obtain more detailed insights from the data.

The mixed swam assay is needed when studying T6SS effectors that are primarily secreted during Proteus’ swarming activity (Saak et al. 2017, Zepeda-Rivera et al. 2018). This limitation is one reason we utilize in vitro, in vivo, and bioinformatic analyses. Though the swarm competition assay yields a binary outcome, we are confident that the observed RdnI protection is due to interaction with a trans-cell RdnE via an active T6SS. By contrast, many manuscripts report co-expression of the EI pair (Yadev et al., 2021, Hespanhol et al., 2022) rather than secreted effectors, as we have achieved in this manuscript.

(3) The discovery of cross-species protection is solely evident in the heterologous expression-competition model. It remains uncertain whether this is an isolated occurrence or a common characteristic of RdnI immunity proteins across various scenarios. Further investigations are necessary to determine the generality of this behavior.

We agree, which is why we submitted this paper as a launching point for further investigations into the generality of non-cognate interactions and their potential impact on community structure.

Comments from Reviewing Editor:<br />  - In addition to the references provided by reviewer#2, the first manuscript to show non-cognate binding of immunity proteins was Russell et al 2012 (PMID: 22607806).<br />  - IdrD was shown to form a subfamily of effectors in this manuscript by Hespanhol et al 2022 PMID: 36226828 that analyzed several T6SS effectors belonging to PDDExK, and it should be cited.

We appreciate that the reviewer and eLife staff pointed out missed citations. We have incorporated these studies and cited them in the revised manuscript.

[1] The Proteus RdnE in complex with either the Prevotella or Pseudomonas RdnI showed low confidence at the interface (pIDDT ~50-70%); this AI-predicted complex might support the lack of binding seen in the bacterial two-hybrid assay. On the other hand, the Proteus and Rothia RdnI N-terminal regions show higher confidence at the interface with RdnE. Despite this, the C-terminus of the Proteus RdnI shows especially low confidence (pIDDT ~50%) where it might interact near RdnE’s active site (as suggested by reviewer 1). Given this low confidence and the already stated inaccuracies of AI-generated complexes, we would rather wait for crystallization data to inform potential protection mechanisms of RdnI.

Author response image 1.

Author response:

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

eLife assessment

In this fundamental study, the authors use innovative fine-scale motion capture technologies to study visual vigilance with high-acuity vision, to estimate the visual fixation of free-feeding pigeons. The authors present convincing evidence for use of the fovea to inspect predator cues, the behavioral state influencing the latency for fovea use, and the use of the fovea decreasing the latency to escape of both the focal individual and other flock members. The work will be of broad interest to behavioral ecologists.

We thank the editor for his interest and feedback on the manuscript. We hereafter addressed the comments of the reviewer.

Reviewer #1 (Public Review):

Summary:

The authors were using an innovative technic to study the visual vigilance based on high-acuity vision, the fovea. Combining motion-capture features and visual space around the head, the authors were able to estimate the visual fixation of free-feeding pigeon at any moment. Simulating predator attacks on screens, they showed that 1) pigeons used their fovea to inspect predators cues, 2) the behavioural state (feeding or head-up) influenced the latency to use the fovea and 3) the use of the fovea decrease the latency to escape of both the individual that foveate the predators cues but also the other flock members.

Strengths:

The paper is very interesting, and combines innovative technic well adapted to study the importance of high-acuity vision for spotting a predator, but also of improving the behavioural response (escaping). The results are strong and the models used are well-adapted. This paper is a major contribution to our understanding of the use of visual adaptation in a foraging context when at risk. This is also a major contribution to the understanding of individual interaction in a flock.

Weaknesses:

I have identified only two weaknesses:

(1) The authors often mixed the methods and the results, Which reduces the readability and fluidity of the manuscript. I would recommend the authors to re-structure the manuscript.<br /> (2) In some parts, the authors stated that they reconstructed the visual field of the pigeon, which is not true. They identified the foveal positions, but not the visual fields, which involve different sectors (binocular, monocular or blind). Similarly, they sometimes mix-up the area centralis and the fovea, which are two different visual adaptations.

Thank you for your positive feedback. We addressed these comments by restructuring the methods and result sections as suggested, and by checking the terminology and specific vocabulary used throughout the manuscript.

Reviewer #1 (Recommendations For The Authors):

First, I would like to say that I really enjoyed the manuscript. This is a great contribution to the field.

Thank you for the positive feedback, we highly appreciate it.

Then, I have some comments that I hope, would help the authors to improve the manuscript.

Major comments :

I would recommend the authors to restructure the methods and the results section. In many parts, the models used are presented in the results section, while this should be presented in the methods section.

Thank you for the suggestion, we now have ensured that the model descriptions are presented in the statistic section of the methods.

To me, the introduction is too long (more than 5 pages). It would be beneficial to reduce it considerably. Furthermore, in the introduction, it misses some information about the visual abilities of your species ((visual acuity, visual field, temporal resolution, contrast sensitivity....).

We agree that the introduction was very long and reduced it by removing the “Methodological issues” as well as strongly reducing the “Experimental rationales” to a minimum. We also added the missing information on the visual abilities of the pigeons in the “Experimental rationales” section (see L135-150). Please note, however, that we refer to the temporal resolution of pigeon vision in the method section, to associate it with the information of the used monitor’s resolution.

Minor comments :

Lines 37-39: This needs a reference.

A reference has been added (McFarland, 1977)

Lines 39-41: But see some papers published recently on Harris's hawks.

Thank you for the references, we added the citation as well as a few more papers (Kane et al., 2015; Kano et al., 2018; Miñano et al., 2023; Yorzinski & Platt, 2014).

Lines 41-43: This sentence needs a reference as well.

A reference has been added (Cresswell, 1994; M. H. R. Evans et al., 2018; Inglis & Lazarus, 1981)

Lines 56-103: In this paragraph, head down and head up also depends from the retinal map of the birds! Some birds have visual streak that allow them to see a potential threats while foraging. Please add more information about the importance of photoreceptors distribution.

Thank you for pointing out this issue. We rewrote the sentence L65-69 as follows to include the importance retinal structures.

“In several species, especially those with a broad visual field and specific retinal structures such as the visual streaks, individuals can simultaneously engage in foraging activities while remaining vigilant (Fernández-Juricic, 2012), likely using peripheral vision to detect approaching threats (Bednekoff & Lima, 2005; Cresswell et al., 2003; Kaby & Lind, 2003; Lima & Bednekoff, 1999).”

Lines 76-79: you wrote : ".... favor alternative hypotheses based on their findings". Which findings? You need to explain.

We rewrote this part as follows (L80-81).

“other studies found evidence for the risk dilution (Beauchamp & Ruxton, 2008) and the edge effect (Inglis & Lazarus, 1981) in their study systems.”

Lines 109-110: It would be good to have a representation of what is an area and a fovea, and how it is placed in the eye, what type of fovea exists and how it is related to visual field. Where does it project?

We now give a better description of the pigeon’s visual field in the experimental rationales section that we hope will help the reader understanding the key features of pigeon’s vision (see L135-150). Specifically, we now say in L137-138:

“they have one fovea centrally located in the retina of each eye, with an acuity of 12.6 c/deg (Hodos et al., 1985). Their fovea projects laterally at ~75° into the horizon in their visual field.”

Lines 109-113: You might need to see some new papers here about the fovea. See for instance Bringmann 2019.

Thank you for the suggestion, we now give a more precise definition of the fovea and refer to Bringmann’s paper for more details (L113-114):

“a pit-like area in the retina with high concentration of cone cells where visual acuity is highest, and is responsible for sharp, detailed, and color vision.”

Lines 113-120: Please explain how the visual field is related to fovea? Where is the fovea project in the visual fields?

Similarly to the question above, we now give a more precise description of the pigeon’s visual field (see L135-150).

Line 131-134: For a non-expert, you would need to explain what is micro, meso and macro scale?

These sentences have been removed when shortening the introduction and we are not referring to micro, meso and macro scales anymore.

Lines 134-136: Please explain in one sentence the technique here.

We now explain in one sentence how motion capture enables the tracking of head and body orientation (L130-132):

“Motion capture cameras track with high accuracy the 3D position of markers, which, when attached to the pigeon’s head and body, enables to reconstruct the rotations of the head and body in all directions.”

Line 140: You presented here for the first time the word "foveation". Has this term been used before? If so, please add a reference. If not, please explain what you mean by foveation precisely.

Thank you for noticing this lack. We are now providing the following definition “directing visual focus to the fovea to achieve the clearest vision” in the first place where we mention the term foveation (L149-150).

Lines 146-148: Please explain why this proves that it is appropriate to not record eyes movements, and is this true for every behaviours?

We acknowledge that some small eye movement might occur and reduce the accuracy of the method. This error is considered in the system using the +-10 degrees range around the foveas. The lines the reviewer referred to were removed when shortening the introduction, but we added an explanation in the paragraph describing pigeon vision to make it clearer (L147-150):

“Yet, it should be noted that their eye movement was not tracked in our system, although it is typically confined within a 5 degrees range (Wohlschläger et al., 1993). We thus considered this estimation error of the foveation (directing visual focus to the fovea to achieve the clearest vision) in our analysis, as a part of the error margin (see Methods).”

Lines 161-163: What is the frontal and binocular field for? You would need to explain the different fields of view and what they are supposed to be for.

Furthermore, does the visual field of pigeon have been studied? If so, you would need to add more information about it.

This information is now given in the new paragraph describing the pigeon’s vision in the  “Experimental rationales” section (see L135-150).

Figure 1: It is not clear here which panels correspond to a, b or c. Please use some boxes to clarify it.

Thank you for the comment, we now have made the figure’s sub-panels clearer.

Lines 193-194: You wrote "... such as foveas (also known as the area centralis). No, this is not the same.

(1) In some species, you have two foveas, one placed centrally in the retina, one place temporally. So the fovea is not the area centralis.

(2) Second, some species do have an area centralis but without a fovea.

Thank you for pointing out the inaccuracy. In this case, we were referring specifically to the pigeon’s fovea which is sometimes referred to as “area centralis”, but we now changed the sentence as follow to avoid any confusion (L174-175):

“The initial two hypotheses (Hypotheses 1 and 2) aim to examine whether foveation correlates with predator detection.”

Lines 192-212: I did not understand the logic of the hypotheses numbers? Why do you have 2.1 but not 3.1 for instance? And if you have two hypotheses for the within a global one (for instance, 2.1 and 2.2), what is the main hypothesis 2? You should explain more here because we get lost here and in the result section as well.

We recognize this section might have appeared confusing to the reader. In short, we had four main hypotheses: 1) the fovea is used to evaluate predator cues, 2) the latency to foveate is related to vigilance behaviors. These first 2 hypotheses aimed to determine if the latency to foveate on the predator cue could be related to the detection. 3) foveation is related to the escape response of the pigeons and 4) there is a collective influence in the escape response. We further divided some of the hypotheses into 2 sub-hypotheses whenever 2 different tests were used to answer the same question. We have modified this section to be clearer.

Lines 224-229: Where are the figures and statistics for these results?

These results are presented in Table S1. We apologize for forgetting to add this reference and have now added it (L211).

Lines 229-231: This should be in the method section.

This model explanation (as well as all other hereafter mentioned) have been moved to the method section as suggested.

Lines 248-252: This should be in the method section. Furthermore, you should better explain the model selection.

Please see earlier comment. Additionally, we are now better explaining how the model has been built.

Figure 2: It is not clear on the figure which letters correspond to which panels. Please improve the readability of the figure.

It was modified accordingly.

Lines 274-278: This should be in the method section.

Please see earlier comment.

Line 281: The "Fig.3" should be mentioned in the previous sentence.

It was modified accordingly.

Figure 3: Please explain why the latency to foveate had negative values in Fig.2 but not here, and not in Fig. 4 as well. This again highlights that we missed a number of information in the methods about the transformation of the data and the model selection.

The variable presented in Fig 2d is not the latency to foveate but the “Normalized frequency at which the object was observed within foveal regions” (hypothesis 1). It represents the amount of time the object was lying within one of the foveal regions of the individual (“how long the pigeons foveated on it”), further normalized to unit sum to make all objects comparable. This variable was indeed logit-transformed (hence the negative value) to improve residual fit in the model, but this information (as well as other transformations) are always clearly stated on the axis caption of the graphs. Additionally, we now have improved the statistical analysis section to make the model used for each hypothesis testing clearer. But please let us know if you have suggestions for a further improvement in terms of presentation.

Lines 297-301: This should be in the method section.

Please see earlier comment.

Lines 301-305: Fig. 3 b and c only referred to the two first factors. Please add more figures for the other factors. This could be in supp. Mat.

We added the 3 graphs for the proportion of time foveating on the monitor, the saccade rate and the proportion of time foveating on conspecifics in the supplementary (Fig S6).

Lines 306-309: This should be in methods, and you should have explained in methods how you performed your model selection.....

We prefer leaving this paragraph in the result section, as it was intended to give the reader extra information on the predictive power of the different variables (by comparing the effectiveness of the models including one variable at a time, all the rest being equal) and not on the model selection per se. However, we now explain our goal better in the statistics section regarding this analysis (L635-636):

“We further tested the relative predictive power of the different test variables by comparing the resulting models’ efficiency using AIC scores.”

Lines 317-319: This should be in the method section.

Please see earlier comment.

Lines 320-322: This should be in the method section.

Please see earlier comment.

Lines 332-334: This should be in the method section.

Please see earlier comment.

Lines 334-336: Then, if this is not significant, you cannot say that.

Thank you for noticing the inaccuracy, we have now rephrased it as (L298-299):

“Earlier foveation of the first pigeon was not significantly related to an earlier escape responses among the other flock members, although there was a trend (χ2(1) = 3.66, p = 0.0559).”

Line 336: Please explain why you did different models. We missed a lot of information in the method about your strategy for statistics.?

We have now added a lot more information on the models in the statistics section, according to this comment as well as the previous ones. We hope the explanations of the analyses are now clearer to the reader.

Lines 339-349: This should be in the method section.

Please see earlier comment.

Results section: As you may have understood, there are too many sentence that should be moved into the method section. Futhermore, I would recommend to modify the headdings so that they are more biologically speaking. Similarly to what you have done in the discussion section.

Thank you for the comments. We agree with most of them, and have modified the manuscript accordingly. Additionally, we now use the same headings in the results section as the ones used in the discussion to make the text easier to follow.

Lines 500-501: What were the body weight of the pigeon? At which weight of their full weight they were?

This information is now added (492 ± 41g; mean ± SD). We did not control the amount of food during our experiments and only ensured 24h without food by feeding the pigeons after the experiment was completed. This information was added as follows (L454-456):

“On experimental days, they were fed only after the experiments was completed; this ensures 24-hour no feeding at the time of the experiment, although we did not control the amount of the food over the course of the experimental periods.”

Line 522-523: Those screens are very good for pigeons.

Thank you for the positive comment, we indeed tried to match bird vision as close as possible.

Lines 527-528: At which frequency was produced the moving stimulus? Your screen can display up to 144Hz, which is very good. But can your laptop do it? If not, it is important to mention it as pigeons may have a temporal resolution of vision up to 149Hz.

Our laptop indeed supports 144Hz display. In addition, we now mention the temporal resolution of pigeon vision (L480-482).

“We specifically chose a monitor with high temporal resolution to match the pigeon’s Critical Flicker Fusion Frequency (threshold at which a flickering light is perceived by the eye as steady) that reaches up to 143Hz (Dodt & Wirth, 1954).”

Lines 555-572: Did you use a control shape in your experiment? Indeed, they may escape because of a moving pattern but not a predator shape?

We did not use a control shape, as the aim of the experiment was not to directly test the effect of the shape itself. We designed the predator cue to resemble an approaching predator to ensure a response from the pigeons, but it might be that other shapes would have worked as well.

Lines 588-589: Please explain why the coordinate system of the pigeon's head is considered as the visual field?

From what I have understood, you did not reconstruct the visual fields, but only the position of the fovea. This should be noted like this as visual field involves more than a sphere around the head (binocular and monocular sectors, blind sectors, vertical extension....).

Thank you for noticing the inaccuracy, we indeed did not consider other sectors of the visual field and therefore rephrased it as (L551): “the location of the objects and conspecifics from the pigeon’s perspective”.

Lines 601-604: How much does it represent?

As this was estimated by visual inspection, we do not have the exact percentage of data loss that was caused by grooming. However, because of the number of cameras in the SMART BARN motion capture system, it is reliable in detecting markers inside the space in “ideal” conditions (without occlusion). For example, a similar set-up found marker track loss of only <1% using a model bird (Itahara & Kano 2022)

Itahara, A., & Kano, F. (2022). “Corvid Tracking Studio”: A custom-built motion capture system to track head movements of corvids. Japanese Journal of Animal Psychology, 72(1), 1–16. https://doi.org/10.2502/janip.72.1.1

Lines 610-612: You would need to cite Wood 1917 and Hodos et al. 1991 who described the presence of a fovea in this species.

We added both citations to the manuscript.

Line 611: Again, the fovea is not egal to area centralis.

Thank you, we changed it as well.

Lines 625-626: you wrote "... in a few instances....". Please explain more. How many? What proportion?

This happened in 9 observations out of 120. We now specify it in the text as well (L587-589):

“in a few instances (9 out of 120 observations), pigeons foveated on the model predator after the looming stimulus had disappeared, but these cases were excluded from our analysis.”

Lines 640-653: We missed a lot of information in the section "statistical analysis". If you moved most of the sentence from the results that describe the methods in the method section, that would be much better. Furthermore, you would need to explain more what statistics you used, which model selection, what type of data transformation....

We agree this section lacked information, and we moved the information from the result to the statistics section.

Supplmentary materials: boxplots from Fig. S1 and S2 are too small and impossible to read. Please improve the readability.

We now have enlarged these plots to make them more readable.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript "Engineering of PAClight1P78A: A High-Performance Class-B1 GPCR-Based Sensor for PACAP1-38" by Cola et al. presents the development of a novel genetically encoded sensor, PAClight1P78A, based on the human PAC1 receptor. The authors provide a thorough in vitro and in vivo characterization of this sensor, demonstrating its potential utility across various applications in life sciences, including drug development and basic research.

The diverse methods to validate PAClight1P78A demonstrate a comprehensive approach to sensor engineering by combining biochemical characterization with in vivo studies in rodent brains and zebrafish. This establishes the sensor's biophysical properties (e.g., sensitivity, specificity, kinetics, and spectral properties) and demonstrates its functionality in physiologically relevant settings. Importantly, the inclusion of control sensors and the testing of potential intracellular downstream effects such as G-protein activation underscore a careful consideration of specificity and biological impact.

Strengths:

The fundamental development of PAClight1P78A addresses a significant gap in sensors for Class-B1 GPCRs. The iterative design process -starting from PAClight0.1 to the final PAClight1P78A variant - demonstrates compelling optimization. The innovative engineering results in a sensor with a high apparent dynamic range and excellent ligand selectivity, representing a significant advancement in the field. The rigorous in vitro characterization, including dynamic range, ligand specificity, and activation kinetics, provides a critical understanding of the sensor's utility. Including in vivo experiments in mice and zebrafish larvae demonstrates the sensor's applicability in complex biological systems.

Weaknesses:

The manuscript shows that the sensor fundamentally works in vivo, albeit in a limited capacity. The titration curves show sensitivity in the nmol range at which endogenous detection might be possible. However, perhaps the sensor is not sensitive enough or there are not any known robust paradigms for PACAP release. A more detailed discussion of the sensors's limitations, particularly regarding in vivo applications and the potential for detecting endogenous PACAP release, would be helpful.

We thank the reviewer for carefully analyzing our in vivo data and highlighting the limitation of our results regarding the sensor’s applicability in detecting endogenous PACAP. We added several sections conversing future possibilities for optimization in the discussion (see paragraphs 2-4). We agree that a more specific discussion of the limitations of our study is an important addition to help design future experiments. 

There are several experiments with an n=1 and other low single-digit numbers. I assume that refers to biological replicates such as mice or culture wells, but it is not well defined. n=1 in experimental contexts, particularly in Figure 1, raises significant concerns about the exact dynamic range of the sensor, data reproducibility, and the robustness of conclusions drawn from these experiments. Also, ROI for cell cultures, like in Figure 1, is not well defined. The methods mentioned ROIs were manually selected, which appears very selective, and the values in Figure 1c become unnecessarily questionable. The lack of definition for "ROI" is confusing. Do ROIs refer to cells, specific locations on the cell membrane, or groups of cells? It would be best if the authors could use unbiased methods for image analysis that include the majority of responsive areas or an explanation of why certain ROIs are included or excluded.

We thank the reviewer for the helpful suggestions. We have increased the number of replicates to n=3 for both HEK293T and neuron data depicted in Fig.1c. Furthermore, we have added Fig.1c’ containing the quantification of the maximum responses obtained in the dataset shown in Fig.1c also depicting the single values for each replicate. To clarify the definition of an ROI in our manuscript, we have detailed the process of ROI selection in the Methods section “Cell culture, imaging and quantification section”. Additionally, we also increased mouse numbers for in vivo PACAP infusions in mice (see Figure 4g).

Reviewer #2 (Public Review):

Summary:

The PAClight1 sensor was developed using an approach successful for the development of other fluorescence-based GPCR sensors, which is the complete replacement of the third intracellular loop of the receptor with a circularly-permuted green fluorescent protein. When expressed in HEK cells, this sensor showed good expression and a weak but measurable response to the extracellular presence of PACAP1-38 (a

F/Fo of 43%). Additional mutation near the site of insertion of the linearized GPF, at the C-terminus of the receptor, and within the second intracellular loop produced a final optimized sensor with F/Fo of >1000%. Finally, screening of mutational libraries that also included alterations in the extracellular ligand-binding domain of the receptor yielded a molecule, PAClight1P78A, that exhibited a high ligand-dependent fluorescence response combined with a high differential sensitivity to PACAP (EC50 30 nM based on cytometric sorting of stably transfected HEK293 cells) compared to its congener VIP, (with which PACAP shares two highly related receptors, VPAC1 and VPAC2) as well as several unrelated neuropeptides, and significantly slowed activation kinetics by PACAP in the presence of a 10-fold molar excess of the PAC1 antagonist PACAP6-38. A structurally highly similar control construct, PAClight1P78Actl, showed correspondingly similar basal expression in HEK293 cells, but no PACAP-dependent enhancement in fluorescent properties.

PAClight1P78A was expressed in neurons of the mouse cortex via AAV9.hSyn-mediated gene transduction. Slices taken from PAClight1P78A-transfected cortex, but not slices taken from PAClight1P78Actl-transfected cortex exhibited prompt and persistent elevation of F/Fo after 2 minutes of perfusion with PACAP1-38 which persisted for up to 14 minutes and was statistically significant after perfusion with 3000, but not 300 or 30 nM, of peptide. Likewise, microinfusion of 200 nL of 300 uM PACAP1-38 into the cortex of optical fiber-implanted freely moving mice elicited a F/Fo (%) of greater than 15, and significantly higher than that elicited by application of similar concentrations of VIP, CRF, or enkephalin, or vehicle alone. In vivo experiments were carried out in zebrafish larvae by the introduction of PAClight1P78A into single-cell stage Danio rerio embryos using a Tol2 transposase-based plasmid with a UAS promoter via injection (of plasmid and transposase mRNA), and sorting of post-fertilization embryos using a marker for transgenesis carried in the UAS :

PAClight1P78A construct. Expression of PAClight1P78A was directed to cells in the olfactory bulb which express the fish paralog of the human PAC1 receptor by using the Tg(GnRH3:gal4ff) line, and fluorescent signals were elicited by intracerebroventricular administration of PACAP1-38 at a single concentration (1 mM), which were specific to PACAP and to the presence of PAClight1P78A per se, as controlled by parallel experiments in which PAClight1P78Actl instead of PAClight1P78A was contained in the transgenic plasmid.

Major strengths and weaknesses of the methods and results

The report represents a rigorous demonstration of the elicitation of fluorescent signals upon pharmacological exposure to PACAP in nervous system tissue expressing PAClight1P78A in both mammals (mice) and fish (zebrafish larvae). Figure 4d shows a change in GFP fluorescence activation by PACAP occurring several seconds after the cessation of PACAP perfusion over a two-minute period, and its persistence for several minutes following. One wonders if one is apprehending the graphical presentation of the data incorrectly, or if the activation of fluorescence efficiency by ligand presentation is irreversible in this context, in which case the utility of the probe as a real-time indicator, in vivo, of released peptide might be diminished.

We thank the reviewer for their careful consideration of our manuscript and agree that the activation of PAClight persisting for several minutes at micromolar concentrations could be a potential limitation for in vivo applications. We added a possible explanation for the persisting sensor activation in response to artificial application of PACAP38 in paragraph 3 of the discussion. We agree that this addition eases the interpretation of PAClight signals detected in vivo. 

Appraisal of achievement of aims, and data support of conclusions:

Small cavils with controls are omitted for clarity; the larger issue of appraisal of results based on the scope of the designed experiments is discussed in the section below. An interesting question related to the time dependence of the PACAP-elicited activation of PAClight1P87A is its onset and reversibility, and additional data related to this would be welcome.

We agree that the reversibility of the sensor’s fluorescence is indeed an important feature especially for detecting endogenous PACAP release. Our data indicate that the sensor’s fluorescence is reversible when detecting small to medium doses of PACAP38 (see Figure 4d – Application of 30-300nM) that are presumably closer to physiological concentrations than the non-reversible concentration of 3000nM. Please, see also our new discussion on peptide concentrations in paragraph 4 of our discussion. For future experiments, it is indeed advisable to adjust the interval of repeated applications to the decay of the response at the respective concentration. Considering, the long-lasting downstream effects of endogenous signaling, longer intervals between ligand applications are generally preferred to match more closely the physiological range in which endogenous PAC1 is most likely affective. 

Discussion of the impact of the work, and utility of the methods and data:

Increasingly, neurotransmitter function may be observed in vivo, rather than by inferring in vivo function from in vitro, in cellular, or ex vivo experimentation. This very valuable report discloses the invention of a genetically encoded sensor for the class B1 GPCR PAC1. PAC1 is the major receptor for the neuropeptide PACAP, which in turn is a major neurotransmitter involved in brain response to psychogenic stress, or threat, in vertebrates as diverse as mammals and fishes. If this sensor possesses the sensitivity to detect endogenously released PACAP in vivo it will indeed be an impactful tool for understanding PACAP neurotransmission (and indeed PACAP action in general, in immune and endocrine compartments as well) in future experiments.

However, the sensor has not yet been used to detect endogenously released PACAP. Until this has been done, one cannot answer the question as to whether the levels of exogenously perfused/administered PACAP used here merely to calibrate the sensor's sensitivity are indeed unphysiologically high. If endogenous PACAP levels don't get that high, then the sensor will not be useful for its intended purpose. The authors should address this issue and allude to what kind of experiments would need to be done in order to detect endogenous PACAP release in living tissue in intact animals. The authors could comment upon the success of other GPCR sensors that have been used to observe endogenous ligand release, and where along the pathway to becoming a truly useful reagent this particular sensor is.

We thank the reviewer for highlighting the lack in clarity that the scope of this paper was not intended to cover the detection of endogenous PACAP release. We therefore expanded our discussion to encompass the intended purpose of detecting artificially infused or applied PAC1 agonists, such as conducting fundamental tests of drug specificity and developing new pharmacological ligands to selectively target PAC1. This includes a more detailed discussion of our in vivo findings and a clearer phrasing that stresses the potential application for applied drugs and not endogenous PACAP (see last paragraph in the discussion).

We also agree that little is known about endogenous concentrations of PACAP in the brain. However, we have supplemented our discussion with several references estimating lower concentrations of PACAP and other peptides in vivo, suggesting average PACAP levels below the detection threshold of the sensor. Importantly, within certain brain regions and in closer proximity to release sites, significantly higher concentrations might be reached. Additionally, our data indicate that the concentrations observed under our current conditions do not saturate the sensor in vivo.  

We therefore acknowledge the reviewer’s comment on the sensor’s potential limitations under our current experimental conditions. Hence, we expanded our discussion and suggest the use of higher resolution imaging to potentially reveal loci of high PACAP concentrations, which should be validated by future studies (see also our added discussion in paragraph 4). 

Reviewer #3 (Public Review):

Summary:

The manuscript introduces PAClight1P78A, a novel genetically encoded sensor designed to facilitate the study of class-B1 G protein-coupled receptors (GPCRs), focusing on the human PAC1 receptor. Addressing the significant challenge of investigating these clinically relevant drug targets, the sensor demonstrates a high dynamic range, excellent ligand selectivity, and rapid activation kinetics. It is validated across a variety of experimental contexts including in vitro, ex vivo, and in vivo models in mice and zebrafish, showcasing its utility for high-throughput screening, basic research, and drug development efforts related to GPCR dynamics and pharmacology.

Strengths:

The innovative design of PAClight1P78A successfully bridges a crucial gap in GPCR research by enabling realtime monitoring of receptor activation with high specificity and sensitivity. The extensive validation across multiple models emphasizes the sensor's reliability and versatility, promising significant contributions to both the scientific understanding of GPCR mechanisms and the development of novel therapeutics. Furthermore, by providing the research community with detailed methodologies and access to the necessary viral vectors and plasmids, the authors ensure the sensor's broad applicability and ease of adoption for a wide range of studies focused on GPCR biology and drug targeting.

Weaknesses

To further strengthen the manuscript and validate the efficacy of PAClight1P78A as a selective PACAP sensor, it is crucial to demonstrate the sensor's ability to detect endogenous PACAP release in vivo under physiological conditions. While the current data from artificial PACAP application in mouse brain slices and microinfusion in behaving mice provide foundational insights into the sensor's functionality, these approaches predominantly simulate conditions with potentially higher concentrations of PACAP than naturally occurring levels.

We thank the reviewer for their valuable comments and agree that the use of PAClight for detecting endogenous PACAP will be of big interest for the scientific community and should be a goal for future research. Considering the time, equipment and additional animal licenses necessary, we are convinced that these questions would go beyond the scope of the current paper and might rather be addressed in a follow-up publication. We therefore rephrased the discussion and added more details to clarify further the intended purpose of the current study. Additionally, we added a paragraph in the discussion suggesting experiments needed to validate PAClight for putative future in vivo applications. 

Although the sensor's specificity for the PAC1 receptor and its primary ligand is a pivotal achievement, exploring its potential application to other GPCRs within the class-B1 family or broader categories could enhance the manuscript's impact, suggesting ways to adapt this technology for a wider array of receptor studies. Additionally, while the sensor's performance is convincingly demonstrated in short-term experiments, insights into its long-term stability and reusability in more prolonged or repeated measures scenarios would be valuable for researchers interested in chronic studies or longitudinal behavioral analyses. Addressing these aspects could broaden the understanding of the sensor's practical utility over extended research timelines.

We extend our gratitude to the reviewer for diligently assessing our results. 

Indeed, the very high level of sensitivity that we could achieve in PAClight leads us to think that potentially a grafting-based approach, such as the one we’ve recently described for class-A GPCR-based sensors (PMID: 37474807) could also work for the direct generation of multiple class-B1 sensors based on the optimized fluorescent protein module present in PAClight. Unfortunately, considering the amount of work that testing this hypothesis would entail, we are not able to perform these experiments in the context of this revision, and would rather pursue them as a future project. Nevertheless, we have expanded the discussion of the manuscript with a paragraph with these considerations.

While we lack comprehensive data on the long-term stability of the sensor, our preliminary findings from photometry recordings optimization indicate consistent baseline expression of PAClight and PACLight ctrl over several weeks. Conducting experiments to systematically assess stability would require several months, which is currently impractical due to limitations in tools and licenses for repeated in vivo infusions. Hence, we intend to include these experiments in potential follow-up studies.

Furthermore, the current in vivo experiments involving microinfusion of PACAP near sensor-expressing areas in behaving mice are based on a relatively small sample size (n=2), which might limit the generalizability of the findings. Increasing the number of subjects in these experimental groups would enhance the statistical power of the results and provide a more robust assessment of the sensor's in vivo functionality. Expanding the sample size will not only validate the findings but also address potential variability within the population, thereby reinforcing the conclusions drawn from these crucial experiments.

We agree with the reviewer that a sample size of N=2 is not sufficient for in vivo recordings. We therefore increased the sample size and now present recordings with 5 PAClight1P78A and 4 PACLight-control mice. Of note, the new data validate our previous findings and conclusions and give a better idea of the variability in vivo that we now discuss in much more detail in the discussion (see paragraph 2). 

Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

The lower potency of maxadilan activation might reflect broader implications for ligand-receptor dynamics. Perhaps the authors could discuss the maxadilan binding from a structural perspective, including AlphaFold models. Also, discussing how these findings might influence sensor application in diverse biological contexts would be insightful. Clear definitions and consistent use of these terms are crucial for ensuring that readers understand the methods and results.

We would like to thank the reviewer for the comments. As part of this work, we did not obtain a dose-response curve for maxadilan peptide, and only reported the maximal response of the sensor to a high concentration of the peptide (10 µM). Thus, our findings would rather inform us on the maximal efficacy of the peptide, as opposed to its potency towards the PAC1R. Furthermore, we would like to point out that due to the lack of structural details for any GPCR-based sensor published to date, we cannot make any molecularly accurate conclusion regarding the precise reasons why a different ligand (in this case the sandfly maxadilan) induces a lower maximal efficacy of the response compared to the endogenous cognate ligand of the receptor. We do not believe that AlphaFold models can accurately replace structural information in this regard, especially given the consideration that the aminoacid linker regions between the GPCR and the fluorescent protein, which are a critical determinant of allosteric chromophore modulation by ligand-induced conformational changes, typically obtain the lowest confidence score in all AlphaFold predicted structural models of GPCR-based sensors. Finally, we would like to refer the reviewer to a very nice recent publication (PMID: 32047270) which resolved the structures of each of these peptides bound to the PAC1 receptor-Gs protein complex, which provides accurate molecular details on the different modalities of receptor binding and activation by PACAP138  versus maxadilan.

Reviewer #2 (Recommendations For The Authors):

The authors are congratulated on the meticulous achievement of their aim, i.e. a fluorescence-based sensor for the detection of PACAP with in vivo utility. Whether or not this sensor will have the requisite sensitivity to detect the release of endogenous PACAP within various regions of the nervous system, in response to specific environmental stimuli or changes in brain or physiological state, remains to be determined.

We thank the reviewer for the very positive evaluation of our manuscript and for the suggested additions that will improve the strength of our arguments.

We agree that the in vivo detection of endogenous PACAP will be an important objective for future studies. Due to time, resource and animal license constraints, we are not able to address this objective in our current study, but we now detail possible future experiments in the discussion section. Please see also our answer to the suggested discussion points previously.

Reviewer #3 (Recommendations For The Authors):

To comprehensively assess the sensor's sensitivity and specificity to endogenous PACAP, I recommend conducting additional in vivo experiments where PAClight1P78A is expressed in neurons that endogenously express the Pac1r receptor (using Adcyap1r1-Cre mouse line). These experiments should involve applying sensory or emotional stimuli known to evoke PACAP release or activating upstream PACAP-expressing neurons. Such studies would offer valuable data on the sensor's performance under natural physiological conditions and its potential utility for exploring PACAP's roles in vivo.

We express our gratitude to the reviewer for providing detailed methodological approaches to examine endogenous PACAP release. These suggestions will prove invaluable for future investigations and are important additions to a follow-up publication. As mentioned earlier, we have incorporated some of these approaches into our discussion. Additionally, we have underscored the existing limitations in detecting endogenous PACAP in vivo and emphasized the relevance of PAClight for drug development purposes.

Author response:

eLife assessment

This useful study describes an antibody-free method to map G-quadruplexes (G4s) in vertebrate cells. While the method might have potential, the current analysis is primarily descriptive and does not add substantial new insights beyond existing data (e.g., PMID:34792172). While the datasets provided might constitute a good starting point for future functional studies, additional data and analyses would be needed to fully support the major conclusions and, at the same time, clarify the advantage of this method over other methods. Specifically, the strength of the evidence for DHX9 interfering with the ability of mESCs to differentiate by regulating directly the stability of either G4s or R-loops is still incomplete.

We thank the editors for their helpful comments.

Given that antibody-based methods have been reported to leave open the possibility of recognizing partially folded G4s and promoting their folding, we have employed the peroxidase activity of the G4-hemin complex to develop a new method for capturing endogenous G4s that significantly reduces the risk of capturing partially folded G4s. We will be happy to clarify the advantage of our method.

In the Fig. 7, we applied the Dhx9 CUT&Tag assay to identify the G4s and R-loops directly bound by Dhx9 and further characterized the differential Dhx9-bound G4s and R-loops in the absence of Dhx9. Dhx9 is a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). Furthermore, we showed that depletion of Dhx9 significantly altered the levels of G4s or R-loops around the TSS or gene bodies of several key regulators of mESC and embryonic development, such as Nanog, Lin28a, Bmp4, Wnt8a, Gata2, and Lef1, and also their RNA levels (Fig.7 I). The above evidence is sufficient to support the transcriptional regulation of mESCs cell fate by directly modulating the G4s or R-loops within the key regulators of mESCs.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Non-B DNA structures such as G4s and R-loops have the potential to impact genome stability, gene transcription, and cell differentiation. This study investigates the distribution of G4s and R-loops in human and mouse cells using some interesting technical modifications of existing Tn5-based approaches. This work confirms that the helicase DHX9 could regulate the formation and/or stability of both structures in mouse embryonic stem cells (mESCs). It also provides evidence that the lack of DHX9 in mESCs interferes with their ability to differentiate.

Strengths:

HepG4-seq, the new antibody-free strategy to map G4s based on the ability of Hemin to act as a peroxidase when complexed to G4s, is interesting. This study also provides more evidence that the distribution pattern of G4s and R-loops might vary substantially from one cell type to another.

We appreciate your valuable points.

Weaknesses:

This study is essentially descriptive and does not provide conclusive evidence that lack of DHX9 does interfere with the ability of mESCs to differentiate by regulating directly the stability of either G4 or R-loops. In the end, it does not substantially improve our understanding of DHX9's mode of action.

In this study, we aimed to report new methods for capturing endogenous G4s and R-loops in living cells. Dhx9 has been reported to directly unwind R-loops and G4s or promote R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). To understand the direct Dhx9-bound G4s and R-loops, we performed the Dhx9 CUT&Tag assay and analyzed the co-localization of Dhx9-binding sites and G4s or R-loops. We found that 47,857 co-localized G4s and R-loops are directly bound by Dhx9 in the wild-type mESCs and 4,060 of them display significantly differential signals in absence of Dhx9, suggesting that redundant regulators exist as well. We showed that depletion of Dhx9 significantly altered the RNA levels of several key regulators of mESC and embryonic development, such as Nanog, Lin28a, Bmp4, Wnt8a, Gata2, and Lef1, which coincides with the significantly differential levels of G4s or R-loops around the TSS or gene bodies of these genes (Fig.7). The comprehensive molecular mechanism of Dhx9 action is indeed not the focus of this study. We will work on it in the future studies. Thank you for the comments.

There is no in-depth comparison of the newly generated data with existing datasets and no rigorous control was presented to test the specificity of the hemin-G4 interaction (a lot of the hemin-dependent signal seems to occur in the cytoplasm, which is unexpected).

The specificity of hemin-G4-induced peroxidase activity and self-biotinylation has been well demonstrated in previous studies (PMID: 19618960, 22106035, 28973477, 32329781). In the Fig.1A, we compared the hemin-G4-induced biotinylation levels in different conditions. Cells treated with hemin and Bio-An exhibited a robust fluorescence signal, while the absence of either hemin or Bio-An almost completely abolished the biotinylation signals, suggesting a specific and active biotinylation activity. To identify the specific signals, we have included the non-label control and used this control to call confident HepG4 peaks in all HepG4-seq assays.

The hemin-RNA G4 complex has also been reported to have mimic peroxidase activity and trigger similar self-biotinylation signals as DNA G4s (PMID: 32329781, 31257395, 27422869). Therefore, it is not surprising to observe hemin-dependent signals in the cytoplasm generated by cytoplasmic RNA G4s.

In the revised version, we will include careful comparison between our data and previous datasets.

The authors talk about co-occurrence between G4 and R-loops but their data does not actually demonstrate co-occurrence in time. If the same loci could form alternatively either R-loops or G4 and if DHX9 was somehow involved in determining the balance between G4s and R-loops, the authors would probably obtain the same distribution pattern. To manipulate R-loop levels in vivo and test how this affects HEPG4-seq signals would have been helpful.

Single-molecule fluorescence studies have shown the existence of a positive feedback mechanism of G4 and R-loop formation during transcription (PMID: 32810236, 32636376), suggesting that G4s and Rloops could co-localize at the same molecule. Dhx9 is a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). Although depletion of Dhx9 resulted in 6,171 Dhx9-bound co-localized G4s and R-loops with significantly altered levels of G4s or R-loops, only 276 of them (~4.5%) harbored altered G4s and R-loops, suggesting that the interacting G4s and R-loops are rare in living cells. Nowadays, the genome-wide co-occurrence of two factors are mainly obtained by bioinformatically intersection analysis. We agreed that the heterogenous distribution between cells will give false positive co-occurrence patterns. We will carefully discuss this point in the revised version. At the same time, we will make efforts to develop a new method to map the co-localized G4 and R-loop in the same molecule in the future study.

This study relies exclusively on Tn5-based mapping strategies. This is a problem as global changes in DNA accessibility might strongly skew the results. It is unclear at this stage whether the lack of DHX9, BLM, or WRN has an impact on DNA accessibility, which might underlie the differences that were observed. Moreover, Tn5 cleaves DNA at a nearby accessible site, which might be at an unknown distance away from the site of interest. The spatial accuracy of Tn5-based methods is therefore debatable, which is a problem when trying to demonstrate spatial co-occurrence. Alternative mapping methods would have been helpful.

In this study, we used the recombinant streptavidin monomer and anti-GP41 nanobody fusion protein (mSA-scFv) to specifically recognize hemin-G4-induced biotinylated G4 and then recruit the recombinant GP41-tagged Tn5 protein to these G4s sites. Similarly, the recombinant V5-tagged N-terminal hybrid-binding domain (HBD) of RNase H1 specifically recognizes R-loops and recruit the recombinant protein G-Tn5 (pG-Tn5) with the help of anti-V5 antibody. Therefore, the spatial distance of Tn5 to the target sites is well controlled and very short, and also the recruitment of Tn5 is specifically determined by the existence of G4s in HepG4-seq and R-loops in HBD-seq.

Reviewer #2 (Public Review):

Summary:

In this study, Liu et al. explore the interplay between G-quadruplexes (G4s) and R-loops. The authors developed novel techniques, HepG4-seq and HBD-seq, to capture and map these nucleic acid structures genome-wide in human HEK293 cells and mouse embryonic stem cells (mESCs). They identified dynamic, cell-type-specific distributions of co-localized G4s and R-loops, which predominantly localize at active promoters and enhancers of transcriptionally active genes. Furthermore, they assessed the role of helicase Dhx9 in regulating these structures and their impact on gene expression and cellular functions.

The manuscript provides a detailed catalogue of the genome-wide distribution of G4s and R-loops. However, the conceptual advance and the physiological relevance of the findings are not obvious. Overall, the impact of the work on the field is limited to the utility of the presented methods and datasets.

Strengths:

(1) The development and optimization of HepG4-seq and HBD-seq offer novel methods to map native G4s and R-loops.

(2) The study provides extensive data on the distribution of G4s and R-loops, highlighting their co-localization in human and mouse cells.

(3) The study consolidates the role of Dhx9 in modulating these structures and explores its impact on mESC self-renewal and differentiation.

We appreciate your valuable points.

Weaknesses:

(1) The specificity of the biotinylation process and potential off-target effects are not addressed. The authors should provide more data to validate the specificity of the G4-hemin.

The specificity of hemin-G4-induced peroxidase activity and self-biotinylation has been well demonstrated in previous studies (PMID: 19618960, 22106035, 28973477, 32329781). In the Fig.1A, we compared the hemin-G4-induced biotinylation levels in different conditions. Cells treated with hemin and Bio-An exhibited a robust fluorescence signal, while the absence of either hemin or Bio-An almost completely abolished the biotinylation signals, suggesting a specific and active biotinylation activity.

(2) Other methods exploring a catalytic dead RNAseH or the HBD to pull down R-loops have been described before. The superior quality of the presented methods in comparison to existing ones is not established. A clear comparison with other methods (BG4 CUT&Tag-seq, DRIP-seq, R-CHIP, etc) should be provided.

Thank you for the suggestions. We will include the comparisons in the revised version.

(3) Although the study demonstrates Dhx9's role in regulating co-localized G4s and R-loops, additional functional experiments (e.g., rescue experiments) are needed to confirm these findings.

Dhx9 has been demonstrate as a versatile helicase capable of directly resolving R-loops and G4s or promoting R-loop formation in previous studies (PMID: 21561811, 30341290, 29742442, 32541651, 35905379, 34316718). We believe that the current new dataset and previous studies are enough to support the capability of Dhx9 in regulating co-localized G4s and R-loops.

(4) The manuscript would benefit from a more detailed discussion of the broader implications of co-localized G4s and R-loops.

Thank you for the suggestions. We will include a more detailed discussion in the revised version.

(5) The manuscript lacks appropriate statistical analyses to support the major conclusions.

We apologized for this point. Whereas we have applied careful statistical analyses in this study, lacking of some statistical details make people hard to understand some conclusions. We will carefully add details of all statistical analysis.

(6) The discussion could be expanded to address potential limitations and alternative explanations for the results.

Thank you for the suggestions. We will include a more detailed discussion about this point in the revised version.

Reviewer #3 (Public Review):

Summary:

The authors developed and optimized the methods for detecting G4s and R-loops independent of BG4 and S9.6 antibody, and mapped genomic native G4s and R-loops by HepG4-seq and HBD-seq, revealing that co-localized G4s and R-loops participate in regulating transcription and affecting the self-renewal and differentiation capabilities of mESCs.

Strengths:

By utilizing the peroxidase activity of G4-hemin complex and combining proximity labeling technology, the authors developed HepG4-seq (high throughput sequencing of hemin-induced proximal labelled G4s), which can detect the dynamics of G4s in vivo. Meanwhile, the "GST-His6-2xHBD"-mediated CUT&Tag protocol (Wang et al., 2021) was optimized by replacing fusion protein and tag, the optimized HBD-seq avoids the generation of GST fusion protein aggregates and can reflect the genome-wide distribution of R-loops in vivo.

The authors employed HepG4-seq and HBD-seq to establish comprehensive maps of native co-localized G4s and R-loops in human HEK293 cells and mouse embryonic stem cells (mESCs). The data indicate that co-localized G4s and R-loops are dynamically altered in a cell type-dependent manner and are largely localized at active promoters and enhancers of transcriptionally active genes.

Combined with Dhx9 ChIP-seq and co-localized G4s and R-loops data in wild-type and dhx9KO mESCs, the authors confirm that the helicase Dhx9 is a direct and major regulator that regulates the formation and resolution of co-localized G4s and R-loops.

Depletion of Dhx9 impaired the self-renewal and differentiation capacities of mESCs by altering the transcription of co-localized G4s and R-loops-associated genes.

In conclusion, the authors provide an approach to studying the interplay between G4s and R-loops, shedding light on the important roles of co-localized G4s and R-loops in development and disease by regulating the transcription of related genes.

We appreciate your valuable points.

Weaknesses:

As we know, there are at least two structure data of S9.6 antibody very recently, and the questions about the specificity of the S9.6 antibody on RNA:DNA hybrids should be finished. The authors referred to (Hartono et al., 2018; Konig et al., 2017; Phillips et al., 2013) need to be updated, and the authors' bias against S9.6 antibodies needs also to be changed. However, as the authors had questioned the specificity of the S9.6 antibody, they should compare it in parallel with the data they have and the data generated by the widely used S9.6 antibody.

Thank you for the updating information about the structure data of S9.6 antibody. We politely disagree the specificity of the S9.6 antibody on RNA:DNA hybrids. The structural studies of S9.6 (PMID: 35347133, 35550870) used only one RNA:DNA hybrid to show the superior specificity of S9.6 on RNA:DNA hybrid than dsRNA and dsDNA. However, Fabian K. et al has reported that the binding affinities of S9.6 on RNA:DNA hybrid exhibits obvious sequence-dependent bias from null to nanomolar range (PMID: 28594954). We will include the comparison between S9.6-derived data and our HBD-seq data in the revised version.

Although HepG4-seq is an effective G4s detection technique, and the authors have also verified its reliability to some extent, given the strong link between ROS homeostasis and G4s formation, and hemin's affinity for different types of G4s, whether HepG4-seq reflects the dynamics of G4s in vivo more accurately than existing detection techniques still needs to be more carefully corroborated.

Thank you for pointing out this issue. In the in vitro hemin-G4 induced self-biotinylation assay, parallel G4s exhibit higher peroxidase activities than anti-parallel G4s. Thus, the dynamics of G4 conformation could affect the HepG4-seq signals (PMID: 32329781). In the future, people may need to combine HepG4-seq and BG4s-eq to carefully explain the endogenous G4s. We will carefully discuss this point in the revised version.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

(1) Due to the significant difference between the infection timeline of mild (1 day post symptom onset) and severe (10 days post symptom onset) cohort at enrollment, an informative analysis to consider is to compare timepoint 2 from the mild cohort to timepoint 1 from the severe cohort.

In agreement with what the reviewer noted on his comment, to be more helpful we completed the analysis comparing timepoint 2 from the mild cohort to timepoint 1 from severe cohort, which is now included as Figure 4-figure supplement 5. The new text added is on pages 13-14, lines 346-355 explaining this analysis. We also included a paragraph in the discussion on page 22, lines 595-604. We have resolved to show this comparison to enforce the main observation related to Natural Killer Cytotoxicity pathways enriched in all analyses of this work.

(2) Alternatively, as this information is available, the authors may group the samples based on the individual's infection timeline as opposed to the recruitment timeline.

Patients in both groups were enrolled at the peak of their symptoms. According to this criterion, we grouped the patients to generate more significant results. Since these infections occurred naturally, we have no accurate information regarding the infection timing of patients. However, if the samples were grouped in order of individual infection timeline, the analysis would be statistically weak to make conclusions about the course of COVID-19, as disease progression would not be coordinated. Our grouping approach provided us a good confidence range, despite the tiny population evaluated.

(3) The authors selected three co-regulated network modules based on the size of module membership genes, selecting the three modules containing the largest gene membership. Small co-regulated networks can also offer important biological insights into specific molecular machinery associated with disease outcomes.

Figure 5 was updated including two more networks (besides blue), for brown and turquoise modules (5E and 5F). This new information allowed us to understand deeply the three larger modules with the most significant results, due to the number of genes they included (blue: 704, brown: 508, and turquoise: 712). The new text describing this analysis is included in page 15 lines 388-396. The remaining 7 modules were also analyzed, and the Gene Ontology/Pathways enrichment were included in 2 new supplemental figures (Figure 5 - figure supplement 1 and 2). The new text describing this analysis is included on page 15, lines 397-401.

(4) An alternative selection criterion that can inform biological associations between module genes and disease severity is the strength of the correlation coefficients. It seems from Figure 5B, that yellow, turquoise, and green modules have a moderate positive correlation with severe patients, while brown, blue, and gray modules show a slight positive correlation with mild outpatients. A recommendation for the authors is to consider revising Figure 5C to include the enrichment of these additional modules and include these modules in the interpretation of the results.

The correlations between cohorts and the modules (blue, brown and turquoise) are clearly identified for severe or mild patients. However, for several smaller modules, correlations are heterogenous for different patients of the cohorts, making it hard to gain a clear conclusion related to severity groups. In this sense, the 7 modules were analyzed as is indicated in the previous response number #3, and the results offer an idea of the different transcriptional programs present at different patients in different stages of disease. However, the small number of genes in some modules brings weak results of GO and enriched pathways, making it difficult to interpretation. The text describing this figure is included in page 15 lines 397-401. Also, the network analyses for brown and turquoise modules were included in figure 5 as 5E-F and the text detailing these figures was included on page 15 lines 388-396.

(5) In Figures 3E and 3F, the authors present enrichment analyses of differentially expressed genes from day 28. However, earlier in the results (lines 226-228), the authors reported no differentially expressed genes observed between the mild and severe participant cohort at this time point. Can the authors clarify which comparison was performed to obtain the list of differentially expressed genes used in the enrichment analyses in Figures 3E and 3F?

The discrepancy in this case stems from separate criteria employed for comparison in each case. At the pairwise comparison, DEGs list is different from the longitudinal comparison mentioned afterwards, as for this later analysis we selected only the genes with different trajectories throughout the study (Figure 3). To clarify this point, we included a new paragraph on page 11, lines 278-285.

Original:

“We detected 828 genes that exhibited temporal and quantitative expression level differences during the progression of disease. We discovered additional biological processes and KEGG pathways that were differentially enriched during the COVID-19 progression in mild and severe patients (Figure 3) using the Enrichr platform (G. Chen et al., 2020)”

Changed to:

“To do so, we first identified genes that were differentially expressed between severity groups, and second, we chose only those that also showed changes in their trajectories across sampling times. In doing so, we found 828 genes that exhibited temporal differences in expression level during disease progression. Then using the Enrichr platform (G. Chen et al., 2020), we discovered additional biological processes and KEGG pathways that were differentially enriched during the COVID-19 progression in mild and severe patients (Figure 3).”

(6) Additionally, the authors refer to specific enriched genes in Figure 3 (lines 298-302), but Figure 3 only displays the enriched terms. Can the authors include the results from the enrichment analysis that include gene membership for each enriched term in the supplement?

Certainly, there is no figure or table in the initial version that includes the gene list for this analysis. We have now included a supplement table 1 and 2 that details each pathway, along with its gene list.

(7) In line 104, can the authors clarify the parameters used to define well-matched samples?

Based on the observations made by the reviewers, we decided to change the wording to make it more obvious about the message of this paper. The update was included on page 5, line  as follows:

Original:

“Here, we designed a longitudinal investigation using well-matched samples to study how changes in gene expression in distinct immune effector cells changed during the earliest time points after diagnosis and during progression of clinical disease”,

Changed to:

“Here, we designed a longitudinal comparison between mild and severe patients, choosing the appropriate samples according to the clinical progression and the unbiased gene expression profile”

(8) In lines 113-116, can the authors clarify how their approach mitigates noise/potential biases and very briefly, describe what the nature of noise/biases could be?

The main goal of this paragraph is to show that, while there are several pathways with statistical significance in our analyses, the focus was on NK cell cytotoxicity because this molecular pathway showed bridges between other relevant immune responses; thus, the pathways chosen to respond to its intricated transcriptional program instead of a biased interest. The text was edited and included on page 6, line 111-131 as follows:

Original:

“We used a pairwise comparison of gene expression, gene set enrichment, and weight-correlated gene network analyses to detect differential expression of genes involved with the cytotoxic signaling pathway of Natural Killer (NK) cells in mild verses severe progression of disease. We promoted a broad and integrated point of view throughout the transcriptomic analysis of functional pathways to mitigate noise and potential biases (Bastard et al., 2020; Delorey et al., 2021; Schultze & Aschenbrenner, 2021; S. Zhang et al., 2022). We found close connectivity between NK signaling pathway genes and those of cytokine-cytokine receptor signaling pathways, along with Th1/Th2 cell differentiation genes, as part of the transcriptional circuit executed preferentially among mildly ill patients. Our results detected transcriptional circuits engaging multiple regulatory checkpoints. These findings indicated that the innate NK signaling pathway (cell cytotoxic activity) is beneficial, perhaps a critically-necessary activity needed to effectively eradicate coronavirus. We interpreted that an adaptive immune response that included early cell-mediated immunity was important for reducing disease severity in mild patients. This balance between humoral- and cell-mediated immunity appeared to be less robust in patients presenting with severe COVID-19. These results detected components of the immune response that were significantly associated with the differences in symptom severity observed between mild and severely ill COVID-19 patients.”

Changed to:

“Briefly, to gain more insights into our findings and complement their functional context, we used a pairwise comparison of gene expression, gene set enrichment, and weight-correlated gene network analyses. By doing so, we identified pathways of genes involved with the NK cell cytotoxicity enriched in mild patients when compared to severe. Besides focusing on a particular molecular pathway, we investigated the interactions to better comprehend the underlying phenomena of a successful immune response, contributing to an integrated point of view throughout the transcriptomic analyses of functional pathways to mitigate potential biases attributed to focusing the study on a single pathway. In this regard, we revealed that the NK signaling pathway was intricately related to other transcriptional circuits, such as those governing Th1/Th2 cell differentiation and cytokine-cytokine receptor signaling pathways. These interactions highlight the importance of these pathways as bridges between the innate and adaptive immune responses throughout the disease, implying that the innate NK signaling pathway (cell cytotoxic activity) is beneficial, and possibly a critical activity required to effectively eradicate coronavirus. We also concluded that an adaptive immune response including early cell-mediated immunity was significant in lowering disease severity. The link between the primary innate NK cell activity and the transcriptional priming of adaptive Th1 and Th2 cell responses appears to be more robust in mild patients than in severe.”

(9) In line 120, can the authors clarify which regulatory checkpoints were being referred to?

The concept of “checkpoint” was changed to “bridges” (line 124), because offers a clearer idea about the molecular interaction displayed across the different enriched pathways described in our study. In this sense, the bridges show the connection between innate immune response by NK cell and the adaptive immune response by Th1/Th2 cells

(10) In lines 125-126, can the authors refer to specific results to support this observation?

Lines 111 to 129 summarize the results of the analysis that support the aforementioned phrase. However, the original sentence referred was modified for better comprehension on page 6, lines 129-131 as follows:

Original:

“This balance between humoral- and cell-mediated immunity appeared to be less robust in patients presenting with severe COVID-19”

Changed to:

“The link between the primary innate NK cell activity and the transcriptional priming of adaptive Th1 and Th2 cell responses appears to be more robust in mild patients than in severe.”

(11) In lines 184-185, can the authors clarify what the term "mixed" specifically refers to?

The original text was modified for better comprehension on page 8, lines 177-179 as follows:

Original:

“Interestingly, on day-28, when the majority of patients had recovered, samples from severely ill patients were still mixed compared to those with mild symptoms.”

Changed to:

“Interestingly, on day-28, when the majority of patients had recovered, samples from severely ill patients were pooled together with those mild patients who had already recovered”.

(12) In line 286, can the authors clarify how quantitative expression level differences are distinct from temporal expression level differences?

Despite the differences in the enrollment time between mild and severe cohorts, it was made precisely during COVID-19 symptoms peaks, as illustrated in figure 1B. Also supporting this criterion, the longitudinal analysis outlined in figure 3 was performed taking into account the changes in gene expression trajectories along all sampling times. This point has significance because the results obtained from it exposed several transcriptional programs that were dynamically executed along disease progression, even independently of the pairwise comparison approaches carried out previously.

(13) In Figure 1C, there seemed to be two data points associated with "M1 0 days" and "M4 28 days" with distinct PC projections. Could these samples be mislabeled?

The figure was revised and completed. The hexagon symbol for day-28 was changed for a star symbol. The “M1 0 days” and “M4 28 days” samples were labeled correctly.  See below figure 1C with changes as follows:  

(14) In Figure 1D caption: could authors clarify if the ranking of 100 genes was based on the log2FC or adjusted p-values?

The criteria considered was Fold Change ≥ 2 and the FDR ≤ 0.05 which is included in the methodology on page 23, lines 657-660

(15) In Figure 4D, can the authors include the expression z score for the healthy participants?

We could include this information, but we consider that it would not help for the understanding of this figure because in this way we put the focus on the differential trajectories between mild and severe patients. Also, DEGs from mild and severe cohorts from this analysis or any other in this work were obtained relatively to healthy donors.

(16) Related to this, can the authors clarify if the expression z scores were computed using the mean and standard deviations of all samples within the study or relative to a specific participant cohort?

The z-score was used considering the mild and severe patients to calculate mean and then the standard deviation of each group. A new paragraph was included in material and methods on page 24, lines 662-664.

(17) In Figure 5B, can the authors include column annotations for participants and sampling time points?

The figure 5B was updated and completed with the suggested information.

(18) In Figure 1 - Figure Supplement 2, can the authors include the volcano plot from the pairwise comparison for day 28 showing no differentially expressed genes between mild and severe participants as reported in the results (lines 226-228)?

The third volcano plot for day 28 was included in the updated figure 1 supplement 2.

Reviewer #2 (Recommendations For The Authors):

The manuscript is generally very well-constructed and well-written. However, the following are the major concerns mostly regarding the study design and participant selection.

(1) The authors have used enrolment day as D0 which is not reflective of the immune response timeline. Especially when the designated 'D0' for the severe group is 10.0 + 1.8 days post symptom (DPS) onset while the 'D0' for the mild group is 1.2 + 1.3 DPS. In the context of an acute infection discussed herewith, this difference is critical.

As tempting as it is to conduct longitudinal studies on COVID-19, the authors might do better focusing on specific acute time points (within 10 days post-symptom onset) and convalescent time points (beyond 28 days post-symptom). A better comparison would be D0 severe with D7 mild (aligning the DPS to be between 7-10 days in both groups).

Despite the differences in the enrolment time between mild and severe cohorts, it was made precisely during COVID-19 symptoms peaks, as illustrated in figure 1B. Also supporting this criterion, the longitudinal analysis outlined in figure 3 was performed taking into account the changes in gene expression trajectories along all sampling times. This point has significance because the results obtained from it exposed several transcriptional programs that were dynamically executed along disease progression, even independently of the pairwise comparison approaches carried out previously. Likewise, we agree with the observation of the reviewer, because as we mentioned in the article, it is difficult to properly compare disease progression between naturally infected patients. So, to better support our findings, we complemented them throughout a pairwise comparison between day-7 samples from mild and day-0 samples from severely ill individuals, finding GO terms and enriched pathways related to NK cell function across the mild cohort, as seen in Figure 4-figure supplement 5. This result enforced the main findings gained from the different analyses carried out in this work, highlighting the relevance of the innate immune response of Natural Killer cells, which correlated with a mild progression of disease. The new paragraph describing this analysis was included in pages 13-14, lines 346-355. We also included a paragraph in the discussion on page 22, lines 595-604.

(2) Though there are four participants within each group, one of the participants with severe infection (S1) only has the D0 time point which probably undermines the statistical significance of the results.

This is an accurate observation, as the statistical weight will allow the deeper alterations to be evaluated while the more subtle ones will most likely be excluded from this study. In our analyses, we focused on variations with high statistical significance, which led to the discovery of a distinct Natural Killer response between mild and severe cohorts.

(3) The authors should also account for any medications administered to the severe group in the ICU before enrolment in the study -immune-dampening drugs or steroids which may alter neutrophil recruitment or other immune functions.

Only one severe patient received medication both prior to and during the COVID-19 disease. Even though several medications were administered to this patient, their effects have not been found to increase the neutrophil response.

(4) What was the viral load status at the different time points analyzed - how does this relate to the immune and clinical findings?

In this recruitment the viral load status was not measured.

(5) Was any complete blood count or basic immune phenotyping conducted on these samples? Important to know the various cell frequencies in the PBMC mix sent for sequencing to account for contamination of lymphocytes with RBCs/monocytes/neutrophils as well as any lymphopenia.

This measurement was not done for these samples. However, our protocol of PBMC purification has been tested before and showed small quantities of red blood cell contamination in the process. Furthermore, in all analysis of Gene Ontology or Enriched Pathways, there is not any related to red blood cell genes that could generate noise in the interpretation of our results.

(6) The neutrophil/lymphocyte ratio is already skewed during SARS-CoV-2 infection - which could be the reason for higher readings in severe participants? - speculate?

Effectively, the ratio in several cell types is changed during SARS-CoV-2 infection. However, despite this noise in the proportion of immune cells, different functions in our study are more represented in cells with less count as Natural Killer cells. The modules of co-expression analysis support the notion that despite the number of cells being in different proportions, a transcriptional program is being executed differentially in the cohorts.

(7) CD247/ZAP70 also influences the CD16-mediated NK cell ADCC activity which the authors can add to the innate-adaptive bridging section.

NK CD16a is more highly expressed in NK cells. The circuit involving CD247/ZAP70 and CD16 could explain the cytotoxicity of these cells and how they contribute to the establishment of a response to fight the viral infection of SARS-CoV-2. In our study, CD16a (FcgammaRIIIa) expression was similar in both mild and severe cohorts. Because our methodology only counts transcriptional changes, genes that did not change were excluded from our discussion. However, our group's research focuses on this node or bridge between innate and adaptive immune responses, with a particular emphasis on fc-antibodies functions, being a topic of interest for future research.

(8) Some of the figures lacked clarity making it difficult to review. (Eg. Fig 4 A, Fig 4 - supplement 1 A&B, Fig 5).

Figure 4A was redesigned, Figure 4-figure supplement 1 was presented in a full page for better resolution.

Specific Comments:

(1) Consider changing "covid-19" in the title of the manuscript to "COVID-19"

Probably the journal platform changes the letters. The original title is in capital letters according to the observation. In the clinical table “COVID-19” was changed to capital letters.

(2) Page 2: Line 24 - Consider revising this line. Not sure what the authors mean by 'early compromise'

The paragraph was revised and rewritten.

Original:

“Mild COVID-19 patients presented an early compromise with NK cell function, whereas severe patients do so with neutrophil function”

Changed to:

”Mild COVID-19 patients displayed an early transcriptional commitment with NK cell function, whereas severe patients do so with neutrophil function”

(3) Page 4: Lines 57 & 58 - Verify the reference. The paper referenced was published in 2016 and is in regard to SARS-CoV, MERS-CoV, and enterovirus D68.

Effectively, this reference was appropriate for drawing parallels with other respiratory viruses. Due to the emphasis on SARS-CoV-2, the paragraph has been strengthened with two additional references: Shen 2023, and Wauters 2022.

(4) Page 10: Lines 229 - 234 - Consider referring to the appropriate figure (i.e., Figure Supplement 2 A or B). The figure associated with D28 DEGs (Volcano plot) is missing in the supplementary. Erroneously referred here as Figure 1C which is a PCA plot?

The original text was changed because the figure referenced was correct but misunderstood. The final sentence is on page 9, lines 220-223.

(5) Page 10: Line 224 - Change the sentence to " We found upregulated.." instead of " We found regulated..".

The text was edited in accordance with this recommendation, which is currently found in line 232.

(6) Page 13: Line 326 - Figure 4A referenced here is not clear - unable to review.

Figure 4A was updated for a better resolution and included in the manuscript.

(7) Page 15: Line 398 - Consider rewording "after diagnosis" since the days here are "after enrolment".

This recommendation was considered and the text was rewritten on page 15, lines 404-406:

Original:

“We systematically analyzed transcriptomic features of PBMCs from COVID-19 patients with mild and severe symptoms at three sequential time-points (D0, D7, and D28) after diagnosis”

Changed to:

“We systematically analyzed transcriptomic features of PBMCs from COVID-19 patients with mild and severe symptoms at three sequential time-points (D0, D7, and D28) during the peak of the symptoms”

(8) Page 17: Move text from the next page to eliminate blank space.

Resolved

(9) Page 32: Figure 1C - Consider changing the symbol for D28 since it looks very similar to the D0 symbol. Use the colors consistently instead of different shades for each group.

The hexagon symbol was changed by a star symbol for D28 in figure 1C.  In this figure each color indicates the three different groups, and the transparent color was used to differentiate the symbols when are close together.

(10) Page 36: Figure 4A - Unable to review.

This figure was resized for better resolution.

(11) Page 42-49: Consider relabeling and renumbering the Supplementary figures for consistency and reference the modified numbers in the appropriate location in the main text.

The supplementary figures were relabeling for consistency and better understanding.

(12) Pages 44 & 48: Unable to review the figures.

The figures indicated were resized for better resolution.

Examples of consistency review:

(1) Use of D0,D7 / D-0, D-7 throughout the manuscript

The selected format for the final version of the manuscript is D0, D7, and D28.

(2) Reporting the source of reagents consistently (Name, Place, Country, Catalog number)

The source reagents were reformatted for consistency in lines 626-628-632-642.

Author response:

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

Editors’ recommendations for the authors

The reviewers recommend the following: 

(a) Digging deeper into the discussion of the density-dependent dispersal. 

(b) Clarifying the microfluidic setup.  

(c) Clarifying the description and interpretation of the transcriptomic evidence. 

(d) Toning down carbon cycle connections (some reviewers felt the evidence did not fully support the claims). 

We would like to thank the editors for their thoughtful evaluation of our manuscript and their clear suggestions. We have revised the manuscript in the light of these comments, as we outline below and address in detail in the point-by-point response to the reviewers’ comments that follows. 

(a) We have expanded the discussion of density-dependent dispersal and revised Figure 2C to improve clarity. 

(b) We have also added further information concerning the microfluidic setup in the results section and provide an illustration of the setup in a new figure panel, Figure 1A.

(c) Addressing the reviewers’ comments on the transcriptomic analysis, we have added more information in the description and interpretation of the results. 

(d) We have rephrased the text describing the role of degradation-dispersal cycles for carbon cycling to highlight it as the motivation of this study and emphasize the link to literature on foraging, without creating expectations of direct measurements of global carbon cycling.

Public Reviews:

Reviewer #1 (Public Review):

Summary: 

The authors attempt to understand how cells forage for spatially heterogeneous complex polysaccharides. They aimed to quantify the foraging behavior and interrogate its genetic basis. The results show that cells aggregate near complex polysaccharides, and disperse when simpler byproducts are added. Dispersing cells tend to move towards the polysaccharide. The authors also use transcriptomics to attempt to understand which genes support each of these behaviors - with motility and transporter-related genes being highly expressed during dispersal, as expected. 

Strengths: 

The paper is well written and builds on previous studies by some of the authors showing similar behavior by a different species of bacteria (Caulobacter) on another polysaccharide (xylan). The conceptual model presented at the end encapsulates the findings and provides an interesting hypothesis. I also find the observation of chemotaxis towards the polysaccharide in the experimental conditions interesting. 

Weaknesses: 

Much of the genetic analysis, as it stands, is quite speculative and descriptive. I found myself confused about many of the genes (e.g., quorum sensing) that pop up enriched during dispersal quite in contrast to my expectations. While the authors do mention some of this in the text as worth following up on, I think the analysis as it stands adds little insight into the behaviors studied. However, I acknowledge that it might have the potential to generate hypotheses and thus aid future studies. Further, I found the connections to the carbon cycle and marine environments in the abstract weak --- the microfluidics setup by the authors is nice, but it provides limited insight into naturalistic environments where the spatial distribution and dimensionality of resources are expected to be qualitatively different. 

We thank the reviewer for their suggestions to improve our manuscript. We agree that the original manuscript would have benefitted from more detailed interpretation of the observed changes in gene expression. We have revised the manuscript to elaborate on the interpretation of the changes in expression of quorum sensing genes (see response to reviewer 1, comment 3), motility genes (see response to reviewer 1, comment 6), alginate lyase genes (see response to reviewer 1, comment 7 and reviewer 2, comment 2), and ribosomal and transporter genes (see response to reviewer 2, comment 2).

In general, we think that the gene expression study not only supports the phenotypic observations that we made in the microfluidic device, such as the increased swimming motility when exposed to digested alginate medium, but  also adds further insights. Our reasoning for studying the transcriptomes in well mixed-batch cultures was the inability to study gene expression dynamics to support the phenotypic observations about differential motility and chemotaxis in our microfluidics setup. The transcriptomic data clearly show that even in well-mixed environments, growth on digested alginate instead of alginate is sufficient to increase the expression of motility and chemotaxis genes. In addition, the finding that expression of alginate lyases and metabolic genes is increased during growth on digested alginate was revealed through the analysis of transcriptomes, something which would not have been possible in the microfluidic setup. We agree with the reviewer that our analyses implicate further, perhaps unexpected, mechanisms like quorum sensing in the cellular response to breakdown products, and that this represents an interesting avenue for further studies.

Finally, we  also agree with the reviewer that it would be good to be more explicit in the text that our microfluidic system cannot fully capture the complex dynamics of natural environments. Our approach does, however, allow the characterization of cellular behaviors at spatial and temporal scales that are relevant to the interactions of bacteria, and thus provides a better understanding of colonization and dispersal of marine bacteria in a manner that is not possible through in situ experiments. We have edited our manuscript to highlight this and modified our statements regarding carbon cycling towards emphasizing the role degradation-dispersal cycles in remineralization of polysaccharides (see response to reviewer 1, comment 2).  

Reviewer #2 (Public Review):

Summary: 

The paper sets out to understand the mechanisms underlying the colonization and degradation of marine particles using a natural Vibrio isolate as a model. The data are measurements of motility and gene expression using microfluidic devices and RNA sequencing. The results reveal that degradation products of alginate do stimulate motility but not chemotaxis. The evidence for these claims is strong. The story of how particle degradation occurs through colonization and dispersal has modest support in the data. A quantitative description of these dynamics awaits future studies. 

Strengths: 

The microfluidic and transcriptional measurements are the central strengths of the paper as they allow the delineation of phenotypes at the cellular and molecular levels in the presence of polymer and byproducts of polymer degradation. 

Weaknesses: 

The explanation of the microfluidics measurements is somewhat confusing but I think this could be easily remedied. The quantitative interpretation of the dispersal data could also be improved and I'm not clear if the data support the claim made. 

We thank the reviewer for their comments and helpful suggestions. We have revised the manuscript with these suggestions in mind and believe that the manuscript is improved by a more detailed explanation of the microfluidic setup. We have added more information in the text (detailed in response to reviewer 2, comments 1 and 2) and have added a depiction of the microfluidic setup (Fig. 1A). We have also modified the presentation and discussion of the dispersal data (Fig. 2C), as described in detail below in response to reviewer 2, comment 4, and argue that they clearly show density-dependent dispersal. We believe that this modification of how the results are presented provides a more convincing case for our main conclusion, namely that the presence of degradation products controls bacterial dispersal in a density-dependent manner.  

Reviewer #3 (Public Review):

Summary: 

In this manuscript, Stubbusch and coauthors examine the foraging behavior of a marine species consuming an abundant marine polysaccharide. Laboratory experiments in a microfluidic setup are complemented with transcriptomic analyses aiming at assessing the genetic bases of the observed behavior. Bacterial cells consuming the polysaccharide form cohesive aggregates, while they start dispersing away when the byproduct of the digestion of the polysaccharide starts accumulating. Dispersing cells tend to be attracted by the polysaccharide. Expression data show that motility genes are enriched during the dispersal phase, as expected. Counterintuitively, in the same phase, genes for transporters and digestion of polysaccharides are also highly expressed. 

Strengths: 

The manuscript is very well written and easy to follow. The topic is interesting and timely. The genetic analyses provide a new, albeit complex, angle to the study of foraging behaviors in bacteria, adding to previous studies conducted on other species. 

Weaknesses: 

I find this paper very descriptive and speculative. The results of the genetic analyses are quite counterintuitive; therefore, I understand the difficulty of connecting them to the observations coming from experiments in the microfluidic device. However, they could be better placed in the literature of foraging - dispersal cycles, beyond bacteria. In addition, the interpretation of the results is sometimes confusing. 

We thank the reviewer for their suggestions to improve the manuscript. We have edited the manuscript to interpret the results of this study more clearly, in particular with regard to the fact that breakdown products of alginate cause cell dispersal (see response to reviewer 2, comment 1), gene expression changes of ribosomal proteins and transporters (see response to reviewer 2, comment 2), as well as genes relating to alginate catabolism (see response to reviewer 2, comment 3).

To provide more context for the interpretation of our results we now also embed our findings in more detail in the previous work on foraging strategies and dispersal tradeoffs.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

(1) The authors should clarify in more detail what they mean by density dependence in Figure 2. Usually density dependence refers to a per capita dependence, but here it seems that the per capita rate of dispersal might be roughly independent of density (Figure 2c; if you double the number of cells it doubles the number of cells leaving). Rather it seems the dispersal is such that the density of remaining cells falls below a threshold (~300 cells). 

We thank the reviewer for raising this important point. To analyze the data more explicitly in terms of per capita dependence and so make the density dependence in the dispersal from the microfluidic chambers more clear, we have modified Figure 2C and edited the text. 

In the modified Figure 2C, we computed the fraction of dispersed cells for each chamber (i.e the change in cell number divided by the cell number at the time of the nutrient switch). This quantity directly reveals the per-capita dependence, as mentioned by reviewer 1, and is now represented on the y-axis of Figure 2C instead of the absolute change in cell number. 

These data demonstrate that the fraction of dispersed cells increases with increasing numbers of cells present in the chamber at the time of switching, with more highly populated chambers showing a higher fraction of dispersed cells. These findings indicate that there is a strong density dependence in the dispersal process.

As pointed out by reviewer 1, another interesting aspect of the data is the transition at low cell number. The fraction of dispersed cells is negative in the case of the chamber with approximately 70 cells, consistent with no dispersal at this low density, and a moderate density increase as a function of continued growth.  

In addition to the new analysis presented in Figure 2C, we have modified the paragraph that discusses this result as follows (line 208):

“We indeed found that the nutrient switch caused a few or no cells to disperse from small cell groups (Fig. 2B), whereas a large fraction of cells from large cell groups dispersed (Fig. 2C). In fact, the e fraction of cells that dispersed upon imposition of the nutrient switch showed a strong positive relationship with the number of cells present, meaning that cells in chambers with many cells were more likely to disperse than cells in chambers with fewer cells (Fig. 2C).”

(2) The authors should tone down their claims about the carbon cycle in the abstract. I do not believe the results as they stand could be used to understand degradation-dispersal cycles in marine environments relevant to the carbon cycle, since these behaviors have been studied in microfluidic environments which in my understanding are quite different. As such, statements such as "degradation-dispersal cycles are an integral part in the global carbon cycle, we know little about how cells alternate between degradation and motility" and "Overall, our findings reveal the cellular mechanisms underlying bacterial degradation-dispersal cycles that drive remineralization in natural environments" are overstated in the abstract. 

We appreciate the reviewer’s comments regarding the connections of our work with the carbon cycle. We have now rephrased these statements in our manuscript to describe a potential connection between our work and the marine carbon cycle. The colonization of polysaccharides particles by bacteria and subsequent degradation has been widely acknowledged to play a significant role in controlling the carbon flow in marine ecosystems. (Fenchel, 2002; Preheim et al., 2011; Yawata et al., 2014, 2020). We still refer to carbon flow in the revised manuscript, though cautiously, as microbial remineralization of biomass, which is recognized as an important factor in the marine biological carbon pump (e.g., (Chisholm, 2000; Jiao et al., 2024). As stated in the previous version of the manuscript, the main motivation of our work was to study the growth behaviors of marine heterotrophic bacteria during polysaccharide degradation, especially to understand when bacteria depart already colonized and degraded particles and find novel patches to grow and degrade, a process that is poorly understood. Therefore, it is conceivable that degradation-dispersal cycles do play a role in the flow of carbon in marine ecosystems. However, we acknowledge that the carbon cycle is influenced by a multitude of biological and chemical processes, and the bacterial degradation-dispersal cycle might not be the sole mechanism at play. 

We also appreciate the reviewer’s comments highlighting that the complexity of natural environments is not fully captured in our microfluidics system. However, our microfluidics setup does allow us to quantify responses and behaviors of microbial groups at high spatial and temporal resolution, especially in the context of environmental fluctuations. Microbes in nature interact at small spatial scales and have to respond to changes in the environment, and the microfluidics setup enables the quantification of these responses. Moreover, dispersal of the bacterium V. cyclitrophicus that we use in our study, has been previously observed even during growth on particulate alginate (Alcolombri et al., 2021), but the cues and regulation controlling dispersal behaviors have been unclear.  Microfluidic experiments have now allowed us to study this process in a highly quantitative manner, and align well with observations from experiments from more nature-like settings. These quantitative experiments on bacterial strains isolated from marine particles are expected to constrain quantitative models of carbon degradation in the ocean (Nguyen et al., 2022).

We have now adjusted our statements throughout our manuscript to reflect the knowledge gaps in understanding the triggers of degradation-dispersal cycles and their links with carbon flow in marine ecosystems. The revised manuscript, especially, contains the following statements (line 47 and line 60):

“Even though many studies indicate that these degradation-dispersal cycles contribute to the carbon flow in marine systems, we know little about how cells alternate between polysaccharide degradation and motility, and which environmental factors trigger this behavioral switch.”

“Overall, our findings reveal cellular mechanisms that might also underlie bacterial degradation-dispersal cycles, which influence the remineralization of biomass in marine environments.”

(3) The authors should clarify why they think quorum-sensing genes are increased in expression on digested alginate. The authors currently mention that QS could be used to trigger dispersal, but given the timescales of dispersal in Figure 2 (~half an hour), I find it hard to believe that these genes are expressed and have the suggested effect on those timescales. As such I would have expected the other way round - for QS genes to be expressed highly during alginate growth, so that density could be sensed and responded to. Please clarify. 

We have now clarified this point in the revised manuscript. While the triggering of dispersal by quorum-sensing genes may indeed appear counterintuitive, and the response is rapid (we see dispersal of cells within 30-40 minutes), both observations are in line with previous studies in another model organism Vibrio cholerae. The dispersal time is similar to the dispersal time of V. cholerae cells from biofilms, as described by Singh and colleagues, (Figure 1E of Ref. Singh et al., 2017). In that case, induction of the quorum sensing dispersal regulator HapR was observed during biofilm dispersal within one hour after switch of condition (Fig. 2, middle panel of Ref. Singh et al., 2017). Even though the specific quorum sensing signaling molecules are probably different in our strain (there is no annotated homolog of the hapR gene in V. cyclitrophicus), we observed that the full set of quorum sensing genes was enriched in cells growing on digested alginate (as reported in line 314 and Fig. 4A).

We have added this information in the manuscript (line 317): 

“The set of quorum sensing genes was also positively enriched in cells growing on digested alginate (Fig. 4A and S4F, Table S13). This role in dispersal is in agreement with a previous study that showed induction of the quorum sensing master regulator in V. cholerae cells during dispersal from biofilms on a similar time scale as here (less than an hour)28.”

Reviewer #2 (Recommendations For The Authors):

(1) Around line 144 - I don't really understand how you flow alginate through the microfluidic platform. It seems if the particles are transiently going through the microfluidic chamber then the flow rate and hence residence time of the alginate particles will matter a lot by controlling the time the cells have to colonize and excrete enzymes for alginate breakdown. Or perhaps the alginate is not particulate but is instead a large but soluble polymer? I think maybe a schematic of the microfluidic device would help -- there is an implicit assumption that we are familiar with the Dal Co et al device, but I don't recall its details and maybe a graphic added to Figure 1 would help. 

a. In reviewing the Dal Co paper I see that cells are trapped and the medium flows through channels and the plane where the cells are held. I am still a little confused about the size of the polymeric alginate -- large scale (>1um) particles or very small polymers? 

We have now provided a detailed description of our microfluidic experimental system. At the start of the experiments, cells are in fact not trapped within the microfluidic device, but grow and can move freely within a chamber designed with dimensions (sub-micron heights) so that growth occurs only as a monolayer. Cells were exposed to nutrients, either alginate or alginate digestion products, both in soluble form (not particles). These compounds were flowed into the device through a main channel, but entered the flowfree growth chambers by diffusion. To make these aspects of our experiments clearer, we have added further information on this in the Materials & Methods section (line 556), added this information in the abstract (line 51), and in the results (line123).

To make our microfluidic setup clearer, we have followed this advice and added a schematic as Figure 1A and have added more information on the setup to the main text (line 153):

“In brief, the microfluidic chips are made of an inert polymer (polydimethylsiloxane) bound to a glass coverslip. The PDMS layer contains flow channels through which the culture medium is pumped continuously. Each channel is connected to several growth chambers that are laterally positioned. The dimensions of these growth chambers (height: 0.85 µm, length: 60 µm, width: 90-120 µm) allow cells to freely move and grow as monolayers. The culture medium, containing either alginate or digested alginate in their soluble form, is constantly pumped through the flow channel and enters the growth chambers primarily through diffusion15,16,4,17,8. Therefore, the number of cells and their positioning within microfluidic chambers is determined by the cellular growth rate as well as by cell movement4. This setup combined with time-lapse microscopy allowed us to follow the development of cell communities over time.”

(2) What makes this confusing is the difference between Figure 1C and Figure S2A -- the authors state that the difference in Figure 1C is due to dispersal, but is there flow through the microfluidic device? So what role does that flow through the device have in dispersal? Is the adhesion of the cell groups driven at all by a physical interaction with high molecular weight polymers in the microfluidic devices or is this purely a biological effect? Could this also be explained by different real concentrations of nutrients in the two cases? 

We realize from this comment that the role of flow of the medium in the microfluidic setup was not clearly addressed in our manuscript. In fact, cells were not exposed to flow, and nutrients were provided to the growth chambers by diffusion. We have added a clearer explanation of this point on line 158:

“The culture medium, containing either alginate or digested alginate in their soluble form, is constantly pumped through the flow channel and enters the growth chambers primarily through diffusion15,16,4,17,8. Therefore, the number of cells and their positioning within microfluidic chambers is determined by the cellular growth rate as well as by cell movement4.“

One purely physical effect that we anticipate is that a high viscosity of the medium could immobilize cells. To address this point, we measured the viscosity of both alginate and digested alginate and conclude that the increase in viscosity is not strong enough to immobilize cells. We added a statement in the text (line 170)

“To test the role of increased viscosity of polymeric alginate in causing the increased aggregation of cells, we measured the viscosity of 0.1% (w/v) alginate or digested alginate dissolved in TR media. For alginate, the viscosity was 1.03±0.01 mPa·s (mean and standard deviation of three technical replicates) whereas the viscosity of digested alginate in TR media was found to be 0.74±0.01 mPa·s. Both these values are relatively close to the viscosity of water at this temperature (0.89 mPa·s18) and, while they may affect swimming behavior19, they are insufficient to physically restrain cell movement20.”

as well as a section in the Materials and Methods (line 594):

“Viscosity of the alginate and digested alginate solution

We measured the viscosity of alginate solutions using shear rheology measurements. We use a 40 mm cone-plate geometry (4° cone) in a Netzsch Kinexus Pro+ rheometer. 1200 uL of sample was placed on the bottom plate, the gap was set at 150 um and the sample trimmed. We used a solvent trap to avoid sample evaporation during measurement. The temperature was set to 25°C using a Peltier element. We measure the dynamic viscosity over a range of shear rates  = 0.1 – 100 s-1. We report the viscosity of each solution as the average viscosity measured over the shear rates 10 – 100 s-1, where the shear-dependence of the viscosity was low.

We measured the viscosity of 0.1% (w/V) alginate dissolved in TR media, which was 1.03 +/- 0.01 mPa·s (reporting the mean and standard deviation of three technical replicates.). The viscosity of 0.1% digested alginate in TR media was found to be 0.74+/-0.01 mPa·s. This means that the viscosity of alginate in our microfluidic experiments is 36% higher than of digested alginate, but the viscosities are close to those expected of water (0.89 mPa·s at 25 degree Celsius according to Berstad and colleagues18).”

While our microfluidic setup allows us to track the position and movement of cells in a spatially structured setting, these observations do not allow us to distinguish directly whether the differences in dispersal are a result of purely physical effects of polymers on cells or are a result of them triggering a biological response in cells that causes them to become sessile. It is known that bacterial appendages like pili interact with polysaccharide residues (Li et al., 2003). Therefore, it is quite plausible that cross-linking by polysaccharides can contribute growth behaviors on alginate. However, our analysis of gene expression demonstrates that flagellum-driven motility is decreased in the presence of alginate compared to digested alginate, alongside other major changes in gene expression. In addition, our measures of dispersal show that dispersal of cells when exposed to digested alginate is density dependent. Both observations suggest that the patterns in dispersal are governed by decision-making processes by cells resulting in changes in cell motility, rather than being a product of purely physical interactions with the polymer. 

The finding that viscosities of both alginate and digested alginate are similar to that of water, suggests that diffusion of nutrients in the growth chambers should be similar. Therefore, we think that the differences in real concentrations of nutrients is likely not contributing to the observed differences in behavior. 

(3) Why is Figure S1 arbitrary units? Does this have to do with the calibration of LC-MS? It would be better, it seems, to know the concentrations in real units of the monomer at least. 

We agree with the reviewer that it would have been better to have absolute concentrations for these compounds. However, to calibrate the mass spectrometer signals (ion counts) to absolute concentrations for the different alginate compounds, we would need an analytical standard of known concentration. We are not aware of such a standard and thus report only relative concentrations. We agree that the y-axis label of Figure S1 should not contain ‘arbitrary’ units, as it shows a ratio (of measurements in the same arbitrary units). We have edited the labels of Figure S1 accordingly and the figure legend in line 26 of the Supplemental Material (“Relative concentrations…”).

(4) Line 188 - density-dependent dispersal. The claim here is that "cells in chambers with many cells were more likely to disperse than cells in chambers with less cells." (my emphasis). Looking at the data in Figure 2C it appears that about 40% of the cells disperse irrespective of the density, before the switch to digested alginate. So it would seem that there is not a higher likelihood of dispersal at higher cell densities. For the very highest cell density, it does appear that this fraction is larger, but I'd be concerned about making this claim from what I understand to be a single experiment. To support the claim made should the authors plot Change in Cell number/Starting Cell number on the y-axis of Fig. 2C to show that the fraction is increasing? It would seem some additional data at higher starting cell densities would help support this claim more strongly. 

We thank the reviewer for this comment, which is in line with a remark made by reviewer 1 in their comment 1. In response to these two comments (and as described above), we have edited Figure 2C and now have plotted the change in cell number relative to starting cell number at the y axis to directly show the density dependence. We observe a positive (approximately linear) relationship between the fraction of dispersed cells with the number of cells present in the chamber at the time of switching. This indicates that there is a density dependence in the dispersal process, with highly populated chambers showing a higher fraction of dispersed cells. 

In addition to the change in Figure 2C, we have modified the paragraph around line 208: “We indeed found that the nutrient switch caused a few or no cells to disperse from small cell groups (Fig. 2B), whereas a large fraction of cells from large cell groups dispersed (Fig. 2C). In fact, the e fraction of cells that dispersed upon imposition of the nutrient switch showed a strong positive relationship with the number of cells present, meaning that cells in chambers with many cells were more likely to disperse than cells in chambers with fewer cells (Fig. 2C).”

The highest cell number at the start of the switch that we include is about 800 cells. The maximum number of cells that can fit into a chamber are ca. 1000 cells. Thus, 800 resident cells are close to the maximal density.

(5) A comment -- I find the result of significant chemotaxis towards alginate but not the monomers of alginate to be quite surprising. The ecological relevance of this (line 219) seems like an important result that is worth expanding on a bit at least in the discussion. For now, my question is whether the authors know of any mechanism by which chemotaxis receptors could respond to alginate but not the monomer. How can a receptor distinguish between the two? 

We agree that this result is surprising, given that oligomers can be more easily transported into the periplasm where sensing takes place, and they also provide an easier accessible nutrient source. Indeed, in case of the insoluble polymer chitin it has been shown that chemotaxis towards chitin is mediated by chitin oligomers (Bassler et al., 1991), which was suggested as a general motif to locate polysaccharide nutrient sources (Keegstra et al., 2022). However, a recent study has changed this perspective by showing widespread chemotaxis of marine bacteria towards the glucose-based marine polysaccharide laminarin, but not towards laminarin oligomers or glucose (Clerc et al., 2023). Together with our results on chemotaxis towards alginate (but not significantly toward alginate oligomers) this suggests that chemotaxis towards soluble polysaccharides can be mediated by direct sensing of the polysaccharide molecules.

As recommended, we expanded the discussion of the ecological relevance and also added more information on possible mechanisms of selective sensing of alginate and its breakdown products (around line 479).:

“Direct chemotaxis towards polysaccharides may facilitate the search for new polysaccharide sources after dispersal. We found that the presence of degradation products not only induces cell dispersal but also increases the expression of chemotaxis genes. Interestingly, we found that V. cyclitrophicus ZF270 cells show chemotaxis towards polymeric alginate but not digested alginate. This contrasts with previous findings for bacterial strains degrading the insoluble marine polysaccharide chitin, where chemotaxis was strongest towards chitin oligomers53, suggesting that oligomers may act as an environmental cue for polysaccharide nutrient sources55. However, recent work has shown that certain marine bacteria are attracted to the marine polysaccharide laminarin, and not laminarin oligomers56. Together with our results, this indicates that chemotaxis towards soluble polysaccharides may be mediated by the polysaccharide molecules themselves. The mechanism of this behavior is yet to be identified, but could be mediated by polysaccharide-binding proteins as have been found in Sphingomonas sp. A1 facilitating chemotaxis towards pectin57. Direct polysaccharide sensing adds complexity to chemosensing as polysaccharides cannot freely diffuse into the periplasm, which can lead to a trade-off between chemosensing and uptake58. Furthermore, most polysaccharides are not immediately metabolically accessible as they require degradation. But direct polysaccharide sensing can also provide certain benefits compared to using oligomers as sensory cues. First, it could enable bacterial strains to preferably navigate to polysaccharide nutrients sources that are relatively uncolonized and hence show little degradation activity. Second, strong chemotaxis towards degradation products could hinder a timely dispersal process as the dispersal then requires cells to travel against a strong attractant gradient formed by the degradation products. Overall, this strategy allows cells to alternate between degradation and dispersal to acquire carbon and energy in a heterogeneous world with nutrient hotspots44,59–61.”

(6) Comment on lines 287-8 -- that the "positive enrichment of the gene set containing bacterial motility proteins matched the increase in motile cells that we observe in Fig 3E." I'm confused about what is meant by the word "matched" here. Is the implication that there is some quantitative correspondence between increased motility in Figure 3 and the change in expression in Figure 4? Or is the statement a qualitative one -- that motility genes are upregulated in the presence of digested alginate? Table S12 didn't help me answer this question. 

We thank the reviewer for their helpful comment. Our original statement was a qualitative one - observing that gene expression enrichment in genes associated with bacterial motility aligned with our expectations based on the previous observation of an increase in motile cells. We have now changed the wording to highlight the qualitative nature of this statement (line 315):

“The positive enrichment of the gene set containing bacterial motility proteins aligned with our expectations based on the increase in motile cells that we observed in Figure 3E (Fig. 4A, Table S12).”

(7) Line 326 - what is the explanation for the production of public enzymes in the presence of digest? How does this square with the previous narrative about cells growing on alginate digest expressing motility genes and chemotaxing towards alginate? It seems like the story is a bit tenuous here in the sense that digested alginates stimulate both motility - which is hypothesized to drive the discovery of new alginate particles - and lyase enzymes which are used to degrade alginate. So do the high motility cells that are chemotaxing towards alginate also express lyases en route? I'm of the opinion that constructing narratives like these in the absence of a more quantitative understanding of the colonization and degradation dynamics of alginate particles presents a major challenge and may be asking more of the data than the data can provide. 

a. I noted later that this is addressed later around lines 393 in the Discussion section.

Indeed, the notion that the presence of breakdown products triggers motility and also increases the expression of alginate lyases and other metabolic genes for alginate catabolism seems counterintuitive. We have now expanded our discussion of these results to contextualize these findings (around line 443):

“One reason for this observation may be that cells primarily rely on intracellular monosaccharide levels to trigger the upregulation of genes associated with polysaccharide degradation and catabolism, as has previously been observed for E. coli across various carbon sources50,51. In fact, the majority of carbon sources are sensed by prokaryotes through one‑component sensors inside the cell50. In the one‑component internal sensing scheme, the enzymes and transporters for the use of various carbon sources are expressed at basal levels, which leads to an increase in pathway intermediates upon nutrient availability. The pathway intermediates are sensed by an internal sensor, usually a transcription factor, and lead to the upregulation of transporter and enzyme expression50,51. This results in a positive feedback loop, which enables small changes in substrate abundance to trigger large transcriptional responses50,52. Thus, the presence of alginate breakdown products may likely result in increased expression of all components of the alginate degradation pathway, including the expression of degrading enzymes. As the gene expression analysis was performed on well-mixed cultures in culture medium containing alginate breakdown products, we therefore expect a strong stimulation of alginate catabolism. In a natural scenario, where cells disperse from a polysaccharide hotspot before its exhaustion, the expression of alginate catabolism genes may likely decrease again once the local concentration of breakdown products decreases. However, continued production of alginate lyases could also provide an advantage when encountering a new alginate source and continued production of alginate lyases may thus help cells to prepare for likely future environments. Further investigations of bacterial enzyme secretion in changing nutrient environments and at relevant spatial scales are required to improve our understanding of the regulation of enzyme secretion along nutrient gradients.“

(8) I like Figure 6, and I think this hypothesis is a good result from this paper, but I think it would be important to emphasize this as a proposal that needs further quantitative analysis to be supported. 

We have now edited the manuscript to make this point more clear. While both degradation and dispersal are well-appreciated parts of microbial ecology, the transitions and underlying mechanisms are unclear. We have edited the discussion to improve the clarity (line 419): 

“This cycle of biomass degradation and dispersal has long been discussed in the context of foraging e.g., 44,45,13,46,47, but the cellular mechanisms that drive the cell dispersal remain unclear.”

Also, we have updated Figure 6 to indicate more clearly which new findings this work proposes (now bold font) and which previous findings that were made in different bacterial taxa and carbon sources that aligns with our  work (now light font). We edited the figure legend accordingly (line 503):

“By integrating our results with previous studies on cooperative growth on the same system, as well as results on dispersal cycles in other systems, we highlight where the specific results of this work add to this framework (bold font).”

Minor comments 

(1) Is there any growth on the enzyme used for alginate digestion? E.g. is the enzyme used to digest the alginate at sufficiently high concentrations that cells could utilize it for a carbon/nitrogen source? 

We thank the reviewer for raising this point. We added the following paragraph as Supplemental Text to address it (line 179):

“Protein amount of the alginate lyases added to create digested alginate

Based on the following calculation, we conclude that the amount of protein added to the growth medium by the addition of alginate lyases is so small that we consider it negligible. In our experiment we used 1 unit/ml of alginate lyases in a 4.5 ml solution to digest the alginate. As the commercially purchased alginate lyases are 10,000 units/g, our 4.5 ml solution contains 0.45 mg of alginate lyase protein. The digested alginate solution diluted 45x when added to culture medium. This means that we added 0.18 µg alginate lyase protein to 1 ml of culture medium.

As a comparison, for 1ml of alginate medium, 1000µg of alginate is added or for 1 ml of Lysogeny broth (LB) culture medium, 3,500 µg of LB are added.  Thus, the amount of alginate lyase protein that we added is ca. 5000 - 20,000 times smaller than the amount of alginate or LB that one would add to support cell growth. Therefore, we expect the growth that the digestion of the added alginate lyases would allow to be negligible.”

(2) The lines in Figure 2B are very hard to see. 

We have addressed this comment by using thicker lines in Figure 2B.

(3) The black background and images in Figure 3A and B are hard to see as well. 

We have now replaced Figure 3A and B, now using a white background.

(4) Typo at the beginning of line 251? 

Unfortunately we failed to find the typo referred to. We are happy to address it if it still exists in the revised manuscript.

Reviewer #3 (Recommendations For The Authors):

(1) I think there is not enough experimental evidence to conclude that the underlying cause of increased motility is the accumulation of digested alginate products. To conclusively show that this is the cause and not just some signal linked to cell density, perhaps the experiment should be repeated with a different carbon source. 

We thank the reviewer for their comment, which made us realize that we did not make the nature of the dispersal cue clear. The gene expression data was obtained from batch cultures and measured at the same approximate bacterial densities in batch, which indeed shows that the digested alginate is a sufficient signal for an increase in motility gene expression. This agrees very well with our observation that cells growing on digested alginate in microfluidic chambers have an increased fraction of motile cells in comparison with cells exposed to alginate (Fig 3E). However, we did not mean to suggest that the observed dispersal by bacterial motility is not influenced by cell density, in fact, we see that dispersal (and hence the increase in cell motility) in microfluidic chambers that are switched from polymeric to digested alginate depends on the bacterial density in the chamber, with higher bacterial densities showing increased dispersal. This shows that the presence of alginate oligomers does trigger dispersal through motility, but this signal affects bacterial groups in a cell density dependent manner.

Similar observations have been made in Caulobacter crescentus, which was found to form cell groups on the polymer xylan while cells disperse when the corresponding monomer xylose becomes available (D’Souza et al., 2021). We reference the additional work in lines 179 and 230. Taken together, these observations indicate a more general phenomenon in dispersal from polysaccharide substrates.

(2) About the expression data: 

• Ribosomal proteins and ABC transporters are enriched in cells grown on digested alginate and the authors discuss that this explains the difference in max growth rate between alginate and digested alginate. However, in Figure S2E the authors report no statistical difference between growth rates. 

We have now edited the manuscript to clarify this point. We found that cells grown on degradation products reached their maximal growth rate around 7.5 hours earlier (Fig. S2D) and showed increased expression of ribosomal biosynthesis and ABC transporters in late-exponential phase (Fig. 4A). We consider this shorter lag time as a sign of a different growth state and therefore a possible reason for the difference in ribosomal protein expression.

As the reviewer correctly points out, the maximum growth rates that were computed from the two growth curves were not significantly different (Fig. S2E). However, for our gene expression analysis, we harvested the transcriptome of cells that reached OD 0.39-0.41 (mid- to late-exponential phase). At this time point, the cell cultures may have differed in their momentary growth rate.

We edited the manuscript to make this clearer (line 287):

“Both observations likely relate to the different growth dynamics of V. cyclitrophicus ZF270 on digested alginate compared to alginate (Fig. S2A), where cells in digested alginate medium reached their maximal growth rate 7.5 hours earlier and thus showed a shorter lag time (Fig. S2D). As a consequence, the growth rate at the time of RNA extraction (mid-to-late exponential phase) may have differed, even though the maximum growth rate of cells grown in alginate medium and digested alginate medium were not found to be significantly different (Fig. S2E).”

• The increased expression of transporters for lyases in cells grown on digested alginate (lines 273-274 and 325-328) is very confusing and the explanation provided in lines 412420 is not very convincing. My two cents on this: Expression of more enzymes and induction of motility might be a strategy to be prepared for more likely future environments (after dispersal, alginate is the most likely carbon source they will find). This would be in line with observed increased chemotaxis towards the polymer rather than the monomer (Similar to C. elegans). 

This comment is in line with reviewer 2, comment 7. In response to these two comments (and as described above), we expanded our discussion of these results to contextualize these findings (around line 443):

“One reason for this observation may be that cells primarily rely on intracellular monosaccharide levels to trigger the upregulation of genes associated with polysaccharide degradation and catabolism, as has previously been observed for E. coli across various carbon sources50,51. In fact, the majority of carbon sources are sensed by prokaryotes through one‑component sensors inside the cell50. In the one‑component internal sensing scheme, the enzymes and transporters for the use of various carbon sources are expressed at basal levels, which leads to an increase in pathway intermediates upon nutrient availability. The pathway intermediates are sensed by an internal sensor, usually a transcription factor, and lead to the upregulation of transporter and enzyme expression50,51. This results in a positive feedback loop, which enables small changes in substrate abundance to trigger large transcriptional responses50,52. Thus, the presence of alginate breakdown products may likely result in increased expression of all components of the alginate degradation pathway, including the expression of degrading enzymes. As the gene expression analysis was performed on well-mixed cultures in culture medium containing alginate breakdown products, we therefore expect a strong stimulation of alginate catabolism. In a natural scenario, where cells disperse from a polysaccharide hotspot before its exhaustion, the expression of alginate catabolism genes may likely decrease again once the local concentration of breakdown products decreases. However, continued production of alginate lyases could also provide an advantage when encountering a new alginate source and continued production of alginate lyases may thus help cells to prepare for likely future environments. Further investigations of bacterial enzyme secretion in changing nutrient environments and at relevant spatial scales are required to improve our understanding of the regulation of enzyme secretion along nutrient gradients.”

Additionally, we agree with the intriguing comment that continued expression of alginate lyases may also prepare cells for likely future environments. Further studies that aim to answer whether marine bacteria are primed by their growth on one carbon source towards faster re-initiation of degradation on a new particle will be an interesting research question. We now address this point in our manuscript (line 458):

“However, continued production of alginate lyases could also provide an advantage when encountering a new alginate source and continued production of alginate lyases may thus help cells to prepare for likely future environments. Further investigations of bacterial enzyme secretion in changing nutrient environments and at relevant spatial scales are required to improve our understanding of the regulation of enzyme secretion along nutrient gradients.“

(3) The yield reached by Vibrio on alginate is significantly higher than the yield in digested alginate, not similar, as stated in lines 133-134. Only cell counts are similar. Perhaps the author can correct this statement and speculate on the reason leading to this discrepancy: perhaps cells tend to aggregate in alginate despite the fact that these are well-mixed cultures. 

We have edited the description of the OD measurements accordingly and agree with the reviewer that aggregation is indeed a possible reason for the discrepancy (line 141):

“We also observed that the optical density at stationary phase was higher when cells were grown on alginate (Fig. S2B and C). However, colony counts did not show a significant difference in cell numbers (Fig. S3), suggesting that the increased optical density may stem from aggregation of cells in the alginate medium, as observed for other Vibrio species7.”

(4) I suggest toning down the importance of the results presented in this study for understanding global carbon cycling. There is a link but at present it is too much emphasized. 

We have edited our statements regarding the carbon cycle. In the revised manuscript we stress the lack of direct quantifications of carbon cycling. . We still refer to carbon flow in the revised manuscript, as we would argue that microbial remineralization of biomass is recognized as an important factor in the marine biological carbon pump (e.g., Chisholm, 2000) and research on marine bacterial foraging investigates how bacterial cells manage to find and utilize this biomass.

Our revised manuscript contains the following modified statements (line 47 and line 60): “Even though many studies indicate that these degradation-dispersal cycles contribute to the carbon flow in marine systems, we know little about how cells alternate between polysaccharide degradation and motility, and which environmental factors trigger this behavioral switch.”

“Overall, our findings reveal cellular mechanisms that might also underlie bacterial degradation-dispersal cycles, which influence the remineralization of biomass in marine environments.”

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Author response:

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

Reviewer #1: The authors may consider moving the supplemental figures into the main body of the paper since they finally would end up with a total of eight figures.

As we added two more supplementary figures, we left them separated from the main part of the manuscript in the supplement. All of them describe important experimental details but we believe that it is easier to follow if there is a focus on the key results.

Reviewer #1: In general, the methods and techniques used here are beside some required but important additions described in sufficient detail.

Reviewer #2: Given the identified importance of glow-discharge treatment of precoated tape to the flat deposition of sections during ATUM, a corresponding schematic or appropriate reference(s) providing more information about the custom-built tape plasma device would likely be a prerequisite for effective reproduction of this technique in other laboratories.

Thank you for the valuable comments on the missing experimental details, which could affect the ease of establishing ATUM-Tomo in other labs. We will clearly highlight the ATUM-Tomo-specific vs. some general EM processing steps of the workflow in the proposed way. A detailed description of the custom-built tape plasma device will be added to the methods section. In addition, we will reference more explicitly our published protocols, which describe the standard electron microscopy embedding steps in great detail (Kislinger et al., STAR protocols, 2020; Kislinger et al., Meth Cell Biol, 2023).

Reviewer #1: Concerning the results section: In my opinion, the results section is a bit unbalanced. There is a mismatch between the detailed description of the methodology (experimental approach) and the scientific findings of the paper. The reviewer can see the enormous methodological impact of the paper, which on the other hand is the major drawback of the paper. To my opinion, the authors should also give a more detailed description of their scientific results.

Concerning the discussion: It would have been nice to give a perspective to which the described methodology can be used not only to describe diverse biological aspects that can be addressed and answered by this experimental approach. For example, how could this method be used to address various questions about the normal and pathologically altered brain?

In my opinion, the paper has one major drawback which is that it is more methodologically based although the authors included a scientific application of the method. The question here is to balance the methodology vs. the scientific achievement of this paper, a decision hard to take. In other words, one could recommend this paper to more methodologically based journals, for example, Nature Methods.

Balancing the technological and biological parts is indeed a difficult issue. We agree that this manuscript mainly describes a technical advancement and demonstrates its power to answer previously unsolved scientific questions. We exemplify this in our model system, neuropathology of the blood-brain barrier. The biological impact of ATUM-SEM has been described in detail in Khalin et al., Small, 2022, and is referenced accordingly. Here we describe how ATUM-Tomo can be applied to reveal biological insights exceeding the capabilities of ATUM-SEM and other volume electron microscopy techniques. However, the description of the methodological development outweighs by far the one of the biological details. We consider eLife‘s Tools and Resources (which, in our view, is in scope similar to Nat Methods) an ideal format for this technically focused manuscript while targeting eLife’s readership with diverse biological fields of interest for potential applications of the method. We suggested the application in connectomics (for chemical synapses), the study of endocytosis and the detection of virus particles in the discussion. Hopefully, this accommodates the Reviewer’s concern that having only a single application might seem arbitrary or even suggest a very narrow utility of the technique.

“While we demonstrate a neuropathology-related application, further biological targets that require high-resolution isotropic voxels and the spatial orientation within a larger ultrastructural context can potentially be studied by ATUM-Tomo. This includes the detection of gap junctions for connectomics or for the study of long-range projections (Holler et al., 2021) and the subcellular location of virus particles (Wu et al., 2022, Roingeard, 2008, Pelchen-Matthews and Marsh, 2007). Thus, ATUM-Tomo opens up new avenues for multimodal volume EM imaging of diverse biological research areas.”

Reviewer #2: Is the separation of sections from permanent marker-treated tape sensitive to the time interval between deposition/SEM imaging and acetone treatment?

Thank you for pointing out this important methodological aspect. We have not systematically investigated whether there is a critical time window between microtomy, SEM, and detachment. From the samples generated for this study, we assessed the importance of timing in retrospect:

“The sections could be recovered even four months after collection and nine months after SEM imaging.”

Reviewer #2: To what extent is slice detachment from permanent marker-treated tape resin-dependent [i.e. has ATUM-Tomo been tested on resin compositions beyond LX112 (LADD)]?

We appreciate this comment addressing the broader technical applicability of ATUM-Tomo. We tested the general workflow with tissue embedded in other commonly used resin types (epon, durcupan).

Reviewer #2: Minor corrections to the text and figures.

Line 83: ((Khalin et al., 2022) should read (Khalin et al., 2022)

Line 86 : 30nm should read 30 nm

Line 139: "...morphological normal tight junctions..." should read "...morphologically normal tight junctions..."

Line 283: "....despite glutaraldehyde fixation, a prerequisite for optimal ultrastructural preservation...".

Line 295: "In contrast, our CLEM approach provides high ultrastructural quality by optimal chemical fixation".

The concepts of optimal preservation and optimal fixation are arguably context- and application-dependent. These statements should be toned down or their context explicitly stated.

Thank you for the detailed corrections. We have applied them accordingly.

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this study, Faniyan and colleagues build on their recent finding that renal Glut2 knockout mice display normal fasting blood glucose levels despite massive glucosuria. Renal Glut2 knockout mice were found to exhibit increased endogenous glucose production along with decreased hepatic metabolites associated with glucose metabolism. Crh mRNA levels were higher in the hypothalamus while circulating ACTH and corticosterone was elevated in this model. While these mice were able to maintain normal fasting glucose levels, ablating afferent renal signals to the brain caused low fasting blood glucose levels. In addition, the higher CRH and higher corticosterone levels of the knockout mice were lost following this denervation. Finally, acute phase proteins were altered, plasma Gpx3 was lower, and major urinary protein MUP18 and its gene expression were higher in renal Glut2 knockout mice. Overall, the main conclusion that afferent signaling from the kidney is required for renal glut2 dependent increases in endogenous glucose production is well supported by these findings.

Strengths:

An important strength of the paper is the novelty of the identification of kidney to brain communication as being important for glucose homeostasis. Previous studies had focused on other functions of the kidney modulated by or modulating brain function. This work is likely to promote interest in CNS pathways that respond to afferent renal signals and the response of the HPA axis to glucosuria. Additional strengths of this paper stem from the use of incisive techniques. Specifically, the authors use isotope enabled measurement of endogenous glucose production by GC-MS/MS, capsaicin ablation of afferent renal nerves, and multifiber recording from the renal nerve. The authors also paid excellent attention to rigor in the design and performance of these studies. For example, they used appropriate surgical controls, confirmed denervation through renal pelvic CGRP measurement, and avoided the confounding effects of nerve regrowth over time. These factors strengthen confidence in their results. Finally, humans with glucose transporter mutations and those being treated with SGLT2 inhibitors show a compensatory increase in endogenous glucose production. Therefore, this study strengthens the case for using renal Glut2 knockout mice as a model for understanding the physiology of these patients.

Weaknesses:

A few weaknesses exist. Most concerns relate to the interpretation of this study's findings. The authors state that loss of glucose in urine is sensed as a biological threat based on the HPA axis activation seen in this mouse model. This interpretation is understandable but speculative. Importantly, whether stress hormones mediate the increase in endogenous glucose production in this model and in humans with altered glucose transporter function remains to be demonstrated conclusively. For example, the paper found several other circulating and local factors that could be causal. This model is also unable to shed light on how elevated stress hormones might interact with insulin resistance, which is known to increase endogenous glucose production. That issue is of substantial clinical relevance for patients with T2D and metabolic disease. Finally, how these findings can contribute to improving the efficiency of drugs like SGLT2 inhibitors remains to be seen.

-  We agree with the reviewer’s overall assessment of this manuscript.

- Confirming the contribution of each secreted protein shown in Fig. 4, whose levels were changed between the two groups of mice, toward causing a compensatory increase in glucose production in response to elevated glycosuria is beyond the scope of this manuscript.

Reviewer #2 (Public Review):

Summary:

The authors previously generated renal Glut2 knockout mice, which have high levels of glycosuria but normal fasting glucose. They use this as an opportunity to investigate how compensatory mechanisms are engaged in response to glycosuria. They show that renal and hepatic glucose production, but not metabolism, is elevated in renal Glut2 male mice. They show that renal Glut2 male mice have elevated Crh mRNA in the hypothalamus, and elevated plasma levels of ACTH and corticosterone. They also show that temporary denervation of renal nerves leads to a decrease in fasting and fed blood glucose levels in female renal Glut2 mice, but not control mice. Finally, they perform plasma proteomics in male mice to identify plasma proteins that are changed (up or down) between the knockouts and controls.

Strengths:

The question that is trying to be addressed is clinically important: enhancing glycosuria is a current treatment for diabetes, but is limited in efficacy because of compensatory increases in glucose production.

Weaknesses:

(1) Although I appreciate that the initial characterization of the mice in another publication showed that both males and females have glycosuria, this does not mean that both sexes have the same mechanisms giving rise to glycosuria. There are many examples of sex differences in HPA activation in response to threat, for example. There is an unfounded assumption here that males and females have the same underlying mechanisms of glycosuria that undermines the significance of the findings.

- We agree with the reviewer that although we didn’t observe sex differences in renal Glut2 KO mice in the context of glucose homeostasis, their response (or mechanisms) to elevated glycosuria in enhancing compensatory glucose production may be different between the sexes. Therefore, we have included this limitation in discussion section.

(2) The authors state that they induced the Glut2 knockout with taxomifen as in their previous publication. The methods of that publication indicate that all experiments were completed within 14 days of inducing the Glut2 knockout. This means that the last dose of tamoxifen was delivered 14 days prior to the experimental endpoint of each experiment. This seems like an important experimental constraint that should be discussed in this manuscript. Is the glycosuria that follows Glut2 knockout only a temporary change? If so, then the long-term change in glycosuria that follows SGLT2 inhibition in humans might not be best modelled by this knockout. Please specify when the surgeries to implant a jugular catheter or ablate the renal nerves performed relative to the Glut2 knockout in the Methods.

- The reviewer’s statement ‘The methods of that publication indicate that all experiments were completed within 14 days of inducing the Glut2 knockout’ is incorrect. In the referred publication, we had explicitly mentioned in methods, ‘All of the experiments, except those using a diet-induced obesity mouse model or noted otherwise, were completed within 14 days of inducing the Glut2 deficiency.’ Please see figures 5h-l and 6 in the cited publication, which demonstrate that all the experiments were not completed within 14 days of inducing renal Glut2 deficiency. Per the reviewer’s advice, in the present manuscript we have include the timeline (which in some cases is 4 months beyond inducing glycosuria) in all the figure legends. In addition, for a separate project (which is unpublished) we have measured glycosuria up to 1 year after inducing renal Glut2 deficiency. Therefore, the glycosuria observed in the renal Glut2 KO mice is not temporary.

(3) I am still unclear what group was used for controls. Are these wild-type mice who receive tamoxifen? Are they KspCadCreERT2;Glut2loxP/loxP mice who do not receive tamoxifen? This is important and needs to be specified.

- In our previous response to the reviewer, we had already mentioned which control group was used in this study. Please see our response to the second reviewer’s point 3. As mentioned to the reviewer, we had used Glut2loxp/loxp mice as the control group, which is also described multiple times in the figure legends of our previous paper that reported the phenotype of renal Glut2 KO mice. Per the reviewer’s advice, we have provided the information again in a revised version of this manuscript.

(4) The authors should report some additional control measures for the renal denervation that could also impact blood glucose and perhaps some of their other measures. The control measures, which one would like to see unimpacted by renal denervation, include body weights, food consumption and water intake, and glycosuria itself.

- Please also see fig. 3 in the present manuscript that demonstrates renal afferent denervation doesn’t influence baseline blood glucose or plasma insulin levels. We have now also mentioned in the text that the denervation doesn’t affect food intake or bodyweight.

(5) The graphical abstract shows a link between the hypothalamus and the liver that is completely unsupported by any of the current findings. That arrow should be removed.

- Because we observed an increase in hepatic glucose production in renal Glut2 KO mice (Fig. 1) - which was reduced by 50% after selective afferent renal denervation (Fig. 3) - in the graphical abstract we are suggesting a neural connection between the kidney-brain-liver or an endocrine factor(s) to account for these changes in blood glucose levels as also described in the discussion section. We can include a question mark ‘?’ in the graphical abstract to show that further studies are need to validate these proposed mechanisms; however, we cannot just remove the arrow as advised by the reviewer.

(6) Though the authors have toned down their language implying a causal link between the HPA measures and compensatory elevation of blood glucose in the face of glycosuria, the title still implies this causal link. It is still the case that their data do not support causation. There are many potential ways to establish a causal link but those experiments are not performed here. The renal afferents are correlated with Crh content of the PVN, but nothing has been done to show that the Crh content is important for elevating blood glucose. In light of this, the title should be toned down. Perhaps something like "Renal nerves maintain blood glucose production and elevated HPA activity in response to glycosuria". The link between HPA and glucose is not shown in this paper.

- We request the reviewer to take a look at figure 1, showing an increase in glucose production in renal Glut2 KO mice and figure 3, which demonstrates that an afferent renal denervation reduces blood glucose levels by 50%. The afferent renal denervation (ablation of afferent renal nerves) does reduce blood glucose levels in renal Glut2 KO mice. Therefore, the use of the word ‘promote’ in the title is accurate and appropriate to reflect the role of the afferent renal nerves in contributing to about 50% increase in blood glucose levels in renal Glut2 KO mice.

- Regarding the reviewer's comment on changes in Crh gene expression, please look at figure 3. Ablation of renal afferent nerves decreases hypothalamic Crh gene expression and other mediators of the HPA axis by 50%. Therefore, the afferent renal nerves do contribute to regulating blood glucose levels, at least in part, by the HPA axis (which is widely known to change blood glucose levels). The use of words such as ‘required’ or ‘necessary’ in the title may have indicated causal role or could have been misleading here; therefore, we have purposely used ‘promote’ in the title to accurately reflect the findings of this study.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I have only minor text corrections to add:

- line 223 "A list"

- line 253 "independent"

- line 271 "the body's"

- line 304 "do not"

Yes, we have corrected these errors in a revised version of this manuscript.

Reviewer #2 (Recommendations For The Authors):

(1) Please report the dilutions used, if any, for the ELISAs. If the samples were run neat, please report this. Many manufacturer's instructions say that the user must determine the correct dilution to use for the samples collected. Also, sometimes when small blood volumes are collected, samples must be diluted to achieve the minimum volume collected for the assay. It is not sufficient to indicate that a reader refers to the manufacturer's instructions.

- Per the reviewer’s advice, we have included the dilutions used for each assay in the methods.

Author response:

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

Reviewer #1:

Point 1: The authors have demonstrated that Cs9g12620 contains the EBE of PthA4 in the promoter region, to show that PthA4 controls Cs9g12620, the authors need to compare to the wild type Xcc and pthA4 mutant for Cs9g12620 expression. The data in Figure 1 is not enough.

The data in Figure 1 D and E show a pthA4 Tn5 insertion mutant Mxac126-80 and the expression level of Cs9g12620 in citrus inoculated with the pthA4 mutant.

Point 2: The authors confirmed the interaction between PthA4 and the EBE in the promoter of Cs9g12620 using DNA electrophoretic mobility shift assay (EMSA). However, Figure 2B is not convincing. The lane without GST-PthA4 also clearly showed a mobility shift. For the EMSA assay, the authors need also to include a non-labeled probe as a competitor to verify the specificity. The description of the EMSA in this paper suggests that it was not done properly. It is suggested the authors redo this EMSA assay following the protocol: Electrophoretic mobility shift assay (EMSA) for detecting protein-nucleic acid interactions PMID: 17703195.

Thank you very much for your comments. We have re-conducted the EMSA analysis based on your suggestion. The DNA probe was labeled with Cy5, included a non-labeled probe as a competitor. (Figure 3 B and D; Figure 4B and E)

Point 3: The authors also claimed that PthA4 suppresses the promote activity of Cs9g12620. The data is not convincing and also contradicts with their own data that overexpression of Cs9g12620 causes canker and silencing of it reduces canker considering PthA4 is required for canker development. The authors conducted the assays using transient expression of PthA4. It should be done with Xcc wild type, pthA4 mutant, and negative control to inoculate citrus plants to check the expression of Cs9g12620.

We have detected Cs9g12620 expression in silencing citrus plants inoculated wild type Xcc 29-1. (Figure 7F)

Point 4: Figure 6 AB is not convincing. There are no apparent differences. The variations shown in B are common in different wild-type samples. It is suggested that the authors conduct transgenic instead of transient overexpression.

It has been proven that transient expression of PthA4 leads to canker-like phenotype, suggesting that this experiment is effective. However, it will be more confident if conduct transgenic plant overexpressing pthA4 and Cs9g12620. We’ll create the plants in our following research to confirm the phenotype.

Point 5: Gene silencing data needs more appropriate controls. Figure D seems to suggest canker symptoms actually happen for the RNAi treated. The authors need to make sure the same amount of Xcc was used for both CTV empty vector and the RNAi. It is suggested a blink test is needed here.

We used the same amount of Xcc to inoculate CTV empty vector and the RNAi. In either inoculation, the cultured Xcc cells were suspended in sterile distilled water to a final concentration of 108 CFU/mL (OD600 = 0.3).

Point 6: Figure 1. Please draw a figure to clearly show the location of the EBE in the promoter of Cs9g12620, including the transcription start site, and translational start site.

The EBE in Cs9g12620 promoter was indicated by underlined in Figure supplement 1. We did not sure about the translation start site, but the translation start site was labelled.

Author response:

Reviewer #1 (Public Review):

Areas of improvement and suggestions:

(1) "These results suggest the SP targets interneurons in the brain that feed into higher processing centers from different entry points likely representing different sensory input" and "All together, these data suggest that the abdominal ganglion harbors several distinct type of neurons involved in directing PMRs"

The characterization of the post-mating circuitry has been largely described by the group of Barry Dickson and other labs. I suggest ruling out a potential effect of mSP in any of the well-known post-mating neuronal circuitry, i.e: SPSN, SAG, pC1, vpoDN or OviDNs neurons. A combination of available split-Gal4 should be sufficient to prove this.

Indeed, we have tested drivers for some of these neurons already and agree that this information is important to distinguish neurons which are direct SP target from neurons which are involved in directing reproductive behaviors.

(2) Authors must show how specific is their "head" (elav/otd-flp) and "trunk" (elav/tsh) expression of mSP by showing images of the same constructs driving GFP.

The expression pattern for tshGAL, which expresses in the trunk is already published (Soller et al., 2006). We will add images for “head” expression.

(3) VT3280 is termed as a SAG driver. However, VT3280 is a SPSN specific driver (Feng et al., 2014; Jang et al., 2017; Scheunemann et al., 2019; Laturney et al., 2023). The authors should clarify this.

According to the reviewers suggestion, we will clarify the specificity of VT3280.

(4) Intersectional approaches must rule out the influence of SP on sex-peptide sensing neurons (SPSN) in the ovary by combining their constructs with SPSN-Gal80 construct. In line with this, most of their lines targets the SAG circuit (4I, J and K). Again, here they need to rule out the involvement of SPSN in their receptivity/egg laying phenotypes. Especially because "In the female genital tract, these split-Gal4 combinations show expression in genital tract neurons with innervations running along oviduct and uterine walls (Figures S3A-S3E)".

We agree with this reviewer that we need a higher resolution of expression to only one cell type. However, this is a major task that we will continue in follow up studies.

In principal, use of GAL80 is a valid approach to restrict expression, if levels of GAL80 are higher than those of GAL4, because GAL80 binds GAL4 to inhibit its activity. Hence, if levels of GAL80 are lower, results could be difficult to interpret.

(5) The authors separate head (brain) from trunk (VNC) responses, but they don't narrow down the neural circuits involved on each response. A detailed characterization of the involved circuits especially in the case of the VNC is needed to (a) show that the intersectional approach is indeed labelling distinct subtypes and (b) how these distinct neurons influence oviposition.

Again, we agree with this reviewer that we need a higher resolution of expression to only one cell type. However, this is a major task that we will continue in follow up studies.

Reviewer #2 (Public Review):

Strength:

The intersectional approach is appropriate and state-of-the art. The analysis is a very comprehensive tour-de-force and experiments are carefully performed to a high standard. The authors also produced a useful new transgenic line (UAS-FRTstopFRT mSP). The finding that neurons in the brain (head) mediate the SP effect on receptivity, while neurons in the abdomen and thorax (ventral nerve cord or peripheral neurons) mediate the SP effect on oviposition, is a significant step forward in the endavour to identify the underlying neuronal networks and hence a mechanistic understanding of SP action. Though this result is not entirely unexpected, it is novel as it was not shown before.

We thank reviewer 2 for recognizing the advance of our work.

Weakness:

Though the analysis identifies a small set of neurons underlying SP responses, it does not go the last step to individually identify at least a few of them. The last paragraph in the discussion rightfully speculates about the neurochemical identity of some of the intersection neurons (e.g. dopaminergic P1 neurons, NPF neurons). At least these suggested identities could have been confirmed by straight-forward immunostainings agains NPF or TH, for which antisera are available. Moreover, specific GAL4 lines for NPF or P1 or at least TH neurons are available which could be used to express mSP to test whether SP activation of those neurons is sufficient to trigger the SP effect.

We appreciate this reviewers recognition of our previous work showing that receptivity and oviposition are separable. As pointed out we have now gone one step further and identified in a tour de force approach subsets of neurons in the brain and VNC.

We agree with this reviewer that we need a higher resolution of expression to only one cell type. As pointed out by this reviewer, the neurochemical identity is an excellent suggestions and will help to further restrict expression to just one type of neuron. However, this is a major task that we will continue in follow up studies.

Reviewer #3 (Public Review):

Strengths:

Besides the main results described in the summary above, the authors discovered the following:

(1) Reduction of receptivity and induction of egg-laying are separable by restricting the expression of membrane-tethered SP (mSP): head-specific expression of mSP induces reduction of receptivity only, whereas trunk-specific expression of mSP induces oviposition only. Also, they identified a GAL4 line (SPR12) that induced egg laying but did not reduce receptivity.

(2) Expression of mSP in the genital tract sensory neurons does not induce PMR. The authors identified three GAL4 drivers (SPR3, SPR 21, and fru9), which robustly expressed mSP in genital tract sensory neurons but did not induce PMRs. Also, SPR12 does not express in genital tract neurons but induces egg laying by expressing mSP.

We thank reviewer 3 for recognizing these two important points regarding the SP response that point to a revised model for how the underlying circuitry induces the post-mating response.

Weaknesses:

(1) Intersectional expression involving ppk-GAL4-DBD was negative in all GAL4AD lines (Supp. Fig.S5). As the authors mentioned, ppk neurons may not intersect with SPR, fru, dsx, and FD6 neurons in inducing PMRs by mSP. However, since there was no PMR induction and no GAL4 expression at all in any combination with GAL4-AD lines used in this study, I would like to have a positive control, where intersectional expression of mSP in ppk-GAL4-DBD and other GAL4-AD lines (e.g., ppk-GAL4-AD) would induce PMR.

We will add positive controls of for ppk-DBD expression and expand the discussion section.

(2) The results of SPR RNAi knock-down experiments are inconclusive (Figure 5). SPR RNAi cancelled the PMR in dsx ∩ fru11/12 and partially in SPR8 ∩ fru 11/12 neurons. SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive; it is unclear whether SPR mediates the phenotype in SPR8 ∩ fru 11/12 and dsx ∩ SPR8 neurons.

We agree with this reviewer that the interpretation of the SPR RNAi results are complicated by the fact that SP has additional receptors (Haussmann et al 2013). The results are conclusive for all three intersections when expressing UAS mSP in SPR RNAi with respect to oviposition, e.g. egg laying is not induced in the absence of SPR. For receptivity, the results are conclusive for dsx ∩ fru11/12 and partially for SPR8 ∩ fru 11/12.

Potentially, SPR RNAi knock-down does not sufficiently reduce SPR levels to completely reduce receptivity in some intersection patterns, likely also because splitGal4 expression is less efficient.

Why SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive is unclear, but we anticipate that we need a higher resolution of expression to only one cell type to resolve this unexpected result. However, this is a major task that we will continue in follow up studies.

SPR RNAi knock-down experiments may also help clarify whether mSP worked autocrine or juxtacrine to induce PMR. mSP may produce juxtacrine signaling, which is cell non-autonomous.

Whether membrane-tethered SP induces the response in a autocrine manner is an import aspect in the interpretation of the results from mSP expression.

Removing SPR by SPR RNAi and expression of mSP in the same neurons did not induce egg laying for all three intersection and did not reduce receptivity for dsx ∩ fru11/12 and for SPR8 ∩ fru 11/12. Accordingly, we can conclude that for these neurons the response is induced in an autocrine manner.

We will add this aspect to the discussion section.

Author response:

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

eLife assessment:

The statistical analyses are incomplete.

I find that the eLife assessment mentions “statistical analyses are incomplete” while the reviewers mention that the data are compelling and results are technically solid. Besides all observations in the manuscript are presented with robust and established norms of statistical analysis.

Public Reviews:

Reviewer #1 (Public Review):

Strengths:

The use of data from before COVID-19 is both a strength and a weakness. Because COVID had effects on vascular health and had higher death rates for groups with the comorbidities of interest here, it has likely shifted the demographics in ways that would shift the results in unpredictable ways if the analysis were repeated with current data. This can be a strength in providing a reference point for studying those changes as well as allowing researchers to study differences between regions without the complication of different public health responses adding extra variation to the data. On the other hand, it limits the usefulness of the data in research concerned with the current status of the various populations.

We completely agree with the observation, but were restricted as the purpose was to use the most robust and technically qualified data from GBD. The post COVID19 GBD data has not yet been released, but I am sure the observations made in the study can help in guiding the issues in the post COVID era too, because genetics is not going to change in these population groups.

However, we did highlight this aspect of COVID19 even in our original version and also in the revised version.

Reviewer #2 (Public Review):

Weaknesses:

The presentation is not focused. It would be better to include p-values and focus presentation on the main effects from the dataset analysis.

The significant p-values were restricted to public health data only to identify and distinguish differences in incidence, prevalence and mortality and how they differ across world populations. These differences have often been interpreted from socio-economic point of view, while our manuscript presents the reasons for differences for main condition (Stroke) and its comorbid condition among different ethnicities from a genetic perspective. This genetic perspective was further explored to identify unique ethnic specific variants and their patterns of linkage disequilibrium in distinguishing the phenotypic variations. Considering the quantum and diversity of data, both for public health and GWAS data, there can be several directions but for presentation we focused only on the most distinguishing and established phenotypic differences. I am sure this will open up avenues for several future investigations including COVID, as has been highlighted by the reviewers too. All observations were presented with robust and established norms of statistical analysis.

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

Thanks for the constructive observations on strengths and weaknesses of our manuscript. Interestingly, some of the weaknesses mentioned here also turns out to be the strength of the article. For example COVID19 has been mentioned by the reviewer as a driver to increase the mortality in some comorbid conditions and stroke. Firstly, I must clarify that, our data is from PreCOVID era and we indeed mention that in COVID era, COVID-19 might differentially impact the risk of stroke. Possibly this differential influence on the comorbidities of stroke, is likely to be influenced by its underlying genetics of stroke and its comorbidities.

I have tried to address the concerns raised by the reviewers, which ideally doesn’t impact the original manuscript. Statistical limitation has been commented pertaining to P-values, which has been clarified here. However, certain minor concerns such as abbreviations have been resolved in the revised manuscript. My response to weakness and reviewer’s comments are mentioned below.

Reviewer #1 (Public Review):

Strengths:

The data provided here will provide a foundation for a lot of future research into the causes of the observed correlations as well as whether the observed differences in comorbidities across regions have clinically relevant effects on risk management.

Weaknesses:

• As with any cross-national analysis of rates, the data is vulnerable to differences in classification and reporting across jurisdictions.

GBD data is the most robust and most comprehensive data resource which has been used and accepted globally in predicting the health metrics statistics.

GBD data indeed considers normalisations, regarding classification and reporting.

To the best of our knowledge this is the best available resource to consider all health metrics analysis.

• Furthermore, given the increased death rate from COVID-19 associated with many of these comorbid conditions and the long-term effects of COVID-19 infection on vascular health, it is expected that many of the correlations observed in this dataset will shift along with the shifting health of the underlying populations.

I must clarify that we have used data prior to COVID-19.

But yes the patterns after COVID19 will shift due to the impact of covid. This makes the study even more relevant as the comorbid conditions of stroke are also the risk drivers for COVID19 and mortality. This shift has been reported by some authors, which has been discussed in the discussion.

Therefore, understanding the genetic factors underlying stroke and its comorbid conditions might help in resolving how COVID19 might differentially impact on health outcome.

We did highlight this aspect of COVID19 even in our original version.

Introduction 1st para:

“It is the accumulated risk of comorbid conditions that enhances the risk of stroke further. Are these comorbid conditions differentially impacted by socio-economic factors and ethnogeographic factors. This was clearly evident in COVID era, when COVID-19 differentially impacted the risk of stroke, possibly due to its differential influence on the comorbidities of stroke.”

Discussion 3rd para:

“Studies reported reduction in life expectancy in 31 of 37 high-income countries, deduced to be due to COVID-191 . However, it would be unfair to ignore the comorbid conditions which could also be the critical determinants for reduced life expectancy in these countries.”

Recommendations For The Authors:

On page 5, the authors make a note about Africa and the Middle East having the highest ASMR for high SBP and comment about the relative populations of these regions. The populations of the regions are irrelevant to the rate.

Since the study is on comorbid factors of stroke and its impact on mortality therefore, relative burden seems critical. This has been further elaborated here to justify the comment, which indeed is an integral part of the original manuscript.

Paragraph referred – Results section 2:

“Ethno-regional differences in mortality and prevalence of stroke and its major comorbid conditions

We observed interesting patterns of ASMRs of stroke, its subtypes and its major comorbidities across different regions over the years as shown in figure 1a, table 1 and supplementary files S2 & S3. When assessed in terms of ranks, high SBP is the most fatal condition followed by IHD in all regions, except Oceania (OCE) where IHD and high SBP swap ranks. Africa (AFR; 206.2/100000, 95%UI 177.4-234.2) and Middle East (MDE; 198.6/100000, 95%UI 162.8-234.4) have the highest ASMR for high SBP, even though they rank as only the third and sixth most populous continents (fig. S2), respectively.”

On page 17, the authors are alarmed by a large ratio between prevalence rates and mortality rates for certain conditions. This is confusing since this indicates that these conditions are not as dangerous as the other conditions.

This has been further elaborated here to justify the comment, which indeed is an integral part of the original manuscript.

Paragraph referred – Discussion para 1:

“While the global stroke prevalence is nearly 15 times its mortality rate, prevalence of comorbid conditions such as high SBP, high BMI, CKD, T2D are alarmingly 150- to 500-fold higher than their mortality rates. These comorbid conditions can drastically affect the outcome of stroke.”

In Figure 4, the colors are not defined.

In Structure plot colours are assigned as per each K, it doesn’t directly refer to any population. But the plot distinguishes the stratification of populations as per K. Ramasamy, R.K., Ramasamy, S., Bindroo, B.B. et al. STRUCTURE PLOT: a program for drawing elegant STRUCTURE bar plots in user friendly interface. SpringerPlus 3, 431 (2014). https://doi.org/10.1186/2193-1801-3-431

Reviewer #2 (Public Review):

Strengths:

The idea is interesting and the data are compelling. The results are technically solid.

The authors identify specific genetic loci that increase the risk of a stroke and how they differ by region.

Weaknesses:

The presentation is not focused. It would be better to include p-values and focus presentation on the main effects of the dataset analysis.

I presume the comment is made with reference to results with significant p-values.

P-values are mentioned in the main text when referring to significant decrease or increase with respect to global rates and time e.g. P-values for comparison of a year 2019, are based on regional rates to global rates of 2019. Supplementary table S2a (mortality) and S3a (prevalence) e.g. P-values for comparison between year is based on 2019 rates to 2009 rates in Supplementary table S2b (mortality) and S3b (prevalence) e.g. P-values for proportional mortality and proportional prevalence in Supplementary table S4 and S5 is also based on global rates.

Recommendations For The Authors:

It would be better to minimize the use of acronyms. Often one has to go back to decipher what the acronym stands for. It is fine to have acronyms in figure legends, if necessary. However, at least for regions, please do not use acronyms.

In the revised version we have tried to minimise the Acronyms.

Removed the acronyms for regions and other places wherever possible however, the diseases acronyms have been maintained as per the GBD terms.

Please focus the presentation on the main results. Currently, the presentation wanders and repeats itself a lot.

Since the manuscript tries to address the global and regional rates of prevalence, mortality and its relationship to genetic correlates, it is difficult not to repeat the same to stress the significant observations coming out of different analysis methods. This might reflect on some amount of repetitiveness but the intention was to stress the significant observations.

I would also recommend acknowledging and discussing socioeconomic factors earlier in the manuscript.

Current mention happens in 3rd para of Discussion

“The changing dynamics of stroke or its comorbid conditions can be attributed to multitude of factors. Often global burden of stroke has been discussed from the point of view of socio-economic parameters. Studies indicate that half of the stroke-related deaths are attributable to poor management of modifiable risk factors 8,9. However, we observe that different socio-economic regions are driven by different risk factors.”

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

This paper by Beath et. al. identifies a potential regulatory role for proteins involved in cytoplasmic streaming and maintaining the grouping of paternal organelles: holding sperm contents in the fertilized embryos away from the oocyte meiotic spindle so that they don't get ejected into the polar body during meiotic chromosome segregation. The authors show that by time-lapse video, paternal mitochondria (used as a readout for sperm and its genome) is excluded from yolk granules and maternal mitochondria, even when moving long distances by cytoplasmic streaming. To understand how this exclusion is accomplished, they first show that it is independent of both internal packing and the engulfment of the paternal chromosomes by maternal endoplasmic reticulum creating an impermeable barrier. They then test whether the control of cytoplasmic steaming affects this exclusion by knocking down two microtubule motors, Katanin and kinesis I. They find that the ER ring, which is used as a proxy for paternal chromosomes, undergoes extensive displacement with these treatments during anaphase I and interacts with the meiotic spindle, supporting their hypothesis that the exclusion of paternal chromosomes is regulated by cytoplasmic streaming. Next, they test whether a regulator of maternal ER organization, ATX-2, disrupts sperm organization so that they can combine the double depletion of ATX-2 and KLP-7, presumably because klp-7 RNAi (unlike mei-1 RNAi) does not affect polar body extrusion and they can report on what happens to paternal chromosomes. They find that the knockdown of both ATX-2 and KLP-7 produces a higher incidence of what appears to be the capture of paternal chromosomes by the meiotic spindle (5/24 vs 1/25). However, this capture event appears to halt the cell cycle, preventing the authors from directly observing whether this would result in the paternal chromosomes being ejected into the polar body. 

Strengths: 

This is a useful, descriptive paper that highlights a potential challenge for embryos during fertilization: when fertilization results in the resumption of meiotic divisions, how are the paternal and maternal genomes kept apart so that the maternal genome can undergo chromosome segregation and polar body extrusion without endangering the paternal genome? In general, the experiments are well-executed and analyzed. In particular, the authors' use of multiple ways to knock down ATX-2 shows rigor. 

Weaknesses: 

The paper makes a case that this regulation may be important but the authors should do some additional work to make this case more convincing and accessible for those outside the field. In particular, some of the figures could include greater detail to support their conclusions, they could explain the rationale for some experiments better and they could perform some additional control experiments with their double depletion experiments to better support their interpretations. Also, the authors' inability to assess the functional biological consequences of the capture of the sperm genome by the oocyte spindle should be discussed, particularly in light of the cell cycle arrest that they observe. 

These general comments are addressed in the more specific critiques below.

Reviewer #2 (Public Review): 

Summary 

In this manuscript, Beath et al. use primarily C. elegans zygotes to test the overarching hypothesis that cytoplasmic mechanisms exit to prevent interaction between paternal chromosomes and the meiotic spindle, which are present in a shared zygotic cytoplasm after fertilization. Previous work, much of which by this group, had characterized cytoplasmic streaming in the zygote and the behavior of paternal components shortly after fertilization, primarily the clustering of paternal mitochondria and membranous organelles around the paternal chromosomes. This work set out to identify the molecular mechanisms responsible for that clustering and test the specific hypothesis that the "paternal cloud" helps prevent the association of paternal chromosomes with the meiotic spindle. 

Strengths 

This work is a collection of technical achievements. The data are primarily 3- and 4-channel time-lapse images of zygotes shortly after fertilization, which were performed inside intact animals. There are many instances in which the experiments show extreme technical skill, such as tracking the paternal chromosomes over large displacements throughout the volume of the embryo. The authors employ a wide variety of fluorescent reporters to provide a remarkably clear picture of what is going on in the zygote. These reagents and the novel characterization of these stages that they provide will be widely beneficial to the community. 

The data provide direct visualization of what had previously been a mostly hypothetical structure, the "paternal cloud," using simultaneous labeling of paternal DNA and mitochondria in combination with a variety of maternal proteins including maternal mitochondria, yolk granules, tubulin, and plasma membrane. Together, these images provided convincing evidence of the existence of this specified cytoplasmic domain. They go on to show that the knockdown of the ataxin-2 homolog ALX-2, a protein previously shown to affect ER dynamics, disrupted the paternal cloud, identifying a role for ER organization in this structure. 

The authors then used the system to test the functional consequences of perturbing the cytoplasmic organization. Consistent with the paternal cloud being a stable structure, it stayed intact during large movements the authors generated using previously published knockdowns (of mei-1/katanin and kinesin-13/kpl-7) that increased cytoplasmic streaming. They used this data to document instances in which the paternal chromosomes were likely to have been attached to the spindle. They concluded with direct evidence of spindle fibers connecting to the paternal chromatin upon knockdown of ATX-2 in combination with increased cytoplasmic streaming, providing strong, direct support for their overarching hypothesis. 

Weaknesses 

While the data is convincing, the narrative of the paper could be streamlined to highlight the novelty of the experiments and better articulate the aims. For example, the cloud of paternal mitochondria and membranous organelles was previously shown, but Figures 1-2 largely reiterate that observation. The innovation seems to be that the combination of ER, yolk, and maternal mitochondrial markers makes the existence of a specified domain more concrete. There are also some instances where more description is needed to make the conclusions from the images clear. 

These general comments are addressed in the more specific critiques below.

The manuscript intersperses what read like basic characterizations of fluorescent markers that, as written, can distract from the main story. The authors characterized the dynamics of ER organization throughout the substages of meiosis and the permeability of the envelope of ER that surrounds the paternal chromatin, but it could be more clearly established how the ability to visualize these structures allowed them to address their aims.

We have added the following after the initial description of ER morphology changes: (ER morphology was used to determine cell-cycle stages during live imaging reported below in Fig. 6.)

More background on what was previously known about ER organization in M-phase and the role of ataxin proteins specifically may help provide more continuity. 

We have added references to transitions to ER sheets during mitotic M-phase in HeLa cells and Xenopus extracts.

Reviewer #3 (Public Review): 

Summary: 

This study by Beath et al. investigated the mechanisms by which sperm DNA is excluded from the meiotic spindle after fertilization. Time-lapse imaging revealed that sperm DNA is surrounded by paternal mitochondria and maternal ER that is permeable to proteins. By increasing cytoplasmic streaming using kinesin-13 or katanin RNAi, the authors demonstrated that limiting cytoplasmic streaming in the embryo is an important step that prevents the capture of sperm DNA by the oocyte meiotic spindle. Further experiments showed that the Ataxin-2 protein is required to hold paternal mitochondria together and close to the sperm DNA. Finally, double depletion of kinesin-13 and Ataxin-2 suggested an increased risk of meiotic spindle capture of sperm DNA. 

Overall, this is an interesting finding that could provide a new understanding of how meiotic spindle capture of sperm DNA and its accidental expulsion into the polar body is prevented. However, some conceptual gaps need to be addressed and further experiments and improved data analyses would strengthen the paper. 

- It would be helpful if the authors could discuss in good detail how they think maternal ER surrounds the sperm DNA

We have added 2 references to papers about nuclear envelope re-assembly from Shirin Bahmanyar’s lab and suggest the ER envelope is a halted intermediate in nuclear envelope reassembly.

and why is it not disrupted following Ataxin disruption. 

We have been attempting to disrupt ER structures in the meiotic embryo for the last 5 years by depleting profilin, BiP, atlastin, ATX-2 and by optogenetically packing ER into a ball in the middle of the oocyte.  None of these treatments prevent envelopment of the sperm DNA by maternal ER.  None of these treatments remove ER from the spindle envelope and none remove ER from the plasma membrane.  These treatments mostly result in “large aggregates” of ER that we have not examined by EM.  Wild speculation: any disruption of the ER strong enough to prevent ER envelopment around chromatin would be sterile because the M to S transition in the mitotic zone of the germline would be blocked.  Rapid depletion of ATX-2 to the extent shown by rigorous data in this manuscript does not prevent ER envelopment around chromatin.  We chose not to speculate about the reasons for this because we do not know why.

- Since important phenotypes revealed in RNAi experiments (e.g. kinesin-13 and ataxin-2 double depletion) are not very robust, the authors should consider toning down their conclusions and revising some of their section headings. I appreciate that they are upfront about some limitations, but they do nonetheless make strong concluding sentences. 

We have changed the discussion of the klp-7 atx-2 double depletion to: “The capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos suggests that the integrity of the exclusion zone around the sperm DNA might insulate the sperm DNA from spindle microtubules.  However, a much larger number of klp-7(RNAi) singly depleted and atx-2(degron) singly depleted time-lapse sequences are needed to rigorously support this idea. “

- The discussion section could be improved further to present the authors' findings in the larger context of current knowledge in the field. 

We have expanded the discussion as suggested.

- The authors previously demonstrated that F-actin prevents meiotic spindle capture of sperm DNA in this system. However, the current manuscript does not discuss how the katanin, kinesin-13 and Ataxin-2 mechanisms could work together with previously established functions of F-actin in this process. 

We have added pfn-1(RNAi) to the discussion section.

- How can the authors exclude off-target effects in their RNAi depletion experiments? Can kinesin-13, katanin, and Ataxin phenotypes be rescued for instance? 

For ataxin-2 phenotypes, two completely independent controls for off target effects are shown.  GFP(RNAi) on a strain with and endogenous ATX-2::GFP tag vs GFP(RNAi) on a strain with no tag on the ATX-2.  ATX-2::AID with or without auxin.  For kinesin-13 and katanin, we did not do a rigorous control for off-target effects of RNAi.  However, the effects of these depletions on cytoplasmic microtubules have been previously reported by others

- How are the authors able to determine if the paternal genome was actually captured by the spindle? Does lack of movement definitively suggest capture without using a spindle marker? 

mKate::tubulin labels the spindle in each capture event.  This can be seen in Video S3. for mei-1(RNAi) and Figure 9 for atx-2 klp-7 double depletions.

(1) Major issues: 

The images provided are not convincing that mitochondria are entirely excluded from the regions with yolk granules from the images provided. Please provide insets of magnified images of the paternal mitochondria in Figure 1E to more clearly show the exclusion even when paternal mitochondria are streaming. Providing grayscale images, individual z-sections and/or some quantification of this data might also be more convincing to this reviewer. 

We have modified Fig. 1 by adding single wavelength magnified insets to more clearly show that paternal mitochondria are in a “black hole” in the maternal yolk granules during  cytoplasmic streaming.

Figure 2 -This figure can be retitled to highlight that the paternal organelle cloud is impermeable to mitochondria and conserved. 

The legend has been re-titled as suggested.

Figure 3B, An image of the DNA within the ring of maternal ER especially since the maternal ER ring is used as a proxy for the paternal chromosomes in later figures would strengthen the authors' claims.

We have added a panel showing DAPI-stained DNA in the center of the ER ring and paternal mitochondria cloud. 

Why is the faster time scale imaging significant? I think this could be more clearly set up in the paper. Perhaps rapid imaging of maternal mito-labeled kca-1(RNAi) embryos would better show the difference in time scale, with the expectation that the paternal cloud forms and persists while the ER invades. 

We are not sure what the reviewer means.  5 sec time intervals were used throughout the paper.  We are also not sure how kca-1(RNAi) would help.  Movement of the entire oocyte into and out of the spermatheca is what limits the ability to keep a fusing sperm in focus.  kca-1(RNAi) would prevent cytoplasmic streaming but not ovulation movements.

Figure 4 - The question about the permeability of the ER envelope seems to come out of nowhere as written. It isn't clear how it contributes to the larger story about preventing sperm incorporation in the spindle.

This section of the results is introduced with: “If the maternal ER envelope around sperm DNA was sealed and impermeable during meiosis, this could both prevent the sperm DNA from inducing ectopic spindle assembly and prevent the sperm DNA from interacting with meiotic spindle microtubules.” 

The data in Figure 4 would probably not be expected to be in this paper based on the paper title. Maybe the title needs something about ER dynamics? "eg. ATX-2 but not an ER envelope" isolates the paternal chromatin? 

In Figure 5, it seems that RNAi of klp-7 and Mei-1 had slightly different effects on short-axis displacement of the ER envelope (klp-7 affecting it more dramatically than mei-1) and slightly different effects on interaction with the meiotic spindle (capture vs streaming past the spindle). The authors mention in their discussion that the difference in the interaction with the meiotic spindle might reflect the effects that loss of Mei-1 may have on the spindle but could it also be a consequence of the differences in cytoplasmic streaming observed?

With our current data, the only statistically significant difference between cytoplasmic streaming of the sperm contents in mei-1(RNAi) vs klp-7(RNAi) is that excessive streaming persists longer into metaphase II in klp-7(RNAi).  We have added a sentence describing this difference to the results.  If differences in streaming were the cause of different capture frequencies, then klp-7(RNAi) would cause more capture events than mei-1(RNAi) but the opposite was observed.  We have avoided too much discussion here because the frequency of capture events is too low to demonstrate statistically significant differences between mei-1(RNAi), klp-7(RNAi), and atx-2(degron) + klp-7(RNAi) without a very large increase in the number of time-lapse sequences.  

Also, the authors should find a way to represent this interaction with the meiotic spindle in a quantitative or table form to allow the reader to observe some of the patterns they report more easily.

We have added a table to Fig. 9 that summarizes capture data.

Finally, can the authors report when they observe the closest association with the meiotic spindle: Does it correlate with the period of greatest displacement (AI) or are they unlinked? 

The low frequency of capture events makes it difficult to test this rigorously.

Figure 6- 'Endogenously tagged ATX-2 was observed throughout oocytes and meiotic embryos without partial co-localization with ER.' How can the authors exclude co-localization with ER? 

We have changed the wording to: “Endogenously tagged ATX-2 was observed throughout oocytes and meiotic embryos (Fig. 6A; Fig. S2).  ATX-2 did not uniquely  co-localize with ER (Fig. S2).“

The rationale for why the authors think that the integrity of sperm organelles is important to keep the genomes apart is not clear to this reviewer and needs to be explained better. Moving the discussion of the displacement experiments in Figure S3 from the end of the results section to the ATX-2 knockdown section would help accomplish this. 

We have added the sentence: “The frequency of sperm capture by the meiotic spindle (Fig. 9D) was significantly higher than wild-type controls in klp-7(RNAi) atx-2(AID) double depleted embryos (p=0.011 Fisher’s exact test).   Although the number of single mutant embryos analyzed was too low to demonstrate a significant difference between single and double mutant embryos,  these results qualitatively support the hypothesis that limiting cytoplasmic streaming and maintaining the integrity of the ball of paternal mitochondria are both important for preventing capture events between the meiotic spindle and sperm DNA.”

It looks like, in the double knockdown of ATX-2 and KLP-7, the spread of paternal mitochondria is less affected than when only ATX-2 is depleted. What effect does this result have on the observation that the incidence of sperm capture appears to increase in the double depletion? What does displacement of the ER ring look like in the double depletion? Is it additive, consistent with their interpretation that both limiting cytoplasmic streaming and maintaining the integrity of the ball of paternal mitochondria is required to keep the genomes separate? 

We cannot show a significant difference between single a double knockdowns without increasing n by alot.  We did not analyze ER ring displacement in the double mutant.

Is the increased incidence of capture in the double-depleted embryos significant? 

We have added the sentence: “The frequency of sperm capture by the meiotic spindle (Fig. 9D) was significantly higher than wild-type controls in klp-7(RNAi) atx-2(AID) double depleted embryos (p=0.011 Fisher’s exact test).   Although the number of single mutant embryos analyzed was too low to demonstrate a significant difference between single and double mutant embryos,  these results qualitatively support the hypothesis that limiting cytoplasmic streaming and maintaining the integrity of the ball of paternal mitochondria are both important for preventing capture events between the meiotic spindle and sperm DNA.”

What do the authors make of the cell cycle arrest observed when paternal chromosomes are captured? Is there an argument to be made that this arrest supports the idea that preventing this capture is actively regulated and therefore functionally important? 

We chose not to discuss the mechanism of this arrest because considerably more work would be required to prove that it is not caused by a combination of imaging conditions and genotype.  The low frequency of these capture + arrest events would make it very difficult to show that the arrest does not occur after depleting a checkpoint protein.

(2) Minor concerns: 

Top of page 4: "streaming because depletion tubulin stops cytoplasmic streaming (7)" should be "streaming because depletion of tubulin stops cytoplasmic streaming (7)" 

The ”of” has been inserted.

Page 6: "This result indicated that the volume of paternal mitochondria excludes maternal mitochondria and yolk granules but not maternal ER." The authors have only shown this for maternal mitochondria, not yolk granules. 

We have deleted the mention of yolk granules here.

Page 7: "These results suggest that all maternal membranes are initially excluded from the sperm at fusion." Should be "These results show that maternal ER are initially excluded from the sperm at fusion. Since maternal mitochondria and yolk granules are excluded later, this suggests that all maternal membranes are initially excluded from the sperm at fusion." 

We have changed this sentence as suggested.

It's not clear why the authors show other types of movement that might be quantified when cytoplasmic streaming is affected in Figure 5A and only quantify long-axis and short-axis displacement. 

We have deleted the other types of movement from the schematic.  Although these parameters were quantified, we did not include this data in the results so it would be confusing for the reader to have them in the schematic.

Bottom of page 7: Mention that the GFP::BAF-1 was maternally provided. 

We have added “Maternally provided..”

Missing an Arrow on Figure 1A 9:20. 

We removed the text citation to an arrow in Fig. 1A because we moved most of the description of the ER ring to Fig. 3 to address other reviewer suggestions.

Supplemental videos should be labeled appropriately to indicate what structures are labeled. It is currently difficult to understand what is being shown. 

(3) Issues with the Discussion section: 

"The simplest explanation is that cytoplasm does not mix during the 45 min from GVBD to pronucleus formation due to the high viscosity of cytoplasm." - Citation page 12. 

We have changed the sentence to: “The simplest hypothesis is that maternal and paternal cytoplasm might not mix during the 45 min from GVBD to pronucleus formation due to the high viscosity of cytoplasm.” 

"The higher frequency of capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos compared with either single depletion suggests that the integrity of the exclusion zone around the sperm DNA may insulate the sperm DNA from spindle microtubule" - Pages 12-13 reference the figures. 

This sentence has been rewritten in response to other comments but the new sentence now references revised Fig. 9.

"ATX-2 is required to maintain the integrity of the ball of paternal mitochondria around the sperm DNA, but the mechanism is unknown." - Page 13 reference figure. 

A reference to Figs 7 and 8 has been inserted.

" In control embryos, the sperm contents rarely came near the meiotic spindle in agreement with a previous study that found that male and female pronuclei rarely form next to each other (6). Streaming of the sperm contents was most commonly restricted to a jostling motion with little net displacement, circular streaming in the short axis of the embryo, or long axis streaming in which the sperm turned away from the spindle before the halfway point of the embryo. Depletion of MEI-1 or KLP-7 resulted in longer excursions of the sperm contents in the long axis of the embryo toward the spindle but frequent capture of the sperm by the spindle was only observed in mei-1(RNAi)." - Page 13, the corresponding figures need to be referenced for these sentences. 

We have inserted figure references.

"In capture events observed after double depletion of ATX-2 and KLP-7, a bundle of microtubules was discernible extending from the spindle into the ER envelope surrounding the sperm DNA. Such bundles were not observed in mei-1(RNAi) capture events, likely because of the previously reported low density of microtubules in mei-1(RNAi) spindles (36, 37)." - Pages 13-14 references figures here. 

We have inserted figure references.

"The higher frequency of capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos compared with either single depletion suggests that the integrity of the exclusion zone around the sperm DNA may insulate the sperm DNA from spindle microtubules." - This should be toned down since this phenotype is not robust. 

We have changed this to: “The capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos suggests that the integrity of the exclusion zone around the sperm DNA might insulate the sperm DNA from spindle microtubules.  However, a much larger number of klp-7(RNAi) singly depleted and atx-2(degron) singly depleted time-lapse sequences are needed to rigorously support this idea. “

ATX-2 depletion alters ER morphology but does not impact the maternal ER envelope - could the authors provide a potential explanation for this? 

In the discussion, we cite papers showing that ATX-2 depletion affects many different cellular processes so the effect we see on paternal mitochondria might have nothing to do with the ER ring.   We have been attempting to disrupt ER structures in the meiotic embryo for the last 5 years by depleting profilin, BiP, atlastin, ATX-2 and by optogenetically packing ER into a ball in the middle of the oocyte.  None of these treatments prevent envelopment of the sperm DNA by maternal ER.  None of these treatments remove ER from the spindle envelope and none remove ER from the plasma membrane.  These treatments mostly result in “large aggregates” of ER that we have not examined by EM.  Wild speculation: any disruption of the ER strong enough to prevent ER envelopment around chromatin would be sterile because the M to S transition in the mitotic zone of the germline would be blocked.  Rapid depletion of ATX-2 to the extent shown by rigorous data in this manuscript does not prevent ER envelopment around chromatin.  We chose not to speculate about the reasons for this because we do not know why.

It would be good to have representative images of what the altered spindle looks like in MEI-1-depleted oocytes. 

The structure of MEI-1-depleted spindles has been described in the cited references.

"Depletion of MEI-1 or KLP-7 resulted in longer excursions of the sperm contents in the long axis of the embryo toward the spindle but frequent capture of the sperm by the spindle was only observed in mei-1(RNAi)" - It is intriguing that this does not happen in the double depletion experiments of kinesin-13 and ATX-2. The authors should perhaps discuss this. 

This does happen in KLP-7 ATX-2 double depleted embryos as shown in Fig. 9.

(4) Missing citations: 

"This analysis was restricted to embryos from anaphase I through anaphase II because our streaming data and that of Kimura 2020 indicate that the sperm contents have not moved significantly before anaphase I." - This needs an appropriate citation. Page 10. 

We have inserted citations here.

" The simplest explanation is that cytoplasm does not mix during the 45 min from GVBD to pronucleus formation due to the high viscosity of cytoplasm." - Citation page 12. Not referencing figures in the discussion. 

We have changed the sentence to: “The simplest hypothesis is that maternal and paternal cytoplasm might not mix during the 45 min from GVBD to pronucleus formation due to the high viscosity of cytoplasm.” 

"The higher frequency of capture of the sperm DNA by the meiotic spindle in ATX-2 KLP-7 double depleted embryos compared with either single depletion suggests that the integrity of the exclusion zone around the sperm DNA may insulate the sperm DNA from spindle microtubule" - Pages 12-13 reference the figures. 

A reference to the revised Fig. 9 has been inserted in the revised version of this sentence.

"ATX-2 is required to maintain the integrity of the ball of paternal mitochondria around the sperm DNA, but the mechanism is unknown." 

References to Figs. 7 and 8 have been inserted.

Page 13 reference figure 

" In control embryos, the sperm contents rarely came near the meiotic spindle in agreement with a previous study that found that male and female pronuclei rarely form next to each other (6). Streaming of the sperm contents was most commonly restricted to a jostling motion with little net displacement, circular streaming in the short axis of the embryo, or long axis streaming in which the sperm turned away from the spindle before the halfway point of the embryo. Depletion of MEI-1 or KLP-7 resulted in longer excursions of the sperm contents in the long axis of the embryo toward the spindle but frequent capture of the sperm by the spindle was only observed in mei-1(RNAi)." Page 13, the corresponding figures need to be referenced for these sentences. 

We have inserted citations here.

"In capture events observed after double depletion of ATX-2 and KLP-7, a bundle of microtubules was discernible extending from the spindle into the ER envelope surrounding the sperm DNA. Such bundles were not observed in mei-1(RNAi) capture events, likely because of the previously reported low density of microtubules in mei-1(RNAi) spindles (36, 37)." Pages 13-14 references figures here. 

We have inserted citations here.

(5) Referencing wrong figures in the text: 

Figure 5 - In the figure legend there is a 5C but there is no 5C panel in the figure. 

A C has been inserted in Fig. 5.

Figure 6A - "Dark holes were observed suggesting exclusion from the lumens of larger membranous organelles (Fig. 6A; Fig. S2)." Page 10. 

6A has been changed to 6C.

Figure 6A is showing background autofluorescence in WT oocytes so I am not certain why it is cited here. 

The Figure citation has been corrected to 6B, C.

Figure 8 - I could not find the supplemental data file with the individual mitochondria distance measurements. 

We are including the Excel file with the revised submission.

The last sentence of the first paragraph should be re-worded to be more concise ". In C. elegans, the nucleus is positioned away from the site of future fertilization so that the meiosis I spindle assembles at the opposite end of the ellipsoid zygote from the site of fertilization (2-4). " 

Every word of this sentence is important.

Last sentence second paragraph typo "These microtubules are thought to drive meiotic cytoplasmic streaming because depletion tubulin stops cytoplasmic streaming (7) and depletion of the microtubule-severing protein katanin by RNAi results in an increased mass of cortical microtubules and an increase in cytoplasmic streaming (8)." Pages 3-4. 

“of” has been inserted.

(6) Typos in the introduction should be corrected: 

Ataxin or kinesin-13 are not mentioned in the introduction but these are a big focus of the paper. 

Gong et al 2024 written instead of number citation (page 5), no citation in References.

This has been corrected. 

Supplemental videos should be labeled appropriately to indicate what structures are labeled. It is currently difficult to understand what is being shown.

Author response:

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

Public Reviews:

Reviewer #2 (Public Review):

Summary:

The authors used four datasets spanning 30 countries to examine funding success and research quality score for various disciplines. They examined whether funding or research quality score were influenced by majority gender of the discipline and whether these affected men, women, or both within each discipline. They found that disciplines dominated by women have lower funding success and research quality score than disciplines dominated by men. These findings, are surprising because even the men in women-dominated fields experienced lower funding success and research quality score.

Strengths:

- The authors utilized a comprehensive dataset covering 30 countries to explore the influence of the majority gender in academic disciplines on funding success and research quality scores.

- Findings suggest a systemic issue where disciplines with a higher proportion of women have lower evaluations and funding success for all researchers, regardless of gender.

- The manuscript is notable for its large sample size and the diverse international scope, enhancing the generalizability of the results.

- The work accounts for various factors including age, number of research outputs, and bibliometric measures, strengthening the validity of the findings.

- The manuscript raises important questions about unconscious bias in research evaluation and funding decisions, as evidenced by lower scores in women-dominated fields even for researchers that are men.

- The study provides a nuanced view of gender bias, showing that it is not limited to individuals but extends to entire disciplines, impacting the perception and funding and quality or worth of research.

- This work underscores the need to explore motivations behind gender distribution across fields, hinting at deep-rooted societal and institutional barriers.

- The authors have opened a discussion on potential solutions to counter bias, like adjusting funding paylines or anonymizing applications, or other practical solutions.

- While pointing out limitations such as the absence of data from major research-producing countries, the manuscript paves the way for future studies to examine whether its findings are universally applicable.

Weaknesses:

- The study does not provide data on the gender of grant reviewers or stakeholders, which could be critical for understanding potential unconscious bias in funding decisions. These data are likely not available; however, this could be discussed. Are grant reviewers in fields dominated by women more likely to be women?

- There could be more exploration into whether the research quality score is influenced by inherent biases towards disciplines themselves, rather than only being gender bias.

- The manuscript should discuss how non-binary gender identities were addressed in the research. There is an opportunity to understand the impact on this group.

- A significant limitation is absence of data from other major research-producing countries like China and the United States, raising questions about the generalizability of the findings. How comparable are the findings observed to these other countries?

- The motivations and barriers that drive gender distribution in various fields could be expanded on. Are fields striving to reach gender parity through hiring or other mechanisms?

- The authors could consider if the size of funding awards correlates with research scores, potentially overlooking a significant factor in the evaluation of research quality. Presumably there is less data on smaller 'pilot' funds and startup funds for disciplines where these are more common. Would funding success follow the same trend for these types of funds?

- The language used in the manuscript at times may perpetuate bias, particularly when discussing "lower quality disciplines," which could influence the reader's perception of certain fields.

- The manuscript does not clarify how many gender identities were represented in the datasets or how gender identity was determined, potentially conflating gender identity with biological sex.

Reviewer #3 (Public Review):

This study seeks to investigate one aspect of disparity in academia: how gender balance in a discipline is valued in terms of evaluated research quality score and funding success. This is important in understanding disparities within academia.

This study uses publicly available data to investigate covariation between gender balance in an academic discipline and:

i) Individual research quality scores of New Zealand academics as evaluated by one of 14 broader subject panels.

ii) Funding success in Australia, Canada, Europe, UK.

The study would benefit from further discussion of it limitations, and from the clarification of some technical points (as described in the recommendations for the authors).

Recommendations For The Authors:

Reviewer #2 (Recommendations For The Authors):

This is a very nice study as-is. In the following comments, I have mainly put my thoughts as I was reading the manuscript. If there are practical ways to answer my questions, I think they could improve the manuscript but the data required for this may not be available.

Are there any data on the gender of grant reviewers or stakeholders who make funding decisions?

The research quality score metrics seem to be more related to unconscious bias. The funding metrics may also, but there are potentially simple fixes (higher paylines for women or remove gender identities from applications).

We have included some details about PBRF funding panel gender diversity. These panels are usually more gender balanced than the field they represent, but in the extreme cases (Engineering, Education, Mathematics) they are skewed as would be expected. Panels for other award decision makers was not available.

I wonder if the research score metric isn't necessarily reflecting on the gender bias in the discipline but rather on the discipline itself? Terms like "hard science" and "soft science" are frequently used and may perpetuate these biases. This is somewhat supported by the data - on line 402-403 the authors state that women in male-dominated fields like Physics have the same expected score as a man. Could it be that Physics has a higher score than Education even if Physics was woman-dominated and Education was man-dominated? Are there any instances in the data where traditionally male- or female-dominated disciplines are outliers and happen to be the opposite? If so, in those cases, do the findings hold up?

Overall we would love to answer this question! But our data is not enough. We mention these points in the Discussion (Lines 472-466). We have extended this a little to cover the questions raised here.

How are those with non-binary gender identities handled in this article? If there is any data on the subject, I would be curious to know how this effects research score and funding success.

These data were either unavailable or the sample size was too small to be considered anonymously (Mentioned on Lines 74-76).

A limitation of the present article is a lack of data on major research-producing countries like China and the United States. Is there any data relevant to these or other countries? Is there reason to believe the findings outlined in this manuscript would apply or not apply to those countries also?

We would be very excited to see if the findings held up in other countries, particularly any that were less European based. Unfortunately we could not find any data to include. Maybe one day!

What are the motivations or other factors driving men to certain fields and women to certain fields over others? What are the active barriers preventing all fields from 50% gender parity?

Field choice is a highly studied area and the explanations are myriad we have included a few references in the discussion section on job choice. I usually recommend my students read the blog post at

https://www.scientificamerican.com/blog/hot-planet/the-people-who-could-have-done-science-didnt/

It is very thoughtful but unfortunately not appropriate to reference here.

The authors find very interesting data on funding rates. Have you considered funding rates and the size of funding awards as a factor in research score? Some disciplines like biomedical science receive larger grants than others like education.

A very interesting thought for our next piece of work. We would definitely like to explore our hypothesis further.

There are instances where the authors writing may perpetuate bias. If possible these should be avoided. One example is on line 458-459 where the authors state "...why these lower quality disciplines are more likely..." This could be re-written to emphasize that some disciplines are "perceived" as lower quality. Certainly those in these discipline would not characterize their chosen discipline as "low quality".

Well-spotted! Now corrected as you suggest.

Similar to the preceding comment, the authors should use care with the term "gender". In the datasets used, how many gender identities were captured? How many gender identity options were given in the surveys or data intake forms? Could individuals in these datasets have been misgendered? Do the data truly represent gender identity or biological sex?

We know that in the PBRF dataset gender was a binary choice and transgender individuals were able to choose which group they identified with. There was no non-binary option (in defence the latest dataset there is from 2018 and NZ has only recently started updating official forms to be more inclusive) and individuals with gender not-stated (a very small number) were excluded. ARC did mention that a small number of individuals were either non-binary or gender not stated, again these are not included here for reasons of anonymity. This is now mentioned on Lines 74-76. The effects on this group are important and understudied likely because, as here, the numbers are too small to be included meaningfully.

Reviewer #3 (Recommendations For The Authors):

Major revisions:

Could you add line numbers to the Supplementary Materials for the next submission?

Yes! Sorry for the omission.

(1) In the main text L146 and Figure 1, it is not clear why the expected model output line is for a 50 year old male from University of Canterbury only, but the data points are from disciplines in all eight universities in New Zealand. I think it would be more clear and informative to report the trend lines that represent the data points. At the moment it is hard to visualise how the results apply to other age groups or universities.

As age and institution are linear variables with no interactions they are only a constant adjustment above or below this line and the adjustment is small in comparison to the linear trend. Unfortunately, if they were included graphically they do not aid understanding. We agree that indluded raw data with an adjusted trend line can be confusing buy after a lor of between-author discussion this was the most informative compromise we could find (many people like raw data so we included it).

(2) Does your logistic regression model consider sample size weighting in pmen? Weighting according to sample sizes needs to be considered in your model. At the moment it is unclear and suggests a proportion between 0 and 1 only is used, with no weighting according to sample size. If using R, you can use glm(cbind(nFem, nMalFem).

Yes. All data points were weighted by group size exactly as you suggest. We have updated the text on Lines 317 to make this clear.

(3) For PBRF, I think it is useful to outline the 14 assessment panels and the disciplines they consider. Did you include the assessment panel as an explanatory variable in your model too to investigate whether quality is assessed in the same manner between panels? If not, then suggest reasons for not doing so.

We have now included more detail in main text on the gender split of the panels. They were not included as an explanatory variable. In theory there was some cross-referencing of panel scores to ensure consistency as part of the PBRF quality assurance guidelines.

(4) There are several limitations which should be discussed more openly:

Patterns only represent the countries studied, not necessarily academia worldwide.

Mentioned on Line 485-487.

Gender is described as a binary variable.

Discussed on Line 74-76.

The measure of research evaluation as a reflection of academic merit.

This is acknowledged in the data limitations paragraph in the discussion, at the end of the discussion

Minor revisions:

(1) L186. Why do you analyse bibliometric differences between individuals from University of Canterbury only? It would be helpful to outline your reasons.

Although bibliometric data is publicly available it is difficult to collect for a large number of individuals. You also need some private data to match bibliometrics with PBRF data which is anonymous. We were only able to do this for our own institution with considerable internal support.

(2) How many data records did you have to exclude in L191 because they could not be linked? This is helpful to know how efficient the process was, should anyone else like to conduct similar studies.

We matched over 80% of available records (384 individuals). We have mentioned this on Line 194.

(3) Check grammar in the sentence beginning in L202.

Thank-you. Corrected.

(4) Please provide a sample size gender breakdown for "University of Canterbury (UC) bibliometric data", as you do for the preceding section. A table format is helpful.

Included on Line 194.

(5) L377 I think this sentence needs revision.

Thank you, we have reworked that paragraph.

(6) L389-392 Is it possible evaluation panels can score women worse than men and that because more women are present in female-biassed disciplines, the research score in these are worse? Women scoring worse between fields, may be a result of some scaling to the mean score.

No.  This is not possible because women in male-dominated fields score higher.

(7) L393 Could you discuss explanations for why men outperform women in research evaluation scores more when disciplines are female dominated?

Unfortunately, we don’t have an explanation for this and can’t get one from our data. We hope it will be an interesting for future work.

(8) Could the figures be improved by having the crosses, x and + scaled, for example, in thickness corresponding to sample size? Alternatively, some description of the sample size variation? Sorting the rows by order of pmen in Table E1 would also be helpful for the reader.

As with the previous figure we have tried many ways of presenting it (including tis one). Unfortunately nothing helped.

We have provided Table E1 as a spreadsheet to allow readers to do this themselves.

(9) Please state in your methods section the software used to aid repeatability.

This is now in Supplementary Materials (Matlab 2022b).

(10) It is great to report your model findings into real terms for PBRF and ARC. Please can you extend this to CIHR and EIGE. i.e. describing how a gender skew increase of x associates with a y increase in funding success chance.

We have added similar explanations for both these datasets comparing the advantage of being male with the advantage of working in a male dominated discipline.

(11) I would apply care to using pronouns "his" and "her" in L322-L324 and avoid if at all possible, instead, replacing them with "men" and "women".

We have updated the text to avoid there pronouns in most places.

The article in general would benefit from a disclosure statement early on conceding that gender investigated here is only as a binary variable, discounting its spectrum.

See Line 74-76.

Please also report how gender balance is defined in the datasets as in the data summary in supplementary materials, within the main text.

Our definition of gender balance (proportion of researchers who are men, ) is given on Line 103.

(12) The data summary Table S1 could benefit from explaining the variables in the first column. It is currently unclear how granularity, size of dataset and quotas/pre-allocation? are defined.

These lines have been removed as they information they contained is included elsewhere in the table with far better explanations!

(13) There are only 4 data points for investigating covariation between gender balance and funding success in CIHR. This should be discussed as a limitation.

The small size of the dataset is now mentioned on Line 348.

(14) L455 "Research varies widely across disciplines" in terms of what?

This sentence has been extended

.

(15) L456 Maybe I am missing something but I don't understand the relevance of "Physicists' search for the grand unified theory" to research quality.

Removed.

(16) Can you provide more discussion into the results of your bibliographic analysis and Figure 2? An explanation into the relationships seen in the figure at least would be helpful.

Thank you we have clarified the relationships seen in each of figures 2A (Lines 226-235), 2B (Lines 236-252), and 2C (lines  260-268).

(17) It would be helpful to include in the discussion a few more sentences outlining:

- Potential future research that would help disentangle mechanisms behind the trends you find.

- How this research could be applied. Should there be some effort to standardise?

We have added a short paragraph to the discussion about implications/applications, and future research (Lines 481-484).

(18) The introduction could benefit from discussing and explaining their a priori hypotheses for how research from female-biassed disciplines may be evaluated differently.

While not discussed in the introduction, possible explanations for why and how research in female dominated fields might be evaluated differently are explored in some detail in the Discussion.  We think once is enough, and towards the end is more effective than at the beginning.

(19) L16 "Our work builds on others' findings that women's work is valued less, regardless of who performs that work." I find this confusing because in your model, there is a significant interaction effect between gender:pmen. This suggests that for female-biassed disciplines, there is even more of a devaluation for women, which I think your lines in figure 1 suggest.

Correct but men are still affected, so the sentence is correct.  What is confusing is that the finding is counter to what we might expect.

Author response:

eLife assessment

This fundamental study provides a near-comprehensive anatomical description and annotation of neurons in a male Drosophila ventral nerve cord, based on large-scale circuit reconstruction from electron microscopy. This connectome resource will be of substantial interest to neuroscientists interested in sensorimotor control, neural development, and analysis of brain connectivity. However, although the evidence is extensive and compelling, the presentation of results in this very large manuscript lacks clarity and concision.

We thank the reviewers for their detailed and thoughtful feedback and the time that they invested to provide it. Organising this manuscript (which is clearly not a standard research article) was quite challenging as it had to fulfil a number of functions: presenting a guide to the system of annotations and the associated online resources; providing an atlas for the annotated cell types; and showcasing various analyses to illustrate the value of the dataset as well as just a few of the many questions it can be used to address. We gave careful consideration to its structure and attempted to signpost the sections that would be most useful to particular types of readers. Nevertheless we can see that this was not completely successful and we thank the reviewers for their suggestions for improvement.

We acknowledge that the resulting manuscript was very large and will endeavour to streamline our text in the revision without compromising the accessibility of the data. We do note that there is some precedent for comprehensive and lengthy connectome papers going all the way back to White et al. 1986 which took 340 pages to describe the 302 neurons of the C. elegans connectome. More recently, we can compare the “hemibrain papers” published in eLife: Scheffer et al., 2020, Li et al., 2020, Schlegel et al., 2021, Hulse et al., 2021. These papers would also be difficult to digest at a single sitting but were game-changing for the Drosophila neuroscience field and have already been cited hundreds of times, a testament to their utility. In the same way that these papers provided the first comprehensively proofread and annotated EM connectome for (a large part of) the adult fly brain, our work now provides the first fully proofread and annotated EM connectome for the nerve cord. Given the pioneering nature of this dataset we feel that the lengthy but highly structured atlas sections of the paper are justified and will prove impactful in the long term.

Whilst no EM dataset is perfect, we have endeavoured to make this one as comprehensive as possible. We found 74.4 million postsynapses and 15,765 neurons of VNC origin, all of which have been carefully proofread, reviewed, annotated and typed. For comparison, the female adult nerve cord dataset (FANC, Azevedo et al., Nature, 2024) contains roughly 45 million synapses and 14,600 neuronal cell bodies of which at the time of writing 5576 have received preliminary proofreading and 222 high quality proofreading. We emphasise that these are highly complementary datasets, given the difference in sex and the fact that each dataset has different artefacts (MANC has poorer preservation of neurons in the leg nerves; FANC is missing part of the abdominal ganglion and has lower synapse recovery). We reconstructed 5484 sensory neurons from the thoracic nerves, 84% of the ~6500 estimated from FANC. The overall recovery rate was ~86.5% if we include the ~1100 sensory neurons from abdominal nerves, which were in excellent condition.

Reviewer #1 (Public Review):

Summary:

The authors present a close to complete annotation of the male Drosophila ventral nerve cord, a critical part of the fly's central nervous system.

Strengths:

The manuscript describes an enormous amount of work that takes the first steps towards presenting and comprehending the complexity and organization of the ventral nerve cord. The analysis is thorough and complete. It also makes the effort to connect this EM-centric view of the nervous system to more classical analyses, such as the previously defined hemilineages, that also describe the organization of the fly nervous system. There are many, many insights that come from this work that will be valuable to the field for the foreseeable future.

We thank the reviewer for acknowledging the enormous collaborative effort represented by this manuscript. We tried to synthesise decades of light-level work by neuroscientists and developmental biologists working in Drosophila and other insects in order to create a standard, systematic nomenclature for >22,000 neurons, most of which had not been typed at light level. We hope that the MANC dataset and this guide to its contents will prove to be useful resources to Drosophila neurobiologists and the wider neuroscience field.

Weaknesses:

With more than 60 primary figures, the paper is overwhelming and cannot be read and digested in a single sitting. The result is more like a detailed resource rather than a typical research paper.

In writing this paper, we had two aims: first, to describe and validate our extensive biological annotation of the connectome and second, to provide interesting illustrative examples of the many analyses that could be carried out on this dataset using the atlas we generated. The resulting paper is intended primarily as a detailed reference rather than a typical research paper. At the end of the Introduction, we outline the structure of the paper and explicitly direct non-specialist readers to focus on the initial and concluding sections for orientation to the dataset so that they would not get bogged down in the details. We will review our section organisation and headings to try to make the paper more straightforward to navigate, and we will add specific figure numbers to the outline.

Reviewer #2 (Public Review):

Summary and strengths:

This massive paper describes the identity and connectivity of neurons reconstructed from a volumetric EM image volume of the ventral nerve cord (VNC) of a male fruit fly. The segmentation of the EM data was described in one companion paper; the classification of the neurons entering the VNC from the brain (descending neurons or DNs) and the motor neurons leaving the VNC was described in a second companion paper. Here, the authors describe a system for annotating the remaining neurons in the VNC, which include intrinsic neurons, ascending neurons, and sensory neurons, representing the vast majority of neurons in the dataset. Another fundamental contribution of this paper is the identification of the developmental origins (hemilineage) of each intrinsic neuron in the VNC. These comprehensive hemilineage annotations can be used to understand the relationship between development and circuit structure, provide insight into neurotransmitter identity, and facilitate comparisons across insect species.Many sensory neurons are also annotated by comparison to past literature. Overall, defining and applying this annotation system provides the field with a standard nomenclature and resource for future studies of VNC anatomy, connectivity, and development. This is a monumental effort that will fundamentally transform the field of Drosophila neuroscience and provide a roadmap for similar connectomic studies in other organisms.

We thank the reviewer for acknowledging the enormous collaborative effort represented by this manuscript. We tried to synthesise decades of light-level work by neuroscientists and developmental biologists working in Drosophila and other insects in order to create a standard, systematic nomenclature for >22,000 neurons, most of which had not been typed at light level. We hope that the MANC dataset and this guide to its contents will prove to be useful resources to Drosophila neurobiologists and the wider neuroscience field.

Weaknesses:

Despite the significant merit of these contributions, the manuscript is challenging to read and comprehend. In some places, it seems to be attempting to comprehensively document everything the authors found in this immense dataset. In other places, there are gaps in scholarship and analysis. As it is currently constructed, I worry that the manuscript will intimidate general readers looking for an entry point to the system, and ostracize specialized readers who are unable to use the paper as a comprehensive reference due to its confusing organization.

In writing this paper, we had two aims: first, to describe and validate our extensive biological annotation of the connectome and second, to provide interesting illustrative examples of the many analyses that could be carried out on this dataset using the atlas we generated. The resulting paper is intended primarily as a detailed reference rather than a typical research paper. At the end of the Introduction, we outline the structure of the paper and explicitly direct non-specialist readers to focus on the initial and concluding sections for orientation to the dataset so that they would not get bogged down in the details. We will review our section organisation and headings to try to make the paper more straightforward to navigate, and we will add specific figure numbers to the outline.

The bulk of the 559 pages of the submitted paper is taken up by a set of dashboard figures for each of ~40 hemilineages. Formatting the paper as an eLife publication will certainly help condense these supplemental figures into a more manageable format, but 68 primary figures will remain, and many of these also lack quality and clarity. Without articulating a clear function for each plot, it is hard to know what the authors missed or chose not to show. As an example, many of the axis labels indicate the hemilineage of a group of neurons, but are ordered haphazardly and so small as to be illegible; if the hemilineage name is too small, and in a bespoke order for that data, then is the reader meant to ignore the specific hemilineage labels?

We will contact eLife professional editing staff to determine whether the paper can be streamlined by moving more material to supplemental without making it difficult to locate the detailed catalogues of neurons that will be of interest to specialist readers. Based on the typical eLife format, we suspect that retaining the dashboard main figures for each hemilineage will be necessary to maintain its utility as a reference. We will, however, shorten the associated main text by, for example, moving background material used to assign the hemilineages to the Methods section and moving specific results to the figure legends where possible.

We articulated the function for each plot as follows: "Below we describe in more depth every hemilineage that produces more than one or two secondary neurons. For each of these 35 hemilineages, we show (A) the overall morphology of the secondary population, (B) representative individual neurons (as estimated by highest average NBLAST score to other members of the hemilineage), and (C) specific notable examples (which in some cases are primary). We then report (D) the locations of their connectors (postsynapses and presynapses), (E) their upstream and downstream partners by class, and (F) their upstream and downstream partners by finer subdivisions corresponding to their systematic types (secondary hemilineage, target, or sensory modality). We also provide supplementary figures showing the morphology and normalised up- and downstream connectivity of all systematic types for each hemilineage."

We have plotted every secondary neuron in each hemilineage, every predicted synapse for those neurons with confidence >0.5, every connection to partner neurons by class (no threshold applied), and then the same information organised by hemilineage in a heatmap (and including partners from all birthtimes and partners of unknown hemilineage). Then the supplementary figures show all connectivity, organised in the same way, for every individual cell type assigned to the hemilineage, including both primary and early secondary neurons. We will add more detail to the figure legends to clarify these points.

We apologise that you were unable to read some of the axis labels in the review copy of the manuscript; we did submit high resolution versions of the figures as a supplemental file, but perhaps this did not reach you; they can also be found at https://www.biorxiv.org/content/10.1101/2023.06.05.543407v2.supplementary-material. The hemilineages are in a conserved (alphanumerical) order for all hemilineage-specific plots and many others. The exceptions arise when neurons are clustered based on their connectivity to hemilineages, in which case the order of the labels necessarily follows the structure of the resulting clusters.

The text has similar problems of emphasis. It is often meandering and repetitive. Overlapping information is found in multiple places, which causes the paper to be much longer than it needs to be. For example, the concept of hemilineages is introduced three times before the subtitle "Introduction to hemilineage-based organisation". When cell typing is introduced, it is unclear how this relates to serial motif, hemilineage, etc; "Secondary hemilineages" follow the Cell typing title. Like the overwhelming number of graphical elements, this gives the impression that little attention has been paid to curating and editing the text. It is unclear whether the authors intend for the paper to be read linearly or used as a reference. In addition, descriptions of the naming system are often followed by extensive caveats and exceptions, giving the impression that the system is not airtight and possibly fluid. At many points, the text vacillates between careful consideration of the dataset's limitations and overly grandiose claims. These presentation flaws overshadow the paper's fundamental contribution of describing a reasonable and useful cell-typing system and placing intrinsic neurons within this framework.

Because we intended this paper to be read primarily as a reference, we tried to make each section stand on its own, which we agree resulted in some redundancy (with more details appearing where relevant). However, we will do our best to tighten the text for the version of record.

Our description immediately under the Cell typing title includes the use of hemilineage, serial (not serial motif, which was not used), and laterality (left-right homologues) in the procedure to assign cell types. We will change this to “Cell typing of intrinsic, ascending, and efferent neurons” for clarity. The “Secondary hemilineages” title marks the start of a new section that serves as a reference for each of the secondary hemilineages; we will change this to “Secondary hemilineage catalogue” or similar for clarity.

References to past Drosophila literature are inconsistent and references to work from other insects are generally not included; for example, the extensive past work on leg sensory neurons in locusts, cockroaches, and stick insects. Such omissions are understandable in a situation where brevity is paramount. However, this paper adopts a comprehensive and authoritative tone that gives the reader an impression of completeness that does not hold up under careful scrutiny.

We did not attempt to review the sensory neuron literature in this manuscript but rather cited those specific papers which included the axon morphology data that informed our modality, peripheral origin, and cell type assignments. Most of these came from the Drosophila literature due to the availability of genetic tools used for sparse labelling of specific populations as well as the greatly increased likelihood of conserved morphology. However we certainly agree that decades of sensory neuron work in larger insects were foundational for this subfield and will add a sentence to this effect in the introduction to our sensory neuron typing.

The paper accompanies the release of the MANC dataset (EM images, segmentation, annotations) through a web browser-based tool: clio.janelia.org. The paper would be improved by distilling it down to its core elements, and then encouraging readers to explore the dataset through this interactive interface. Streamlining the paper by removing extraneous and incomplete analyses would provide the reader with a conceptual or practical framework on which to base their own queries of the connectome.

We certainly hope that this paper will encourage readers to explore the MANC dataset. Indeed, as we state in the Discussion, "Moreover, its ultimate utility depends on how widely it is leveraged in the future experimental and computational work of the entire neuroscience community. We have only revealed the tip of the iceberg in this report, with a wealth of opportunities now available in this publicly available dataset for forthcoming connectomic analyses that will feed into testable functional hypotheses." In the first few sections of the Results, we include a visual introduction to annotated features, a glossary of annotation terms, a visual guide to our cell typing nomenclature, and two video tutorials on the use of Clio Neuroglancer to query the dataset. To further encourage exploration, we have also included illustrative examples of just a few of the many analyses that can now be performed with this comprehensive and publicly available dataset.

Author response:

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

Reviewer #1 (Public Review): 

Q1: First of all, the term organoid must be discarded. The authors just seed the endometrial cell mixture which assembles and aggregates into a 3D structure which is then immediately used for analysis. Organoids grow from tissue stem cells and must be passage-able (see their own description in lines 69-71). So, the term organoid must be removed everywhere, to not confuse the organoid field. It is not shown that the whole 3D assembly is passageable, which would be very surprising given the fact that immune and stromal cells do not grow in Matrigel because of the unfavorable growing conditions (which are targeted to epithelial cell growth).

We appreciate for your highlighting concerns regarding our organoid construction.

(1) The organoids in our system were originated from tissue stem cells.

We induced adult stem cells derived from endometrial tissue to construct organoids in vitro by various small molecules (such as Noggin, EGF, FGF2, WNT-3A and R-Spondin1), which involves a complex self-assembly process rather than a mere cellular assembly. Initially, there are single cells and small cell clusters in the system two days after the planting. On the fourth day, the glandular epithelial cells gradually assembled to glands, while the stromal cells spontaneously organized themselves around the glands.  On the eleventh day, the endometrial glands enlarged, epithelial cells organized in a paving stone arrangement, and stromal cells established an extensive network. (Author response image1) (Figure 1C)

(2) The organoids we constructed are passage-able.  

Most organoids were used for experiments up to the fifth generation, while some are extended to the 10th generation and cryopreserved. (Response Figure 1B, C)

(3) Immune and stromal cells are present in our system from the primary to the fourth generation. In our study, immune and stromal cells were identified not only from scRNA-seq data (third generation of organoids) (Figure 2A), but also from the morphology using 3D transparent staining and light sheet microscopy imaging (third generation of organoids), with Vimentin marking stromal cells, CD45 designating immune cells, and FOXA2 identifying glands. Further, flow cytometric analysis was applied to verify immune cells within the organoids (third generation of organoids). (Response Figure 1D, E, F)  

Moreover, Immune cells and stromal cells can grow in Matrigel, which was also found in the study of organoid pioneer Hans Clevers (Hans Clevers et al., Nature Reviews Immunology 2019).

Author response image 1.

(A) The growth condition of endometrial cells was observed from day2 to day11 after plating under an inverted microscope. Scale bar = 200 μm. (B) The endometrial organoids of different passages were observed from P1 to P5. Scale bar = 200 μm. (C) Stromal cells formed an extensive network (down). The arrowhead indicates dendritic stromal cells. Scale bar = 100 μm (left), Scale bar = 50 μm (right). (D) Exhibition of stromal cells marked by vimentin. Nuclei were counterstained with DAPI. The arrow indicates stromal cells. Scale bar = 40 μm (up), Scale bar = 30 μm (down). (E)Exhibition of immune cells marked by CD45 and endometrial gland marked by FOXA2. Nuclei were counterstained with DAPI. The arrow indicates immune cells. Scale bar = 50 μm. (F) Flow cytometric analysis of T cells and macrophages in the endometrial organoid. Gating strategy used for determining white blood cells (CD45+ cells), T cells (CD45+CD3+ cells) and macrophages (CD45+CD68+CD11b+ cells).

Q2: Second, the study remains fully descriptive, bombing the reader with a mass of bioinformatic analyses without clear descriptions and take-home messages. The paper is very dense, meaning readers may give up. Moreover, functional validation, except for morphological and immunostaining analyses (which are posed as "functional" but actually are only again expression) is missing, such as in vivo functionality (after transplantation e.g.) and embryo interaction. Importantly, the 3D structure misses the right architecture with a lining luminal epithelium which is present in the receptive endometrium in vivo and needed as the first contact site with the embryo. So, in contrast to what the authors claim, this is not the best model to study embryo interaction, or the closest model to the in vivo state (line 318, line 326).

Thank you.

(1) We have made the following improvements. Firstly, we have conducted additional experiments to validate the bioinformatics analysis. Secondly, the structure of the manuscript has been refined to ensure logical coherence and clear transitions between paragraphs. Thirdly, important findings have been emphasized to ensure readers’ comprehension and inspiration. Furthermore, the manuscript was revised by both domestic and international experts to enhance the readability and clarity.

(2)  For the functional validation, in vivo transfer could not be carried out so far due to ethical limitation. But human embryos are able to develop and grow more efficiently in combining with the receptive endometrial organoids we generated (unpublished data).

(3) As you suggested, we replaced the “closest” with “closer”. It is undeniable that the model cannot completely simulate the in vivo implantation process that the luminal epithelium of the endometrium contacts the embryo first.  

Q3: Third, receptive endometrial organoids (assembloids; Rawlings et al., eLife 2021) and receptive organoid-derived "open-faced endometrial layer" (Kagawa et al., Nature 2022) have already been described, which is in contrast to what the authors claim in several places that "they are the first" (e.g. lines 87-88, 316-319, etc). These studies used real organoids to achieve their model (and even showed embryo interaction), while in the present study, different cell types are just seeded and assembled. Hence, logically, immune cells are present which are never found in real organoid models. The only original aspect in the present study is the use of hormones to enhance the WOI phenotype. However, crucial information on this original aspect is missing such as concentration of the hormones, refreshment schedule, all 3 hormones added together or separately, and all 3 required?

Thank you for pointing out these researches referring to endometrial organoids.

(1) While we didn’t explicitly state "the first", we should be careful to use the expressions similar to "the first". It has been changed to a gentle and modest expression, as follows “we are far from understanding how embryo implantation occurs during the WOI due to ethical limitations and fewer in vitro receptive endometrial model” and “which confirms that they are closer to the in vivo state”.

(2) The definition of organoids and the existence of immune cells have been detailed addressed in the first question.

(3) In terms of hormone scheme, hormone concentrations have been detailed in Table S2 of Supplementary. Estrogen was supplemented to the basal medium for the initial two days, after which a combination treatment of MPA, cAMP, PRL, hPL, and HCG was administered for the subsequent six days. The medium was refreshed every two days.

All three hormones were deemed necessary, which was validated by multiple group comparisons. Only the organoids treated with all six hormones together exhibited an endometrial receptivityrelated gene expression profile. (Author response image 2).

Author response image 2.

Heatmap showing receptivity related gene expression profile of organoids in each hormone regimen.  

Q4: Moreover, it is not a "robust" model at all as the authors claim, given the variability of the initial cell mixture (varying from patient to patient). Actually, the reproducibility is not shown. The proportions of the different cell types seeded in the Matrigel droplet will be different with every endometrial biopsy. It would be much better to recombine epithelial (passageable) organoids with stromal and immune cells in a quantified, standardized manner to establish a "robust" model.

Thanks for your suggestion.  

Firstly, the constructed endometrial organoids generally consist of epithelial, stromal, and immune cells. However, it is undeniable that the cell proportions may vary slightly among different patients. Secondly, the term "robust" is intended to convey strong support for embryo development, which will be supported by our next study (unpublished data). Therefore, robust is replaced here as alternative. Thirdly, as for "reproducibility", the hormone-treated organoids from different women exhibited similarity to the in vivo receptive endometrium through multi-omics analysis, ERT, and various other experiments.  

Reviewer #2 (Public Review):

Q1: With endometrial receptivity analysis, they suggest a successful formation of the implantation window in vitro, but this result is difficult to interpret.

Thanks for your question.  

We understand that the most effective way to demonstrate endometrial receptivity is embryo implantation, which was conducted simultaneously and will be presented in our next study. In this study, we validated the receptivity based on the current researches.

(1) At the single-cell transcriptome level, the cellular composition and function of the receptive endometrial organoids were similar to those of the in vivo implantation window (Stephen R. Quake et al, 2020).

(2) At the whole organoids level, the receptive endometrial organoids exhibited the similar characteristics in transcriptome and proteome to the in vivo mid-secretory endometrium (Andres Salumets 2017, Qi Yu 2018, Triin Laisk 2018, Edson Guimarães Lo Turco 2018, Xiaoyan Chen 2020, Francisco Domínguez 2020, DavidW. Greening 2021, Norihiro Sugino 2023). The receptive endometrial organoids were also validated by endometrial receptivity test (ERT), which utilized high-throughput sequencing and machine learning to assess endometrial receptivity (Yanping Li et al., 2021).  

(3) At the microstructural level under electron microscope, the receptive endometrial organoids exhibited characteristics of the implantation window, such as pinopodes, glycogen particles, microvilli, and cilia.

Overall, the receptive organoids we constructed closely resemble the in vivo implantation window at the single-cell, organoids, and microstructural levels based on existing researches.

Q2: Analyzing transcriptome and proteome information of WOI organoids, authors demonstrate a strong response to estrogen and progesterone, but some comparisons are made with CTRL and SEC, and others only with CTRL, which limits the power of some results. In the same way, some genes related to Cilia and pinopodes appear dominant in WOI organoids, but the comparison by electron microscopy is made only against CTRL organoids.  

In subsequent analysis, WOI organoids showed a marked differentiation from proliferative to secretory epithelium, and from proliferative epithelium to EMT-derived stromal cells than SEC organoids. These statements are based on their upregulation of monocarboxylic acid and lipid metabolism, their enhanced peptide metabolism and mitochondrial energy metabolism, or their pseudotime trajectories. However, other analyses (such as the accumulation of secretory epithelium or decreased proliferative epithelium, the increased ciliated epithelium after hormonal treatment, or the presence of EMT-derived stromal cells) show only small differences between SEC and WOI organoids.

Thank you for raising these important questions.

(1) At the organoid level, the differences in transcriptome and proteome between SEC and WOI organoids are not significant. This is understandable because WOI organoids are further induced towards the implantation window based on the secretory phase (i.e. SEC organoids), and both are similar at the overall organoid level.  

(2) At the single-cell level, the accumulation of secretory epithelium, decreased proliferative epithelium, increased ciliated epithelium post hormonal treatment, or the presence of EMTderived stromal cells are the fundamental features of the secretory endometrium. Therefore, these features are present in both WOI and SEC organoids. However, the most notable differences lie in the more comprehensive differentiation and varied cellular functions exhibited by WOI organoids compared to SEC organoids.

(3) Regarding electron microscopy, we have now quantitatively compared the presence of various characteristic structures such as microvilli, cilia, pinopodes and glycogen in the CTRL, SEC and WOI groups. It has been observed that WOI organoids possess longer microvilli and increased cilia, glycogen, and pinopodes compared to SEC organoids (Fig2H).

Reviewer #1 (Recommendations For The Authors):

Q1: Several of the key methods are performed by companies, hence not in detail described and therefore not verifiable which is essential for reviewers and readers.

We are grateful for the suggestion. Specific methods have now been incorporated into the "Supporting Information" section. (Line91~102, Line 107~123, Line 132~139)

Q2 - Line 49: It is not shown in the present study whether the WOI organoids are a 'robust' platform.

- Line 76: There is a study (Dolat L., Valdivia RH., Journal of Cell Science, 2021) that developed a co-culture with endometrial organoids and immune cells (neutrophils) which should be mentioned.:

We have reweighed the word and now replace 'robust' with 'alternative' (Line 54).  We have considered the reviewer's suggestion and added this citation (Line 82-83) about the cocultivation of immune cells with endothelial organoids, which was not previously cited mainly because the research model was mouse.

Q3: Figure 1: Endometrial organoids possess endometrial morphology and function. - The authors should further explain their decision to add PRL, hCG, and hPL to the organoid culture. Why these particular compounds? What is their specific role during the WOI?

In terms of hormone scheme, estrogen and progesterone promote the transition of endometrial organoids into the secretory phase, and on this basis, pregnancy hormones can further promote their differentiation. PRL promotes immune regulation and angiogenesis during implantation, HCG improves endometrial thickness and receptivity, and HPL promotes the development and function of endometrial glands. Our constructed WOI organoid is in a state conducive to embryo implantation. We aim to develop an in vitro model for embryo implantation study. The detailed explanation of this aspect was initially provided in the Discussion section (Lines 298–313). To enhance the clarity for reviewers and readers regarding the selection of the hormonal regimen, we have now articulated it in the Results section (Lines 124–130).

When selecting hormone formulations, multiple group comparisons were made. It was found that the number, area, and average intensity of organoids in these groups were similar over time. But the WOI organoids showed endometrial receptivity related gene expression profile, which highly expressed genes positively correlated with endometrial receptivity, and lowly expressed genes negatively correlated with receptivity, compared to the other hormone formulations (added to Figure S1E, S1F). Hormone dosage was primarily based on peri-pregnant maternal body or localized endometrium levels (Margherita Y. Turco et al., Nature Cell Biology 2017).

-  Line 108: "the endometrial cells" instead of "endometrial organoid"? Because the authors also refer to the stromal cells.

You should be referring to this sentence “The endometrial organoid, consisting of vesicle-like glands, fibrous stromal cells, and other surrounding cells, developed into a 3D structure with the support of Matrigel”. Organoid, a self-assembled 3D structure, consists of multiple cells and closely resembles in vivo tissue or organ. It offers high expansibility, phenotypic, and functional properties. Here, we aim to delineate the endometrial organoid, comprising epithelial cells, stromal cells, and other cellular components that assemble to form intricate 3D structures. Hence, the term "endometrial organoid" is more appropriate.

-  Line 110: "the endometrial glands", do the authors mean the endometrial organoids? The authors also mention they enlarge, which must be quantified.

You should be referring to this sentence “As the organoids grew and differentiated, the endometrial glands enlarged, epithelial cells adopted a paving stone arrangement, and stromal cells formed an extensive network”. Here, we mean the “endometrial glands” grow progressively in the organoids. We agree with your suggestion to quantify the change of organoids’ area over time, and found that they increased progressively in all three groups (shown as follows) (Fig.S1E) (Line130-131) 

Author response image 3.

The dynamic changes of the area of organoids over time in the CTRL, SEC and WOI organoids.

-  Line 112: E-cadherin is a general epithelial marker, not a glandular marker.

We agree with your suggestion and now change to ‘The epithelium marker E-cadherin’ (Line110).

-  Line 116: Which group was used for KI67 and CC3 staining?

The CTRL organoids were used for Ki67 and CC3 staining. We have modified this expression in the Figure 1E Legend.

-  Line 123: Organoid size (diameter or area) needs to be quantified to claim that WOI organoids grow slower than SEC/CTRL organoids. The same goes for Ki67+ cells for proliferation. In the legend of Fig 1B, the authors in contrast state that the organoids show a similar growth pattern.

We are extremely grateful to you for pointing out this problem. We quantitatively analyzed the size of organoids in the three groups. The area was found to be increasing over time, with the three groups growing the most vigorously in the CTRL group, followed by the SEC group and the WOI group, but the differences were not statistically significant. Relevant results have been added to Figure S1E (Line130-131). There were no significant differences in Ki67 expression of these organoids. Therefore, the three groups of organoids showed a similar growth pattern. We decided to delete the statement “Following hormonal stimulation, WOI organoids exhibited slower growth than SEC and CTRL organoids, while CTRL organoids maintained robust proliferative activity (Fig. 1B)”.

Author response image 4.

The dynamic changes of the area of organoids over time in the CTRL, SEC and WOI organoids.

-  Line 126: Fourteen days of organoid treatment is a very long time. Growing organoids may already be dying which should be checked by CC3 staining to prove that organoids are still fully viable.

Endometrial organoids are vigorous in proliferation and have a long survival period due to the presence of adult stem cells. To address your queries effectively, we conducted CC3 staining on the organoids treated for 14 days, revealing negligible expression levels (shown as below).

Author response image 5.

Figure note: The Ki67 and CC3 immunostaining on the organoids after 14-day hormone treatment.

-  Line 128: Changes in hormone receptors should be supported by RT-qPCR data to be more convincing

We agree with your suggestion. Here we supplemented the RT-PCR results of hormone receptors as follows (Figure S1D) (Line119-121). PAEP and PGR are associated with progesterone, and OLFM4 and EGR1 are associated with estrogen.

-  1A: Are authors able to see and characterize decidualized stromal cells as indicated in the illustration?

Upon the reviewer's inquiry, we carefully observed the morphology of stromal cells in hormone-treated organoids. Regrettably, the morphology of decidualized stromal cells was not ascertainable through light microscopy in our endometrial organoids.

-  1C: Which treatment condition are the organoids in these images?

This figure showed the bright-field morphology of the CTRL organoids, which is now noted in the Figure 1C legend.

-  1D: PAS staining should be quantified to support the claims.

We agree with your suggestion. The quantitative comparison of PAS staining was conducted in these three groups of organoids (Figure S1G) (Line142-143)

-  1D: Where are the stromal cells in the model? There should be vimentin-positive cells outside of the glands.

The figure 1D illustrates the outcomes of section staining, which owned limitation to displaying stromal cells around the gland. Considering the 3D structure of organoids, we conducted organoid clearing and staining, and observed stromal cells (marked by Vimentin) under light sheet microscope (shown as below). The stromal cells were also presented using this method in the original Figure 2B.

Author response image 6.

Exhibition of stromal cell marked by vimentin of CTRL organoid through whole-mount clearing, immunostaining and light sheet microscopy imaging. Nuclei were counterstained with DAPI. The arrowhead indicates stromal cells. Scale bar = 70 μm.

Figure 2: Developing receptive endometrial organoids in vitro mimicking the implantation window endometrium.

-  Line 142: CD44 is not an exclusive marker for immune cells. It has been shown to be expressed in glandular secretory epithelial cells (Fonseca et al., 2023). The authors also mention that CD44 is expressed in stromal cells (line 265). Staining for CD45 (or another immune-specific marker) is needed to demonstrate the presence of immune cells. 

We appreciated your suggestions. We demonstrated the distribution of immune cells in organoids using the organoid clearing technique in combination with light-sheet microscopy imaging, using CD45 as a marker (Figure 2C).

-  Line 144: What are the proportions of the immune cells? What is the variation between patient samples?

We assessed the proportion of immune cells with the help of flow cytometry and analyzed the proportion of Macrophages and T cells in organoids derived from 8 patients. The proportion of WBC in organoids was about 3%~4% (Figure 2D), among which macrophages were less than 1% and T cells less than 2% (Figure S2E). There existed a very few patients with large heterogeneity, and the proportion of immune cells in most patients was

relatively stable.

-  Line 161: What is the endometrial receptivity test (ERT)? Not explained at all.

Endometrial Receptivity Test (ERT) is a kind of gene analysis-based method for detecting endometrial receptivity, which combines high-throughput sequencing and machine learning to analyze the expression of endometrial receptivity-related genes, allowing for a relatively accurate assessment of endometrial receptivity. It is currently used in clinical practice to determine endometrial receptivity and guide personalized embryo transfer (Yanping Li et al., J Transl Med 2021). (line179-183)

-  2A: The authors' dataset is compared to a published dataset. How were they combined? Were they merged, mapped on each other, or integrated? Were all cells employed from the published dataset or specific cell types? Much detail to evaluate the analysis is missing.

We are very grateful for your comments.  

(1) The four raw datasets (CTRL, SEC and WOI organoids, and mid-secretory endometrium) underwent batch correction and integration using Harmony. Subsequently, the integrated dataset underwent dimensionality reduction via  PCA. The soft k-means clustering algorithm was employed to address batch effects and clustering, utilizing a clustering parameter resolution of 0.5. Finally, the clustering results were visualized using tSNE based on the cell subpopulation classification. (“Methods” Line164-175)

(2) The Figure 2A displayed comparison of glandular and luminal epithelium, secretory epithelium, LGR5 epithelium, EMT-derived stromal cells, ciliated epithelium, and glandular secretory epithelium (shown as Figure S2C~S2D) (Line150-154)

- 2E: Please add the cell type names above the heatmaps to improve readability.

Thanks to your suggestion, we have added the cell type names above the heatmaps.

- 2G: The difference between the left and right graphs is not clear from the figure itself. Improve by adding a title and more explanation.

Thanks for your careful review. We have added the title to the left and right graphs.

Supplementary Figure 3 is referenced with Figure 2. Supplementary Figure 2 is referenced with Figure 3. The order needs to be changed.

Thanks for your careful review. We have changed the order.

- S3B: Typical markers for annotation of the different cell clusters are not included and therefore it is not convincing enough that annotations are correct. E.g. Epithelial markers (EPCAM, CDH1), Stromal cells (VIM, PDGFRA), SOX9+LGR5+ cells (SOX9, LGR5). How were the EMT-derived stromal cells designated? It is not clear from the data whether they are in fact EMT-derived or whether they show epithelial markers as well (stated in line 246).

We deeply appreciate your suggestion. We provided more details to describe the cell clustering as the following. Single-cell transcriptomics analysis referred to CellMarker, PanglaoDB, Human Cell Atlas, Human Cell Landscape, and scRNASeqDB, and previous endometrium related studies. (W. Wang et al., Nat Med 2020, P. D. Harriet C. Fitzgerald et al., PNAS 2019, K. M. Thomas, M Rawlings et al., eLife 2021, L. Garcia-Alonso et al., Nat Genet 2021) 

(1) SOX9+LGR5+ cells: SOX9 and LGR5 are both proliferative markers. SOX9 is expressed in all clusters dispersedly. LGR5 is mainly expressed in two clusters, one of which is stem derived epithelium, and the other cluster expresses LGR5 in a scattered manner. Refer to the markers of SOX9+LGR5+ cells, SOX9+LGR5- cells, and SOX9+ proliferative cells in 2021 Nature Genetics (L. Garcia-Alonso et al., Nat Genet 2021), the cells in this cluster expressed high levels of NUAK2, CNKSR3, FOS and LIF, which was consistent with the expression profiles of SOX9+LGR5+ cells and SOX9+ proliferative cells. However, considering that the number of cells expressing LGR5 was relatively small, this cluster of cells was renamed SOX9+ proliferative epithelium.

Figure 3: Receptive endometrial organoids recapitulate WOI-associated biological characteristics. - Line 173-174: The WOI organoids should be compared in detail to the SEC organoids in addition to the CTRL organoids, to show that this WOI model and new hormonal treatment is providing better results compared to the SEC organoids and the results obtained in previous studies.

Thanks for your suggestion. At the organoid level, the differences in transcriptome and proteome between SEC and WOI organoids are not significant. This is understandable because WOI organoids are further induced towards the implantation window based on the secretory phase (i.e. SEC organoids), which prompted us to continue exploring at the single-cell level.

- Line 190: Quantification of pinopodes is required to claim that they are more densely arranged in WOI organoids. 

- Line 190-191: Again, is there a difference in pinopode presence between the WOI and SEC organoids to show that the WOI organoids are really distinct and a better model?

We agree with the reviewer’s suggestion and quantified the pinopodes. The CTRL, SEC and WOI organoids were found to have increasing numbers of pinopodes, with WOI organoid owning the most abundant pinopodes under electron microscope. (Figure 2H) (Line184-186)

- Line 194: Also here, quantification of the glycogen particles is missing.

We agree with your suggestion. We have quantified the area of glycogen particles under electron microscope in the CTRL, SEC and WOI organoids. It was found that WOI organoid had the most glycogen particles. (Figure 2H) (Line184-186)

- 3C: There is no difference between SEC and WOI organoids condition for OLFM4 and PRA/B. What is the purpose then of adding extra hormones if no difference is present?

The figure 3C indicated that there was no significant difference in OLFM4 and PRA/B level (reflecting estrogen and progesterone responsiveness) in SEC and WOI organoids at the organoids level. It is understandable because WOI organoids are induced further into the implantation window on the basis of the secretory phase (i.e., SEC organoids), and both are similar at the overall level of organoids. Based on this, we further explored the differences between WOI organoids and SEC organoids at the single-cell level.

- 3G: A higher magnification is necessary to evaluate cilia staining. From these images, it seems like CTRL organoids also express acetyl-a-tubulin.

Thanks for your suggestion. The figure has been enlarged and shown as below. The acetyl-a-tubulin of WOI organoids is different from that of CTRL organoids in morphology and expression level. The glands of WOI organoids have small green tips (expressing acetyl-α-tubulin) convex toward the lumen. WOI organoids expressed higher level of acetyl-α-tubulin than CTRL organoids. (Now replaced with Figure 3G in the revised draft).

Figure 4: Structural cells construct WOI with functionally dynamic changes

- Line 211: To which figure are these claims referring to?

You should be referring to this sentence “In terms of energy metabolism, the WOI organoids exhibited upregulation of monocarboxylic acid and lipid metabolism, and hypoxia response”. Up-regulation of monocarboxylic acid and lipid metabolism in WOI organoids is reflected in Figure 3B, and up-regulation of hypoxia responses is reflected in Figure S3F.

- In general, it should be stated in the text that CellPhoneDB is a useful tool to investigate ligandreceptor interactions, however, it only proposes potential interactions. To validate such interactions, stainings and functional assays are required.

Thanks for your suggestion. The CellphoneDB was briefly introduced in the "Methods" section of "Supporting information" originally. Now it has been explained in the line 256-257 of main text.

We agree that staining and functional assays are required to validate the ligand-receptor interactions. Therefore, we used the proximity ligation assay (PLA) to verify the trend of interaction. (Figure S2J, Line259-261, Line 277-279, Line 285-288）

- Line 243: Please describe the process of EMT in the endometrium more specifically.

EMT is a common and crucial biological event in the endometrium during the implantation window. During the EMT process, epithelial cells lose their epithelial characteristics while gaining migratory and invasive properties of fibroblasts.

During the attachment and adhesion phases of embryo implantation, interaction mediated by trophoblastic factors (e.g. integrins) and maternal ECM factors (e.g. fibronectin) induce the eventual EMT in the trophectoderm. During the peri-implantation period, microRNAs, (e.g. miR429 and miR-126a-3p) which regulate EMT, are expressed in the maternal luminal epithelium to different degrees, mediating its transformation process as the blastocyst invades the maternal decidua. The epithelium of endometrium transforms to epithelioid stromal cells with increased migratory and invasive capacities through the EMT process. The decidual stromal cells migrate away from the implantation site, having acquired increased motility. (Line 265-267)

- Lines 247-251 and 313-316: the claim that proliferative epithelium transforms into EMT derived stromal cells by pseudotime trajectory is too bold and must be underpinned by other means. Pseudotime analysis only suggests and is by definition biased since the first/originating population must be defined by the operator.

In addition to pseudotime analysis based on monocle, RNA rate analysis based on scVelo is also used for cell evolution analysis. They can prove each other if both analyses indicate the transformation from proliferative epithelium to EMT-derived stromal cell. RNA rate analysis automatically determines the direction of differentiation, which can be used as evidence to determine the starting point of pseudotime analysis.

RNA rate analysis showed that the EMT derived stromal cell was most closely connected to the proliferative epithelium. Besides, the pseudotime point plot inferred that the proliferative epithelium was the root cell. It can be mutually proved with pseudotime analysis that the transformation from proliferative epithelium to EMT-derived stromal cell.

Author response image 7.

RNA rate junction diagram (To infer intercellular connectivity)

Author response image 8.

Time differentiation of cells

Discussion

- Line 300-302: It would be interesting to investigate ATP production and IL8 release in the WOI organoids to validate with findings from in vivo.

To answer this point of your interest, we purposely examined ATP production and IL8 release. It was found that WOI organoids indeed produced much more ATP and IL8 than CTRL and

SEC organoids (Figure S3L) (Line323-324)

- Line 313-316: Do the WOI organoids lose polarity and cell-to-cell junctions?

Transcriptome sequencing revealed downregulation of cell adhesion and RHO GTPase signaling in WOI organoids (Figure 3B). Electron microscopy revealed that the cellular arrangement of WOI organoids was slightly looser than that of CTRL organoids, but the microvilli were still oriented toward the medial side of the glands and did not undergo polarity reversal (shown as below).

Author response image 9.

Electron micrograph of the CTRL (left), and WOI (right) endometrial organoid. Scale bar = 5 μm.  

- Line 322: Where is the data that shows that 'a decreased abundance of immune cells', is observed?  

A decreased abundance of immune cells was observed through single-cell transcriptome sequencing and flow cytometry. The number of immune cells was reduced in WOI organoids compared to CTRL organoids in single-cell sequencing results (Figure 4A). Besides, flow cytometry also showed that the percentage of WBCs in WOI organoids was lower than that in CTRL organoids (Figure S2F).  

- Line 324: Elaborate more on how the immune cell composition differs from the endometrium.

The differences of immune cell composition between organoids and endometrium were mainly reflected in the proportion of WBC, the proportion of immune cell subtypes and the changes of T cells after entering the implantation window.

Firstly, the proportion of WBCs in organoids was lower than that in endometrium. Flow cytometry showed that the proportion of WBC in organoids was about 3%~4% (Figure 2D), but the proportion of WBCs in endometrium was about 8% (W. Wang et al., Nat Med 2020). Secondly, the proportions of T cells and macrophages in organoids were about 2%~3% and 1% (Figure 2D), respectively, but the proportions of lymphocytes and macrophages in endometrium were 7%~8% and 0.6%~0.7% (W. Wang et al., Nat Med 2020). Besides, after entering the implantation window, T cells in WOI organoids decreased (Figure S2F), while T cells in endometrium increased (W. Wang et al., Nat Med 2020). These three aspects have differences in vivo and in vitro. (Line347353)

Material and Methods

-  What are the concentrations of all medium components?

Thanks to your suggestions. The concentrations of all medium components have now been refined in Table S1.

-  Authors mention 10x while Smartseq2 is mentioned in Dataset S7?

Thanks for your careful review. Single cell transcriptome sequencing in this study was done using 10X Genomics. Smartseq2 was used to sequence the transcriptome of a gland and its surrounding cells, which can be regarded as small bulk RNA sequencing. A small number of cells are utilized in Smartseq2 to construct a full-length mRNA library with enhanced transcript sequencing coverage, making it particularly well-suited for small-scale samples such as organoids.

The data in Dataset S7 are acquired from small bulk RNA-seq with Smartseq2.  

Reviewer #2 (Recommendations For The Authors):

Q1: The theoretical choice of extra reagents added to the WOI organoids culture (PRL, hCG, and hPL) is theoretically justified, but not experimentally. On what previous studies, or performed experiments, are the choice of conditions used based?

When selecting hormone formulations, multiple group comparisons were made. It was found that the number, area, and average intensity of organoids in these groups were similar over time. But the WOI organoids showed endometrial receptivity related gene expression profile, which highly expressed genes positively correlated with endometrial receptivity, and lowly expressed genes negatively correlated with receptivity, compared to the other hormone formulations (added to Figure S1E, S1F). Hormone dosage was primarily based on peri-pregnant maternal body or localized endometrium levels (Margherita Y. Turco et al., Nature Cell Biology 2017).

Q2: Text in line 111 indicates that "stromal cells formed an extensive network", but vimentin fluorescence is not present on any image surrounding organoids in that figure. This assertion could only be supported by the subsequent results in Figure 2B. In addition, it is not indicated what kind of organoids have been used for these experiments

The stromal cells arranged around the glands in the 3D structure (as shown in Figure 1C and Figure 2B), where bright-field high magnification photography, clearing staining of the organoids, and light microscopy imaging were used, respectively. However, there are many steps of fixation, embedding, staining and elution during the immunostaining of sections. It is difficult to preserve the arrangement and morphology of the stromal cells in the slice, so the stromal cells were not intentionally captured in the other images.  

Figure 1C and Figure 2B are both CTRL organoids, which are now noted in the corresponding figure legend section.  

Q3: It is not clear how glycogen secretion into the lumen is assessed in Figure 1D.

Glycogen from the subnuclear region of the glandular cells gradually reaches the top of the cells, i.e., the supranuclear region, and is discharged into the glandular lumen as parietal plasma secretion. Glycogen-containing eosinophilic secretion can be seen in the glandular lumen in Figure1D.

Q4: Assertions about differences in proliferation between groups are purely subjective; some kind of measurement and analysis would be necessary to be sure that there is differential proliferation based on Figure 1B.

We are extremely grateful to you for pointing out this problem. We quantitatively analyzed the size of organoids in the three groups. The area was found to be increasing over time, with the three groups growing the most vigorously in the CTRL group, followed by the SEC group and the WOI group, but the differences were not statistically significant. Relevant results have been added to Figure S1E (Line130-131).

Q5: For progesterone receptor expression analysis organoids are cultured for fourteen days. What is the basis for this change in culture time? 

The choice of time point here is based on the secretary period of 14 days in the female menstrual cycle, when the endometrium is stimulated by estrogen and progesterone to maximized

level.

Q6: "n" number of individuals analysed through single-cell transcriptomics is not indicated.

One patient's endometrium was simultaneously constructed into CTRL, SEC and WOI organoids, which were then subjected to single-cell transcriptome sequencing. This is described in the Supporting Information (Line 141-142).

Q7: Where does the classification of EMT-derived stromal cells come from?

EMT is a common and crucial biological event in the endometrium during the implantation window. During the EMT process, epithelial cells lose their epithelial characteristics while gaining migratory and invasive properties of fibroblasts.

This cluster of cells expresses both epithelium markers CDH1 and EPCAM, and specifically expresses high levels of the EMT-related stromal cell markers AURKB, HJURP and UBE2C. During endometrial EMT, AURKB upregulates MMP2, VEGFA/Akt/mTOR and Wnt/β-catenin/Myc pathways to induce EMT (Zhen Wang et al., Cancer Manag Res 2020). HJURP also activates Wnt/β-catenin signaling to promote EMT (Y Wei et al., Eur Rev Med Pharmacol Sci 2019, Tianchi Chen et al., Int J Biol Sci 2019). UBE2C is upregulated by estrogen to promote EMT (Yan Liu et al., Mol Cancer Res 2020). Therefore, this cluster was defined as "EMT-derived stromal cells”.

Q8: In the endometrial receptivity test (ERT), endometrium sample data matches with prereceptive endometrium and WOI organoids data matches with a receptive endometrium, but why there is no information about CTRL and SEC organoids?

We performed ERT on these samples at a time when our hospital has a cooperative project with Yikon Genomics (Jiangsu, China). However, only endometrium and WOI organoids were sent for testing due to the limited quotas. Considering the end of cooperation and batch effect, no more CTRL and SEC organoids were tested. Moreover, the current ERT is a machine learning model based on the sequencing data of endometrium samples. But there are still differences in cellular composition between endometrial organoids and endometrium. Thus, the results need to be interpreted in conjunction with other results.

Q9: When analysing the transcriptome and proteome, some comparisons are made between WOI vs CTRL and SEC, or just WOI vs CTRL. It would be interesting to have all the comparisons since the power of WOI organoids lies in their differences with SEC organoids.

Thanks for your suggestion. At the organoid level, the differences in transcriptome and proteome between SEC and WOI organoids are not significant. This is understandable because WOI organoids are further induced towards the implantation window based on the secretory phase (i.e. SEC organoids), which prompted us to continue exploring at the single-cell level.

Q10: Electron microscopy comparisons with respect to pinopods, cilia, and microvilli are only performed between WOI and CTRL. It would be interesting to check it with SEC.

We now quantitatively compared the presence of various characteristic structure like microvilli, cilia, pinopodes and glycogen in the CTRL, SEC and WOI organoids. It was found that WOI organoid had longer microvilli and increased cilia, glycogen, and pinopodes (Figure 2H).

Q11: Line 190 states that pinopods are arranged more densely in WOI organoids than in CTRL organoids. Seems to be a subjective observation. Is there an objective method to quantify this?

We agree with the reviewer’s suggestion and quantified the pinopodes. The CTRL, SEC and WOI organoids were found to have increasing numbers of pinopodes, with WOI organoid owning the most abundant pinopodes. (Figure 2H) (Line184-186)

Q12: Some characteristics are very similar between WOI and SEC organoids (such as the accumulation of secretory epithelium or decreased proliferative epithelium, the increased ciliated epithelium after hormonal treatment, or the presence of EMT-derived stromal cells). The authors should complement the discussion by objectively justifying the use of WOI versus SEC organoids. Would they be useful in more specific cases or at a general level when studying implementation?

Thanks for your comments. WOI organoids are differentiated from SEC organoids towards the implantation window. Therefore, WOI organoids are suitable for studying periimplantation physiological changes or exploring pathological mechanisms. SEC organoids can be used when studying only a range of pathological problems such as endometrial secretory phase changes or hormone reactivity. (Line 365-368)

Q13：ExM media is described in Table S1, but it does not include the concentration of the different reagents in the culture medium, which is the most interesting data about the ExM medium.

Thanks to your suggestions. The concentrations of all medium components have now been refined in Table S1.

Q14: It is not specified which organoid pass is used in each experiment. Is it always the same pass?

Our experiments were conducted using P1~P3 generation endometrial organoids, as specified in the “Supporting Information” Line 54~55.

Q15: As a protocol for freezing organoids is included in materials and methods, do the authors use freshly cultured organoids or do they cryopreserve them and thaw them for culturing?

Thanks for your question. We used freshly cultured organoids in the manuscript. We listed the freezing protocol to illustrate that the constructed organoids can be frozen and recovered for special experimental needs and the establishment of sample banks.

Q16: The most important point: Neither of the two studies that developed human endometrial organoids from tissue biopsies (Boretto et al. 2017 and Turco et al. 2017), observed stromal cell growth in culture. They disappeared between the first and second pass (as indicated by Turco et al. 2017). How do the authors justify the presence of stromal cells in their organoid culture if they rely on the protocols previously described by these research groups? If it is the case that they can only use the initial pass (freshly planted cells from endometrium), it does not make sense to include the freezing of the different passes in materials and methods, since the expansion capacity of the culture would be lost, which implies a major limitation of the model.

Thanks for your question.  

(1) We did not completely follow the protocols of these research groups. To maximize the recovery of both epithelial and stromal cells, we optimized key steps such as tissue digestion and cell strainer filtration. We shortened the digestion time to 20 minutes to protect cells from the digestion solution and retain some cell aggregates, which are beneficial for maintaining cell stemness and preserving stromal and immune cells cluster. The 40 μm filter membrane was used to isolate the endometrial cells, which may acquire both epithelial, and stromal cells.

(2) Our experiments were conducted using P1~P3 generation of freshly constructed organoids. However, we also used recovered organoids when fresh endometrial samples were not available due to the COVID-19 epidemic. It was found that the organoids (e.g., P0~P5) still exhibited vigorous growth condition after recovery and could continue to be cultured by passaging (shown as below).

The recovered organoids can be used for special experiments and biobank establishment.

Author response image 10.

The endometrial organoids of different passages were observed before cryopreservation and after recovery. Scale bar = 200 μm.

Q17: It is not clear which organoids include Figure S2F. Does it include the three types of organoids or just WOI organoids?

This circle diagram showed the functions of upregulated genes in the WOI group compared to CTRL group from combined transcriptome and proteome analysis, which has been labeled in the figure legend section.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Major comments:

(1)  Regarding the cell studies of human pediatric bone-derived osteoblast-like cells (HBO), the authors should provide a rationale for their selection of specific cell lines (15,16, 17, 19, 20, 23, 24) in this study. As for animal studies, could the authors clarify which cell lines were utilized in the murine in vivo experiments?

We appreciate the opportunity to address this. To reduce confusion, we have numbered the patient primary cell lines used in these studies sequentially from 1 – 7. Additionally, we have added “HBO cell lines used for experiments were selected based on the ability of the primary cell line to proliferate and mineralize in culture” to the Methods section. 

In vivo experiments: “HBO cell lines 2, 6 and 7 from separate individuals were selected for these experiments based on similar growth and passage characteristics.” This statement is included in the Methods section.

(2)  In this study, the authors performed the murine in vivo experiments using both male and female mice. Could the author clarify if any difference was observed between male and female mice in the findings? This information would contribute to a more comprehensive understanding of the study.

We agree and have added the following to the Results section: “There was no sex-based difference in regenerated bone volume.”

(3)  Although the histological results showed an elevated collagen expression in mice treated with BMP2, JAG1, and JAG1 + DAPT compared to those treated with the cells alone, the differences among groups were subtle. The authors should consider the immunohistochemical (IHC) staining for collagen 1 on the samples, allowing for a quantitative assessment of collagen 1 expression.

Thank you for this comment. The differences between BMP2, JAG1, and JAG1 + DAPT are indeed subtle. We have added Supplementary Figure 5, showing collagen staining of sections from the same FFPE blocks that were sectioned and stained with Masson Trichrome in Figure 2C. 

Minor Comments:

(4)  Please specify which cell lines are represented in the staining results shown in Fig.1A and Fig. 5A, respectively.

In Fig 1A the representative images are of HBO2. Fig 5A representative images are of HBO7. We have added this information to the figure legends for these figures. 

(5)  There appears to be a discrepancy in the specified size of the critical defect. The manuscript states that the size is 4mm, while Supplemental Figure 3 indicates 3.5mm.

Thank you for this catch! Yes, it should be 4mm. This has been corrected in Supplementary Figure 3.

(6)  The scale bar for Figure 2 C is missing.

Scale bars have been added which also gave us an opportunity to brighten the images equally, allowing for better distinction between the different colors of the Masson Trichrome staining.

(7)  In the methodological section 2.5 for JAG1 delivery, it would be helpful if the authors could review the initial dosage of JAG1 delivery to confirm if HBO cells were included or not, given that the MicroCT results indicate that all groups incorporated HBO cells. 

We appreciate this suggestion. In response to another question, we have added Supplementary Figure 4 which includes an “Empty Defect” condition with no HBO cells, making the original method statement accurate.

Reviewer #2 (Recommendations For The Authors):

In the current study, using in vitro and in vivo models the authors clearly show that JAG1 can enhance osteogenesis and thus can be helpful in designing new therapeutic approaches in the field of bone regenerative research. The in vivo mouse CF model is very convincing and shows that JAG1 promotes osteogenesis via non-canonical signaling. Mechanistically it seems that JAG1 activates STAT5, AKT, P38, JNK, NF-ĸB, and p70 S6K. However, additional evidence is needed to convincingly conclude that all the non-canonical pathways activated via JAG1 converge at p70 S6K activation. The following concerns need to be addressed.

(1) In Fig 1A: Even though the Jag1-Fc shows a very significant increase in HBO mineralization, there are no significant increases in cells in osteogenic media when compared to control growth media. Even though the different conditions were subjected to RNAseq analysis in the later figures, qPCR analysis of some osteogenic genes in Figure 1 might be helpful. 

We appreciate the opportunity to explore this question further. We conducted mineralization experiments in triplicate and performed qRT-PCR, assessing for gene expression of 5 osteogenic genes: ALPL, BGLAP (osteocalcin), COL1A1, RUNX2, and SP7. Results are shown in Figure 1C and this text was added to Results: “Additionally, PCR analysis of HBO1 cells from a repeat experiment collected at days 7, 14, and 21 showed significantly increased expression of osteogenic genes with JAG1-bds stimulation (Figure 1C). ALPL was significantly expressed at Day 7, with a 3.5-fold increase (p=0.0004) compared to HBO1 cells grown in growth media. In contrast, significant expression levels of COL1A1 and BGLAP were observed at 14 days, with a 5.1-fold increase (p=0.0021) of COL1A1 and a 12.3-fold increase (0.0002) of BGLAP when compared to growth media conditions. Interestingly, while some mineralization is observed in the osteogenic media and Fc-bds

(Figure 1A) conditions, there were no significant increases in osteogenic gene expression (Figure

1C). Expression of RUNX2 and SP7 was not significantly altered across all conditions and time points (not shown).”

(2) In Fig 2: even though not needed in respect to the hypothesis, was there any Control group without any cells or JAG1 beads? What were the changes in between that group and cells cells-only group?

We have not observed differences between the “Empty Defect” group and the “Cells alone” group.

We have addressed the reviewer’s comments by adding this comparison in Supplementary Figure 4.

(3) Transcriptional profiling and ELISA (Fig 3 and 4) show upregulation of NF-ĸB signaling in response to JAG1. In the discussion, the authors have referenced a previous study showing NF-ĸB as prosurvival in human OB cells. However, based on many published reports, NF-ĸB activation has been shown to inhibit OB function. Does JAG1 regulate HBO cell survival via NF-ĸB activation?

Experimenting using NF-ĸB inhibitor can be helpful to show that JAG1 mediates NF-ĸB activation is anabolic in this experimental setup.

We thank the reviewer for this excellent suggestion. We are eager to explore this new direction for our research in a subsequent study. We have added this to our future directions. 

(4) Fig 5: 

(A)  Condition showing JAG1+ DAPT is needed to compare between JAG1 canonical and noncanonical signaling. 

Thank you for pointing this out. We have added Supplementary Figure 6, which includes a dose response experiment for JAG1 + DAPT.

(B)  S6K18 alone seems to be increasing OB mineralization. Is that statistically significant?  

No, and we have added the statistical analysis for S6K-18 to Figure 5B.

(C)  Fc alone condition seems to have a very significant increase in OB mineralization. Does Fc alone upregulate OB function? 

We do see some upregulation of mineralization with Fc in vitro, which we also observed in our previous studies with mouse neural crest cells, but we have not found it to be osteogenic in vivo. We have added a statement to this effect, with references. Additionally, osteogenic gene expression was not upregulated in our in vitro mineralization experiments with Fc.  See Revised Figure 1.

(D)  Although overall quantification shows that S6K18 partially inhibits HBO mineralization, the representative images do not represent the quantification. Transcriptional analysis (qPCR) is required to validate these findings.

We performed qRT-PCR on cells from a repeat mineralization assay, collecting cells at 9, 14, and 21 days. We have added the following to the Results:” While inhibition of NOTCH and p70 S6K decreased mineralization in our mineralization assay, there are no statistically significant changes in gene expression for ALPL, COL1A1, or BGLAP (Supplementary Figure 7). These results suggest that the HBO cells phenotypes are maturing into osteocytes and that inhibiting p70 S6K hinders the cellular ability to mineralize but not the cell phenotype progression.”

(5) Finally, to convincingly conclude the data from Fig 5, the mouse CF model can be helpful to support the authors' claim that JAG1 acts via p70 S6K.

Thank you for this feedback. We have modified our conclusions to reflect that p70 S6K is one of the non-canonical pathways that JAG1 may be activating in bone regeneration.

Thank you very much for your consideration of our revised manuscript.

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this paper, proteomics analysis of the plasma of human subjects that underwent an exercise training regime consisting of a combination of endurance and resistance exercise led to the identification of several proteins that were responsive to exercise training. Confirming previous studies, many exercise-responsive secreted proteins were found to be involved in the extra-cellular matrix. The protein CD300LG was singled out as a potential novel exercise biomarker and the subject of numerous follow-up analyses. The levels of CD300LG were correlated with insulin sensitivity. The analysis of various open-source datasets led to the tentative suggestion that CD300LG might be connected with angiogenesis, liver fat, and insulin sensitivity. CD300LG was found to be most highly expressed in subcutaneous adipose tissue and specifically in venular endothelial cells. In a subset of subjects from the UK Biobank, serum CD300LG levels were positively associated with several measures of physical activity - particularly vigorous activity. In addition, serum CD300LG levels were negatively associated with glucose levels and type 2 diabetes. Genetic studies hinted at these associations possibly being causal. Mice carrying alterations in the CD300LG gene displayed impaired glucose tolerance, but no change in fasting glucose and insulin. Whether the production of CD300LG is changed in the mutant mice is unclear.

Strengths:

The specific proteomics approach conducted to identify novel proteins impacted by exercise training is new. The authors are resourceful in the exploitation of existing datasets to gain additional information on CD300LG.

Weaknesses:

While the analyses of multiple open-source datasets are necessary and useful, they lead to relatively unspecific correlative data that collectively insufficiently advance our knowledge of CD300LG and merely represent the starting point for more detailed investigations. Additional more targeted experiments of CD300LG are necessary to gain a better understanding of the role of CD300LG and the mechanism by which exercise training may influence CD300LG levels. One should also be careful to rely on external data for such delicate experiments as mouse phenotyping. Can the authors vouch for the quality of the data collected. 

Thank you for the valuable feedback on our manuscript. We recognize concerns about the specificity of correlative data from open-source datasets and the limitations it presents for understanding CD300LG's role. To address this, we have expanded the manuscript with a paragraph in the discussion regarding the need of targeted experiments confirm CD300LG’s functions and relationship with glucose metabolism. We also emphazise caution regarding external data reliance and we acknowledge the need for generating primary data including direct phenotyping of mice with CD300LG gene alterations to better understand its regulatory mechanisms and effects on glucose tolerance. Please see lines 446-456.

Reviewer #2 (Public Review):

Summary:

This manuscript from Lee-Odegard et al reports proteomic profiling of exercise plasma in humans, leading to the discovery of CD300LG as a secreted exercise-inducible plasma protein. Correlational studies show associations of CD300LG with glycemic traits. Lastly, the authors query available public data from CD300LG-KO mice to establish a causal role for CD300LG as a potential link between exercise and glucose metabolism. However, the strengths of this manuscript were balanced by the moderate to major weaknesses. Therefore in my opinion, while this is an interesting study, the conclusions remain preliminary and are not fully supported by the experiments shown so far.

Strengths:

(1) Data from a well-phenotyped human cohort showing exercise-inducible increases in CD300LG.

(2) Associations between CD300LG and glucose and other cardiometabolic traits in humans, that have not previously been reported.

(3) Correlation to CD300LG mRNA levels in adipose provides additional evidence for exercise-inducible increases in CD300LG.

Weaknesses:

(1) CD300LG is by sequence a single-pass transmembrane protein that is exclusively localized to the plasma membrane. How CD300LG can be secreted remains a mystery. More evidence should be provided to understand the molecular nature of circulating CD300LG. Is it full-length? Is there a cleaved fragment? Where is the epitope where the o-link is binding to CD300LG? Does transfection of CD300LG to cells in vitro result in secreted CD300LG?

(2) There is a growing recognition of specificity issues with both the O-link and somalogic platforms. Therefore it is critical that the authors use antibodies, targeted mass spectrometry, or some other methods to validate that CD300LG really is increased instead of just relying on the O-link data.

(3) It is insufficient simply to query the IMPC phenotyping data for CD300LG; the authors should obtain the animals and reproduce or determine the glucose phenotypes in their own hands. In addition, this would allow the investigators to answer key questions like the phenotype of these animals after a GTT, whether glucose production or glucose uptake is affected, whether insulin secretion in response to glucose is normal, effects of high-fat diet, and other standard mouse metabolic phenotyping assays.

(4) I was unable to find the time point at which plasma was collected at the 12-week time point. Was it immediately after the last bout of exercise (an acute response) or after some time after the training protocol (trained state)?

We acknowledge the importance of understanding the molecular form of CD300LG in circulation. We have expanded the discussion with a paragraph regarding the need of follow-up experiments on whether circulating CD300LG is full-length or a cleaved fragment, to identify the epitope for O-link binding, and assess CD300LG secretion in vitro through transfection experiments. We also discuss the need of targeted mass spectrometry and antibody-based validation of O-link measurements of CD300LG, and the need for more validation experiments on CD300LG-deficient mice. Please see lines 446-456.

The plasma collected post-intervention is in a state that reflects the new baseline trained condition of the subjects, 3 days after the last exercise session during the intervention. We have clarified this in our manuscript. The information is updated in line 491-493.

Reviewer #1 (Recommendations For The Authors):

In the present form, the paper raises interest in the potential role of CD300LG in the response to exercise training but unfortunately does not provide clear answers. The authors should focus their efforts on firmly validating the status of CD300LG as an exercise biomarker in humans and carefully examine the function of CD300LG through mechanistic and animal-based studies.

The authors are encouraged to acquire CD300LG-deficient mice and perform specific experiments to validate hypotheses forthcoming from the analysis of the open-source datasets. In addition, it needs to be validated that the cd300lgtm1a(KOMP)Wtsi mice are actually deficient in CD300LG. It is not uncommon that Tm1a mice have (almost) normal expression of the targeted gene.

We have now revised the manuscript and added a new section to the discussion regarding the limitations with open-source data, cd300lgtm1a(KOMP)Wtsi mice and the need for more validation experiments on CD300LG-deficient mice. Please see lines 446-456.

The value of the correlative data presented in Figure 5 is rather limited. The same can be argued for the data presented in Supplementary Figure 2. If CD300LG is expressed in endothelial cells, it stands to reason that its expression is correlated with angiogenesis. Hence, this observation does not really carry any additional value.

We agree that correlations cannot imply causality. However, similar patterns were observed in several tissues and across different data sets, which at least suggest a role CD300LG related to angiogesis. We have included a section in the discussion were we clarify that our observations should only be regarded as indications and that follow-up studies are needed to confirm any causal role for CD300LG on angiogenesis/oxidativ capacity. Please see lines 446-456.

Figure 6 may be better accommodated in the supplement.

Figure 6 is now moved to the supplement.

Figure 3A and B are a bit awkward. The description "no overlap" is confusing. Isn't it more accurate to say "no enrichment" or "no over-representation"? There will always be some overlap with certain pathways. However, there may be no enrichment. Furthermore, the use of arrows to indicate No overlap is visually not very appealing. Maybe the numbers can be given a specific color?

We have now removed the arrows and text, and rather stated in the text that there were no enrichements other than for the proteins down-regulated in the overweight group.

The description of the figure legend of figure 5E-H is incomplete.

The description is now completed.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors attempt to fully characterize the immunoglobulin (Ig) heavy (H) chain repertoire of tumor-infiltrating B cells from three different cancer types by identifying the IgH repertoire overlap between these, their corresponding draining lymph nodes (DLNs), and peripheral B cells. The authors claim that B cells from tumors and DLNs have a closer IgH profile than those in peripheral blood and that DLNs are differentially involved with tumor B cells. The claim that tumor-resident B cells are more immature and less specific is made based on the characteristics of the CDR-H3 they express.

Strengths:

The authors show great expertise in developing in-house bioinformatics pipelines, as well as using tools developed by others, to explore the IgH repertoire expressed by B cells as a means of better characterizing tumor-associated B cells for the future generation of tumor-reactive antibodies as a therapy.

Weaknesses:

This paper needs major editing, both of the text and the figures, because as it stands it is convoluted and extremely difficult to follow. The conclusions reached are often not obvious from the figures themselves. Sufficient a priori details describing the framework for their analyses are not provided, making the outcome of their results questionable and leaving the reader wondering whether the findings are on solid ground.

The authors are encouraged to explain in more detail the premises used in their algorithms, as well as the criteria they follow to define clonotypes, clonal groups, and clonal lineages, which are currently poorly defined and are crucial elements that may influence their results and conclusions.

In response to this comment, we significantly expanded the paragraph dedicated to the tumor and non-tumor repertoire overlap and isotype composition. The following sections were added:

First, we characterized the relative similarity of IGH repertoires derived from tumors, DLN, and PBMC on the individual CDR-H3 clonotype level. We define clonotype as an instance with an identical CDR-H3 nucleotide sequence  and identical V- and J- segment attribution (isotype attribution may be different). Unlike other authors, here we do not pool together similar CDR-H3 sequences to account for hypermutation. (Hypermutation analysis is done separately and defined as clonal group analysis. )

As overlap metrics are dependent on overall repertoire richness, we normalized the comparison using the same number of top most frequent clonotypes of each isotype from each sample (N = 109). Repertoire data for each sample were split according to the immunoglobulin isotype, and the F2 metric was calculated for each isotype separately and plotted as an individual point.

We also analyzed D metric, which represents the relative overlap diversity uninfluenced by clonotype frequency (Dij\=dij/(di*dj), where dij is the number of clonotypes present in both samples, while di and dj are the diversities of samples i and j respectively). The results for D metric are not shown, as they indicate a similar trend to that of F2 metric. This observation allows us to conclude that tumor IGH repertoires are more similar to the repertoires of lymph nodes than to those of peripheral blood, both if clonotype frequency is taken into account, and when it is not.

Having excluded the IGHD gene segment from some of their analyses (at least those related to clonal lineage inference and phylogenetic trees), it is not well explained which region of CDR-H3 is responsible for the charge, interaction strength, and Kidera factors, since in some cases the authors mention that the central part of CDR-H3 consists of five amino acids and in others of seven amino acids.

We considered different ways of calculating amino acid properties of CDR3 and used different parameters for sample-average and individual-sequence CDR3s. Now plots for Fig S6 C are updated  for consistency and the parameters depicted there are now calculated using 5 central amino acids, as in other sections.

How can the authors justify that the threshold for CDR-H3 identity varies according to individual patient data? 

Ideal similarity threshold may depend on several factors, such as sampling, sequencing depth etc. For example, imagine a sample picking up 100% of the clonal lineage sequences which differ only 1 amino acid from each other, and a worse quality sample/sequencing picking up only every other sequence. Obviously, the minimal threshold required to accumulate these into a cluster/clonal group  would be different for these two cases (1aa for the former, and ~2 aa for the latter for single-linkage clustering). Or, in other words, the more the sequencing depth, the more dense the clusters will be. The method of individual threshold tailoring relies on the following: https://changeo.readthedocs.io/en/latest/examples/cloning.html

Although individual kidera factors that are significant in the context of our analysis are described in the text one by one on their first appearance, we now also added a sentence to describe Kidera factor analysis in general (page 8):

Kidera factors are a set of scores which quantify physicochemical properties of protein sequences (Nakai et al. 1988). 188 physical properties of the 20 amino acids are encoded using dimension reduction techniques.

Throughout the analyses, the reasons for choosing one type of cancer over another sometimes seem subjective and are not well justified in the text.

Whenever possible, we pooled all patients with all cancer types together, because the number of available samples did not allow us to draw any significant conclusions comparing between individual cancer types. When analyzing and showing individual patient data, we also did not attempt to depict any cancer-type-specific findings, but it is inevitable that we name a specific cancer type when labelling a sample coming from a specific tumor.

Overall, the narrative is fragmented. There is a lack of well-defined conclusions at the end of the results subheadings.

In addition to the described above, a conclusion was added to the paragraph describing hypermutation analysis:

IGHG clonotypes from lung cancer samples show higher number of hypermutations, possibly reflecting high mutational load found in lung cancer tissue. For melanoma, another cancer known for high mutational load, no statistically significant difference was found. This may be due to higher variance between melanoma samples, which hinders the analysis, or due to the small sample size.

The exact same paragraph is repeated twice in the results section.

Corrected.

The authors have also failed to synchronise the actual number of main figures with the text, and some panels are included in the main figures that are neither described nor mentioned in the text  (Venn diagram Fig. 2A and phylogenetic tree Fig. 5D). Overall, the manuscript appears to have been rushed and not thoroughly read before submission.

Corrected.

Reviewers are forced to wade through, unravel, and validate poorly explained algorithms in order to understand the authors' often bold conclusions.

We hope that the aforementioned additions to the text and also addition to the Figure 1 make the narrative more easily understandable.

Reviewer #2 (Public Review):

Summary:

The authors sampled the B cell receptor repertoires of Cancers, their draining lymph nodes, and blood. They characterized the clonal makeup of all B cells sampled and then analyzed these clones to identify clonal overlap between tissues and clonal activation as expressed by their mutation level and CDR3 amino acid characteristics and length. They conclude that B cell clones from the Tumor interact more with their draining lymph node than with the blood and that there is less mutation/expansion/activation of B cell clones in Tumors. These conclusions are interesting but hard to verify due to the under-sampling and short sequencing reads as well as confusion as to when analysis is across all individuals or of select individuals.

Strengths:

The main strength of their analysis is that they take into account multiple characteristics of clonal expansion and activation and their different modes of visualization, especially of clonal expansion and overlap. The triangle plots once one gets used to them are very nice.

Weaknesses:

The data used appears inadequate for the conclusions reached. The authors' sample size of B cells is small and they do not address how it could be sufficient. At such low sampling rates, compounded by the plasmablast bias they mention, it is unclear if the overlap trends they observe show real trends. Analyzing only top clones by size does not solve this issue. As it could be that the top 100 clones of one tissue are much bigger than those of another and that all overlap trends are simply because the clones are bigger in one tissue or the other. i.e there is equal overlap of clones with blood but blood is not sufficiently sampled given its greater diversity and smaller clones.

Regarding the number of clonotypes to be taken into account,  we were limited by the B cell infiltration of tumor samples and our ability to capture their repertoire. However, we use technical replicates on the level of cell suspension to ensure that at least top clonotypes are consistently sampled. So, this is how the data should be interpreted - as describing the most abundant clones in the repertoire (which also may be considered the most functionally relevant in case of tumor infiltrating lymphocytes).

To analyze the repertoire overlap, we generally use the F2 metric that takes clone size into account - because we think that clone size is an important functional factor. However, we have now added the description of using D metric (does not include clone frequency as a parameter) - which shows exactly the same trend as F2 metric. So, both F2 and D overlap metrics support our conclusion of higher overlap between tumor and LN.

The following text was added:

We also analyzed D metric, which represents the relative overlap diversity uninfluenced by clonotype frequency (Dij\=dij/(di*dj), where dij is the number of clonotypes present in both samples, while di and dj are the diversities of samples i and j respectively). The results for D metric are not shown, as they indicate a similar trend to that of F2 metric. This observation allows us to conclude that tumor IGH repertoires are more similar to the repertoires of lymph nodes than to those of peripheral blood, both if clonotype frequency is taken into account, and when it is not.

All in all, of course, the deeper the better, but given the data we were able to generate from the samples, this was the best approach to normalization that could be used.

Similarly, the read length (150bp X2) is too short, missing FWR1 and CDR1 and often parts of FWR2 if CDR3 is long. As the authors themselves note (and as was shown in (Zhang 2015 - PMC4811607) this makes mutation analysis difficult.

Indeed, we are aware of this problem, and therefore only a small part of the manuscript is dedicated to the hypermutation analysis. However, as the CDR-H3 region is the most mutated part, we still can capture significant diversity of mutations. To address the question of applicability of our data for the hypermutation phylogeny analysis, we compare the distribution of physico-chemical properties along the trees of hypermutation using the 150+150 and 300+300 data from the same donor and the same set of samples. The main conclusion is that neither for long, nor for short datasets could any correlation of physicochemical properties of the CDR-H3 region with the rank of the clonotype on the tree be found.  

It also makes the identification of V genes and thus clonal identification ambiguous. This issue becomes especially egregious when clones are mutated.

Again, this would be important for clonotype phylogeny analysis. However, for the simple questions that we address with our clonal group analysis, such as clonal group overlap between tissues etc, we consider this data acceptable, because if any mislabelling of V segment occurs, it is a) rare and b) is equally frequent in all types of samples. Therefore, any conclusions made are still valid despite this technical drawback.

To directly address the question of mislabelling of V-genes in our data, we looked at the average number of different  V-genes attributed to the same nucleotide sequence of CDR-H3 region in the short (150+150) and long (300+300) datasets from the same donor. Indeed, some ambiguity of V-gene labelling is observed (see below), but we think that it is unlikely to influence any of our cautious conclusions.

Author response image 1.

Finally, it is not completely clear when the analysis is of single individuals or across all individuals. If it is the former the authors did not explain how they chose the individuals analyzed and if the latter then it is not clear from the figures which measurements belong to which individual (i.e they are mixing measurements from different people).

We addressed this issue by adding a comment to each figure caption, describing whether a particular figure or panel describes individual or pooled data, and also whether the analysis is done on individual clonotype or clonal group level.

Also, in case pooled data were used, we added the number of patients that was pooled for a particular type of analysis. This number differs from one type of analysis to the other, because not all the patients had a complete set of tissues, and also not all samples passed a quality check for a particular analysis.

Here are the numbers listed:

Fig 2A: N=6 (we were only considering those who had all three tissues)

Fig 2C, N=14 (all)

2D: N=14 (all)

2E N=7 (have both tum and PBMC).

2F N=9 (have both tum and PBMC).

2G N=9 (have both tum and PBMC)

2H N=7 (have both tum and LN)

3A N=14 (all)

3B N=11 (only those with tumor)

3E - N=14

7F N=11 (all that have tumor)

Reviewer #3 (Public Review):

In multiple cancers, the key roles of B cells are emerging in the tumor microenvironment (TME). The authors of this study appropriately introduce that B cells are relatively under-characterised in the TME and argue correctly that it is not known how the B cell receptor (BCR) repertoires across tumors, lymph nodes, and peripheral blood relate. The authors therefore supply a potentially useful study evaluating the tumor, lymph node, and peripheral blood BCR repertoires and site-to-site as well as intra-site relationships. The authors employ sophisticated analysis techniques, although the description of the methods is incomplete. Among other interesting observations, the authors argue that the tumor BCR repertoire is more closely related to that of draining lymph node (dLN) than the peripheral blood in terms of clonal and isotype composition. Furthermore, the author's findings suggest that tumor-infiltrating B cells (TIL-B) exhibit a less mature and less specific BCR repertoire compared with circulating B cells. Overall, this is a potentially useful work that would be of interest to both medical and computational biologists working across cancer. However, there are aspects of the work that would have benefitted from further analysis and areas of the manuscript that could be written more clearly and proofread in further detail.

Major Strengths:

(1) The authors provide a unique analysis of BCR repertoires across tumor, dLN, and peripheral blood. The work provides useful insights into inter- and intra-site BCR repertoire heterogeneity. While patient-to-patient variation is expected, the findings with regard to intra-tumor and intra-dLN heterogeneity with the use of fragments from the same tissue are of importance, contribute to the understanding of the TME, and will inform future study design.

(2) A particular strength of the study is the detailed CDR3 physicochemical properties analysis which leads the authors to observations that suggest a less-specific BCR repertoire of TIL-B compared to circulating B cells.

Major Weaknesses:

The study would have benefitted from a deeper biological interpretation of the data. While given the low number of patients one can plausibly understand a reluctance to speculate about clinical details, there is limited discussion about what may contribute to observed heterogeneity.

We indeed do not want to overinterpret our data, especially where it comes to the difference between types of cancer. On the other hand, extracting similar patterns between different cancer types allows to pinpoint mechanisms that are more general and do not depend on cancer type. As for the potential source of intratumoral heterogeneity that we observe, we think that it may be coming from the selective sampling of tertiary lymphoid structures. We include IHC data for TLS detection in the supplementary Fig.5.  Also, tumor mutation clonality may correlate with differential antibody response (i.e. different IGH clonotypes developing to recognize different antigens) – as has been previously described for TCRs by the lab of B.Chain in https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6890490/.

For example, for the analysis of three lymph nodes taken per patient which were examined for inter-LN heterogeneity, there is a lack of information regarding these lymph nodes.

Unfortunately no clinical information about the lymph nodes was available.

'LN3' is deemed as exhibiting the most repertoire overlap with the tumor but there is no discussion as to why this may be the case.

The following phrases describes this in the “LN-to-LN heterogeneity in colorectal cancer” paragraph:

Similarly, an unequal interaction of tumors with DLNs was observed at the level of hypermutating clonal groups.

Functionally, this may again indicate that within a group of DLNs, nodes are unequal in terms of access to tumor antigens, and this inequality shapes the BCR repertoires within these lymph nodes.

(2) At times the manuscript is difficult to follow. In particular, the 'Intra-LN heterogeneity' section follows the 'LN-LN heterogeneity in colorectal cancer' section and compares the overlap of LN fragments (LN11, LN21, LN31) with the tumor in two separate patients (Fig 6A). In the previous section (LN-LN), LN11, LN21, LN31 are names given to separate lymph nodes from the same patient. The fragments are referred to as 'LN2' and the nodes in the previous section are referred to similarly. This conflation of naming for nodes and fragments is confusing.

We corrected this.

(3) There is a duplicated paragraph in 'Short vs long trees' and the following section 'Productive involvement in hypermutation lineages depends on CDR3 characteristics.

Corrected.

Reviewer #1 (Recommendations For The Authors):

- Figures:

Figure 1A lacks resolution

Corrected

Figure 2A, Venn diagram: What do the colors indicate?

Corrected

Figure 5D, why include this tree when there is no mention of it in the text?

Described

Figures 8, 9, and 10 are not to be found. One should not have to figure out that they became supplementary in the end.

Corrected

Regarding the physicochemical properties of CDR-H3, what do the authors mean by "the central part"? Do the authors refer to the CDR-H3 loop, and if so, how is that defined when the IGHD gene segment is excluded from the analyses? Is it 5 amino acids (Productive involvement in hypermutating lineages depends on CDR3 characteristics, Page 21/39 in merged document) and (CDR3 properties, Page 8/39 in merged document), or 7 amino acids (Short vs long trees phylogeny analysis, Page 19/39 in merged document)? Please clarify.  

We considered different ways of calculating amino acid properties of CDR3 and used different parameters for sample-average and individual-sequence CDR3s. Now plots for Fig S6 C are updated for consistency. IGHD segment was not excluded from the analysis. The reviewer might be confused by our description of phylogenetic inference, when an artificial outgroup with D segment deleted is added to the clonal group to facilitate the inference process. All other sequences were analyzed in their original form with the D segment. This way, we could avoid biases in phylogeny introduced by misassignment of D gene germline to the outgroup.

What was the threshold for CDR-H3 identity in their analyses? How can the authors justify that this value changes according to individual patient datasets? (Materials & methods, Clonal lineage inference Page 29/39 in merged document).

As described earlier, ideal similarity threshold may depend on several factors, such as sampling, sequencing depth etc. For example, imagine a sample picking up 100% of the clonal lineage sequences which differ only 1 amino acid from each other, and a worse quality sample/sequencing picking up only every other sequence. Obviously, the minimal threshold required to accumulate these into a clonotype would be different for these two cases (1aa for the former, and ~2 aa for the latter for single-linkage clustering). The method of individual threshold tailoring relies on this: https://changeo.readthedocs.io/en/latest/examples/cloning.html

What is the difference between tumor-induced and tumor-infiltrating B cells? How can the authors discriminate between the two? Page 6/39 in the merged document.

corrected to tumor-infiltrating

"Added nucleotides" meaning N additions? Page 3/39 in the merged document.

yes

How many cancer patients were enrolled? 17 or 14(Materials & methods page 27/39 in the merged document)? Please clarify.   

In the current project 14 patients were enrolled. The appropriate changes have been introduced in the final text. Supplementary table 2 has been added with the patient data.

Abbreviations are used without full descriptions.

According to reviewer’s recommendation, a list of abbreviations was added in the manuscript, and also full descriptions were added in the text upon first mentioning of the term.

Use either CDR3 or CDR-H3

We corrected the text to use CDR-H3 abbreviation throughout the text.

Reviewer #2 (Recommendations For The Authors):

I would like to start by apologizing for the time it took me to review.

As I mentioned above there are issues with the clonal sampling of the sequencing length and the statistics in this paper. From reading the paper I am not sure if they are fixable but there are some things that could be tried.

(1) The authors mention the diversity of their individual analysis - 17 individuals across 3 cancer types, but do not then systematically show us how the different things they measure track across the different individuals and cancer types. it is possible that some trends would be more convincing if we saw them happening again and again across all individuals. But, as I said above, the authors do not identify individuals clearly across all their types of analysis nor do they explain why sometimes they show analysis of specific individuals.

For overlap analysis (Fig. 2 except panel B), CDR3 properties analysis (Fig. 3, Fig. S7), clonal group analysis (Fig. 4) we used pooled data on all cancers, unless it is indicated otherwise on the panel. For overlap analysis, we used Cytoscape graph (Fig. 2B) for one patient, mp3, to illustrate the findings that were made on pooled data. For other types of analysis, such as overlap between individual lymph nodes, or tumor fragments (Fig. 5, 6, 7 except panel F) pooled analysis is not possible due to the individual nature of the processes in question.

(2) The authors do not address how lacking their sampling is nor the distribution of clone sizes in different tissues/ individuals/ subsets. Without such a discussion it is not clear how tenuous or convincing their conclusions are.

(3) The short sequencing lengths limit the ability to exactly identify V and thus the germline root of clones, whose positions are mutated and clonal association of sequences. The authors appear to be aware of this as they often use the most common ancestor as the start of their analysis... however, again there are inconsistencies that are not clearly described in the text. in creating trees with change they defined roots as the putative germline and at least in most cases also in clone association although in some analyses potentially similar clones were collapsed into clonotypes. Again it is not clear when one method was used or the other and how the choice was made what to choose.

Here we can only state that we consistently used the approach described in the Methods section, which was the following:

First, the repertoires were clustered into clonal lineages using the criteria described in “Methods: Clonal lineage inference” Assuming that each clonotype sequence in the clonal lineage originated from the same ancestor, we try to recover the phylogeny. Please note that we refer to the individual BCR sequences as “clonotypes”, and to a group of clonotypes that presumably share a common ancestor - as “clonal lineage” or “clonal group”.

The phylogeny of B-cell hypermutations was inferred for each clonal lineage of size five or more using the maximum likelihood method and the GTR GAMMA nucleotide substitution model. To find the most recent common ancestor (MRCA) or “root” of the tree, we used an artificial outgroup constructed as a conjugate of germline segments V and J defined by MIXCR and added it to the clonal lineage. The D segment was excluded from the outgroup formation, as there was insufficient confidence in the germline annotations due to its short length and high level of mutations. The rest of the clonotypes were still analyzed in their original form with D segment in place. Deleting D segment from the outgroup simply eliminates the risk of biasing the phylogeny by missasigning D segment germline sequence to the outgroup. The MUSCLE tool was used for multiple sequence alignment and RAxML software was used to build and root phylogenetic trees.

(4) Beyond the statistical issues mentioned above: the unclear selection of individual examples for comparison and significance testing, the mixing of individuals and cancer types without clear identification, etc. there is in general a lack of coherence in the statistical analysis performed. specifically:

(a) the authors should choose one cutoff for significance (0.01 for instance) and then just mention when things are significant and when not. There is no need and it is confusing to add the p-value for every comparison. P-values are not good measures of effect size.

We corrected the figures and left p-values only where they are below significance threshold.

(b) the Bonferroni correction used is not well characterized. For an alpha of 0.01 in Figures 3 C and D how many tests were performed?

The number of tests performed that was used for Bonferroni-Holm correction equals the number of comparisons on the heatmap which makes it 39 for each heatmap on Fig 3C and 13 for Fig 3D.

Finally some minor issues -

(1) Not all acronyms are described, for instance, TME and TIL. The first time any acronym is used it should be spelled out.  -> Katya B- список сокращений

(2) The figure captions are not all there...

(a) there is no caption for Figure 3E.

corrected

(b) there are Figure 7 F and G panels but no Figure 7E panel and Figure F is described after Figure G.

corrected

(3) A few problems with wording -

(a) bottom paragraph of page 3 - instead of :

"different lymph nodes from one draining lymph node pool may be more or less involved"

Corrected to "different lymph nodes from one draining lymph node pool may be differentially involved"

(b) figure caption for figure 3a: instead of:

"CDR3 are on average significantly higher in tumor"

Corrected to "CDR3 are on average significantly longer in tumor"

Reviewer #3 (Recommendations For The Authors):

- FIG1A - Suggest expanding the legend to include more information on the computational analyses.

added

- PAGE SIX: Suggest adding a table or some text on patient characteristics. Numbers of unique clonotypes per sample etc. Are there differences in age/sex that need to be considered? Some clonotype information is available in S1 but some summary and statistics would be appreciated.

Added patient information as Supplementary table 2.

- PAGE SIX: F2 Metric, suggestion to explain why this was used vs. other metrics.

We expanded the following paragraph to include information about F2 metric and D metric, and the reason why we are using F2.

Repertoire data for each sample were split according to the immunoglobulin isotype, and the F2 metric was calculated for each isotype separately and plotted as an individual point. We used the repertoire overlap metric F2 (Сlonotype-wise sum of geometric mean frequencies of overlapping clonotypes), which accounts for both the number and frequency of overlapping clonotypes (Fig. 2A). As expected, significantly lower overlaps were observed between the IGH repertoires of peripheral blood and tumors compared to LN/tumor overlaps. The LN/PBMC overlap also tended to be lower, but the difference was not statistically significant. We also analyzed D metric, which represents the relative overlap diversity uninfluenced by clonotype frequency (Dij\=dij/(di*dj), where dij is the number of clonotypes present in both samples, while di and dj are the diversities of samples i and j respectively). The results for D metric are not shown, as they indicate a similar trend to that of F2 metric. This observation allows us to conclude that tumor IGH repertoires are more similar to the repertoires of tumor-draining LNs than to those of peripheral blood, both if clonotype frequency is taken into account, and when it is not.

- PAGE SIX: Make clear in the text that mp3 is a patient.

Added “melanoma patient mp3”

- PAGE EIGHT: Suggest explaining kidera factors at first use - not all readers will know what they are.

We expanded the following paragraph to add more information about Kidera factors:

To explore CDR-H3 physicochemical properties, we calculated the mean charge, hydropathy, predicted interaction strength, and Kidera factors 1 - 9 (kf1-kf9) for five central amino acids of the CDR-H3 region for the 100 most frequent clonotypes of each sample using VDJtools. Kidera factors are a set of scores which quantify physicochemical properties of protein sequences 61. 188 physical properties of the 20 amino acids are encoded using dimension reduction techniques, to yield 9 factors which are used to quantitatively characterize physicochemical properties of amino acid sequences.

- Fig 5D is not referred to.

Corrected

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary: 

Kroeg et al. describe a novel method for 2D culture human induced pluripotent stem cells (hiPSCs) to form cortical tissue in a multiwell format. The method claims to offer a significant advancement over existing developmental models. Their approach allows them to generate cultures with precise, reproducible dimensions and structure with a single rosette; consistent geometry; incorporating multiple neuronal and glial cell types (cellular diversity); avoiding the necrotic core (often seen in free-floating models due to limited nutrient and oxygen diffusion). The researchers demonstrate the method's capacity for long-term culture, exceeding ten months, and show the formation of mature dendritic spines and considerable neuronal activity. The method aims to tackle multiple key problems of in vitro neural cultures: reproducibility, diversity, topological consistency, and electrophysiological activity. The authors suggest their potential in high-throughput screening and neurotoxicological studies.

Strengths: 

The main advances in the paper seem to be: The culture developed by the authors appears to have optimal conditions for neural differentiation, lineage diversification, and long-term culture beyond 300 days. These seem to me as a major strength of the paper and an important contribution to the field. The authors present solid evidence about the high cell type diversity present in their cultures. It is a major point and therefore it could be better compared to the state of the art. I commend the authors for using three different IPS lines, this is a very important part of their proof. The staining and imaging quality of the manuscript is of excellent quality.

We thank the reviewer for the positive comments on the potential of our novel platform to address key problems of in vitro neural culture, highlighting the longevity and reproducibility of the method across multiple cell lines.

Weaknesses: 

(1) The title is misleading: The presented cultures appear not to be organoids, but 2D neural cultures, with an insufficiently described intermediate EB stage. For nomenclature, see: doi: 10.1038/s41586-022-05219-6. Should the tissue develop considerable 3D depth, it would suffer from the same limited nutrient supply as 3D models - as the authors point out in their introduction. 

We appreciate the opportunity to clarify this point. We respectfully disagree that the cultures do not meet the consensus definition of an organoid. In fact, a direct quote from the seminal nomenclature paper referenced by the reviewer states: “We define organoids as in vitro-generated cellular systems that emerge by self-organization, include multiple cell types, and exhibit some cytoarchitectural and functional features reminiscent of an organ or organ region. Organoids can be generated as 3D cultures or by a combination of 3D and 2D approaches (also known as 2.5D) that can develop and mature over long periods of time (months to years).” (Pasca et al, 2022 doi10.1038/s41586-022-05219-6). Therefore, while many organoid types indeed have a more spherical or globular 3D shape, the term organoid also applies to semi-3D or non-globular adherent organoids, such as renal (Czerniecki et al 2018, doi.org/10.1016/j.stem.2018.04.022) and gastrointestinal organoids (Kakni et al 2022, doi.org/10.1016/j.tibtech.2022.01.006). Accordingly, the adherent cortical organoids described in the manuscript exhibit self-organization to single radial structures consisting of multiple cell layers in the z-axis, reaching ~200um thickness (therefore remaining within the limits for sufficient nutrient supply), with consistent cytoarchitectural topology and electrophysiological activity, and therefore meet the consensus definition of an organoid.

(2) The method therefore should be compared to state-of-the-art (well-based or not) 2D cultures, which seems to be somewhat overlooked in the paper, therefore making it hard to assess what the advance is that is presented by this work. 

It was not our intention to benchmark this model quantitatively against other culture systems. Rather, we have attempted to characterize the opportunities and limitations of this approach, with a qualitative contrast to other culture methods. Compared to state-of-the-art 2D neural network cultures, adherent cortical organoids provide distinct advantages in:

(1) Higher order self-organized structure formation, including segregation of deeper and upper cortical layers.

(2) Longevity: adherent cortical organoids can be successfully kept in culture up to 1 year where 2D cultures typically deteriorate after 8-12 weeks.

(3) Maturity, including the formation of dendritic mushroom spines and robust electrophysiological activity.

(4) Cell type diversity including a more physiological ratio of inhibitory and excitatory neurons (10% GAD67+/NeuN+ neurons in adherent cortical organoids, vs 1% in 2D neural networks) and the emergence of oligodendrocyte lineage cells.

On the other hand, limitations of adherent cortical organoids compared to 2D neural network cultures are:

(1) Culture times for organoids are much longer than for 2D cultures and the method can therefore be more laborious and more expensive.

(2) Whole cell patch clamping is not easily feasible in the organoids because of the restricting dimensions of the 384well plates.

(3) Reproducibility is prominently claimed throughout the manuscript. However, it is challenging to assess this claim based on the data presented, which mostly contain single frames of unquantified, high-resolution images. There are almost no systematic quantifications presented. The ones present (Figure S1D, Figure 4) show very large variability. However, the authors show sets of images across wells (Figure S1B, Figure S3) which hint that in some important aspects, the culture seems reproducible and robust. 

We made considerable efforts to establish quantitative metrics to assess reproducibility. We applied a quantitative scoring system of single radial structures at different time points for multiple batches of all three lines as indicated in Figure S1D. This figure represents a comprehensive dataset in which each dot represents the average of a different batch of organoids containing 10-40 organoids per batch. To emphasize this, we will adapt the graph to better reflect the breadth of the dataset. Additional quantifications are given in Figure S2 for progenitor and layer markers for Line 1 and in Figure S5 for interneurons across all three lines, showing relatively low variability. That being said, we acknowledge the reviewer’s concerns and will modify the text to reduce the emphasis of this point, pending more extensive data addressing reproducibility across a wide range of parameters.

(4) What is in the middle? All images show markers in cells present around the center. The center however seems to be a dense lump of cells based on DAPI staining. What is the identity of these cells? Do these cells persist throughout the protocol? Do they divide? Until when? Addressing this prominent cell population is currently lacking. 

A more comprehensive characterization of the cells in the center remains a significant challenge due to the high cell density hindering antibody penetration. However, dye-based staining methods such as DAPI and the LIVE/DEAD panel confirm a predominance of intact nuclei with very minimal cell death. The limited available data suggest that a substantial proportion of the cells in the center are proliferative neural progenitors, indicated by immunolabeling for SOX2 and Ki67. We will add additional figures to support these findings. Furthermore, we are currently optimizing the conditions to perform single cell / nuclear RNA sequencing to further characterize the cellular composition of the organoids.

(5) This manuscript proposes a new method of 2D neural culture. However, the description and representation of the method are currently insufficient. <br /> (a) The results section would benefit from a clear and concise, but step-by-step overview of the protocol. The current description refers to an earlier paper and appears to skip over some key steps. This section would benefit from being completely rewritten. This is not a replacement for a clear methods section, but a section that allows readers to clearly interpret results presented later.

We will revise the manuscript to include a more detailed step-by-step overview of the protocol.

(b) Along the same lines, the graphical abstract should be much more detailed. It should contain the time frames and the media used at the different stages of the protocol, seeding numbers, etc. 

As suggested, we will also adapt the graphical abstract to include more detail.

Reviewer #2 (Public Review): 

Summary: 

In this manuscript, van der Kroeg et al have developed a method for creating 3D cortical organoids using iPSC-derived neural progenitor cells in 384-well plates, thus scaling down the neural organoids to adherent culture and a smaller format that is amenable to high throughput cultivation. These adherent cortical organoids, measuring 3 x 3 x 0.2 mm, self-organize over eight weeks and include multiple neuronal subtypes, astrocytes, and oligodendrocyte lineage cells.

Strengths: 

(1) The organoids can be cultured for up to 10 months, exhibiting mature dendritic spines, axonal myelination, and robust neuronal activity. 

(2) Unlike free-floating organoids, these do not develop necrotic cores, making them ideal for high-throughput drug discovery, neurotoxicological screening, and brain disorder studies.

(3) The method addresses the technical challenge of achieving higher-order neural complexity with reduced heterogeneity and the issue of necrosis in larger organoids. The method presents a technical advance in organoid culture.

(4) The method has been demonstrated with multiple cell lines which is a strength. 

(5) The manuscript provides high-quality immunostaining for multiple markers. 

We appreciate the reviewer’s acknowledgement of the strengths of this novel platform as a technical advance in organoid culture that reduces heterogeneity and shows potential for higher throughput experiments.

Weaknesses: 

(1) Direct head-to-head comparison with standard organoid culture seems to be missing and may be valuable for benchmarking, ie what can be done with the new method that cannot be done with standard culture and vice versa, ie what are the aspects in which new method could be inferior to the standard.

In our opinion, it would be extremely difficult to directly compare methods because of substantial differences. Most notably, whole brain organoids grow to large and irregular globular shapes, while adherent cortical organoids have a highly standardized shape confined by the limits of a 384-well. Moreover, it was not our intention to benchmark this model quantitatively against other culture systems. Rather, we have attempted to characterize the opportunities and limitations of this approach, with a qualitative contrast to other culture methods.

(2) It would be important to further benchmark the throughput, ie what is the success rate in filling and successfully growing the organoids in the entire 384 well plate? 

Figure S1D shows the success rate of organoid formation and stability of the organoid structures over time. In addition, we will add the number of wells that were filled per plate.

(3) For each NPC line an optimal seeding density was estimated based on the proliferation rate of that NPC line and via visual observation after 6 weeks of culture. It would be important to delineate this protocol in more robust terms, in order to enable reproducibility with different cell lines and amongst the labs. 

Figure S1C provides the relationship between proliferation rate and seeding density, allowing estimation of seeding densities based on the proliferation rate of the NPCs. However, we appreciate the reviewers feedback and will modify the methods to provide more detail.

Reviewer #3 (Public Review): 

Summary: 

Kroeg et al. have introduced a novel method to produce 3D cortical layer formation in hiPSC-derived models, revealing a remarkably consistent topography within compact dimensions. This technique involves seeding frontal cortex-patterned iPSC-derived neural progenitor cells in 384-well plates, triggering the spontaneous assembly of adherent cortical organoids consisting of various neuronal subtypes, astrocytes, and oligodendrocyte lineage cells. 

Strengths: 

Compared to existing brain organoid models, these adherent cortical organoids demonstrate enhanced reproducibility and cell viability during prolonged culture, thereby providing versatile opportunities for high-throughput drug discovery, neurotoxicological screening, and the investigation of brain disorder pathophysiology. This is an important and timely issue that needs to be addressed to improve the current brain organoid systems. 

We thank the reviewer for highlighting the strengths of our novel platform. We appreciate that all three reviewers agree that the adherent cortical organoids presented in this manuscript reliably demonstrate increased reproducibility and longevity. They also commend its potential for higher throughput drug discovery and neurotoxicological/phenotype screening purposes.

Weaknesses: 

While the authors have provided significant data supporting this claim, several aspects necessitate further characterization and clarification. Mainly, highlighting the consistency of differentiation across different cell lines and standardizing functional outputs are crucial elements to emphasize the future broad potential of this new organoid system for large-scale pharmacological screening.

We appreciate the feedback and will add more detail on consistency and standardization of functional outputs.

Author response:

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

To the Senior Editor and the Reviewing Editor:

We sincerely appreciate the valuable comments provided by the reviewers, the reviewing editor, and the senior editor. Based on our last response and revision, we are confused by the two limitations noted in the eLife assessment. 

(1) benchmarking against comparable methods is limited.

In our last revision, we added the comparison experiments with TNDM, as the reviewers requested. Additionally, it is crucial to emphasize that our evaluation of decoding capabilities of behaviorally relevant signals has been benchmarked against the performance of the ANN on raw signals, which, as Reviewer #1 previously noted, nearly represents the upper limit of performance. Consequently, we believe that our benchmarking methods are sufficiently strong.

(2) some observations may be a byproduct of their method, and may not constitute new scientific observations.

We believe that our experimental results are sufficient to demonstrate that our conclusions are not byproducts of d-VAE based on three reasons:

(1) The d-VAE, as a latent variable model, adheres to the population doctrine, which posits that latent variables are responsible for generating the activities of individual neurons. The goal of such models is to maximize the explanation of the raw signals. At the signal level, the only criterion we can rely on is neural reconstruction performance, in which we have achieved unparalleled results. Thus, it is inappropriate to focus on the mixing process during the model's inference stage while overlooking the crucial de-mixing process during the generation stage and dismissing the significance of our neural reconstruction results. For more details, please refer to the first point in our response to Q4 from Reviewer #4.

(2) The criterion that irrelevant signals should contain minimal information can effectively demonstrate that our conclusions are not by-products of d-VAE. Unfortunately, the reviewers seem to have overlooked this criterion. For more details, please refer to the third point in our response to Q4 from Reviewer #4

(3) Our synthetic experimental results also substantiate that our conclusions are not byproducts of d-VAE. However, it appears the reviewers did not give these results adequate consideration. For more details, please refer to the fourth point in our response to Q4 from Reviewer #4.

Furthermore, our work presents not just "a useful method" but a comprehensive framework. Our study proposes, for the first time, a framework for defining, extracting, and validating behaviorally relevant signals. In our current revision, to clearly distinguish between d-VAE and other methods, we have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem. To our knowledge, current methods have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals. Similarly, existing research has not yet defined and validated behaviorally relevant signals. For more details, please refer to our response to Q1 from Reviewer #4.

Based on these considerations, we respectfully request that you reconsider the eLife assessment of our work. We greatly appreciate your time and attention to this matter.

The main revisions made to the manuscript are as follows:

(1) We have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem, enabling a clearer distinction between d-VAE and other models.

(2) We have moderated the assertion about linear readout to highlight its conjectural nature and have broadened the discussion regarding this conclusion. 

(3) We have elaborated on the model details of d-VAE and have removed the identifiability claim.

To Reviewer #1

Q1: “As reviewer 3 also points out, I would, however, caution to interpret this as evidence for linear read-out of the motor system - your model performs a non-linear transformation, and while this is indeed linearly decodable, the motor system would need to do something similar first to achieve the same. In fact to me it seems to show the opposite, that behaviour-related information may not be generally accessible to linear decoders (including to down-stream brain areas).”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by linear decoders or downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our opinion, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

Q2: “As in my initial review, I would also caution against making strong claims about identifiability although this work and TNDM seem to show that in practise such methods work quite well. CEBRA, in contrast, offers some theoretical guarantees, but it is not a generative model, so would not allow the type of analysis done in this paper. In your model there is a para,eter \alpha to balance between neural and behaviour reconstruction. This seems very similar to TNDM and has to be optimised - if this is correct, then there is manual intervention required to identify a good model.”

Thank you for your comments. 

Considering your concerns about our identifiability claims and the fact that identifiability is not directly relevant to the core of our paper, we have removed content related to identifiability.

Firstly, our model is based on the pi-VAE, which also has theoretical guarantees. However, it is important to note that all such theoretical guarantees (including pi-VAE and CEBRA) are based on certain assumptions that cannot be validated as the true distribution of latent variables remains unknown.

Secondly, it is important to clarify that the identifiability of latent variables does not impact the conclusions of this paper, nor does this paper make specific conclusions about the model's latent variables. Identifiability means that distinct latent variables correspond to distinct observations. If multiple latent variables can generate the same observation, it becomes impossible to determine which one is correct given the observation, which leads to the issue of nonidentifiability. Notably, our analysis focuses on the generated signals, not the latent variables themselves, and thus the identifiability of these variables does not affect our findings. 

Our approach, dedicated to extracting these signals, distinctly differs from methods such as TNDM, which focuses on extracting behaviorally relevant latent dynamics. To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝑥# denotes generated behaviorally-relevant signals, 𝑥 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓).  Other studies have not explicitly proposed extracting behaviorally-relevant signals, nor have they identified and addressed the key challenges involved in extracting relevant signals. Consequently, our approach is distinct from other methods.

Thank you for your valuable feedback.

Q3: “Somewhat related, I also found that the now comprehensive comparison with related models shows that the using decoding performance (R2) as a metric for model comparison may be problematic: the R2 values reported in Figure 2 (e.g. the MC_RTT dataset) should be compared to the values reported in the neural latent benchmark, which represent well-tuned models (e.g. AutoLFADS). The numbers (difficult to see, a table with numbers in the appendix would be useful, see: https://eval.ai/web/challenges/challenge-page/1256/leaderboard) seem lower than what can be obtained with models without latent space disentanglement. While this does not necessarily invalidate the conclusions drawn here, it shows that decoding performance can depend on a variety of model choices, and may not be ideal to discriminate between models. I'm also surprised by the low neural R2 for LFADS I assume this is condition-averaged) - LFADS tends to perform very well on this metric.”

Thank you for your comments. The dataset we utilized is not from the same day as the neural latent benchmark dataset. Notably, there is considerable variation in the length of trials within the RTT paradigm, and the dataset lacks explicit trial information, rendering trial-averaging unsuitable. Furthermore, behaviorally relevant signals are not static averages devoid of variability; even behavioral data exhibits variability. We computed the neural R2 using individual trials rather than condition-averaged responses. 

Thank you for your valuable feedback.

Q4: “One statement I still cannot follow is how the prior of the variational distribution is modelled. You say you depart from the usual Gaussian prior, but equation 7 seems to suggest there is a normal prior. Are the parameters of this distribution learned? As I pointed out earlier, I however suspect this may not matter much as you give the prior a very low weight. I also still am not sure how you generate a sample from the variational distribution, do you just draw one for each pass?”

Thank you for your questions.

The conditional distribution of prior latent variables 𝑝%(𝒛|𝒚) is a Gaussian distribution, but the distribution of prior latent variables 𝑝(𝒛) is a mixture Gaussian distribution. The distribution of prior latent variables 𝑝(𝒛) is:

where denotes the empirical distribution of behavioral variables

𝒚, and 𝑁 denotes the number of samples, 𝒚(𝒊) denotes the 𝒊th sample, δ(⋅) denotes the Dirac delta function, and 𝑝%(𝒛|𝒚) denotes the conditional distribution of prior latent variables given the behavioral variables parameterized by network 𝑚. Based on the above equation, we can see that 𝑝(𝒛) is not a Gaussian distribution, it is a Gaussian mixture model with 𝑁 components, which is theoretically a universal approximator of continuous probability densities.

Learning this prior is important, as illustrated by our latent variable visualizations, which are not a Gaussian distribution. Upon conducting hypothesis testing for both latent variables and behavioral variables, neither conforms to Gaussian distribution (Lilliefors test and Kolmogorov-Smirnov test). Consequently, imposing a constraint on the latent variables towards N(0,1) is expected to affect performance adversely.

Regarding sampling, during training process, we draw only one sample from the approximate posterior distribution . It is worth noting that drawing multiple samples or one sample for each pass does not affect the experimental results. After training, we can generate a sample from the prior by providing input behavioral data 𝒚(𝒊) and then generating corresponding samples via and . To extract behaviorally-relevant signals from raw signals, we use and .

Thank you for your valuable feedback.

Q5: “(1) I found the figures good and useful, but the text is, in places, not easy to follow. I think the manuscript could be shortened somewhat, and in some places more concise focussed explanations would improve readability.

(2) I would not call the encoding "complex non-linear" - non-linear is a clear term, but complex can mean many things (e.g. is a quadratic function complex?) ”

Thank you for your recommendation. We have revised the manuscript for enhanced clarity.  We call the encoding “complex nonlinear” because neurons encode information with varying degrees of nonlinearity, as illustrated in Fig. 3b, f, and Fig. S3b.

Thank you for your valuable feedback.

To Reviewer #2

Q1: “I still remain unconvinced that the core findings of the paper are "unexpected". In the response to my previous Specific Comment #1, they say "We use the term 'unexpected' due to the disparity between our findings and the prior understanding concerning neural encoding and decoding." However, they provide no citations or grounding for why they make those claims. What prior understanding makes it unexpected that encoding is more complex than decoding given the entropy, sparseness, and high dimensionality of neural signals (the "encoding") compared to the smoothness and low dimensionality of typical behavioural signals (the "decoding")?” 

Thank you for your comments. We believe that both the complexity of neural encoding and the simplicity of neural decoding in motor cortex are unexpected.

The Complexity of Neural Encoding: As noted in the Introduction, neurons with small R2 values were traditionally considered noise and consequently disregarded, as detailed in references [1-3]. However, after filtering out irrelevant signals, we discovered that these neurons actually contain substantial amounts of behavioral information, previously unrecognized. Similarly, in population-level analyses, neural signals composed of small principal components (PCs) are often dismissed as noise, with analyses typically utilizing only between 6 and 18 PCs [4-10]. Yet, the discarded PC signals nonlinearly encode significant amounts of information, with practically useful dimensions found to range between 30 and 40—far exceeding the usual number analyzed. These findings underscore the complexity of neural encoding and are unexpected.

The Simplicity of Neural Decoding: In the motor cortex, nonlinear decoding of raw signals has been shown to significantly outperform linear decoding, as evidenced in references [11,12]. Interestingly, after separating behaviorally relevant and irrelevant signals, we observed that the linear decoding performance of behaviorally relevant signals is nearly equivalent to that of nonlinear decoding—a phenomenon previously undocumented in the motor cortex. This discovery is also unexpected.

Thank you for your valuable feedback.

(1) Georgopoulos, Apostolos P., Andrew B. Schwartz, and Ronald E. Kettner. "Neuronal population coding of movement direction." Science 233.4771 (1986): 1416-1419.

(2) Hochberg, Leigh R., et al. "Reach and grasp by people with tetraplegia using a neurally controlled robotic arm." Nature 485.7398 (2012): 372-375. 

(3) Inoue, Yoh, et al. "Decoding arm speed during reaching." Nature communications 9.1 (2018): 5243.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(7) Sadtler, Patrick T., et al. "Neural constraints on learning." Nature 512.7515 (2014): 423426.

(8) Golub, Matthew D., et al. "Learning by neural reassociation." Nature neuroscience 21.4 (2018): 607-616.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

(11) Glaser, Joshua I., et al. "Machine learning for neural decoding." Eneuro 7.4 (2020).

(12) Willsey, Matthew S., et al. "Real-time brain-machine interface in non-human primates achieves high-velocity prosthetic finger movements using a shallow feedforward neural network decoder." Nature Communications 13.1 (2022): 6899.

Q2: “I still take issue with the premise that signals in the brain are "irrelevant" simply because they do not correlate with a fixed temporal lag with a particular behavioural feature handchosen by the experimenter. In the response to my previous review, the authors say "we employ terms like 'behaviorally-relevant' and 'behaviorally-irrelevant' only regarding behavioral variables of interest measured within a given task, such as arm kinematics during a motor control task.". This is just a restatement of their definition, not a response to my concern, and does not address my concern that the method requires a fixed temporal lag and continual decoding/encoding. My example of reward signals remains. There is a huge body of literature dating back to the 70s on the linear relationships between neural and activity and arm kinematics; in a sense, the authors have chosen the "variable of interest" that proves their point. This all ties back to the previous comment: this is mostly expected, not unexpected, when relating apparently-stochastic, discrete action potential events to smoothly varying limb kinematics.”

Thank you for your comments. 

Regarding the experimenter's specification of behavioral variables of interest, we followed common practice in existing studies [1, 2]. Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [3-5]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [68].

Concerning the issue of rewards, in the paper you mentioned [9], the impact of rewards occurs after the reaching phase. It's important to note that in our experiments, we analyze only the reaching phase, without any post-movement phase. 

If the impact of rewards can be stably reflected in the signals in the reaching phase of the subsequent trial, and if the reward-induced signals do not interfere with decoding—since these signals are harmless for decoding and beneficial for reconstruction—our model is likely to capture these signals. If the signals induced by rewards during the reaching phase are randomly unstable, our model will likely be unable to capture them.

If the goal is to extract post-movement neural activity from both rewarded and unrewarded trials, and if the neural patterns differ between these conditions, one could replace the d-VAE's regression loss, used for continuous kinematics decoding, with a classification loss tailored to distinguish between rewarded and unrewarded conditions.

To clarify the definition, we have revised it in the manuscript. Specifically, before a specific definition, we briefly introduce the relevant signals and irrelevant signals. Behaviorally irrelevant signals refer to those not directly associated with the behavioral variables of interest and may include noise or signals from variables of no interest. In contrast, behaviorally relevant signals refer to those directly related to the behavioral variables of interest. For instance, rewards in the post-movement phase are not directly related to behavioral variables (kinematics) in the reaching movement phase.

It is important to note that our definition of behaviorally relevant signals not only includes decoding capabilities but also specific requirement at the signal level, based on two key requirements:

(1) they should closely resemble raw signals to preserve the underlying neuronal properties without becoming so similar that they include irrelevant signals. (encoding requirement), and  (2) they should contain behavioral information as much as possible (decoding requirement). Signals that meet both requirements are considered effective behaviorally relevant signals. In our study, we assume raw signals are additively composed of behaviorally-relevant and irrelevant signals. We define irrelevant signals as those remaining after subtracting relevant signals from raw signals. Therefore, we believe our definition is clearly articulated. 

Thank you for your valuable feedback.

(1) Sani, Omid G., et al. "Modeling behaviorally relevant neural dynamics enabled by preferential subspace identification." Nature Neuroscience 24.1 (2021): 140-149.

(2) Buetfering, Christina, et al. "Behaviorally relevant decision coding in primary somatosensory cortex neurons." Nature neuroscience 25.9 (2022): 1225-1236.

(3) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(4) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(5) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(6) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(7) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(8) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(9) Ramkumar, Pavan, et al. "Premotor and motor cortices encode reward." PloS one 11.8 (2016): e0160851.

Q3: “The authors seem to have missed the spirit of my critique: to say "linear readout is performed in motor cortex" is an over-interpretation of what their model can show.”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our view, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Regarding the question of whether the brain employs linear readout, given the limitations of current observational methods and our incomplete understanding of brain mechanisms, it is challenging to ascertain whether the brain employs a linear readout. In many cortical areas, linear decoders have proven to be sufficiently accurate. Consequently, numerous studies [4, 5, 6], including the one you referenced [4], directly employ linear decoders to extract information and formulate conclusions based on the decoding results. Contrary to these approaches, our research has compared the performance of linear and nonlinear decoders on behaviorally relevant signals and found their decoding performance is comparable. Considering both the decoding accuracy and model complexity, our results suggest that the motor cortex may utilize linear readout to decode information from relevant signals. Given the current technological limitations, we consider it reasonable to analyze collected data to speculate on the potential workings of the brain, an approach that many studies have also embraced [7-10]. For instance, a study [7] deduces strategies the brain might employ to overcome noise by analyzing the structure of recorded data and decoding outcomes for new stimuli.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

(4) Jurewicz, Katarzyna, et al. "Irrational choices via a curvilinear representational geometry for value." bioRxiv (2022): 2022-03.

(5) Hong, Ha, et al. "Explicit information for category-orthogonal object properties increases along the ventral stream." Nature neuroscience 19.4 (2016): 613-622.

(6) Chang, Le, and Doris Y. Tsao. "The code for facial identity in the primate brain." Cell 169.6 (2017): 1013-1028.

(7) Ganmor, Elad, Ronen Segev, and Elad Schneidman. "A thesaurus for a neural population code." Elife 4 (2015): e06134.

(8) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

Q4: “Agreeing with my critique is not sufficient; please provide the data or simulations that provides the context for the reference in the fano factor. I believe my critique is still valid.”

Thank you for your comments. As we previously replied, Churchland's research examines the variability of neural signals across different stages, including the preparation and execution phases, as well as before and after the target appears. Our study, however, focuses exclusively on the movement execution phase. Consequently, we are unable to produce comparative displays similar to those in his research. Intuitively, one might expect that the variability of behaviorally relevant signals would be lower; however, since no prior studies have accurately extracted such signals, the specific FF values of behaviorally relevant signals remain unknown. Therefore, presenting these values is meaningful, and can provide a reference for future research. While we cannot compare FF across different stages, we can numerically compare the values to the Poisson count process. An FF of 1 indicates a Poisson firing process, and our experimental data reveals that most neurons have an FF less than 1, indicating that the variance in firing counts is below the mean.  Thank you for your valuable feedback.

To Reviewer #4

Q1: “Overall, studying neural computations that are behaviorally relevant or not is an important problem, which several previous studies have explored (for example PSID in (Sani et al. 2021), TNDM in (Hurwitz et al. 2021), TAME-GP in (Balzani et al. 2023), pi-VAE in (Zhou and Wei 2020), and dPCA in (Kobak et al. 2016), etc). However, this manuscript does not properly put their work in the context of such prior works. For example, the abstract states "One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive", which is not the case given that these prior works have done that. The same is true for various claims in the main text, for example "Furthermore, we found that the dimensionality of primary subspace of raw signals (26, 64, and 45 for datasets A, B, and C) is significantly higher than that of behaviorally-relevant signals (7, 13, and 9), indicating that using raw signals to estimate the neural dimensionality of behaviors leads to an overestimation" (line 321). This finding was presented in (Sani et al. 2021) and (Hurwitz et al. 2021), which is not clarified here. This issue of putting the work in context has been brought up by other reviewers previously but seems to remain largely unaddressed. The introduction is inaccurate also in that it mixes up methods that were designed for separation of behaviorally relevant information with those that are unsupervised and do not aim to do so (e.g., LFADS). The introduction should be significantly revised to explicitly discuss prior models/works that specifically formulated this behavior separation and what these prior studies found, and how this study differs.”  

Thank you for your comments. Our statement about “One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive” is accurate. To our best knowledge, there is no prior works to do this work--- separating accurate behaviorally relevant neural signals at both single-neuron and single-trial resolution. The works you mentioned have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals, namely determining the optimal degree of similarity between the generated relevant signals and raw signals. Those works focus on the latent neural dynamics, rather than signal level.

To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝒙𝒓 denotes generated behaviorally-relevant signals, 𝒙 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓). All the works you mentioned did not have the key part 𝑅(𝒙𝒓).

Regarding the dimensionality estimation, the dimensionality of neural manifolds quantifies the degrees of freedom required to describe population activity without significant information loss.

There are two differences between our work and PSID and TNDM. 

First, the dimensions they refer to are fundamentally different from ours. The dimensionality we describe pertains to a linear subspace, where a neural dimension or neural mode or principal component basis, , with N representing the number of neurons. However, the vector length of a neural mode of PSID and our approach differs; PSID requires concatenating multiple time steps T, essentially making , TNDM, on the other hand, involves nonlinear dimensionality reduction, which is different from linear dimensionality reduction.

Second, we estimate neural dimensionality by explaining the variance of neural signals, whereas PSID and TNDM determine dimensionality through decoding performance saturation. It is important to note that the dimensionality at which decoding performance saturates may not accurately reflect the true dimensionality of neural manifolds, as some dimensions may contain redundant information that does not enhance decoding performance.

We acknowledge that while LFADS can generate signals that contain some behavioral information, it was not specifically designed to do so. Following your suggestion, we have removed this reference from the Introduction.

Thank you for your valuable feedback.

Q2: “Claims about linearity of "motor cortex" readout are not supported by results yet stated even in the abstract. Instead, what the results support is that for decoding behavior from the output of the dVAE model -- that is trained specifically to have a linear behavior readout from its embedding -- a nonlinear readout does not help. This result can be biased by the very construction of the dVAE's loss that encourages a linear readout/decoding from embeddings, and thus does not imply a finding about motor cortex.”

Thank you for your comments. We respectfully disagree with the notion that the ability of relevant signals to be linearly decoded is due to constraints that allow embedding to be linearly decoded. Embedding involves reorganizing or transforming the structure of original signals, and they can be linearly decoded does not mean the corresponding signals can be decoded linearly.

Let's clarify this with three intuitive examples:

Example 1: Image denoising is a well-established field. Whether employing supervised or blind denoising methods [1, 2], both can effectively recover the original image. This denoising process closely resembles the extraction of behaviorally relevant signals from raw signals. Consider if noisy images are not amenable to linear decoding (classification); would removing the noise enable linear decoding? The answer is no. Typically, the noise in images captured under normal conditions is minimal, yet even the clear images remain challenging to decode linearly.

Example 2: Consider the task of face recognition, where face images are set against various backgrounds, in this context, the pixels representing the face corresponds to relevant signals, while the background pixels are considered irrelevant. Suppose a network is capable of extracting the face pixels and the resulting embedding can be linearly decoded. Can the face pixels themselves be linearly decoded? The answer is no. If linear decoding of face pixels were feasible, the challenging task of face recognition could be easily resolved by merely extracting the face from the background and training a linear classifier.

Example 3: In the MNIST dataset, the background is uniformly black, and its impact is minimal. However, linear SVM classifiers used directly on the original pixels significantly underperform compared to non-linear SVMs.

In summary, embedding involves reorganizing the structure of the original signals through a feature transformation function. However, the reconstruction process can recover the structure of the original signals from the embedding. The fact that the structure of the embedding can be linearly decoded does not imply that the structure of the original signals can be linearly decoded in the same way. It is inappropriate to focus on the compression process without equally considering the reconstruction process.

Thank you for your valuable feedback.

(1) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(2) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

Q3: “Related to the above, it is unclear what the manuscript means by readout from motor cortex. A clearer definition of "readout" (a mapping from what to what?) in general is needed. The mapping that the linearity/nonlinearity claims refer to is from the *inferred* behaviorally relevant neural signals, which themselves are inferred nonlinearly using the VAE. This should be explicitly clarified in all claims, i.e., that only the mapping from distilled signals to behavior is linear, not the whole mapping from neural data to behavior. Again, to say the readout from motor cortex is linear is not supported, including in the abstract.” 

Thank you for your comments. We have revised the manuscript to make it more clearly. Thank you for your valuable feedback.

Q4: “Claims about individual neurons are also confounded. The d-VAE distilling processing is a population level embedding so the individual distilled neurons are not obtainable on their own without using the population data. This population level approach also raises the possibility that information can leak from one neuron to another during distillation, which is indeed what the authors hope would recover true information about individual neurons that wasn't there in the recording (the pixel denoising example). The authors acknowledge the possibility that information could leak to a neuron that didn't truly have that information and try to rule it out to some extent with some simulations and by comparing the distilled behaviorally relevant signals to the original neural signals. But ultimately, the distilled signals are different enough from the original signals to substantially improve decoding of low information neurons, and one cannot be sure if all of the information in distilled signals from any individual neuron truly belongs to that neuron. It is still quite likely that some of the improved behavior prediction of the distilled version of low-information neurons is due to leakage of behaviorally relevant information from other neurons, not the former's inherent behavioral information. This should be explicitly acknowledged in the manuscript.”

Thank you for your comments. We value your insights regarding the mixing process. However, we are confident in the robustness of our conclusions. We respectfully disagree with the notion that the small R2 values containing significant information are primarily due to leakage, and we base our disagreement on four key reasons.

(1) Neural reconstruction performance is a reliable and valid criterion.

The purpose of latent variable models is to explain neuronal activity as much as possible. Given the fact that the ground truth of behaviorally-relevant signals, the latent variables, and the generative model is unknow, it becomes evident that the only reliable reference at the signal level is the raw signals. A crucial criterion for evaluating the reliability of latent variable models (including latent variables and generated relevant signals) is their capability to effectively explain the raw signals [1]. Consequently, we firmly maintain the belief that if the generated signals closely resemble the raw signals to the greatest extent possible, in accordance with an equivalence principle, we can claim that these obtained signals faithfully retain the inherent properties of single neurons. 

Reviewer #4 appears to focus on the compression (mixing) process without giving equal consideration to the reconstruction (de-mixing) process. Numerous studies have demonstrated that deep autoencoders can reconstruct the original signal very effectively. For example, in the field of image denoising, autoencoders are capable of accurately restoring the original image [2, 3]. If one persistently focuses on the fact of mixing and ignores the reconstruction （demix） process, even if the only criterion that we can rely on at the signal level is high, one still won't acknowledge it. If this were the case, many problems would become unsolvable. For instance, a fundamental criterion for latent variable models is their ability to explain the original data. If the ground truth of the latent variables remains unknown and the reconstruction criterion is disregarded, how can we validate the effectiveness of the model, the validity of the latent variables, or ensure that findings related to latent variables are not merely by-products of the model? Therefore, we disagree with the aforementioned notion. We believe that as long as the reconstruction performance is satisfactory, the extracted signals have successfully retained the characteristics of individual neurons.

In our paper, we have shown in various ways that our generated signals sufficiently resemble the raw signals, including visualizing neuronal activity (Fig. 2m, Fig. 3i, and Fig. S5), achieving the highest performance among competitors (Fig. 2d, h, l), and conducting control analyses. Therefore, we believe our results are reliable. 

(1) Cunningham, J.P. and Yu, B.M., 2014. Dimensionality reduction for large-scale neural recordings. Nature neuroscience, 17(11), pp.1500-1509.

(2) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(3) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

(2) There is no reason for d-VAE to add signals that do not exist in the original signals.

(1) Adding signals that does not exist in the small R2 neurons would decrease the reconstruction performance. This is because if the added signals contain significant information, they will not resemble the irrelevant signals which contain no information, and thus, the generated signals will not resemble the raw signals. The model optimizes towards reducing the reconstruction loss, and this scenario deviates from the model's optimization direction. It is worth mentioning that when the model only has reconstruction loss without the interference of decoding loss, we believe that information leakage does not happen. Because the model can only be optimized in a direction that is similar to the raw signals; adding non-existent signals to the generated signals would increase the reconstruction loss, which is contrary to the objective of optimization. 

(2) Information carried by these additional signals is redundant for larger R2 neurons, thus they do not introduce new information that can enhance the decoding performance of the neural population, which does not benefit the decoding loss.

Based on these two points, we believe the model would not perform such counterproductive and harmful operations.

(3) The criterion that irrelevant signals should contain minimal information can effectively rule out the leakage scenario.

The criterion that irrelevant signals should contain minimal information is very important, but it seems that reviewer #4 has continuously overlooked their significance. If the model's reconstruction is insufficient, or if additional information is added (which we do not believe will happen), the residuals would decode a large amount of information, and this criterion would exclude selecting such signals. To clarify, if we assume that x, y, and z denote the raw, relevant, and irrelevant signals of smaller R2 neurons, with x=y+z, and the extracted relevant signals become y+m, the irrelevant signals become z-m in this case. Consequently, the irrelevant signals contain a significant amount of information.

We presented the decoding R2 for irrelevant signals in real datasets under three distillation scenarios: a bias towards reconstruction (alpha=0, an extreme case where the model only has reconstruction loss without decoding loss), a balanced trade-off, and a bias towards decoding (alpha=0.9), as detailed in Table 1. If significant information from small R2 neurons leaks from large R2 neurons, the irrelevant signals should contain a large amount of information. However, our results indicate that the irrelevant signals contain only minimal information, and their performance closely resembles that of the model training solely with reconstruction loss, showing no significant differences (P > 0.05, Wilcoxon rank-sum test). When the model leans towards decoding, some useful information will be left in the residuals, and irrelevant signals will contain a substantial amount of information, as observed in Table 1, alpha=0.9. Therefore, we will not choose these signals for analysis.

In conclusion, the criterion that irrelevant signals should contain minimal information is a very effective measure to exclude undesirable signals.

Author response table 1.

Decoding R2 of irrelevant signals

(4) Synthetic experiments can effectively rule out the leakage scenario.

In the absence of ground truth data, synthetic experiments serve as an effective method for validating models and are commonly employed [1-3]. 

Our experimental results demonstrate that d-VAE can effectively extract neural signals that more closely resemble actual behaviorally relevant signals (Fig. S2g).  If there were information leakage, it would decrease the similarity to the ground truth signals, hence we have ruled out this possibility. Moreover, in synthetic experiments with small R2 neurons (Fig. S10), results also demonstrate that our model could make these neurons more closely resemble ground truth relevant signals and recover their information. 

In summary, synthetic experiments strongly demonstrate that our model can recover obscured neuronal information, rather than adding signals that do not exist.

(1) Pnevmatikakis, Eftychios A., et al. "Simultaneous denoising, deconvolution, and demixing of calcium imaging data." Neuron 89.2 (2016): 285-299.

(2) Schneider, Steffen, Jin Hwa Lee, and Mackenzie Weygandt Mathis. "Learnable latent embeddings for joint behavioural and neural analysis." Nature 617.7960 (2023): 360-368.

(3) Zhou, Ding, and Xue-Xin Wei. "Learning identifiable and interpretable latent models of high-dimensional neural activity using pi-VAE." Advances in Neural Information Processing Systems 33 (2020): 7234-7247.

Based on these four points, we are confident in the reliability of our results. If Reviewer #4 considers these points insufficient, we would highly appreciate it if specific concerns regarding any of these aspects could be detailed.

Thank you for your valuable feedback.

Q5: “Given the nuances involved in appropriate comparisons across methods and since two of the datasets are public, the authors should provide their complete code (not just the dVAE method code), including the code for data loading, data preprocessing, model fitting and model evaluation for all methods and public datasets. This will alleviate concerns and allow readers to confirm conclusions (e.g., figure 2) for themselves down the line.”

Thanks for your suggestion.

Our codes are now available on GitHub at https://github.com/eric0li/d-VAE. Thank you for your valuable feedback.

Q6: “Related to 1) above, the authors should explore the results if the affine network h(.) (from embedding to behavior) was replaced with a nonlinear ANN. Perhaps linear decoders would no longer be as close to nonlinear decoders. Regardless, the claim of linearity should be revised as described in 1) and 2) above, and all caveats should be discussed.”

Thank you for your suggestion. We appreciate your feasible proposal that can be empirically tested. Following your suggestion, we have replaced the decoding of the latent variable z to behavior y with a nonlinear neural network, specifically a neural network with a single hidden layer. The modified model is termed d-VAE2. We applied the d-VAE2 to the real data, and selected the optimal alpha through the validation set. As shown in Table 1, results demonstrate that the performance of KF and ANN remains comparable. Therefore, the capacity to linearly decode behaviorally relevant signals does not stem from the linear decoding of embeddings.

Author response table 2.

Decoding R2 of behaviorally relevant signals obtained by d-VAE2

Additionally, it is worth noting that this approach is uncommon and is considered somewhat inappropriate according to the Information Bottleneck theory [1]. According to the Information Bottleneck theory, information is progressively compressed in multilayer neural networks, discarding what is irrelevant to the output and retaining what is relevant. This means that as the number of layers increases, the mutual information between each layer's embedding and the model input gradually decreases, while the mutual information between each layer's embedding and the model output gradually increases. For the decoding part, if the embeddings that is not closest to the output (behaviors) is used, then these embeddings might contain behaviorally irrelevant signals. Using these embeddings to generate behaviorally relevant signals could lead to the inclusion of irrelevant signals in the behaviorally relevant signals.

To demonstrate the above statement, we conducted experiments on the synthetic data. As shown in Table 2, we present the performance (neural R2 between the generated signals and the ground truth signals) of both models at several alpha values around the optimal alpha of dVAE (alpha=0.9) selected by the validation set. The experimental results show that at the same alpha value, the performance of d-VAE2 is consistently inferior to that of d-VAE, and d-VAE2 requires a higher alpha value to achieve performance comparable to d-VAE, and the best performance of d-VAE2 is inferior to that of d-VAE.

Author response table 3.

Neural R2 between generated signals and real behaviorally relevant signals

Thank you for your valuable feedback.

(1) Shwartz-Ziv, Ravid, and Naftali Tishby. "Opening the black box of deep neural networks via information." arXiv preprint arXiv:1703.00810 (2017).

Q7: “The beginning of the section on the "smaller R2 neurons" should clearly define what R2 is being discussed. Based on the response to previous reviewers, this R2 "signifies the proportion of neuronal activity variance explained by the linear encoding model, calculated using raw signals". This should be mentioned and made clear in the main text whenever this R2 is referred to.”

Thank you for your suggestion. We have made the modifications in the main text. Thank you for your valuable feedback.

Q8: “Various terms require clear definitions. The authors sometimes use vague terminology (e.g., "useless") without a clear definition. Similarly, discussions regarding dimensionality could benefit from more precise definitions. How is neural dimensionality defined? For example, how is "neural dimensionality of specific behaviors" (line 590) defined? Related to this, I agree with Reviewer 2 that a clear definition of irrelevant should be mentioned that clarifies that relevance is roughly taken as "correlated or predictive with a fixed time lag". The analyses do not explore relevance with arbitrary time lags between neural and behavior data.”

Thanks for your suggestion. We have removed the “useless” statements and have revised the statement of “the neural dimensionality of specific behaviors” in our revised manuscripts.

Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [1-3]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [4-6]. To clarify the definition, we have revised the definition in our manuscript. For details, please refer to the response to Q2 of reviewer #2 and our revised manuscript. We believe our definition is clearly articulated.

Thank you for your valuable feedback.

(1) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(2) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(3) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239. 

Q9: “CEBRA itself doesn't provide a neural reconstruction from its embeddings, but one could obtain one via a regression from extracted CEBRA embeddings to neural data. In addition to decoding results of CEBRA (figure S3), the neural reconstruction of CEBRA should be computed and CEBRA should be added to Figure 2 to see how the behaviorally relevant and irrelevant signals from CEBRA compare to other methods.”

Thank you for your question. Modifying CEBRA is beyond the scope of our work. As CEBRA is not a generative model, it cannot obtain behaviorally relevant and irrelevant signals, and therefore it lacks the results presented in Fig. 2. To avoid the same confusion encountered by reviewers #3 and #4 among our readers, we have opted to exclude the comparison with CEBRA. It is crucial to note, as previously stated, that our assessment of decoding capabilities has been benchmarked against the performance of the ANN on raw signals, which almost represents the upper limit of performance. Consequently, omitting CEBRA does not affect our conclusions.

Thank you for your valuable feedback.

Q10: “Line 923: "The optimal hyperparameter is selected based on the lowest averaged loss of five-fold training data." => why is this explained specifically under CEBRA? Isn't the same criteria used for hyperparameters of other methods? If so, clarify.”

Thank you for your question. The hyperparameter selection for CEBRA follows the practice of the original CEBRA paper. The hyperparameter selection for generative models is detailed in the Section “The strategy for selecting effective behaviorally-relevant signals”.  Thank you for your valuable feedback.

Author response:

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

Reviewer #1 (Recommendations For The Authors): 

Major points: 

(1) A central question regarding VGCC differences at Is vs Ib active zones is why is calcium influx higher at Is active zones compared to Ib. Ideally, the authors would have started this study by showing correlations between Cac abundance, presynaptic calcium influx, and Pr at Is vs Ib active zones. If they had, they would likely find that Cac abundance scales with calcium influx and Pr within Is vs Ib, but that calcium influx is over two-fold enhanced at Is over Ib when normalized to the same Cac abundance. This is more than sufficient to explain the Pr differences, so the rest of the study should have focused on revealing why influx is different at Is over Ib despite an apparently similar level of Cac abundance. Then the examination of CaBeta, Stj, etc could have been used to help explain this conundrum. 

A lesson might be gleaned in how to structure this narrative from the Rebola 2019 study, which the authors cite and discuss at length. Similar to the current study, that paper started with two synapses ("strong" vs "weak") and sought to explain why they were so different in synaptic strength. First, they examined presynaptic calcium influx, and surprisingly found that the strong synapse had reduced calcium influx compared to the weak. Then the rest of the paper sought to explain why synaptic strength (Pr) was higher at the strong synapse despite reduced calcium influx. The authors do not use this logical flow and narrative in the present study, despite the focus being on how Cav2 channels contribute to strong vs weak synapses - and the primary function of Cav2 channels is to pass calcium at active zones to drive vesicle fusion. 

Although the authors did not show that presynaptic calcium influx is higher at Is vs Ib active zones in the current manuscript, other studies have previously established that calcium influx is two-fold higher at Is active zones vs Ib (as the authors cite). Rather than focusing so much on Pr at Is vs Ib active zones, which as the authors know can be influenced by myriad differences, it seems the more relevant parameter to study is simply to address presynaptic calcium influx at Is vs Ib, which is the primary function of Cac. Put more simply, if Cac levels are the same at Is vs Ib active zones, why is calcium influx at least two-fold higher at Is? 

It would therefore seem crucial for the authors to determine presynaptic calcium influx levels (ideally at individual AZs) to really understand how Cac intensity levels correlate with calcium influx. The authors instead map Pr at individual AZs, but as the authors know there are many variables that influence whether a SV releases in addition to calcium influx. There are a number of options for this kind of imaging in Drosophila, including genetically encoded calcium indicators targeted to active zones. But since several studies have previously established that influx is higher at Is active zones over Ib, this may not be necessary. That being said, there is a lot of value in quantitatively analyzing Cac/Stj/CaBeta abundance, calcium influx, and Pr together at individual active zones.

We appreciate the perspective that we could have focused on why Ca2+ influx is 2x greater at type Is active zones, which we agree is an important and interesting question. However, growing evidence indicates that Ca2+ influx alone, like Ca2+ channel abundance, does not reliably predict synaptic strength between inputs. So, here we focused instead on how other differences between synapses influence Pr and contribute to synaptic heterogeneity between and/or among synapses formed by strong and weak inputs. We have changed our title and framing to better reflect this focus. 

As Reviewer 1 notes, Rebola et al. (2019) found that lower Pr granule synapses exhibit higher Ca2+ influx (and Ca2+ channel abundance). In another example, Aldahabi et al. (2022) demonstrated that even when Ca2+ influx is greater at high-Pr synapses, it does not necessarily explain differences in synaptic strength as raising Ca2+ entry at low-Pr synapses to high-Pr synapse levels was not sufficient to increase synaptic strength to high-Pr input levels. Similar findings have been reported at tonic and phasic synapses of the Crayfish NMJ (Msghina, 1999).

Several lines of evidence argue that factors beyond Ca2+ influx also play important roles in establishing distinct release properties at the Drosophila NMJ. A recent study using using a botulinum transgene to isolate type Ib and Is synapses for electrophysiological analysis found that increasing external [Ca2+] from physiological levels (1.8 mM) to 3 mM or even 6 mM does not result in a 3-fold increase in EPSCs or quantal content at type Ib synapses despite the prediction that the increase would be even greater given the power dependence of release on between Ca2+ concentration (He et al., 2023). The authors further found that type Ib synapses are more sensitive than type Is synapses to the slow Ca2+ chelator EGTA, indicating looser Ca2+ channel-SV coupling. 

Consistently, we find that although VGCC levels are similar at the two inputs, their density is greater at type Is active zones (Figs. 1 and 2). Our findings also reveal additional molecular differences that may contribute to the observed differences in neurotransmitter release properties between the two inputs, including lower levels of the active zone protein Brp (Fig 3) and the auxiliary subunit α2δ-3/Stj (Fig. 6) at high Pr type Is inputs. In contrast, levels of each of these proteins positively correlate with synaptic strength among active zones of a single input, whether low- or high-Pr (Figs. 1, 3, 6). Similarly, levels of each of these proteins increase during homeostatic potentiation of neurotransmitter release (Figs. 4 and 7). Thus, we propose that two broad mechanisms contribute to synaptic diversity in the nervous system: (1) spatial organization and relative molecular content establish distinct average basal release probabilities that differ between inputs and (2) among individual synapses of distinct inputs, coordinated modulation of Ca2+ channel and active zone protein abundance independently tunes Pr. These intersecting mechanisms provide a framework for understanding the extensive and dynamic synaptic diversity observed across nervous systems.

(2) In addition to key points made above, it seems the authors should at least consider (if not experimentally test) what other differences might contribute to the higher calcium influx at Is over Ib:  

- Distinct splice isoforms of Cac (and/or Stj/Cabeta): The recent RNAseq analysis of gene expression at Is vs Ib motor neurons from Troy Littleton's group may inform this consideration? 

- Stj reduction at Is: Do channel studies in heterologous systems give any insight into VGCC channel function with and without a2d-3? Do Cav2 channels without a2d pass more calcium? This would then offer an obvious solution to the key conundrum underlying this study. 

These are excellent questions that we are actively pursuing. While there is no evidence of differentially expressed splice isoforms of Stj or Ca-β in the recent RNA-seq data from Jetti et al., 2023, subtle changes in Cac isoform usage were observed that may contribute to differences in Ca2+ influx. In heterologous systems, α2δ expression generally increases Ca2+ channel membrane insertion and  Ca2+ currents. However, in vivo α2δ’s can also mediate extracellular interactions that may modulate channel function. We address these points in greater detail in the revised discussion.  

(3) Assess Stj and CaBeta levels at AZs after PhTx: The successful generation of endogenously tagged Stj and CaBeta enables some relatively easy experiments that would be of interest, similar to what the authors present for Cac. Does Brp similarly control Stj and CaBeta at Is vs Ib compared to what they show for Cac? In addition, does homeostatic plasticity similarly change Stj and CaBeta at Is vs Ib compared to what the authors have shown for Cac? i.e., do they both similarly increase in intensity, by the same amount, as Cac? 

We agree and have included an analysis of α2δ-3/Stj levels following PhTx exposure (Fig. 7A-C). We have also investigated the regulation of Stj during chronic presynaptic homeostatic potentiation (Fig. 7D-F). In both cases, StjV5-N levels significantly increase at type Ib and Is active zones, consistent with our finding that among AZs of either type Ib or Is inputs, Stj levels correlate with Cac abundance and, thus, Pr. Together with our and others’ findings, this suggests that coordinated increases Ca2+ channel, auxiliary subunit,  and active zone protein abundance positively tunes synaptic strength at diverse synaptic subtypes.

Minor points: 

(1) Including line numbers would make reviewing/commenting easier. 

We apologize for this oversight and have added line numbers to the revised manuscript.

(2) Fig. 2I: It is not apparent what the mean cluster density is between Ib vs Is (as it is in Fig. 2F-H graphs). The mean and error bars should be included in 2I as it is in 2G. Same with Fig. 3C. 

Thank you for pointing this out. We have added error bars to the paired analysis in 2I as well as in 3C and 1C.

(3) Fig. 4 - it might make more sense to normalize Brp and Cac intensity as a percentage of baseline (PhTx at Is or Ib) rather than normalizing everything to control Ib. 

We have revised the graphs as suggested in Figure 4 and throughout.

(4) Page 5 bottom - REFS missing after Fig. 1E. 

Thank you for catching this. We have fixed it.

Reviewer #2 (Recommendations For The Authors): 

This reader found differentiating between low Pr sites (deep purple) and cac measurements (black) difficult in Fig 1B. You may consider depicting this differently. 

Thank you for this feedback. We have changed the color scheme to improve readability.

I found it difficult to discern the difference between experiments Fig 1E and Fig 1J. Why are individual dots distributed differently? 

The individual data points are the same as in 1E and 1F, but we have removed the individual NMJ dimensionality to combine all Is and Ib data points together along with best fit lines for comparison of their slopes. We have added text to the revised manuscript to clarify this.

Results section, second paragraph, add references, remove 'REF': We next investigated the correlation between Pr and VGCC levels and found that at type Is inputs, single-AZ Cac intensity positively correlates with Pr (Fig. 1E; REFS). 

Thank you. We have corrected this error.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Although the manuscript is well organized and written, it could be largely improved and therefore made more plausible and easier to read. See my point-by-point comments listed below:

(1) The introduction section is a bit overloaded with some unnecessary information. For example, the authors discussed the relationship between neurotransmitters in the prefrontal and striatum and substance use/sustained attention. However, the results are related to neither the neurotransmitters nor the striatum. In addition, there is a contradictory description about neurotransmitters there, Nicotine/THC leads to increased neurotransmitters, and decreased neurotransmitters is related to poor sustained attention. Does that mean that the use of Nicotine/THC could increase sustained attention?

Thanks for this insightful question. We understand your concern regarding the seemingly contradictory statements about neurotransmitters and sustained attention. Previous studies have shown that acute administration of nicotine can improve sustained attention (Lawrence et al., 2002; Potter and Newhouse, 2008; Valentine and Sofuoglu, 2018; Young et al., 2004). On the other hand, the acute effects of smoking cannabis on sustained attention are mixed and depend on factors such as dosage and individual differences (Crean et al., 2011). For instance, a previous study (Hart et al., 2001) found that performance on a tracking task, which requires sustained attention, was found to improve significantly after smoking cannabis with a high dose of THC, albeit in experienced cannabis users. However, chronic substance use, including nicotine and cannabis, has been associated with impaired sustained attention (Chamberlain et al., 2012; Dougherty et al., 2013).

To address your concerns and improve clarity and succinctness of the Introduction, we have removed the description of neurotransmitters from the Introduction. This revision should make the introduction more concise and focus on the direct relationships pertinent to our study.

(2) It is a bit hard to follow the story for the readers because the Results section went straight into detail. For example, the authors directly introduced that they used the ICV from the Go trials to index sustained attention without basic knowledge about the task. Why use the ICV of Go trials instead of other trials (i.e., successful stop trials) as an index of sustained attention? I suggest presenting the subjects and task details about the data before the detailed behavioral results. The results section should include enough information to understand the presenting results for the readers, rather than forcing the reader to find the answer in the later Methods section.

We appreciate your suggestion to provide more context about the task and ICV before diving into the detailed behavioural results.

We used the ICV derived from the Go trials instead of Success stop trials as an index of sustained attention, based on the nature of the stop-signal task and the specific data it generates. Previous studies have indicated that reaction time (RT) variability is a straightforward measure of sustained attention, with increasing variability thought to reflect poorer ability to sustain attention (Esterman and Rothlein, 2019). RT variability is defined as ICV, calculated as the standard deviation of mean Go RT divided by the mean Go RT from Go trials (O'Halloran et al., 2018). The stop signal task includes both Go trials and stop trials. During Go trials, participants are required to respond as quickly and accurately as possible to a Go signal, allowing for the recording of RT for calculating ICV. In contrast, stop trials are designed to measure inhibitory control, where successful response inhibition results in no RT or response recorded in the output. Therefore, Go trials are specifically used to assess sustained attention, while Stop trials primarily assess inhibitory control (Verbruggen et al., 2019).

We acknowledge the importance of providing this contextual information within the Results section to enhance reader understanding. We have added this information before presenting the behavioural results on Page 6.

Results

(1) Behavioural changes over time

Reaction time (RT) variability is a straightforward measure of sustained attention, with increasing variability thought to reflect poor sustained attention. RT variability is defined as intra-individual coefficient of variation (ICV), calculated as the standard deviation of mean Go RT divided by the mean Go RT from Go trials in the stop signal task. Lower ICV indicates better sustained attention.

(3) The same problem for section 2 in the Results. What are the predictive networks? Are the predictive networks the same as the networks constructed based on the correlation with ICV? My intuitive feeling is that they are the circular analyses here. The positive/negative/combined networks are calculated based on the correlation between the edges and ICV. Then the author used the network to predict the ICV again. The manipulation from the raw networks (I think they are based on PPI) to the predictive network, and the calculation of the predicted ICV are all missing. The direct exposure of the results to the readers without enough detailed knowledge made everything hard to digest.

We thank the Reviewer for the insightful comment. We agree with the need for more clarity regarding the predictive networks and the CPM analysis before presenting results. CPM, a data-driven neuroscience approach, is applied to predict individual behaviour from brain functional connectivity (Rosenberg et al., 2016; Shen et al., 2017). The CPM analysis used the strength of the predictive network to predict the individual difference in traits and behaviours. CPM includes several steps: feature selection, feature summarization, model building, and assessment of prediction significance (see Fig. S1).

During feature selection, we assessed whether connections between brain areas (i.e., edges) in a task-related functional connectivity matrix (derived from general psychophysiological interaction analysis) were positively or negatively correlated with ICV using a significance threshold of P < 0.01. These positively or negatively correlated connections are regarded as positive or negative network, respectively. The network strength of the positive network (or negative network) was determined in each individual by summing the connection strength of each positively (or negatively) correlated edge. The combined network was determined by subtracting the strength of the negative network from the positive network. Next, CPM built a linear model between the network strength of the predictive network and ICV. This model was initially developed using the training set. The predictive networks were then applied to the test set, where network strength was calculated again, and the linear model was used to predict ICV using k-fold cross-validation. Following your advice, we have updated it in the Results section to include these details on Page 7.

Results

(2) Cross-sectional brain connectivity

This study employed CPM, a data-driven neuroscience approach, to identify three predictive networks— positive, negative, and combined— that predict ICV from brain functional connectivity. CPM typically uses the strength of the predictive networks to predict individual differences in traits and behaviors. The predictive networks were obtained based on connectivity analyses of the whole brain. Specifically, we assessed whether connections between brain areas (i.e., edges) in a task-related functional connectivity matrix derived from generalized psychophysiological interaction analysis were positively or negatively correlated with ICV using a significance threshold of P < 0.01. These positively or negatively correlated connections were regarded as positive or negative network, respectively. The network strength of positive networks (or negative networks) was determined for each individual by summing the connection strength of each positively (or negatively) correlated edge. The combined network was determined by subtracting the strength of the negative network from the positive network. We then built a linear model between network strength and ICV in the training set and applied these predictive networks to yield network strength and a linear model in the test set to calculate predicted ICV using k-fold cross validation.

(4) The authors showed the positive/negative/combined networks from both Go trials and successful stop trials can predict the ICV. I am wondering how the author could validate the specificity of the prediction of these positive/negative/combined networks. For example, how about the networks from the failed stop trials?

We appreciate the opportunity to clarify the specificity of the predictive networks identified in our study. Here is a more detailed explanation of our findings and their implications.

To validate the specificity of the sustained attention network identified from CPM analysis, we calculated correlations between the network strength of positive and negative networks and performances from a neuropsychology battery (CANTAB) at each timepoint separately. CANTAB includes several tasks that measure various cognitive functions, such as sustained attention, inhibitory control, impulsivity, and working memory. We found that all positive and negative networks derived from Go and Successful stop trials significantly correlated with a behavioural assay of sustained attention – the rapid visual information processing (RVP) task – at ages 14 and 19 (all P values < 0.028). Age 23 had no RVP task data in the IMAGEN study. There were sporadic significant correlations between constructs such as delay aversion/impulsivity and negative network strength, for example, but the correlations with the RVP were always significant. This demonstrates that the strength of the sustained attention brain network was specifically and robustly correlated with a typical sustained attention task, rather than other cognitive measures. The results are described in the main text on Page 8 and shown in Supplementary materials (Pages 1 and 3) and Table S12.

In addition, we conducted a CPM analysis to predict ICV using gPPI under Failed stop trials. Our findings showed that positive, negative, and combined networks derived from Failed stop trials significantly predicted ICV: at age 14 (r = 0.10, P = 0.033; r = 0.19, P < 0.001; and r = 0.17, P < 0.001, respectively), at age 19 (r = 0.21; r = 0.18; and r = 0.21, all P < 0.001, respectively), and at age 23 (r = 0.33, r = 0.35, and r = 0.36, respectively, all P < 0.001). Similar results were obtained using a 5-fold CV and leave-site-out CV.

Our analysis further showed that task-related functional connectivity derived from Go trials, Successful Stop trials, and Failed Stop trials could predict sustained attention across three timepoints. However, the predictive performances of networks derived from Go trials were higher than those from Successful Stop and Failed Stop trials. This suggests that sustained attention is particularly crucial during Go trials when participants need to respond to the Go signal. In contrast, although Successful Stop and Failed Stop trials also require sustained attention, these tasks primarily involve inhibitory control along with sustained attention.

Taken together, these findings underscore the specificity of the predictive networks of sustained attention. We have updated these results in the Supplementary Materials (Pages 3-5 and Page 7 ):

Method

CPM analysis using Failed stop trials

We performed another CPM analysis using Failed stop trials using gPPI matrix obtained from the second GLM, described in the main text. The CPM analysis was conducted using 10-fold CV, 5-fold CV and leave-site-out CV.

Results

CPM predictive performance under Failed stop trials

Positive, negative, and combined networks derived from Failed stop trials significantly predicted ICV: at age 14 (r = 0.10, P = 0.033; r = 0.19, P < 0.001; and r = 0.17, P < 0.001, respectively), at age 19 (r = 0.21; r = 0.18; and r = 0.21, all P < 0.001, respectively), and at age 23 (r = 0.33, r = 0.35, and r = 0.36, respectively, all P < 0.001). We obtained similar results using a 5-fold CV and leave-site-out CV (Table S6).

Discussion

Specificity of the prediction of predictive networks

We found that task-related function connectivity derived from Go trials, Successful stop trials, and Failed stop trials successfully predicted sustained attention across three timepoints. However, predictive performances of predictive networks derived from Go trials were higher than those derived from Successful stop trials and Failed stop trials. These results suggest that sustained attention is particularly crucial during Go trials when participants need to respond to the Go signal. In contrast, although Successful Stop and Failed Stop trials also require sustained attention, these tasks primarily involve inhibitory control along with sustained attention.

(5) The author used PPI to define the connectivity of the network. I am not sure why the author used two GLMs for the PPI analysis separately. In the second GLM, Go trials were treated as an implicit baseline. What does this exactly mean? And the gPPI analysis across the entire brain using the Shen atlas is not clear. Normally, as I understand, the PPI/gPPI is conducted to test the task-modulated connectivity between one seed region and the voxels of the whole rest brain. Did the author perform the PPI for each ROI from Shen atlas? More details about how to use PPI to construct the network are required.

Thank you for your insightful questions. Here, we’d like to clarify how we applied generalized PPI across the whole brain using the Shen atlas and why we used two separate GLMs for the gPPI analysis.

Yes, PPI is conducted to test the task-modulated connectivity between one seed region and other brain areas. This method can be both voxel-based and ROI-based. In our study, we performed ROI-based gPPI analysis using Shen atlas with 268 regions. Specifically, we performed the PPI on each seed region of interest (ROI) to estimate the task-related FC between this ROI and the remaining ROI (267 regions) under a specific task condition. By performing this analysis across each ROI in the Shen atlas, we generated a 268 × 268 gPPI matrix for each task condition. The matrices were then transposed and averaged with the original matrices, which yielded symmetrical matrices, which were subsequently used for CPM analysis.

Regarding the use of two separate GLMs for the gPPI analysis, our study aimed to define the task-related FC under two conditions: Go trials and Successful stop trials. The first GLM including Go trials was built to estimate the gPPI during Go trials. However, due to the high frequency of Go trials in the stop signal task, it is common to regard the Go trials as an implicit baseline, as in previous IMAGEN studies (D'Alberto et al., 2018; Whelan et al., 2012). Therefore, to achieve a more accurate estimation of FC during Successful stop trials, we built a second GLM specifically for these trials. Accordingly, we have updated it in the Method Section in the main text on Page 16.

Method

2.5 Generalized psychophysiological interaction (gPPI) analysis

In this study, we adopted gPPI analysis to generate task-related FC matrices and applied CPM analysis to investigate predictive brain networks from adolescents to young adults. PPI analysis describes task-dependent FC between brain regions, traditionally examining connectivity between a seed region of interest (ROI) and the voxels of the whole rest brain. However, this study conducted a generalized PPI analysis, which is on ROI-to-ROI basis (Di et al., 2021), to yield a gPPI matrix across the whole brain instead of just a single seed region.

Given the high frequency of Go trials in SST, it is common to treat Go trials as an implicit baseline in previous IMAGEN studies (D'Alberto et al., 2018; Whelan et al., 2012). Hence, we built a separate GLM for Successful stop trials, which included two task regressors (Failed and Successful stop trials) and 36 nuisance regressors.

(6) Why did the author use PPI to construct the network, rather than the other similar methods, for example, beta series correlation (BSC)?

Thanks for your question. PPI is an approach used to calculate the functional connectivity (FC) under a specific task (i.e., task-related FC). Although most brain connectomic research has utilized resting-state FC (e.g., beta series correlation), FC during task performance has demonstrated superiority in predicting individual behaviours and traits,  due to its potential to capture more behaviourally relevant information (Dhamala et al., 2022; Greene et al., 2018; Yoo et al., 2018). Specifically, Zhao et al. (2023) suggested that task-related FC outperforms both typical task-based and resting-state FC in predicting individual differences. Therefore, we chose to use task-related FC to predict sustained attention over time. We have updated it in the Introduction on Page 5.

Introduction

Although most brain connectomic research has utilized resting-state fMRI data, functional connectivity (FC) during task performance has demonstrated superiority in predicting individual behaviours and traits, due to its potential to capture more behaviourally relevant information (Dhamala et al., 2022; Greene et al., 2018; Yoo et al., 2018). Specifically, Zhao et al. (2023) suggested that task-related FC outperforms both typical task-based and resting-state FC in predicting individual differences. Hence, we applied task-related FC to predict sustained attention over time.

(7) In the section of 'Correlation analysis between the network strength and substance use', the author just described that 'the correlations between xx and xx are shown in Fig5X', and repeated it three times for three correlation results. What exactly are the results? The author should describe the results in detail. And I am wondering whether there are scatter plots for these correlation analyses?

We’d like to clarify the results in Fig. 5. Fig. 5 illustrates the significant correlations between behaviour and brain activity associated with sustained attention and Cigarette and cannabis use (Cig+CB) after FDR correction. Panel A shows the significant correlation between behaviour level of sustained attention and Cig+CB. Panels B and C show the correlations between brain activity associated with sustained attention and Cig+CB. While Panel B presents the brain activity derived from Go trials, Panel C presents brain activity derived from Successful stop trials. In response to your suggestion, we have described these results in detail on Page 9. We also have included scatter plots for the significant correlations, which are shown in Fig. 5 in Supplementary materials (Fig. S10).

Results

(6) Correlation between behaviour and brain to cannabis and cigarette use

Figs. 5A-C summarizes the results showing the correlation between ICV/brain activity and Cig+CB per timepoint and across timepoints. Fig. 5A shows correlations between ICV and Cig+CB (Tables S14-15). ICV was correlated with Cig+CB at ages 19 (Rho = 0.13, P < 0.001) and 23 (Rho = 0.17, P < 0.001). ICV at ages 14 (Rho = 0.13, P = 0.007) and 19 (Rho = 0.13, P = 0.0003) were correlated with Cig+CB at age 23. Cig+CB at age 19 was correlated with ICV at age 23 (Rho = 0.13, P = 9.38E-05). Fig. 5B shows correlations between brain activity derived from Go trials and Cig+CB (Tables S18-19). Brain activities of positive and negative networks derived from Go trials were correlated with Cig+CB at age 23 (positive network: Rhop = 0.12, P < 0.001; negative network: Rhon = -0.11, P < 0.001). Brain activity of the negative network derived from Go trials at age 14 was correlated with Cig+CB at age 23 (Rhon = -0.16, P = 0.001). Cig+CB at age 19 was correlated with brain activity of the positive network derived from Go trials at age 23 (Rhop = 0.10, P = 0.002). Fig. 5C shows the correlations between brain activity derived from Successful stop and Cig+CB (Tables S18-19). Brain activities of positive and negative networks derived from Successful stop were correlated with Cig+CB at ages 19 (positive network: Rhop = 0.10, P = 0.001; negative network: Rhon = -0.08, P = 0.013) and 23 (positive network: Rhop = 0.13, P < 0.001; negative network: Rhon = -0.11, P = 0.001).

(8) Lastly, the labels of (A), (B) ... in the figure captions are unclear. The authors should find a better way to place the labels in the caption and keep them consistent throughout all figures.

Thank you for this valuable comment. We have revised the figure captions in the main text to ensure the labels (A), (B), etc., are placed more clearly and consistently across all figures.

Reviewer #2 (Public Review):

While the study largely achieves its aims, several points merit further clarification:

(1) Regarding connectome-based predictive modeling, an assumption is that connections associated with sustained attention remain consistent across age groups. However, this assumption might be challenged by observed differences in the sustained attention network profile (i.e., connections and related connection strength) across age groups (Figures 2 G-I, Fig. 3 G_I). It's unclear how such differences might impact the prediction results.

Thank you for your insightful comment. We’d like to clarify that we did not assume that connections associated with sustained attention remain completely consistent across age groups. Indeed, we expected that connections would change across age groups, due to the developmental changes in brain function and structure from adolescence to adulthood. Our focus was on the consistency of individual differences in sustained attention networks over time, recognising that the actual connections within those networks may change. However, we did show that there is some consistency in the specific connections associated with sustained attention over time. Notably, this consistency markedly increases when comparing ages 19 and 23, when developmental factors are less relevant. We support our reasoning above with the following analyses:

(1) Supplementary materials (Pages 2 and 5), relevant sections highlighted here for emphasis.

Method

Comparison of predictive networks identified at one timepoint versus another

Steiger’s Z value was employed to compare predictive performances of networks identified at different timepoints. This analysis involved comparing the R values derived from networks defined at distinct ages to predict ICV at the same age. For example, we compared the r values of brain networks defined at age 14 when predicting ICV at 19 (i.e., positive network: r = 0.25, negative network: r = 0.25, combined network: r = 0.28) with those R values of brain networks defined at age 19 itself (i.e., positive network: r = 0.16, negative network: r = 0.14, combined network: r = 0.16) derived from Go trials using Steiger's Z test (age 14 → age 19 vs. age 19 → 19). Similarly, comparisons were made between networks defined at age 14 predicting ICV at age 23 and those at age 23 predicting ICV at age 23 (age 14 → age 23 vs. age 23 → 23), as well as between networks defined at age 19 predicting ICV at age 23 and those at age 23 predicting ICV at age 23 (age 19 -> age 23 vs. age 23 -> age 23). These comparisons were performed separately for Go trials and Successful Stop trials.

Results

Comparison of predictive performance at different timepoints

For positive, negative, and combined networks predicting ICV derived from Go trials at age 19, the R values were higher when using predictive networks defined at 19 than those defined at 14 (Z = 3.79, Z = 3.39, Z = 3.99, all P < 0.00071). Similarly, the R values for positive, negative, and combined networks predicting ICV derived from Go trials at age 23 were higher when using predictive networks defined at age 23 compared to those defined at ages 14 (Z = 6.00, Z = 5.96, Z = 6.67, all P < 3.47e-9) or 19 (Z = 2.80, Z = 2.36, Z = 2.57, all P < 0.005).

At age 19, the R value for the positive network predicting ICV derived from Successful stop trials was higher when using predictive networks defined at 19 compared to those defined at 14 (Z = 1.54, P = 0.022), while the negative and combined networks did not show a significant difference (Z = 0.85, P = 0.398; Z = 2.29, P = 0.123). At age 23, R values for the positive and combined networks predicting ICV derived from Successful stop trials were higher when using predictive networks defined at 23 compared to those defined at 14 (Z = 3.00, Z = 2.48, all P < 3.47e-9) or 19 (Z = 2.52, Z = 1.99, all P < 0.005). However, the R value for the negative network at age 23 did not significantly differ when using predictive networks defined at 14 (Z = 1.80, P = 0.072) or 19 (Z = 1.48, P = 0.138).

These results indicate that some specific pairwise connections associated with sustained attention at earlier ages, such as 14 and 19, are still relevant as individuals grow older. However, some connections are not optimal for good sustained attention at older ages. That is, the brain reorganizes its connection patterns to maintain optimal functionality for sustained attention as it matures.

(2) Consistency of Individual Differences:

We found individual differences in ICV were significantly correlated between the three timepoints (Fig. 1B). In addition, we calculated the correlations of network strength of predictive networks predicting sustained attention derived from Go trials and Successful trials between each timepoints. We found that the correlations of network strength for predictive networks (derived from Go trials and Successful trials) were also significant (all P < 0.003). We have updated these results in the main text (Pages 7-8) and Supplementary Materials (Table S7).

(2) Cross-sectional brain connectivity

In addition, we found that network strength of positive, negative, and combined networks derived from Go trials was significantly correlated between the three timepoints (Table S7, all P < 0.003).

In addition, we found that network strength of positive, negative, and combined networks derived from Successful stop trials was significantly correlated between the three timepoints (Table S7, all P < 0.001).

(3) Predictive networks across timepoints: Predictive networks defined at age 14 were successfully applied to predict ICV at ages 19 and 23. Similarly, predictive networks defined at age 19 were successfully applied to predict ICV at age 23 (Fig. 4). These results reflect the robustness of the brain network associated with sustained attention over time.

(4) Dice coefficient analysis: We calculated the Dice coefficient to quantify the similarity of predictive networks across the three timepoints. Connections in the sustained attention networks were significantly similar from ages 14 to 23 (Table S13), despite relatively few overlapping edges over time (as discussed in Supplementary Materials on Page 6).

(5) Global brain activation: Based on these findings, we indicate that sustained attention relies on global brain activation (i.e., network strength) rather than specific regions or networks (see also (Zhao et al., 2021)).

In summary, brain network connections undergo change and are not completely consistent across time. However, individual differences in sustained attention and its network are consistent across time, as we found that 1) the brain reorganizes its connection patterns to maintain optimal functionality for sustained attention as it matures. 2) ICV and network strength of sustained attention network were significantly correlated between each timepoint. 3) Sustained attention networks identified from previous timepoints could predict ICV in the subsequent timepoint. 4) Dice coefficient analysis indicated that the edges in the sustained attention networks were significantly similar from ages 14 to 23. 5) Sustained attention networks function as a global activation, rather than specific regions or networks.

(2) Another assumption of the connectome-based predictive modeling is that the relationship between sustained attention network and substance use is linear and remains linear over development. Such linear evidence from either the literature or their data would be of help.

Thanks for your valuable suggestion. We'd like to clarify that while CPM assumes a linear relationship between brain and behaviour (Shen et al., 2017), it does not assume that the relationship between the sustained attention network and substance use remains linear over development.

Our approach in applying CPM to predict sustained attention across different timepoints was based on previous neuroimaging studies (Rosenberg et al., 2016; Rosenberg et al., 2020), which indicated linear associations between brain connectivity patterns and sustained attention using CPM analysis. These findings support the notion of a linear relationship between brain connectivity and sustained attention. In this study, we performed CPM analysis to identify predictive networks predicting sustained attention, not substance use and used the network strength of these predictive networks to represent sustained attention activity.

To examine the relationship between substance use and sustained attention, as well as its associated brain activity, we conducted correlation analyses and utilized a latent change score model instead of CPM analysis. This decision was informed by cross-sectional studies (Broyd et al., 2016; Lisdahl and Price, 2012) that consistently reported linear associations between substance use and impairments in sustained attention. Additionally, longitudinal research by (Harakeh et al., 2012) indicated a linear relationship between poorer sustained attention and the initiation and escalation of substance use over time.

Given these previous findings, we assumed a linear relationship between sustained attention and substance use. Our analyses included calculating correlations between substance use and sustained attention, as well as its associated brain activity at each timepoint and across timepoints (Fig. 5). Furthermore, we employed a three-wave bivariable latent change score model, a longitudinal approach, to assess the relationship between substance use and behavirour and brain activity associated with sustained attention (Figs. 6-7). We have added more information in the Introduction to make it more clear on Page 6.

Introduction

Additionally, previous cross-sectional and longitudinal studies (Broyd et al., 2016; Harakeh et al., 2012; Lisdahl and Price, 2012) have shown that there are linear relationships between substance use and sustained attention over time. We therefore employed correlation analyses and a latent change score model to estimate the relationship between substance use and both behaviours and brain activity associated with sustained attention.

(3) Heterogeneity in results suggests individual variability that is not fully captured by group-level analyses. For instance, Figure 1A shows decreasing ICV (better-sustained attention) with age on the group level, while there are both increasing and decreasing patterns on the individual level via visual inspection. Figure 7 demonstrates another example in which the group with a high level of sustained attention has a lower risk of substance use at a later age compared to that in the group with a low level of sustained attention. However, there are individuals in the high sustained attention group who have substance use scores as high as those in the low sustained attention group. This is important to take into consideration and could be a potential future direction for research.

Thanks for this valuable comment. We appreciate your observation regarding the individual variability that is not fully captured by group-level analyses to some degree. Fig. 1A shows the results from a linear mixed model, which explains group-level changes over time while accounting for the random effect within subjects. Similarly, Fig. 7 shows the group-level association between substance use and sustained attention. We agree that future research could indeed consider individual variability. For example, participants could be categorized based on their consistent trajectories of ICV or substance use (i.e., keep decreasing/increasing) over multiple timepoints. We agree that incorporating individual-level analyses in the future could provide valuable insights and are grateful for your suggestion, which will inform our future research directions.

The above-mentioned points might partly explain the significant but low correlations between the observed and predicted ICV as shown in Figure 4. Addressing these limitations would help enhance the study's conclusions and guide future research efforts.

We have updated the text in the Discussion on Page 13:

Discussion

However, there are still some individual variabilities not captured in this study, which could be attributed to the diversity in genetic, environmental, and developmental factors influencing sustained attention and substance use. Future research should aim to explore these variabilities in greater depth to gain better understanding of the relationship between sustained attention and substance use.

Reviewer #3 (Public Review):

Weaknesses: It's questionable whether the prediction approach (i.e., CPM), even when combined with longitudinal data, can establish causality. I recommend removing the term 'consequence' in the abstract and replacing it with 'predict'. Additionally, the paper could benefit from enhanced rigor through additional analyses, such as testing various thresholds and conducting lagged effect analyses with covariate regression.

Thank you for your comment. We have replaced “consequence” by “predict” in the abstract.

Abstract

Previous studies were predominantly cross-sectional or under-powered and could not indicate if impairment in sustained attention was a predictor of substance-use or a marker of the inclination to engage in such behaviour.

Reviewer #3 (Recommendations For The Authors):

(1) The connectivity analysis predicts both baseline and longitudinal attention measures. However, given the high correlation in attention abilities across the three time-points, it's unclear whether the connectivity predicts shared variations of attention across three time points. It would be insightful to assess if predictions at the 2nd and 3rd-time points remained  significant after controlling for attention abilities at the initial time point.

Thanks for your comments. We performed the CPM analysis to predict ICV at the 2nd and 3rd timepoint, controlling for ICV at age 14 as a covariate. We found that controlling for ICV at age 14, positive, negative, and combined networks derived from Successful stop trials defined at age 14 still predicted ICV at ages 19 and 23. In addition, positive, negative, and combined networks derived from Successful stop trials defined at age 19 predicted ICV at age 23. In addition, positive, negative, and combined networks derived from Go trials defined at age 19 still predicted ICV at age 23, after controlling for ICV at age 14. However, positive, negative, and combined networks derived from Go trials defined at age 14 had lower predictive performances in predicting ICV at ages 19 and 23, after controlling for ICV at age 14. Notably, controlling for ICV at the initial timepoint did not significantly impact the performances of predictive networks derived from Successful stop trials. Accordingly, we have added this analysis and the results in the Supplementary Materials (Pages 3 and 5).

Method

Prediction across timepoints controlling for ICV at age 14

To examine whether connectivity predictors shared variations of sustained attention across timepoints, we applied predictive models developed at ages 14 and 19 to predict ICV at subsequent timepoints controlling for ICV at age 14. Specifically, we used predictive models (including parameters and selected edges) developed at age 14 to predict ICV at ages 19 and 23 separately. First, we calculated the network strength using the gPPI matrix at ages 19 and 23 based on the selected edges identified from CPM analysis at age 14. We then estimated the predicted ICV at ages 19 and 23 by applying the linear model parameters (slope and intercept) obtained from CPM analysis at age 14 to the network strength. Finally, we evaluated the predictive performance by calculating the partial correlation between the predicted and observed values at ages 19 and 23, controlling for ICV at age 14. Similarly, we applied models developed at age 19 to predict ICV at age 23, also controlling for ICV at age 14. To assess the significance of the predictive performance, we used a permutation test, shuffling the predicted ICV values and calculating partial correlation to general a random distribution over 1,000 iterations.

Results

Predictions across timepoints controlling for ICV at age 14

Positive and combined networks derived from Go trials defined at age 14 predicted ICV at ages 19 (r = 0.10, P = 0.028; r = 0.08, P = 0.047) but negative network did not (r = 0.06, P = 0.119). Positive network derived from Go trials defined at age 14 predicted ICV at age 23 (r = 0.11, P = 0.013) but negative and combined networks did not (r = 0.04, P = 0.187; r = 0.08, P = 0.056).  Positive, negative, and combined networks derived from Go trials defined at age 19 predicted ICV at age 23 (r = 0.22, r = 0.19, and r = 0.22, respectively, all P < 0.001).

Positive, negative, and combined networks derived from Successful stop trials defined at age 14 predicted ICV at age 19 (r = 0.08, P = 0.036; r = 0.10, P = 0.012; r = 0.11, P = 0.009) and 23 (r = 0.11, P = 0.005; r = 0.13, P = 0.005; r = 0.13, P = 0.017) respectively. Positive, negative, and combined networks derived from Successful stop trials defined at age 19 predicted ICV at age 23 (r = 0.18, r = 0.18, and r = 0.17, respectively, all P < 0.001).

(2) In the Results section, a significance threshold of p = 0.01 was used for the CPM analysis. It would be beneficial to test the stability of these findings using alternative thresholds such as p = 0.05 or p = 0.005.

We appreciate this insightful comment. We appreciate the suggestion to test the stability of our findings using alternative significance thresholds. Indeed, we have already conducted CPM analyses using a range of thresholds, including 0.1, 0.05, 0.01, 0.005, 0.001, 0.0005, and 0.0001 (see Table S8 in supplementary Materials). The results were similar across different thresholds. Following prior studies (Feng et al., 2024; Ren et al., 2021; Yoo et al., 2018) which used P < 0.01 for feature selection, we chose to focus on the threshold of P < 0.01 for our main analysis. Following your suggestion, we have highlighted this in the Method section on Pages 17-18.

Method

2.6.1 ICV prediction

The r value with an associated P value for each edge was obtained, and a threshold P = 0.01 (Feng et al., 2024; Ren et al., 2021; Yoo et al., 2018) was set to select edges.

2.6.2 Three cross-validation schemes

In addition, we conducted the CPM analysis using a range of thresholds for feature selection and observed similar results across different thresholds (See Supplementary Materials Table S8).

(3) Could you clarify if you used one sub-sample to extract connectivity related to sustained attention and then used another sub-sample to predict substance use with attention-related connectivity?

Thank you very much for the question. We used the same sample to extract the brain network strength and estimated the correlation with substance use using both the Spearman correlation and latent change score model across three timepoints. We controlled for covariates including sex, age, and scan site at the same time. Accordingly, we have clarified this in the Method section on Page 20. We note that the CPM analyses were conducted using cross-validation, plus a leave-site-out analysis.

Method

2.7.3 Correlation between network strength and substance use

It is worth noting that all the correlations between substance use and sustained attention were conducted using the same sample across three timepoints.

(4) Could you clarify whether you have regressed covariates in the lagged effects analysis of part 7?

Thanks for this question. Yes, we confirmed that we controlled the covariates including age, sex and scan sites in the latent change score model. We have described them more clearly now in the Method section (Page 18).

Method

2.7.3 Correlation between network strength and substance use

Additionally, cross-lagged dynamic coupling (i.e., bidirectionality) was employed to explore individual differences in the relationships between substance use and linear changes in ICV/brain activity, as well as the relationship between ICV/brain activity and linear change in substance use. The model accounted for covariates such as age, sex and scan sites.

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Author response:

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

Reviewer #1 (Public Reviews):

Summary:

This paper by Schommartz and colleagues investigates the neural basis of memory reinstatement as a function of both how recently the memory was formed (recent, remote) and its development (children, young adults). The core question is whether memory consolidation processes as well as the specificity of memory reinstatement differ with development. A number of brain regions showed a greater activation difference for recent vs. remote memories at the long versus shorter delay specifically in adults (cerebellum, parahippocampal gyrus, LOC). A different set showed decreases in the same comparison, but only in children (precuneus, RSC). The authors also used neural pattern similarity analysis to characterize reinstatement, though I have substantive concerns about how this analysis was performed and as such will not summarize the results. Broadly, the behavioural and univariate findings are consistent with the idea that memory consolidation differs between children and adults in important ways, and takes a step towards characterizing how.

Strengths:

The topic and goals of this paper are very interesting. As the authors note, there is little work on memory consolidation over development, and as such this will be an important data point in helping us begin to understand these important differences. The sample size is great, particularly given this is an onerous, multi-day experiment; the authors are to be commended for that. The task design is also generally well controlled, for example as the authors include new recently learned pairs during each session.

Weaknesses:

As noted above, the pattern similarity analysis for both item and category-level reinstatement was performed in a way that is not interpretable given concerns about temporal autocorrelation within the scanning run. Below, I focus my review on this analytic issue, though I also outline additional concerns.

We thank the reviewer for both the positive and critical appraisal of our paper.

(1) The pattern similarity analyses were not done correctly, rendering the results uninterpretable (assuming my understanding of the authors' approach is correct).

a. First, the scene-specific reinstatement index: The authors have correlated a neural pattern during a fixation cross (delay period) with a neural pattern associated with viewing a scene as their measure of reinstatement. The main issue with this is that these events always occurred back-to-back in time. As such, the two patterns will be similar due simply to the temporal autocorrelation in the BOLD signal. Because of the issues with temporal autocorrelation within the scanning run, it is always recommended to perform such correlations only across different runs. In this case, the authors always correlated patterns extracted from the same run, which moreover have temporal lags that are perfectly confounded with their comparison of interest (i.e., from Fig 4A, the "scene-specific" comparisons will always be back-to-back, having a very short temporal lag; "set-based" comparisons will be dispersed across the run, and therefore have a much higher lag). The authors' within-run correlation approach also yields correlation values that are extremely high - much higher than would be expected if this analysis was done appropriately. The way to fix this would be to restrict the analysis to only cross-run comparisons, but I don't believe this is possible unfortunately given the authors' design; I believe the target (presumably reinstated) scene only appears once during scanning, so there is no separate neural pattern during the presentation of this picture that they can use. For these reasons, any evidence for "significant scene-specific reinstatement" and the like is completely uninterpretable and would need to be removed from the paper.

We thank the reviewer for this important input. We acknowledge that our study design leads to temporal autocorrelation in the BOLD signal when calculating RSA between fixation and scene time windows. We also recognize that we cannot interpret the significance of scene-specific reinstatement compared to zero and have accordingly removed this information. Nevertheless, our primary objective was to investigate changes in scene-specific reinstatement in relation to the different time delays of retrieval. Given that the retrieval procedure is the same over time and presumably similarly influenced by temporal autocorrelations, we argue that our results must be attributed to the relative differences in reinstatement across recent and remote trials. Bearing this in mind, we argue that our results can be interpreted in terms of delay-related changes in reinstatement. This information is discussed in pp. 21, 40 of the manuscript.

We agree with the reviewer that cross-run comparisons would be extremely interesting. This could be achieved by introducing the same items repeatedly across different runs, which was not possible in our current setup since we were interested in single exposure retrieval and practical time restriction in scanning children. We have  introduced this idea in Limitations and Discussion sections (pp. 40, 44) of the manuscript to inform future studies.

Finally, thanks to the reviewer’s comment, we identified a bug in the final steps of our RSA calculation. Fischer’s z-transformation was incorrectly applied to r-1 values, resulting in abnormally high values. We apologize for this error. We have revised the scripts and rectified the bug by correctly applying Fischer’s z-transformation to the r similarity values. We also adjusted the methods description figure accordingly (Figure 5, p. 22). This adjustment led to slightly altered reinstatement indices. Nevertheless, the overall pattern of delay-related attenuation in the scene-specific reinstatement index, observed in both children and adults, remains consistent. Similarly, we observed gist-like reinstatement uniquely in children.

b. From a theoretical standpoint, I believe the way this analysis was performed considering the fixation and the immediately following scene also means that the differences between recent and remote could have to do with either the reactivation (processes happening during the fixation, presumably) or differences in the processing of the stimulus itself (happening during the scene presentation). For example, people might be more engaged with the more novel scenes (recent) and therefore process those scenes more; such a difference would be interpreted in this analysis as having to do with reinstatement, but in fact could be just related to the differential scene processing/recognition, etc.

Thank you for your insightful comments. We acknowledge the theoretical concerns raised about distinguishing between the effects of reactivation processes occurring during fixation and differential processing of the stimulus itself during scene presentation. Specifically, the notion that engagement levels with recent scenes could result in enhanced processing, which might be misattributed to memory reinstatement mechanisms.

We argue, however, that during scene presentation, scenes are processed more “memory-wise” rather than “perception-wise”, since both recent and remote memories are well-learned, as we included only correctly recalled memories in the analysis.

We concur that scene presentations entail perceptual processing; however, such processing would be consistent across all items, given that they were presented with the same repeated learning procedure, rendering them equally familiar to participants. In addition, we would argue that distinct activation patterns elicited during varying delays are more likely attributable to memory-related processing, since participants actively engaged in a memory-based decision-making task during these intervals. We have incorporated this rationale into the discussion section of our manuscript (p. 40).

With this in mind, we hypothesized that in case of “memory-wise” processing, the neural engagement during the scene time window should be higher for remote compared to recent  items, and this increases with passing time as more control and effort should be exhibited during retrieval due to reorganized and distributed nature of memories. If the scenes are processed more “perception-wise”, we would expect higher neural engagement during the retrieval of recent compared to remote items. Our exploratory analysis (detailed overview in supplementary materials, Figure S3, Table S9) revealed a higher neural activation for remote compared to recent items in medial temporal, prefrontal, occipital and cerebellar brain regions, supporting the notion of “memory-wise” processes during scene time window. However, this exploratory analysis cannot provide a direct solution to the reviewer’s concern as our paradigm per se cannot arbitrate between “memory-wise” and “perception-wise” nature of retrieval. We added the point to the discussion (see p. 40).

c. For the category-based neural reinstatement:

(1) This suffers from the same issue of correlations being performed within the run. Again, to correct this the authors would need to restrict comparisons to only across runs (i.e., patterns from run 1 correlated with patterns for run 2 and so on). With this restriction, it may or may not be possible to perform this analysis, depending upon how the same-category scenes are distributed across runs. However, there are other issues with this analysis, as well.

(2) This analysis uses a different approach of comparing fixations to one another, rather than fixations to scenes. The authors do not motivate the reason for this switch. Please provide reasoning as to why fixation-fixation is more appropriate than fixation-scene similarity for category-level reinstatement, particularly given the opposite was used for item-level reinstatement. Even if the analyses were done properly, it would remain hard to compare them given this difference in approach.

(3) I believe the fixation cross with itself is included in the "within category" score  Is this not a single neural pattern correlated with itself, which will yield maximal similarity (pearson r=1) or minimal dissimilarity (1-pearson r=0)? Including these comparisons in the averages for the within-category score will inflate the difference between the "within-category" and "between-category" comparisons. These (e.g., forest1-forest1) should not be included in the within-category comparisons considered; rather, they should be excluded, so the fixations are always different but sometimes the comparisons are two retrievals of the same scene type (forest1-forest2), and other times different scene types (forest1-field1)

(4) It is troubling that the results from the category reinstatement metric do not seem to conceptually align with past work; for example, a lot of work has shown category-level reinstatement in adults. Here the authors do not show any category-level reinstatement in adults (yet they do in children), which generally seems extremely unexpected given past work and I would guess has to do with the operationalization of the metric.

Thank you for this important input regarding category-based reinstatement.

(1) The distribution of within-category items across runs was approximately similar and balanced. Additionally, within runs, they were presented randomly without close temporal proximity. Based on this arrangement, we believe that the issue of close temporal autocorrelation, as pointed out by the reviewer in the context of scene-specific reinstatement, may not apply to the same extent here. Again, our focus is not on the absolute level of category-based reinstatement, but the relative difference across conditions (recent vs. remote short delay vs. remote long delay) which are equally impacted by the autocorrelations.  

(2) We apologize for not motivating this analysis further. Whereas the scene-reinstatement index (i.e., fixation to scene correlation) gives us a measure of the pre-activation of a concrete scene (e.g., a yellow forest in autumn), the gist-like reinstatement gives us a measure of the pre-activation of a whole category of scenes (e.g., forests). Critically, our window of interest is the fixation period for both sets of analysis (in the absence of any significant visual input). The scene-specific reinstatement uses the scene window as a neural template against which the fixation period can be compared, while the gist-like reinstatement compares similarity of reactivation pattern for trials from the same category but differ in the exact memory content. The reinstatement of more generic, gist-like memory (e.g., forest) across multiple trials should yield more similar neural activation patterns. Significant gist-like reinstatement would suggest that neural patterns for scenes within the same category are more generic, as indicated by higher similarity among them. On the other hand, a more detailed reinstatement of specific types of forests (e.g., a yellow forest in autumn, green pine trees, a bare-leaved forest in spring, etc.) that differ in various dimensions could result in neural activation patterns that are as dissimilar as those seen in the reinstatement of scenes from entirely different categories. Through this methodology, we could distinguish between more generic, gist-like reinstatement and more specific, detailed reinstatement. This is now clarified in the manuscript, see p. 25.

(3) We apologize for the confusion caused by the figure and analysis description. In our analysis, we indeed excluded the correlation of the fixation cross with itself. Consequently, the diagonal in the figure should be blank to indicate this. This is now revised in the manuscript (Figure 7B and in Methods).

(4) We appreciate your concern and recognize that the terminology we used might not align perfectly with the conventional understanding of category-based reinstatement. Typically, category-level neural representations (as discussed in Polyn et al., 2005; Jafarpour et al., 2014; among others) are investigated to identify specific brain areas associated with encoding/perception of scenes or faces. Our aim, however, was to explore the mnemonic reinstatement of highly detailed scenes that were elaborately encoded, with the hypothesis that substantial representational transformations would occur over time and vary with age. This hypothesis is based on the memory literature, including the Fuzzy-Trace Theory, the Contextual Binding Theory, and the Trace Transformation Theory (Brainerd & Reyna, 1998; Yonelinas, 2019; Moscovitch & Gilboa, 2023). Therefore, we renamed 'category-based' reinstatement to 'gist-like' reinstatement, which clarifies our concept and better aligns it with existing literature.

We anticipated that young adults, having the ability to retain detailed narratives post-encoding, would demonstrate a reinstatement of scenes with distinct details, making these scenes dissimilar from each other (see similar findings in Sommer et al., 2021). In contrast, given the anticipated lesser strategic elaboration during learning in children, we hypothesized that they would demonstrate a shallower, more gist-like reinstatement (for instance, children recalling a forest or a field in a general sense without specific details or vivid imagery). This could result in higher category-based similarity, as children might reinstate a more generic forest concept.

We did not gather additional data on the verbal quality of reinstatement due to the limited scanning time available for children, so these assumptions remain unverified. However, anecdotal observations post-retrieval indicated that adults often reported very vivid scenes associated with clear narrative recall. In contrast, children frequently described more vague memories (e.g., “I know it was a forest”) without specific details. Future studies should include measures to assess the quality of reinstatement, potentially outside the scanning environment.

(2) I did not see any compelling statistical evidence for the claim of less robust consolidation in children.

Specifically in terms of the behavioral results of retention of the remote items at 1 vs 14 days, shown in Figure 2B, the authors conclude that memory consolidation is less robust in children (line 246). Yet they do not report statistical evidence for this point, as there was no interaction of this effect with the age group. Children had worse memory than adults overall (in terms of a main effect - i.e. across recent and remote items). If it were consolidation-specific, one would expect that the age differences are bigger for the remote items, and perhaps even most exaggerated for the 14-day-old memories. Yet this does not appear to be the case based on the data the authors report. Therefore, the behavioral differences in retention do not seem to be consolidation specific, and therefore might have more to do with differences in encoding fidelity or retrieval processes more generally across the groups. This should be considered when interpreting the findings.

Thank you for highlighting this important issue. We acknowledge that our initial description and depiction of our behavioral findings may not have effectively conveyed the main message about memory consolidation. Therefore, we have revised the behavioral results section (see pp. 12-14) to communicate our message more clearly.

As detailed in the methods section, we reported retention rates only for those items that were correctly (100%) learned on day 0, day 1, and day 14. This approach meant that different participants had varying numbers of items learned correctly. However, this strategy allowed us to address our primary question: whether memory consolidation, based on all items initially encoded successfully, is comparably robust between groups.

To illustrate the change in retention rate slopes over time for recently learned items (i.e., immediately 30 minutes after learning), short delay remote, and long delay remote items, relative to the initially correctly learned items more clearly and straightforward, we conducted the following analysis: after observing no differences between sessions in both age groups for recent items on days 1 and 14, we combined the recent items. This approach enabled us to investigate how the slope of memory retention for initially correctly learned items (with a baseline of 100%) changes over time. We observed a significant interaction between item type (recent, short delay remote, long delay remote) and group (F(3,250) = 17.35, p < .001, w2 = .16). The follow up of this interaction revealed significantly less robust memory consolidation across all delay times in children compared to young adults. This information is added in the manuscript in pp. 12-14. We have also updated the figures, incorporating the baseline of 100% correct performance.

(3) Please clarify which analyses were restricted to correct retrievals only. The univariate analyses states that correct and incorrect trials were modelled separately but does not say which were considered in the main contrast (I assume correct only?). The item specific reinstatement analysis states that only correct trials were considered, but the category-level reinstatement analysis does not say. Please include this detail.

Thank you for bringing this to our attention. We indeed limited our analysis – including univariate, specific reinstatement, and gist-like analyses – to only correctly remembered items. This decision was made because our goal was to observe delay-related changes in the neural correlates of correct memories, which are potentially stronger. We have incorporated this information into the manuscript.

(4) To what extent could performance differences be impacting the differences observed across age groups? I think (see prior comment) that the analyses were probably limited to correct trials, which is helpful, but still yields pretty big differences across groups in terms of the amount of data going into each analysis. In general, children showed more attenuated neural effects (e.g., recent/remote or session effects); could this be explained by their weaker memory? Specifically, if only correct trials are considered that means that fewer trials would be going into the analysis for kids, especially for the 14-day remote memories, and perhaps pushing the remove > recent difference for this condition towards 0. The authors might be able to address this analytically; for example, does the remote > recent difference in the univariate data at day 14 correlate with day 14 memory?

Thank you for pointing this out. Indeed, there was a significant relationship between remote > recent difference in the univariate data and memory performance at day 14 across both age group (see Figure 4C-D). The performance of all participants including children was above chance level for remote trial on day 14. In addition, although number of remote trials was lower in children (18 trials on average) in comparison to adults (22 trials on average), we believe that the number of remote trials was not too low or different across groups for the contrast.

(5) Some of the univariate results reporting is a bit strange, as they are relying upon differences between retrieval of 1- vs. 14-day memories in terms of the recent vs. report difference, and yet don't report whether the regions are differently active for recent and remote retrieval. For example, in Figure 3A, neither anterior nor posterior hippocampus seem to be differentially active for recent vs. remote memories for either age group (i.e., all data is around 0). This difference from zero or lack thereof seems important to the message - is that correct? If so, can the authors incorporate descriptions of these findings?

Thank you for this valuable input. When examining recent and remote retrieval separately, indeed both the anterior and posterior regions of the hippocampus exhibited significant activation from zero in adults (all p < .0003FDRcorr) and children (all p < .014FDRcorr, except for recent posterior hippocampus) during all delays. We include this information in the manuscript (see p. 17) and add it to the supplementary materials (Figure S2, Table S7).

(6) Please provide more details about the choices available for locations in the 3AFC task. (1) Were they different each time, or always the same? If they are always the same, could this be a motor or stimulus/response learning task? (2) Do the options in the 3AFC always come from the same area - in which case the participant is given a clue as to the gist of the location/memory? Or are they sometimes randomly scattered across the image (in which case gist memory, like at a delay, would be sufficient for picking the right option)? Please clarify these points and discuss the logic/impact of these choices on the interpretation of the results.Response: Thank you for pointing this out. During learning and retrieval, we employed the 3AFC (Three-Alternative Forced Choice) task.

The choices for locations varied across scenes while remained the same across time within individuals. There were 18 different key locations for the objects, distributed across the stimulus set. This means the locations of the objects were quite heterogeneous and differed between objects. The location of the object within the task was presented once during encoding and remained consistent throughout learning. Given the location heterogeneity, we believe our task cannot be reduced to a mere “stimulus/response learning task” but is more accurately described as an object-location associations task.

Similar to the previous description, the options for the 3AFC task did not originate from the same area, as there were 18 different areas in total. The three choice options were distributed equally: so sometimes the “correct” answer was the left option, sometimes in the middle option, or sometimes the right option. Therefore, we believe that the 3AFC task did not provide clues to the location but required detailed and precise memory of the location. Moreover, the options were not randomly scattered but rather presented close together in the scene, demanding a high level of differentiation between choices.

Taking all the above into consideration, we assert that precise object-location associative memory is necessary for a correct answer. We have added this information to the manuscript (p. 9).

(7) Often p values are provided but test statistics, effect sizes, etc. are not - please include this information. It is at times hard to tell whether the authors are reporting main effects, interactions, pairwise comparisons, etc.

Thank you for bringing this to our attention. We realize that including this information in the Tables may not be the most straightforward approach. Therefore, we have incorporated the test statistics, effect sizes, and related details into the text of the results section for clarity.

(8) There are not enough methodological details in the main paper to make sense of the results. For example, it is not clear from reading the text that there are new object-location pairs learned each day.

Thank you for pointing this out. We have added this information to the main manuscript. Additionally, we have emphasized this information in the text referring to Figure 1B.

(9) The retrieval task does not seem to require retrieval of the scene itself, and as such it would be helpful for the authors to both explain their reasoning for this task to measure reinstatement. Strictly speaking, participants could just remember the location of the object on the screen. Was it verified that children and adults were recalling the actual scene rather than just the location (e.g. via self-report)? It's possible that there may be developmental differences in the tendency to reinstate the scene depending on e.g., their strategy.

Thank you for highlighting this important point. Indeed, the retrieval task included explicit instructions for participants to recall and visualize the scene associated with the object presented during the fixation time window. Participants were also instructed to recollect the location of the object within the scene. Since the location was contextually bound to the scene and each object had a unique location in each scene, the location of the object was always embedded in the specific scene context. We have added this information to both the Methods and Results sections.

From the self-reports of the participants (which unfortunately were not systematically collected on all occasions), they indicated that when they could recall the scene and the location due to the memory of stories created during strategic encoding, it aided their memory for the scene and location immensely. We also concur with your observation that children and young adults may differ in their ability to reinstate scenes, depending on the success of their employed recall strategies. This task was conducted with an awareness of potential developmental differences in the ability to form complex contextual memories. Our elaborative learning procedure was designed to minimize these differences. It is important to note though we did not expect children to achieve performance levels fully comparable to adults. There may indeed be developmental differences in reinstatement, such as due to differences in knowledge availability and accessibility (Brod, Werkle-Bergner, & Shing, 2013). We think that these differences may underlie our findings of neural reinstatement. This is now discussed in p. 34-35, 39-43 of the manuscript.

(10) In general I found the Introduction a bit difficult to follow. Below are a few specific questions I had.

a. At points findings are presented but the broader picture or take-home point is not expressed directly. For example, lines 112-127, these findings can all be conceptualized within many theories of consolidation, and yet those overarching frameworks are not directly discussed (e.g., that memory traces go from being more reliant on the hippocampus to more on the neocortex). Making these connections directly would likely be helpful for many readers.

Thank you for bringing this to our attention. We have incorporated a summary of the general frameworks of memory consolidation into the introduction. This addition outlines how our summarized findings, particularly those related to memory consolidation for repeatedly learned information, align with these frameworks (see lines 126-138, 146-150).

b. Lines 143-153 - The comparison of the Tompary & Davachi (2017) paper with the Oedekoven et al. (2017) reads like the two analyses are directly comparable, but the authors were looking at different things. The Tompary paper is looking at organization (not reinstatement); while the Oedekoven et al. paper is measuring reinstatement (not organization). The authors should clarify how to reconcile these findings.

Thank you for highlighting this aspect. We have revised how we present the results from Tompary & Davachi (2017). This study examined memory reorganization for memories both with and without overlapping features, and it observed higher neural similarity for memories with overlapping features over time. The authors also explored item-specific reinstatement for recent and remote memories by assessing encoding-retrieval similarity. Since Oedekoven et al. (2017) utilized a similar approach, their results are comparable in terms of reinstatement. We have updated and expanded our manuscript to clarify the parallels between these studies (see lines 157-162).

c. Line 195-6: I was confused by the prediction of "stable involvement of HC over time" given the work reviewed in the Introduction that HC contribution to memory tends to decrease with consolidation. Please clarify or rephrase.

Drawing on the Contextual Binding Theory (Yonelinas et al., 2019), as well as the Multiple Trace Theory (Nadel et al., 2000) and supported for instance by evidence from Sekeres et al. (2018), we hypothesized that detailed contextual memories formed through repeated and strategic learning would strengthen the specificity of these memories, resulting in consistent hippocampal involvement for successfully recalled contextualized detailed memories. We have included additional explanatory information in the manuscript to clarify this hypothesis (see lines 217-219).

d. Lines 200-202: I was a bit confused about this prediction. Firstly, please clarify whether immediate reinstatement has been characterized in this way for kids versus adults. Secondly, don't adults retain gist more over long delays (with specific information getting lost), at least behaviourally? This prediction seems to go against that; please clarify.

Thank you for raising this important point. Indeed, there are no prior studies that examined memory reinstatement over extended durations in children. The primary existing evidence suggests that neural specificity or patterns of neural representations in children can be robustly observed, while neural selectivity or univariate activation in response to the same stimuli tends to mature later (i.e., Fandakova et al., 2019). Bearing this in mind and recognizing that such neural patterns can be observed in both children and adults, we hypothesized that adults may form stronger detailed contextual memories compared to children. By employing strategies such as creating stories, adults might more easily recall scenes without the need to resort to forming generic or gist-like memories (for example, 'a red fox was near the second left pine tree in a spring green forest'). This assumption aligns with the Fuzzy Trace Theory (Reyna & Brainerd, 1995), which posits that verbatim memories can be created without the extraction of a gist.

Conversely, we hypothesized that children, due to the ongoing maturation of associative and strategic memory components (as discussed in Shing et al., 2008 and 2010), which are dependent respectively on the hippocampus (HC) and the prefrontal cortex (PFC), would be less adept at creating, retaining, and extracting stories to aid their retrieval process. This could result in them remembering more generic integrated information, like the relationship between a fox and some generic image of a forest. We have added explanatory information to the manuscript to elucidate these points (see lines 225-230).

Reviewer #1 (Recommendations For The Authors):

(1) For Figure 3, I would highly recommend changing the aesthetics for the univariate data - at least on my screen they appear to be open boxes with solid vs. dashed lines, and as such look identical to the recent vs. remove distinction in Figure 2B. It also doesn't match the legend for me, which shows the age groups having purple vs. yellow coloring.

Thank you for this observation. We have adjusted Figure 2 (now Figure 3) (please refer to p. 14) accordingly, now utilizing purple and yellow colors to distinguish between the age groups.

(2) Lines 329-330, it is not true that "all" indices were significant from zero but this is only apparent if you read the next sentence. Please rephrase to clarify. e.g., "All ... indices with a few exceptions ... were significantly..."?

Based on the above suggestions and considering our primary focus on time-related changes in scene-specific reinstatement, we will refrain from further interpreting the relative expression of individual scene-specific indices against 0. Consequently, we have removed this information from our analysis.

(3) It is challenging to interpret some of the significance markers, such as those in Figure 3. For example what effects are being denoted by the asterisks and bars above vs. below the data on panel D? Please clarify and/or note in the legend.

We have included a note in the legend to clarify the meaning of all significance markers. In addition, we decided to state any significant main and interaction effects in the figure rather that to use significance markers.

(4) For Figures 2 and 3, only the meaning of error bars is described in the caption. It is not explained in the caption what the boxes, lines, and points denote. Please clarify.

Thank you for highlighting this. We have added explanations to the figure's annotation for clarity. Please note, that considering other review’s suggestions figure plots may have been adjusted or changed, resulting in adjustment of the explanations in the figure annotation.

(5) How were recent and remote interspersed relative to one another? The text says that each run had 10 recent and 10 remote pairs, presented in a "pseudo-random order" - not clear what that (pseudo) means in this case. Please clarify.

Thank you for raising this point. We provide this information in the Methods section “Materials and Procedure”: 'The jitters and the order of presentation for recent and remote items were determined using OptimizeXGUI (Spunt, 2016), following an exponential distribution (Dale, 1999). Ten unique recently learned pairs (from the same testing day) and ten unique remotely learned items (from Day 0) were distributed within each run (in total three runs) in the order as suggested by the software as the most optimal. There were three runs with unique sets of stimuli each resulting in thirty unique recent and thirty unique remote stimuli overall.'

(6) Figure 1A, second to last screen on the learning cycles row - what would be presented to participants here, one of these three emojis? What does the sleepy face represent? I see some of these points were mentioned in the methods, but additional clarification in the caption would be helpful.

Thank you for highlighting this. We have included this information in the figure caption. Specifically, the sleepy face symbol in the figure denotes a 'missed response'.

(7) Not clear how the jittered fixation time between object presentation and scene test is dealt with in representational similarity analyses.

Thank you for pointing this out. Beta estimates were obtained from a Least Square Separate (LSS) regression model. Each event was modeled with their respective onset and duration and, as such, one beta value was estimated per event (with the lags between events differing from trial to trial). We have edited the corresponding section (see p. 53).  

(8) It was a little bit strange to have used anterior vs posterior HPC ROIs separately in univariate analysis but then combined them for multivariate. There are many empirical and theoretical motivations for looking at item-specific and category reinstatement in anterior and posterior HPC separately, so I was surprised not to see this. Please explain this reasoning.

Thank you for pointing this out. We agree with the reviewer and included the anterior and posterior HC ROIs into the multivariate analysis. Please see the revised results section (pp. 13-15).

(9) The term "neural specificity" is introduced (line 164) without explanation; please clarify.

Thank you for bringing this to our attention. The term ‘neural specificity’ refers to the neural representational distinctiveness of information. In other words, ‘neural specificity,’ as defined by Fandakova et al. (2019), refers to the distinctiveness of neural representations in the regions that process that sensory input. We decided, however to refrain from using this term and instead to use neural representational distinctiveness, which is more self-explaining and was also introduced in the manuscript.

(10) Age range is specified as 5-7 years initially (line 187) and then 6-7 years (line 188).

We have corrected the age range in line 188 to '5 to 7 years.'

Reviewer #2 (Public Reviews):

Schommartz et al. present a manuscript characterizing neural signatures of reinstatement during cued retrieval of middle-aged children compared to adults. The authors utilize a paradigm where participants learn the spatial location of semantically related item-scene memoranda which they retrieve after short or long delays. The paradigm is especially strong as the authors include novel memoranda at each delayed time point to make comparisons across new and old learning. In brief, the authors find that children show more forgetting than adults, and adults show greater engagement of cortical networks after longer delays as well as stronger item-specific reinstatement. Interestingly, children show more category-based reinstatement, however, evidence supports that this marker may be maladaptive for retrieving episodic details. The question is extremely timely both given the boom in neurocognitive research on the neural development of memory, and the dearth of research on consolidation in this age group. Also, the results provide novel insights into why consolidation processes may be disrupted in children. Despite these strengths, there are quite a few important design and analytical choices that derail my enthusiasm for the paper. If the authors could address these concerns, this manuscript would provide a solid foundation to better understand memory consolidation in children.

We thank the reviewer for both the positive and critical appraisal of our paper.

Reviewer #2 (Recommendations For The Authors):

(1) My greatest concern is the difference in memory accuracy that emerges as soon as immediate learning, which undermines the interpretation of any consolidation-related differences. This concern is two-fold. The authors utilize an adaptive learning approach in which participants learn to criteria or stop after 4 repetitions. This type of approach leads to children seeing the stimuli more often during learning compared to adults, which on its own could have consequences for consolidation-related neural markers. Specifically, within adults theoretical and empirical work this shows that repeating information can actually lead to more gist-like representations, which is the exact profile the children are showing. While there could be a strength to this approach because it allows for equivocal memory, the decision to stop repetitions before criteria means that memory performance is significantly lower in the children, which again could have consequences to consolidation-related neural markers. First, the authors do not show any of the learning-related data which would be critical to assess the impact of this design choice. Second, there are likely differences in memory strength at the delay, making it extremely difficult to determine if the neural markers reflect development, worse memory strength, or both. This issue is compounded by the use of a 3-AFC paradigm, wherein "correct responses" included in the analysis could contain a significant amount of guessing responses. I think a partial solution to this problem is to analyze the RT data and include them in the analyses or use a drift-diffusion modeling approach to get more precise estimates of memory strength to control for this feature. An alternative is to sub-select participants in each group to have a sample matched on performance (including # of repetitions) and re-run all the analyses in this sub-sample. Without addressing these concerns it is near impossible to interpret the presented data.

Thank you for highlighting this point.

Firstly, we believe that our approach, involving strategic and repeated learning coupled with feedback, enhances the formation of detailed contextual memories. The retrieval procedure also emphasized the need for detailed memory for location. These are critical differences in experimental procedure from previous studies, which enhanced the importance of detailed representations and likely reduced the likelihood of forming gist-like memories.

Indeed, we ceased further learning after the fourth repetition. Extensive piloting, where we initially stopped after the seventh repetition, showed no improvement beyond the fourth repetition. In fact, performance tended to decline due to fatigue. Therefore, we limited the number of repetition cycles to the point where an improvement of performance was still feasible. Even though children exhibited lower final learning performance overall, we believe our procedure facilitated them to reach their maximal performance within the experimental setup.

To address the reviewer’s concern, we included learning data to illustrate the progression of learning (see Fig. 1C, pp. 9-10 in Results).

When interpreting the retention rates, it is important to note that we reported retention rates only for items that were correctly learned (100%) on day 0, day 1, and day 14. This approach meant that different participants had varying numbers of items learned correctly. However, this method enabled us to address our primary question: whether memory consolidation, based on all items initially encoded successfully, is comparably robust between the groups. To simultaneously examine the change in retention rate slopes over time for recent (30 minutes after learning), short delay (one night after) remote, and long delay (two weeks after) remote items, we conducted a separate analysis of retention rates for recent items on days 1 and 14. After observing no differences between sessions in both age groups, we combined the data for recent items. This allowed us to investigate how the slope of memory retention for initially correctly learned items (with a baseline of 100%) changes over time. We observed a significant interaction between item type (recent, short delay remote, long delay remote) and group. Analysis of this interaction revealed significantly less robust memory consolidation across all delay times for children compared to young adults. The figures have been adjusted accordingly to incorporate the baseline of 100% correct performance.

Following your suggestion, we also employed the drift diffusion model approach to characterize memory strength, calculating drift rate, boundary and non-decision time parameters. We added the results to the Supplementary Materials (section S2.1, Figure S1).

Generally, our findings indicate lower overall drift rate in children when considering all items that had to be learned. We also observed that adults show higher slope of decline in drift rate in short and long delay, which, however, are characterized still by higher memory strength compared to children. Both age groups required similar amount of evidence to make decision, which declined with delay. It may indicate an adaptation of weaker memory. Further, we observed lesser non-decision time in children compared to adults, potentially suggesting less error checking or less thorough processing and memory access through strategy in children.

Overall, these results indicate weaker memory strength in children as a quantitative measure. It may nevertheless stem from qualitatively different memory representations that children form, as our RSA findings suggest. We believe that our neural effect reflects the effect of interest (i.e., worse memory due to lower memory strength in children). When controlled for, it will take away variance of interest in the neural data. Therefore, we will refrain from including memory strength into the model. However, we will include mean RT as the indicator of general response tendencies.

Given that the paper is already very complex and long, we opted to add the diffusion model results to the Supplementary Materials (section S2.1, Fig. S1), while discussing the results in the discussion (p. 35).

(2) More discussion of the behavioral task should be included in the results, in particular the nature of the adaptive learning paradigm including the behavioral results as well as the categorical nature of the memoranda. Without this information, it is difficult for the reader to understand what category-level versus item-level reinstatement reflects.

Thank you for this valuable input. We have incorporated this information into the results section. Please refer to pp. 9-10, 12, 14, 21, 25-26 for the added details.

(3) Some of the methods for the reinstatement analysis were unclear to me or warranted further adjustment. I believe the authors compared the scene against all other scenes. I believe it would be more appropriate to only compare this against scenes drawn from the same category as opposed to all scenes. Secondly, from my reading, it seems like the reinstatement was done during the scene presentation, rather than the object presentation in which they would retrieve the scene. I believe the reinstatement results would be much stronger if it was captured during the object presentation rather than the re-presentation of the scene. Or perhaps both sets of analyses should be included.

We apologize for the confusion regarding the analysis method.

During the review process we have improved the description of this analysis and hope it is easier to follow now. In short, we used both approaches (within and between categories) to suit different goals (I.e., measuring scene-reinstatement and gist-like reinstatement).

Both types of reinstatement were assessed during the fixation cross to avoid confounds with the object itself being on the screen. We only used the scene window in one analysis (scene-reinstatement index) as a neural template to track its pre-activation during the fixation. So, as the reviewer suggests, our rationale is that the reinstatement indeed starts taking place at the short object presentation window, but importantly, extends to the fixation window. We added this clarifying information to the results section (see p. 21-27).

(4) For the univariate results, it was unclear to me when reading the results whether they were focusing on the object presentation portion of the trial or the scene presentation portion of the trial. Again, I think the claims of reinstatement related activity would be stronger if they accounted for the object presentation period.

Thank you for pointing this out. Indeed, the univariate results were based on the object presentation time window. We added this information to the results section (Fig. 3, pp. 14, 16).

(5) Further, given the univariate differences shown across age groups, the authors should re-run all analyses for the RSA controlling for mean activation within the ROI.

Thank you for highlighting this. We re-ran all analysis for the RSA controlling for the mean activation within the ROI. The results remained unchanged. We have added this information to the results section as well as in Table S8 and S11 in the Supplementary Materials for further details.

(6) The authors should include explicit tests across groups for their brain-behavior analyses if they want to make any developmentally relevant interpretations of the data. Also, It would be helpful to include similar analyses to those using the univariate signals, and not just the RSA results.

Following reviewer’s suggestion, we included brain-behavior analyses for univariate data as well as RSA data with explicit tests across groups. These can be found in the Results Section pp. 18-20, 28-32. Due to the interdependence of predefined ROIs and to avoid running a high number of correlation tests, we employed the partial least square correlation analysis for this purpose. This approach focuses on multivariate links between specified Regions of Interest (ROIs) and fluctuations in memory performance over short and long delays across different age cohorts. We argue that this multivariate strategy offers a more comprehensive understanding of the relationships between brain metrics across various ROIs and memory performance, given their mutual dependence and connectivity (refer to Genon et al. (2022) for similar discussions).

(7) There could be dramatic differences in memory processing across 5-7 year olds. I know the sample is a little small for this, but I would like to see regressions done within the middle childhood group in addition to the across-group comparisons.

We have included information detailing the relationship between memory retention rate and age within the child group (refer to p. 13). In the child group, both recent and short delay remote memory improved with age. However, the retention rate for long-delayed memory did not show a significant improvement with increasing age in children.

(8) I am concerned that the authors used global-signal as a regressor in their first-level analyses, given that there could be large changes in the amount of univariate activation that occurs across groups. This approach can lead to false positives and negatives that obscure localized differences. The authors should remove this term, and perhaps use the mean sum of the white matter or CSF to achieve the noise regressor they wanted to include.

We understand the reviewers' concerns. However, we believe that our approach is recommended for the pediatric population. Specifically, Graff et al., 2021, found that global signal regression is a highly efficacious denoising technique in their study of 4 to 8-year-old children. This technique was previously suggested for adults by Ciric et al., 2017, and the benefits in terms of motion and physiological noise removal outweigh the potential costs of removing some signal of interest, as indicated by Behzadi et al., 2007. Additionally, we incorporated the six anatomic component-based noise correction (CompCor) to account for WM and CSF signals, as recommended in the pediatric literature.

(9) The authors discuss the relationship between hippocampal reactivation and worse memory through the lens of Schapiro et al., but a new paper by Tanriverdi et al came out in JOCN recently that is more similar to the authors' findings.

Thank you for highlighting the recent paper by Tanriverdi et al. in JOCN, which aligns closely with our findings. We appreciate the suggestion and agree that exploring this alignment could further enrich our discussion on the relationship between hippocampal reactivation and memory retention. We incorporated this work in our revised manuscript .

Minor Comments

- I was surprised that the authors did not see any differences in univariate signals for memory retrieval as a function of development, as much of the prior work has shown differences (for example work by Tracy Riggins). I believe this contrast should be highlighted in the discussion.

- Given the robust differences in sleep patterns across childhood and the role of sleep in systems consolidation framework, I think this feature should be highlighted in either the introduction or discussion.

- Could the authors report on differences (or lack of differences) in head motion across the groups, and if they are different whether they could include them as a confounding variable.

I believe we included six motion parameters and their derivatives into the model

Thank you for your comments.

First, prior works on univariate signals of memory retrieval focused mostly on remembered vs forgotten contrasts, while in our study we focused on remote vs recent in short and long delay only for correctly remembered items. This can partially explain the results. We highlighted this information in the discussion session.

Second, we agree with the reviewer that sleep patterns across childhood should be addressed in the analysis. Therefore, we incorporated them in the discussion section.

Third, indeed head motion were included in the analysis as confounding variables, as adding them is highly recommended for the developmental population (e.g., Graff et al. 2021). As an example, we observed higher framewise displacement in children compared to adults, t = -16(218), p <. 001, as well as in translational y, t = -2.33(288), p = .02.

Reviewer #3 (Public Reviews):

Summary:

This study aimed to understand the neural correlates of memory recall over short (1-day) and long (14-days) intervals in children (5-7 years old) relative to young adults. The results show that children recall less than young adults and that this is accompanied by less activation (relative to young adults) in brain networks associated with memory retrieval.

Strengths:

This paper is one of few investigating long-term memory (multiple days) in a developmental population, an important gap in the field. Also, the authors apply a representational similarity analysis to understand how specific memories evolve over time. This analysis shows how the specificity of memories decreases over time in children relative to adults. This is an interesting finding.

We thank the reviewer for the appraisal of our manuscript.

Weaknesses:

Overall, these results are consistent with what we already know: recall is worse in children relative to adults (e.g., Cycowicz et al., 2001) and children activate memory retrieval networks to a lesser extent than adults (Bauer et al, 2017).

It seems that the reduced activation in memory recall networks is likely associated with less depth of memory encoding in children due to inattentiveness, reduced motivation, and documented differences in memory strategies. In regard to this, there was consideration of IQ, sex, and handedness but these were not included as covariates as they were not significant although I note p<.16 suggests there was some level of association nonetheless. Also, IQ is measured differently for the children and adults so it's not clear these can be directly contrasted. The authors suggest the instructed elaborative encoding strategy is effective for children and adults but the reference in support of this (Craik & Tulving, 1975) does not seem to support this point.

Thank you for your review, and we appreciate your valuable feedback. Here are our responses and clarifications:

Regarding the novelty of the results in terms of mentioned existent literature, we believe that in contrast to Cycowicz et al. (2001) and Bauer et al (2017), etc, we assess not only immediate memory after encoding with semantic judgement of abstract associations, but add to these findings investigating consolidation-related changes in complex associative and contextual information in much under investigated sample of 5-to-7-year-old preschoolers. With this we are able to infer also how neural representations of children change over time, providing invaluable insights into knowledge formation in this developmental cohort.

With this, the observed age differences are not so of primary importance, as time-related changes in mnemonic representations observed in children.

Regarding the assumption of inattentiveness in children, we want to emphasize that the experimenter was present throughout the learning process, closely supervising the children. We observed prompt responses to every trial in children and noted an increase in accuracy over the encoding-learning cycles, leading us to conclude that the children were indeed attentive to the task. The observed accuracy improvement across learning cycles  indicates increase in remembered information. Furthermore, we took measures to ensure their engagement, including extensive training in both verbal and computerized versions to ensure that they understood and actively created stories to support their learning.

We collected motivation data after each task execution in children, and the results indicated that they scored high in motivation. Children not only completed the tasks but also expressed their willingness to participate in subsequent appointments, highlighting their active involvement in the study.

The observed differences in the efficiency of strategy utilization were expected, given developmental differences in the associative and strategic components of memory in children, as noted in prior research (Shing, 2008, 2010).

We appreciate your point about IQ, sex, and handedness. These variables were indeed included in the behavioral models, and mean brain activation was also included in the brain data models, addressing the potential influence of these factors on our results.

While it's true that we applied different tests to measure IQ in children and adults, these tests targeted comparable subtests that addressed similar cognitive constructs. As the final IQ values are standardized, we believe it is appropriate to compare them between the two groups.

Lastly, we agree that the citation Craik & Tulving, 1975 supports the notion of effectiveness of instructed elaborative learning only in adults, but not in children. For this purpose, we added relevant literature for the child cohort (i.e., Pressley, 1982; Pressley et al., 1981; Shing et al., 2008).

Reviewer #3 (Recommendations For The Authors):

An additional point for the authors to consider is that the hypotheses were uncertain. The first is that prefrontal, parietal, cerebellar, occipital, and PHG brain regions would have greater activation over time in adults and not children - which is very imprecise as this is basically the whole brain. Moreover, brain imaging data may be in opposition to this prediction: e.g., the hippocampus has a delayed maturational pattern beyond 5-yrs (e.ge., Canada 2019; Uematsu 2012) and some cortical data predicts earlier development in these regions.

Thank you for your feedback, and we appreciate your insights regarding our hypotheses.

The selection of our regions of interest (ROIs) was guided by prior literature that has demonstrated the interactive involvement of multiple brain areas in memory retrieval and consolidation processes. Additionally, our recent work utilizing multivariate partial least square correlation analysis (Schommartz, 2022, Developmental Cognitive Neuroscience) has indicated that unique profiles derived from the structural integrity of multiple brain regions are differentially related to short and long-delay memory consolidation.

Indeed, the literature suggests that the hippocampus may exhibit a more delayed maturational pattern extending into adolescence, as supported by studies such as Canada (2019) and Uematsu (2012), etc. We added this information as well as findings from the literature on cortical development to be more balanced in our review of the literature.

Given this complexity, we believe it is important to emphasize in our discussion that both the medial temporal lobe, including the hippocampus, and cortical structures, as well as the cerebellum, undergo profound neural maturation. We highlight these nuances in our revised manuscript to provide a more comprehensive perspective on the developmental differences in memory retention over time.

The writing was challenging to follow - consider as an example on page 9 the sentence that spans 10 lines of text.

Thank you for bringing this to our attention. We have carefully reviewed the manuscript and have made efforts to streamline the text, ensuring that sentences are not overly long or complex to improve readability and comprehension.

I found the analysis (and accompanying figures) a bit of a data mine - there are so many results that are hard to digest and in other cases highly redundant one from the other. This may be resolved in part by moving redundant findings to the supplemental. Some were hard to follow - so when there is a line between recent and recent data, that seems confusing to connect data that, I believe, are different sets of items. Later scatterplots (Fig 7) have pale yellow dots that I had a hard time seeing.

Thank you for bringing up your concerns regarding the analysis and figures in our manuscript. We have carefully considered your feedback and made several improvements to address these issues.

To alleviate the challenge of digesting numerous results, we have taken steps to enhance clarity and reduce redundancy. Specifically, we have moved some of the redundant findings to the supplementary sections, which should help streamline the main manuscript and make it more reader friendly.

Regarding the line between 'recent' and 'recent data,' figure were transformed to a clearer version. Furthermore, we have improved the visibility of certain elements, such as the pale-yellow dots in the scatterplots (Fig 1, 2, 4, etc. ), to ensure that readers can better discern the data points.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review): 

[…] 

Weaknesses: 

The question of the physiological relevance of short bouts of ischemia remains.

The chemical ischemia protocol induces a duration-dependent ATP depletion in acute slices on a time scale of minutes (Pape and Rose 2023). This is about the same time scale as the peri-infarct depolarisation (Lauritzen et al. 2011) that the protocol attempts to model. Of course, such models do not completely replicate the complex situation in vivo. However, the presented analyses of synapse function cannot be performed in vivo. We discuss this now in the manuscript.

The precise mechanisms underlying the shift between ischemia-induced long-term potentiation and long-term failure of synaptic responses were not addressed. Could this be cell death?

Thank you for the comment. Yes, we indeed believe that the persistent failure of synaptic transmission is because of neuronal cell death (i.e., of CA1 pyramidal cells) or at least persistent depolarisation. We did not explicitly state that in the original submission but do so in the revised manuscript. It is supported by the unquantified observation of swelling and/or loss of integrity of CA1 pyramidal cell bodies in parallel to postsynaptic failure. It is also in line with many reports from the literature, of which we now cite two (lines 186-198).

Sex differences are not addressed or considered.

We have performed all experiments on male mice, as indicated in Material and Methods. We have indeed not addressed sex differences of the observed effects. We consider this, and many other important factors, to be interesting topics for follow-up studies. This is now discussed (lines 413-424).

Reviewer #2 (Public Review): 

[…]

Weaknesses: 

The weaknesses are minor and only relate to the interpretation of some of the data regarding the presynaptic mechanisms causing the potentiation of release. The authors measured the fiber volley, which reflects the extracellular voltage of the compound action potential of the fiber bundle. The half-duration of the fiber volley was increased, which could be due to the action potential broadening of the individual axons but could also be due to differences in conduction velocity. We are therefore skeptical whether the conclusion of action broadening is justified.

These are excellent points. We have added an analysis demonstrating that axonal conduction velocity is unlikely to be affected. Nonetheless, the fiber volley is indeed an indirect measure of what happens in individual axons. We have adjusted our interpretation accordingly and now also discuss alternative explanations of our findings (lines 363-379).

Reviewer #3 (Public Review): 

[…]

Weaknesses: 

The data on fiber volley duration should be supported by more direct measurements to prove that chemical ischemia increases presynaptic Ca2+ influx due to a presynaptic broadening of action potentials. Given the influence that positioning of the stimulating and recording electrode can have on the fiber volley properties, I found this data insufficient to support the assumption of a relationship between increased iGluSnFR fluorescence, action potential broadening, and increased presynaptic Ca2+ levels.

We have added a new analysis showing that the latency of the fiber volley is unaffected and relatively constant, which strengthens our conclusion. But the fiber volley is indeed an indirect measure of action potential firing in individual axons. The suggested experiment, which would require simultaneous recording of Ca2+ and action potentials in single axons in combination with chemical ischemia, is extremely difficult, if possible at all. Instead, we have extended the discussion and include now further alternative mechanistic explanations (lines 363-379).

The results are obtained in an ex-vivo preparation, it would be interesting to assess if they could be replicated in vivo models of cerebral ischemia. 

This would certainly be very interesting but also extremely challenging technically. For a detailed analysis of synaptic changes as presented here, the main difficulty will be to stimulate and visualise glutamate release exclusively in an isolated population of synapses while recording postsynaptic responses in a stroke model.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors): 

[…]

Labelling of experimental groups of 2-minute and 5-minute chemical ischemia is more accurate than "metabolic stress" and "with postsynaptic failure". The critical difference between these two conditions is lost with this nomenclature. The reader could be misled to believe that the two groups form a heterogenous population of responses from the same experimental manipulation which is incorrect.

We had stated in the manuscript that we ‘ … grouped combined iGluSnFR and electrophysiological recordings according to the effect of chemical ischemia on the synaptic response: ‘chemical ischemia with postsynaptic failure’ if the postsynaptic response did not recover to above 50% of the baseline level and ‘chemical ischemia’ when it did (as indicated in Fig. 1H). …’. The recordings were not grouped according to chemical stress duration but according to the effect on the postsynaptic response. We have revised the text explaining this (lines 125-135) and illustrate that now also in Fig. 1H. We hope this is easier to follow now.

More details on the long-term impact of 5-minute ischemia on cell viability would be enlightening regarding the specific mechanism separating these two conditions. With 2 minutes it would appear that cells remain alive (i.e. intact post-synaptic responses), 5 minutes however, inducing cell death. 

Yes, our observations, although not quantified, are in line with cell death as CA1 pyramidal cell bodies appeared swollen and/or lost their integrity when chemical ischemia was followed by postsynaptic failure. This is also in line with reports from the literature. We have revised the results section accordingly (lines 186-201).

In the paragraph titled "glutamate uptake is unaffected after acute chemical ischemia", there are two erroneous citations of Figure S3 that should be Figure S4.

Thank you. We corrected this mistake.

The sex of animals is not given. This is essential information. 

We used male mice as indicated in the initial version of the manuscript (Material and Methods). We have added a statement regarding the role of sex to the final section of the Discussion.

Reviewer #2 (Recommendations For The Authors):

We propose addressing the weaknesses mentioned in the public review. As said, the fibre volley is a very indirect measure of action potential broadening. Based on the iGluSnFR data, the authors predict that the potentiation is mediated by depolarization, action potential broadening, and increased presynaptic calcium influx. The latter could be tested experimentally, but this does not seem necessary if the data are interpreted more cautiously. For example, other explanations for the broadened fiber volley could be mentioned, such as a slowing and/or dispersion of the action potential propagation speed. Furthermore, depolarization could cause elevated resting calcium concentrations, which could potentiate release independently of action potential broadening. Finally, classical forms of presynaptic potentiation of the release machinery that occur during homeostatic plasticity or Hebbian plasticity may operate independently of calcium dynamics.

Thank you for this comment. The discussion of the mechanism was indeed too short. We have added an analysis of the fiber volley delay after stimulation, which was not affected. Presynaptic action potential broadening is, in our opinion, a very likely explanation for our observations but we did not perform direct experiments. Directly recording presynaptic action potentials and Ca2+ transients in the chemical ischemia model over extended periods of time is a major technical challenge and certainly of interest in the future. As suggested, we have expanded the discussion section and now mention various alternative explanations (lines 363-379).

There are the following minor suggestions:

Add line numbers.

We have added line numbers.

We would suggest providing exact P values instead of asterisks in the figures. 

We agree that having exact P values in the figure panels can be very helpful. However, in the present figures they are hard to integrate without overcrowding the already complex panels and thereby obscuring other important details. All p-values are included in the figure legends and/or main text.

Abstract: "We also observed an unexpected hierarchy of vulnerability of the involved mechanisms and cell types." This sentence is hard to understand and cell types were not directly compared (i.e. axons of CA3 and axons of CA1 neurons were not compared).

We have revised this statement and removed the reference to cell types.

In Figure 1G there seems to be an increase in the fiber volley. Is this significant? Could this be due to swelling of the slice during chemical ischemia? Or an increase in excitability? Maybe this could be discussed. 

The effect was analysed in the context of Fig. 2. A significant increase of the fiber volley amplitude was detected in chemical ischemia (Fig. 2H) but also under control conditions (Fig. 2F). We therefore consider this a change that is detectable but not related to chemical ischemia and not a potential explanation for increased glutamate release (lines 157-160). Also, no significant fiber volley increase was detected in chemical ischemia with postsynaptic failure (Fig. 2H) and in the experiments illustrated in Fig. 4E. Our interpretation is that the fiber volley unspecifically increases in some experiments over the time course of the experiment (~ 60 min) but this is unrelated to chemical ischemia.

In the results: "A fully separate set of experiments..." Please explain better what this means. 

We have revised the entire section to explain more clearly how recordings were grouped (lines 125135).

In the results: "...(Syková and Nicholson, 2008) (Figure S3). However, this was not observed for chemical ischemia without postsynaptic failure (Figure S3), in which the increased glutamate transients were observed." This should probably refer to Figure S4. 

Thank you for spotting this mistake. We corrected it.

The last sentence in the results "... most likely by increased presynaptic Ca2+ influx, and, at the same time, the postsynaptic response." This is difficult to understand. Does "at the same time" refer to another mechanism or the consequence of more Ca2+? 

We revised this part of the results section to improve clarity and toned down our conclusions (lines 328-335 and 363-379).

Reviewer #3 (Recommendations For The Authors): 

There are a few points that the author needs to clarify: 

The authors do not discuss the different behaviour of iGlu F0 during chemical ischemia and chemical ischemia with postsynaptic failure shown in Figure 2, panels D and E. In the first case, during the application of the solution to induce ischemia, iGluF0 decreases while in the other case, it strongly increases before falling down. In both cases, the fEPSP slope is decreased. How does the author explain this observation? 

We attribute the transient increase of extracellular glutamate during prolonged chemical ischemia to the increase of synaptic glutamate release observed previously under such conditions (Hershkowitz et al. 1993; Tanaka et al. 1997) and other mechanisms reviewed by us (Passlick et al. 2021) (e.g., glial glutamate release, transiently reduced glutamate uptake), which we could not detect during shorter chemical ischemia. The initial drop of the fEPSP slope is most likely due to postsynaptic depolarisation, which is followed by a repolarisation if the chemical stress duration is short. We now explain this in more detail in lines 185-200 of the revised manuscript. Although we focussed on the bi-directional effect on longer timescales in this manuscript, this transient phase during chemical ischemia is very interesting for further investigations.

On page 8, first line, I think that the authors meant Figure S4, not Figure S3 when they mentioned results on ECS diffusivity and ECS fraction. 

Yes, thank you for spotting this. We corrected the mistake.

In Supplementary Figure 5 panel B It seems that PPR is significantly reduced upon chemical ischemia (asterisk on columns green) but the authors claimed in the paper at page 10 that "Analysing the paired-pulse ratio (PPR) of postsynaptic response and iGluSnFR transients revealed no consistent changes after chemical ischemia (Figure S5).". Did the authors refer to the data normalized in panel D? In this case, I do not see the need to normalize raw data that have been already shown in a previous panel and that give different statistical results, probably due to the different tests used (paired in panel B and not paired in panel D). 

We have clarified this point in the supplementary material (Figure S5, legend). There is a relevant difference between the analyses presented in panel B and D. The paired test presented in B analyses the change of the electrophysiological PPR in response to chemical ischemia. The test in D on the electrophysiologically PPR asks if the reduction in B is significantly different from the changes seen under control conditions. Because it is not, we conclude that chemical ischemia has no relevant effect on the electrophysiological PPR and, in combination with the results on the iGluSnFR PPR, also not on short-term plasticity, as tested here.

References

Hershkowitz N, Katchman AN, Veregge S. Site of synaptic depression during hypoxia: a patch-clamp analysis. Journal of Neurophysiology 69: 432–441, 1993.

Lauritzen M, Dreier JP, Fabricius M, Hartings JA, Graf R, Strong AJ. Clinical Relevance of Cortical Spreading Depression in Neurological Disorders: Migraine, Malignant Stroke, Subarachnoid and Intracranial Hemorrhage, and Traumatic Brain Injury. J Cereb Blood Flow Metab 31: 17–35, 2011.

Pape N, Rose CR. Activation of TRPV4 channels promotes the loss of cellular ATP in organotypic slices of the mouse neocortex exposed to chemical ischemia. The Journal of Physiology 601: 2975–2990, 2023.

Passlick S, Rose CR, Petzold GC, Henneberger C. Disruption of Glutamate Transport and Homeostasis by Acute Metabolic Stress. Front Cell Neurosci 15: 637784, 2021.

Tanaka E, Yamamoto S, Kudo Y, Mihara S, Higashi H. Mechanisms Underlying the Rapid

Depolarization Produced by Deprivation of Oxygen and Glucose in Rat Hippocampal CA1 Neurons In Vitro. Journal of Neurophysiology 78: 891–902, 1997.

Author response:

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

Public Review:

Reviewer #1 (Public Review):

In 'Systems analysis of miR-199a/b-5p and multiple miR-199a/b-5p targets during chondrogenesis', Patel et al. present a variety of analyses using different methodologies to investigate the importance of two miRNAs in regulating gene expression in a cellular model of cartilage development. They first re-analysed existing data to identify these miRNAs as one of the most dynamic across a chondrogenesis development time course. Next, they manipulated the expression of these miRNAs and showed that this affected the expression of various marker genes as expected. An RNA-seq experiment on these manipulations identified putative mRNA targets of the miRNAs which were also supported by bioinformatics predictions. These top hits were validated experimentally and, finally, a kinetic model was developed to demonstrate the relationship between the miRNAs and mRNAs studied throughout the paper.

I am convinced that the novel relationships reported here between miR-199a/b-5p and target genes FZD6, ITGA3, and CAV1 are likely to be genuine. It is important for researchers working on this system and related diseases to know all the miRNA/mRNA relationships but, as the authors have already published work studying the most dynamic miRNA (miR-140-5p) in this biological system I was not convinced that this study of the second miRNA in their list provided a conceptual advance on their previous work.

We believe this study is an enhancement on our previous work for two reasons, which have been alluded to in new text within the introduction. Firstly, our previous work used experimental and bioinformatic analysis to identify microRNAs with significant regulatory roles during chondrogenesis. This new manuscript additionally uses  a systems biology approaches to identify novel miRNA-mRNA interactions and capture these within an in silico model. Secondly, this work was initiated by the analysis of our previously generated data – using a novel tool we developed for this type of data (Bioconductor - TimiRGeN).  

I was also concerned with the lack of reporting of details of the manipulation experiments. The authors state that they have over-expressed miR-199a-5p (Figure 2A) and knocked down miR-199b-5p (Figure 2B) but they should have reported their proof that these experiments had worked as predicted, e.g. showing the qRT-PCR change in miRNA expression. Similarly, I was concerned that one miRNA was over-expressed while the other was knocked down - why did the authors not attempt to manipulate both miRNAs in both directions? Were they unable to achieve a significant change in miRNA expression or did these experiments not confirm the results reported in the manuscript?

We agree with the reviewer that some additional data were needed to demonstrate the effective regulation of miR-199-5p.  Hence, Supplementary Figure 1 is now included which provides validation of the effects of miR-199a-5p overexpression

(Supplementary Figure 1A) and inhibition of miR-199a/b-5p (Supplementary Figure 1B). Within the main manuscript, Figure 2B has been amended to include the consequences of inhibition of miR-199a-5p, with 2C showing the consequences of miR-199b-5p inhibition. Further, we include new data with regards to miR-199a/b-5p inhibition on CAV1 (Figure 4A). 

I had a number of issues with the way in which some of the data was presented. Table 1 only reported whether a specific pathway was significant or not for a given differential expression analysis but this concealed the extent of this enrichment or the level of statistical significance reported. Could it be redrawn to more similarly match the format of Figure 3A? The various shades of grey in Figure 2 and Figure 4 made it impossible to discriminate between treatments and therefore identify whether these data supported the conclusions made in the text. It also appeared that the same results were reported in Figure 3B and 3C and, indeed, Figure 3B was not referred to in the main text. Perhaps this figure could be made more concise by removing one of these two sets of panels.

We agree with all points made here and have amended these within the manuscript. Figure 1A is now pathway enrichment plots from the TimiRGeN R Bioconductor package, and the table which previously showed the pathways enriched at each time point is now in the supplementary materials (supp. Table 1). Figure 2 and 4 now have color instead of shades of grey. Figure 3C has now been moved to supplementary materials (Supplementary Figure 2) and is referenced in the text. 

Overall, while I think that this is an interesting and valuable paper, I think its findings are relatively limited to those interested in the role of miRNAs in this specific biomedical context.

Reviewer #2 (Public Review):

Summary:

This study represents an ambitious endeavor to comprehensively analyze the role of miR199a/b-5p and its networks in cartilage formation. By conducting experiments that go beyond in vitro MSC differentiation models, more robust conclusions can be achieved.

Strengths:

This research investigates the role of miR-199a/b-5p during chondrogenesis using bioinformatics and in vitro experimental systems. The significance of miRNAs in chondrogenesis and OA is crucial, warranting further research, and this study contributes novel insights.

Weaknesses:

While miR-140 and miR-455 are used as controls, these miRNAs have been demonstrated to be more relevant to Cartilage Homeostasis than chondrogenesis itself. Their deficiency has been genetically proven to induce Osteoarthritis in mice. Therefore, the results of this study should be considered in comparison with these existing findings.

We agree with the reviewers comments. miR-455-null mice develop normally but miR-140-null (or mutated) mice and humans do have skeletal abnormalities (e.g. Nat Med. 2019 Apr;25(4):583-590. doi: 10.1038/s41591-019-0353-2), indicating a role in chondrogenesis.  We have made an addition in the description to point towards the need to assess the roles miR-199a/b-5p may play during skeletogenesis and OA. We anticipate miR-199a/b-5p to be relevant in OA and have ongoing additional work for this – but this beyond the scope of this manuscript. 

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

Beyond the issues raised in the public review, I had a few minor recommendations that are largely designed to help improve the understanding of the manuscript as it is currently written.

(1) Please provide the statistical tests used to obtain p-values in the Figure 2 and 4 legends.

We have now added statistical test information to the figure legends of figures 2 and 4.

(2) It is stated on p. 9 that both miRNAs may share a functional repertoire because 25 and 341 genes are interested between their inhibition experiments. Please provide statistical support that this overlap is an enrichment over the null background in this experiment. Total DE genes – chi squared. Expected / Observed. 

A chi-squared test is now presented in the manuscript which shows that the number of significant genes which were found in common between miR-199a-5p knockdown and miR-199b-5p knockdown were significantly more than expected for day 0 or day 1 of the experiments. 

(3) The final sentence on p. 12 (beginning 'Size of the points reflect...') seemed out of place - is it part of a legend?

Thank you for pointing out this mistake - it was part of figure 3C and now is in the supplementary materials.

(4) A sentence on p. 14 reads that 'FZD6 and ITGA3 levels increased significantly' but this should read decreased, rather than increased. Quite an important typo!

Thank you for pointing this error out. It has been corrected.

(5) Theoretical transcripts are mentioned in the legend of Figure 5A but these were not present in the figure. Please include these or remove them from the legend.

This error has been removed form Figure 5A.

(6) On p 20, the references 22 and 27 should I think be moved to earlier in the sentence (after 'miR-199a-5p-FZD6 has been predicted previously'). Currently, it reads as if these references support your luciferase assays which you claim are the first evidence for this target relationship.

We agree with this change and have corrected the manuscript.

(7) The reference to Figure 5D on p. 20 should be a reference to Figure 5C.

Thank you for pointing this error out – this has been corrected.

Reviewer #2 (Recommendations For The Authors):

(1) The paper is based on the importance of miR-140 and miR-455 as miRNAs in chondrogenesis, citing only Barter, M. J. et al. Stem Cells 33, (2015). Considering the scope and results of this study, this citation is insufficient.

We agree with this reviewers comments. For many year miR-140 and miR-455 have been experimented on and their importance in OA research has become apparent. We included additional references within the introduction to address this.

(2) Analyzing chondrogenesis solely through differentiation experiments from MSCs is inadequate. It is essential to perform experiments involving the network within normal cartilage tissue and/or the generation of knockout mice to understand the precise role of miR199a/b-5p in chondrogenesis.

We have added an additional paragraph in the discussion to state this, and do believe it is highly important that miR-199a/b-5p be tested in OA samples – however this would be beyond the intended scope of this article.

(3) In light of the above points, it is imperative to investigate the role of miR-199a/b-5p beyond the in vitro differentiation model from MSCs, encompassing mouse OA models or human disease samples.

In tangent with the previous address, we agree with the pretense and believe additional experiments should be performed to gain more insight to the mechanism of how miR-199a/b-5p regulate OA. But development of a new mouse line to investigate this is not in the scope of this manuscript.

Author response:

eLife assessment

This important study describes the crystallographic screening of a number of small molecules against a viral enzyme critical for the 5' capping of SARS-CoV-2 RNA and viral replication. While the high-quality crystal structures and complementary biophysical assays in this study provide solid evidence to support the major claims regarding how these small molecule compounds bind to the viral enzyme, the mismatch between the antiviral activity and binding to the viral enzyme of several small molecule compounds could have been more thoroughly investigated or discussed. This paper would be of interest to the fields of coronavirus biology, structural biology, and drug discovery.

We do fully agree that the antiviral assay results could be brought better into context clarifying that the antiviral effects of tubercine and its derivates are due to off-target effects.

Reviewer #1 (Public Review):

Summary:

This manuscript describes the crystallographic screening of a number of small molecules derived from the natural substrates S-adenosyl methionine (SAM) and adenine, against the SARS-CoV-2 2'-O-methyltransferase NSP16 in complex with its partner NSP10. High-quality structures for several of these are presented together with efforts to evaluate their potential biophysical binding and antiviral activities. The structures are of high quality and the data are well presented but do not yet show potency in biophysical binding. They only offer limited insights into the design of inhibitors of NSP16/10.

Strengths:

The main strengths of the study are the high quality of the structural data, and associated electron density maps making the structural data highly accurate and informative for future structure-based design. These results are clearly presented and communicated in the manuscript. Another strength is the authors' attempts to probe the binding of the identified fragments using biophysical assays. Although in general the outcome of these experiments shows negative data or very weak binding affinities the authors should be commended for attempting several techniques and showing the data clearly. This study is also useful as an example of the complexities associated with drug discovery on a bi-substrate target such as a methyltransferase, several of the observed binding poises were unexpected with compounds that are relatively similar to substrates binding in different parts of the active site or other unexpected orientations. This serves as an example of how experimental structural information is still of crucial importance to structure-based drug design. In general, the claims in the manuscript are well supported by the data.

Weaknesses:

The main limitations of the study are that the new structures generated in the study are fairly limited in terms of chemical space being similar to either SAM or RNA-CAP analogues. It feels a little bit of a lost opportunity to expand this to more diverse ligands which may reveal potential inhibitors that are distinct from current methyltransferase inhibitors based on SAM analogues and truly allow a selective targeting of this important target.

It is true that it makes sense to screen for more diverse compounds to expand to a more diverse ligand set and we do hope our study motivates to do so. Given the limited number of crystal structures of nsp10-16 with potential drug molecules, the aim of this study was to upgrade the data base with new complex structures to have a pool of complex structures for future compound designs with increased selectivity. Furthermore, some of the hits are known inhibitors of similar enzymes and most prominent and potent methyltransferase inhibitors are structurally related to SAM, like sinefungin and tubercidine. We do think that knowing which SAM compounds or fragments of SAM are able to bind in the nsp10-16 active site is highly valuable for further specific and optimized inhibitor design.

Another limitation is the potentially misleading nature of the antiviral assays. It is not possible to say if these compounds display on-target activity in these assays or even if the inhibition of NSP16/10 would have any effect in these assays. Whilst the authors do mention these points I think this should be emphasized more strongly.

That is a very valid point and we do not believe that the antiviral activity is based on on-target effects. We do agree that the way it is currently presented can be considered misleading and we indeed clarify this point in the revised version.

Minor critical points:

The authors state that their crystals and protein preps have co-purified SAM occupying the active site of the crystals. Presumably, this complicates the interpretation of electron density maps as many of the ligands share overlap with the existing SAM density making traditional analysis of difference maps challenging. The authors did not utilize the PanDDA analysis for this step, perhaps this is related to the presence of SAM in the ground state datasets? Also, occupancies are reported in the manuscript in some cases to two significant figures, this seems to be an overestimation of the ability of refinement to determine occupancy based on density alone and the authors should clarify how these figures were reached.

We have used PanDDA in parallel for hit finding. We however did not see any advantages for this target over the hit finding results from the visual inspection. This is probably as mentioned because of SAM being present is the “ground state” which complicates the PanDDA map calculations.

Regarding the occupancies, we fully agree with this comment and change it to reasonable digits and clarify how the figures were reached.  

The molecular docking approach to pre-selection of library compounds to soak did not appear to be successful. Could the authors make any observations about the compounds selected by docking or the docking approach used that may explain this?

Yes, it is a good point to give possible explanations why the docking approach was not successful to facilitate similar approaches in future studies.

Reviewer #2 (Public Review):

Summary:

The study by Kremling et al. describes a study of the nsp16-nsp10 methyl transferase from SARS CoV-2 protein which is aimed at identifying inhibitors by x-ray crystallography-based compound screening.<br /> A set of 234 compounds were screened resulting in a set of adenosine-containing compounds or analogues thereof that bind in the SAM site of nsp16-nsp10. The compound selection was mainly based on similarity to SAM and docking of commercially available libraries. The resulting structures are of good quality and clearly show the binding mode of the compounds. It is not surprising to find that these compounds bind in the SAM pocket since they are structurally very similar to portions of SAM. Nevertheless, the result is novel and may be inspirational for the future design of inhibitors. Following up on the crystallographic screen the identified compounds were tested for antiviral activity and binding to np16-nsp10. In addition, an analysis of similar binding sites was presented.

Strengths:

The crystallography is solid and the structures are of good quality. The compound binding constitutes a novel finding.

Weaknesses:

The major weakness is the mismatch between antiviral activity and binding to the target protein. Only one of the compounds could be demonstrated to bind to the nsp16-nsp10 protein. By performing a displacement experiment using ITC Sangivamycin is concluded to bind with a Kd > 1mM. However, the same compound displays antiviral activity with an EC50 of 0.01 microM. Even though the authors do not make specific claims that the antiviral effect is due to inhibition of nsp16-nsp10, it is implicit. If the data is included, it should state specifically that the effect is not likely due to nsp16-nsp10 inhibition.

We do believe that the antiviral data are valuable and should be published within this work. We also agree with the comment that it should be clearly stated that the antiviral effect is not likely because of nsp10-16 inhibition and we will optimize that accordingly.

The structure of the paper and the language needs quite a lot of work to bring it to the expected quality.

We will go through the manuscript again and further improve the structure and language as much as possible

Technical point:

Refinement of crystallographic occupancies to single digit percentage is not normally supported by electron density.

We agree with that point and correct it in the revised version.

Author response:

Reviewer #1 (Public Review):  

Weaknesses:  

The weakness of this study lies in the fact that many of the genomic datasets originated from novel methods that were not validated with orthogonal approaches, such as DNA-FISH. Therefore, the detailed correlations described in this work are based on methodologies whose efficacy is not clearly established. Specifically, the authors utilized two modified protocols of TSA-seq for the detection of NADs (MKI67IP TSA-seq) and LADs (LMNB1-TSA-seq). Although these methods have been described in a bioRxiv manuscript by Kumar et al., they have not yet been published. Moreover, and surprisingly, Kumar et al., work is not cited in the current manuscript, despite its use of all TSA-seq data for NADs and LADs across the four cell lines. Moreover, Kumar et al. did not provide any DNA-FISH validation for their methods. Therefore, the interesting correlations described in this work are not based on robust technologies.    

An attempt to validate the data was made for SON-TSA-seq of human foreskin fibroblasts (HFF) using multiplexed FISH data from IMR90 fibroblasts (from the lung) by the Zhuang lab (Su et al., 2020). However, the comparability of these datasets is questionable. It might have been more reasonable for the authors to conduct their analyses in IMR90 cells, thereby allowing them to utilize MERFISH data for validating the TSA-seq method and also for mapping NADs and LADs. 

We disagree with the statement that the TSA-seq approach and data has not been validated by orthogonal approaches and with the conclusion that the TSA-seq approach is not robust as summarized here and detailed below in “Specific Comments”.  TSA-seq is robust because it is based only on the original immunostaining specificity provided by the primary and secondary antibodies plus the diffusion properties of the tyramide-free radical. TSA-seq has been extensively validated by microscopy and by the orthogonal genomic measurements provided by LMNB1 DamID and NAD-seq.  This includes: a) the initial validation by FISH of both nuclear speckle (to an accuracy of ~50 nm) and nuclear lamina TSA-seq  and the cross-validation of nuclear lamina TSA-seq with lamin B1 DamID in a first publication (Chen et al, JCB 2018, doi: 10.1083/jcb.201807108); b) the further validation of SON TSA-seq by FISH in a second publication ((Zhang et al, Genome Research 2021, doi:10.1101/gr.266239.120); c) the cross-validation of nucleolar TSA-seq using NAD-seq and the validation by light microscopy of the predictions of differences in the relative distributions of centromeres, nuclear speckles, and nucleoli made from nuclear speckle, nucleolar, and pericentric heterochromatin TSA-seq in the Kumar et al, bioRxiv preprint (which is in a last revision stage involving additional formatting for the journal requirements) doi:https://doi.org/10.1101/2023.10.29.564613; d) the extensive validation of nuclear speckle, LMNB1, and nucleolar TSA-seq generated in HFF human fibroblasts using published light microscopy distance measurements of hundreds of probes generated by multiplexed immuno-FISH MERFISH data (Su et al, Cell 2020, https://doi.org/10.1016/j.cell.2020.07.032), as we described for nucleolar TSA-seq in the Kumar et al, bioRxiv preprint and to some extent for LMNB1 and SON TSA-seq in the current manuscript version (see Specific Comments with attached Author response image 2).

Reviewer 1 raised concerns regarding this FISH validation given that the HFF TSA-seq and DamID data was compared to IMR90 MERFISH measurements.  The Su et al, Cell 2020 MERFISH paper came out well after the 4D Nucleome Consortium settled on HFF as one of the two main “Tier 1” cell lines.  We reasoned that the nuclear genome organization in a second fibroblast cell line would be sufficiently similar to justify using IMR90 FISH data as a proxy for our analysis of our HFF data. Indeed, there is a high correlation between the HFF TSA-seq and distances measured by MERFISH to nuclear lamina, nucleoli, and nuclear speckles (Author response image 1).  Comparing HFF SON-TSA-seq data with published IMR90 SON TSA-seq data (Alexander et al, Mol Cell 2021, doi.org/10.1016/j.molcel.2021.03.006), the HFF SON TSA-seq versus MERFISH scatterplot is very similar to the IMR90 SON TSA-seq versus MERFISH scatterplot.  We acknowledge the validation provided by the IMR90 MERFISH is limited by the degree to which genome organization relative to nuclear locales is similar in IMR90 and HFF fibroblasts. However, the correlation between measured microscopic distances from nuclear lamina, nucleoli, and nuclear speckles and TSA-seq scores is already quite high. We anticipate the conclusions drawn from such comparisons are solid and will only become that much stronger with future comparisons within the same cell line.

Author response image 1.

Scatterplots showing the correlation between TSA-seq and MERFISH microscopic distances. Top: IMR90 SON TSA-seq (from Alexander et al, Mol Cell 2021) (left) and HFF SON TSA-seq (right) (x-axis) versus distance to nuclear speckles (y-axis). Bottom: HFF Lamin B1 TSA-seq (x-axis) versus distance to nuclear lamina (y-axis) (left) and HFF MKI67IP (nucleolar) TSA-seq (x-axis) versus distance to nucleolus (y-axis) (right).

In our revision, we will add justification of the use of IMR90 fibroblasts as a proxy for HFF fibroblasts through comparison of available data sets. 

Reviewer #2 (Public Review):  

Weaknesses:  

The experiments are largely descriptive, and it is difficult to draw many cause-and-effect relationships. Similarly, the paper would be very much strengthened if the authors provided additional summary statements and interpretation of their results (especially for those not as familiar with 3D genome organization). The study would benefit from a clear and specific hypothesis.

We acknowledge that this study was hypothesis-generating rather than hypothesis-testing in its goal. This research was funded through the NIH 4D-Nucleome Consortium, which had as its initial goal the development, benchmarking, and validation of new genomic technologies.  Our Center focused on the mapping of the genome relative to different nuclear locales and the correlation of this intranuclear positioning of the genome with functions- specifically gene expression and DNA replication timing. By its very nature, this project has taken a discovery-driven versus hypothesis-driven scientific approach.  Our question fundamentally was whether we could gain new insights into nuclear genome organization through the integration of genomic and microscopic measurements of chromosome positioning relative to multiple different nuclear compartments/bodies and their correlation with functional assays such as RNA-seq and Repli-seq.

Indeed, as described in this manuscript, this study resulted in multiple new insights into nuclear genome organization as summarized in our last main figure.  We believe our work and conclusions will be of general interest to scientists working in the fields of 3D genome organization and nuclear cell biology.  We anticipate that each of these new insights will prompt future hypothesis-driven science focused on specific questions and the testing of cause-and-effect relationships. 

Given the extensive scope of this manuscript, we were limited in the extent that we could describe and summarize the background, data, analysis, and significance for every new insight. In our editing to reach the eLife recommended word count, we removed some of the explanations and summaries that we had originally included. 

As suggested by Reviewer 2, in our revision we will add back additional summary and interpretation statements to help readers unfamiliar with 3D genome organization.

Specific Comments in response to Reviewer 1:

(1)  We disagree with the comment that TSA-seq has not been cross-validated by other orthogonal genomic methods.  In the first TSA-seq paper (Chen et al, JCB 2018, doi: 10.1083/jcb.201807108), we showed a good correlation between the identification of iLADs and LADs by nuclear lamin and nuclear speckle TSA-seq and the orthogonal genomic method of lamin B1 DamID, which is reproduced using our new TSA-seq 2.0 protocol in this manuscript.  Similarly, in the Kumar et al, bioRxiv preprint (doi:https://doi.org/10.1101/2023.10.29.564613), we showed a general agreement between the identification of NADs by nucleolar TSA-seq and the orthogonal genomic method of NAD-seq.  (We expect this preprint to be in press soon; it is now undergoing a last revision involving only reformatting for journal requirements.) Additionally, we also showed a high correlation between Hi-C compartments and subcompartments and TSA-seq in the Chen et al, JCB 2018 paper. Specifically, there is an excellent correlation between the A1 Hi-C subcompartment and Speckle Associated Domains as detected by nuclear speckle TSA-seq.  Additionally, the A2 Hi-C subcompartment correlated well with iLAD regions with intermediate nuclear speckle TSA-seq scores, and the B2 and B3 Hi-C subcompartments with LADs detected by both LMNB TSA-seq and LMNB1 DamID.  More generally, Hi-C A and B compartment identity correlated well with predictions of iLADs versus LADs from nuclear speckle and nuclear lamina TSA-seq.

(2)  In the Chen et al, JCB 2018 paper we also qualitatively and quantitatively validated TSA-seq using FISH.  Qualitatively, we showed that both nuclear speckle and nuclear lamin TSA-seq correlated well with distances to nuclear speckles versus the nuclear lamina, respectively, measured by immuno-FISH.

Quantitatively, we showed that SON TSA-seq could be used to estimate the microscopic mean distance to nuclear speckles with mean and median residuals of ~50 nm.  First, we used light microscopy to show that the spreading of tyramide-biotin signal from a point-source of TSA staining fits well with the exponential decay predicted theoretically by reaction-diffusion equations assuming a steady rate of tyramide-biotin free radical generation by the HRP enzyme and a constant probability throughout the nucleus of free-radical quenching (through reaction with protein tyrosine residues and nucleic acids).  Second, we used the exponential decay constant measured by light microscopy together with FISH measurements of mean speckle distance for several genomic regions to fit an exponential function and to predict distance to nuclear speckles genome-wide directly from SON TSA-seq sequencing reads.  Third, we used this approach to test the predictions against a new set of FISH measurements, demonstrating an accuracy of these predictions of ~50 nm.

(3)  The importance of the quantitative validation by immuno-FISH of using TSA-seq to estimate mean distance to nuclear speckles is that it demonstrates the robustness of the TSA-seq approach.  Specifically, it shows how the TSA-seq signal is predicted to depend only on the specificity of the primary and secondary antibody staining and the diffusion properties of the tyramide-biotin free radicals produced by the HRP peroxidase.  This is fundamentally different from the significant dependence on antibodies and choice of marker proteins for molecular proximity assays such as DamID, ChIP-seq, and Cut and Run/Tag which depend on molecular proximity for labeling and/or pulldown of DNA.

This robustness leads to specific predictions.  First, it predicts similar TSA-seq signals will be produced using antibodies against different marker proteins against the same nuclear compartment.  This is because the exponential decay constant (distance at which the signal drops by one half) for the spreading of the TSA is in the range of several hundred nm, as measured by light microscopy for several TSA staining conditions.  Indeed, we showed in the Chen et al, JCB 2018 paper that antibodies against two different nuclear speckle proteins produced very similar TSA-seq signals while antibodies against LMNB versus LMNA also produced very similar TSA-seq signals.  Similarly, we showed in the Kumar et al preprint that antibodies against four different nucleolar proteins showed similar TSA-seq signals, with the highest correlation coefficients for the TSA-seq signals produced by the antibodies against two GC nucleolar marker proteins and the TSA-seq signals produced by the antibodies against two FC/DFC nucleolar marker proteins.

Author response image 2.

Comparison of TSA-seq data from different cell lines versus IMR90 MERFISH.  The observed correlation between SON (nuclear speckle) TSA-seq versus MERFISH is nearly as high for TSA-seq data from HFF as it is for TSA-seq data from the IMR90 cell line (Alexander et al, Mol Cell 2021) in which the MERFISH was performed. The correlations for SON, LMNB1 (nuclear lamina) and MKI67IP (nucleolus) versus MERFISH are highest for HFF TSA-seq data as compared to TSA-seq data from other cell lines (H1, K562, HCT116).  Comparison of measured distances to nuclear locale (y-axis) versus TSA-seq scores (x-axis) from different cell lines labeled in red. Left to right: SON, LMNB1, and MKI67IP.  Top to bottom: SON TSA-seq versus MERFISH for two TSA-seq replicates; TSA-seq from HFF, H1, K562, and HCT116 versus MERFISH.

Second, it predicts that the quantitative relationship between TSA-seq signal and mean distance from a nuclear compartment will depend on the convolution of the predicted exponential decay of spreading of the TSA signal produced by a point source with the more complicated staining distribution of nuclear compartments such as the nuclear lamina or nucleoli.  We successfully used this concept to explain the differences emerging between LMNB1 DamID and TSA-seq signals for flat nuclei and to recognize the polarized distribution of different LADs over the nuclear periphery.

(4)  After our genomic data production and during our data analysis, a valuable resource from the Zhuang lab was published, using MERFISH to visualize hundreds of genomic loci in IMR90 cells. We acknowledge that the much more extensive validation of TSA-seq by the multiplexed immuno-FISH MERFISH data is dependent on the degree to which the nuclear genome organization is similar between IMR90 and HFF fibroblasts.  However, the correlation between distances to nuclear speckles, nucleoli, and the nuclear lamina measured in IMR90 fibroblasts and the nuclear speckle, nucleolar, and nuclear lamina TSA-seq measured in HFF fibroblasts is already striking (See Author response image 1, below).  With regard to SON TSA-seq, the MERFISH versus HFF TSA-seq correlation is close to what we observe using published IMR90 SON TSA-seq data (correlation coefficients of 0.89 (IMR90 TSA-seq) versus 0.86 (HFF TSA-seq).  Moreover, this correlation is highest using TSA-seq data from HFF cells as compared to the three other cell lines. (see Author response image 1).  We believe these correlations can be considered a lower bound on the actual correlations between the FISH distances and TSA-seq that we would have observed if we had performed both assays on the same cell line. 

(5)  Currently, we still require tens of millions of cells to perform each TSA-seq assay.  This requires significant expansion of cells and a resulting increase in passage numbers of the IMR90 cells before we can perform the TSA-seq. During this expansion we observe a noticeable slowing of the IMR90 cell growth as expected for secondary cell lines as we approach the Hayflick limit.  We still do not know to what degree nuclear organization relative to nuclear locales may change as a function of cell cycle composition (ie percentage of cycling versus quiescent cells) and cell age.  Thus, even if we performed TSA-seq on IMR90 cells we would be comparing MERFISH from lower passages with a higher percentage of actively proliferating cells with TSA-seq from higher passages with a higher percentage of quiescent cells. 

We are currently working on a new TSA-seq protocol that will work with thousands of cells.  We believe it is better investment of time and resources to wait until this new protocol is optimized before we repeat TSA-seq in IMR90 cells for a better comparison with multiplexed FISH data. 

Specific Comments in response to Reviewer 2:

(1)  As we acknowledge in our Response summary, we were limited in the degree to which we could actually follow-up our findings with experiments designed to test specific hypotheses generated by our data.  However, we do want to point out that our comparison of wild-type K562 cells with the LMNA/LBR double knockout was designed to test the long-standing model that nuclear lamina association of genomic loci contributes to gene silencing.  This experiment was motivated by our surprising result that gene expression differences between cell lines correlated strongly with differences in positioning relative to nuclear speckles rather than the nuclear lamina.  Despite documenting in these double knockout cells a decreased nuclear lamina association of most LADs, and an increased nuclear lamina association of the “p-w-v” fiLADs identified in this manuscript, we saw no significant change in gene expression in any of these regions as compared to wild-type K562 cells.  Meanwhile, distances to nuclear speckles as measured by TSA-seq remained nearly constant.

We would argue that this represents a specific example in which new insights generated by our genomics comparison of cell lines led to a clear and specific hypothesis and the experimental testing of this hypothesis.

In response to Reviewer 2, we are modifying the text to make this clearer and to explicitly describe how we were testing the hypothesis that distance to nuclear lamina is correlated with but not causally linked to gene expression and how to test this hypothesis we used a DKO of LMNA and LBR to change distances relative to the nuclear lamina and to test the effect on gene expression.

Author response:

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

eLife assessment

This study defines a fundamental aspect of protein kinase signalling in the protist parasite Toxoplasma gondii that is required for acute and chronic infections. The authors provide compelling evidence for the role of SPARK/SPARKEL kinases in regulating cAMP/cGMP signalling, although evidence linking the loss of these kinases to changes in the phosphoproteome is incomplete. Overall, this study will be of great interest to those who study Toxoplasma and related apicomplexan parasites.

We thank the reviewers for their thoughtful and positive evaluation of our work. Below, we have addressed all of the public reviews and recommendations for the authors in point-by-point responses. Additionally, we include with this resubmission RT-qPCR data where we observe no significant change in transcript levels for the relevant AGC kinases, supporting the hypothesis that SPARK/SPARKEL–regulation is post-translational.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Herneisen et al characterise the Toxoplasma PDK1 orthologue SPARK and an associated protein SPARKEL in controlling important fate decisions in Toxoplasma. Over recent years this group and others have characterised the role of cAMP and cGMP signalling in negatively and positively regulating egress, motility, and invasion, respectively. This manuscript furthers this work by showing that SPARK and SPARKEL likely act upstream, or at least control the levels of the cAMP and cGMP-dependent kinases PKA and PKG, respectively, thus controlling the transition of intracellular replicating parasites into extracellular motile forms (and back again).

The authors use quantitative (phospho)proteomic techniques to elegantly demonstrate the upstream role of SPARK in controlling cAMP and cGMP pathways. They use sophisticated analysis techniques (at least for parasitology) to show the functional association between cGMP and cAMP signalling pathways. They therefore begin to unify our understanding of the complicated signalling pathways used by Toxoplasma to control key regulatory processes that control the activation and suppression of motility. The authors then use molecular and cellular assays on a range of generated transgenic lines to back up their observations made by quantitative proteomics that are clear in their design and approach.

The authors then extend their work by showing that SPARK/SPARKEL also control PKAc3 function. PKAc3 has previously been shown to negatively regulate differentiation into bradyzoite forms and this work backs up and extends this finding to show that SPARK also controls this. The authors conclude that SPARK could act as a central node of regulation of the asexual stage, keeping parasites in their lytic cell growth and preventing differentiation. Whether this is true is beyond the scope of this paper and will have to be determined at a later date.

Strengths:

This is an exceptional body of work. It is elegantly performed, with state-of-the-art proteomic methodologies carefully being applied to Toxoplasma. Observations from the proteomic datasets are masterfully backed up with validation using quantitative molecular and cellular biology assays.

The paper is carefully and concisely written and is not overreaching in its conclusions. This work and its analysis set a new benchmark for the use of proteomics and molecular genetics in apicomplexan parasites.

Weaknesses:

This reviewer did not identify any weaknesses.

Reviewer #2 (Public Review):

Summary:

The manuscript by Herneisen et al. examines the Toxoplasma SPARK kinase orthologous to mammalian PDK1 kinase. The extracellular signals trigger cascades of the second messengers and play a central role in the apicomplexan parasites' survival. In Toxoplasma, these cascades regulate active replication of the tachyzoites, which manifests as acute toxoplasmosis, or the development into drug-resilient bradyzoites characteristic of the chronic stage of the disease. This study focuses on the poorly understood signaling mechanisms acting upstream of such second messenger kinases as PKA and PKG. The authors showed that similar to PDK1, Toxoplasma SPARK appears to regulate several AGC kinases.

Strengths:

The study demonstrated a strong association of the SPARK kinase with an elongin-like SPARKEL factor and an uncharacterized AGC kinase. Using a set of standard assays, the authors determined the SPARK/SPARKEL role in parasite egress and invasion. Finally, the study presented evidence of the SPARK/SPARKEL involvement in the bradyzoite differentiation.

Weaknesses:

Although the study can potentially uncover essential sensing mechanisms operating in Toxoplasma, the evidence of the SPARK/SPARKEL mechanisms is weak. Specifically, due to incomplete data analysis, the SPARK/SPARKEL-dependent phosphoregulation of AGC kinases cannot be evaluated. The manuscript requires better organization and lacks guidance on the described experiments. Although the study is built on advanced genetics, at times, it is unnecessarily complicated, raising doubts rather than benefiting the study.

The evidence for the SPARK/SPARKEL interaction is demonstrated through diverse experimental approaches that are internally consistent. Five separate mass spectrometry experiments, with replicates and appropriate controls, with tags on either SPARK or SPARKEL, showed that SPARK and SPARKEL form a strong interaction (Figure 1A, 1D, 1E; Figure 1—figure supplement 1). Global mass spectrometry experiments assessing the impact of  SPARK or SPARKEL depletion showed similar features (a reduction in PKG and PKA abundance and up-regulation of bradyzoite-associated proteins; Figure 3C–D). The phenotypes associated with SPARK and SPARKEL depletion phenocopy one another in all cell biological assays we tested (Figure 2A, 2D and PMID: 35484233; Figure 2E–J; Figure 4E–F; Figure 6A–B). Measuring the abundance of SPARK and SPARKEL in unenriched samples was challenging, but immunoblotting and proteomics suggest that depletion of one factor leads to down-regulation of the other (Figure 2B, 2C; Figure 3—figure supplement 1), which explains the genetic and cell biological phenocopying described above. We note that “further biochemical studies are required to discern the regulatory interactions between SPARK and SPARKEL” (first submission lines 590-591) and are beyond the scope of this work.

The evidence for SPARK/SPARKEL regulation of AGC kinase activity is demonstrated through diverse experimental approaches that are also internally consistent. PKA C1 and PKG abundance levels decrease in parasites depleted of SPARK/SPARKEL, as measured by mass spectrometry (Figure 3A and 3C) and cell-based assays for PKA C1/R (Figure 4D–F). Comparisons of the global SPARK-, PKA R-, PKG-, and PKA C3-depleted phosphoproteomes suggest that PKA and PKG activity is reduced upon SPARK depletion whereas the activity of an unrelated factor (PP1) is unaffected (Figure 4G–H, Figure 4—figure supplement 1, Figure 5D–E, Figure 7I–J). Parasites depleted of SPARK are hypersensitized to a PKG inhibitor (Figure 5B–C). SPARK, PKA, and PKG are proximal in cellulo (Figure 3I) and SPARK co-purifies with PKA C3 (Figure 7A). The kinetic-phase phenotypes associated with SPARK and SPARKEL depletion (PMID: 32379047, Figure 2A, 2D–2J) are consistent with reduced PKG activity (PMID: 28465425) and only develop after PKG has been depleted as shown by proteomics experiments (Figure 2E-J and Figure 3C). Other studies have shown that the effects of reduced PKG activity are dominant to reduced PKA C1 activity (PMID: 29030485). The replicative-phase phenotypes associated with SPARK and SPARKEL depletion are consistent with reduced PKA C3 activity (PMID: 27247232 and herein). Mechanistically, PKG and PKA C1 activity must be lower in SPARK-depleted parasites because the abundances of these kinases are lower (Figure 3A, 3C). The mechanism of regulation may be more complex in the case of PKA C3, as SPARK depletion did not cause a reduction in PKA C3 abundance as measured by cellular assays (Figure 7B–F), but PKA C3 activity decreased (Figure 7I–K). We concede that multiple mechanisms may lead to the reduction in PKA C1 and PKG abundances, such as decreased activation loop phosphorylation and autophosphorylation at other stabilizing sites or enhanced ubiquitin ligase activity leading to active degradation of the kinases; we have moved speculation regarding such mechanisms to the Discussion.

Although the reviewer commented that the manuscript “requires better organization” in the public review, no specific recommendations were provided to the authors. Therefore, we did not change the organization of the manuscript. We added an additional paragraph to the Discussion to reiterate key findings: “A prior study identified SPARK as a regulator of parasite invasion and egress following 24 hours of kinase depletion (Smith et al., 2022). Unexpectedly, we observed that three hours of SPARK or SPARKEL depletion were insufficient to impact T. gondii motility or calcium-dependent signaling, indicating that the phenotypes associated with SPARK and SPARKEL depletion develop over time. Quantitative proteomics revealed that PKA and PKG abundances began to decrease after more than three hours of SPARK depletion. Proximity labeling experiments also suggested that SPARK, PKA, and PKG are spatially associated within the parasite cell. We propose a model in which SPARK down-regulation coincides with reduced PKG and PKA activity due to diminished protein levels.” This work built upon genetic and proteomic approaches recently described by our group, which we cited in the text and extensive methods section. We added additional experimental detail where noted in the reviewer’s recommendations to the authors.

The study utilizes advanced genetics because biochemical tools for eukaryotic parasites are limited. For example, no antibodies for T. gondii SPARK, PKA subunits, or PKG exist; to say nothing of phosphosite-specific antibodies, which are common in the mammalian cell signaling field. Therefore, to measure the relationship between SPARK, SPARKEL, and PKA subunits, we had to generate strains in which multiple proteins were tagged with epitopes for downstream analysis. The genetic experiments included appropriate controls and were internally consistent with results obtained using orthogonal approaches, such as mass spectrometry.

Reviewer #3 (Public Review):

Summary:

This paper focuses on the roles of a toxoplasma protein (SPARKEL) with homology to an elongin C and the kinase SPARK that it interacts with. They demonstrate that the two proteins regulate the abundance of PKA and PKG, and that depletion of SPARKEL reduces invasion and egress (previously shown with SPARK), and that their loss also triggers spontaneous bradyzoite differentiation. The data are overall very convincing and will be of high interest to those who study Toxoplasma and related apicomplexan parasites.

Strengths:

The study is very well executed with appropriate controls. The manuscript is also very well and clearly written. Overall, the work clearly demonstrates that SPARK/SPARKEL regulate invasion and egress and that their loss triggers differentiation.

Weaknesses:

(1) The authors fail to discriminate between SPARK/SPARKEL acting as negative regulators of differentiation as a result of an active role in regulating stage-specific transcription/translation or as a consequence of a stress response activated when either is depleted

We demonstrate a novel function for SPARK and SPARKEL as negative regulators of differentiation. The pathways leading to differentiation are being actively studied. Up-regulation of a positive transcriptional regulator of chronic differentiation, BFD1, is sufficient to trigger differentiation in vitro in the absence of other stressful growth conditions (PMID: 31955846). SPARK or SPARKEL depletion results in up-regulation of proteins that are up-regulated upon BFD1 overexpression. Whether BFD1 overexpression or SPARK and SPARKEL depletion triggers cellular stress pathways is beyond the scope of the current work, which focused instead on the immediate effect of these pathways on AGC kinases. Study of the effect of the various kinases on the parasite phosphoproteome shows that the putative targets of PKA C3 are specifically downregulated upon SPARK knockdown, indicating PKA C3 activity is indeed decreased in the latter condition.

(2) The function of SPARKEL has not been addressed. In mammalian cells, Elongin C is part of an E3 ubiquitin ligase complex that regulates transcription and other processes. From what I can tell from the proteomic data, homologs of the Elongin B/C complex were not identified. This is an important issue as the authors find that PKG and PKA protein levels are reduced in the knockdown strains

Our experiments suggest that SPARK and SPARKEL form a complex, and down-regulation of one complex member leads to down-regulation of the other. Thus in all tested assays, knockdown of SPARK and SPARKEL phenocopy one another. Further biochemical and structural work will be required to determine the mechanism by which SPARKEL regulates SPARK.

Nearly all studies of the function of elongin C have been conducted in mammalian cells. Proteins with elongin C domains may serve alternative and unexplored functions in unicellular eukaryotes. We searched for the presence of Elongin A/B and known Elongin C complex members in the T. gondii genome and were unable to identify orthologs, explaining why these proteins were not identified in mass spectrometry experiments. Please see our response in Recommendations for the Authors, Reviewer 3 point 2.

Beyond the concerns raised by the review team, we have identified and corrected the following errors or omissions in the first submission of the manuscript:

- Line 176 of the first submission referred to a “peptide sequence match (PSM)”, which we have changed to “peptide-spectrum match”.

- We recolored and relabeled the lines in Figure 5A so that it is easier to match a specific peptide with a specific line; and also corrected a mislabeling.

- Figure 7B SPARK panel was incorrectly centered. The raw files can be viewed in Figure 7—source data 2.

- Figure 7—figure supplement 1D was missing an x-axis label.

- Line 1172 referred to “Supplementary File X”, which we corrected to “Supplementary File 3”.

- We have updated references to preprints that have since been published, including PMID: 38093015, 37933960, 37966241, and 37610220.

Editors comments:

The proteomics data reported in this study underpin the major findings and are very comprehensive. As noted in the reviews, it is strongly recommended that the authors normalize the levels of detected phosphopeptides against the levels of the parent protein in the different mutant lines in order to identify changes in protein phosphorylation that are linked to protein kinase activity rather than protein degradation. A focus on changes that occur at early time points following protein knock-down may also help to identify the main targets of each kinase.

Please see our response to Reviewer 2 Recommendations for the Authors, points 1 and 2.

Reviewer #1 (Recommendations For The Authors):

During my reading, I only found one small mistake. In Figure 7F, the x-axis is missing the word 'PKA'.

We have updated the x-axis to read “SPARK-AID/PKA C3-mNG (h. + IAA)”.

All information, code, and reagents are clearly explained.

Reviewer #2 (Recommendations For The Authors):

How the phosphoproteome was analyzed needs to be clarified. The normalization step, computing the ratio of the phosphopeptide to the protein (peptide) intensity, appears omitted. It is the most critical step of the analysis. The minor shifts between protein and phosphosite intensity seem negligible, as seen in Figure 4 AB. The significant changes can only be deduced by calculating this ratio. In the current state, the presented results are inconclusive. The manuscript contains overreaching and often unsupported statements because the data has not been appropriately filtered. Related to this topic, it is advisable to use well-accepted terminology and complete words when describing proteome and phosphoproteome. The interexchange of a "peptide" and a "phosphopeptide" in the text confuses and misleads.

To clarify the phosphoproteome analysis:

We cite a previous description of the phosphoproteomics sample preparation workflow (lines 1124-1125 of the first submission for example). Our quantitative phosphoproteomics experiments comprise two datasets generated from the same multiplexed samples. The samples were split at the point of phosphopeptide enrichment. Ninety-five percent of the samples were subjected to phosphopeptide enrichment (titanium dioxide followed by nickel affinity chromatography; “enriched samples”). Five percent of the samples were reserved as a reference for the non-enriched proteome (“non-enriched samples”). To clarify this point, we have added the sentences “Approximately 95% of the proteomics sample was used for phosphopeptide enrichment” and “The remaining 5% of the sample was not subjected to the phosphopeptide enrichment protocol” to the Methods sections, after describing the multiplexing steps.

The samples were fractionated separately and run separately on an LC-MS system, which is described in the Methods section, for example lines 1130-1149 of the first submission. Raw files of the phosphopeptide-enriched and unenriched samples were analyzed separately, which is described in the Methods section, for example lines 1151-1158 of the first submission. To clarify this point, we have added the sentence “Raw files of the phosphopeptide-enriched and unenriched samples were analyzed separately” to the Methods sections. Many of the search parameters and descriptions of normalization and protein abundances were described in lines 1085-1093 of the first submission in reference to the 24h SPARK depletion proteome. We added this information to the description of the SPARK depletion time course phosphoproteome data analysis: “The allowed mass tolerance for precursor and fragment ions was 10 ppm and 0.02 Da, respectively. False discovery was assessed using Percolator with a concatenated target/decoy strategy using a strict FDR of 0.01, relaxed FDR of 0.05, and maximum Delta CN of 0.05. Only unique peptide quantification values were used. Co-isolation and signal-to-noise thresholds were set to 50% and 10, respectively. Normalization was performed according to total peptide amount. In the case of the unenriched samples, protein abundances were calculated from summation of non-phosphopeptide abundances.”

We hope that this clarifies how the unenriched sample protein-level abundances were calculated. When we discuss “protein abundance”, we are referencing the unenriched sample summed non-phosphopeptide abundance. Our phosphoproteome analysis was based only on phosphopeptides, as our phosphopeptide enrichment resulted in 99% efficiency, and peptides lacking phosphorylation sites were filtered out before subsequent analyses. We used “peptide” and “phosphopeptide” interchangeably because the only peptide-level analysis performed was based on phosphopeptide abundances. We have changed any mention of “peptide” to “phosphopeptide” in the main text. 

“The normalization step, computing the ratio of the phosphopeptide to the protein (peptide) intensity, appears omitted. It is the most critical step of the analysis.”:

Unlike common differential gene expression analysis pipelines, proteomics analysis pipelines are not settled. Many analyses do not perform peptide-to-parent-protein corrections; some normalize phosphopeptide abundances to parent protein abundances calculated from summing non-phosphopeptides or a combination of phosphopeptide and non-phosphopeptides on an ad hoc basis; some calculate global normalization factors based on regressions of protein and phosphopeptide abundances or other pairwise comparisons. A caveat of protein normalization of phosphopeptides is that it over-corrects cases in which protein abundance and phosphorylation are interdependent, as is the case for auto-phosphorylation and some activation loop phosphorylations (PMID: 37394063). We used the approach that retained the greatest complexity of the data, which is to not normalize abundances across different mass spectrometry experiments and discard information that was not in the overlap. We have updated Supplementary File 3.3 to include protein-level quantification values (from Supplementary File 3.2) if measured.

We clarified that the phosphopeptide abundances and protein-level abundances were derived from different datasets that were each internally normalized (globally centered by total peptide amount). Protein-level abundances were summed from non-phosphopeptide abundances. The calculated log2 changes are based on the globally centered data within each dataset. We analyzed the kinetic profiles of changing phosphopeptide abundances relative to a control using approaches similar to those described for several recent temporally resolved T. gondii phosphoproteomes (e.g. PMID: 37933960, 35976251, 36265000, 29141230) and as described in the Methods. The approach does not first correct for unenriched-sample parent protein abundance—in some applications, unenriched samples are not collected at all; instead, phosphopeptide ratios are median-normalized to non-phosphopeptide ratios (quantified due to inefficient phosphopeptide enrichment) and are individually tested against the null distribution of non-phosphopeptide ratios (e.g. PMID: 36265000, 29141230). We did not use this approach because our phosphopeptide enrichment was 99% efficient (18518 phosphopeptides of 18758 peptides with quantification values). In several cases using our approach, parent protein abundance is not quantified in the unenriched proteome dataset, but phosphopeptides are reliably quantified in the enriched proteome dataset. We note that phosphopeptide abundance changes can be difficult to interpret in such cases, e.g. in the first submission lines 178-186 and 193-194. We have added similar text to the results noting that in the case of PKA and PKG, both unenriched parent protein and enriched phosphopeptide abundances decreased (see below). We have also moved speculation about whether SPARK phosphorylates the activation loop of PKA and PKG, or whether the down-regulation of PKA and PKG arises from indirect effects, to the Discussion.

We have moved comparisons of protein and phosphopeptide abundances from the Results to the Discussion. We added the following sentences to the result section Clustering of phosphopeptide kinetics identifies seven response signatures: “Because non-phosphopeptide and phosphopeptide abundances were quantified in different mass spectrometry experiments, it is challenging to compare the rates of phosphopeptide and parent protein abundance changes, especially when phosphorylation status and protein stability are interconnected. In general, both PKA C1, PKA R, and PKG protein and phosphosite abundances decreased following SPARK depletion (Figure 3—figure supplement 1), as discussed further below. We also observed down-regulation of phosphosite and protein abundances of a MIF4G domain protein.” Figure 3—figure supplement 1E is a new panel that shows PKA C1, PKA R, and PKG phosphopeptide and parent protein abundances along with global changes in phosphopeptide and parent protein abundances in the cases which both were quantified. We changed lines 278-282 in the first submission to “The SPARK depletion time course phosphoproteome showed a reduction in the abundance of PKA C1 T190 and T341, which are located in the activation loop and C-terminal tail, respectively (Figure 4A). Several phosphosites residing in the N terminus of PKA R (e.g. S17, S27, and S94) also decreased following SPARK depletion (Figure 4B).” We changed lines 313-315 in the first submission to “The SPARK depletion time course phosphoproteome showed a reduction in the abundance of several phosphosites residing in the N terminus of PKG as well as T838, which corresponds to the activation loop (Figure 5A). By contrast, S105 did not greatly decrease, and S40 abundance slightly increased.”

The description of experiments should be more detailed. For example, the 3, 8, and 24 h treatments were used reversely; thus, they should be emphasized as time points before natural egress. Consequently, it seems that 3h treatment should be prioritized, given the SPARK/SPARKEL role in egress/invasion. Unexpectedly, the study draws more attention to a 24-hour treatment. If the AID-SPARK/SPARKEL is eliminated within 1h, parasites undoubtedly accumulate numerous secondary defects during a prolonged 23h deprivation. Since the SPARK pathway activates kinase/phosphatase cascades, the 24h data is likely overwhelmed with the consequences of the long-term complex degradation, making it a poor source of the putative SPARK substrates. Likewise, the downregulation of PKA observed in the 8 hours after SPARK depletion may be an indirect effect of the SPARK degradation. The direct effects and immediate substrates should be detectable within 2-3h of auxin treatment of the nearly egressing cultures.

The first submission described how parasites were harvested at 32 hours post-infection with 0, 3, 8, or 24 hours of IAA treatment (lines 157-160, 1097-1110, and Figure 3B). To reiterate this experimental detail, we have added “harvested 32 hours post-infection” to the sentence “...quantitative proteomics with tandem mass tag multiplexing that included samples with 0, 3, 8, and 24 hours of SPARK or SPARKEL depletion” and similarly in the figure legend. The time points are unrelated to natural egress because the experiment was terminated at 32 hours post-infection, which is earlier than the window typically used to study natural egress under these conditions (40-48 hours post-infection). We chose to terminate the experiment before natural egress to better localize phosphopeptide changes related to SPARK depletion. The phosphoproteome undergoes dramatic reorganization during egress due to the activity of myriad kinases and phosphatases (see PMID: 35976251, 37933960, and 36265000), which would have likely complicated the signal.

A pivotal result motivating time-course experiments and analysis was that SPARK/SPARKEL's role in egress and invasion emerges only after an extended depletion period (Figure 2E–J, first submission lines 126-145). The 24h depletion was used in the experimental system that first identified SPARK as a regulator of egress, which motivated our initial experiments, as stated in the first submission lines 126-144 and 149-151. We draw attention to the observation that SPARK and SPARKEL phenotypes develop over time in the first submission, lines 137-145. The role for SPARK/SPARKEL in egress/invasion does not manifest at 3h depletion; it manifests at 24h depletion. To ensure that this point is not overlooked by the reader, we have created a new heading in the Results section (SPARK and SPARKEL depletion phenotypes develop over time) for the paragraph that was previously lines 137-145. The remainder of the manuscript integrates data from proteomic, genetic, and cell-based assays across temporal dimensions to build a working model of how the phenotypes associated with SPARK depletion develop over time.

Underpinning this comment is an assumption that phosphopeptides that decrease the most rapidly following a kinase’s depletion are direct substrates, whereas phosphopeptides that decrease with slower kinetics are not. This is not always the case. Consider a kinase that phosphorylates sites on substrate A and substrate B. The site on substrate A is also the target of a phosphatase, whereas the site on substrate B is recalcitrant to phosphatase activity. If the kinase were inhibited, then the site on substrate A would be actively dephosphorylated. As measured by a phosphoproteomics experiment, the abundance of the substrate A phosphopeptide would drop rapidly due to the inactivity of the kinase and activity of the phosphatase. In the text, we called such sites “constitutively regulated” or dynamic—they are actively dephosphorylated and phosphorylated within a short timeframe. The phosphosite on substrate B is comparatively static; once it is phosphorylated by the kinase, it is unaffected by subsequent inhibition of the kinase. Only newly synthesized substrate B molecules would be affected by kinase inhibition. As measured by a phosphoproteomics experiment, the abundance of the substrate B phosphopeptide would drop more gradually after kinase inhibition, as the unphosphorylated peptide is found only on newly synthesized proteins that were not previously exposed to kinase activity. An example of the scenario described for substrate A would be that of yeast Cdk1 T14/Y15, which is phosphorylated by Wee1 and dephosphorylated by Cdc25 (e.g. PMID: 7880537). An example of the scenario described for substrate B would be that of the human PKA C activation loop T197, which is phosphorylated by PDK1 and is phosphatase-resistant under physiological conditions (e.g. PMID: 22493239, 15533936).

Both substrate A and B may be “direct” and functionally relevant targets of the kinase. Categorizing substrates as “immediate” is comparatively less informative in this context (although it may be relevant when studying fast, synchronized processes with high temporal resolution, such as induced Plasmodium spp. gametocyte activation or stimulation of T. gondii secretion). Furthermore, our earlier experiments had shown that the role for SPARK/SPARKEL in motility manifests after 3h depletion and is complete by 24h depletion. By this logic, we were most interested in the candidates showing differences at these time points. We conducted proximity labeling experiments to identify the overlap of proteins that exhibited SPARK-dependent decreases in the global proteomics and were also proximal to SPARK in space (first submission Figure 3I and lines 260-275), thus revealing a prioritized list of candidates, which included PKG and PKA. When technically feasible, we included a temporal dimension to follow-up experiments, rather than relying on a 24h terminal comparison (e.g. Figure 4E–H, Figure 5D–E, Figure 7D–F, Figure 7I–K; all first submission).

Fig2 (B and C). What antibodies had been used to detect tagged proteins? There is a concern regarding the use of multiple tags attached to the same protein to the point that it doubles the size of the studied protein. The switch of the mobility of the SPARK and SPARKEL on the WB due to a change in MW adds to the confusion. Furthermore, the study did not use all the fused epitopes (e.g., HA). At the same time, the same V5 tag was used to detect two factors in the same parasite. Although the controls are provided, it does not eliminate the possibility that the second band on the WB results from one protein degradation rather than the presence of two individual proteins. Different tags should be used to confirm the co-expression of two proteins. Panel E is missing the X-axis label.

Figure 2B was incorrectly labeled; the labels corresponding to SPARK and SPARKEL were switched. We corrected this error in the revised figures. The antibodies used were mouse monoclonal anti-V5 as described in the key resources table of the first submission. We added “V5” to Figure 2A and 2B. Regarding the effect of the tagging payload attached to the proteins, we have included in all assays a control relative to a parental strain (TIR1) without a tagging payload, and additionally included internal controls within tagged strains to calculate dependency of a phenotype on IAA treatment. The western blots in Figure 2B and 2C are from two different strains and experiments. The strains and experiments are described in the first submission main text (lines 113-124), the figure legend (lines 1847-1850), the key resources table, and the methods (lines 650-664, 872-891). A description of the SPARK-AID/SPARKEL-mNG strain was included in the key resources table but omitted in the methods. We therefore added the following section to the Methods:

“SPARKEL-V5-mNG-Ty/SPARK-V5-mAID-HA/RHΔku80Δhxgprt/TIR1

The HiT vector cutting unit gBlock for SPARKEL (P1) was cloned into the pALH193 HiT empty vector. The vector was linearized with BsaI and co-transfected with the pSS014 Cas9 expression plasmid into SPARK-V5-mAID-HA/RHΔku80Δhxgprt/TIR1 parasites. Clones were selected with 1 µM pyrimethamine and isolated via limiting dilution to generate the SPARKEL-V5-mNG-Ty/SPARK-V5-mAID-HA/RHΔku80Δhxgprt/TIR1 strain. Clones were verified by PCR amplification and sequencing of the junction between the 3′ end of SPARKEL (5’-GGGAGGCCACAACGGCGC-3’) and 5′ end of the protein tag (5’-gggggtcggtcatgttacgt-3’).”

To clarify the expected MW of each species, we have added the following text to the Methods:

“The expected molecular weight of SPARKEL-V5-HaloTag-mAID-Ty is 66 kDa, from the 42.7 kDa tagging payload and 23.3 kDa protein sequence. The expected molecular weight of SPARK-V5-mCherry-HA is 89.7 kDa, from the 31.9 kDa tagging payload and 57.8 kDa protein sequence. The expected molecular weight of SPARK-V5-mAID-HA is 71.3 kDa, from the 13.5 kDa tagging payload and 57.8 kDa protein sequence. The expected molecular weight of SPARKEL-V5-mNG-Ty is 55.2 kDa, from the 31.9 kDa tagging payload and 23.3 kDa protein sequence.”

SPARK and SPARKEL are lowly expressed, which may have been compounded by basal degradation due to the AID tag (see for example Figure 3—figure supplement 1D of the first submission). We attempted several immunoblot conditions and antibodies, and only the V5 antibody proved effective in recognizing these proteins above the limit of detection. For this reason, we included an additional single-tagged control in each immunoblot experiment. Uncropped images of the blots are included in the first submission as Figure 2—figure supplement 1D and E and as Figure 2 source data. We added the following statement to the results section of the text:

“However, SPARK and SPARKEL abundances are low and approach the limit of detection. We could only detect each protein by the V5 epitope. Although our experiments included single-tagged controls, we cannot formally eliminate the possibility that SPARK-AID yields degradation products that run at the expected molecular weight of SPARKEL. More sensitive methods, such as targeted mass spectrometry, may be required to measure the absolute abundance and stoichiometries of SPARK and SPARKEL.”

We added “h +IAA” to the x-axis of panel 2E.

Fig. 3. There is plentiful proteomic data on the factor-depleted parasites. Can it be used to confirm the co-degradation of the SPARK/SPARKEL complex components? This figure mainly includes quality control data that can be moved to Supplement. Did you detect SPARKEL in the TurboID experiment described in panel I? The plot shows only an AGC kinase.

SPARK and SPARKEL are lowly expressed, and we often do not detect SPARK or SPARKEL peptides with quantification values in complex samples (such as global depletion proteomes and phosphoproteomes; IPs and streptavidin pull-downs are comparatively less complex, with IPs being the least complex samples). We discussed this caveat in the first submission lines 178-186. To additionally clarify this point, we have added “We were unable to measure SPARK or SPARKEL abundances in this proteome” earlier in the text.

We consider the figure panels relevant to the discussion in the text.

SPARKEL was not quantified in the SPARK-TurboID experiment (Supplementary File 2). We have added “SPARKEL was not quantified in this experiment” to the text. “Not quantified” is a different outcome from “quantified but not enriched”. The interaction between SPARK and SPARKEL is supported by five other independent interaction experiments in which SPARKEL was quantified (Figure 1A, 1D, 1E; and Figure 1—figure supplement 1). The added insight from the SPARK proximity labeling experiments comes from integration with the global proteomics, which suggests that AGC kinases are in proximity to SPARK and exhibit SPARK-dependent stability and hence activity. The logic of the proximity labeling experiment is described in lines 258-275 of the first submission.

Fig. 6G is missing deltaBDF1 control for unbiased evaluation of the SPARK KD effect.

The logic of this experiment was to evaluate whether excess differentiation caused by SPARK and PKA C3 depletion (Figure 6A and 6B) was dependent on the BFD1 circuit. The ∆bfd1 phenotype is well-established under these experimental conditions: parasites lacking BFD1 do not differentiate under spontaneous or alkaline conditions (e.g. PMID: 31955846, 37081202, 37770433). Parasites lacking BFD1 do not differentiate when SPARK and PKA C3 are depleted, suggesting that differentiation caused by SPARK or PKA C3 depletion occurs through the BFD1 circuit. If differentiation caused by SPARK or PKA C3 depletion did not depend on the BFD1 circuit, we might have observed differentiation in the SPARK- and PKA C3-AID/∆bfd1 mutants.

To clarify this point, we have changed the first sentences of the last paragraph in the results section Depletion of SPARK, SPARKEL, or PKA C3 promotes chronic differentiation: “To assess whether excess differentiation caused by SPARK and PKA C3 depletion is dependent on a previously characterized transcriptional regulator of differentiation, BFD1 (Waldman et al., 2020), we knocked out the BFD1 CDS with a sortable dTomato cassette in the SPARK- and PKA C3-AID strains (Figure 6–figure supplement 1). The resulting SPARK- and PKA C3-AID/∆bfd1 mutants failed to undergo differentiation as measured by cyst wall staining (Figure 6G–H), suggesting that differentiation caused by depletion of these kinases depends on the BFD1 circuit.”

Lines 239-242. The logic behind the categories of "constitutively regulated sites" and "newly synthesized proteins dependent on SPARK activation" is odd. The former (3h treatment) represents the SPARK-specific events (even though it should be shortened to 1-2h), while an 8h treatment is already contaminated with secondary effects. Since Toxoplasma divides asynchronously, the "newly synthesized" proteins will be present at the time. Also, the protein phosphorylation does not always lead to substrate activation; it can be repressive, too.

We describe the logic in response to a comment above (substrate A vs. substrate B). It is correct that T. gondii divides asynchronously, with a cell cycle of approximately 8 hours, and 60% of parasites in G1 at a given time (PMID: 11420103). The proteomics experiments measure peptide and protein abundances at a population level. Newly synthesized proteins will be present at all time points; but the proportion of proteins synthesized after SPARK depletion relative to proteins synthesized before SPARK depletion will increase over time.

We moved lines 238-243 from the first submission to the Discussion.

It is accurate that phosphorylation does not always lead to substrate activation; it can also be repressive or not change substrate behavior. However, in the case of protein kinases, activation loop phosphorylation is highly correlated with activation (e.g. PMID: 15350212, 31521607).

Line 250-252: Because the SPARK degradation did not affect intracellular replication, SPARK is unlikely to affect cell cycle-specific phosphorylation.

To parallel the prior sentences describing different SPARK-dependent down-regulated clusters, we truncated this sentence to “The final cluster of depleted phosphopeptides, Cluster 4, only exhibits down-regulation at 8h of IAA treatment.”

SPARKEL depletion did not significantly affect intracellular replication under the time frames investigated here (approximately 25 hours post-invasion; Figure 2D). A prior study reported that SPARK depletion did not affect intracellular replication measured on a similar timescale (PMID: 35484233).

The opening sentence of the Discussion: Typically, we refer to the newly discovered proteins as the orthologs of the previously discovered counterparts and not the vice versa. Thus, calling Toxoplasma SPARK the ortholog of mammalian PDK1 would be more appropriate.

We changed the opening sentence of the Discussion to “SPARK is an ortholog of PDK1, which is considered a key regulator of AGC kinases”.

Reviewer #3 (Recommendations For The Authors):

(1) Authors should show alignment of SPARKEL with Elongin C. Are key residues conserved?

We have added an alignment of the SKP1/BTB/POZ domains of Homo sapiens elongin C, S. cerevisiae elongin C, and T. gondii SPARKEL as Figure 1—figure supplement 1B. This panel highlights elongin B interface, cullin binding sites, and target protein binding sites based on the human elongin C annotation. As discussed below, these interfaces may not be functionally conserved in T. gondii. Ultimately, future mechanistic and structural studies beyond the scope of the current work will be required to determine how SPARK and SPARKEL physically interact. The Discussion states, “further biochemical studies are required to discern the regulatory interactions between SPARK and SPARKEL” (lines 590-591).

(2) The failure to identify other Elongin B/C complex members should be addressed by direct IP analysis.

Indeed, elongin C has traditionally been characterized as a component of multisubunit complexes comprising Elongin A/B/C or Elongin BC/cullin/SOCS that regulate transcription or function as ubiquitin ligases, respectively (for a review, PMID: 22649776). We see two major issues when attempting to generalize these results to apicomplexan parasites. First, nearly all studies of the function of elongin C have been conducted in a single eukaryotic supergroup (the opisthokonts, including yeast and metazoans). The majority of eukaryotic diversity exists in other supergroups, including the SAR supergroup to which apicomplexans such as T. gondii belong (PMID: 31606140). Proteins with elongin C domains may serve alternative and unexplored functions in non-opisthokont unicellular eukaryotes. Second (in support of the first), we were unable to find orthologs of many of the opisthokont complex members in T. gondii, as systematically described below.

By BLAST, the most similar protein to SPARKEL in S. cerevisiae is ELC1 (YPL046C), with a BLAST E = 0.003. The next most similar protein was SCF ubiquitin ligase subunit SKP1 (YDR328C) with an E value of 0.62. ELC1 is 99 amino acids. The Elongin C (IPR039948) and SKP1/BTB/POZ superfamily domains (IPR011333) span most of this sequence. SPARKEL is 216 amino acids; the Elongin C and  SKP1/BTB/POZ superfamily domains occupy the C-terminal half of the protein. The N-terminal domain of SPARKEL may be important for its function; however, future work is required to address this hypothesis.

Elongin B: Elongin B is not found universally amongst even opisthokonts; fungi and choanoflagellates lack obvious orthologs. The most similar T. gondii protein to human Elongin B (Q15370) by BLAST is TGME49_223125 (E = 0.017), an apicoplast ubiquitin-like protein PUBL (PMID: 28655825, 33053376). TGME49_223125 has a C-terminal ubiquitin-like domain (IPR000626) but no ELOB domain (IPR039049); indeed, no T. gondii protein has an ELOB domain that can be identified by sequence searching. Given the lack of similarity between EloB and TGME49_223125, as well as this protein’s possible red algal endosymbiont origin, we consider it an unlikely ortholog of EloB and topologically unlikely to  interact with the SPARK/SPARKEL complex. We did not detect TGME49_223125 in SPARK or SPARKEL IPs (Supplementary File 1).

Elongin A: T. gondii appears to lack a human elongin A ortholog (Q14241) on the basis of sequence similarity. The most similar T. gondii protein to yeast Elongin A (O59671) by BLAST is TGME49_299230 (E = 0.022). Yeast EloA is 263 amino acids. TGME49_299230 is 1101 amino acids and does not have an EloA domain (IPR010684), suggesting it is not a true EloA ortholog.

Suppressor of cytokine signaling (SOCS): T. gondii appears to lack human SOCS1 or SOCS2 orthologs (O15524 and O14508) on the basis of sequence similarity. We were unable to identify T. gondii proteins with SOCS domains (PF07525, SM00253, SM00969, and SSF158235).

Von Hippel-Lindau tumor suppressor (VHL): T. gondii appears to lack a human VHL ortholog (P40337) on the basis of sequence similarity.  We were unable to identify T. gondii proteins with VHL domains (IPR024048, IPR024053, PF01847, and SSF49468).

Cul-2/5: Cullins appeared early in the eukaryotic radiation (PMID: 21554755), and thus T. gondii possesses several. Since the ELC complex has been best characterized with human cullin-2 (Q13617) and cullin-5 (Q93034), we searched for orthologs of these proteins and identified TGME49_289310, TGME49_289310, and TGME49_316660. TGME49_289310 functionally resembles cullin-1 of the SCF complex (PMID: 31348812). None of these proteins were enriched in the SPARK or SPARKEL IPs (Supplementary Table 1).

Rbx1: We searched for human Rbx1 orthologs (P62877) and identified TGME49_213690, which functionally resembles Rbx1 of the SCF complex (PMID: 31348812); as well as several other RING proteins (TGME49_267520, TGME49_277740, TGME49_261990, and TGME49_232160) that were not found in the SPARK or SPARKEL IPs (Supplementary File 1).

Rbx2: We searched for human Rbx2 orthologs (Q9UBF6) and identified several RING proteins (TGME49_285190, TGME49_254700, TGME49_292340, TGME49_226740, TGME49_244610, and TGME49_304460) that were not found in the SPARK or SPARKEL IPs (Supplementary File 1). No T. gondii protein has an Rbx2 domain (cd16466) that can be identified by sequence searching.

In conclusion, we conducted “direct IP analysis” (Figure 1A, 1D; Figure 1-supplement 1A) of the SPARK and SPARKEL complex in the first submission of the manuscript. The observation that SPARK and SPARKEL form strong interactions was validated in cellulo via proximity labeling (Figure 1E; Figure 1-supplement 1B) in the first submission of the manuscript. These results are described together in the results section SPARK complexes with an elongin-like protein, SPARKEL (lines 75-110, first submission of manuscript). The failure to identify an interaction between SPARKEL and Elongin B/C complex members in T. gondii may be due to the observation that Elongin B and several ELC complex members do not exist in most eukaryotes, including T. gondii. We added the sentences “The function of proteins with Elongin C-like domains has not been widely investigated in unicellular eukaryotes” to the Results and “However, the SPARK and SPARKEL IPs and proximity experiments failed to identify obvious components of ubiquitin ligase complexes” to the Discussion.

(3) PKA and PKG half-lives should be measured as well as their transcript abundances.

The finding that PKA C1 and PKG protein abundances decreased upon SPARK/SPARKEL depletion was internally consistent across experiments. This down-regulation may be due to transcriptional, translational, or post-translational mechanisms. We measured PKG and PKA C1 transcript abundances in SPARK-AID and TIR1 parasites after 24 hours of IAA treatment using RT-qPCR. We did not detect significant differences in transcript levels of the queried kinases. These findings suggest that SPARK depletion leads to PKG and PKA down-regulation through post-transcriptional mechanisms. Translational control is normally enacted globally, for example through regulation of eukaryotic translation factors (PMID: 15459663). The rapid and specific down-regulation of PKG and PKA C1 would suggest that the kinase abundance levels are regulated by non-global translational mechanisms (e.g. mRNA-specific) or rather post-translational mechanisms.

Substantial additional work is required to determine protein half-lives in eukaryotic parasites. In our discussion of possible mechanisms and models, we were agnostic as to the cause of reduced PKG and PKA abundances upon SPARK depletion. We note in the discussion, “The cause for reduction of PKA C1 and PKG levels requires further study” (lines 541-542).

Author response:

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

Reviewer #2:

(1) P-values should be reported adjusted for multiple tests or, at the very least, note that they are unadjusted to alert the reader that they may be biased by winner's curse.

Throughout the manuscript, we applied the false discovery rate threshold to declare results that were statistically relevant for discussion. However, for reporting in abstract, we believe the raw p-values are most straightforward as we only reported the most important and robust results, and considering that 1) multiple testing correction does not change the ranking of the adjusted p-values; 2) p-value adjustment depends on both the method and the number of hypothesis tested; 3) all reporting of the most significant discovery results are prone to winner’s curse, but in the context of our study: the GFI1 finding was confirmatory in nature, thus raw p-value allows for a direct comparison with existing studies.

We have taken the suggestion to quote the FDR-adjusted p-values throughout the manuscript for meta-analyzed results and discussed the impact of FDR correction for the EWAS and MRS association differed as a result of the number of hypothesis in each context:

“For each EWAS or meta-analysis, the false discovery rate (FDR) adjustment was used to control multiple testing and we considered CpGs that passed an FDR-adjusted p-value < 0.05 to be relevant for maternal smoking.”

“An FDR adjustment was used to control the multiple testing of meta-analyzed association between MRS and 25 (or 23, depending on the number of phenotypes available in the cohort) outcomes, and we considered association that passed an FDR-adjusted p-value < 0.05 to be relevant.”

(2) The odds ratios and p-values reported in the abstract for associations of the MRS with smoking status and smoking exposure per week appear to be missing from the results section of the manuscript or (supplementary) tables.

The results for smoking status during pregnancy was added to the results:

“As a result, the epigenetic maternal smoking score was strongly associated with smoking status during pregnancy (OR=1.09 [1.07,1.10], p=5.5×10-33) in the combined European cohorts.”

The exposure association was reported in the result section and Supplementary Table 8. We do note the typo in the cohort specific p-values, which now has been corrected.

(3) It is misleading to report a lack of MRS associations with maternal smoking in South Asians without also stating that there were only two smokers.

We agree with the reviewer that an association test would not be justified given the lack of smoking in the present South Asian cohort. We also removed the p-value of association for the START cohort in Figure 3, based on this and comment #4 from reviewer #3. The relevant results have been revised as follows:

“The HM450 MRS was significantly associated with maternal smoking history in CHILD and FAMILY (n = 397), but we failed to meaningfully validate the association in START (n = 503; Figure 3) – not surprisingly – due to the low number of ever-smokers (n = 2).”

(4) It is potentially confusing to report MRS associations with maternal smoking by ethnicity but then report associations with birth size and length combined without any explanation. The most novel result of this study is that there is virtually no maternal smoking among the South Asians and yet the MRS is associated with birth weight and size and with height at age 2. This result is buried in the combined analysis. I would suggest reporting the MRS associations with height and weight separately as has been done for maternal smoking behavior.

We thank the reviewer for this suggestion and this has now been added the new Table 3, showing the cohort specific and meta-analyzed effect sizes. In the revision, we highlighted that the ethnic specific MRS associations, such as with smoking exposure at various age (1 and 3 years) and skinfold thickness in European cohorts but not the South Asian cohort, as well as associations that were more homogenous, such as the birth weight and unique body size association in combined cohorts. In particular, the MRS in the South Asian cohort exhibited a consistent association with body size at various time points (at birth, 1, 2, and 5 year) with similar effect sizes. The following was added to the results:

“A higher maternal smoking MRS was significantly associated with smaller birth size (-0.37±0.12, p = 0.0023; Table 3) and height at 1, 2, and 5 year visits in the South Asian cohort (Table 3). We observed similar associations with body size in the white European cohorts (heterogeneity p-values> 0.2), collectively, the MRS was associated with a smaller birth size (-0.22±0.07, p=0.0016; FDR adjusted p = 0.019) in the combined European and South Asian cohorts (Table 3). Meanwhile, a higher maternal smoking MRS was also associated with a lower birth weight (-0.043±0.013, p = 0.001; FDR adjusted p = 0.011) in the combined sample, though the effect was weaker in START (-0.03±0.02; p = 0.094) as compared to the white European cohorts.

The meta-analysis revealed no heterogeneity in the direction nor the effect size of associations for body size and weight between populations at birth or at later visits (heterogeneity p-values = 0.16–1; Supplementary Table 8).”

Reviewer #3:

(1) You mention that the 450K Score performs best even though only 10/143 are included for some populations. Did you explore recalibration of the MRS using only those 10 CpGs?

We thank the reviewer for this comment – due to an error in result transferring, the number of overlapping CpGs between the 450K score and the targeted array was in fact 26. This error only impacted results relevant to the FAMILY study using the HM450K score and did not materially change our results nor conclusions. We have updated accordingly, Table 3, Suppl. Tables 5, 8, 9, Figure 3-B, and Suppl. Figures 5, 6-B), 7-B) and 7-D), and throughout the manuscript for meta-analyzed MRS associations.

The subset of 26 CpGs using the originally derived weight was expected to perform worse than the original HM450K score using the full 143 CpGs. When we did restrict the methylation score construction to these 26 CpGs, the performance in CHILD was worse than the original score, but comparable to FAMILY (updated Suppl. Table 5). These 26 CpGs did overlap with the targeted score derived in CHILD (13 out of 15 present) and in FAMILY (19 out of 63 present), suggesting moderate agreement between the array platform as well as across studies.

In other words, while the subset of 26 CpGs had reasonable performance in both CHILD and FAMILY, both studies could benefit by inclusion of the additional CpGs in the original score. We have included a sentence to discuss the choice of validation study and the trade-off between sample size and # of CpGs under response to Reviewer 3 comment # 2.

(2) Could the internal validation performance be driven by sample size of the training, providing support for the need for larger training sizes? Should this be discussed in the study?

The validation study, CHILD, has the smaller sample size between the two European cohorts. While both potential data for validation had smaller sample sizes, we chose CHILD (n=347), rather than FAMILY (n=397) as it had better coverage with respect to the discovery EWAS or the training data (# of associated CpGs = 3,092, n = 5,647). Beyond the signals of association, the validation performance also depends on a mix of overall sample size and the proportion of current smokers. Given the proportion of current smokers, the effective sample size for a direct comparison, i.e. equivalently-powdered sample size of a balanced (50% cases, 50% controls) design, are 41.7 and 104.7 for CHILD and FAMILY, respectively. While we are unable to directly compare whether a larger effective sample size produced a better performing score, we believe this to be the case, and thus a larger validation study would boost the performance of the methylation score. We have added the following to the discussion:

“Given the proportion of current smokers, the effective sample size for a direct comparison between CHILD and FAMILY, i.e. equivalently-powdered sample size of a balanced (50% cases, 50% controls) design, were 41.7 and 104.7, respectively. While CHILD had a lower effective sample size, we ultimately chose it for validating the methylation score to better cover the CpGs that were significant in the discovery EWAS. A larger validation study will likely further boost the performance of the methylation score and be considered in future research.”

(3) Figure 1: It is very helpful to have an overview diagram, but this should then follow the flow of the manuscript to aid the reader. Currently, the diagram does not follow the flow of the manuscript and thus is rather confusing - for instance, the figure starts with the MRS but initially an EWAS is conducted in the manuscript itself. I suggest to adapt the overview figure accordingly. Moreover, a description for (A), (B), (C) is not provided in the figure legends. Figure 1 could thus be improved further.

We thank the reviewer for the suggestion to improve the key figure that summarizes the manuscript. The EWAS workflow for the primary, secondary and tertiary outcomes, as well as the European cohorts meta-analysis has been added to the updated sub-figure A). The description for each subfigures has also been added to the figure legends as follows:

“Figure 1-A) shows the epigenome-wide association studies conducted in the European cohorts (CHILD and FAMILY); Figure 1-B) illustrated the workflow for methylation risk score (MRS) construction using an external EWAS (Joubert et al., 2016) as the discovery sample and CHILD study as the external validation study, while Figure 1-C) demonstrates the evaluation of the MRS in two independent cohorts of white European (i.e. FAMILY) and South Asian (i.e. START). The validated MRS was then tested for association with smoking specific, maternal, and children phenotypes in CHILD, FAMILY, and START, as shown in Figure 1-D).”

(4) Figure 3: The readability and information content in this figure, and other figures containing boxplots (e.g., Supplementary Figure 5), could be improved. I would suggest to justify X axis labels to the axis rather than overlapping, and importantly, show individual data points wherever possible (e.g., overlaying the box plots). In c), the ANOVA is not justified given the sample size in START. In general, it is worth excluding the START cohorts from this analysis on the justification of a too small sample size for maternal smokers.

We thank the reviewer for their thoughtful points for improvement. The axis labels have been wrapped to avoid overlapping, and the data points added to the boxplots. ANOVA p-value for START was removed due to the low counts of smokers in the figure and manuscript throughout. However, we retained START in Figure 3 and other boxplots to show the distribution of the score for non-smokers to benchmark with the European cohorts.

(5) In addition to boxplots, it may be helpful to show AUC diagrams for ROC curves (e.g. Figure 3). AUCs are reported in the Tables but not shown. Additionally, all AUC results should include 95% Confidence intervals.

This is a great suggestion and we have added the corresponding ROC, annotated with AUC (95% CI) to Figure 3. The 95% CI for all AUC results were added to the Tables and main text. The following was added to Methods:

“The reported 95% confidence interval for each estimated AUC was derived using 2,000 bootstrap samples.”

(6) Supplementary Figure 6: It could be helpful to discuss the amount of overlap between the different MRS.

Most of the scores were derived using the Joubert et al., (2016) EWAS as the discovery sample, including ours, and thus there will be overlap between the scores. The exception was the GondaliaScore, which contained only 3 CpGs that do not overlap with any other scores.

While different scores might not have selected completely identical sets of CpGs, the mapped genes are highly consistent across the scores. We have added to the discussion and results the extent of overlap between the top scores:

“In particular, scores that were derived using the Joubert EWAS as the discovery sample, including ours, had higher pairwise correlation coefficients across the birth cohorts, with many of the CpGs mapping to the same genes, such as AHRR, MYO1G, GFI1, CYP1A1, and RUNX3.”

(7) Supplementary Figure 7: This figure is never referenced in the text and from the legend itself it is not too clear what it is trying to show. Please refer to it in the main text with some additional context.

Supplementary Figure 7 was referenced in the Results under subsection “Methylation Risk Score (MRS) Captures Maternal Smoking and Smoking Exposure”, following the<br /> Methods subsection “Statistical analysis” where we wanted to examine a systematic difference. We made revision to the main text to clarify the analysis:

“For the derived MRS, we empirically assessed whether a systematic difference existed in the resulting score with respect to all other derived scores. This was examined via pairwise mean differences between the HM450 and other score using a two-sample t-test and an overall test of mean difference using an ANOVA F-test, among all samples and the subset of never smokers.”

(8)   Tables: Tables are currently challenging to read and perhaps more formatting could be done to improve readability.

We thank the reviewer for the suggestion. Main tables have been reformatted to a landscape layout and each numeric cell moved to the centre to improve readability.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review): 

(1) In Figure 1, the authors show that TF3C binds to the amino terminus of MYCN (Myc box I region), as shown previously. The data in Figure 1 B-D support, but do not rigorously confirm a 'direct' interaction because it has not been ruled out that accessory proteins mediating the association may be present in the mixture.

In Figure 1B-D we have purified MYCN and the TFIIIC/TauA complex separately and then mixed the purified preparations, demonstrating that the purified proteins interact. We have additionally performed mass spectrometry, which shows that the TauA/MYCN complex is formed without further accessory proteins, as the molecular weight would be higher. Based on the Coomassie stained SDS-PAGE gels, there is no plausible contaminating band in the purified complex that could be mediating the interaction between MYCN and TauA, either in the purified complex (Figure 1C), or in the purified protein used to reconstitute the complex (Figure S1A & S1B).

(2) The authors indicate in Figure 2 that TF3C has essentially no effect on MYCNdependent gene expression and/or transcription elongation. Yet a previous study (PMID: 29262328) associated with several of the same authors concluded that TF3C positively affects transcription elongation. The authors make no attempt to reconcile these disparate results and need to clarify this point.

We agree that the data in this manuscript do not support the role on transcription elongation. This point was also raised by Reviewer 3. Comparing our new results to the data published previously we can summarize that the data sets in the two studies show three key results: First, the traveling ratio of RNAPII changes upon induction of MYCN. Second, RNAPII decreases at the transcription start side and third, it increases towards the end side.

We agree that in the previous study we linked the traveling ratio directly to elongation. However performing ChIP-seq with different RNAPII antibodies showed us that for example RNAPII (N20), which is unfortunately discontinued, gives different results compared to RNAPII (A10). Combining our new results using the RNAPII (8WG16) antibody shows that the traveling ratio is not only reflecting transcription elongation but also includes that the RNAPII is kicked-off chromatin at the start side.

(3) Figures 2B and C show that unphosphorylated pol2 is TSS-centered, and Ser2-P pol2 occupation is centered beyond the TES. From this data, however, the reader can't tell how much of the phospho-Ser2- pol2 is centered on the TSS. The authors should include overall plots over TSS and TES, and also perhaps the gene-body to allow a better comparison for TSS and TES plotted for both antibodies over the collected gene sets.

We focused on the TSS for unphosphorylated RNAPII and the TES for pSer2-RNAPII, as these are the regions with specific enrichment of the respective antibodies. As requested for comparison, we now include metagenes showing TSS, gene-body, and TES for both antibodies as new Figure S2A and B. Additionally, we included density plots for unphosphorylated RNAPII at the TES as well as for pSer2-RNAPII at the TSS as a Figure for the Reviewers (Figure 1).

(4) The authors see more TF3C at promoters in cells with MYCN (Figure 2F). What are the levels of TF3C in the absence and presence of MYCN?

As shown in the immunoblot in Figure S1E, TF3C5 levels do not change upon induction of MYCN. We therefore think that MYCN helps to recruit TFIIIC5 to RNAPII promoter sites. This is also in accordance to what we previously reported 1.

(5) The finding that TF3C is increased at TSS (Figure 2F) doesn't necessarily indicate that 1) MYCN is recruiting TF3C there, and 2) that this is due to the phosphorylation status of pol2. It could mean many other things. The logic of conflating these 3 points based on the data shown is questionable.

We showed previously that knock-down of MYCN affects TFIIIC5 binding, showing that MYCN is required for binding of TFIIIC5 at promoter sites 1.

Additionally, we included data with DRB treated cells (Figure 2F), which prevents RNAPII loading by preventing downstream de novo elongation. Those data show that TFIIIC5 binding at the TSS is massively increased upon induction of MYCN and additionally upon treatment with DRB. Conversely, we observed that the major effect of TFIIIC knock-down was at the nonphosphorylated RNAPII at the TSS on MYCN induction (Figure 2B). Therefore, we would argue that our assumption fits well to the data presented in the manuscript.

(6) Figure 3A doesn't add much to the paper, as it is overplotted and no relationship is clear, except that Pol2 and MYCN occupy many of the same sites. Perhaps a less complex or different type of plot would allow the interactions to be better visible.

We agree with the comment and since in another comment we were asked to show the same window for all shown Hi-ChIP data plots, we changed Figure 3A.

(7) That depletion of TF3C leads to increased promoter hubs may or may not have anything to do with its association with MYCN (Figure 4E). This could be a direct consequence of its known structural function in cohesin complexes, and the MYCN changes as a secondary consequence of this (also see point 4, above).

As shown in Büchel et al. (2017) 1 MYCN is needed to recruit RAD21 and depletion of RAD21 has no impact on the recruitment of MYCN. Since RAD21 is part of the cohesin complex we would exclude that the MYCN changes are a secondary consequence.

(8) Depletion of TF3C5 results in a loss of EXOSC5 (exosome) at TSS in the presence and absence of MYCN (Figure 5B). As TF3C5 is a cohesin, could this simply be a consequence of genomic structure changes?

We agree that the discovered changes in EXOSC5 can be due to depletion of TFIIIC5. TFIIIC has been shown to recruit cohesin 1 and condensin complexes 2, as well as inducing chromatin architectural changes 3. However, MYCN is needed to recruit TFIIIC and depletion of TFIIIC had no impact on MYCN recruitment 1. Furthermore, MYCN has been shown to recruit exosome 4. Therefore, we would argue that either MYCN can directly play a role or thru chromatin architectural changes.

(9) The authors suggest that RNA dynamics are affected by changes in exosome function (RNA degradation, etc). What effect, if any does TF3C depletion have on the overall gene expression profile?

We show in the manuscript that TFIIIC depletion in unperturbed cells has no effect on the global gene expression profile in the time frame analyzed (Figure 2E and S2B).

Reviewer #2 (Public Review):

(1) Dynamic inferences are made without kinetic experiments.

While we agree that we did not collect kinetic data to study the dynamics of RNA polymerase we would argue that the integration of our different data sets make it possible to draw conclusions about dynamic interferences. The transcription cycle and its sequential steps have been well described. In this sense, we use the non-phosphorylated RNAPII data that is situated between RNAPII recruitment and initiation and RNAPII-pSer2 that shows pause-release to elongation to draw conclusions on the dynamic. Likewise, we also made use of our previous published datasets.

Reviewer #2 (Recommendations For The Authors):  

(1) A number of changes are reported in hub size, expression, etc. upon treatment with tamoxifen to activate MCN-ER. But MYC is already present in the SHEP cells, so why doesn't MYC support these same phenomena? It would seem that either the ability to cooperate with TFIIIC to clear non-productive polymerase complexes from promoters is particular to MYCN, or else it reflects a quantitative increase in total MYC proteins due to the entry of MYCN-ER into the nucleus with tamoxifen. The authors should address or discuss this issue.

It could be that protein levels are the limiting factor between MYC and MYCN observed effects in this system. This interpretation would be in accordance with the results of Lorenzin et al. 5, which reported that different levels of MYC had different targets based on the affinity to Eboxes and protein level. A similar profile of MYC levels compared to function was also reported regarding SPT5 6. Those high protein levels mimic what is found in certain tumors in contrast to physiological levels. In this sense, the observed differences can also be between physiological and oncological levels of MYC proteins.

On the other hand, it has been described both a core MYC- and an isoform specific-signature of target genes. MYCN is described to be involved in gene expression during the S-phase of the cell cycle 7. This suggests that there are differences between MYC and MYCN other than gene sets. The interaction with TFIIIC appears to be one of these differences. We have found multiple TFIIIC subunits as part of the MYCN interactome, but the interaction of TFIIIC with MYC is weaker and we are uncertain how relevant it is 7,8. We show here that depletion of different subunits of the TFIIIC complex show a MYCN-dependent growth defect (Figure 1 E). Similarly, nuclear exosome is a MYCN-specific dependence 4, and we show here that MYCNdependent recruitment of the exosome requires TFIIIC5. We take this as an indication that there is an intrinsic difference between MYC and MYCN and that MYCN engages TFIIIC for this pathway.

(2) Reciprocal to TFIIIC recruitment to MYCN- rRNA, and other RNAPIII genes. Does this happen targets would be MYCN association with tRNA genes, 5S, and if so, is this association TFIIIC dependent? What happens to the expression of these genes?

We did observe MYCN in interactions involving tRNA and other RNAPIII sites, such as SINE elements and tRNAs (Figure 4B, 4D, S3F, and S4B). There was no relevant number of 5S rRNA involved in interactions – either because the difficulty to properly map these repetitive regions or due to biology. In any case, none of those regions appeared to be specifically dependent on TFIIIC as the overall number of interactions increased in TFIIIC depletion regardless of the genomic annotation (Figure S4B). Regarding the expression of RNAPIII genes, we are constrained by technical limitations of poly(A) enrichment RNA-seq to globally analyze it in an unbiased way. However, we addressed this point for tRNAs expression in an earlier work 1 and found that tRNA levels do not change upon TFIIIC depletion. We think this is because tRNAs are stable transcripts and RNAPIII recycling can occur in a TFIIICindependent manner 9. Conversely, we reported no significant expression changes in RNAPII genes upon TFIIIC depletion in this work.

(3) The authors show that TFIIIC depletion does not alter the RNA-expression profile; how do they account for this? Can they comment on "background" transcription that it would seem should be suppressed by TFIIIC-dependent removal of various hypofunctional polymerases?

Since TFIIIC is important for the removal of non-functional RNAPII we would not expect changes to the gene expression profile upon depletion of TFIIIC in the time frame analyzed. Monitoring the elongating form of RNAPII by measuring pSer2 indeed shows us that transcription elongation is not affected.

(4) Global changes in expression are difficult to assess with DESEQ2. This hypernormalizing algorithm is not really suited to distinguish differential, but universal upregulation from some targets being truly upregulated while others are downregulated. The authors should comment.

The authors acknowledge that DESEQ2 relies on the conjecture that genewise estimates of dispersion are generally unchanged among samples. We address this comment in two different ways. We include those in the Figure for the Reviewers (Figure 2). The first was to sequence samples deeper to avoid any bias created by random effect of lower coverage, the range of total reads increased from 6.8-9.3 to 16.5-20.7 million reads. The second was to compare the fold average bin dot plot for RNA-seq of SH-EP-MYCN-ER showing mRNA expression normalized by control per bin using the DESEQ2 (Figure 2A) normalization to TMM in edgeR (Figure 2B) and to quantile normalization (Figure 2C). No major differences were found from the original data or using the different methods, but we updated the Figure 2E in the manuscript to include the deeper sequencing dataset, we also adjusted it to show -/+ MYCN and transformed to log2 to make it more intuitive. Overall, it enhances our original understanding that gene expression remains largely unaffected by TFIIIC5 knockdown.

(5) On page 7, the authors claim that MYCN-ER increased Ser-2 can reflect MYCN-stimulated transcription elongation. In fact, without kinetic studies, this is not fully supported. Accumulation of Ser-2 RNAPII along a gene can reflect increased initiation of full-speed RNAPs or a pile-up of RNAPs slowing down. This should be resolved or qualified.

While we agree that we did not collect kinetic data to study the dynamics of RNA polymerase we would argue that the integration of our different data sets make it possible to draw conclusions about dynamic interferences. We showed on the one side that pSer-2 accumulates on the TES and on the other side the induction of MYCN-ER up-regulates gene expression which proves productive transcription elongation.

(6) pLHiChIP needs to be better described, the Mumbach reference is not sufficient.

We have reformulated the pLHiChIP in the method section and hope that this will provide now a better description of the method.

(7) Can the authors recheck all the labels in Figure 2D-I believe there is an error involving + or - MYCN.

We carefully rechecked all the labels in Figure 2 and it was correct as it was. We understand the confusion that may have created comparing Figure 2D and Figure 2E. To avoid confusion, we updated Figure 2E to show the same direction of Figure 2D. We also log2 transformed the y-axis of Figure 2E to foster a more intuitive reading.

(8) Why are there different scales for the regions of chromosome 17 shown in Figures 3 and 4? It would be easier to compare if the examples were all shown at the same scale (about 2 MB is shown in another Figure).

We now show the same region of chromosome 17 in Figure 3 and 4.

Reviewer #3 (Public Review):

(1) The connection between the three major findings presented in this study regarding the role of TFIIIC in the regulation of MYCN function remains unclear. Specifically, how the TFIIICdependent restriction of MYCN localization to promoter hubs enhances the association of factors involved in nascent RNA degradation to prevent the accumulation of inactive RNA polymerase II at promoters is not apparent. As they are currently presented, these findings appear as independent observations. Cross-comparison of the different datasets obtained may provide some insight into addressing this question.

We previously observed that TFIIIC does not affect MYCN recruitment, while MYCN affects TFIIIC binding 1. Moreover, our group reported that MYCN recruits exosome 4 and BRCA1 to promoter-proximal regions 10 to clear out non-functional RNAPII. We are currently reporting that MYCN-TFIIIC complexes exclude non-functional RNAPII. However, MYCN-active promoter hubs have more RNAPII and more transcription than MYCN-active promoter outside hubs. Furthermore, TFIIIC binding occurs upstream of BRCA1 and exosome recruitments as depletion of TFIIIC leads to recruitment decrease of both factors. Therefore, we argue that TFIIIC is required for the proper function of those MYCN-active promoter hubs.

(2) Another concern involves the disparities in RNA polymerase II ChIP-seq results between this study and earlier ones conducted by the same group. In Figure 2, the authors demonstrate that activation of MYCN results in a reduction of non-phosphorylated RNA polymerase II across all expressed genes. This discovery contradicts prior findings obtained using the same methodology, where it was concluded that the expression of MYCN had no significant effect on the chromatin association of hypo-phosphorylated RNA polymerase II (Buchel et al, 2017). In this regard, the choice of the 8WG16 antibody raises concern, as fluctuations in the signal may be attributed to changes in the phosphorylation levels of the Cterminal domain. It remains unclear why the authors decided against using antibodies targeting the N-terminal domain of RNA polymerase II, which are unaffected by phosphorylation and consistently demonstrated a significant signal reduction upon MYCN activation in their previous studies (Buchel et al, 2017) (Herold et al, 2019). Similarly, the authors previously proposed that depletion of TFIIIC5 abrogates the MYCN-dependent increase of Ser2phosphorylated RNA polymerase II (Buchel et al, 2017), whereas they now show that it has no obvious impact. These aspects need clarification.

We politely disagree that our discoveries are contradicting each other. Comparing our new results to the data published previously we can summarize that the data sets in the two studies show three key results: First, the traveling ratio of RNAPII changes upon induction of MYCN. Second, RNAPII decreases at the transcription start side and third, it increases towards the end side.

We agree that in the previous study we linked the traveling ratio directly to elongation. However performing ChIP-seq with different RNAPII antibodies showed us that for example RNAPII (N20), which is unfortunately discontinued, gives different results compared to RNAPII (A10). Combining our new results using the RNAPII (8WG16) antibody shows that the traveling ratio is not only reflecting transcription elongation but also includes that the RNAPII is kicked-off chromatin at the start side.

In the previous study we only performed manual ChIP experiments for RNAPII (8WG16) and pSer2. Now we did a global analysis which is more meaningful and is also reflected in the RNA sequencing data.

(3) Finally, the varied techniques employed to explore the role of TFIIIC in MYCNdependent recruitment of nascent RNA degradation factors make it challenging to draw definitive conclusions about which factor is affected and which one is not. While conducting ChIPseq experiments for all factors may be beyond the scope of this manuscript, incorporating proximity ligation assays (PLA) or ChIP-qPCR assays with each factor would have enabled a more direct and comprehensive comparison.

We understand the criticism that we are comparing different assays. We have performed PLAs with different antibodies. Since the controls of the PLAs were not sufficient for us, we refrain from using them. ChIP-qPCR experiments are much more challenging to do side by side compared to PLAs, which is why we decided against looking at all factors with this method.

Recommendations For The Authors:

Reviewer #3 (Recommendations For The Authors):

(1) Figure 2: Why did the authors choose the 8WG16 antibody? Does TFIIIC5 depletion suppress the MYCN-dependent reduction of total RNA polymerase II binding to promoters that they consistently showed in previous studies? Given that phosphorylation of the CTD impacts 8WG16 recognition, including Ser5-phosphorylated RNA polymerase II ChIPseq experiments might clarify this issue.

We used the RNAPII (8WG16) antibody to exactly map non-phosphorylated RNAPII which shows us the binding of non-functional RNAPII.

(2) Figures 3 and 4: As it stands, the manuscript does not convincingly establish a functional connection between the results in Figures 2, 3, and 4 or elucidate potential mechanisms. Are changes in RNA polymerase II levels upon MYCN activation more pronounced at promoters located at MYCN hubs? Do changes in MYCN-enriched chromatin contacts upon TFIIIC5 depletion somehow correlate with alterations in RNA polymerase II levels? Performing similar cross-comparisons as in Figure 3C may help address this issue. Furthermore, it not clear how the authors concluded that MYCN/TFIIIC5-bound genes are not part of these so-called promoter hubs.

In Figure 3C we show that RNAPII levels are more pronounced upon MYCN activation at promoters located at MYCN hubs. Additionally, we show non-phosphorylated ChIP-seq on TSS and RNAPII-pSer2 ChIP-seq on TES density plots for promoters with MYCN interactions in the Figure for the Reviewers (Figure 3). We found no other difference than binding compared to the overall global analysis for all expressed genes showed in Figure 2B and Figure 2C. This goes on the same direction of the high expression observed of those genes in MYCN interactions observed in Figure 3C.

The changes observed in Figures 2B and 2C are global and do include the promoters with MYCN interactions. At the same time, it is required a higher number of replicates to statistically distinguish the MYCN interaction differences between TFIIIC5 presence and depletion. We acknowledge this limitation, and we therefore restrain any attempt towards this end. We base our conclusions on the other parts of the manuscript and on our previous studies that show that MYCN recruits TFIIIC, BRCA1, and the exosome to promoter proximal regions 1,4,10.

(3) Figure 5: According to the PLA results, activation of MYCN could enhance RNA polymerase II-NELFE interaction in a TFIIC5-dependent manner. Considering the raised issues regarding the use of the 8WG16 antibody, this result might be of relevance.

Nevertheless, PLA does not seem to be the optimal technique to address these questions, and I would rather suggest performing ChIP-qPCR experiments for all the factors to be compared. Finally, do the authors conclude that the TFIIIC5 effect on MYCN-dependent changes in RNA polymerase II depends upon the recruitment of EXOSC5 and BRCA1? If so, it would be interesting to determine whether depletion of these factors phenocopies the effects observed with TFIIC5.

We understand the criticism that we are comparing different assays. We have performed PLAs with different antibodies. Since the controls of the PLAs were not sufficient for us, we refrain from using them.

(4) In Figure S2 the labels should be EtOH, 4-OHT, and Input.

We changed this accordingly.

(5) On page 7, the sentence "We have shown previously that TFIIIC5 depletion does not cause significant changes in expression of multiple tRNA genes that are transcribed by RNAPIII (Buchel et al., 2017)" appears to lack a connection.

We agree with the reviewer and we deleted this sentence from the manuscript.

Author response image 1.

(A) Density plot of ChIP-Rx signal for non-phosphorylated RNAPII. Data show mean (line) ± standard error of the mean (SEM indicated by the shade) of different gene sets based on an RNA-seq of SH-EP-MYCN-ER cells ± 4-OHT. The y-axis shows the number of spike-in normalized reads and it is centered to the TES ± 2 kb. N = number of genes in the gene set defined in the methods. (B) Density plot of ChIP-Rx signal for RNAPII pSer2 as described for panel A. The signal is centered to the TSS ± 2 kb.

Author response image 2.

Bin dot plot for RNA-seq of SH-EP-MYCN-ER showing mRNA expression normalized by control per bin comparing the fold average using DESEQ2 (A), normalization to TMM in edgeR (B) and to quantile normalization (C).

Author response image 3.

Average density plot of ChIP-Rx signal for non-phosphorylated RNAPII (A) or RNAPII pSer2 (B) at promoters with MYCN interactions.

References

(1) Büchel, G., Carstensen, A., Mak, K.-Y., Roeschert, I., Leen, E., Sumara, O., Hofstetter, J., Herold, S., Kalb, J., and Baluapuri, A. (2017). Association with Aurora-A controls NMYC-dependent promoter escape and pause release of RNA polymerase II during the cell cycle. Cell reports 21, 3483-3497.

(2) Yuen, K.C., Slaughter, B.D., and Gerton, J.L. (2017). Condensin II is anchored by TFIIIC and H3K4me3 in the mammalian genome and supports the expression of active dense gene clusters. Sci Adv 3, e1700191. 10.1126/sciadv.1700191.

(3) Ferrari, R., de Llobet Cucalon, L.I., Di Vona, C., Le Dilly, F., Vidal, E., Lioutas, A., Oliete, J.Q., Jochem, L., Cutts, E., Dieci, G., et al. (2020). TFIIIC Binding to Alu Elements Controls Gene Expression via Chromatin Looping and Histone Acetylation. Mol Cell 77, 475-487 e411. 10.1016/j.molcel.2019.10.020.

(4) Papadopoulos, D., Solvie, D., Baluapuri, A., Endres, T., Ha, S.A., Herold, S., Kalb, J., Giansanti, C., Schulein-Volk, C., Ade, C.P., et al. (2021). MYCN recruits the nuclear exosome complex to RNA polymerase II to prevent transcription-replication conflicts. Mol Cell. 10.1016/j.molcel.2021.11.002.

(5) Lorenzin, F., Benary, U., Baluapuri, A., Walz, S., Jung, L.A., von Eyss, B., Kisker, C., Wolf, J., Eilers, M., and Wolf, E. (2016). Different promoter affinities account for specificity in MYC-dependent gene regulation. Elife 5. 10.7554/eLife.15161.

(6) Baluapuri, A., Hofstetter, J., Dudvarski Stankovic, N., Endres, T., Bhandare, P., Vos, S.M., Adhikari, B., Schwarz, J.D., Narain, A., Vogt, M., et al. (2019). MYC Recruits SPT5 to RNA Polymerase II to Promote Processive Transcription Elongation. Mol Cell 74, 674-687 e611. 10.1016/j.molcel.2019.02.031.

(7) Baluapuri, A., Wolf, E., and Eilers, M. (2020). Target gene-independent functions of MYC oncoproteins. Nat Rev Mol Cell Biol. 10.1038/s41580-020-0215-2.

(8) Koch, H.B., Zhang, R., Verdoodt, B., Bailey, A., Zhang, C.D., Yates, J.R., 3rd, Menssen, A., and Hermeking, H. (2007). Large-scale identification of c-MYCassociated proteins using a combined TAP/MudPIT approach. Cell Cycle 6, 205-217. 10.4161/cc.6.2.3742.

(9) Ferrari, R., Rivetti, C., Acker, J., and Dieci, G. (2004). Distinct roles of transcription factors TFIIIB and TFIIIC in RNA polymerase III transcription reinitiation. Proc Natl Acad Sci U S A 101, 13442-13447. 10.1073/pnas.0403851101.

(10) Herold, S., Kalb, J., Büchel, G., Ade, C.P., Baluapuri, A., Xu, J., Koster, J., Solvie, D., Carstensen, A., and Klotz, C. (2019). Recruitment of BRCA1 limits MYCN-driven accumulation of stalled RNA polymerase. Nature 567, 545-549.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

(1) Data on SSCs are published from a previous report (Fig. 1C). These should be deleted or marked as such.

We acknowledge the need for clarification regarding our study population for the germ cell stainings. As stated in our Materials and Methods section, our current study population includes the cohort from our previous publication (Vereecke et al., 2020), supplemented by nine additional participants, totaling n=106 trans women. Fig. 1C incorporates both previous and new data on germ cells, and this was further clarified in the Materials and Methods section.

(2) Many micrographs are suboptimal and need to be replaced by better photos presenting cellular details more clearly. 

The Figures were remade to solve the suboptimal resolution.

(3) Table 2 would benefit from a column indicating the target cell or organelle.

This column was added to Table 2.

(4) The pubertal status is poorly defined by pre- and peripubertal terms. The authors should add more informative clinical scores. 

We included information on the Tanner stages of the trans women in our cohort (all G5), as well as details on the selection criteria for our controls and their pubertal status.

(5) The characterization of Leydig cells is incomplete. Several better markers would validate the findings. 

As briefly touched upon in the discussion, the marker delta-like homolog 1 would indeed be valuable to assess the presence of truly immature Leydig cells. Unfortunately, our attempts to optimize the immunofluorescence protocol for this marker were unsuccessful, resulting in a double staining instead of a triple staining for the Leydig cells. This statement was also added to the Discussion.  

(6) The selection bias for datasets is obvious. It seems that the authors try to create nice stories but do not always refer to less compelling datasets. Here a more critical view may be necessary to gain a more realistic view and may open alternative explanations. 

We would appreciate clarification on which datasets may have been insufficiently reviewed and how our selection of highlights may have introduced bias to the interpretation and conclusion of the study. It is important to note that we did not select any patients/ data; all patient data were incorporated into our results section.

(7) The term rejuvenation for the stem cell niche/germ cell complement is misleading in the title and text. Could the authors consider another team e.g... restoration., (de)differentiation. Alternatively, define the term juvenation in a more substantial manner. 

We did not change the term “partial rejuvenation” as we believe it best describes our findings. We did however introduce the term in a more substantial manner in our Abstract and Discussion.

Reviewer #2 (Recommendations For The Authors):

(1) The authors provided a lot of scattered data, but it would be useful to formulate clear criteria (hormonal therapy, age, end points, etc.) that the material must meet so that it can be used for research into prepubertal processes. 

We have added these criteria to our Discussion. However, our current results do not yet reveal how these tissues behave in vitro. Ongoing research is addressing this question and will be presented in a future paper.

(2) Is there any research on the preservation of functions of testicular cells from trans women?

This data would be very useful, for example, for models for drug testing.  Yes: a reference to this paper was added to our Discussion.

(3) It is recommended to present the data in a table reflecting the correlations found by the authors and the correlations from the literature between cellular changes and hormone levels and age. 

After careful consideration, we have decided to proceed without incorporating these suggested changes. Our paper focuses on original findings rather than synthesizing existing literature. As such, we have chosen to emphasize our novel results and to compare them to the existing literature in the discussion section.

(4) The authors can also provide data on clinical standards for hormone levels depending on gender and age. 

This was added as Supplementary Tables 1-6.

(5) It is recommended to add links to sources from which information about cellular prepubertal, pubertal and adult markers was taken. 

This information was added throughout the manuscript.  

(6) Is it known which cells within the wall of the seminiferous tubules in adults express AMH? Please clarify. 

It has been shown that AMH receptor type 2 starts to be expressed in peritubular mesenchymal cells within the tubular walls during puberty and it remains so throughout adulthood (Sansone et al., 2020). AMH bound to this receptor may help explain the observed AMH signal in the tubular wall of peripubertal and adult controls. This information was added to our Discussion.

(7) How was the degree of hyalinization assessed? It's not obvious from the pictures.

This was further clarified in the Materials & Methods section.

(8) Why were inhibin B and AMH not measured in all patients? 

Inhibin B and AMH levels were not available for all patients due to the retrospective nature of these analyses. The measurements were not consistently recorded for all individuals within the historical dataset upon which our research relies.

(9) Why does picture 3A present few SOX9 on adult Sertoli cells, although this is their typical marker?

SOX9 was present in the adult Sertoli cells. However, this signal appears to be more "diluted" in adults due to their ongoing spermatogenesis.

Author response:

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

Reviewer #1 (Public Review):

Summary:

Ewing sarcoma is an aggressive pediatric cancer driven by the EWS-FLI oncogene. Ewing sarcoma cells are addicted to this chimeric transcription factor, which represents a strong therapeutic vulnerability. Unfortunately, targeting EWS-FLI has proven to be very difficult, and a better understanding of how this chimeric transcription factor works is critical to achieving this goal. Towards this perspective, the group had previously identified a DBD-𝛼𝛼4 helix (DBD) in FLI that appears to be necessary to mediate EWS-FLI transcriptomic activity. Here, the authors used multi-omic approaches, including CUT&tag, RNAseq, and MicroC to investigate the impact of this DBD domain. Importantly, these experiments were performed in the A673 Ewing sarcoma model where endogenous EWS-FLI was silenced, and EWS-FLI-DBD proficient or deficient isoforms were re-expressed (isogenic context). They found that the DBD domain is key to mediating EWS-FLI cis activity (at msat) and to generating the formation of specific TADs. Furthermore, cells expressing DBD-deficient EWS-FLI display very poor colony-forming capacity, highlighting that targeting this domain may lead to therapeutic perspectives.

We thank Reviewer 1 for their strong summary of Ewing sarcoma background and accurate description of our experimental approaches and findings.

Strengths:

The group has strong expertise in Ewing sarcoma genetics and epigenetics and also in using and analyzing this model (Theisen et al., 2019; Boone et al., 2021; Showpnil et al., 2022).

We thank the reviewer.  

They aim at better understanding how EWS-FLI mediated its oncogenic activity, which is critical to eventually identifying novel therapies against this aggressive cancer.

We are happy to see that our overall aim was also appreciated by Reviewer 1.

They use the most recent state-of-the-art omics methods to investigate transcriptome, epigenetics, and genome conformation methods. In particular, Micro-C enables achieving up to 1kb resolved 3D chromatin structures, making it possible to investigate a large number of TADs and sub-TADs structures where EWS-FLI1 mediates its oncogenic activity.

We thank Reviewer 1 for their acknowledgement of our approaches and the resolution achieved with our Micro-C experiments.  

They performed all their experiments in an Ewing sarcoma genetic background (A673 cells) which circumvents bias from previously reported approaches when working in non-orthologous cell models using similar approaches.

We agree with the reviewer about the importance of using model systems that accurately capture features of the disease being studied. As we have added an additional cell line in the revision we should note that this second model also represents a Ewing sarcoma genetic background while representing tumors expressing another oncogenic fusion found in this disease. 

Weaknesses:

The main weakness comes from the poor reproducibility of Micro-C data . Indeed, it appears that the distances/clustering observed between replicates are typically similar or even larger than between biological conditions. For instance, in Figure 1B, I do not see any clustering when considering DBD1, DBD2, DBD+1, DBD+2.

Lanes 80-83: "KD replicates clustered together with DBD replicate 1 on both axes and with DBD replicate 2 on the y-axis. DBD+ replicates, on the other hand, clustered away from both KD and DBD replicates. These observations suggest that the global chromatin structure of DBD replicates is more similar to KD than DBD+ replicates."

When replacing DBD replicate 1 with DBD replicate 2, their statement would not be true anymore.

Additional replicates to clarify this aspect seem absolutely necessary since those data are paving the way for the entire manuscript.

These are valid concerns and we thank the reviewers for highlighting this limitation of poor clustering of Micro-C replicates on MDS plot. We account for this variability between different replicates when identifying differentially interacting regions. By using an adjusted p-value < 0.05, we aim to ensure that repeating the experiments we will discover the same differentially interacting regions with a false discovery rate of 5%.

We also would like to note that the replicates cluster much closely on PCA plot of RNA-seq data (Supplementary Figure 1C) and as well as on PCA plot of H3K27ac CUT&Tag data (Figure 4A). Notably, the RNA-seq result has now reproduced when performed with different sets of hands across multiple studies (Boone, et. al., 2021 and this report), as well as in a second cell line (as reported in this manuscript revision). These observations suggest that the cells of these replicates are functionally similar to each other at a population level. Chromatin organization detected by Micro-C is a highly heterogenous within cells of a population (Misteli, et. al., 2020). Moreover, despite increased resolution with Micro-C over Hi-C, the conventional sequencing depth that Micro-C is performed at makes resolving finer scale 3D interactions, particularly between enhancers and promoters, challenging (Goel, et. al., 2023). Thus biologically relevant interactions driving EWSR1::ETS transcriptional regulation through de novo enhancers may have relatively weak signal in Micro-C. Both the strength of the signal and the heterogeneous chromatin state present in bulk samples could affect the average signal leading to poor clustering replicates (Hafner and Boettiger, 2022). 

Importantly, rather than add an additional replicate of a single cell line, we repeated our study in an additional cell line, TTC466, and largely reproduced our high-level findings for transcription, enhancer formation, and 3D chromatin. Specific limitations of the TTC466 study are addressed in the Discussion section (392-420). The reproduction of weak/moderate clustering in the MDS plot in both A673 and TTC466 cell lines suggests the α4 helix of EWSR1::ETS fusions are important for reshaping 3D chromatin. However, higher resolution analyses focused on specific EWSR1::ETS-bound loci are likely an important area of future study required to fully understand the role of the α4 helix in chromatin regulation in Ewing sarcoma.

Similarly:

- In Figure 1C, how would the result look when comparing DBD2/KD2/DBD+2? Same when comparing DBD 1 with KD1 and DBD+1. Would the difference go in the same direction?

This is a great point. We added distance decay plots of individual replicates in Supplementary Figure 2 and added discussion of these results in lines 88-89 of the text.

- Figure 1D-E. How would these plots look like when comparing each replicate to each other's? How much difference would be observed when comparing, for instance, DBD1/DBD2 ? or DBD1/DBD+1?

Unfortunately, separate replicates are required to conduct Differentially Interacting Region analysis as it determines statistically significant interactions. Therefore, we are unable to plot these analyses with individual replicates. 

- Figure 2: again, how would these analyses look like when performing the analysis with only DBD1/DBD+1/KD1 or DBD2/DBD+2/KD?

This is a good suggestion. It is possible to do such analysis. However, we will lose resolution as such that we may not accurately detect TADs, especially smaller TADs. Therefore, we decided to combine the biological replicates.   

Another major question is the stability of EWS-FLI DBD vs EWS-FLI DBD+ proteins. In the WB, FLAG intensities seem also higher (2/3 replicates) in DBD+ condition compared to the DBD condition (Figure S1B).

This is a valid concern with shRNA knock-down/rescue system and we regularly validate new constructs to ensure that they have similar expression levels as rescue with the wildtype fusion before proceeding to more exhaustive experimental workups. We would note that while we have not tested for differences in protein stability, for these constructs we largely see similar expression levels across multiple experiments, multiple cell lines, and multiple sets of hands. There may be some variations in expression level from experiment to experiment, but western blotting is a semiquantitative assay and it is also not possible to rule out that slight differences in band intensity may be a result of error in gel loading. For this reason, alongside western blotting for construct expression, we also validate construct function using RNA-seq and colony formation assays (as reported in this manuscript) and these show good agreement across biological replicates.  

Indeed, it seems that they have more FLAG (i.e., EWS-FLI) peaks in the DBD+ condition compared to the DBD condition (Figure 2B). 

We appreciate the comment since the legend of Figure 2B led to a misunderstanding. Figure 2B depicts the number of TADs detected in DBD and DBD+ conditions (height of the bar graphs) and the proportion of those TADs overlapped with FLAG, CTCF, both or neither peaks on y-axis. The number of FLAG peaks is actually lower in DBD+ as compared to DBD as shown in Figure 5A-B.  We clarified our Figure 2 legend to accurately describe the various proportions (color coded section) of TADs bound by DBD/DBD+ FLAG and CTCF.

Would it be possible that DBD+ is just more expressed or more stable than DBD? The higher stability of the re-expressed DBD+ could also partially explain their results independently of the 3D conformational change. In other words, can they exclude that DBD+ and DBD binding are not related to their respective protein stability or their global re-expression levels?

It is possible that DBD+ protein is overexpressed or more stable than DBD. With our current set of data, we cannot conclusively exclude if binding by DBD and DBD+ are not related to their expression level or stability. We would note, as above, that western blots, RNA-seq, and agar assays have largely reproduced across experiments, hands, and cell lines and that western blot is an imperfect assay for assessing protein stability.

Surprisingly, WB FLI bands in DBD+ conditions are systematically (3/3 replicates) fainter than in DBD conditions (Figure S1B). How do the authors explain these opposite results between FLI and FALG in the WB?

This is an excellent observation that highlights one of the intricacies of studying EWSR1::FLI1 in our KD/rescue system. Often the limiting factor for an experiment is whether or not the KD condition maintains KD through a second viral transduction for rescue and selection. We have observed over many years of working with this system that rescue conditions which are fully functional (i.e. wildtype EWSR1::FLI1, DBD+, etc.) tend to maintain better KD of endogenous EWSR1::FLI1. Constructs that don’t rescue EWSR1::FLI1 function sometimes maintain KD to a lesser degree, though frequently to a functional degree (i.e. cells are not transformed and EWSR1::FLI1 transcriptional regulation is not rescued). We suspect this observation, also raised by Reviewer 1 is resulted from a potential selection of cells with more endogenous EWSR1::FLI1 escaping KD in in DBD conditions due to selective pressures during expansion in tissue culture.

We should note that the antibody used for detecting FLI recognizes residues that are deleted in

DBD and DBD+ constructs, such that the FLI1 blot in Supplementary Figure 1B does not detect either construct. It only detects endogenous EWSR1::FLI1 and the 3X-FLAG-EWSR1::FLI1 construct in the middle lane that runs at a slightly higher molecular weight. The FLAG antibody is the only antibody that detects all three rescue constructs.    

Reviewer #2 (Public Review):

Summary:

The manuscript by Bayanjargal et al. entitled "The DBD-alpha4 helix of EWS::FLI is required for GGAA microsatellite binding that underlies genome regulation in Ewing sarcoma" reports on the critical role of a small alpha helix in the DNA binding domain (DBD) of the FLI1 portion of EWS::FLI1 that is critical for binding to repetitive stretches of GGAA-motifs, i.e. GGAA microsatellites, which serve as potent neoenhancers in Ewing sarcoma.

We thank Reviewer 2 for their succinct and accurate summary of our manuscript. 

Strengths:

The paper is generally well-written, and easy to follow and the data presented are of high quality, welldescribed and underpin the conclusions of the authors. The report sheds new light on how EWS::FLI1 mechanistically binds to and activates GGAA microsatellite enhancers, which is of importance to the field.

We appreciate the reviewer’s assessment of our work. 

Weaknesses:

While there are no major weaknesses in this paper, there are a few minor issues that the authors may wish to address before publication:

(1) While the official protein symbol for the gene EWSR1 is indeed EWS, the protein symbol for the gene FLI1 is identical, i.e. FLI1. The authors nominate the fusion oncoprotein EWS::FLI1 (even in the title) but it appears more adequate to use EWS::FLI1.

We appreciate the reviewer for bringing this to our attention. Indeed, the most recent guideline for fusion proteins nomenclature is to use the full gene symbols separated by double colons. Therefore, the accurate nomenclature is EWSR1::FLI1. We replaced instances of EWS::FLI with EWSR1::FLI1 and have used the EWSR1::ERG nomenclature in our revised manuscript.  

(2) The used cell lines should be spelled according to their official nomenclature (e.g. A-673 instead of A673).

Corrected, thanks!

(3) It appears as if the vast majority of results were generated in a single Ewing sarcoma cell line (A-673) which is an atypical Ewing sarcoma cell line harboring an activating BRAF mutation and may be genomically quite unstable as compared to other Ewing sarcoma cell lines (Kasan et al. 2023 preprint at bioRxiv https://www.biorxiv.org/content/10.1101/2023.11.20.567802v1). Hence, it may be supportive for the paper to recapitulate/cross-validate a few key results in other Ewing sarcoma cell lines, e.g. by using EWS::ERG-positive cell lines. Perhaps the authors could make use of available published data.

We thank Reviewer 2 for this helpful comment. We replicated the experiments in TTC-466 cells containing EWSR1::ERG fusion and found that as for A-673 cells the DBD-α4 helix is important for transcriptional, enhancer, and 3D chromatin regulation (Supplementary Figures 9-18).  

(4) Figure 6 and Supplementary Figure 5 are very interesting but focus on two selected target genes of the fusion (FCGRT and CCND1). It would be interesting to see whether these findings also extend to common EWS::ETS transcriptional signatures that have been reported. The authors could explore their data and map established consensus EWS::ETS signatures to investigate which other hubs might be affected at relevant target genes.

We expanded our analysis to other genes demonstrated to be regulated by EWSR1::FLI1 nucleated transcriptional hubs (Chong, et. al., 2018) and included NKX2-2 and GSTM4 gene regions in

Supplementary Figure 7-8 in A-673 cells. We also investigated the same gene regions of FCGRT, CCND1, NKX2-2, GSTM4 in TTC466 cells and report them in Supplementary Figures 14-17. For the purpose brevity, we decided to include the above examples. We may need to develop different tools to conduct further analysis to understand the gene regulatory networks driven by DBD and DBD+ in relation to hub formation. Although it is a great suggestion to map such network, this may be outside the scope of this manuscript. We thank the reviewer for bringing such a good point to our attention.  

(5) Table 1 is a bit hard to read. In my opinion, it is not necessary to display P-values with up to 8 decimal positions. The gene symbols should be displayed in italic font.

Suggestions are adapted, thanks!

Reviewing Editor (Recommendations For The Authors):

We would draw the authors' attention to the following issues that would best benefit from additional revision.

As indicated by Referee 1, an important issue concerns the apparent poor reproducibility of Micro-C data. In Figure 1B, the clustering of the DBD1, DBD2, DBD+1, and DBD+2 is poor.

It appears that the distances/clustering observed between replicates are typically similar or even larger than between biological conditions. Lines 80-83: "KD replicates clustered together with DBD replicate 1 on both axes and with DBD replicate 2 on the y-axis. DBD+ replicates, on the other hand, clustered away from both KD and DBD replicates. If one replaced DBD replicate 1 with DBD replicate 2, this statement would no longer be true. The referees believe that it is important to fully account for these potential discrepancies. Most of the study is based on analyses of these data sets, so if there are issues with them it has repercussions on the entire study. We note however that in Figure 4A the clustering of the H3K27ac data is much more convincing. The referees also feel that it is important to show immunoblots of the expression of DBD and DBD+ levels in the experiments performed here. While this was previously shown in the Boone et al publication in 2021, it could be illustrated again here.

We thank the editors for concisely summarizing the main weaknesses of the paper and underscoring the importance of the Micro-C data in the rest of the paper. While the Editors note tighter clustering of the H3K27ac (Figure 4A), we would like to note that the replicates cluster much closely on PCA plot of RNA-seq data (Supplementary Figure 1C). Notably, the RNA-seq result has now reproduced when performed with different sets of hands across multiple studies (Boone, et. al., 2021 and this report), as well as in a second cell line (as reported in this manuscript revision). Though not as tight, the H3K27ac CUT&Tag also reproduces in TTC466 cells. Thus, we interpret these findings to indicate that our replicates are functionally similar to each other. As discussed above in the response to Reviewer 1 in more detail, there are several factors that could affect how these functional similarities are represented in Micro-C data. Micro-C is ultimately a readout of the chromatin organization in a heterogeneous population of cells (Misteli et al., 2020). Additionally, sequencing depth limitations in conventional Micro-C experiments limit the ability to faithfully assess the enhancer-promoter interactions that may be relevant for our model system (Goel, et. al., 2023). Thus, both the strength of the biologically relevant signal and the heterogeneous chromatin state present in bulk samples could affect the average signal and lead to poorly clustering replicates (Hafner and Boettiger, 2022). 

To address these important concerns about rigor and reproducibility of the analyses, we repeated our study in an additional cell line, TTC466, and largely reproduced our high-level findings for transcription, enhancer formation, and 3D chromatin. These additional studies were not without their own limitations and these are addressed in the Discussion section (392-420). The reproduction of weak/moderate clustering in the MDS plot in both A673 and TTC466 cell lines suggests the α4 helix of EWSR1::ETS fusions are important for reshaping 3D chromatin. However, additional genomic analyses geared toward higher resolution at specific EWSR1::ETS-bound loci are likely an important area of future study required to fully understand the role of the α4 helix in chromatin regulation in Ewing sarcoma. Live cell imaging, as performed by Chong, et. al., 2018 and additional biochemical techniques may also be informative and are beyond the scope of this report.

With regards to concerns about construct expression, we have included immunoblots of the rescue constructs in both cell lines (Supplementary Figure 1B and 9A) and discussed Reviewer 1’s specific concerns in detail above.  

The referees also raise the issue of using an additional cell line to make a more general message. Although it would perhaps be asking too much to repeat the MicroC experiments, consolidation of the observations could be performed by focusing on specific loci such as FCGRT and CCND1 that were analyzed in this study. Could the authors use 4C-type experiments to reproduce the conclusions in an additional cell line? It would also be pertinent to consolidate the findings at these loci by 4C-type approaches even in the cell line used here. For the moment, all conclusions are based on the same set of data and a single technical approach.

We repeated the experiments in TTC466 cells and analyzed the data using same cut-offs used in A-673 cells. This allows us to compare between the two cell lines. We hope this new set of experiments and analyses address the reviewers’ concerns.  

Reviewer #1 (Recommendations For The Authors):

All the data are performed in A673 cells. Knowing the transcriptomic and epigenetic heterogeneity of Ewing sarcoma cells, some of the experiments supporting their findings should be replicated in at least another Ewing sarcoma model.

Per our discussion above, we have replicated our experiments in an additional cell line model of Ewing sarcoma. Importantly, the TTC466 cell line used expresses the EWSR1::ERG fusion found in 10-15% of Ewing sarcoma cases.  

Supplementary Figure 2B. Proportion of TAD boundaries bound by FLAG (i.e., EWS-FLI1) and CTCF. The number/proportion of FLAG (i.e., EWS-FLI) peaks observed at CTCF peak/TAD boundaries seems unexpectedly high. How do they explain this result since EWS-FLI peaks are rather intra-TAD to mediate their enhancer function?

In our previous study, we showed that EWSR1::FLI1 binding can be detected at boundaries of TADs (Showpnil, et. al., 2022). We think therefore it is likely that EWSR1::FLI1 binding is able to mediate enhancer function both inside TADs as well as at the borders of TADs and may, in some cases, function as an insulator between TADs.  

For the >50kb loop analysis, what was the low-range threshold? Up to 15-20 kp, contact frequency interactions may be caused by PFA crosslink (did they use a 5kb threshold ?). Were those excluded from that analysis?

We acknowledge that we did not use a lower threshold to exclude those short-range loop interactions. In our previous study, we observed that EWSR1::FLI1 binding reduces long-range interactions in favor of short-range interactions (Showpnil, et. al., 2022) and wanted to be able to capture short-range loops in our analysis.  

In Figure 2D, they observed that within TADs containing FLAG peaks at GGAA microsatellites, the intensity of the DBD+ FLAG peaks was higher compared to DBD FLAG peaks. How would this analysis look when considering the ETS FLAG peaks (i.e., EWS-FLI rather repressive peaks)? Could they compare TAD with GGAA msat vs TAD with ETS peaks?

We agree that this is an interesting observation. In our prior analyses we found no discernible relationship between EWSR1::FLI1 binding and changes in 3D chromatin associated with repression (Showpnil, et. al., Nucleic Acids Research, 2022). In contrast, EWSR1::FLI1-bound superenhancers had greater H3K27ac deposition when overlapping both a bound GGAA repeat and a non-microsatellite site. While there have been several additional reports about the relevance of EWSR1::FLI1 binding at nonmicrosatellite peaks, motifs at these loci have not yet been rigorously defined as GGAA repeats were by Johnson, et. al. in PLoS One, 2017. Each ETS factor binds different motifs containing the core 5’-GGAA-3’ with varying affinities depending on the flanking residues. There may be >100-fold difference in sequence-specific binding affinity for “high” vs. “low” affinity motifs. Better defining the types of ETS motifs bound by EWSR1::FLI1 and the functional changes associated with them thus represents an interesting area of future study.

Figure 1F: What is the biological meaning of these results (29.7, 39.5, and 54Mbp)? These distances are typically the size of a chromosome arm and clearly beyond classical chromatin loop/TAD structures in which EWS-FLI mediates its cis-activity.

We agree with referee here. This panel is now removed in our revised manuscript.  

How do DBD, KD, and DBD+ conditions compare with WT parental cells in the omics data? (Figures 1B, 4A). Do DBD+ conditions overlap with WT conditions? It would be nice to have these analyses also for Micro-C and Cut&Tag data. To be acknowledged here, the transcriptome data showing this aspect in Figure S1C are very convincing.

This is a fair point. We were not able to obtain similar sequencing depth of wtEF Micro-C libraries to that of KD, DBD and DBD+ due to disproportional use of wtEF libraries in troubleshooting. Therefore, we decided to exclude wtEF condition from these analysis. 

EWS-FLI cis-regulation at CCND1 also occurs through a much closer EWS-FLI peak (~-20kb msat upstream of CCND1 TSS) which was not taken into consideration. EWS-FLI peak intensity in both DBD and DBD+ at this msta seems similar. How would this fit into their model?

The referee is correct. The closest peak upstream of CCND1 TSS is about ~19kb away. We highlighted this peak with the dashed boxes near the CCND1 TSS (Supplementary Figure 6). Peak intensity of DBD+ FLAG is slightly higher compared to DBD. Nonetheless, we acknowledge that the difference is small. We suspect that the DBD-α4 helix is affecting binding dynamics at GGAA repeats, but these genomics approaches are not well suited to detect small, but significant, changes in binding affinity or dynamics. In this case a more biochemical approach may be needed. Even though, both protein can still bind the same microsatellites, it is possible that they might differ in their stability of binding or in the recruitment of additional proteins. These possibilities are discussed in the Discussion section (444-463).  

For the Micro-C, they sequenced only 7 to 8 million reads per condition. This coverage seems particularly low, especially for their analyses using 1-5kb bins. How does this compare with other published Micro-C data? Can this explain the variability observed between replicates?

We apologize for the inconsistent verbiage of sequencing coverage that may have caused confusion. 7 to 8 million reads were used for shallow sequencing and QC analysis. Once a sample passed QC, we then sequenced 300 million reads per sample. 300M is now changed to 300 million to prevent a misunderstanding at line 598.  

They mention:

"In our recent studies of EWS::FLI, we found a small alpha helix in the DNA binding domain DBD-𝛼𝛼4, to

be required for transcription and regulation by the fusion protein (Boone et al., 2021). Interestingly, this study did not find any change in chromatin accessibility (ATAC-Seq) and genome localization of EWS::FLI constructs (CUT&RUN) when DBD-𝛼𝛼4 helix was deleted leaving the mechanistic basis for the requirement of DBD-𝛼𝛼4 in transcription regulation unclear. "

And

"To assay the enhancer landscape, we collected H3K27ac CUT&Tag data from KD, DBD, and DBD+ cells. Principal component analysis of H3K27ac localization shows that the DBD replicates were clustered closer to the KD replicates while being in between the KD and the DBD+ replicates (Figure 4A), suggesting that DBD-𝛼𝛼4 helix is required to reshape the enhancer landscape."

But now H3K27ac CUT&Tag show strong differences which were not observed in ATAC seq. How to explain this discrepancy?

Though both H3K27ac and ATAC signal are associated with enhancers and promoters in euchromatin, they are not exactly measurements of the same thing. H3K4me2 is a mark more closely associated with ATAC signal than H3K27ac (Henikoff, et. al., 2020). Nonetheless, there are clear differences between the prior publication (Boone, et. al., 2021) and this work with regards to similar ATAC signal for each replicate and differences in H3K27ac. We suspect this may be related to a tighter association between H3K27ac and EWSR1::FLI1-mediated genome regulation and ATAC. Notably, there were very few differentially accessible regions between EWSR1::FLI1-depleted cells and conditions with EWSR1::FLI1 expression (either endogenous or wildtype rescue) using the A673 KD/Rescue system in Boone, et. al., 2021. In contrast, other A673 KD-rescue studies have reported differences in H3K27ac in EWSR1::FLI1 expressing conditions relative to EWSR1::FLI1-depleted conditions (Theisen, et. al., 2021). .  

The authors mention:

"Our study thus uncovered a surprising role for FLI DBD in the process of hub formation which is usually attributed to the EWS low complexity domain."

Not sure this can be claimed, hubs are composed of many other factors that are not investigated here. Furthermore, promoter enhancer hubs/loops often include combined ETS and mSat chains to generate transcriptional hubs which have not been considered here. None of these points were discussed here.

We replaced “uncovered” with “suggest” in our revised manuscript at line 476.  

What are the barcode patterns in Supp 5, are those frequently observed in their Micro-C data, likely mapping artifacts, do they have any impact on their analyses?

The barcode patterns in now Supplementary Figure 6 are blind spots in the hg19 genome assembly. Since they are few in numbers, we don’t expect these blind spots to impact our analysis.

Author response:

Reviewer #1 (Public Review): 

Summary: 

The authors use fluorescence lifetime imaging (FLIM) and tmFRET to resolve resting vs. active conformational heterogeneity and free energy differences driven by cGMP and cAMP in a tetrameric arrangement of CNBDs from a prokaryotic CNG channel. 

Strengths: 

The excellent data provide detailed measures of the probability of adopting resting vs. activated conformations with and without bound ligands. 

Weaknesses: 

Limitations are that only the cytosolic fragments of the channel were studied, and the current manuscript does not do a good job of placing the results in the context of what is already known about CNBDs from other methods that yield similar information. 

In the revision, we will put our results into context of the previous work of CNBD channels where possible.

Reviewer #2 (Public Review): 

The authors investigated the conformational dynamics and energetics of the SthK Clinker/CNBD fragment using both steady-state and time-resolved transition metal ion Förster resonance energy transfer (tmFRET) experiments. To do so, they engineered donor-acceptor pairs at specific sites of the CNBD (C-helix and β-roll) by incorporating a fluorescent noncanonical amino acid donor and metal ion acceptors. In particular, the authors employed two cysteine-reactive metal chelators (TETAC and phenM). This allowed them to coordinate three transition metals (Cu2+, Fe2+, and Ru2+) to measure both short (10-20 Å, Cu2+) and long distances (25-50 Å, Fe2+, and Ru2+). By measuring tmFRET with fluorescence lifetimes, the authors determined intramolecular distance distributions in the absence and presence of the full agonist cAMP or the partial agonist cGMP. The probability distributions between conformational states without and with ligands were used to calculate the changes in free energy (ΔG) and differences in free energy change (ΔΔG) in the context of a simple four-state model. 

Overall, the work is conducted in a rigorous manner, and it is well-written. I greatly enjoyed reading it. 

Nonetheless, I do not see the novelty that the authors claim. 

We will try to highlight the novelty in the revision. (See below for examples).

In terms of methodology, this work provides further support to steady-state and time-resolved tmFRET approaches previously developed by the authors of the present work to probe conformational rearrangements by using a fluorescent noncanonical amino acid donor (Anap) and transition metal ion acceptor (Zagotta et al., eLIfe 2021; Gordon et al., Biophysical Journal 2024; Zagotta et al., Biophysical Journal 2024). 

This work is the first use of the time-resolved tmFRET method to obtain intrinsic DG (of an apo conformation) and DDG values for different ligands, and the first application of this approach to a protein other than MBP.

Regarding cyclic nucleotide-binding domain (CNBD)-containing ion channels, I disagree with the authors when they state that "the precise allosteric mechanism governing channel activation upon ligand binding, particularly the energetic changes within domains, remains poorly understood". On the contrary, I would say that the literature on this subject is rather vast and based on a significantly large variety of methodologies. This is a not exhaustive list of papers: Zagotta et al., Nature 2003; Craven et al., GJP, 2004; Craven et al., JBC, 2008; Taraska et al., Nature Methods, 2009; Puljung et al., JBC, 2013; Saponaro et al., PNAS 2014; Goldschen-Ohm et al., eLife, 2016; Bankston et al., JBC, 2017; Hummert et al., PLoS Comput Biol., 2018; Porro et al., eLife, 2019; Ng et al., JGP, 2019; Porro et al., JGP, 2020; Evans et al., PNAS, 2020; Pfleger et al., Biophys J. 2021; Saponaro et al., Mol Cell, 2021; Dai et al., Nat Commun. 2021; Kondapuram et al., Commun Biol. 2022. These studies were conducted either on the isolated Clinker/CNBD fragments or on the entire full-length proteins. As is evident from the above list, the authors of the present work have significantly contributed to the understanding of the allosteric mechanism governing the ligand-induced activation of CNBD-containing channels, including a detailed description of the energetic changes induced by ligand binding. Particularly relevant are their works based on DEER spectroscopy. In DeBerg et al., JBC 2016, the authors described, in atomic detail, the conformational changes induced by different cyclic nucleotides on the HCN CNBD fragment and derived energetics associated with ligand binding to the CNBD (ΔΔG). In Collauto et al., Phys Chem Chem Phys. 2017, they further detailed the ligand-CNBD conformational changes by combining DEER spectroscopy with microfluidic rapid freeze quench to resolve these processes and obtain both equilibrium constants and reaction rates, thus demonstrating that DEER can quantitatively resolve both the thermodynamics and the kinetics of ligand binding and the associated conformational changes. 

Despite this vast literature, some of which is our own work, there is no consensus about the energetics and coupling of domains that underlies the allosteric mechanism in any CNBD channel. Our approach addresses energetics of the CNBD upon ligand binding, which we aim to later expand to a more complete assessment of the allosteric mechanism in the intact channel.

Suggestions: 

- In light of the above, I suggest the authors better clarify the contribution/novelty that the present work provides to the state-of-the-art methodology employed (steady-state and time-resolved tmFRET) and of CNBD-containing ion channels. In particular, it would be nice to have a comparison with the conformational dynamics and energetics reported in the previous works of the authors based on DEER spectroscopy (DeBerg et al., JBC 2016, Collauto et al., Phys Chem Chem Phys. 2017 and Evans et al., PNAS, 2020) and with Goldschen-Ohm et al., eLife, 2016, where single-molecule events (FRET-based) of cAMP binding to HCN CNBD were measured and kinetic rate constants were models in the context of a simple four-state model, reminiscent of the model employed in the present work. 

In the revision, we will put our results into context of the previous work of CNBD channels where possible.

- Even considering the bacterial SthK channel, cryo-EM has significantly advanced the atomistic understanding of its ligand-dependent regulation (Rheinberger et al., eLife, 2018). More recently, the authors of the present work have elegantly employed DEER on full-length SthK protein to reveal ligand-dependent conformational rearrangements in the Clinker region (Evans et al., PNAS, 2020). In light of the above, what is the contribution/novelty that the present work provides to the SthK biophysics? 

Neither of the papers mentioned above (structure or DEER) reported energetics for SthK. This work describes an approach that will allow us to get a more complete picture of the energetics of SthK.

- The authors decided to use the Clinker/CNBD fragment of SthK. On the basis of the above-cited work (Evans et al., PNAS, 2020) the authors should clarify why they have decided to work on the isolated Clinker/CNBD fragment and not on the full-length protein. I assume that the use of the C-licker/CNBD fragment was necessary to isolate tetramers with only one labelled subunit (fSEC and MP were used to confirm this) to avoid inter-subunit crass-talk. However, I am not clear if this is correct. 

We chose to start on the C-terminal fragment to provide a technically more tractable system for validating our approach using time-resolved tmFRET before moving to the full-length membrane protein.

- What is the advantage of using the Clinker/CNBD fragment of a bacterial protein and not one of HCN channels, as already successfully employed by the authors (see above citations)? 

SthK is a useful model system that allows us to later express full-length channels in bacteria.

Reviewer #3 (Public Review): 

Summary: 

This manuscript aims to provide insights into conformational transitions in the cyclic nucleotide-binding domain of a cyclic nucleotide-gated (CNG) channel. The authors use transition metal FRET (tmFRET) which has been pioneered by this lab and previously led to detailed insights into ion channel conformational changes. Here, the authors not only use steady-state measurements but also time-resolved, fluorescence lifetime measurements to gain detailed insights into conformational transitions within a protein construct that contains the cytosolic C-linker and cyclic nucleotide-binding domain (CNBD) of a bacterial CNG channel. The use of time-resolved tmFRET is a clear advancement of this technique and a strength of this manuscript. 

In summary, the present work introduced time-resolved tmFRET as a novel tool to study conformational distributions in proteins. This is a clear technological advance. At this stage, conclusions made about energetics in CNG channels are overstated. However, it will be interesting to see in the future how results compare to similar measurements on full-length channels, for example, reconstituted into nanodiscs. 

Strengths: 

The results capture known differences in promoting the open state between different ligands (cAMP and cGMP) and are consistent across three donor-acceptor FRET pairs. The calculated distance distributions further are in reasonable agreement with predicted values based on available structures. The finding that the C-helix is conformationally more mobile in the closed state as compared to the open state quantitatively increases our understanding of conformational changes in these channels. 

Weaknesses: 

While the use of a truncated construct of SthK is justified, it also comes with certain limitations. The construct is missing the transmembrane part including the pore for ions. However, the pore is the central part of every ion channel and is crucial to describe conformational transitions and energetics that lead to ion channel gating. Two observations in the present study disagree with the results for the full-length channel protein. Here, under apo conditions, the CNBD can adopt an 'open' conformation, and second, cooperativity of channel opening is lost. These differences need to be weighed carefully when judging the impact of the presented results for understanding allostery in CNG channels. Qualitatively, the results can describe movements of the C-helix in CNBDs, but detailed energetics as calculated in this study, need to be limited to the truncated protein construct used. The entire ion channel is an allosteric system and detailed, energetic conclusions cannot be made for the full-length channel when working with only the cytosolic domains. Similarly, the statement "These results demonstrate that time-resolved tmFRET can be utilized to obtain energetic information on the individual domains during the allosteric activation of SthK." is misleading. The data only describe movements of the C-helix. Upon ligand binding, the C-helix moves upwards to coordinate the ligand. Thus, the results are ligand-induced conformational changes (as the title states). Allosteric regulation usually involves remote locations in the protein, which is not the case here. 

We agree that the full-length channel is more complicated than the C-terminal fragment studied here, but we disagree that there isn’t relevant energetic information from the individual domains. For example, the DDG values measured for the C-helix movement in the isolated fragment should be the same as those of the intact channel. In the future we aim to make direct comparisons of the energetics between the fragment and the intact channel.

Author response:

We thank the editors and the reviewers for their considered comments and helpful suggestions.

In our revision, we plan to focus on tightening the relationship between the bias-variance tradeoff theory and the empirical analyses that follow.

We will also work to better communicate what we argue—and what is beyond our scope—with respect to GxE in complex traits. For example, our language is currently insufficiently clear as it suggested to the editor and reviewers that we are developing a method to characterize polygenic GxE here. Developing a new method that does so (let alone evaluating performance in extensive scenarios) is beyond the scope of this manuscript.

Similarly, we use amplification only as an example of a mode of GxE that is not adequately characterized by current approaches. We do not wish to argue it is an omnibus explanation for all GxE in complex traits. In many cases, a mixture of polygenic GxE relationships seems most fitting (as observed, for example, in Zhu et al., 2023, for GxSex in human physiology).

Author response:

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

eLife assessment

This important study combines fMRI and electrophysiology in sedated and awake rats to show that LFPs strongly explain spatial correlations in resting-state fMRI but only weakly explain temporal variability. They propose that other, electrophysiology-invisible mechanisms contribute to the fMRI signal. The evidence supporting the separation of spatial and temporal correlations is convincing, however, the support of electrophysiological-invisible mechanisms is incomplete, considering alternative potential factors that could account for the differences in spatial and temporal correlation that were observed. This work will be of interest to researchers who study the fundamental mechanisms behind resting-state fMRI.

We appreciate the encouraging comments. We added a section in discussion that thoroughly discussed the potential alternative factors that could account for the differences in spatial and temporal correlation that we observed. 

Public Reviews:

Reviewer #1 (Public Review):

Tu et al investigated how LFPs recorded simultaneously with rsfMRI explain the spatiotemporal patterns of functional connectivity in sedated and awake rats. They find that connectivity maps generated from gamma band LFPs (from either area) explain very well the spatial correlations observed in rsfMRI signals, but that the temporal variance in rsfMRI data is more poorly explained by the same LFP signals. The authors excluded the effects of sedation in this effect by investigating rats in the awake state (a remarkable feat in the MRI scanner), where the findings generally replicate. The authors also performed a series of tests to assess multiple factors (including noise, outliers, and nonlinearity of the data) in their analysis.

This apparent paradox is then explained by a hypothetical model in which LFPs and neurovascular coupling are generated in some sense "in parallel" by different neuron types, some of which drive LFPs and are measured by ePhys, while others (nNOS, etc.) have an important role in neurovascular coupling but are less visible in Ephys data. Hence the discrepancy is explained by the spatial similarity of neural activity but the more "selective" LFPs picked up by Ephys account for the different temporal aspects observed.

This is a deep, outstanding study that harnesses multidisciplinary approaches (fMRI and ephys) for observing brain activity. The results are strongly supported by the comprehensive analyses done by the authors, which ruled out many potential sources for the observed findings. The study's impact is expected to be very large.

Comment: There are very few weaknesses in the work, but I'd point out that the 1second temporal resolution may have masked significant temporal correlations between

LFPs and spontaneous activity, for instance, as shown by Cabral et al Nature Communications 2023, and even in earlier QPP work from the Keilholz Lab. The synchronization of the LFPs may correlate more with one of these modes than the total signal. Perhaps a kind of "dynamic connectivity" analysis on the authors' data could test whether LFPs correlate better with the activity at specific intervals. However, this could purely be discussed and left for future work, in my opinion.

We appreciate this great point. Indeed, it is likely that LFP and rsfMRI signals are more strongly related during some modes/instances than others, and hence correlation across the entire time series may have masked this effect. In addition, we agree that 1-second temporal resolution may obscure some temporal correlations between LFPs and rsfMRI signal. The choice of 1-second temporal resolution was made to be consistent with the TR in our fMRI experiment, considering the slow hemodynamic response. Ultrafast fMRI imaging combined with dynamic connectivity analysis in a future study might enable more detailed examination of BOLD-LFP temporal correlations at higher temporal resolutions. We have added the following paragraph to the revised manuscript:

“Our proposed theoretic model represents just one potential explanation for the apparent discrepancy in temporal and spatial relationships between resting-state electrophysiology and BOLD signals. It is important to acknowledge that there may be other scenarios where a stronger temporal relationship between LFP and BOLD signals could manifest. For instance, recent research suggests that the relationship between LFP and rsfMRI signals may vary across different modes or instances (Cabral et al., 2023), which can be masked by correlations across the entire time series. Moreover, the 1-second temporal resolution employed in our study may obscure certain temporal correlations between LFPs and rsfMRI signals. Future investigations employing ultrafast fMRI imaging coupled with dynamic connectivity analysis could offer a more nuanced exploration of BOLD-LFP temporal correlations at higher temporal resolutions (Bolt et al., 2022; Cabral et al., 2023; Ma and Zhang, 2018; Thompson et al., 2014).”

Reviewer #2 (Public Review):

The authors address a question that is interesting and important to the sub-field of rsfMRI that examines electrophysiological correlates of rsfMRI. That is, while electrophysiology-produced correlation maps often appear similar to correlation maps produced from BOLD alone (as has been shown in many papers) is this actually coming from the same source of variance, or independent but spatially-correlated sources of variance? To address this, the authors recorded LFP signals in 2 areas (M1 and ACC) and compared the maps produced by correlating BOLD with them to maps produced by BOLD-BOLD correlations. They then attempt to remove various sources of variance and see the results.

The basic concept of the research is sound, though primarily of interest to the subset of rsfMRI researchers who use simultaneous electrophysiology. However, there are major problems in the writing, and also a major methodological problem.

Major problems with writing:

Comment 1: There is substantial literature on rats on site-specific LFP recording compared to rsfMRI, and much of it already examined removing part of the LFP and examining rsfMRI, or vice versa. The authors do not cover it and consider their work on signal removal more novel than it is.

We have added more literature studies to the revised manuscript. It is important to note that while there exists a substantial body of literature on site-specific LFP recording coupled with rsfMRI, our paper makes a significant contribution by unveiling the disparity in temporal and spatial relationships between resting-state electrophysiological and fMRI signals. This goes beyond mere reporting of spatial/temporal correlations. Furthermore, our exploration of the impact of removing LFP on rsfMRI spatial patterns constitutes one among several analyses employed to demonstrate that the temporal fluctuations of LFP minimally affect BOLD-derived RSN spatial patterns. We wish to clarify that our intention is not to claim this aspect of our work is more novel than similar analyses conducted in previous studies (we apologize if our original manuscript conveyed that impression). Rather, the novelty lies in the objective of this analysis, which is to elucidate the displarity in temporal and spatial relationships between resting-state electrophysiological and fMRI signals—a crucial issue that has not been thoroughly addressed previously. 

Comment 2: The conclusion of the existence of an "electrophysiology-invisible signal" is far too broad considering the limited scope of this study. There are many factors that can be extracted from LFP that are not used in this study (envelope, phase, infraslow frequencies under 0.1Hz, estimated MUA, etc.) and there are many ways of comparing it to the rsfMRI data that are not done in this study (rank correlation, transformation prior to comparison, clustering prior to comparison, etc.). The one non-linear method used, mutual information, is low sensitivity and does not cover every possible nonlinear interaction. Mutual information is also dependent upon the number of bins selected in the data. Previous studies (see 1) have seen similar results where fMRI and LFP were not fully commensurate but did not need to draw such broad conclusions.

First we would like to clarify that the existence of "electrophysiologyinvisible signal" is not necessarily a conclusion of the present study, per se, as described by the reviewer. As we stated in our manuscript, it is a proposed theoretical model. We fully acknowledge that this model represents just one potential explanation for the apparent discrepancy in temporal and spatial relationships between resting-state electrophysiology and BOLD signals. It is important to acknowledge that there may be other scenarios where a stronger temporal relationship between LFP and BOLD signals could manifest. This issue has been further clarified in the revised manuscript (see the section of Potential pitfalls). 

We agree with the reviewer that not all factors that can be extracted from LFP are examined. In our current study we focused solely on band-limited LFP power as the primary feature in our analysis, given its prevalence in prior studies of LFP-rsfMRI correlates. More importantly, we demonstrate that band-specific LFP powers can yield spatial patterns nearly identical to those derived from rsfMRI signals, prompting a closer examination of the temporal relationship between these same features. Furthermore, since correlational analysis was used in studying the LFP-BOLD spatial relationship, we used the same analysis method when comparing their temporal relationship. 

Extracting all possible features from the electrophysiology signal and examining their relationship with the rsfMRI signal or exploring all other types of ways of comparing LFP and rsfMRI signals goes beyond the scope of the current study. However, to address the reviewer’s concern, we tried a couple of analysis methods suggested by the reviewer, and results remain persistent. Figure S14 shows the results from (A) the rank correlation and (B) z transformation prior to comparison. We added these new results to the revised manuscript.

Comment 3: The writing refers to the spatial extent of correlation with the LFP signal as "spatial variance." However, LFP was recorded from a very limited point and the variance in the correlation map does not necessarily reflect underlying electrophysiological spatial distributions (e.g. Yu et al. Nat Commun. 2023 Mar 24;14(1):1651.)

The reviewer accurately pointed out that in our paper, “spatial variance” refers to the spatial variance of BOLD correlates with the LFP signal. Our objective is to assess the extent to which this spatial variance, which is derived from the neural activity captured by LFP in the M1 or ACC, corresponds to the BOLD-derived spatial patterns from the same regions. We acknowledge that this spatial variance may differ from the spatial map obtained by multi-site electrophysiology recordings. Nevertheless, numerous studies have consistently reported a high spatial correspondence between BOLD- and electrophysiology-derived RSNs using various methodologies across different physiological states in both humans and animals. For instance, research employing electroencephalography (EEG) or electrocorticography (ECoG) in humans demonstrates that RSNs derived from the power of multiple-site electrophysiological signals exhibit similar spatial patterns to classic BOLD-derived RSNs such as the default-mode network (Hacker et al., 2017; Kucyi et al., 2018). These studies well agree with our findings. Notably, the reference paper cited by the reviewer studies brain-wide changes during transitions between awake and various sleep stages, which is quite different from the brain states examined in our study.

Major method problem:

Comment 4: Correlating LFP to fMRI is correlating two biological signals, with unknown but presumably not uniform distributions. However, correlating CC results from correlation maps is comparing uniform distributions. This is not a fair comparison, especially considering that the noise added is also uniform as it was created with the rand() function in MATLAB.

This is a good point. We examined the distributions of both LFP powers and fMRI signals. They both seem to follow a normal distribution. Below shows distributions of the two signals from a random scan. In addition, z transformation prior to comparison generated the same results (Fig. S14).

Author response image 1.

Exemplar distributions of A) the fMRI signal of M1, and B) HRF-convolved LFP power in M1.

Reviewer #1 (Recommendations For The Authors):

Comment 1: In the Discussion, a few more calcium imaging papers could be fruitfully discussed (e.g. Ma et al Resting-state hemodynamics are spatiotemporally coupled to synchronized and symmetric neural activity in excitatory neurons, PNAS 2016, or more recently Vafaii et al, Multimodal measures of spontaneous brain activity reveal both common and divergent patterns of cortical functional organization, Nat Comms 2024).

We appreciate this suggestion. We have added the following discussions to the revised manuscript: 

“These findings indicate the temporal information provided by gamma power can only explain a minor portion (approximately 35%) of the temporal variance in the BOLD time series, even after accounting for the noise effect, which is in line with the reported correlation value between the cerebral blood volume and fluctuations in GCaMP signal in head-fixed mice during periods of immobility (R = 0.63) (Ma et al., 2016).” 

“It is plausible that employing different features or comparison methods could yield a stronger BOLD-electrophysiology temporal relationship (Ma et al., 2016).”

“Furthermore, in a more recent study by Vafaii and colleagues, overlapping cortical networks were identified using both fMRI and calcium imaging modalities, suggesting that networks observable in fMRI studies exhibit corresponding neural activity spatial patterns (Vafaii et al., 2024).” 

“Furthermore, Vafaii et. al. revealed notable differences in functional connectivity strength measured by fMRI and calcium imaging, despite an overlapping spatial pattern of cortical networks identified by both modalities (Vafaii et al., 2024).”

Comment 2: Similarly when discussing the "invisible" populations, perhaps Uhlirova et al eLife 2016 should be mentioned as some types of inhibitory processes may also be less clearly observed in LFPs but rather strongly contribute to NVC.

We appreciate the suggestion. We added the following sentences to the revised manuscript. 

“Additionally, Uhlirova et al. conducted a study where they utilized optogenetic stimulation and two-photon imaging to investigate how the activation of different neuron types affects blood vessels in mice. They discovered that only the activation of inhibitory neurons led to vessel constriction, albeit with a negligible impact on LFP (Uhlirova et al., 2016).”

Reviewer #2 (Recommendations For The Authors):

Major problems with writing:

Comment 1: The authors need to review past work to better place their study in the context of the literature (some review articles: Lurie et al. Netw Neurosci. 2020 Feb 1;4(1):30-69. & Thompson et al. Neuroimage. 2018 Oct 15;180(Pt B):448-462.)

Here are some LFP and BOLD "resting state" papers focused on dynamic changes.

Many of these papers examine both spatial and temporal extents of correlations. Several of these papers use similar methods to the reviewed paper.

Also, many of these papers dispute the claim that correlations seen are

"electrophysiology invisible signal." Note that I am NOT saying that "electrophysiology invisible" correlations do not exist (it seems very likely some DO exist). However, the authors did not show that in the reviewed paper, and some of the correlations which they call an "electrophysiology invisible signal" probably would be visible if analyzed in a different manner.

Quite a few literature studies that the reviewer suggested were already included in the original manuscript. We have also added more literature studies to the revised manuscript. Again, we would like to emphasize that the novelty of our study centers on the discovery of the disparity in temporal and spatial relationships between resting-state electrophysiological and fMRI signals. See below our responses to individual literature studies listed.

In humans:

https://pubmed.ncbi.nlm.nih.gov/38082179/ Predicts by using models the paper under review does not use here.

The following discussion was added to the revised manuscript: 

“Some other comparison methods such as rank correlation and transformation prior to comparison were also tested and results remain persistent (Fig. S14). These findings align with the notion that, compared to nonlinear models, linear models offer superior predictive value for the rsfMRI signal using LFP data, as comprehensively illustrated in (Nozari et al., 2024) (also see Fig. S7). Importantly, in this study, the predictive powers (represented by R2) of various comparison methods tested all remain below 0.5 (Nozari et al., 2024), suggesting that while certain models may enhance the temporal relationship between LFP and BOLD signals, the improvement is likely modest.”

In nonhuman primates: https://pubmed.ncbi.nlm.nih.gov/34923136/ Most of the variance that could be creating resting state networks is in the <1 Hz band which the paper under review did not study

]We also examined infraslow LFP activity (< 1Hz) in our data. Consistent with the finding in the reference paper (Li et al., 2022), infraslow LFP power and the BOLD signal can derive consistent RSN spatial patterns (for M1, spatial correlation = 0.70), while the temporal correlation remains very low (temporal correlation = 0.08). These results and the reference paper were added to the revised manuscript.

https://pubmed.ncbi.nlm.nih.gov/28461461/ Compares actual spread of LFP vs. spread of BOLD instead of just correlation between LFP and BOLD.

The following sentence has been added to the revised manuscript.

“This high spatial correspondence between rsfMRI and LFP signals can even be found at the columnar level (Shi et al., 2017).”   

https://pubmed.ncbi.nlm.nih.gov/24048850/ Comparison of small (from LFP) to large (from BOLD) spatial correlations in the context of temporal correlations.

In this study, researchers compared neurophysiological maps and fMRI maps of the inferior temporal cortex in macaques in response to visual images. They observed that the spatial correlation increased as the neurophysiological maps got greater levels of spatial smoothing. This suggests that fMRI can capture large-scale spatial information, but it may be limited in capturing fine details. Although interesting, this paper did not study the electrophysiology-fMRI relationship at the resting state and hence is not very relevant to our study.

https://pubmed.ncbi.nlm.nih.gov/20439733/ Electrophysiology from a single site can correlate across nearly the entire cerebral cortex.

We have included the discussion of this paper in the original manuscript.

https://pubmed.ncbi.nlm.nih.gov/18465799/ The original dynamic BOLD and LFP work from 2008 by Shmuel and Leopold included spatiotemporal dynamics.

We have included the discussion of this paper in the original manuscript.

In rodents:

https://pubmed.ncbi.nlm.nih.gov/34296178/ Better electrophysiological correspondence was found using alternate methods the paper under review does not use.

This study investigates the electrophysiological correspondence in taskbased fMRI, while our study focused on resting state signals.

https://pubmed.ncbi.nlm.nih.gov/31785420/ Electrophysiological basis of co-activation patterns, similar comparisons to the paper under review.

We have included the discussion of this paper in the original manuscript.

https://pubmed.ncbi.nlm.nih.gov/29161352/ Cross-frequency coupling of LFP modulating the BOLD, perhaps more so than raw amplitudes.

This paper investigated the impact of AMPA microinjections in the VTA and found reduced ventral striatal functional connectivity, correlation between the delta band and BOLD signal, and phase–amplitude coupling of low-frequency LFP and highfrequency LFP, suggesting changes in low-frequency LFP might modulate the BOLD signal.

Consistent with our study, we also found that low-frequency LFP is negatively coupled with the BOLD signal, but we did not investigate changes in neurovascular coupling with disturbed neural activity using pharmacological methods, and hence, we did not discuss this paper in our study.

https://pubmed.ncbi.nlm.nih.gov/24071524/ This paper did the same kind of tests comparing LFP-BOLD correlations to BOLD-BOLD correlations as the paper under review.

This study examined the neural mechanism underpinning dynamic restingstate fMRI, revealing a spatiotemporal coupling of infra-slow neural activity with a quasiperiodic pattern (QPP). While our current investigation centered on stationary restingstate functional connectivity, we acknowledge that dynamic analysis will provide additional value for investigating the relationship between LFP and rsfMRI signals. This warrants more investigation in a future study. This point has been added to the revised manuscript.

https://pubmed.ncbi.nlm.nih.gov/24904325/ This paper found that different frequencies of electrophysiology (including ones not studied in the reviewed paper) contribute independently to the BOLD signal

This paper identified phase-amplitude coupling in rats anesthetized with isoflurane but not with dexmedetomidine, indicating that this coupling arises from a special type of neural activity pattern, burst-suppression, which was probably induced by high-dose isoflurane. They conjectured that high and low-frequency neural activities may independently or differentially influence the BOLD signal. Our study also examined the influence of various LFP frequency bands on the BOLD signal and found inversed LFP-BOLD relationship between low- and high-frequency LFP powers. We also added more results on the analysis of infraslow LFP signals. Regardless, since the reference study did not examine the spatial relationship of LFP and BOLD activities, we cannot comment on how it may provide insight into our results. 

https://pubmed.ncbi.nlm.nih.gov/26041826/ This paper found electrophysiological correlates within the BOLD signal when using BOLD analysis methods not used in the reviewed paper, and furthermore that some of these correlate with electrophysiological frequencies not studied in the reviewed paper (< 1 Hz).

We have added more results on the analysis of infraslow LFP signals and acknowledged the value of dynamic rsfMRI analysis in studies of BOLDelectrophysiology relationship.

I am not saying the authors need to use all these methods or even cite these papers. As I stated in their review, they merely need to (1) cite some of the most relevant for the proper context, the above list can maybe help (2) remove the claim of an "electrophysiology invisible signal" (3) use terms more commonly used in these papers for the extent of correlation with the electrode, other than "spatial variance."

We thank the reviewer again for providing a detailed list of reference studies. We have added the related discussion to the revised manuscript as described above.

Comment 2: The abstract entirely and much of the rest of the paper should be rewritten to be more reasonable. The authors would do well to review some of the past controversies in this area, e.g. Magri et al. J Neurosci. 2012 Jan 25;32(4):1395-407.

We have made significant revision to improve the writing of the paper. The reference paper has been added to the revised manuscript.

Comment 3: This should be re-written and the terminology used here should be chosen more carefully.

The writing of the manuscript has been improved with more careful choice of terminology.    

Major method problem:

Comment 4: At a minimum, the authors should be transforming the uniform distribution of CC results to Z or T values and using randn() instead of rand() in MATLAB.

Below is the figure illustrating the simulation results by transforming CC values to Z score. Results obtained remain consistent.

Author response image 2.

Minor problems:

Comment 5: "MR-510 compatible electrodes (MRCM16LP, NeuroNexus Inc)"

Details of this type of electrode are not readily available. But for studies like this one, further information on materials is critical as this determines the frequency coverage, which is not even across all LFP frequencies for all materials. Most commercially prepared electrodes cannot record <1Hz accurately, and this study includes at least 0.11Hz in some of its analysis.

The type of electrode used in our current study is a silicon-based micromachined probe. These probes are fabricated using photolithographic techniques to pattern thin layers of conductive materials onto a silicon substrate. This probe is capable of recording the LFP activity within a broad frequency range, starting from 0.1Hz . We added this information to the revised manuscript. 

Comment 6: Grounding to the cerebellum in theory would remove global conduction from the LFP but also global signal regression is done to the fMRI. Does the LFP-rsfMRI correlation change due to the regression or does only the rsfMRI-rsfMRI correlation change?

The results obtained with global signal regression were consistent with those obtained without it (see Figs. S4-S5), and therefore, we do not believe our results are affected by this preprocessing step. 

Comment 7. Avoid colloquial language like "on the other hand" etc.

We used more appropriate language in the revised manuscript.

References:

Bolt, T., Nomi, J.S., Bzdok, D., Salas, J.A., Chang, C., Thomas Yeo, B.T., Uddin, L.Q., Keilholz, S.D., 2022. A parsimonious description of global functional brain organization in three spatiotemporal patterns. Nat Neurosci 25, 1093-1103.

Cabral, J., Fernandes, F.F., Shemesh, N., 2023. Intrinsic macroscale oscillatory modes driving long range functional connectivity in female rat brains detected by ultrafast fMRI. Nat Commun 14, 375.

Hacker, C.D., Snyder, A.Z., Pahwa, M., Corbetta, M., Leuthardt, E.C., 2017. Frequencyspecific electrophysiologic correlates of resting state fMRI networks. Neuroimage 149, 446-457.

Kucyi, A., Schrouff, J., Bickel, S., Foster, B.L., Shine, J.M., Parvizi, J., 2018. Intracranial Electrophysiology Reveals Reproducible Intrinsic Functional Connectivity within Human Brain Networks. J Neurosci 38, 4230-4242.

Li, J.M., Acland, B.T., Brenner, A.S., Bentley, W.J., Snyder, L.H., 2022. Relationships between correlated spikes, oxygen and LFP in the resting-state primate. Neuroimage 247, 118728.

Ma, Y., Shaik, M.A., Kozberg, M.G., Kim, S.H., Portes, J.P., Timerman, D., Hillman, E.M., 2016. Resting-state hemodynamics are spatiotemporally coupled to synchronized and symmetric neural activity in excitatory neurons. Proc Natl Acad Sci U S A 113, E8463-E8471.

Ma, Z., Zhang, N., 2018. Temporal transitions of spontaneous brain activity. Elife 7.

Shi, Z., Wu, R., Yang, P.F., Wang, F., Wu, T.L., Mishra, A., Chen, L.M., Gore, J.C., 2017. High spatial correspondence at a columnar level between activation and resting state fMRI signals and local field potentials. Proc Natl Acad Sci U S A 114, 52535258.

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Author response:

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

In addition to our responses to reviewer suggestions below, a minor bug in the calculation of CAIS was brought to our attention by a reader of our preprint. We have corrected this bug and rerun analyses, whose results became slightly stronger as noise was removed. While we were doing that, someone pointed out to us that our equations were almost the same as Kullback-Leibler divergence, which explains why our metric performed so well. We have made the numerically trivial (see before vs. after image below) mathematical change to use Kullback-Leibler divergence instead, and now have a better story, with a solid basis in information theory, as to why CAIS works.

Author response image 1.

Unfortunately, we discovered a second bug that caused our PIC correction code to fail to perform the needed correction for phylogenetic confounding. The previously reported correlation between CAIS (or ENC) with body mass no longer survives PIC-correction. We have therefore removed this analysis from the manuscript. Our story now stands more on the theoretical basis of CAIS and ENC than on the post facto validation than it previously did. We now also present CAIS and ENC on a more equal footing. ENC results are slightly stronger, while CAIS has the complementary advantage of correcting for amino acid frequencies.

The work involved in these changes, as well as some of the responses to reviews below, justifies changing the second author into a co-first author, and adding an additional coauthor (Hanon McShea) who discovered the second bug.

Reviewer #1 (Public Review): 

In this manuscript, the authors propose a new codon adaptation metric, Codon Adaptation Index of Species (CAIS), which they present as an easily obtainable proxy for effective population size. To permit between-species comparisons, they control for both amino acid frequencies and genomic GC content, which distinguishes their approach from existing ones. Having confirmed that CAIS negatively correlates with vertebrate body mass, as would be expected if small-bodied species with larger effective populations experience more efficient selection on codon usage, they then examine the relationship between CAIS and intrinsic structural disorder in proteins. 

The idea of a robust species-level measure of codon adaptation is interesting. If CAIS is indeed a reliable proxy for the effectiveness of selection, it could be useful to analyze species without reliable life history- or mutation rate data (which will apply to many of the genomes becoming available in the near future). 

A key question is whether CAIS, in fact, measures adaptation at the codon level. Unfortunately, CAIS is only validated indirectly by confirming a negative correlation with body mass. As a result, the observations about structural disorder are difficult to evaluate. 

As discussed in the preamble above, we have replaced the body mass validation with a stronger theoretical basis in information theory.

A potential problem is that differences in GC between species are not independent of life history. Effective population size can drive compositional differences due to the effects of GC-biased gene conversion (gBGC). As noted by Galtier et al. (2018), genomic GC correlates negatively with body mass in mammals and birds. It would therefore be important to examine how gBGC might affect CAIS, and to what extent it could explain the relationship between CAIS and body mass. 

Suppose that gBGC drives an increase in GC that is most pronounced at 3rd codon positions in highrecombination regions in small-bodied species. In this case, could observed codon usage depart more strongly from expectations calculated from overall genomic GC in small vertebrates compared to large ones? The authors also report that correcting for local intergenic GC was unsuccessful, based on the lack of a significant negative relationship with body mass (Figure 3D). In principle, this could also be consistent with local GC providing a relatively more appropriate baseline in regions with high recombination rates. Considering these scenarios would clarify what exactly CAIS is capturing. 

Figure 3 (previously Supplementary Figures S5A and S5B) shows that CAIS is negligibly correlated with %GC (not robust to multiple comparisons correction), and ENC not at all. We believe this is evidence against the possibility brought up by the reviewer, i.e. that Ne might affect gBGC (and hence global %GC). This relationship, if present, could act as a confounding effect, but it is not present within our species dataset. 

Note that we expect our genomic-GC-based codon usage expectations to reflect unchecked gBGC in an average genomic region, independently of whether that species has high or low Ne. Our working model is that non-selective forces, include gBGC as well as conventional mutation biases, vary among species, and that they rather than selection determine each species’ genome-wide %GC. By correcting for genome-wide %GC, CAIS and ENC correct for both mutation bias and gBGC, in order to isolate the effects of selection.

This argument, based on an average genomic region, is vulnerable to gene-rich genomic regions having differentially higher recombination rates and hence GC-biased gene conversion. However, we do not see the expected positive correlation between |𝐥𝐨𝐜𝐚𝐥 𝐆𝐂 - global GC| and CAIS (see new Figure 5), again suggesting that gene conversion strength is not a confounding factor acting on CAIS.

Given claims about "exquisitely adapted species", the case for using CAIS as a measure of codon adaptation would also be stronger if a relationship with gene expression could be demonstrated. RSCU is expected to be higher in highly expressed genes. Is there any evidence that the equivalent GCcontrolled measure behaves similarly? 

Correlations with gene expression are outside the scope of the current work, which is focused on producing and exploiting a single value of codon adaptation per species. It is indeed possible that our general approach of using Kullback-Leibler divergence to correct for genomic %GC could be useful in future work investigating differences among genes.  

The manuscript is overall easy to follow, though some additional context may be helpful for the general reader. A more detailed discussion of how this work compares to the approach taken by Galtier et al. (2018), which accounted for GC content and gBGC when examining codon preferences, would be appropriate, for example. In addition, it would have been useful to mention past work that has attempted to explicitly quantify selection on codon usage. 

One key difference between our work and that of Galtier et al. 2018 is that our approach does not rely on identifying specific codon preferences as a function of species. Our approach might therefore be robust to scenarios where different genes have different codon preferences (see Gingold et al. 2014 https://doi.org/10.1016/j.cell.2014.08.011). At a high level, our results are in broad agreement with those of Galtier et al., 2018, who found that gBGC affected all animal species, regardless of Ne, and who like us, found that the degree of selection on codon usage depended on Ne.

Reviewer #2 (Public Review): 

Summary 

The goal of the authors in this study is to develop a more reliable approach for quantifying codon usage such that it is more comparable across species. Specifically, the authors wish to estimate the degree of adaptive codon usage, which is potentially a general proxy for the strength of selection at the molecular level. To this end, the authors created the Codon Adaptation Index for Species (CAIS) that controls for differences in amino acid usage and GC% across species. Using their new metric, the authors find a previously unobserved negative correlation between the overall adaptiveness of codon usage and body size across 118 vertebrates. As body size is negatively correlated with effective population size and thus the general strength of natural selection, the negative correlation between CAIS and body size is expected. The authors argue this was previously unobserved due to failures of other popular metrics such as Codon Adaptation Index (CAI) and the Effective Number of Codons (ENC) to adequately control for differences in amino acid usage and GC content across species. Most surprisingly, the authors also find a positive relationship between CAIS and the overall "disorderedness" of a species protein domains. As some of these results are unexpected, which is acknowledged by the authors, I think it would be particularly beneficial to work with some simulated datasets. I think CAIS has the potential to be a valuable tool for those interested in comparing codon adaptation across species in certain situations. However, I have certain theoretical concerns about CAIS as a direct proxy for the efficiency of selection $sN_e$ when the mutation bias changes across species.  

Strengths 

(1) I appreciate that the authors recognize the potential issues of comparing CAI when amino acid usage varies and correct for this in CAIS. I think this is sometimes an under-appreciated point in the codon usage literature, as CAI is a relative measure of codon usage bias (i.e. only considers synonyms). However, the strength of natural selection on codon usage can potentially vary across amino acids, such that comparing mean CAI between protein regions with different amino acid biases may result in spurious signals of statistical significance (see Cope et al. Biochemica et Biophysica Acta - Biomembranes 2018 for a clear example of this). 

We now cite Cope et al. as an example of how amino acid composition can act as a confounding factor.

(2) The authors present numerous analysis using both ENC and mean CAI as a comparison to CAIS, helping given a sense of how CAIS corrects for some of the issues with these other metrics. I also enjoyed that they examined the previously unobserved relationship between codon usage bias and body size, which has bugged me ever since I saw Kessler and Dean 2014. The result comparing protein disorder to CAIS was particularly interesting and unexpected. 

Unfortunately, our previous PIC correction code was buggy, and in fact the relationship with body size does not survive PIC correction (although it is strong prior to PIC correction). We have therefore removed it from the paper. However, the more novel result on protein disorder remains strong.

(3) The CAIS metric presented here is generally applicable to any species that has an annotated genome with protein-coding sequences. 

Weaknesses 

(1) The main weakness of this work is that it lacks simulated data to confirm that it works as expected. This would be particularly useful for assessing the relationship between CAIS and the overall effect of protein structure disorder, which the authors acknowledge is an unexpected result. I think simulations could also allow the authors to assess how their metric performs in situations where mutation bias and natural selection act in the same direction vs. opposite directions. Additionally, although I appreciate their comparisons to ENC and mean CAI, the lack of comparison to other popular codon metrics for calculating the overall adaptiveness of a genome (e.g. dos Reis et al.'s $S$ statistic, which is a function of tRNA Adaptation Index (tAI) and ENC) may be more appropriate. Even if results are similar to $S$, CAIS has a noted advantage that it doesn't require identifying tRNA gene copy numbers or abundances, which I think are generally less readily available than genomic GC% and protein-coding sequences. 

The main limitation of dos Reis’s test in our view is that, like the better versions of CAI, it requires comparable orthologs across species. See also the discussion below re the benefits of proteome-wide approach. We now also note the advantage of not needing tRNA gene copy numbers and abundances. 

Simulated datasets would be great, but we think it a nice addition rather than must-have, in particular because we are skeptical about whether our understanding of all relevant processes is good enough such that simulations would add much to our more heuristic argument along the lines of Figure 2. E.g. the complications of Gingold et al. 2014 cited above are pertinent, but incorporating them would make simulations quite involved. Instead, we now have a stronger theoretical justification for CAIS grounded in information theory. We have significantly expanded discussion of Figure 2 to give a clearer idea of the conceptual underpinnings of CAIS and ENC.

The authors mention the selection-mutation-drift equilibrium model, which underlies the basic ideas of this work (e.g. higher $N_e$ results in stronger selection on codon usage), but a more in-depth framing of CAIS in terms of this model is not given. I think this could be valuable, particularly in addressing the question "are we really estimating what we think we're estimating?" 

Let's take a closer look at the formulation for RSCUS. From here on out, subscripts will only be used to denote the codon and it will be assumed that we are only considering the case of $r = genome$ for some species $s$. 

\begin{align*} 

RSCUS_i &= \frac{O_i}{E_i} 

\end{align*} 

I think what the authors are attempting to do is "divide out" the effects of mutation bias (as given by $E_i$), such that only the effects of natural selection remain, i.e. deviations from the expected frequency based on mutation bias alone represent adaptive codon usage. Consider Gilchrist et al. MBE 2015, which says that the expected frequency of codon $i$ at selection-mutation-drift equilibrium in gene $g$ for an amino acid with $N_a$ synonymous codons is 

\begin{align} 

E_{i,g} &= \frac{e^{-\Delta M_i-\Delta\eta_i\phi_g}}{\sum_{j=1}^{N_a}e^{-\Delta M_j\Delta\eta_j\phi_g}} 

\end{align} 

where$\Delta M$ is the mutation bias, $\Delta\eta$ is the strength of selection scaled by the strength of drift, and $\phi_g$ is the gene expression level of gene $g$. In this case, $\Delta M$ and $\Delta\eta$ reflect the strength and direction of mutation bias and natural selection relative to a reference codon, for which $\Delta M_ref, \Delta\eta_ref = 0$. Assuming the selection-mutation-drift equilibrium model is generally adequate to model the true codon usage patterns in a genome (as I do and I think the authors do, too), the $E_{i,g}$ could be considered the expected observed frequency codon $i$ in gene $g$ $E[O_{i,g}]$. 

Let's re-write the $E_i = \frac{p_i}{\sum_{j=1}^{N_a}p_j}$ in the form of Gilchrist et al., such that it is a function of mutation bias $\Delta M$. For simplicity, we will consider just the two-codon case and assume the amino acid sequence is fixed. Assuming GC% is at equilibrium, the term $g_r$ and $1 - g_r$ can be written as 

\begin{align*} 

g_r &= \frac{\mu_{AT\rightarrow GC}}{\mu_{AT\rightarrow GC} + \mu_{GC\rightarrow AT}} \1 - g_r & = \frac{\mu_{GC\rightarrow AT}}{\mu_{AT\rightarrow GC} + \mu_{GC\rightarrow AT}}  \end{align*} 

where $\mu_{x\rightarrow y}$ is the mutation rate from nucleotides $x$ to $y$. As described in Gilchrist et al. MBE 2015 and Shah and Gilchrist PNAS 2011, the mutation bias $\Delta M_{NNA,NNG} = log(\frac{\mu_{AT\rightarrow GC}}{\mu_{GC\rightarrow AT}})$. This can be expressed in terms of the equilibrium GC content by recognizing that 

\begin{align*} 

\frac{g_r}{1-g_r} &= \frac{\mu_{AT\rightarrow GC}}{\mu_{GC\rightarrow AT}} \\implies \frac{g_r}{1-g_r} &= e^{\Delta M} 

\end{align*} 

As we are assuming the amino acid sequence is fixed, the probability of observing a synonymous codon $i$ at an amino acid becomes just a Bernoulli process. 

\begin{align*} 

p_i &= g_r^x(1-g_r)^{(1-x)} 

\end{align*} 

If we do this, then 

\begin{align} 

E_{NNA} &= \frac{p_{NNA}}{p_{NNA} + p_{NNG}} \ &= \frac{1-g_r}{g_r + (1-g_r)} \ &=

\frac{1}{\frac{g_r}{1-g_r} + 1} \ &= \frac{1}{e^{\Delta M} + 1} \ & = \frac{e^{-\Delta M}}{1 + e^{-\Delta M}} 

\end{align} 

Recall that in the Gilchrist et al. framework, the reference codon has $\Delta M_{NNG,NNG} = 0 \implies e^{-\Delta M_{NNG,NNG}} = 1$. Thus, we have recovered the Gilchrist et al. model from the formulation of $E_i$ under the assumption that natural selection has no impact on codon usage and codon NNG is the pre-defined reference codon. To see this, plug in 0 for $\Delta\eta$ in equation (1). 

We can then calculate the expected RSCUS using equation (1) (using notation $E[O_i]$) and equation (6) for the two codon case. For simplicity assume, we are only considering a gene of average expression (defined as $\phi_g = 1$). 

Assume in this case that NNG is the reference codon ($\Delta M_{NNG},\Delta\eta_{NNG} = 0$). 

\begin{align} 

E[RSCUS_{NNA}] &= \frac{E[O_{NNA}]}{E_{NNA}} \ &= \frac{e^{-\Delta\eta_{NNA}}(e^{-\Delta

M_{NNA}}+e^{-\Delta M_{NNG}})}{e^{-\Delta M_{NNA}-\Delta\eta_{NNA}} + e^{-\Delta M_{NNG}\Delta\eta_{NNG}}} \ & = \frac{e^{-\Delta M_{NNA} - \Delta\eta_{NNA}} + e^{-\Delta M_{NNG} -

\Delta\eta_{NNA}}}{e^{-\Delta M_{NNA} - \Delta\eta_{NNA}} + e^{-\Delta M_{NNG} -

\Delta\eta_{NNG}}} \ &= \frac{e^{-\Delta M_{NNA} - \Delta\eta_{NNA}} + e^{- \Delta\eta_{NNA}}}{e^{\Delta M_{NNA} - \Delta\eta_{NNA}} + 1} 

\end{align} 

This shows that the expected value of RSCUS for a two-codon amino acid is expected to increase as the strength of selection $\Delta\eta$ increases, which is desired. Note that $\Delta\eta$ in Gilchrist et al. is formulated in terms of selection *against* a codon relative to the reference, such that a negative value represents that a codon is favored relative to the reference. If $\Delta\eta = 0$ (i.e. selection does not favor either codon), then $E[RSCUS] = 1$. Also note that the expected RSCUS does not remain independent of the mutation bias. This means that even if $sN_e$ (i.e. the strength of natural selection) does not change between species, changes to the strength and direction of mutation bias across species could impact RSCUS. Assuming my math is right, I think one needs to be cautious when interpreting CAIS as representative of the differences in the efficiency of selection across species except under very particular circumstances. One such case could be when it is known that mutation bias varies little across the species of interest. Looking at the species used in this manuscript, most of them have a GC content ranging around 0.41, so I suspect their results are okay. 

Although I have not done so, I am sure this could be extended to the 4 and 6 codon amino acids. 

We thank Reviewer 2 for explicitly laying out the math that was implicit in our Figures 1 and 2. While we keep our more heuristic presentation, our revised manuscript now more clearly acknowledges that the per-site codon adaptation bias depicted in Figure 1 has limited sensitivity to s*Ne. The reason that we believe our approach worked despite this, is that we think the phenomenon is driven by what is shown in Figure 2. I.e., where Ne makes a difference is by determining the proteome-wide fraction of codons subject to significant codon adaptation, rather than by determining the strength of codon adaptation at any particular site or gene. We have made multiple changes to the texts to make this point clearer.

Another minor weakness of this work is that although the method is generally applicable to any species with an annotated genome and the code is publicly available, the code itself contains hard-coded values for GC% and amino acid frequencies across the 118 vertebrates. The lack of a more flexible tool may make it difficult for less computationally-experienced researchers to take advantage of this method. 

Genome-wide %GC values are hard-coded because they were taken from the previous study of James et al. (2023) https://doi.org/10.1093/molbev/msad073. As summarized in the manuscript, genome-wide %GC was a byproduct of a scan of all six reading frames across genic and intergenic sequences available from NCBI with access dates between May and July 2019. The more complicated code used to calculate the intergenic %GC, and the code used to calculate amino acid frequencies is located at https://github.com/MaselLab/CodonAdaptation-Index-of-Species. Luckily, someone else just wrote a simpler end to end pipeline for us, on the basis of our preprint. We now note this in the Acknowledgements, and link to it: https://github.com/gavinmdouglas/handy_pop_gen/blob/main/CAIS.py.

Author response:

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

Reviewer #1 (Public Review):

Summary: The global decline of amphibians is primarily attributed to deadly disease outbreaks caused by the chytrid fungus, Batrachochytrium dendrobatidis (Bd). It is unclear whether and how skin-resident immune cells defend against Bd. Although it is well known that mammalian mast cells are crucial immune sentinels in the skin and play a pivotal role in immune recognition of pathogens and orchestrating subsequent immune responses, the roles of amphibian mast cells during Bd infections is largely unknown. The current study developed a novel way to enrich X. laevis skin mast cells by injecting the skin with recombinant stem cell factor (SCF), a KIT ligand required for mast cell differentiation and survival. The investigators found an enrichment of skin mast cells provides X. laevis substantial protection against Bd and mitigates the inflammation-related skin damage resulting from Bd infection. Additionally, the augmentation of mast cells leads to increased mucin content within cutaneous mucus glands and shields frogs from the alterations to their skin microbiomes caused by Bd. 

Strengths: This study underscores the significance of amphibian skin-resident immune cells in defenses against Bd and introduces a novel approach to examining interactions between amphibian hosts and fungal pathogens. 

We thank the reviewer for recognizing the significance and the novelty of our work.

Weaknesses: The main weakness of the study is lack of functional analysis of X. laevis mast cells. Upon activation, mast cells have the characteristic feature of degranulation to release histamine, serotonin, proteases, cytokines, and chemokines, etc. The study should determine whether X. laevis mast cells can be degranulated by two commonly used mast cell activators IgE and compound 48/80 for IgE-dependent and independent pathway. This can be easily done in vitro. It is also important to assess whether in vivo these mast cells are degranulated upon Bd infection using avidin staining to visualize vesicle releases from mast cells. Figure 3 only showed rSCF injection caused an increase in mast cells in naïve skin. They need to present whether Bd infection can induce mast cell increase and rSCF injection under Bd infection causes a mast cell increase in the skin. In addition, it is unclear how the enrichment of mast cells provides the protection against Bd infection and alternations to skin microbiomes after infection. It is important to determine whether skin mast cell release any contents mentioned above. 

We would like to thank the reviewer for taking the time to review our work and providing us with valuable feedback.

Please note, that as indicated in our previous rebuttal to reviewers, amphibians do not possess the IgE antibody isotype1.

To our knowledge, there are no published works describing the approaches used in studying mammalian mast cell degranulation towards examining amphibian mast cells. While there are commercially available kits and reagents for examining mammalian mast cell granule content, most of these do not cross-react with amphibian counterparts. This is especially true of cytokines and chemokines, which diverged quickly with evolution and thus do not share substantial protein sequence identity across species as diverged as frogs and mammals. We would also like to highlight the fact that several studies suggest that amphibian mast cells lack histamine2, 3, 4, 5 and serotonin2, 6. While following up on these findings would be possible, we would like to respectfully emphasize that adopting approaches used in mammalian research to comparative immunology work is not always straightforward.

As we highlight in our manuscript, frog mast cells upregulate their expression of interleukin-4 (IL4), a hallmark cytokine associated with mammalian mast cells7. The additional findings presented in our revised manuscript indicate that mast cells respond to Bd by upregulating IL4 expression in vitro and in vivo. Together, this suggests that IL4 may be a central means by which frog mast cells confer protection against Bd, by counteracting Bd-elicited inflammation, including minimizing neutrophil infiltration, maintaining skin integrity, and promoting cutaneous mucus production. Please find that these additional results are presented in Figure 8 and are described in the results and discussion sections of our revised manuscript.

Our attempts to elicit degranulation of frog mast cells using compound 48/80 have so far not been successful. This may reflect technical issues with assays optimized for mammalian mast cells or biological difference between frog and mammalian mast cells, such as species differences in mas-related G-protein coupled receptors, through which compound 48/80 acts8. We will continue to explore means to study frog mast cell degranulation both in vitro and in vivo but also respectfully point out that while degranulation is a feature commonly associated with mammalian mast cells, this is not the only means by which the mammalian mast cells confer their immunological effects. Indeed, our studies suggest that frog mast cell IL4 production may be a key means by which these cells offer anti-Bd protection.

Please note that we successfully adopted an avidin staining approach to visualize mast cell heparin content in vitro and to evaluate cutaneous mast cell numbers in vivo in control and mast cell-enriched, mock- and Bd-infected animals. This additional work is depicted in Figure 4 and addressed in the results and discussion sections of our revised manuscript.

Reviewer #2 (Public Review):

Summary: In this study, Hauser et al investigate the role of amphibian (Xenopus laevis) mast cells in cutaneous immune responses to the ecologically important pathogen Batrachochytrium dendrobatidis (Bd) using novel methods of in vitro differentiation of bone marrow-derived mast cells and in vivo expansion of skin mast cell populations. They find that bone marrow-derived myeloid precursors cultured in the presence of recombinant X. laevis Stem Cell Factor (rSCF) differentiate into cells that display hallmark characteristics of mast cells. They inject their novel (r)SCF reagent in the skin of X. laevis and find that this stimulates expansion of cutaneous mast cell populations in vivo. They then apply this model of cutaneous mast cell expansion in the setting of Bd infection and find that mast cell expansion attenuates skin burden of Bd zoospores and pathologic features including epithelial thickness and improves protective mucus production and transcriptional markers of barrier function. Utilizing their prior expertise with expanding neutrophil populations in X. laevis, the authors compare mast cell expansion using (r)SCF to neutrophil expansion using recombinant colony stimulating factor 3 (rCSF3) and find that neutrophil expansion in Bd infection leads to greater burden of zoospores and worse skin pathology. Combining these two observations, they demonstrate that mast cell expansion using rSCF attenuates cutaneous neutrophilic infiltration. They further show that mast cell expansion correlates to cutaneous IL-4 expression, and that treatment with exogenous rIL-4 reduces neutrophilic infiltration and restores markers of epithelial health, offering a mechanism by which mast cell expansion protects from Bd infection. 

Strengths: The authors report a novel method of expanding amphibian mast cells utilizing their custom-made rSCF reagent. They rigorously characterize expanded mast cells in vitro and in vivo using histologic, morphologic, transcriptional, and functional assays. This establishes solid footing with which to then study the role of rSCF-stimulated mast cell expansion in the Bd infection model. This appears to be the first demonstration of exogenous use of rSCF in amphibians to expand mast cell populations and may set a foundation for future mechanistic studies of mast cells in the X. laevis model organism. Building on prior work, they are able to contrast mast cell expansion with their neutrophil expansion model, allowing them to infer a mechanistic link between mast cell expansion and IL-4 production and subsequent suppression of neutrophil infiltration and cutaneous dysbiosis. 

We thank the reviewer for recognizing the rigorousness and utility of the studies presented in our manuscript.

Weaknesses: The main weaknesses derive from technical limitations inherent to the Xenopus model at this time. For example, in mice a mechanistic study would be expected to use IL-4 knockouts, preferably mast cell-specific, to prove the link between mast cell expansion and IL-4 production being necessary and sufficient to suppress neutrophils. However, the novel reagents in this manuscript present a compelling technical advance and a step forward in the tools available to study amphibian biology. 

We agree with the reviewer that an IL4 knock-out animal model would be a great way to support our findings. Unfortunately, working with a non-mammalian model such as X. laevis poses limitations that include lack of knock-out lines for immunology research. Moreover, as mentioned in our manuscript, we do not believe that IL4 is the sole mast cell-produced component responsible for the conferred antifungal protection. We thank the reviewer for acknowledging the limitations of our model system and recognizing the novelty, technical advances, and merits of the work presented in our manuscript.

In addition to their discussion, one open question from the revised manuscript is how a single treatment with rSCF leads to a peak in mast cell numbers and then decline to baseline in mock-infected frogs, while Bd infection either sustains rSCF-boosted mast cells or leads to steady mast cell increase over time in control-treated frogs. Whether this is mediated by endogenous SCF or some other factor remains unexplored.

This is an interesting question that we hope to explore in future studies. We did not see significant differences in skin SCF gene expression at 21 days post Bd infection. This does not rule out the possibility that the observed Bd-mediated effects to frog skin mast cell composition are not due to changes in skin SCF gene expression at earlier infection times, alone or in combination with other host or pathogen derived factors. We know that other factors are responsible for homing/retention of antimicrobial and immunosuppressive granulocyte subsets within frog skin9 and we postulate that some of these may be distinct mast cell types. Additionally, Bd is known to produce a myriad of immunomodulatory factors10, which may well also directly affect frog skin mast cell composition. Mammalian mast cells are heterogenous and are homed or recruited into tissues by an extensive array of host as well as microbiome-derived components11, 12. Undoubtedly, the frog skin mast cell composition is likewise complex, dynamic, and contingent on a plethora of host, cutaneous microbial flora- and in this case also Bd-produced factors.

References

(1) Flajnik, M.F. A cold-blooded view of adaptive immunity. Nat Rev Immunol 18, 438-453 (2018).

(2) Mulero, I., Sepulcre, M.P., Meseguer, J., Garcia-Ayala, A. & Mulero, V. Histamine is stored in mast cells of most evolutionarily advanced fish and regulates the fish inflammatory response. Proc Natl Acad Sci U S A 104, 19434-19439 (2007).

(3) Reite, O.B. A phylogenetical approach to the functional significance of tissue mast cell histamine. Nature 206, 1334-1336 (1965).

(4) Reite, O.B. Comparative physiology of histamine. Physiol Rev 52, 778-819 (1972).

(5) Takaya, K., Fujita, T. & Endo, K. Mast cells free of histamine in Rana catasbiana. Nature 215, 776-777 (1967).

(6) Galli, S.J. New insights into "the riddle of the mast cells": microenvironmental regulation of mast cell development and phenotypic heterogeneity. Lab Invest 62, 5-33 (1990).

(7) Babina, M., Guhl, S., Artuc, M. & Zuberbier, T. IL-4 and human skin mast cells revisited: reinforcement of a pro-allergic phenotype upon prolonged exposure. Archives of dermatological research 308, 665-670 (2016).

(8) Hermans, M.A.W. et al. Human Mast Cell Line HMC1 Expresses Functional Mas-Related G-Protein Coupled Receptor 2. Front Immunol 12, 625284 (2021).

(9) Hauser, K. et al. Discovery of granulocyte-lineage cells in the skin of the amphibian Xenopus laevis. FACETS 5, 571 (2020).

(10) Rollins-Smith, L.A. & Le Sage, E.H. Batrachochytrium fungi: stealth invaders in amphibian skin. Curr Opin Microbiol 61, 124-132 (2021).

(11) Halova, I., Draberova, L. & Draber, P. Mast cell chemotaxis - chemoattractants and signaling pathways. Front Immunol 3, 119 (2012).

(12) West, P.W. & Bulfone-Paus, S. Mast cell tissue heterogeneity and specificity of immune cell recruitment. Front Immunol 13, 932090 (2022).

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

Reviewer #1 (Public Review):

Summary:

The global decline of amphibians is primarily attributed to deadly disease outbreaks caused by the chytrid fungus, Batrachochytrium dendrobatidis (Bd). It is unclear whether and how skin-resident immune cells defend against Bd. Although it is well known that mammalian mast cells are crucial immune sentinels in the skin and play a pivotal role in the immune recognition of pathogens and orchestrating subsequent immune responses, the roles of amphibian mast cells during Bd infections are largely unknown. The current study developed a novel way to enrich X. laevis skin mast cells by injecting the skin with recombinant stem cell factor (SCF), a KIT ligand required for mast cell differentiation and survival. The investigators found an enrichment of skin mast cells provides X. laevis substantial protection against Bd and mitigates the inflammation-related skin damage resulting from Bd infection. Additionally, the augmentation of mast cells leads to increased mucin content within cutaneous mucus glands and shields frogs from the alterations to their skin microbiomes caused by Bd.

Strengths:

This study underscores the significance of amphibian skin-resident immune cells in defenses against Bd and introduces a novel approach to examining interactions between amphibian hosts and fungal pathogens. 

We thank the reviewer for acknowledging the novelty and importance of the work presented in our manuscript.

Weaknesses:

The main weakness of the study is the lack of functional analysis of X. laevis mast cells. Upon activation, mast cells have the characteristic feature of degranulation to release histamine, serotonin, proteases, cytokines, and chemokines, etc. The study should determine whether X. laevis mast cells can be degranulated by two commonly used mast cell activators IgE and compound 48/80 for IgE-dependent and independent pathways. This can be easily done in vitro. It is also important to assess whether in vivo these mast cells are degranulated upon Bd infection using avidin staining to visualize vesicle releases from mast cells. Figure 3 only showed rSCF injection caused an increase in mast cells in naïve skin. They need to present whether Bd infection can induce mast cell increase and rSCF injection under Bd infection causes a mast cell increase in the skin. In addition, it is unclear how the enrichment of mast cells provides protection against Bd infection and alternations to skin microbiomes after infection. It is important to determine whether skin mast cells release any contents mentioned above. 

We would like to thank the reviewer for taking the time to review our work and providing us with valuable feedback. We feel that we have successfully incorporated the reviewer’s suggestions into our revised manuscript, thereby improving this work.

Please note that amphibians do not possess the IgE antibody isotype1.

To our knowledge there have been no published work assimilating approaches used when studying mammalian mast cell degranulation towards examining amphibian mast cells. While there are commercially available kits and reagents for examining mammalian mast cell granule content, most of these reagents do not cross-react with amphibian counterparts. This is especially true of cytokines and chemokines, which diverged quickly with evolution and thus do not share substantial protein sequence identity across species as diverged as frogs and mammals. Additionally, several studies suggest that amphibian mast cells lack histamine2, 3, 4, 5 and serotonin2, 6. Respectfully, while following up on these findings is possible, we would not consider adopting approaches used in mammalian research to comparative immunology work as easy.

As noted in our manuscript, frog mast cells upregulate their expression of interleukin-4 (IL4), which is a hallmark cytokine associated with mammalian mast cells7. The additional findings, presented in our revised manuscript indicate that mast cells respond to Bd by upregulating IL4 expression in vitro and in vivo. In turn, our work indicates that IL4 may be a central means by which frog mast cells confer protection against Bd, by counteracting Bd-elicited inflammation, including minimizing neutrophil infiltration, maintaining skin integrity, and promoting mucus production by skin mucus glands. Please find that these additional findings are presented in Figure 8 of our revised manuscript and are described in the results and discussion sections of the paper.

Our attempts to elicit degranulation of frog mast cells using compound 48/80 have so far not been successful. This may reflect technical issues with assays optimized for mammalian mast cells or biological difference between frog and mammalian mast cells, such as species differences in mas-related G-protein coupled receptors, through which compound 48/80 acts8. We will continue explore means to study frog mast cell degranulation both in vitro and in vivo but would also like to respectfully point out that while mast cell degranulation is a feature most associated with mammalian mast cells, this is not the only means by which the mammalian mast cells confer their immunological effects. Indeed, our additional studies suggest that mast cell IL4 production may be a key means by which these cells offer anti-Bd protection.

Please find that we have adopted an avidin-staining approach to visualize mast cell heparin content in vitro and to evaluate mast cell numbers in vivo in the skins of control and mast cell-enriched, mock- and Bd-infected animals. This additional work is depicted in Figure 4 of our revised manuscript and addressed in the results and discussion sections of our revised paper.

Reviewer #2 (Public Review):

Summary:

In this study, Hauser et al investigate the role of amphibian (Xenopus laevis) mast cells in cutaneous immune responses to the ecologically important pathogen Batrachochytrium dendrobatidis (Bd) using novel methods of in vitro differentiation of bone marrow-derived mast cells and in vivo expansion of skin mast cell populations. They find that bone marrow-derived myeloid precursors cultured in the presence of recombinant X. laevis Stem Cell Factor (rSCF) differentiate into cells that display hallmark characteristics of mast cells. They inject their novel (r)SCF reagent into the skin of X. laevis and find that this stimulates the expansion of cutaneous mast cell populations in vivo. They then apply this model of cutaneous mast cell expansion in the setting of Bd infection and find that mast cell expansion attenuates the skin burden of Bd zoospores and pathologic features including epithelial thickness and improves protective mucus production and transcriptional markers of barrier function. Utilizing their prior expertise with expanding neutrophil populations in X. laevis, the authors compare mast cell expansion using (r)SCF to neutrophil expansion using recombinant colony-stimulating factor 3 (rCSF3) and find that neutrophil expansion in Bd infection leads to greater burden of zoospores and worse skin pathology. 

Strengths:

The authors report a novel method of expanding amphibian mast cells utilizing their custom-made rSCF reagent. They rigorously characterize expanded mast cells in vitro and in vivo using histologic, morphologic, transcriptional, and functional assays. This establishes solid footing with which to then study the role of rSCF-stimulated mast cell expansion in the Bd infection model. This appears to be the first demonstration of the exogenous use of rSCF in amphibians to expand mast cell populations and may set a foundation for future mechanistic studies of mast cells in the X. laevis model organism. 

We thank the reviewer for recognizing the breadth and extent of the undertaking that culminated in this manuscript. Indeed, this manuscript would not have been possible without considerable reagent development and adaptation of techniques that had previously not been used for amphibian immunity research. In line with the reviewer’s sentiment, to our knowledge this is the first report of using molecular approaches to augment amphibian mast cells, which we hope will pave the way for new areas of research within the fields of comparative immunology and amphibian disease biology.

Weaknesses:

The conclusions regarding the role of mast cell expansion in controlling Bd infection would be stronger with a more rigorous evaluation of the model, as there are some key gaps and remaining questions regarding the data. For example: 

(1) Granulocyte expansion is carefully quantified in the initial time courses of rSCF and rCSF3 injections, but similar quantification is not provided in the disease models (Figures 3E, 4G, 5D-G). A key implication of the opposing effects of mast cell vs neutrophil expansion is that mast cells may suppress neutrophil recruitment or function. Alternatively, mast cells also express notable levels of csfr3 (Figure 2) and previous work from this group (Hauser et al, Facets 2020) showed rG-CSF-stimulated peritoneal granulocytes express mast cell markers including kit and tpsab1, raising the question of what effect rCSF3 might have on mast cell populations in the skin. Considering these points, it would be helpful if both mast cells and neutrophils were quantified histologically (based on Figure 1, they can be readily distinguished by SE or Giemsa stain) in the Bd infection models. 

We thank the reviewer for this insightful suggestion. Please find that we successfully adopted an in situ hybridization approach to evaluate neutrophil numbers in the skins of control and mast cell-enriched, mock- and Bd-infected animals based on expression of the neutrophil marker, myeloperoxidase (MPO9).  Please find these results are presented in Figures 6 and 8 of our revised manuscript and addressed in the appropriate sections of our revised paper.

Our findings suggest that rSCF administration results in the accumulation of mast cells that are polarized such, that they ablate the inflammatory response elicited by Bd infection, such as through mechanisms like IL4 production. Mammalian mast cells, including peritonea-resident mast cells, express csf3r10, 11. For this reason, we used MPO expression to visualize neutrophil skin infiltration in Figures 6 and 8 of our revised work. While the X. laevis animal model does not permit nearly the degree of immune cell resolution afforded by mammalian animal models, we do know that the adult X. laevis peritonea contain a myriad of immune cell subsets. We anticipate that the high kit expression reported by Hauser et al., 2020 in the rCSF3-recruited peritoneal leukocytes reflects the presence of mast cells therein.

Please find that we have used avidin-staining and MPO in situ hybridization to respectively visualize and enumerate mast cells and neutrophils in the skin of control and mast cell-enriched, mock- and Bd-infected animals. Indeed, our results show interesting, experimental condition-dependent changes in both the skin neutrophil and mast cell numbers. The results of these additional studies are presented in Figures 4, 6 and 8 of the revised manuscript and addressed in the results and discussions sections of our revised paper.

(2) Epithelial thickness and inflammation in Bd infection are reported to be reduced by rSCF treatment (Figure 3E, 5A-B) or increased by rCSF3 treatment (Figure 4G) but quantification of these critical readouts is not shown.

We thank the reviewer for this suggestion. We scored epithelial thickness under the distinct conditions described in our manuscript and presented the quantified data in Figures 5 and 8 of the revised paper.

(3) Critical time points in the Bd model are incompletely characterized. Mast cell expansion decreases zoospore burden at 21 dpi, while there is no difference at 7 dpi (Figure 3E). Conversely, neutrophil expansion increases zoospore burden at 7 dpi, but no corresponding 21 dpi data is shown for comparison (Figure 4G). Microbiota analysis is performed at a third time point,10 dpi (Figure 5D-G), making it difficult to compare with the data from the 7 dpi and 21 dpi time points. Reporting consistent readouts at these three time points is important to draw solid conclusions about the relationship of mast cell expansion to Bd infection and shifts in microbiota.

We thank reviewer for noting this discrepancy. Please find that we have repeated our mast cell-enrichment, Bd-challenge studies, examining days 10 and 21 post infection. Our new findings indicate that compared to control animals, mast cell-enrichment does result in significant reduction in Bd loads at both 10 and 21 dpi. The difference in Bd loads between r-ctrl and rSCF-treated animals at 10 dpi corroborates the other parameters that are altered between the two treatment groups at this experimental time point.

Our question regarding the roles of inflammatory granulocytes/neutrophils during Bd infections was that of ‘how’ rather ‘when’ these cells affect Bd infections.  Thus, and because the central focus of this work was mast cells and not other granulocyte subsets; when we saw that rCSF3-recruited granulocytes adversely affect Bd infections at 7 days, we did not pursue the kinetics of these observations further. We plan to explore the roles of inflammatory mediators and immune cell subsets during the course of Bd infections but feel that these future studies are more peripheral to the central thesis of the present manuscript regarding the roles of frog mast cells during Bd infections.

(4) Although the effect of rSCF treatment on Bd zoospores is significant at 21 dpi (Figure 3E), bacterial microbiota changes at 21 dpi are not (Figure S3B-C). This discrepancy, how it relates to the bacterial microbiota changes at 10 dpi, and why 7, 10, and 21 dpi time points were chosen for these different readouts (Figure 5F-G), is not discussed.

Please find that our additional studies indicate that compared to control animals, frog skin mast cell-enrichment results in significant reduction in Bd loads at 10 dpi. This corroborate our other findings including the observation that at 10 dpi, control animals exhibit reduced microbial richness whereas mast cell-enriched frogs were protected from this disruption of their microbiome. The amphibian microbiome serves as a major barrier to these fungal infections12 and we anticipate that Bd-mediated disruption of microbial richness facilitates host skin colonization by this pathogen. In turn, we anticipate that frog mast cells are conferring the observed anti-Bd protection in part by preventing microbial disassembly and thus interfering with optimal Bd colonization and growth on frog skins. Please find that we acknowledge and discuss these notions in our revised manuscript.

(5) The time course of rSCF or rCSF3 treatments relative to Bd infection in the experiments is not clear. Were the treatments given 12 hours prior to the final analysis point to maximize the effect? For example, in Figure 3E, were rSCF injections given at 6.5 dpi and 20.5 dpi? Or were treatments administered on day 0 of the infection model? If the latter, how do the authors explain the effects at 7 dpi or 21 dpi given mast cell and neutrophil numbers return to baseline within 24 hours after rSCF or rCSF3 treatment, respectively?

Please find that in our revised manuscript, we underlined the kinetics of our animal treatments and Bd-infections. In brief, for mast cell-enrichment, animals were injected with r-ctrl or rSCF, challenged 12 hours later with Bd and examined after 10 (per reviewers’ suggestions) and 21 days of infection. For neutrophil enrichment, animals were injected with r-ctrl or rCSF3, challenged 12 hours later with Bd and examined after 7 days of infection.

The title of the manuscript may be mildly overstated. Although Bd infection can indeed be deadly, mortality was not a readout in this study, and it is not clear from the data reported that expanding skin mast cells would ultimately prevent progression to death in Bd infections.

We acknowledge this point. The revised manuscript will be titled: “Amphibian mast cells: barriers to chytrid fungus infections”.

Reviewer #3 (Public Review):

Summary:

Hauser et al. provide an exceptional study describing the role of resident mast cells in amphibian epidermis that produce anti-inflammatory cytokines that prevent Batrachochytrium dendrobatidis (Bd) infection from causing harmful inflammation, and also protect frogs from changes in skin microbiomes and loss of mucin in glands and loss of mucus integrity that otherwise cause changes to their skin microbiomes. Neutrophils, in contrast, were not protective against Bd infection. Beyond the beautiful cytology and transcriptional profiling, the authors utilized elegant cell enrichment experiments to enrich mast cells by recombinant stem cell factor, or to enrich neutrophils by recombinant colony-stimulating factor-3, and examined respective infection outcomes in Xenopus.

Strengths:

Through the use of recombinant IL4, the authors were able to test and eliminate the hypothesis that mast cell production of IL4 was the mechanism of host protection from Bd infection. Instead, impacts on the mucus glands and interaction with the skin microbiome are implicated as the protective mechanism. These results will press disease ecologists to examine the relative importance of this immune defense among species, the influence of mast cells on the skin microbiome and mucosal function, and open the potential for modulating mucosal defense.

We thank the reviewer for recognizing the utility of the work presented in our manuscript.

Weaknesses:

A reduction of bacterial diversity upon infection, as described at the end of the results section, may not always be an "adverse effect," particularly given that anti-Bd function of the microbiome increased. Some authors (see Letourneau et al. 2022 ISME, or Woodhams et al. 2023 DCI) consider these short-term alterations as encoding ecological memory, such that continued exposure to a pathogen would encounter an enriched microbial defense. Regardless, mast cell-initiated protection of the mucus layer may negate the need for this microbial memory defense.

We thank the reviewer their insightful comment. We have revised our discussion to include this notion.

While the description of the mast cell location in the epidermal skin layer in amphibians is novel, it is not known how representative these results are across species ranging in chytridiomycosis susceptibility. No management applications are provided such as methods to increase this defense without the use of recombinant stem cell factor, and more discussion is needed on how the mast cell component (abundance, distribution in the skin) of the epidermis develops or is regulated.

We thank the reviewer for this suggestion. Please find that we have added a paragraph to our revised manuscripts to address possible source(s) of skin mast cells and a statement acknowledging that greater understanding of mast cell biology across distinct amphibian species may be used to develop future strategies for management of amphibian diseases.

We are very thankful to the reviewer for this excellent suggestion but would like to point out that the work presented in our manuscript was driven by comparative immunology questions more than by conservation biology. As such and considering just how little is known about mast cells outside of mammals; we chose not to speculate too much into possible utilities of altering amphibian skin mast cell composition and instead to focus our discussion on the immediate takeaways of the work presented by our paper.

References

(1) Flajnik, M.F. A cold-blooded view of adaptive immunity. Nat Rev Immunol 18, 438-453 (2018).

(2) Mulero, I., Sepulcre, M.P., Meseguer, J., Garcia-Ayala, A. & Mulero, V. Histamine is stored in mast cells of most evolutionarily advanced fish and regulates the fish inflammatory response. Proc Natl Acad Sci U S A 104, 19434-19439 (2007).

(3) Reite, O.B. A phylogenetical approach to the functional significance of tissue mast cell histamine. Nature 206, 1334-1336 (1965).

(4) Reite, O.B. Comparative physiology of histamine. Physiol Rev 52, 778-819 (1972).

(5) Takaya, K., Fujita, T. & Endo, K. Mast cells free of histamine in Rana catasbiana. Nature 215, 776-777 (1967).

(6) Galli, S.J. New insights into "the riddle of the mast cells": microenvironmental regulation of mast cell development and phenotypic heterogeneity. Lab Invest 62, 5-33 (1990).

(7) Babina, M., Guhl, S., Artuc, M. & Zuberbier, T. IL-4 and human skin mast cells revisited: reinforcement of a pro-allergic phenotype upon prolonged exposure. Archives of dermatological research 308, 665-670 (2016).

(8) Hermans, M.A.W. et al. Human Mast Cell Line HMC1 Expresses Functional Mas-Related G-Protein Coupled Receptor 2. Front Immunol 12, 625284 (2021).

(9) Buchan, K.D. et al. A transgenic zebrafish line for in vivo visualisation of neutrophil myeloperoxidase. PLoS One 14, e0215592 (2019).

(10) Aponte-Lopez, A., Enciso, J., Munoz-Cruz, S. & Fuentes-Panana, E.M. An In Vitro Model of Mast Cell Recruitment and Activation by Breast Cancer Cells Supports Anti-Tumoral Responses. Int J Mol Sci 21 (2020).

(11) Jamur, M.C. et al. Mast cell repopulation of the peritoneal cavity: contribution of mast cell progenitors versus bone marrow derived committed mast cell precursors. BMC Immunol 11, 32 (2010).

(12) Walke, J.B. & Belden, L.K. Harnessing the Microbiome to Prevent Fungal Infections: Lessons from Amphibians. PLoS Pathog 12, e1005796 (2016).

Reviewer #2: (Recommendations For The Authors): 

We thank the reviewer for their excellent suggestions, their time reviewing this work and their help with this manuscript.

While we were not able to incorporate some of these changes, please find that we have significantly altered our manuscript in accordance with the reviewer’s suggestions from their public review. We feel that we have substantially altered our paper, including providing considerable additional data, supporting the key findings therein.

(1) The heatmap in Figure 1I appears to be scaled data, similar to Figure 4A, in which case the indicated scale numbers are not correct (e.g. they should be -2 to 2, or -3 to 3) 

Thank you for the suggestion. Please find that we have changed this figure accordingly.

(2) For Figure 1, additional curated gene lists might better illustrate the difference in cell types, e.g. include the data for a panel of mast cell genes in a heatmap (mcpt1, tpsab1, etc.) and another panel of curated neutrophil genes (e.g. lyz) in a heatmap. If the authors still have leftover RNA, qPCR verification of some of the critical genes (e.g. kit) would add to the rigor of the analysis, as this study is the foundation of a new method for culturing amphibian mast cells. 

We thank the reviewer for this suggestion. Unfortunately, we do not have leftover RNA/cDNA and we have not been able to locate mcpt1 or tpsab1 in our DEGs. We anticipate that this issue may stem from the suboptimal annotation of the Xenopus laevis genome. We agree that curating more mast cell/neutrophil genes would be ideal but feel that we have adequately highlighted those genes that are differentially expressed between the two populations in our analysis.

(3) The presentation of counts in Figure 2 is a bit hard to interpret. Although it is mentioned that everything is statistically significant, explicitly showing statistics for each gene would be better. One possibility would be to use a volcano plot (p-value vs log2 fold change) and highlight the genes shown in Figure 2, potentially with an accompanying heat map to show replicate variability. 

We thank the reviewer for this suggestion. We entertained presenting the data as volcano plots or heat maps, but in the end felt that the bar graphs better conveyed the information that we are hoping to get across. Please note that the error bars in the bar graph depict the replicate variability. Please also note that to highlight that all the depicted genes were differentially expressed, we italicized the statement in the corresponding figure legend: “All depicted genes were significantly differentially expressed between the two populations”.

(4) Narratively, it might make more sense to put Figure 4A-C with Figure 3. 

We thank the reviewer for this suggestion. Please find that we significantly revised most of our figures to better convey the content therein. We combined the content of Figure 4A-C with Figure 5A-C and added data on epidermal thickness under different conditions into this figure; Figure 5 of our revised manuscript.

(5) If possible, complementing the skin RNA-seq from rSCF treatment in Bd infection with skin RNA-seq from rCSF3 treatment to compare effects on transcriptional programs of barrier function, etc would elevate this study and add additional insights into cutaneous inflammation in the setting of Bd infection. 

We thank the reviewer for this suggestion. We anticipate that the skin inflammation caused by Bd infection is not due solely to neutrophil infiltration and artificially altering the frog skin neutrophil content would thus not recapitulate chytridiomycosis progression. We completely agree that it would be valuable to examine barrier functions in control and mast cell-enriched, Bd-infected frogs. This is something that we hope to pursue further in future studies but feel that together with our additional findings, we are presenting a significant amount of data to constitute a stand-alone story.

(6) In Figure S1A, analyzing only 3 AMP genes by qPCR is perhaps too focused. As a control, it would be useful to also test some genes known to be functionally important in neutrophil anti-microbial responses, e.g. lyz. Expanding on this experiment by performing RNA-seq on Bd-treated, bone-marrow-derived mast cells and neutrophils would be a great addition to the manuscript and an important resource for future studies in the field. The fact that the use of rSCF (or rCSF3) enables the differentiation of these cells in large numbers of pure populations presents this unique opportunity. Although IL-4 did not end up affecting mucus production, clues to the mediator(s) of this mast cell-dependent effect may be found with unbiased RNA-seq after exposure to Bd. 

We thank the reviewer for this suggestion but would like to point out that our manuscript is focused on mast cells rather than neutrophils. We also believe that in vitro exposure of leukocytes to Bd is not the most physiologically relevant model of what would happen to skin-resident and incoming immune cell subsets, since Bd primarily infects top-most keratinocytes. We anticipate that rather than coming into direct contact with the fungus, cells like mast cells and neutrophils are responding to Bd-produced and infected cell-produced products. For this reason, we did not perform RNA-seq analysis of in vitro derived mast cells or neutrophils stimulated with Bd. As we develop more X. laevis-specific reagents, we hope to revisit the question of infected skin mast cell and neutrophil gene expression profiles but are not in a position to ask these questions at this time.

This work is also guided by a finite budget, and we feel that together with our significant additional findings described in our revised manuscript, we are presenting a substantial amount of work to constitute a stand-alone story and manuscript.

Reviewer #3 (Recommendations For The Authors): 

The following are minor edits needed in the text and figure legends: 

Standardize terms such as IL4 instead of il4 or ril4 vs rIL4 throughout. Also, r-SCF vs rSCF. 

Thank you. Please find that we have standardized such terms throughout our revised manuscript. Please note that we are adhering to the convention that gene names are in lower case, protein names are in upper case and recombinant protein names are preceded by an ‘r’.

Pg 9 Change "In contract" to "In contrast". 

Thank you and changed accordingly.

Fig 4 - Perhaps indicate if results in addition to 7dpi are also available. 

Please find that we analyzed Bd loads in control and mast cell-enriched, infected frogs after 10 dpi. This data is presented in Figures 3 and 4 of our revised manuscript.

Similarly in Fig. 5, are results other than 10dpi available in the supplement? 

Please find that the results from the microbiome studies are presented in supplemental figure 3 (Fig. S3). Please note that the results presented in original manuscript Fig. 5A-C - revised manuscript Fig. 5B-E depict data for 21 dpi, which is the longest examined infection timepoint. We present data from 1 and 10 dpi in Fig. 4 of our revised manuscript.

Indicate why these days were chosen in the methods. 

Please find that we indicated why the experimental timepoints were chosen, in the methods section of our revised manuscript.

Fig S1 legend has errors in describing which panels are for which asterisks. 

Fig. S3 legend indicates panels F and G. 

Thank you. Please find that we revised our supplemental figures and amended the corresponding figure legends.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The study entitled "Rifampicin tolerance and growth fitness among isoniazid-resistant clinical Mycobacterium tuberculosis isolates: an in-vitro longitudinal study" by Vijay et al. provides valuable insights into the association of rifampicin tolerance and growth fitness with isoniazid resistance among clinical isolates of M. tuberculosis. Antibiotic tolerance in M. tuberculosis is an important topic since it contributes to the lengthy and complicated treatment required to cure tuberculosis disease and may portend the emergence of antibiotic resistance. The authors found that rifampicin tolerance was correlated with bacterial growth, rifampicin minimum inhibitory concentrations, and isoniazid-resistance mutations.

Strengths:

The large number of clinical isolates evaluated and their longitudinal nature during treatment for TB (including exposure to rifampin) are strengths of the study.

Weaknesses:

Some of the methodologies are not well explained or justified and the association of antibiotic tolerance with growth rate is not a novel finding. In addition, the molecular mechanisms underlying rifampicin tolerance only in rapidly growing isoniazid-resistant isolates have not been elucidated and the potential implications of these findings for clinical management are not immediately apparent.

We thank the reviewer for the comments, we have modified the method section and figure 1 to clarify the method as suggested by the reviewer.

Although we agree that previous studies have shown the association of slow growth rate with antibiotic tolerance, ours is the most comprehensive assessment of rifampicin tolerance among clinical isolates, to our knowledge. In particular, we show that the degree of tolerance in clinical isolates can vary over several orders of magnitude: which had not been previously documented or appreciated. Furthermore, the association of high tolerance among IR isolates is a new finding, and given the potential for tolerance to increase risk of de novo drug resistance, our study suggests that IR isolates with high rifampicin tolerance may present a risk for development of MDR-TB.

In addition, we have also analysed the longitudinal isolates and the genetic variants emerging in them associated with increase in rifampicin tolerance. This analysis reveals possible multiple pathways to increase in rifampicin tolerance among clinical M. tuberculosis isolates. Possible clinical implication includes associating high rifampicin tolerance and isoniazid resistance as a risk factor for tuberculosis treatment failure. This study helps to develop further clinical studies to evaluate the role of rifampicin tolerance in IR isolates and treatment outcome. We have focused on these aspects in the discussion of the revised manuscript.

Reviewer #2 (Public Review):

Summary:

This study by Vijay and colleagues addresses a clinically important, and often overlooked aspect of Tb treatment. Detecting for variations in the level of antibiotic tolerance amongst otherwise antibiotic-susceptible isolates is difficult to routinely screen for, and consequently not performed. The authors, present a convincing argument that indeed, there is significant variation in the susceptibility of isoniazid-resistant strains to killing by rifampicin, in some cases at the same tolerance levels as bona fide resistant strains. On the whole, the study is easy to follow and the results are justified. This work should be of interest to the wider TB community at both a clinical and basic level.

Weaknesses:

The manuscript is long, repetitive in places, and the figures could use some amending to improve clarity (this could be a me-specific issue as they look ok on my screen, yet the colour is poor when printed).

We thank the reviewer for the comments, we have modified the revised manuscript as per the reviewer suggestions.

It would have been great to have seen some correlation between increased rifampicin tolerance and treatment outcome, although I'm not sure if this data is available to the researchers. I agree with the researchers the use of a single media condition is a limitation. However, this is true of a lot of studies. Rifampicin tolerance and treatment outcome analysis.

We agree with the reviewer that correlation between rifampicin tolerance and treatment outcome is important. This needs to be performed in future studies with better design to correlate rifampicin tolerance with treatment progression or outcome data.  

Reviewer #3 (Public Review):

Summary:

The authors have initiated studies to understand the molecular mechanisms underlying the devolvement of multi-drug resistance in clinical Mtb strains. They demonstrate the association of isoniazid-resistant isolates by rifampicin treatment supporting the idea that selection of MDR is a microenvironment phenomenon and involves a group of isolates.

Strengths:

The methods used in this study are robust and the results support the authors' claims to a major extent.

Weaknesses:

The manuscript needs a thorough vetting of the language. At present, the language makes it very difficult to comprehend the methodology and results.

We thank the reviewer for the comments, we have revised the manuscript as per the reviewer’s suggestions.

Reviewer #1 (Recommendations For The Authors):

Major comments:

(1) Methods: The authors attempt to differentiate between "fast"- and "slow"-growing bacteria in order to determine if the growth rate is associated with rifampicin tolerance. This is accomplished by assessing growth on solid agar at 15 and 60 days post-incubation, respectively. However, mycobacterial growth rate is not a binary phenomenon but rather a continuous variable. Moreover, it is not clear why 15 and 60 days were selected. Also, instead of a "slow growth" phenotype, the 60-day time point might simply reflect a longer lag phase. Were the plates examined at any interval time points? It would be interesting to know whether colony growth was delayed overall in the populations observed only at 60 days, or simply if the appearance of microcolonies visible to the naked eye was delayed (with normal growth afterwards).

We thank the reviewer for the comments, we want to clarify that we have not used agar plates but most-probable number method to determine the survival fraction post antibiotic treatment. We have clarified this in the revised manuscript and revised figure 1. The MPN method is a binary measure (growth/ no growth) and therefore cannot differentiate between long lag time and other mechanisms. In our original analysis, we included an intermediate time point of 30 days, but these data (included as supp fig. 1) cannot address the issue of lag phase directly. Since the 30-day time point did not add to the overall analysis and interpretation, we had not included them in the original submission.

(2) Methods/Results/Discussion: Some important clinical information is missing-how were the patients treated who had IR isolates? Did they receive the standard regimen for DS TB or was another drug substituted for isoniazid? Exposure to different drugs could affect the rifampicin-tolerant populations during the intensive phase (Figure 5).

Thank you for this comment, we have included the information regarding the treatment regimen in the revised manuscript.

Were there differences in microbiological (sputum culture conversion rate at 8 weeks or time to culture negativity) or clinical outcomes based on isoniazid susceptibility? Perhaps more importantly, were there differences in microbiological/clinical outcomes based on the proportion of bacterial subpopulations with rifampicin tolerance for a particular isolate? There should be more discussion on the potential clinical implications of the study's findings.

We agree with the reviewer that correlation between rifampicin tolerance and treatment progression or outcome is important. This needs to be performed in future studies with better design to correlate rifampicin tolerance with treatment progression or outcome data.  

(3) Results (Figure 3A): Although an interesting finding, the increased rifampicin tolerance observed only in the "rapidly" growing populations of isoniazid-resistant isolates (IR) vs. isoniazid-susceptible (IS) isolates is not explained. In contrast, equally, increased rifampicin tolerance is seen in the "slowly" growing populations of both IR and IS isolates. It would be interesting to know if these slowly growing populations show specific tolerance to rifampicin or if, as expected, slow growth confers tolerance to a range of different bactericidal antibiotics.

We thank the reviewer for the suggestions. we agree these will be interesting to investigate in a future study but are outside the scope of the current study.

(4) Results (Figure 3B): The basis for the classification into tertiles is not clear and appears somewhat arbitrary-does this represent the survival of a particular isolate following rifampicin exposure relative to the other isolates based on isoniazid susceptibility (IS or IR) or the % growth relative to other populations for the same isolate? Figure 3B is missing a y-axis label. Is it a log10 MPN ratio?

We thank the reviewer for pointing this, we want to clarify that for the classification into tertiles, first we pooled both group of isolates isoniazid susceptible (IS) and isoniazid resistant (IR) into a single population. Subsequently, we categorized this unified population into three distinct groups: low, medium, and high, based on their survival fraction following rifampicin treatment. Consequently, the 'low,' 'medium,' and 'high' tertiles represent the survival of each isolate following rifampicin exposure relative to the total number of isolates  combing both IS and IR isolates.

For clarity, we provide a breakdown of the criteria for each tertile:

+Low tertile: Consists of isolates with the lowest survival fraction (bottom 25%).

+Medium tertile: Encompasses isolates with survival fractions that fall between the bottom 25% and the top 25%.

+High tertile: Comprises isolates with the highest survival fractions (top 25%). This we have modified in the revised manuscript to clarify.

We have also modified the Figure 3B to correct the y-axis label.

(5) Results (lines 185-186): For correlating relative growth in the absence of antibiotics, 19 clinical isolates "outliers" were removed without explanation.

We have added explanation for the “outliers” which were removed earlier due to deviation from normal distribution, we have also provided the supplementary figure 3 which includes these outliers.

(6) Results (lines 203-211): The authors attempted to investigate a potential association between the mechanism of M. tuberculosis isoniazid resistance and the degree of rifampicin tolerance. However, the vast majority of IR clinical isolates (n=71) had a katG_S315X mutation and only 8 isolates had alternative mutations (inhA_I21T and fabG1_C-15X). Given the wide range of rifampicin tolerance observed within these isoniazid-resistant isolates, they concluded that other genetic or epigenetic determinants must be playing a role. WGS of longitudinally collected isolates from the same patients during TB treatment yielded non-synonymous SNPs in a list of genes previously reported to be associated with persistence, tolerance, and mycobacterial survival. However, precise mechanisms (including, e.g., expression of efflux pumps) are not investigated.

We thank the reviewer for summarising the findings. Yes, we agree that investigating the precise mechanism of rifampicin tolerance is beyond the scope of the current work.

Minor comments:

(1) Abstract (line 41): The nonstandard abbreviations "IR" and "IS" have not been introduced prior to this usage.

We have modified this in the abstract.

(2) Introduction (line 60): Insert "phenomena" or "mechanisms" after "two".

We have modified this in the introduction.

(3) Introduction (lines 66-69): This sentence is confusing, especially the second part ("supporting this studies...").

We have modified the lines to clarify.

(4) Introduction (line 84): In the current text, it appears as if "IR" is the abbreviation for "isoniazid". Therefore, I recommend changing "resistance to isoniazid" to "isoniazid resistance".

We have modified this in the revised manuscript.

(5) Results (line 141): Insert "the" before "rest".

We have modified this in the revised manuscript.

(6) Results (line 187): Replace "did not had" with "did not have".

We have modified this in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

Abstract:

The abstract is long and repetitive. It needs reworking and shortening to improve clarity and highlight the main takeaway message.

We thanks the reviewer for the suggestions and have modified this in the revised manuscript.

The introduction is interesting and contains relevant information. However, it is long and takes a while to get to the point of the study. It needs re-writing to emphasise key prior results and the purpose of this study.

We thanks the reviewer for the suggestions and we have modified this in the revised manuscript.

Results:

As the study relies predominately on the use of MPN, I think a simple schematic of how the experiment is performed would be informative. Could this be added to Figure 1?

We have revised the figure 1 in the manuscript to include the schematic representation.

Some of the differences in MKD90, whilst they may be significant, are small so it would at least provide context as to the relevance of these differences. This may also alleviate my confusion as to how the authors can measure the time required to achieve MDK90 as 1.23-1.31 days when the first time point that is taken is day 2 (the data in Figure 2). They have FigS6 but this is small and hard to follow.

We thank the reviewer for this suggestion, we have modified this in the revised manuscript and figureS6.

Figure 2:

Would be helpful to have -1 on the Y axis.

The grey dots don't print very well (Might be my printer)

We have modified this in the revised manuscript, figure 2.

Line 142: The authors note a difference in RIF tolerance at day 15 that disappeared by day 60. I assume they are referring to the day 5 timepoint although this isn't clear as written.

Yes, it is referring to the day 5 time point and we have clarified this in the revised manuscript.

The section starting at line 148 (fig 3) is interesting, but it is difficult to read and follow what the difference is between this data and the prior data in Figure 2. It also wasn't until about line 165 that the purpose became clear. Overall the conclusions are sound and interesting.

We have modified this in the revised manuscript.

Line 154: What are the early and late time recovery time points?

Is Figure 3A the same data as Figure 2?

We have clarified this in the revised manuscript, the figure 3A is the same data as Figure 2.

I found Figure 6 hard to follow. I'm not sure how better to present this data, but it should be improved. Some further clarification in the text would be helpful.

We thank the reviewer for the suggestions. We have added more explanation in the text to clarify figure 6.

Conclusions:

The conclusions are sound, based on the data presented. The clinical relevance is highlighted, yet appropriately phrased to not be too far-reaching.

Again, I think the conclusions could be condensed considerably. It is repetitive in places, which distills the main outcomes of this otherwise interesting and important study. The authors appropriately highlight some of the limitations of their study.

We thank the reviewer for these comments and have modified this in the revised manuscript.

Reviewer #3 (Recommendations For The Authors):

The manuscript "Rifampicin tolerance and growth fitness among isoniazid-resistant clinical Mycobacterium tuberculosis isolates: an in-vitro longitudinal study" by Srinivasan et.al., details the identification/ development of isoniazid-resistant strains in clinical isolates following testament with rifampicin. This is an important aspect of understanding MDR development in TB strains. the results are promising and gel well with the hypothesis. However, the manuscript requires a thorough language modification. While the overall idea is clear the methodology does not come out clearly.

Specific comments:

(1) It is not clear whether rifampicin treatments were given for 2 and 5 days before kill curves or for 15 and 60 days? The methodology needs to be phased clearly. Why was this time interval of 15 days and 60 days taken? is there a rationale for this?

We thank the reviewer for the suggestions, we have modified the method and figure 1 to clarify this in the revised manuscript.

(2) A concentration of 2ug/ml was used for in vitro culture in this study. While the authors themselves indicate that this is well above the MIC, this might represent a non- natural dose and hence may force the evolution of strains. What will be the scenario in the natural course of antibiotic treatment (dose at MIC or less than MIC)?

We have observed that till 5 days there is no significant resistant emergence but after 5 days only resistance emerges, therefore we avoided determining the survival fraction after resistance emergence, the kill curve represents mostly tolerant sub population. ADD: Pharmacokinetic studies of rifampicin dosing suggest that peak concentrations of >2-32 µg/mL are typical for standard doses of the drug, therefore we believe the chosen concentration of 2 µg/mL to be physiologically relevant.

(3) As described in line 155, the survival spanned a broad distribution, across a million times in difference. This is rather surprising that 5 days of rifampicin treatment would lead to such a spread in resistance patterns. Did the authors study the different populations to understand this phenomenon? This is important given the scale of resistance developed in this short time.

We want to clarify that the broad range of survival fraction reflect the difference in tolerant sub-populations but not resistant sub-population to rifampicin as they are determined post rifampicin treatment in rifampicin free media, this has been clarified in the revised figure 1.

Overall, the manuscript is a detailed study with new insights into the development of multi-drug resistance by Mtb. A thorough vetting for language is essential for a greater impact of the study.

We thank the reviewer and have attempted to improve the clarity of the language to increase the potential impact of our findings.

Author response:

The following is the authors' response to the current reviews.

Reviewer #1 (Public Review):

I'll begin by summarizing what I understand from the results presented, and where relevant how my understanding seems to differ from the authors' claims. I'll then make specific comments with respect to points raised in my previous review (below), using the same numbering. Because this is a revision I'll try to restrict comments here to the changes made, which provide some clarification, but leave many issues incompletely addressed.

As I understand it the main new result here is that certain recurrent network architectures promote emergence of coordinated grid firing patterns in a model previously introduced by Kropff and Treves (Hippocampus, 2008). The previous work very nicely showed that single neurons that receive stable spatial input could 'learn' to generate grid representations by combining a plasticity rule with firing rate adaptation. The previous study also showed that when multiple neurons were synaptically connected their grid representations could develop a shared orientation, although with the recurrent connectivity previously used this substantially reduced the grid scores of many of the neurons. The advance here is to show that if the initial recurrent connectivity is consistent with that of a line attractor then the network does a much better job of establishing grid firing patterns with shared orientation.

Beyond this point, things become potentially confusing. As I understand it now, the important influence of the recurrent dynamics is in establishing the shared orientation and not in its online generation. This is clear from Figure S3, but not from an initial read of the abstract or main text. This result is consistent with Kropff and Treves' initial suggestion that 'a strong collateral connection... from neuron A to neuron B... favors the two neurons to have close-by fields... Summing all possible contributions would result in a field for neuron B that is a ring around the field of neuron A.' This should be the case for the recurrent connections now considered, but the evidence provided doesn't convincingly show that attractor dynamics of the circuit are a necessary condition for this to arise. My general suggestion for the authors is to remove these kind of claims and to keep their interpretations more closely aligned with what the results show.

We would like to clarify that the simple (flexible) attractor is a weaker condition than the ones previously used to align grid cells. However, by no means we claim that it is a necessary condition for grid maps to align. Other architectures, certainly more complex ones but perhaps even simpler ones, can align grid maps in our model.

Major (numbered according to previous review)

(1) Does the network maintain attractor dynamics after training? Results now show that 'in a trained network without feedforward Hebbian learning the removal of recurrent collaterals results in a slight increase in gridness and spacing'. This clearly implies that the recurrent collaterals are not required for online generation of the grid patterns. This point needs to be abundantly clear in the abstract and main text so the reader can appreciate that the recurrent dynamics are important specifically during learning.

We respectfully disagree with the interpretation of this result. In this model cells self-organize to produce aligned grid maps. In such systems it makes sense to characterize the equilibrium states of the system. We turned learning off in Figure S3 to show that the recurrent connections have a contractive effect on grid spacing. But artificially turning off learning means that one can no longer make claims about the equilibrium states of the system, since it can no longer evolve freely. In a functional network, if the recurrent attractor is removed, the system will evolve towards poor gridness and no alignment no matter what the starting point is, as also shown in Figure S3. Several experimental results invite us to think of grid cells as the equilibrium solution of a series of constraints that is ready to change at any time: Barry et al, 2012; Yoon et al, 2013; Carpenter et al, 2015; Krupic et al, 2015; Krupic et al, 2018; Jayakumar et al, 2019.

One point in which we perhaps agree with the reviewer is that information about the hexagonal maps is kept in the feedforward weights, while behavior and the recurrent collaterals act as constraints of which these feedforward weights are the equilibrium solution.

(2) Additional controls for Figure 2 to test that it is connectivity rather than attractor dynamics (e.g. drawing weights from Gaussian or exponential distributions). The authors provide one additional control based on shuffling weights. However, this is far from exhaustive and it seems difficult on this basis to conclude that it is specifically the attractor dynamics that drive the emergence of coordinated grid firing.

Again, we do not claim that this is the only way in which grid maps can be aligned, but it is the simplest one proposed so far. We were asked if it was the specific combination of input weights to a cell rather than the organization provided by the attractor which resulted in aligned maps. By shuffling the inputs to a cell we keep the combination of inputs invariant but lose the attractor architecture. Since grid maps in this new situation are not aligned, we can safely conclude that it is not the combination of inputs per se, but the specific organization of these inputs that allows grid alignment. It is not fully clear to us what ‘exhaustive’ means in this context.

(3) What happens if recurrent connections are turned off? The new data clearly show that the recurrent connections are not required for online grid firing, but this is not clear from the abstract and is hard to appreciate from the main text.

This point is related to (1). Absent this constraint, Figure S3 shows that the system evolves toward larger spacing, with poorer gridness and no alignment.

(4) This is addressed, although the legend to Fig. S2D could provide an explanation / definition for the y-axis values.

We have now added: Mean input fields are the sum of all inputs of a given kind entering a neuron at a given moment in time, averaged across cells and time.

(5) Given the 2D structure of the network input it perhaps isn't surprising that the network generates 2D representations and this may have little to do with its 1D connectivity. The finding that the networks maintain coordinated grids when recurrent connections are switched off supports my initial concern and the authors explanation, to me at least, remain confusing. I think it would be helpful to consider that the connectivity is specifically important for establishing the coordinated grid firing, but that the online network does not require attractor dynamics to generate coordinated grid firing.

This point is related to (1) and (3). We agree with the reviewer that the input lies within a 2D manifold, but this is not something that the network has to find out because it receives one datapoint of information at a time. This alone is not enough to form aligned grid cells, since each grid cell can find a roughly equivalent equilibrium in a different direction. It is only the constraint imposed by the recurrent collaterals that aligns grid maps, and, as we show, this constraint does not need to be constructed ad hoc to work on 2D, as previously thought. When recurrent connections are switched off, the system evolves toward unaligned grid maps, with larger spacing and lower gridness. Regarding the results obtained after modifying the network and turning off learning, we think they have a very limited scope (in this case showing the contractive effect of recurrent collaterals on grid spacing), given that the system is artificially being kept out of its natural equilibrium.

(6) Clarity of the introduction. This is somewhat clearer, but I wonder if it would be hard for someone not familiar with the literature to accurately appreciate the key points.

We have made our best effort to improve the clarity of the introduction.

(7) Remapping. I'm not sure why this is ill posed. It seems the proposed model can not account for remapping results (e.g. Fyhn et al. 2007). Perhaps the authors could just clearly state this as a limitation of the model (or show that it can do this).

We view our model as perfectly consistent with Fyhn et al, 2007. Remapping is not triggered by the network itself, though, but rather by a re-arrangement of the inputs requiring the network to learn new associations. Different simulations of the same model with identical parameters can be interpreted as remapping experiments.

Reviewer #3 (Public Review):

Summary:

The paper proposes an alternative to the attractor hypothesis, as an explanation for the fact that grid cell population activity patterns (within a module) span a toroidal manifold. The proposal is based on a class of models that were extensively studied in the past, in which grid cells are driven by synaptic inputs from place cells in the hippocampus. The synapses are updated according to a Hebbian plasticity rule. Combined with an adaptation mechanism, this leads to patterning of the inputs from place cells to grid cells such that the spatial activity patterns are organized as an array of localized firing fields with hexagonal order. I refer to these models below as feedforward models.

It has already been shown by Si, Kropff, and Treves in 2012 that recurrent connections between grid cells can lead to alignment of their spatial response patterns. This idea was revisited by Urdapilleta, Si, and Treves in 2017. Thus, it should already be clear that in such models, the population activity pattern spans a manifold with toroidal topology. The main new contributions in the present paper are (i) in considering a form of recurrent connectivity that was not directly addressed before. (ii) in applying topological analysis to simulations of the model. (iii) in interpreting the results as a potential explanation for the observations of Gardner et al.

We wanted to note that we do not see this paper as proposing an alternative to the attractor hypothesis, given that we use attractor networks, but rather as an exploration of possibilities not yet visited by this hypothesis.

Strengths:

The exploration of learning in a feedforward model, when recurrent connectivity in the grid cell layer is structured in a ring topology, is interesting. The insight that this not only align the grid cells in a common direction but also creates a correspondence between their intrinsic coordinate (in terms of the ring-like recurrent connectivity) and their tuning on the torus is interesting as well, and the paper as a whole may influence future theoretical thinking on the mechanisms giving rise to the properties of grid cells.

Weaknesses:

(1) In Si, Kropff and Treves (2012) recurrent connectivity was dependent on the head direction tuning, in addition to the location on a 2d plane, and therefore involved a ring structure. Urdapilleta, Si, and Treves considered connectivity that depends on the distance on a 2d plane. The novelty here is that the initial connectivity is structured uniquely according to latent coordinates residing on a ring.

The recurrent architectures in the cited works are complex and require arranging cells in a 2D manifold to calculate connectivity based on their relative 2D position. In other words, the 2D structure is imprinted in the architecture, as in our 2D condition. In this work the network is much simpler and only requires neighboring relations in 1D. Such relationships have been shown to spontaneously emerge in the hippocampal formation (Pastalkova et al, 2008; Gonzalo Cogno et al, 2024).

(2) The paper refers to the initial connectivity within the grid cell layer as one that produces an attractor. However, it is not shown that this connectivity, on its own, indeed sustains persistent attractor states. Furthermore, it is not clear whether this is even necessary to obtain the results of the model. It seems possible that (possibly weaker) connections with ring topology, that do not produce attractor dynamics but induce correlations between neurons with similar locations on the ring would be sufficient to align the spatial response patterns during the learning of feedforward weights.

Regarding the first part of the comment, the recurrent collaterals create one or at times multiple bumps of activity in the network so that neighboring (interconnected) cells activate together. An initial random state of activity rapidly falls into this dynamic, constrained by the attractor. To us this is not surprising given that this connectivity is the classical means of creating a continuous attractor. Perhaps there is some deeper meaning in this comment that we are not fully grasping.

Regarding the second part of the comment, we fully agree with the reviewer. We are presenting what so far is the simplest connectivity that can align grid maps, but by no means we claim that it is the simplest possible one. Regarding weaker connections with ring topology, we show in Figure S2 that a ring attractor with too weak or too strong connections is incapable of aligning grids, since a balance between feedforward and feedback inputs is required.

(3) Given that all the grid cells are driven by an input from place cells that span a 2d manifold, and that the activity in the grid cell network settles on a steady state which is uniquely determined by the inputs, it is expected that the manifold of activity states in the grid cell layer, corresponding to inputs that locally span a 2d surface, would also locally span a 2d plane. The result is not surprising. My understanding is that this result is derived as a prerequisite for the topological analysis, and it is therefore quite technical.

We understand that the reviewer is referring to the motivation behind studying local dimensionality. We agree that the topological analysis approach is quite technical, but it provides unique insights. The theorem of closed surfaces, which allows us to deduce a toroidal topology from Betti numbers (1,2,1), only applies to closed surfaces. One thus needs to show that the point cloud is a surface (local dimensionality of 2) and is closed (no borders or singularities). If borders or singularities were present, a toroidal topology could not be claimed from these Betti numbers. Thus, it is a crucial step of the analysis.

(4) The modeling is all done in planar 2d environments, where the feedforward learning mechanism promotes the emergence of a hexagonal pattern in the single neuron tuning curve. Under the scenario in which grid cell responses are aligned (i.e. all neurons develop spatial patterns with the same spacing and orientation) it is already quite clear, even without any topological analysis that the emerging topology of the population activity is a torus.

However, the toroidal topology of grid cells in reality has been observed by Gardner et al also in the wagon wheel environment, in sleep, and close to boundaries (whereas here the analysis is restricted to the a sub-region of the environment, far away from the walls). There is substantial evidence based on pairwise correlations that it persists also in various other situations, in which the spatial response pattern is not a hexagonal firing pattern. It is not clear that the mechanism proposed in the present paper would generate toroidal topology of the population activity in more complex environments. In fact, it seems likely that it will not do so, and this is not explored in the manuscript.

We agree that our work was constrained to exploration in 2D and that the situations posed by the reviewer are challenging, but we do not see them as unsurmountable. The wagon wheel shows a preservation of toroidal topology locally, where the behavior of the animal is rather 2-dimensional. Globally, hexagonal maps are lost, which is compatible with some flexibility in the way grid maps are formed. If sleep meant that all inputs are turned off, our model would predict a dynamic dictated by the architecture (1D for the ring attractor, for example), but we do not really know that this is the case. In the future, we intend to explore predictive activity along the linear attractor, which could both result in path integration and in some level of preservation of the activity when inputs are completely turned off.

Regarding boundaries, as we have argued before, the cited work chooses to filter away what looks like more than half of the overall explained variance through PCA, and this is only before applying a non-linear dimensionality reduction algorithm. It is specifically shown that the analyzed components are the ones with global periodicity throughout the environment. Thus, it is conceivable that through this approach, local irregularities found only at the borders are disregarded in favor of a clearer global picture. While using a different methodology, our approach follows a similar spirit, albeit with far less noisy data.

(5) Moreover, the recent work of Gardner et al. demonstrated much more than the preservation of the topology in the different environments and in sleep: the toroidal tuning curves of individual neurons remained the same in different environments. Previous works, that analyzed pairwise correlations under hippocampal inactivation and various other manipulations, also pointed towards the same conclusion. Thus, the same population activity patterns are expressed in many different conditions. In the present model, this preservation across environments is not expected. Moreover, the results of Figure 6 suggest that even across distinct rectangular environments, toroidal tuning curves will not be preserved, because there are multiple possible arrangements of the phases on the torus which emerge in different simulations.

We agree with this observation. A symmetry in our implementation results in the fact that only ~50% of times the system falls in the preferred solution, and the rest of the times it falls into other local minima. Whether this result is at odds with current observations can be debated on the basis of probabilities. However, we believe that the symmetry we found is purely circumstantial, and that it can be broken by elements such as head direction modulation or other ingredients used to achieve path integration. In other words, we acknowledge that symmetry is an issue of the implementation we show here (which has been kept as simple as possible to serve as a proof-of-principle) but we do not think that it is a defining feature of flexible attractors in general. We expect that future implementations that incorporate path integration capabilities will not present this kind of symmetry in the space of solutions.

Regarding the rigid phase translation across modalities, while this effect is very clear in Gardner et al, it is less so in other datasets. The analyses shown in Hermansen et al (2024) can rather be interpreted as somewhere in the way between perfect rigid translation and fully randomized phases across navigation modalities.

(6) In real grid cells, there is a dense and fairly uniform representation of all phases (see the toroidal tuning of grid cells measured by Gardner et al). Thus, the highly clustered phases obtained in the model (Fig. S1) seem incompatible with the experimental reality. I suspect that this may be related to the difficulty in identifying the topology of a torus in persistent homology analysis based on the transpose of the matrix M.

We partly agree with this observation and note that a pattern of ordered phases is an issue not only for the 1D attractor but also for the 2D one, which appears much more uniform than in experimental data. The low number of neurons we used for computational economy and the full connectivity could be key ingredients to generate these phase patterns. To show that this is not a defining feature of flexible attractors, apart from the fact that these patterns appear also with non-flexible 2D architectures, we included in Figure S1 simulations with ‘fragmented 1D’ architectures. In this case the architecture is a superposition of 20 random 1D stripe-like attractors. While the alignment of maps achieved with this architecture is almost at the same level as the one obtained with 1D and 2D attractors, the phases are much more similar to what has been observed experimentally, and less uniform than what is obtained with 2D attractors.

(7) The motivations stated in the introduction came across to me as weak. As now acknolwledged in the manuscript, attractor models can be fully compatible with distortions of the hexagonal spatial response patterns - they become incompatible with this spatial distortions only if one adopts a highly naive and implausible hypothesis that the attractor state is updated only by path integration. While attractor models are compatible with distortions of the spatial response pattern, it is very difficult to explain why the population activity patterns are tightly preserved across multiple conditions without a rigid two-dimentional attractor structure. This strong prediction of attractor models withstood many experimental tests - in fact, I am not aware of any data set where substantial distortions of the toroidal activity manifold were observed, despite many attempts to challenge the model. This is the main motivation for attractor models. The present model does not explain these features, yet it also does not directly offer an explanation for distortions in the spatial response pattern.

Some interesting examples are experiments in 3D, where grid cells presumably communicate with each other through the same recurrent collaterals, but global periodicity is lost and only some local order is preserved even away from boundaries (Ginosar et al, 2021; Grieves et al, 2021). While these datasets have not been explored using topological analysis, they serve as strong motivators to understanding 2D grid cells as one equilibrium solution that arises under some set of constraints, but belongs to a wider space of possible solutions that may arise as well under more flexible constraints. Even (and especially) if one adheres to the hypothesis that grid cells are pre-wired into a 2D torus, a concept like flexible attractors might become useful to understand how their activity is rendered in 3D. Another strong motivation is our lack of understanding of how a perfectly balanced 2D structure is formed and maintained. Simpler architectures could be thought of as alternatives, but also as an intermediate step towards it.

Regarding the rigid phase translation across modalities, while this effect is very clear in Gardner et al, it is less so in other datasets. The analyses shown in Hermansen et al (2024) can rather be interpreted as somewhere in the way between perfect rigid translation and fully randomized phases.

In a separate point, although it might not be strictly related to the comment, we do not fully share the idea that persistent activity patterns during sleep are necessary or sufficient conditions for attractor dynamics, although we do agree that attractors could be the mechanism behind them and any alternative is at least as complex as attractors. On the necessity side, attractors in the hippocampus are not constantly engaged (Wills et al, 2005). For sufficiency, one should prove that no other network is capable of reproducing the phenomenon, and to our best knowledge we are still far from that point.

(8) There is also some weakness in the mathematical description of the dynamics. Mathematical equations are formulated in discrete time steps, without a clear interpretation in terms of biophysically relevant time scales. It appears that there are no terms in the dynamics associated with an intrinsic time scale of the neurons or the synapses (a leak time constant and/or synaptic time constants). I generally favor simple models without lots of complexity, yet within this style of modelling, the formulation adopted in this manuscript is unconventional, introducing a difficulty in interpreting synaptic weights as being weak or strong, and a difficulty in interpreting the model in the context of other studies.

We chose to keep the model as simple as possible and in the line of previous publications developing it. However, we see the usefulness of putting it in what in the meantime has become a canonical framework. Fortunately this has been done by D’Albis and Kempter (2017). In our simplified version of the model there is no leak term and adaptation on its own brings down activity in the absence of input, but we agree that such a term could be added, albeit not without modifying all other network parameters.

In my view, the weaknesses discussed above limit the ability of the model, as it stands, to offer a compelling explanation for the toroidal topology of grid cell population activity patterns, and especially the rigidity of the manifold across environments and behavioral states. Still, the work offers an interesting way of thinking on how the toroidal topology might emerge.

Reviewer 1:

Reviewer #1 (Recommendations For The Authors):

See comments above. In addition:

(1) Abstract: '...interconnected by a two-dimensional attractor guided by path integration'. This is unclear. I think the intended meaning might be along the lines of '...their being computed by a 2D continous attractor that performs path integration'?

'path integration allowing for no deviations from the hexagonal pattern' This is incorrect. Local modulation of the gain of the speed input to a standard CAN would distort the grid pattern.

'Using topological data analysis, we show that the resulting population activity is a sample of a torus' Activity in the model?

'More generally, our results represent a proof of principle against the intuition that the architecture and the representation manifold of an attractor are topological objects of the same dimensionality, with implications to the study of attractor networks across the brain' I guess one might hold this intuition, but it strikes me as obvious that if you impose an sufficiently strong n-dimensional input on a network then it it's activity could have the same dimensionality. I don't really see this as being a point worth highlighting. Perhaps the more interesting point, it that during learning the recurrent connectivity aligns the grid fields of neurons in the network, and this may be a specific function of the 1D attractor dynamcis, although I don't think the authors have made this point convincing.

'The flexibility of this low dimensional attractor allows it to negotiate the geometry of the representation manifold with the feedforward inputs'. See above for comments on the use of 'negotiate'.

'while the ensemble of maps preserves features of the network architecture'. I don't understand this. What is the 'ensemble of maps' and what are the features referred to.

We have reviewed the abstract considering these points. Regarding the ‘strong n-dimensional input’, we want to point out that it is not the input itself that generates a torus (the no attractor condition does not lead to a torus) but rather the interplay between the input and the attractor.

‘Perhaps the more interesting point …’, we do not fully understand how this sentence deviates from our own conclusions. We here show that a strong n-dimensional input is not enough to align grid cells (produce a n-torus), it is the interplay between inputs and attractor dynamics that does so, even if the attractor is not n-dimensional in terms of architecture.

The ensemble of maps refers to the transpose of the population activity matrix, where each point in the cloud is a map, and the features refer to the persistent homology.

(2) The manuscript still fails to clarify the difference between a model that path integrates in two dimensions and a model that simply represents information with a given dimensionality. The argument that it's surprising that a network with 1D architecture represents a higher dimensional input strikes me as incorrect and an unnecessary attempt to argue for conceptual importance. At least to me this isn't surprising. It would be surprising if the 1D network could path integrate but this doesn't seem to be the case.

In response to the reviewer’s concerns, we have made clear in the introduction and discussion that this model has no path integration capabilities, although we aim to develop a model capable of path integration using the kind of simple architecture presented here. We want to highlight here that equating attractor dynamics with path integration would be a conceptual mistake.

(3) Other wording also seems to make unnecessary conceptual claims. E.g. The repeated use of 'negotiate' implies some degree of intelligence, or at least an exchange of information, that isn't shown to exist. I wonder if more precise language could be used? As I understand it the dimensionality is bounded by the inputs on the one hand, and the network connectivity on the other, with the actual dimensionality being a function of the recurrent and feedforward synaptic weights. There's clearly some role for the relative weights and the properties of plasticity rules, but I don't see any evidence for a negotiation.

An interesting observation in Figure S2 is that grid maps are aligned only if the relative strength of feedforward and recurrent inputs is similar. If one of them can impose over the other, grid maps do not align. This equilibrium can metaphorically be thought of as a negotiation instance, where the negotiation is an emergent property of the system rather than something happening at an individual synapse.

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

Reviewer #1:

Reviewer #1 (Recommendations For The Authors):

Major

(1) What is the evidence that, after training, the 1D network maintains its attractor dynamics when feedforward inputs are active? If the claim is that it does then it's important to provide evidence, e.g. responses to perturbations, or other tests. The alternative is that after training the recurrent inputs are drowned out by the feed forward spatial inputs.

We agree with the reviewer on the importance of this point. In our model, networks are always learning, and the population activity represented by aligned grid maps in a trained network is a dynamic equilibrium that emerges from the interplay between feedforward and collateral constraints. If Hebbian learning is turned off, one gets a snapshot of the network at that moment. We now show in Fig. S3 that in a trained network without feedforward Hebbian learning the removal of recurrent collaterals results in a slight increase in gridness and spacing. The expansion is due to the fact that, as we argue in the Results section, the attractor has a contractive effect on grid maps, which could relate to observations in novel environments (Barry et al, 2007). If Hebbian learning is turned on in the same situation, the maps, no longer constrained by the attractor, drift toward the equilibrium solution of the ‘No attractor’ condition, with significantly larger spacing, no alignment and lower individual gridness. Thus, the attractor is the force preventing them to do so when feedforward Hebbian learning is on.

These observations point to the key role played by the attractor not only in forming but also in sustaining grid activity. The dynamic equilibrium framework fits well known properties of the system, such as its capacity to recalibrate very fast (Jayakumar et al, 2019), although this particular feature cannot be modeled with the current version of our model, that lacks path integration capabilities.

(2) It would be useful to include additional control conditions for Figure 2 to test the hypothesis that it is simply connectivity, rather than attractor dynamics, that drives alignment.

This could be achieved by randomly assigning strengths to the recurrent connections, e.g. drawing from exponential or Gaussian distributions.

We agree and have included Fig. S2b-d, showing that the same distribution of collateral input weights entering each neuron, but lacking the 1D structure provided by the attractor, does not align grid maps. This is achieved by shuffling rows in the connectivity matrix, while avoiding self connections to make the comparison fair (self connections substantially alter the dynamic of the network, making it much more rigid). We observed that individual grid maps have very low gridness levels, even lower than in the no-attractor condition. In contrast, they have levels of population gridness slightly higher than in the no-attractor condition, but closer to 0 than to levels achieved with attractors. Our interpretation of these results is that irregular connectivity achieves some alignment in a few arbitrary directions and/or locations, which improves the coordination between maps at the expense of impairing rather than improving hexagonal responses of individual cells. Such observations stand in clear context to what is observed with continuous attractors with an orderly architecture.

These results suggest that it is the structure of the attractor that allows grid cells to be aligned rather than the mere presence of recurrent collateral connections.

(3) It seems conceivable that once trained the recurrent connections would no longer be required for alignment. Can this be evaluated by considering what happens if the recurrent connections are turned off after training (or slowly turned off during training)? Does the network continue to generate aligned grid fields?

This point has elements in common with point 1. As we argued in that response, the attractor has two main effects on grid maps: it aligns them and it contracts them. If the attractor is turned off, feedforward Hebbian learning progressively drives maps toward the solution obtained for the ‘no attractor’ condition, characterized by maps with larger spacing, poorer gridness and lack of alignment.

(4) After training what is the relative strength of the recurrent and feedforward inputs to each neuron?

Both recurrent and feedforward synaptic-strength matrices are normalized throughout training, so that the overall incoming synaptic strength to each neuron is invariant. Because of this, although individual feed-forward and recurrent input fields vary dynamically, their average is constant, with the exception of the very first instances of the simulation, before a stable regime is reached in grid-cell activity levels. We have included Fig. S2d, showing the dynamics of feedforward and recurrent mean fields throughout learning as well as their ratio. In addition, Fig. S2a shows that the strength of recurrent relative to feedforward inputs is an important parameter, since alignment is only obtained in an intermediate range of ratios.

(5) It would be helpful to also evaluate the low dimensional structure of the input to the network. Assuming it has a 2D structure, as it represents 2D space, can an explanation be provided for why it is surprising that the trained network also encodes activity with a 2D manifold? It strikes me that the more interesting finding might relate to alignment of the grids rather than claims about a 1D attractor encoding a 2D representation. Either way, stronger evidence and clearer discussion would be helpful.

The reviewer is correct in assuming that the input has a 2D structure, that can be represented by a sheet embedded in a high dimensional space and thus has the Betti numbers [1,0,0]. The surprising element in our results is that we are showing for the first time that the population activity of an attractor network is constrained to a manifold that results from the negotiation between the architecture of the attractor and the inputs, and does not merely reflect the former as previously assumed. In this sense, the alignment of grid cells by a 1D attractor is an instance of the more general case that 1D attractors can encode 2D representations.

It is certainly the case that the 2D input is a strong constraint pushing population activity toward a 2D manifold. However, the final form of the 2D manifold is strongly constrained by the attractor, as shown by the contrast with the no-attractor condition (a 2D sheet, as in the input, vs a torus when the attractor is present). The 1D attractor is able to flexibly adapt to the constraint posed by the inputs while doing its job (as demonstrated in previous points), which results in 2D grid maps aligned by a 1D attractor. Generally speaking, this work provides a proof of principle demonstrating that the topology of the attractor architecture and the manifold of the population activity space need not be identical, as previously widely assumed by the attractor community, and need not even have the same dimensionality. Instead, a single architecture can potentially be applied to many purposes. Hence, our work provides a valuable new perspective that applies to the study of attractors throughout the brain.

(6) The introduction should be clearer about the different types of grid model and the computations they implement. E.g. The authors' previous model generates grid fields from spatial inputs, but if my understanding is correct it isn't able to path integrate. By contrast, while the many 2D models with continuous attractor dynamics also generate grid representations, they do so by path integration mechanisms that are computationally distinct from the spatial transformation implemented by feedforward models (see also general comments above).

We agree with the reviewer and have made this point explicit in the introduction.

(7) A prediction from continuous attractor models is that when place cells remap the low dimensional manifold of the grid activity is unaffected, except that the location of the activity bump is moved. It strikes me as important to test whether this is the case for the model presented here (my intuition is that it won't be, but it would be important to establish either way).

We want to emphasize that our model is a continuous attractor model, so the question regarding the difference between what our model and continuous attractor network models predict is an ill-posed one. One of our main conclusions is precisely that attractors can work in a wider spectrum of ways than previously thought.

In lack of a better definition, our multiple simulations could be thought of as training in different arenas. It is true that in our model maps take time to form, but this is also the case in novel environments (Barry et al, 2007 ), and continuous attractor models exclusively or strongly guided by self motion cues struggle to replicate this phenomenon. We show that the current version of our model accepts multiple solutions (in practice four but conceptually infinite countable), all of them resulting in a torus for the population activity (i.e. the same topology or low dimensional manifold). It is not clear to us how easy it would be to differentiate between most of these solutions in experimental data, with only incomplete information. This said, incorporating a symmetry-breaking ingredient to the model, for example related to head direction modulation, could perhaps lead to the prevalence of a single type of solution. We intend to explore this possibility in the future in order to add path-integration capabilities to the system, as described in the discussion.

(8) The Discussion implies that 1D networks could perform path integration in a manner similar to 2D networks. This is a strong claim but isn't supported by evidence in the study. I suggest either providing evidence that this is the case for models of this kind or replacing it with a more careful discussion of the issue.

The current version of our model has no path integration capabilities, as is now made explicit in the Introduction and Discussion. In addition, we have now made clear that the idea that path integration could perhaps be implemented using 1D networks is, although reasonable, purely speculative.

Minor

(1) Introduction. 'direct excitatory communication between them'. Suggest rewording to 'local synaptic interactions', as communication can also be purely inhibitory (e.g. Burak and Fiete, 2009) or indirect by excitation of local interneurons (e.g. Pastoll et al., Neuron, 2013).

We agree and have adopted this phrasing.

(2) The decision to focus the topology analysis on the 60 cm wide central square appears somewhat arbitrary. Are the irregularities referred to a property of the trained networks or would they also emerge with analysis of simulated ideal data? Can more justification be expanded and supplementary analyses be shown when the whole arena is used?

In practical terms, a subsampling of the data to around half was needed because the persistent homology packages struggle to handle large amounts of data, especially in the calculation of H2. We decided to cut a portion of contiguous pixels in the open field at least larger than the hexagonal tile representing the whole grid population period (as represented in Figure 6). Leaving the borders aside was a logical choice since it is known that the solution at the borders is particularly influenced by the speed anisotropy of the virtual rat (see Si, Kropff & Treves, 2012), in a way that mimics how borders locally influence grid maps in actual rats (Krupic et al, 2015). The specific way in which our virtual rat handles borders is arbitrary and might not generalize. A second issue around borders is that maps are differently affected by incomplete smoothing, although this issue does not apply to our data because we did not smooth across neighboring pixels. In sum, considering the central 60 cm wide square was sufficient to contain the whole torus and a reasonable compromise that would allow us to perform all analyses in the part of the environment less influenced by boundaries.

(3) It could help the general reader to briefly explain what a persistence diagram is.

This is developed in the Appendix, but we have now added a reference to it and a brief description in the main text.

(4) For the analyses in Figure 3-4, and separately for Figure 5, it might help the reader to provide visualizations of the low dimensional point cloud.

All these calculations take place in the original high-dimensional point cloud. Doing them in a reduced space would be incorrect because there is no dimensionality reduction technique that guarantees the preservation of topology. In Figure 7 we reduce the dimensionality of data but emphasize that it is only done for visualization purposes, not to characterize topology. We also point out in this Figure that the same non-linear dimensionality reduction technique applied to objects with identical topology yields a wide variety of visualizations, some of them clear and some less clear. This observation further exemplifies why one cannot assume that a dimensionality-reduction technique preserves topology, even for a low-dimensional object embedded in a high-dimensional space.

(5) The detailed comparison of the dynamics of each model is limited by the number of data points. Why not address this by new simulations with more neurons?

We are not sure we understand this comment. In Figure 2, the dynamics for each model are markedly different. These are averages over 100 simulations. We are not sure what benefit would be obtained from adding more neurons. Before starting this work we searched for the minimal number of neurons that would result in convergence to an aligned solution in 2D networks, which we found to be around 100. Optimizing this parameter in advance was important to reduce computational costs throughout our work.

(6) Could the variability in Figure 7 also be addressed by increasing the number of data points?

As we argued in a previous point, there is no reason to expect preservation of topology after applying Isomap. We believe this lack of topology preservation to be the main driver of variability.

(7) Page/line numbers would be useful.

We agree. However, the text is curated by biorxiv which, to our best knowledge, does not include them.

Reviewer 2:

Reviewer #2 (Recommendations For The Authors):

(1) I highly suggest that the author rewrite some parts of the Results. There are lots of details which should be put into the Methods part, for example, the implementation details of the network, the analysis details of the toroidal topology, etc. It will be better to focus on the results part first in each section, and then introduce some of the key details of achieving these results, to improve the readability of the work.

This suggestion contrasts with that of Reviewer #1. As a compromise, we decided to include in the Results section only methodological details that are key to understanding the conclusions, and describe everything else in the Methods section.

(2) 'Progressive increase in gridness and decrease in spacing across days have been observed in animals familiarizing with a novel environment...' From Fig.2c I didn't see much decrease. The authors may need to carry out some statistical test to prove this. Moreover, even the changes are significant, this might be not the consequence of the excitatory collateral constraint. To prove this, the authors may need to offer some direct evidence.

We agree that the decrease is not evident in this figure due to the scale, so we are adding the correlation in the figure caption as proof. In addition, several arguments, some related to new analyses, demonstrate that the attractor contracts grid maps. First, the ‘no attractor’ condition has a markedly larger spacing compared to all other conditions (Fig. 2a). We also now show that spacing monotonically decreases with the strength of recurrent relative to feedforward weights, in a way that is rather independent of gridness (Fig. S2a). Second, as we now show in Fig. S2b-d, simulations with a shuffled 1D attractor, such that the sum of input synapses to each neuron are the same as in the 1D condition but no structure is present, lead to a spacing that is mid-way between the ‘no attractor’ condition and the conditions with attractors. Third, as we now show in Fig. S3a, turning off both recurrent connections and feedforward learning in a trained network results in a small increase in spacing. Fourth, as we now show in Fig. S3b, turning off recurrent connections while feedforward learning is kept on increases grid spacing to levels comparable to those of the ‘no attractor’ condition. All these elements support a role of the attractor in contracting grid spacing.

(3) Some of the items need to be introduced first before going into details in the paper, for instance, the stipe-like attractor network, the Betti number, etc.

We have added in the Results section a brief description and references to full developments in the Appendix.

Reviewer 3 (Public Review):

(1) It is not clear to me that the proposal here is fundamentally new. In Si, Kropff and Treves (2012) recurrent connectivity was dependent on the head direction tuning and thus had a ring structure. Urdapilleta, Si, and Treves considered connectivity that depends on the distance on a 2d plane.

In the work of Si et al connectivity is constructed ad-hoc for conjunctive cells to represent a torus, it depends on head-directionality but also on the distance in a 2D plane. The topology of this architecture has not been assessed, but it is close to the typical 2D ‘rigid’ constraint. In the work of Urdapilleta et al, the network is a simple 2D one. The difference with our work is that we focus on the topology of the recurrent network and do not use head-direction modulation. In this context, we prove that a 1D network is enough to align grid cells and, more generally, we provide a proof of principle that the topology of the architecture and the representation space of an attractor network do not need to be identical, as previously assumed by the attractor community. These two important points were neither argued, speculated nor self-evident from the cited works.

(2) The paper refers to the connectivity within the grid cell layer as an attractor. However, would this connectivity, on its own, indeed sustain persistent attractor states? This is not examined in the paper. Furthermore, is this even necessary to obtain the results in the model? Perhaps weak connections that do not produce an attractor would be sufficient to align the spatial response patterns during the learning of feedforward weights, and reproduce the results? In general, there is no exploration of how the strength of collateral interactions affects the outcome.

The reviewer makes several important points. Local excitation combined with global inhibition is the archetypical architecture for continuous attractors (see for example Knierim and Zhang, Annual review of neuroscience, 2012). Thus, in the absence of feedforward input, we observe a bump of activity. As in all continuous attractors, this bump is not necessarily ‘persistent’ and instead is free to move along the attractor.

We cannot prove that there is not a simpler architecture that has the same effect as our 1D or 1DL conditions, and we think that there are some interesting candidates to investigate in the future. What we now prove in new Fig. S2b-d is that it is not the strength of recurrent connections themselves, but instead the continuous attractor structure that aligns grid cells in our model. To demonstrate this, we shuffle incoming recurrent connections to each neuron in the 1D condition (while avoiding self-connections for fairness), and show that training does not lead to grid alignment. We also show in Fig. S1 that an architecture represented by 20 overlapping 1DL attractors, each formed by concatenating 10 random cells, aligns grid cells to levels slightly lower but similar to the 1D or 1DL attractors. This architecture can perhaps be considered as simpler to build in biological terms than all the others, but it is still constituted by continuous attractors.

The strength of recurrent collaterals, or more precisely the recurrent to feedforward ratio, is crucial in our model to achieve a negotiated outcome from constraints imposed by the attractor and the inputs. We now show explicit measures of this ratio in Fig. S2, as well as examples showing that an imbalance in this ratio impairs grid alignment. When the ratio is too high or too low, both individual and population gridness are low. Interestingly, grid spacing behaves differently, decreasing monotonically with the relative strength of recurrent connections.

(3) I did not understand what is learned from the local topology analysis. Given that all the grid cells are driven by an input from place cells that spans a 2d manifold, and that the activity in the grid cell network settles on a steady state that depends only on the inputs, isn't it quite obvious that the manifold of activity in the grid cell layer would have, locally, a 2d structure?

The dimensionality of the input is important, although not the only determinant of the topology of the activity. The recurrent collaterals are the other determinant, and their architecture is a crucial feature. For example, as we now show in Figure S2b-d, shuffled recurrent synaptic weights fail to align grid cells. In the 1D condition, if feedforward inputs were absent, the dynamics of the activity would be confined to a ring. The opposite condition is our ‘no attractor’ condition, in which activity in the grid cell layer mimics the topology of inputs, a 2D sheet (and not a torus). It is in the intermediate range, when both feedforward and recurrent inputs are important, that a negotiated solution (a torus) is achieved.

The analyses of local dimensionality and local homology of Figure 3 are crucial steps to demonstrate toroidal topology. According to the theorem of classification of closed surfaces, global homology is not enough to univocally define the topology of a point cloud, and thus this step cannot be skipped. The step is aimed to prove that the point cloud is indeed a closed surface.

(4) The modeling is all done in planar 2d environments, where the feedforward learning mechanism promotes the emergence of a hexagonal pattern in the single neuron tuning curve. This, combined with the fact that all neurons develop spatial patterns with the same spacing and orientation, implies even without any topological analysis that the emerging topology of the population activity is a torus.

We cannot agree with this intuition. In the ‘no attractor’ condition, individual maps have hexagonal symmetry with standardized spacing, but given the lack of alignment the population activity is not a closed surface and thus not a torus. It can rather be described as a 2D sheet embedded in a high dimensional space, a description that also applies to the input space.

While it is rather evident that an ad hoc toroidal architecture folds this 2D population activity into a torus, it is less evident and rather surprising that 1D architectures have the same capability. This is the main novelty in our work.

(5) Moreover, the recent work of Gardner et al. demonstrated much more than the preservation of the topology in the different environments and in sleep: the toroidal tuning curves of individual neurons remained the same in different environments. Previous works, that analyzed pairwise correlations under hippocampal inactivation and various other manipulations, also pointed towards the same conclusion. Thus, the same population activity patterns are expressed in many different conditions. In the present model, the results of Figure 6 suggest that even across distinct rectangular environments, toroidal tuning curves will not be preserved, because there are multiple possible arrangements of the phases on the torus which emerge in different simulations.

We agree with the reviewer in the main point, although the recently found ring activity in the absence of sensory feedback (Gonzalo Cogno et al, 2023) suggests that what is happening in the EC is more nuanced than a pre-wired torus. Solutions in Figure 6 are different ways of folding a 1D strip into a torus, with or without the condition of periodicity in the 1D strip. Whether or not these different solutions would be discernible from one another in a practical setup is not clear to us. For example, global homology, as addressed in the Gardner paper, is the same for all these solutions. Furthermore, while our solutions of up to order 3 are highly discernable, higher order solutions, potentially achievable with other network parameters, would be impossible to discern by eye in representations similar to the ones in Figure 6. In addition, while we chose to keep our model in the simplest possible form as a clear proof of principle, new elements introduced to the model such as head directionality could break the symmetry and lead to the prevalence of one preferred solution for all simulation replicates. We plan to investigate this possibility in the future when attempting to incorporate path-integration capabilities to the model.

(6) In real grid cells, there is a dense and fairly uniform representation of all phases (see the toroidal tuning of grid cells measured by Gardner et al). Here the distribution of phases is not shown, but Figure 7 suggests that phases are non uniformly represented, with significant clustering around a few discrete phases. This, I believe, is also the origin for the difficulty in identifying the toroidal topology based on the transpose of the matrix M: vectors representing the spatial response patterns of individual neurons are localized near the clusters, and there are only a few of them that represent other phases. Therefore, there is no dense coverage of the toroidal manifold that would exist if all phases were represented equally. This is not just a technical issue, however: there appears to be a mismatch between the results of the model and the experimental reality, in terms of the phase coverage.

As mentioned in the results section, Figure 7 is meant for visualization purposes only, and serves more as cautionary tale regarding the imprevisible risks of non-linear dimensionality reduction than as a proof of the organization of activity in the network. Isomap is a non-linear transformation that deforms each of our solutions in a unique way so that, while all have the topology of a torus embedded in a high dimensional space, only a few of them exhibited one of two possible toroidal visualizations in a 3D Isomap reduction. Isomap, as well as all other popular dimensionality reduction techniques, provide no guarantee of topology invariance. A better argument to judge the homogenous distribution of phases is persistent homology, which identifies relatively large holes (compared to the sampling spacing) in the original manifold embedded in a high dimensional space. In our case, persistent homology identified only two holes significantly larger than noise (the two cycles of a torus) and one cavity in all conditions that included attractors. Regarding the specific distribution of phases in different conditions, however, see our reply below.

(7) The manuscript makes several strong claims that incorrectly represent the relation between experimental data and attractor models, on one hand, and the present model on the other hand. For the latter, see the comments above. For the former, I provide a detailed list in the recommendations to the authors, but in short: the paper claims that attractor models induce rigidness in the neural activity which is incompatible with distortions seen in the spatial response patterns of grid cells. However, this claim seems to confuse distortions in the spatial response pattern, which are fully compatible with the attractor model, with distortions in the population activity patterns, which would be incompatible with the attractor model. The attractor model has withstood numerous tests showing that the population activity manifold is rigidly preserved across conditions - a strong prediction (which is not made, as far as I can see, by feedforward models). I am not aware of any data set where distortions of the population activity manifold have been identified, and the preservation has been demonstrated in many examples where the spatial response pattern is disrupted. This is the main point of two papers cited in the present manuscript: by Yoon et al, and Gardner et al.

First of all, we would like to note that our model is a continuous attractor model. Different attractor models have different outcomes, and one of the main conclusions of our manuscript is that attractors can do a wider range of operations than previously thought.

We agree with the reviewer that distortions in spatial activity (which speak against a purely path-integration guided attractor) should not be confused with distortions in the topology of the population activity (which would instead speak against the attractor dynamics itself). We have rephrased these observations in the manuscript. In fact, we believe that the capacity of grid cells to present distorted maps without a distortion of the population activity topology, as shown for example by Gardner and colleagues, could result from a tension between feedforward and recurrent inputs, the potential equilibriums of which our manuscript aims to characterize.

(8) There is also some weakness in the mathematical description of the dynamics. Mathematical equations are formulated in discrete time steps, without a clear interpretation in terms of biophysically relevant time scales. It appears that there are no terms in the dynamics associated with an intrinsic time scale of the neurons or the synapses, and this introduces a difficulty in interpreting synaptic weights as being weak or strong. As mentioned above, the nature of the recurrent dynamics within the grid cell network (whether it exhibits continuous attractor behavior) is not sufficiently clear.

We agree with the reviewer that our model is rather simple, and we value the extent to which this simplicity allows for a deep characterization. All models are simplifications and the best model in any given setup is the one with the minimum amount of complexity necessary to describe the phenomenon under study. We believe that to understand whether or not a 1D continuous attractor architecture can result in a toroidal population activity, a biophysically detailed model, with prohibitive computational costs, would have been unnecessarily complex. This argument does not intend to demerit biophysically detailed models, which are capable of addressing a wider range of questions regarding, for example, the spiking dynamics of grid cells, which cannot be addressed by our simple model.

Reviewer #3 (Recommendations For The Authors):

The work points to an interesting scenario for the emergence of toroidal topology, but the interpretation of this idea should be more nuanced. I recommend reconsidering the claims about limitations of the attractor theory, and acknowledging the limitations of the present theory.

I don't see the limitations mentioned above as a reason to reject the ideas proposed in this manuscript, for two main reasons: first, additional research might reveal a regime of parameters where some issues can be resolved (e.g. the clustering of phases). In addition, the mechanism described here might act at an early stage in development to set up initial dynamics along a toroidal manifold, while other mechanisms might be responsible for the rigidity of the toroidal manifold in an adult animal. But all this implies that the novelty in the present manuscript is weaker than implied, the ability to explain experimental observations is more limited than implied, and these limitations should be acknowledged and discussed.

I recommend reporting on the distribution of grid cell phases and, if indeed clustered, this should be discussed. It will be helpful to explore whether this is the reason for the difficulty in identifying the toroidal topology based on the collection of spatial response patterns (using the transpose of the matrix M).

Ideally, a more complete work would also explore in a more systematic and parametric way the influence of the recurrent connectivity's strength on the learning, and whether a toroidal manifold emerges also in non-planar, such as the wagon-wheel environment studied in Gardner et al.

Part of these recommendations have been addressed in the previous points (public review). Regarding the reason why the transpose of M does not fully recapitulate architecture with our conservative classification criteria, we believe that there is no reason why it should in the first place. We view the fact that the transpose of M recapitulates some features of the architecture as a purely phenomenological observation, and we think it is important as a proof that M is not exactly the same for the different conditions. We imagined that if M matrices were exactly the same this could be due to poor spatial sampling by our bins. Knowing that they are intrinsically different is important even if the reason why they have these specific features is not fully clear to us.

Although we do not think that the distribution of phases is related to the absence of a cavity in the transpose of M or to the four clusters found in Isomap projections, it remains an interesting question that we did not explore initially. We are now showing examples of the distribution of phases in Figure S1. We observed that in both 2D and 1D conditions phases are distributed following rather regular patterns. Whether or not these patterns are compatible with experimental observations of phase distribution is to our view debatable, given that so far state-of-the-art techniques have only allowed to simultaneously record a small fraction of the neurons belonging to a given module. This said, we think that it is important to note that ordered phase patterns are an anecdotal outcome of our simulations rather than a necessary outcome of flexible attractors or attractors in general. To prove this point, we simulated a condition with a new architecture represented by the overlap of 20 short 1DL attractors, each recruiting 10 random neurons from the pool of 100 available ones.

The rest of the parameters of the simulations were identical to those in the other conditions.

By definition, the topology of this architecture has Betti numbers [20,0,0]. We show in Figure S1 that this architecture aligns grid cells, with individual and population gridness reaching slightly lower levels compared to the 1D condition. However, the distribution of phases of these grid cells has no discernible pattern. This result is an arbitrary example that serves as a proof-of-principle to show that flexible attractors can align grid cells without exhibiting ordered phases, not a full characterization of the outcome of this type of architecture, which we leave for future work. For the rest of our work, we stick to the simplest versions of 1D architectures, which allow for a more in-depth characterization.

The wagon-wheel is an interesting case in which maps loose hexagonal symmetry although the population activity lies in a torus, perhaps evidencing the tension between feedforward and recurrent inputs and suggesting that grid cell response does not obey the single master of path integration. If we modeled it with a 1D attractor, we believe the outcome would strongly depend on virtual rat trajectory. If the trajectory was strictly linear, the population activity would be locally one-dimensional and potentially represented by a ring. Instead, if the trajectory allowed for turns, i.e. a 2D trajectory within a corridor-like maze, the population activity would be toroidal as in our open field simulations, while maps would not have perfect hexagonal symmetry, mimicking experimental results.

More minor comments:

Recurrent dynamics are modeled as if there is no intrinsic synaptic or membrane time constant. This may be acceptable for addressing the goals of this paper, but it is a bit unusual and it will be helpful to explain and justify this choice.

As mentioned above, we believe that the best model in a given setup is the one with the lowest number of complexities that can still address the phenomenon under study. One does not use general relativity to build a bridge, although it provides a ‘more accurate’ description of the physics involved. All models are simplifications, and the more complex a model, the more it has to be taken as a black box.

The Introduction mentions that in most models interaction between co-modular neurons occurs through direct excitatory communication, but in quite a few models the interaction is inhibitory. The crucial feature is that the interaction is strongly inhibitory between neurons that differ in their tuning, and either less inhibitory or excitatory between neurons with similar phases.

We agree that directed inhibition has been shown to be as efficient as directed excitation, and we have modified the introduction to reflect this.

The Discussion claims that the present work is the first one in which the topology of the recurrent architecture differs from the topology of the emergent state space. However, early works on attractor models of grid cells showed how neural connectivity which is arranged on a 2d plane, without any periodic boundary conditions, leads to a state space that exhibits the toroidal topology. Therefore, this claim should be revised.

We agree, although the 2D sheet in this case acts as a piece of the torus, and locally the input space and architecture are identical objects. It could be argued that architectures that represent a 2D local slice of the torus, the whole torus, or several cycles around the torus form a continuous family parametrized by the extension of recurrent connections, and as a consequence it is not surprising that these works have not made claims about the incongruence between architecture and representation topologies. The 2D sheet connectivity is still constructed ad hoc to organize activity in a 2D bump, and there is no negotiation between disparate constraints because locally the constraints imposed by input and architecture are the same. We believe this situation is conceptually different from our flexible 1D attractors. We have adapted our claim to include this technical nuance.

Why are neural responses in the perimeter of the environment excluded from the topological analysis? The whole point of the toroidal manifold analysis on real experimental data is that the toroidal manifold is preserved regardless of the animal's location and behavioral condition.

We agree, although experimental data needs to go through extensive pre-processing such as dimensionality reduction before showing a toroidal topology. Such manipulations might smooth away the specific effects of boundaries on maps, together with other sources of noise. In our case, the original reason to downsample the dataset is related to the explosion in computational time that we experience with the ripser package when using more than ~1000 data points. For a proof-of-principle characterization we were much more interested in what happened in the center of the arena, where a 1D attractor could fold itself to confine population activity into a torus. The area we chose was sufficiently large to contain the whole torus. Borders do affect the way the attractor folds (they also affect grid maps in real rats). We feel that these imperfections could be interesting to study in relation to the parameters controlling how our virtual rat behaves at the borders, but not at this proof-of-principle stage.

The periodic activity observed in Ref. 29 could in principle provide the basis for the ring arrangement of neurons. However, it is not yet clear whether grid cells participate in this periodic activity.

We agree. So far it seems that entorhinal cells in general participate in the ring, which would imply that all kinds of cells are involved. However, it could well be that only some functional types participate in the ring and grid cells specifically do not, as future experiments will tell.

Author response:

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

eLife assessment

This valuable work explores death coding data to understand the impact of COVID-19 on cancer mortality. The work provides solid evidence that deaths with cancer as a contributing cause were not above what would be expected during pandemic waves, suggesting that cancer did not strongly increase the risk of dying of COVID-19. These results are an interesting exploration into the coding of causes of death that can be used to make sense of how deaths are coded during a pandemic in the presence of other underlying diseases, such as cancer.

We thank the editor and reviewers for the time they took to review our manuscript and for the thoughtful suggestions they provided. We have completed several revisions based on their feedback and we feel our paper is stronger as a result. However, none of these revisions change the overall conclusions of our study.

Reviewer #1 (Public Review):

Summary:

In the paper "Disentangling the relationship between cancer mortality and COVID-19", the authors study whether the number of deaths in cancer patients in the USA went up or down during the first year (2020) of the COVID-19 pandemic. They found that the number of deaths with cancer mentioned on the death certificate went up, but only moderately. In fact, the excess with-cancer mortality was smaller than expected if cancer had no influence on the COVID mortality rate and all cancer patients got COVID with the same frequency as in the general population. The authors conclude that the data show no evidence of cancer being a risk factor for COVID and that the cancer patients were likely actively shielding themselves from COVID infections.

Strengths:

The paper studies an important topic and uses sound statistical and modeling methodology. It analyzes both, deaths with cancer listed as the primary cause of death, as well as deaths with cancer listed as one of the contributing causes. The authors argue, correctly, that the latter is a more important and reliable indicator to study relationships between cancer and COVID. The authors supplement their US-wide analysis by analysing three states separately.

Weaknesses:

The main findings of the paper can be summarized as six numbers. Nationally, in 2022, multiple-cause cancer deaths went up by 2%, Alzheimer's deaths by 31%, and diabetes deaths by 39%. At the same time, assuming no relationship between these diseases and either Covid infection risk or Covid mortality risk, the deaths should have gone up by 7%, 46%, and 28%. The authors focus on cancer deaths and as 2% < 7%, conclude that cancer is not a risk factor for COVID and that cancer patients must have "shielded" themselves against Covid infections.

However, I did not find any discussion of the other two diseases. For diabetes, the observed excess was 39% instead of "predicted by the null model" 28%. I assume this should be interpreted as diabetes being a risk factor for Covid deaths. I think this should be spelled out, and also compared to existing estimates of increased Covid IFR associated with diabetes.

And what about Alzheimer's? Why was the observed excess 31% vs the predicted 46%? Is this also a shielding effect? Does the spring wave in NY provide some evidence here? Why/how would Alzheimer's patients be shielded? In any case, this needs to be discussed and currently, it is not.

We thank the reviewer for their positive feedback on the paper and for these suggestions. It is true that we have emphasized the impact on cancer deaths, as this was the primary aim of the paper. In the revised version, we have expanded the results and discussion sections to more fully describe the other chronic conditions we used as comparators (lines 267-284;346 – 386).

Note that we are somewhat reluctant to designate any of these conditions as risk factors based solely on comparing the time series model with the demographic model of our expectations. As we mention in the discussion, there is considerable uncertainty around estimates from the demographic model in terms of the size of the population-at-risk, the mean age of the population-at-risk, and the COVID-19 infection rates and infection fatality ratios. Our demographic model is primarily used to demonstrate the effects of competing risks across types of cancers and chronic conditions, since these findings are robust to model assumptions. In contrast, the demographic model should be used with caution if the goal is to titrate the level of these risk factors (as the level of imputed risk is dependent on model assumptions). In the updated version of the manuscript, we have included uncertainty intervals in Table 3, using the upper and lower bounds of the estimated infection rates and IFRs, to better represent this uncertainty. We have also discussed this uncertainty more explicitly in the text and ran sensitivity analyses with different infection rate assumptions in the discussion (lines 354-362; 367 -370).

We would like to note that rather than interpreting the absolute results, we used this demographic model as a tool to understand the relative differences between these conditions. From the demographic model we determined that we would expect to see much higher mortality in diabetes and Alzheimer’s deaths compared to cancer deaths due to three factors (1. Size of population-at-risk, 2. Mean age of the population-at-risk, 3. Baseline risk of mortality from the condition), that are separate from the COVID-19 associated IFR. And in general, this is what we observed.

In comparing the results from the demographic model to the observed excess, diabetes does standout as an outlier from cancer and Alzheimer’s disease in that the observed excess is consistently above the null hypothesis which does lend support to the conclusion that diabetes is in fact a risk factor for COVID-19. A conclusion which is also supported by many other studies. Our findings for hematological cancers are also similar, in that we find consistent support for this condition being a risk factor. We have commented on this in the discussion and added a few references (lines 346-354; 395-403).

Our hypothesis regarding non-hematological cancer deaths (lower than anticipated mortality due to shielding) could also apply to Alzheimer’s deaths. Furthermore, we used the COVID-19 attack rate for individuals >65 years (based on the data that is available), but we estimate that the mean age of Alzheimer’s patients is actually 80-81 years, so this attack rate may in fact be a bit too high, which would increase our expected excess. We have commented on this in the discussion (lines 363-377).

Reviewer #2 (Public Review):

The article is very well written, and the approach is quite novel. I have two major methodological comments, that if addressed will add to the robustness of the results.

(1) Model for estimating expected mortality. There is a large literature using a different model to predict expected mortality during the pandemic. Different models come with different caveats, see the example of the WHO estimates in Germany and the performance of splines (Msemburi et al Nature 2023 and Ferenci BMC Medical Research Methodology 2023). In addition, it is a common practice to include covariates to help the predictions (e.g., temperature and national holidays, see Kontis et al Nature Medicine 2020). Last, fitting the model-independent for each region, neglects potential correlation patterns in the neighbouring regions, see Blangiardo et al 2020 PlosONE.

Thank you for these comments and suggestions. We agree there are a range of methods that can be used for this type of analysis, and they all come with their strengths, weaknesses, and caveats. Broadly, the approach we chose was to fit the data before the pandemic (2014-2019), and project forward into 2020. To our knowledge it is not a best practice to use an interpolating spline function to extrapolate to future years. This is demonstrated by the WHO estimates in Germany in the paper you mention. This was our motivation for using polynomial and harmonic terms.

Based on the above:

a. I believe that the authors need to run a cross-validation to justify model performance. I would suggest training the data leaving out the last year for which they have mortality and assessing how the model predicts forward. Important metrics for the prediction performance include mean square error and coverage probability, see Konstantinoudis et al Nature Communications 2023. The authors need to provide metrics for all regions and health outcomes.

Thank you for this suggestion. We agree that our paper could be strengthened by including cross validation metrics to justify model performance. Based on this suggestion, and your observations regarding Alzheimer’s disease, we have done two things. First, for the full pre-pandemic period (2014-2019) for each chronic condition and location we tested three different models with different degree polynomials (1. linear only, 2. linear + second degree polynomial, 3. linear + second degree polynomial + third degree polynomial) and used AIC to select the best model for each condition and location. Next, also in response to your suggestion, we estimated coverage statistics. Using the best fit model from the previous step, we then fit the model to data from 2014-2018 only and used the model to predict the 2019 data. We calculated the coverage probability as the proportion of weekly observed data points that fell within the 95% prediction interval. For all causes of death and locations the coverage probability was 100% (with the exception of multiple cause kidney disease in California, which is only shown in the appendix). The methods and results have been updated to reflect this change and we have added a figure to the appendix showing the selected model and coverage probability for each cause of death and location (lines 504 – 519; 847-859; Appendix 1- Figure 11).

b. In the context of validating the estimates, I think the authors need to carefully address the Alzheimer case, see Figure 2. It seems that the long-term trends pick an inverse U-shape relationship which could be an overfit. In general, polynomials tend to overfit (in this case the authors use a polynomial of second degree).It would be interesting to see how the results change if they also include a cubic term in a sensitivity analysis.

Thank you for this observation. Based on the changes described above, the model for Alzheimer’s disease now includes a cubic term in the national data and in Texas and California. The model with the second-degree polynomial remained the best fit for New York (Appendix 1 – Figure 11).

c. The authors can help with the predictions using temperature and national holidays, but if they show in the cross-validation that the model performs adequately, this would be fine.

At the scale of the US, adding temperature or environmental covariates is difficult and few US-wide models do so (see Goldstein 2012 and Quandelacy 2014 for examples from influenza). Furthermore, because we are looking at chronic disease outcomes, it is unclear that viral covariates or national holidays would drive these outcomes in the same way as they would if we were looking at mortality outcomes more directly related to transmissible diseases (such as respiratory mortality). Our cross validation also indicates that our models fit well without these additional covariates.

d. It would be nice to see a model across the US, accounting for geography and spatial correlation. If the authors don't want to fit conditional autoregressive models in the Bayesian framework, they could just use a random intercept per region.

We think the reviewer is mistaken here about the scale of our national analysis. Our national analysis did not fit independent models for each state or region. Rather, we fit a single model to the weekly-level national mortality data where counts for the whole of the US have been aggregated. We have clarified in the text (lines 156, 464). As such, we do not feel a model accounting for spatial correlation would be appropriate nor would we be able to include a random intercept for each region. We did fit three states independently (NY, TX, CA), but these states are very geographically distant from each other and unlikely to be correlated. These states were chosen in part because of their large population sizes, yet even in these states, confidence intervals were very wide for certain causes of death. Fitting models to each of the 50 US states, most of which are smaller than those chosen here, would exacerbate this issue.

(2) I think the demographic model needs further elaboration. It would be nice to show more details, the mathematical formula of this model in the supplement, and explain the assumptions

Thank you for this comment. We have added additional details on the demographic model to the methods. We have also extended this analysis to each state to further strengthen our conclusions (lines 548-590).

Reviewing Editor Recommendations:

I think that perhaps something that is missing is that the authors never make their underlying assumption explicit: they are assuming that if cancer increases the risk of dying of COVID-19, this would be reflected in the data on multiple causes of death where cancer would be listed as one of the multiple causes rather than as the underlying cause, and that their conclusions are predicated on this assumption. I would suggest explicitly stating this assumption, as opposed to other reasons why cancer mortality would increase (ex. if cancer care worsened during pandemic waves leading to poorer cancer survival).

Response: Thank you for this suggestion. We have added a few sentences to the introduction to make this assumption clear (lines 106-112).

Reviewer #1 (Recommendations For The Authors):

- It could make sense to add "in the United States" into the title, as the paper only analyses US data.

- It may make sense to reformulate the title from "disentangling the relationship..." into something that conveys the actual findings, e.g. "Lack of excess cancer mortality during Covid-19 pandemic" or something similar. Currently, the title tells nothing about the findings.

Thank you for these suggestions. We have added “in the US” to the title. However, we feel that our findings are a bit more subtle than the suggested reformulation would imply, and we prefer to leave it in its current form.

- Abstract, lines 42--45: This is the main finding of the paper, but I feel it is simplified too strongly in the abstract. Your simulations do *not* "largely explain" excess mortality with cancer; they give higher numbers! Which you interpret as "shielding" etc., but this is completely absent from the abstract. This sentence makes the impression that you got a good fit between simulated excess and real excess, which I would say is not the case.

Thank you for this comment. We have rephrased the sentence in the abstract to better reflect our intentions for using the demographic model (lines 46-49). As stated above, the purpose of the demographic model was not to give a good fit with the observed excess mortality. Rather, we used the demographic model as a tool to understand the relative differences between these conditions in terms of expected excess mortality given the size, age-distribution, and underlying risk of death from the condition itself, assuming similar IFR and attack rates. And based on this, we conclude that it is not necessarily surprising that we see higher excess mortality for diabetes and Alzheimer’s compared to cancer.

- Results line 237: you write that it's "more consistent with the null hypothesis", however clearly it is *not* consistent with the null hypothesis either (because 2% < 7%). You discuss in the Discussion that it may be due to shielding, but it would be good to have at least one sentence about it already here in the Results, and refer to the Discussion.

We have mentioned this in the results and refer to the discussion (lines 277-278).

- Results line 239: why was it closer to the assumption of relative risk 2? If I understand correctly, your model prediction for risk=1 was 7% and for risk=2 it was 13%. In NY you observed 8% (line 187). How is this closer to risk=2?

Thank you for this observation. We have updated the demographic model with new data, extended the model to state-level data, and included confidence intervals on these estimates. We have also added additional discussion around the differences between our observations and expectations (lines 249-284).

- Discussion line 275: "we did not expect to see large increases" -- why exactly? Please spell it out here. Was it due to the age distribution of the cancer patients? Was it due to the high cancer death risk?

We demonstrate that it is the higher baseline risk of death for cancer that seems to be driving our low expectations for cancer excess mortality (lines 304-320). We have added this to the sentence to clarify our conclusions on this point and have added a figure to better illustrate this concept of competing risks (Figure 6).

- Methods, line 405: perhaps it makes sense to cite some other notable papers on Covid excess mortality such as Msemburi et al Nature 2023, Karlinsky & Kobak eLife 2021, Islam et al BMJ 2021, etc.

Thank you for mentioning this oversight. We certainly should have cited these papers and have included them in the updated version.

- Methods line 410: why did you use a 5-week moving average? Why not fit raw weekly death counts? NB regression should be able to deal with it.

Smoothing time series data with a moving average prior to running regression models is a very common practice. We did a sensitivity analysis using the raw data. This produced excess estimates with slightly larger confidence intervals, but does not change the overall conclusions of the paper.

- Methods line 416: please indicate the software/library/package you used for fitting NB regression.

We fit the NB regression using the MASS package in R version 4.3. We have added this to the methods (line 519).

- Line 489: ORCHID -> ORCID

Author response:

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

Reviewer #1 (Public Review):

Summary:

Codol et al. present a toolbox that allows simulating biomechanically realistic effectors and training Artificial Neural Networks (ANNs) to control them. The paper provides a detailed explanation of how the toolbox is structured and several examples that demonstrate its usefulness.

Main comments:

(1) The paper is well written and easy to follow. The schematics help in understanding how the toolbox works and the examples provide an idea of the results that the user can obtain.

We thank the reviewer for this comment.

(2) As I understand it, the main purpose of the paper should be to facilitate the usage of the toolbox. For this reason, I have missed a more explicit link to the actual code. As I see it, researchers will read this paper to figure out whether they can use MotorNet to simulate their experiments, and how they should proceed if they decide to use it. I'd say the paper provides an answer to the first question and assures that the toolbox is very easy to install and use. Maybe the authors could support this claim by adding "snippets" of code that show the key steps in building an actual example.

This is an important point, which we also considered when writing this paper. We instead decided to focus on the first approach, because it is easier to illustrate the scientific use of the toolbox using code or interactive (Jupyter) notebooks than a publication format. We find the “how to proceed” aspect of the toolbox can more easily and comprehensively be covered using online, interactive tutorials. Additionally, this allows us to update these tutorials as the toolbox evolves over different versions, while it is more difficult to update a scientific article. Consequently, we explicitly avoided code snippets on the article itself. However, we appreciate that the paper would gain in clarity if this was more explicitly stated early. We have modified the paper to include a pointer to where to find tutorials online. We added this at the last paragraph of the introduction section:

The interested reader may consult the full API documentation, including interactive tutorials on the toolbox website at https://motornet.org.

(3) The results provided in Figures 1, 4, 5 and 6 are useful, because they provide examples of the type of things one can do with the toolbox. I have a few comments that might help improving them:

a. The examples in Figures 1 and 5 seem a bit redundant (same effector, similar task). Maybe the authors could show an example with a different effector or task? (see point 4).

The effectors from figures 1 and 5 are indeed very similar. However, the tasks in figure 1 and 5 present some important differences. The training procedure in figure 1 never includes any perturbations, while the one from figure 5 includes a wide range of perturbations of different magnitudes, timing and directions. The evaluation procedure of figure 1 includes center-out reaches with permanent viscous (proportional to velocity) external dynamics, while that of figure 5 are fixed, transient, square-shaped perturbation orthogonal to the reach direction. Finally, the networks in figure 1 undergo a second training procedure after evaluation while the network of figure 5 do not.

While we agree that some variation of effectors would be beneficial, we do show examples of a point-mass effector in figure 6. Overall, figure 5 shows a task that is quite different from that of figure 1 with a similar effector, while the opposite is true for figure 6. We have modified the text to clarify this for the reader, by adding the following.

End of 1st paragraph, section 2.4.

Therefore, the training protocol used for this task largely differed from section 2.1 in that the networks are exposed to a wide range of mechanical perturbations with varying characteristics.

1st paragraph of section 2.5

[…] this asymmetrical representation of PMDs during reaching movements did not occur when RNNs were trained to control an effector that lacked the geometrical properties of an arm such as illustrated in Figure 4c-e and section 2.1.

b. I missed a discussion on the relevance of the results shown in Figure 4. The moment arms are barely mentioned outside section 2.3. Are these results new? How can they help with motor control research?

We thank the reviewer for this comment. This relates to a point from reviewer 2 indicating that the purpose of each section was sometimes difficult to grasp as one reads. Section 2.3 explains the biomechanical properties that the toolbox implements to improve realism of the effector. They are not new results in the sense that other toolboxes implement these features (though not in differentiable formats) and these properties of biological muscles are empirically well-established. However, they are important to understand what the toolbox provides, and consequently what constraints networks must accommodate to learn efficient control policies. An example of this is the results in figure 6, where a simple effector versus a more biomechanically complex effector will yield different neural representations.

Regarding the manuscript itself, we agree that more clarity on the goal of every paragraph may improve the reader’s experience. Consequently, we ensured to specify such goals at the start of each section. Particularly, we clarify the purpose of section 2.3 by adding several sentences on this at the end of the first paragraph in that section. We also now clearly state the purpose of section 2.3 with the results of figure 6 and reference figure 4 in that section.

c. The results in Figure 6 are important, since one key asset of ANNs is that they provide access to the activity of the whole population of units that produces a given behavior. For this reason, I think it would be interesting to show the actual "empirical observations" that the results shown in Fig. 6 are replicating, hence allowing a direct comparison between the results obtained for biological and simulated neurons.

These empirical observations are available from previous electrophysiological and modelling work. Particularly, polar histograms across reaching directions like panel C are displayed in figures 2 and 3 of Scott, Gribble, Graham, Cabel (2001, Nature). Colormaps of modelled unit activity across time and reaching directions like panel F are also displayed in figure 2 of Lillicrap, Scott (2013, Neuron). Electrophysiological recordings of M1 neurons during a similar task in non-human primates can also be seen on “Preserved neural population dynamics across animals performing similar behaviour” figure 2 B (https://doi.org/10.1101/2022.09.26.509498) and “Nonlinear manifolds underlie neural population activity during behaviour” figure 2 B as well (https://doi.org/10.1101/2023.07.18.549575). Note that these two pre-prints use the same dataset.

We have added these citations to the text and made it explicit that they contain visualizations of similar modelling and empirical data for comparison:

This heterogeneous set of responses matches empirical observations in non-human primate primary motor cortex recordings (Churchland & Shenoy, 2007; Michaels et al., 2016) and replicate similar visualizations from previously published work (Fortunato et al., 2023; Lillicrap & Scott, 2013; Safaie et al., 2023).

(4) All examples in the paper use the arm26 plant as effector. Although the authors say that "users can easily declare their own custom-made effector and task objects if desired by subclassing the base Plant and Task class, respectively", this does not sound straightforward. Table 1 does not really clarify how to do it. Maybe an example that shows the actual code (see point 2) that creates a new plant (e.g. the 3-joint arm in Figure 7) would be useful.

Subclassing is a Python process more than a MotorNet process, as python is an object-oriented language. Therefore, there are many Python tutorials on subclassing in the general sense that would be beneficial for that purpose. We have amended the main text to ensure that this is clearer to the reader.

Subclassing a MotorNet object, in a more specific sense, requires overwriting some methods from the base MotorNet classes (e.g., Effector or Environment classes, which correspond to the original Plant and Task object, respectively). Since we made the decision (mentioned above) to not include code in the main text, we added tutorials to the online documentation, which include dedicated tutorials for MotorNet class subclassing. For instance, this tutorial showcases how to subclass Environment classes:

https://colab.research.google.com/github/OlivierCodol/MotorNet/blob/master/examples/3-environments.ipynb

(5) One potential limitation of the toolbox is that it is based on Tensorflow, when the field of Computational Neuroscience seems to be, or at least that's my impression, transitioning to pyTorch. How easy would it be to translate MotorNet to pyTorch? Maybe the authors could comment on this in the discussion.

We have received a significant amount of feedback asking for a PyTorch implementation of the toolbox. Consequently, we decided to enact this, and the next version of the toolbox will be exclusively in PyTorch. We will maintain the Application Programming Interface (API) and tutorial documentation for the TensorFlow version of the toolbox on the online website. However, going forward we will focus exclusively on bug-fixing and expanding from the latest version of MotorNet, which will be in PyTorch. We now believe that the greater popularity of PyTorch in the academic community makes that choice more sustainable while helping a greater proportion of research projects.

These changes led to a significant alteration of the MotorNet structure, which are reflected by changes made throughout the manuscript, notably in Figure 3 and Table 1.

(6) Supervised learning (SL) is widely used in Systems Neuroscience, especially because it is faster than reinforcement learning (RL). Thus providing the possibility of training the ANNs with SL is an important asset of the toolbox. However, SL is not always ideal, especially when the optimal strategy is not known or when there are different alternative strategies and we want to know which is the one preferred by the subject. For instance, would it be possible to implement a setup in which the ANN has to choose between 2 different paths to reach a target? (e.g. Kaufman et al. 2015 eLife). In such a scenario, RL seems to be a more natural option Would it be easy to extend MotorNet so it allows training with RL? Maybe the authors could comment on this in the discussion.

The new implementation of MotorNet that relies on PyTorch is already standardized to use an API that is compatible with Gymnasium. Gymnasium is a standard and popular interfacing toolbox used to link RL agents to environments. It is very well-documented and widely used, which will ensure that users who wish to employ RL to control MotorNet environments will be able to do so relatively effortlessly. We have added this point to accurately reflect the updated implementation, so users are aware that it is now a feature of the toolbox (new section 3.2.4.).

Impact:

MotorNet aims at simplifying the process of simulating complex experimental setups to rapidly test hypotheses about how the brain produces a specific movement. By providing an end-to-end pipeline to train ANNs on the simulated setup, it can greatly help guide experimenters to decide where to focus their experimental efforts.

Additional context:

Being the main result a toolbox, the paper is complemented by a GitHub repository and a documentation webpage. Both the repository and the webpage are well organized and easy to navigate. The webpage walks the user through the installation of the toolbox and the building of the effectors and the ANNs.

Reviewer #2 (Public Review):

MotorNet aims to provide a unified interface where the trained RNN controller exists within the same TensorFlow environment as the end effectors being controlled. This architecture provides a much simpler interface for the researcher to develop and iterate through computational hypotheses. In addition, the authors have built a set of biomechanically realistic end effectors (e.g., an 2 joint arm model with realistic muscles) within TensorFlow that are fully differentiable.

MotorNet will prove a highly useful starting point for researchers interested in exploring the challenges of controlling movement with realistic muscle and joint dynamics. The architecture features a conveniently modular design and the inclusion of simpler arm models provides an approachable learning curve. Other state-of-the-art simulation engines offer realistic models of muscles and multi-joint arms and afford more complex object manipulation and contact dynamics than MotorNet. However, MotorNet's approach allows for direct optimization of the controller network via gradient descent rather than reinforcement learning, which is a compromise currently required when other simulation engines (as these engines' code cannot be differentiated through).

The paper could be reorganized to provide clearer signposts as to what role each section plays (e.g., that the explanation of the moment arms of different joint models serves to illustrate the complexity of realistic biomechanics, rather than a novel discovery/exposition of this manuscript). Also, if possible, it would be valuable if the authors could provide more insight into whether gradient descent finds qualitatively different solutions to RL or other non gradient-based methods. This would strengthen the argument that a fully differentiable plant is useful beyond improving training time / computational power required (although this is a sufficiently important rationale per se).

We thank the reviewer for these comments. We agree that more clarity on the section goals may improve the reader’s experience and ensured this is the case throughout the manuscript. Particularly, we added the following on the first paragraph of section 2.3, for which an explicit goal was most missing:

In this section we illustrate some of these biomechanical properties displayed by MotorNet effectors using specific examples. These properties are well-characterised in the biology and are often implemented in realistic biomechanical simulation software.

Regarding the potential difference in solutions obtained from reinforcement or supervised learning, this would represent a non-trivial amount of work to do so conclusively and so may not be within the scope of the current article. We do appreciate however that in some situations RL may be a more fitting approach to a given task design. In relation to this point we now specify in the discussion that the new API can accommodate interfacing with reinforcement learning toolboxes for those who may want to pursue this type of policy training approach when appropriate (new section 3.2.4.).

Reviewer #3 (Public Review):

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

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

The possibility of adding code snippets to the article is something we originally considered, and which aligns with comment two from reviewer one (see above). Hopefully this provides a good overview of the motivation behind our choice not to add code to the article.

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

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

We thank the reviewer for these comments.

Author response:

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

Reviewer #1 (Public Review):

The authors sought to test whether anterior insular cortex neurons increase or decrease firing during fear behavior and freezing, bi-directionally control fear via separate, anatomically defined outputs. Using a fairly simple behavior where mice were exposed to tone-shock pairings, they found roughly equal populations that do indeed either increase or decrease firing during freezing. Next, they sought to test whether these distinct populations may also have distinct outputs. Using retrograde tracers they found that the anterior insular cortex contains non-overlapping neurons which project to the mediodorsal thalamus or amygdala. Mediodorsal thalamus-projecting neurons tended to cluster in deep cortical layers while amygdala-projecting neurons were primarily in more superficial layers. Stimulation of insula-thalamus projection decreased freezing behavior, and stimulation of insula-amygdala projections increased fear behavior. Given that the neurons that increased firing were located in deep layers, that thalamus projections occurred in deep layers, and that stimulation of insula-thalamus neurons decreased freezing, the authors concluded that the increased firing neurons may be thalamus projections. Similarly, given that decreased-firing neurons tended to occur in more superficial layers, that insula-amygdala projections were primarily superficial, and that insula-amygdala stimulation increased freezing behavior, authors concluded that the decreased firing cells may be amygdala projections. The study has several strengths though also some caveats.

Strengths:

The potential link between physiological activity, anatomy, and behavior is well laid out and is an interesting question. The activity contrast between the units that increase/decrease firing during freezing is clear.

It is nice to see the recording of extracellular spiking activity, which provides a clear measure of neural output, whereas similar studies often use bulk calcium imaging, a signal that rarely matches real neural activity even when anatomy suggests it might (see London et al 2018 J Neuro - there are increased/decreased spiking striatal populations, but both D1 and D2 striatal neurons increase bulk calcium).

Weaknesses:

The link between spiking, anatomy, and behavior requires assumptions/inferences: the anatomically/genetically defined neurons which had distinct outputs and opposite behavioral effects can only be assumed the increased/decreased spiking neurons, based on the rough area of the cortical layer they were recorded.

Yes, we are aware that we could not provide a direct link between spiking, anatomy and behavior. We have specifically noted this in the discussion section and added a possible experiment that could be carried out to provide a more direct link in a future study.

[Lines 371-375] We would like to provide a more direct evidence between the neuronal response types and projection patterns in future studies by electrophysiologically identifying freezing-excited and freezing-inhibited aIC neurons and testing whether those neurons activates to optogenetic activation of amygdala or medial thalamus projecting aIC neurons.

The behavior would require more control to fully support claims about the associative nature of the fear response (see Trott et al 2022 eLife) - freezing, in this case, could just as well be nonassociative. In a similar vein, fixed intertrial intervals, though common practice in the fear literature, pose a problem for neurophysiological studies. The first is that animals learn the timing of events, and the second is that neural activity is dynamic and changes over time. Thus it is very difficult to determine whether changes in neural activity are due to learning about the tone-shock contingency, timing of the task, simply occur because of time and independently of external events, or some combination of the above.

Trott et al. (2022) stated that "...freezing was the purest reflection of associative learning." The nonassociative processes mentioned in the study were related to running and darting behaviors, which the authors argue are suppressed by associative learning. Moreover, considerable evidence from immediate postshock freezing and immediate postshock context shift studies all indicate that the freezing response is an associative (and not nonassociative) response (Fanselow, 1980 and 1986; and Landeira-Fernandez et al., 2006). Thus, our animals' freezing response to the tone CS presentation in a novel context, following three tone CS-footshock US pairings, most likely reflects associative learning. 

Concerning the issue of fixed inter-trial intervals (ITIs), which are standard in fear conditioning studies, particularly those with few CS-US paired trials, we acknowledge the challenge in interpreting the neural correlates of behavior. However, the ITIs in our extinction study was variable and we still found neural activities that had significant correlation with freezing. The results of our extinction study, carried out with variable it is, suggest that the aIC neural activity changes measured in this study is likely due to freezing behavior associated with fear learning, not due to learning the contingencies of fixed ITIs.

Reviewer #2 (Public Review):

In this study, the authors aim to understand how neurons in the anterior insular cortex (insula) modulate fear behaviors. They report that the activity of a subpopulation of insula neurons is positively correlated with freezing behaviors, while the activity of another subpopulation of neurons is negatively correlated to the same freezing episodes. They then used optogenetics and showed that activation of anterior insula excitatory neurons during tones predicting a footshock increases the amount of freezing outside the tone presentation, while optogenetic inhibition had no effect. Finally, they found that two neuronal projections of the anterior insula, one to the amygdala and another to the medial thalamus, are increasing and decreasing freezing behaviors respectively. While the study contains interesting and timely findings for our understanding of the mechanisms underlying fear, some points remain to be addressed.

We are thankful for the detailed and constructive comments by the reviewer and addressed the points. Specifically, we included possible limitations of using only male mice in the study, included two more studies about the insula as references, specified the L-ratio and isolated distance used in our study, added the ratio of putative-excitatory and putative-inhibitory neurons obtained from our study, changed the terms used to describe neuronal activity changes (freezing-excited and freezing-inhibited cells), added new analysis (Figure 2H), rearranged Figure 2 for clarity, added new histology images, and added atlas maps with viral expressions (three figure supplements).

Reviewer #1 (Recommendations For The Authors):

- I would suggest keeping the same y-axis for all figures that display the same data type - Figure 5D, for example.

Thank you for the detailed suggestion. We corrected the y-axis that display the same data type to be the same for all figures.

- In the methods, it says 30s bins were used for neural analysis (line 435). I cannot imagine doing this, and looking at the other figures, it does not look like this is the case so could you please clarify what bins, averages, etc were used for neural and behavioral analysis?

Bin size for neural analysis varied; 30s, 5s, 1s bins were used depending on the analysis. We corrected this and specified what time bin was used for which figure in the methods.

Bin size for neural and freezing behavior was 30s and we also added this to the methods.

- I would not make any claims about the fear response here being associative/conditional. This would require a control group that received an equal number of tone and shock exposures, whether explicitly unpaired or random.

The unpaired fear conditioning paradigm, unpaired tone and shock, suggested by the reviewer is well characterized not to induce fear behavior by CS (Moita et al., 2003 and Kochli et al., 2015). In addition, considerable evidence from immediate post-shock freezing and immediate post-shock context shift studies all indicate that the freezing response is an associative (and not nonassociative) response (Fanselow, 1980 and 1986; and Landeira-Fernandez et al., 2006). Thus, our animals' freezing response to the tone CS presentation in a novel context, following three tone CS-footshock US pairings, most likely reflects associative learning.

- I appreciate the discussion about requiring some inference to conclude that anatomically defined neurons are the physiologically defined ones. This is a caveat that is fully disclosed, however, I might suggest adding to the discussion that future experiments could address this by tagging insula-thalamus or insula-amygdala neurons with antidromic (opto or even plain old electric!) stimulation. These experiments are tricky to perform, of course, but this would be required to fully close all the links between behavior, physiology, and anatomy.

As suggested, we have included that, in a future study, we would like to elucidate a more direct link between physiology, anatomy and behaviors by optogenetically tagging the insula-thalamus/insula-amygdala neurons and identifying whether it may be a positive or a negative cell (now named the freezing-excited and freezing-inhibited cells, respectively) in the discussion.

[Lines 371-375] We would like to provide a more direct evidence between the neuronal response types and projection patterns in future studies by electrophysiologically identifying freezing-excited and freezing-inhibited aIC neurons and testing whether those neurons activates to optogenetic activation of amygdala or medial thalamus projecting aIC neurons.

Reviewer #2 (Recommendations For The Authors):

Major comments:

(1) As all experiments have been performed only in male mice, the authors need to clearly state this limit in the introduction, abstract, and title of the manuscript.

With increasing number of readers becoming interested in the biological sex used in preclinical studies, we also feel that it should be mentioned in the beginning of the manuscript. As suggested, we explicitly wrote that we only used male mice in the title, abstract, and introduction. In addition, we discussed possible limitations of only using male mice in the discussion section as follows:

[Lines 381-386] Another factor to consider is that we have only used male mice in this study. Although many studies report that there is no biological sex difference in cued fear conditioning (42), the main experimental paradigm used in this study, it does not mean that the underlying brain circuit mechanism would also be similar. The bidirectional fear modulation by aIC→medial thalamus or the aIC→amygdala projections may be different in female mice, as some studies report reduced cued fear extinction in females (42).

(2) The authors are missing important publications reporting findings on the insular cortex in fear and anxiety. For example, the authors should cite studies showing that anterior insula VIP+ interneurons inhibition reduces fear memory retrieval (Ramos-Prats et al., 2022) and that posterior insula neurons are a state-dependent regulator of fear (Klein et al., 2021). Also, regarding the anterior insula to basolateral amygdala projection (aIC-BLA), the author should include recent work showing that this population encodes both negative valence and anxiogenic spaces (Nicolas et al., 2023). 

We appreciate the detailed suggestions and we added appropriate publications in the discussion section. The anterior insula VIP+ interneuron study (Ramos-Prats et al., 2022) is interesting, but based on the evidence provided in the paper, we felt that the role of aIC VIP+ interneuron in fear conditioning is low. VIP+ interneurons in the aIC seem to be important in coding sensory stimuli, however, it’s relevance to conditioned stimuli seems to be low; overall VIP intracellular calcium activity to CS was low and did not differ between acquisition and retrieval. Also, inhibition of VIP did not influence fear acquisition. VIP inhibition during fear acquisition did reduce fear retrieval (CS only, no light stimulation), but this does not necessarily mean that VIP activity will be involved in fear memory storage or retrieval, especially because intracellular calcium activity of VIP+ neurons was low during fear conditioning and retrieval.

Studies by Klein et al. (2021) and Nicolas et al. (2023) are integrated in the discussion section as follows.

[Lines 297-301] Group activity of neurons in the pIC measured with fiberphotometry, interestingly, exhibited fear state dependent activity changes—decreased activity with high fear behavior and increased activity with lower fear behavior (29)—suggesting that group activity of the pIC may be involves in maintain appropriate level of fear behavior.

[Lines 316-319] Another distinction between the aIC and pIC may be related with anxiety, as a recent study showed that group activity of aIC neurons, but not that of the pIC, increased when mice explored anxiogenic space (open arms in an elevated plus maze, center of an open field box) (32).

(3) The authors should specify how many neurons they excluded after controlling the L-ratio and isolation distance. It is also important to specify the percentage of putative excitatory and inhibitory interneurons recorded among the 11 mice based on their classification (the number of putative inhibitory interneurons in Figure 1D seems too low to be accurate).

We use manual cluster cutting and only cut clusters that are visually well isolated. So we hardly have any neurons that are excluded after controlling for L-ratio and isolation distance. The criterion we used was L-ratio<0.3 and isolation distance>15, and we specified this in the methods as follows.

[Lines 454-458] We only used well-isolated units (L-ratio<0.3, isolation distance>15) that were confirmed to be recorded in the aIC (conditioned group: n = 116 neurons, 11 mice; control group: n = 14 neurons, 3 mice) for the analysis (46). The mean of units used in our analysis are as follows: L-ratio = 0.09 ± 0.012, isolation distance = 44.97 ± 5.26 (expressed as mean ± standard deviation).

As suggested, we also specified the percentage of putative excitatory and inhibitory interneurons recorded from our study in the results and methods section. The relative percentage of putative excitatory and inhibitory interneurons were similar for both the conditioned and the control groups (conditioned putative-excitatory: 93.1%, putative-inhibitory: 6.9%; control putative-excitatory: 92.9%, putative-inhibitory: 7.1%). Although the number of putative-interneurons isolated from our recordings is low that is what we obtained. Putative inhibitory neurons, probably because of their relatively smaller size, has a tendency to be underrepresented than the putative excitatory cells.

[Lines 83-87] Of the recorded neurons, we analyzed the activity of 108 putative pyramidal neurons (93% of total isolated neurons) from 11 mice, which were distinguished from putative interneurons (n = 8 cells, 7% of total isolated neurons) based on the characteristics of their recorded action potentials (Figure 1D; see methods for details).

[Lines 464-467] The percentage of putative excitatory neurons and putative inhibitory interneurons obtained from both groups were similar (conditioned putative-excitatory: 93.1%, putative-inhibitory: 6.9%; control putative-excitatory: 92.9%, putative-inhibitory: 7.1%).

(4) While the use of correlation of single-unit firing frequency with freezing is interesting, classically, studies analyze the firing in comparison to the auditory cues. If the authors want to keep the correlation analysis with freezing, rather than correlations to the cues, they should rename the cells as "freezing excited" and "freezing inhibited" cells instead of positive and negative cells.

As suggested, we used the terms “freezing-excited” and “freezing-inhibited” cells instead of positive and negative cells.

(5) To improve clarity, Figure 2 should be reorganized to start with the representative examples before including the average of population data. Thus Panel D should be the first one. The authors should also consider including the trace of the firing rate of these representative units over time, on top of the freezing trace, as well as Pearson's r and p values for both of them. Then, the next panels should be ordered as follows: F, G, H, C, A, B, I, and finally E.

We have rearranged Figure 2 based on the suggestions.

(6) It is unclear why the freezing response in Figure 2 is different in current panels F, G, and H. Please clarify this point.

It was because the freezing behaviors of slightly different population of animals were averaged. Some animals did not have positive/negative (or both) cells and only the behavior of animals with the specified cell-type were used for calculating the mean freezing response. With rearrangement of Figure 2, now we do not have plots with juxtaposed mean neuronal response-types and behavior.

(7) Even though the peak of tone-induced firing rate change between negative and positive cells is 10s later for positive cells, the conclusion that this 'difference suggests differential circuits may regulate the activities of different neuron types in response to fear' is overstating the observation. This statement should be rephrased. Indeed, it could be the same circuits that are regulated by different inputs (glutamatergic, GABA, or neuromodulatory inputs).

We agree and delete the statement from the manuscript.

(8) The authors mention they did not find tone onset nor tone offset-induced responses of anterior insula neurons. It would be helpful to represent this finding in a Figure, especially, which were the criteria for a cell to be tone onset or tone offset responding.

We added how tone-onset and tone-offset were analyzed in the methods section and added a plot of the analysis in Figure 2H.

(9) Based on the spread of the viral expression shown in Figure 3B, it appears that the authors are activating/inhibiting insula neurons in the GI layer, whereas single-unit recordings report the electrodes were located in DI, AID, and AIV layers. The authors should provide histology maps of the viral spread for ChR2, NpHR3, and eYFP expression.

Thank you for the excellent suggestion. Now the histological sample in Figure 3B is a sample with expression in the GI/DI/AID layers and it also has an image taken at higher resolution (x40) to show that viral vectors are expressed inside neurons. We also added histological maps with overlay of viral expression patterns of the ChR2, eYFP, and NpHR3 groups in Figure 3—figure supplement 1.

(10) In Figure 5B, the distribution of terminals expressing ChR2 appears much denser in CM than in MD. This should be quantified across mice and if consistent with the representative image, the authors should refer to aIC-CM rather than aIC-MD terminals.

Overall, we referred to the connection as aIC-medial thalamus, which collectively includes both the CM and the MD. Microscopes we have cannot determine whether terminals end at the CM or MD, but the aIC projections seems to pass through the CM to reach the MD. The Allen Brain Institute’s Mouse brain connectivity map (https://connectivity.brain-map.org/projection/experiment/272737914) of a B6 mouse, the mouse strain we used in our study, with tracers injected in similar location as our study also supports our speculation and shows that aIC neuronal projections terminate more in the MD than in the CM. In addition, the power of light delivered for optogenetic manipulation is greatly reduced over distance, and therefore, the MD projecting terminals which is closer to the optic fiber will be more likely to be activated than the CM projecting terminals. However, since we could not determine whether the aIC terminate at the CM or the MD, we collectively referred to the connection as the aIC-medial thalamus throughout the manuscript.

Author response image 1.

(11) Histological verifications for each in vivo electrophysiology, optogenetic, and tracing experiments need to include a representative image of the implantation/injection site, as well as a 40x zoom-in image focusing on the cell bodies or terminals right below the optic fiber (for optogenetic experiments). Moreover, an atlas map including all injection locations with the spread of the virus and fiber placement should be added in the Supplement Figures for each experiment (see Figure S1 Klein et al., 2021). Similarly, the authors need to add a representation of the spread of the retrograde tracers for each mouse used for this tracing experiment.

As suggested, we added a histology sample showing electrode recording location for in-vivo electrophysiology in Figure 1 and added atlas maps for the optogenetic and tracing experiments in supplementary figures. We also provide a 40x zoom-in image of the expression pattern for the optogenetic experiments (Figure 3B).

(12) To target anterior insula neurons, authors mention coordinates that do not reach the insula on the Paxinos atlas (AP: +1.2 mm, ML: -3.4 mm, DV: -1.8 mm). If the DV was taken from the brain surface, this has to be specified, and if the other coordinates are from Bregma, this also needs to be specified. Finally, the authors cite a review from Maren & Fanselow (1996), for the anterior insula coordinates, but it remains unclear why.

AP and ML coordinates are measurement made in reference to the bregma. DV was calculated from the brain surface. We specified these in the Methods. We did not cite a review from Maren & Fenselow for the aIC coordinates.

Minor comments:

(1) A schematic of the microdrive and tetrodes, including the distance of each tetrode would also be helpful.

We used a handcrafted Microdrives with four tetrodes. Since they were handcrafted, the relative orientation of the tetrodes varies and tetrode recording locations has to be verified histologically. We, however, made sure that the distance between tetrodes to be more than 200 μm apart so that distinct single-units will be obtained from different tetrodes. We added this to the methods as follows.

[Lines 430-431] The distance between the tetrodes were greater than 200 μm to ensure that distinct single-units will be obtained from different tetrodes.

(2) Figure 2E: representation of the baseline firing (3-min period before the tone presentation) is missing.

Figure 2E is the 3 min period before tone presentation

(3) Figure 2: Averages Pearson's correlation r and p values should be stated on panels F, G, and H (positive cell r = 0.81, P < 0.05; negative cell r = -0.68, P < 0.05).

They were all originally stated in the figures. But with reorganization of Figure 2, we now have a plot of the Pearson’s Correlation with r and p values in Figure 2F.

(4) Figure 2I: Representation of the absolute value of the normalized firing is highly confusing. Indeed, as the 'negative cells' are inhibited to freezing, firing should be represented as normalized, and negative for the inhibited cells.

To avoid confusion, we did not take an absolute value of the “negative cells”, which are now called the “freezing-inhibited cells”.

(5) Figure 4E (retrograde tracing): representation of individual values is missing.

Figure 4E now has individual values.

References:

London, T. D., Licholai, J. A., Szczot, I., Ali, M. A., LeBlanc, K. H., Fobbs, W. C., & Kravitz, A. V. (2018). Coordinated ramping of dorsal striatal pathways preceding food approach and consumption. Journal of Neuroscience, 38(14), 3547-3558.

Trott, J. M., Hoffman, A. N., Zhuravka, I., & Fanselow, M. S. (2022). Conditional and unconditional components of aversively motivated freezing, flight and darting in mice. Elife, 11, e75663.

Fanselow, M. S. (1980). Conditional and unconditional components of post-shock freezing. The Pavlovian journal of biological science: Official Journal of the Pavlovian, 15(4), 177-182.

Fanselow, M. S. (1986). Associative vs topographical accounts of the immediate shock-freezing deficit in rats: implications for the response selection rules governing species-specific defensive reactions. Learning and Motivation, 17(1), 16-39.

Landeira-Fernandez, J., DeCola, J. P., Kim, J. J., & Fanselow, M. S. (2006). Immediate shock deficit in fear conditioning: effects of shock manipulations. Behavioral neuroscience, 120(4), 873.

Moita, M. A., Rosis, S., Zhou, Y., LeDoux, J. E., & Blair, H. T. (2003). Hippocampal place cells acquire location-specific responses to the conditioned stimulus during auditory fear conditioning. Neuron, 37(3), 485-497.

Kochli, D. E., Thompson, E. C., Fricke, E. A., Postle, A. F., & Quinn, J. J. (2015). The amygdala is critical for trace, delay, and contextual fear conditioning. Learning & memory, 22(2), 92-100.

Ramos-Prats, A., Paradiso, E., Castaldi, F., Sadeghi, M., Mir, M. Y., Hörtnagl, H., ... & Ferraguti, F. (2022). VIP-expressing interneurons in the anterior insular cortex contribute to sensory processing to regulate adaptive behavior. Cell Reports, 39(9).

Klein, A. S., Dolensek, N., Weiand, C., & Gogolla, N. (2021). Fear balance is maintained by bodily feedback to the insular cortex in mice. Science, 374(6570), 1010-1015.

Nicolas, C., Ju, A., Wu, Y., Eldirdiri, H., Delcasso, S., Couderc, Y., ... & Beyeler, A. (2023). Linking emotional valence and anxiety in a mouse insula-amygdala circuit. Nature Communications, 14(1), 5073.

Maren, S., & Fanselow, M. S. (1996). The amygdala and fear conditioning : Has the nut been cracked? Neuron, 16(2), 237‑240. https://doi.org/10.1016/s0896-6273(00)80041-0

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The main goal of the authors was to study the testis-specific role of the protein FBXO24 in the formation and function of the ribonucleoprotein granules (membraneless electron-dense structures rich in RNAs and proteins).

We appreciate the summary comment of reviewer #1.

Strengths:

The wide variety of methods used to support their conclusions (including transgenic models)

We appreciate the positive comment of reviewer #1.

Weaknesses:

The lack of specific antibodies against FBXO24. Some of the experiments showing a specific phenotype are descriptive and lack of logical explanation about the possible mechanism (i.e. AR or the tail structure).

Because we could not obtain specific antibodies against FBXO24, we generated Fbxo24-FLAG transgenic mice, which can be used to show the interaction between FBXO24 and IPO5. For the mechanism of impaired acrosome reaction, we added some results and discussion as written in the response to the question (1) of reviewer #1 (public review). For the mechanism of abnormal flagellar structure, we added new results and fixed the manuscript as written in the response to the major comments of reviewer #3 (recommendations for the authors).

Questions:

The paper is excellent and employs a wide variety of methods to substantiate the conclusions. I have very few questions to ask:

(1) KO mice cannot undergo acrosome reaction (AR) even spontaneously. How do you account for this, given that no visible defects were observed in the acrosome?

One possibility is that Fbxo24 KO spermatozoa cannot undergo capacitation; however, it is difficult to analyze the capacitation status such as tyrosine phosphorylation because most Fbxo24 KO spermatozoa are not alive (Figure S3A). Other possibility is that AR-related proteins are affected in Fbxo24 KO spermatozoa. Therefore, we analyzed the amounts of AR-related proteins with mass spectrometry (Figure S3C). Although previous studies indicate that the assembly of the SNARE complex is a key event prior to AR [Hutt et al., 2005 (PMID: 15774481); Katafuchi et al., 2000 (PMID: 11066067); Schulz et al., 1997 (PMID: 9356173); Tomes et al., 2002 (PMID: 11884041)], no clear differences were detected for SNARE proteins (Figure S3C and D). PLCD4 that is important for AR [Fukami et al., 2001 (PMID: 11340203)) was also detected in Fbxo24 KO spermatozoa (Figure S3C). Although we could not find differences in the amounts of AR-related proteins, it is still possible that FER1L5, another AR-related protein [Morohoshi et al., 2023 (PMID: 36696506)] not detected in the mass spectrometry analyses, or AR-related proteins not yet identified are affected in Fbxo24 KO spermatozoa. We added these results and discussion (line 160-166 and 305-312).

(2) KO sperm are unable to migrate in the female tract, and, more intriguingly, they do not pass through the utero-tubal junction (UTJ). The levels of ADAM3 are normal, suggesting that the phenotype is influenced by other factors. The authors should investigate the levels of Ly6K since mice also exhibit the same phenotype but with normal levels of ADAM3.

We detected LY6K in Fbxo24 KO spermatozoa with immunoblotting, but no difference was found.

We added the results (Figure S3E and line 172–175).

(3) In Figure 4A, the authors assert that "RBGS Tg mice revealed that mitochondria were abnormally segmented in Fbxo24 KO spermatozoa." I am unable to discern this from the picture shown in that panel. Could you please provide a more detailed explanation or display the information more explicitly?

We are sorry for the ambiguous explanation on the morphology of sperm mitochondria sheath. Fbxo24 KO cauda epidydimal spermatozoa shows disorganized mitochondria sheath rather than “segmented”. We fixed the sentence (line 190-192) and added white arrowheads that indicate the disorganized regions (Figure 4A).

Reviewer #2 (Public Review):

Summary:

The manuscript by Kaneda et al "FBXO24 ensures male fertility by preventing abnormal accumulation of membraneless granules in sperm flagella" is a significant paper on the role of FBXO24 in murine male germ cell development and sperm ultrastructure and function. The body of experimental evidence that the authors present is extraordinarily strong in both breadth and depth. The authors investigate the protein's functions in male germ cells and sperm using a wide variety of approaches but focusing predominantly on their novel mouse model featuring deletion of the Fbxo24 gene and its product. Using this mouse, and a cross of it with another model that expresses reporters in the head and midpiece, they logically build from one experiment to the next. Together, their data show that this protein is involved in the regulation of membraneless electron-dense structures; loss of FBXO24 led to an accumulation of these materials and defects in the sperm flagellum and fertilizing ability. Interestingly, the authors found that several of the best-known components of electron-dense ribonucleoprotein granules that are found in the intermitochondrial cement and chromatoid body were not disrupted in the Fbxo24 knockout, suggesting that the electron-dense material and these structures are not all the same, and the biology is more complicated than some might have thought. They found evidence for the most changes in IPO5 and KPNB1, and biochemical evidence that FBXO24 and IPO5 could interact.

We appreciate the summary comment of reviewer #2.

Strengths:

The authors are to be commended for the thoroughness of their experimental approaches and the extent to which they investigated impacts on sperm function and potential biochemical mechanisms. Very briefly, they start by showing that the Fbxo24 message is present in spermatids and that the protein can interact with SKP1, in a way that is dependent on its F-box domain. This points toward a potential function in protein degradation. To test this, they next made the knockout mouse, validated it, and found the males to be sterile, although capable of plugging a female. Looking at the sperm, they identified a number of ultrastructural and morphological abnormalities, which they looked at in high resolution using TEM. They also cross their model with RBGS mice so that they have reporters in both the acrosome and mitochondria. The authors test a variety of sperm functions, including motility parameters, ability to fertilize by IVF, cumulus-free IVF, zona-free-IVF, and ICSI. They found that ICSI could rescue the knockout but not other assisted reproductive technologies. Defects in male fertility likely resulted from motility disruption and failure to get through the utero-tubal junction but defects in acrosome exocytosis also were noted. The authors performed thorough investigations including both targeted and unbiased approaches such as mass spectrometry. These enabled them to show that although the loss of the FBXO24 protein led to more RNA and elevated levels of some proteins, it did not change others that were previously identified in the electron-dense RNP material.

The manuscript will be highly significant in the field because the exact functions of the electron-dense RNP materials have remained somewhat elusive for decades. Much progress has been made in the past 15 years but this work shows that the situation is more complex than previously recognized. The results show critical impacts of protein degradation in the differentiation process that enables sperm to change from non-descript round cells into highly polarized and compartmentalized mature sperm, with an equally highly compartmentalized flagellum. This manuscript also sets a high bar for the field in terms of how thorough it is, which reveals wide-ranging impacts on processes such as mitochondrial compaction and arrangement in the midpiece, the correct building of the major cytoskeletal elements in the flagellum, etc.

We appreciate the positive comment of reviewer #2.

Weaknesses:

There are no real weaknesses in the manuscript that result from anything in the control of the authors. They attempted to rescue the knockout by expressing a FLAG-tagged Fbxo24 transgene, but that did not rescue the phenotype, either because of inappropriate levels/timing/location of expression, or because of interference by the tag. They also could not make anti-FBXO24 that worked for coimmunoprecipitation experiments, so relied on the FLAG epitope, an approach that successfully showed co-IP with IPO5 and SKP1.

We could not rescue the phenotype with Fbxo24-FLAG transgene, but different Fbxo24 mutant mice show the same phenotypes (Figure S6G). Further, another group showed that Fbxo24 KO mice exhibited abnormal mitochondrial coiling [Li et al., 2024 (PMID: 38470475)], confirming that

FBXO24 is involved in the mitochondrial sheath formation.

Reviewer #3 (Public Review):

Summary:

In this manuscript, the authors found that FBXO24, a testis-enriched F-box protein, is indispensable for male fertility. Fbxo24 KO mice exhibited malformed sperm flagellar and compromised sperm motility.

We appreciate the summary comment of reviewer #3.

Strengths:

The phenotype of Fbxo24 KO spermatozoa was well analyzed.

We appreciate the positive comment of reviewer #3.

Weaknesses:

The authors observed numerous membraneless electron-dense granules in the Fbxo24 KO spermatozoa. They also showed abnormal accumulation of two importins, IPO5 and KPNB1, in the Fbxo24 KO spermatozoa. However, the data presented in the manuscript do not support the conclusion that FBXO24 ensures male fertility by preventing the abnormal accumulation of membraneless granules in sperm flagella, as indicated in the manuscript title.

Fbxo24 KO mice showed abnormal accumulation of membraneless granules in sperm flagella and male infertility, suggesting that FBXO24 is involved in these processes, but there are no results that show the direct relationship as reviewer #3 mentioned. Therefore, we fixed the title.

Recommendations For The Authors:

Reviewer #2 (Recommendations For The Authors):

On page 4, lines 152-154, the authors introduce the RBGS mouse model and use it in their experiments.

However, they left out an obvious but helpful sentence that tells the reader that they crossed the Fbxo24-null mouse with the RBGS. As one continues reading it is clear, but best to avoid even slight confusion.

We revised the explanation in the result section (line 150-153).

Reviewer #3 (Recommendations For The Authors):

In this manuscript, the authors found that FBXO24, a testis-enriched F-box protein, is indispensable for male fertility. Fbxo24 KO mice exhibited malformed sperm flagellar and compromised sperm motility. The phenotype of Fbxo24 KO spermatozoa was well analyzed.

The authors observed numerous membraneless electron-dense granules in the Fbxo24 KO spermatozoa. They also showed abnormal accumulation of two importins, IPO5 and KPNB1, in the Fbxo24 KO spermatozoa. However, the data presented in the manuscript do not support the conclusion that FBXO24 ensures male fertility by preventing the abnormal accumulation of membraneless granules in sperm flagella, as indicated in the manuscript title.

Fbxo24 KO mice showed abnormal accumulation of membraneless granules in sperm flagella and male infertility, suggesting that FBXO24 is involved in these processes, but there are no results that show the direct relationship as reviewer #3 mentioned. Therefore, we fixed the title.

Major comments:

In the title, abstract, introduction, and some sections such as lines 275-276, the authors conclude that FBXO24 prevents the accumulation of importins and RNP granules during spermiogenesis. However, the provided data do not substantiate this claim. To provide conclusive evidence to support the current title, the authors need to present evidence supporting: 1) direct degradation of IPO5 and KPNB1 by FBXO24; 2) the direct requirement of IPO5 for the formation of the membraneless granules, and 3) infertility resulting from the presence of membraneless granules, rather than other issues such as abnormal ODF and AX.

(1) direct degradation of IPO5 and KPNB1 by FBXO24.

To examine if IPO5 can be degraded by FBXO24, we performed a ubiquitination assay using HEK293T cells. Ubiquitination of IPO5 was upregulated in the presence of WT FBXO24 but not with the mutant ΔF-box FBXO24, suggesting that IPO5 can be ubiquitinated by FBXO24. We did not examine the ubiquitination of KPNB1 because we failed to construct a plasmid vector expressing mouse KPNB1. We think that KPNB1 is not the substrate because we did not detect the interaction between FBXO24 and KPNB1 (Figure 5E). We added the results of the ubiquitination assay (Figure

5F and line 261-265) and mentioned it in the abstract (line 35).

(2) the direct requirement of IPO5 for the formation of the membraneless granules.

(3) infertility resulting from the presence of membraneless granules, rather than other issues such as abnormal ODF and AX.

We revealed that IPO5 aggregate under stress condition in COS7 cells (Figure 6C and D); however, we did not examine whether IPO5 is required for the formation of the membraneless granules. We consider that protein degradation systems such as PROTAC or Trim-Away to knockdown IPO5 at the protein level in Fbxo24 KO mice could be a good way to see if the membraneless granules are diminished and male fertility is rescued. However, it takes time to apply the degradation systems in vivo. Therefore, we would like to leave this rescue experiment for future studies. We fixed the title and  abstract (line 37-38), and removed the last sentence of the introduction.

Also, the other group reported the analyses of Fbxo24 KO mice [Li et al., 2024 (PMID: 38470475)] right after we submitted our manuscript to the eLife. They reported not only disorganized flagellar structures but also abnormal head morphology, which may lead to male infertility. The differences from our study may be due to different mouse genetic backgrounds. We mentioned it in the discussion section (line 348-353).

Minor comments:

(1) The authors claimed a significant increase in the total amount of RNAs in Fbxo24 KO spermatozoa (lines 259-261), suggesting that the ...contain RNAs. More direct evidence supporting this claim should be provided.

We show that the amounts of IPO5 and KBNB1 increased in Fbxo24 KO spermatozoa (Figure 5A and B), both of which could be incorporated into RNP granules in COS7 cells (Figure 6C and D), supporting the idea that membraneless electron-dense structures may be RNP granules. However, because we did not show direct evidence that electron-dense structures contain RNAs, we removed the sentences (line 259-261 of the 1st submission manuscript). 

(2) The author should provide an explanation for the absence of a FLAG band in the input Tg in Figure 5D and the larger size of the IPO5 band in the FLAG-IP group compared to the input. Similar observations are also noted in Figure 5E.

The FLAG band is weak because the protein amount is low. When we increase the contrast, we can see the FLAG band. We added an image with high contrast (Figure 5D). Sometimes, proteins run differently with SDS-PAGE after immunoprecipitation, likely due to varying protein composition in the sample. We explained it in the figure legend (line 868-869).

(3) In Line 526, clarify the procedure for sperm purification, and determine the potential for contamination from somatic cells.

We did not perform sperm purification, but when we observed spermatozoa obtained from cauda epididymis, we rarely observed either somatic cells or immature spermatogenic cells. We added  pictures in Figure S7. Further, we added detailed explanation about how to collect spermatozoa from the epididymis (line 549-550).

(4) Define the Y-axis in Figure 2E, F, and G.

We have revised the figures.

Author response:

Reviewer #1 (Public Review):

Using the UK Biobank, this study assessed the value of nuclear magnetic resonance measured metabolites as predictors of progression to diabetes. The authors identified a panel of 9 circulating metabolites that improved the ability in risk prediction of progression from prediabetes to diabetes. In general, this is a well-performed study, and the findings may provide a new approach to identifying those at high risk of developing diabetes. I have some comments that may improve the importance of this study.

We deeply appreciate the reviewer's invaluable time dedicated to the review of this manuscript and the insightful comments to enhance its overall quality.

(1) It is unclear why the authors only considered the top 20 variables in the metabolite selection and why they did not set a wider threshold.

Thank you for the comment. We set the top 20 variables in the metabolite selection balancing the performance of the final diabetes risk prediction model and the clinical applicability due to measurement costs. We have added this explanation in the “Methods” section.

“We chose the intersection set of the top 20 most important variables selected by the three machine learning models, after balancing the performance of the final diabetes risk prediction model and the clinical applicability associated with measurement costs of metabolites.”

(2) The methods section would benefit from a more detailed exposition of how parameter tuning was conducted and the range of parameters explored during the training of the RSF model.

According to the reviewer’s suggestion, we have added a more detailed description of parameters tunning and the range of parameters explored during the training of the RSF model in the “Method S2” section in the Supplementary material.

“The RSF model was fitted using the “randomForestSRC” package and the grid search method was used for hyperparameter tuning. Specifically, the grid search method was used to tune hyperparameters among the RSF model, through minimizing out-of-sample or out-of-bag error1. Each tree in the RSF is constructed from a random sample of the data, typically a bootstrap sample or 63.2% of the sample size (as in the present study). Consequently, not all observations are used to construct each tree. The observations that are not used in the construction of a tree are referred to as out-of-bag observations. In an RSF model, each tree is built from a different sample of the original data, so each observation is “out-of-bag” for some of the trees. The prediction for an observation can then be obtained using only those trees for which the observation was not used for the construction. A classification for each observation is obtained in this way and the error rate can be estimated from these predictions. The resulting error rate is referred to as the out-of-bag error. Through calculating the out-of-bag error in each iteration, the best hyperparameters were finally determined.

The hyperparameters to be tuned and range of grid search in the present study were below: number of trees (50-1000, by 50), number of variables to possibly split at each node (3-6, by 1), and minimum size of terminal node (1-20, by 1)2.”

(3) It is hard to understand the meaning of the decision curve analysis and the clinical implications behind the net benefit, which are required to clarify the application values of models.

Thank you for the comment. We have added more description and discussion about the decision curve analysis in the “Methods” and “Discussion” sections.

“Furthermore, we used decision curve analysis (DCA) to assess the clinical usefulness of prediction model-based guidance for prediabetes management, which calculates a clinical “net benefit” for one or more prediction models in comparison to default strategies of treating all or no patients3.”

“Most importantly, a model with good discrimination does not necessarily have high clinical value. Hence, DCA was used to compare the clinical utility of the model before and after adding the metabolites, and this showed a higher net benefit for the latter than the basic model, suggesting the addition of the metabolites increased the clinical value of prediction, i.e., the potential benefit of guiding management in individuals with prediabetes3,4. These results provided novel evidence supporting the value of metabolic biomarkers in risk prediction and stratification for the progression from prediabetes to diabetes.”

(4) Notably, the NMR platform utilized within the UK Biobank primarily focused on lipid species. This limitation should be discussed in the manuscript to provide context for interpreting the results and acknowledge the potential bias from the measuring platform.

Thank you for the comment. We acknowledged this limitation that NMR platform within the UK Biobank primarily focused on lipid species and the potential bias from the measuring platform and have added this in “Discussion” section.

“Third, the Nightingale metabolomics platform primarily focused on lipids and lipoprotein sub-fractions, and thus the predictive value of other metabolites in the progression from prediabetes to diabetes warranted further research using an untargeted metabolomics approach.”

(5) The manuscript should explain the potential influence of non-fasting status on the findings, particularly concerning lipoprotein particles and composition. There should be a detailed discussion of how non-fasting status may impact the measurement and the findings.

According to the reviewer’s suggestion, we have added more details to explain the potential influence of non-fasting status on our findings in the “Discussion” section.

“Additionally, the use of non-fasting blood samples might increase inter-individual variation in metabolic biomarker concentrations, however, fasting duration has been reported to account for only a small proportion of variation in plasma metabolic biomarker concentrations5. Therefore, we believe the impact of non-fasting samples on our findings would be minor.”

(6) Cross-platform standardization is an issue in metabolism, and further descriptions of quality control are recommended.

Thank you for the comment. We have added more description of quality control in the “Method S1” section in the Supplementary material.

“Metabolic biomarker profiling by Nightingale Health’s NMR platform provides consistent results over time and across spectrometers. Furthermore, the sample preparation is minimal in the Nightingale Health’s metabolic biomarker platform, circumventing all extraction steps. These aspects result in highly repeatable biomarker measurements. Pre-specified quality metrics were agreed between UK Biobank and Nightingale Health to ensure consistent results across the samples, and pilot measurements were conducted. Nightingale Health performed real-time monitoring of the measurement consistency within and between spectrometers throughout the UK Biobank samples. Two control samples provided by Nightingale Health were included in each 96-well plate for tracking the consistency across multiple spectrometers. Furthermore, two blind duplicate samples provided by the UK Biobank were included in each well plate, with the position information unlocked only after results delivery. Coefficient of variation (CV) targets across the metabolic biomarker profile were pre-specified for both Nightingale Health’s internal control samples and UK Biobank’s blind duplicates. The targets were met for each consecutively measured batch of ~25,000 samples. For the majority of the metabolic biomarkers, the CVs were below 5% (https://biobank.ndph.ox.ac.uk/showcase/refer.cgi?id=3000). Further, the distributions of measured biomarkers from 5 sample batches indicated absence of batch effects (https://biobank.ctsu.ox.ac.uk/ukb/ukb/docs/nmrm_app1).”

Reviewer #2 (Public Review):

Deciphering the metabolic alterations characterizing the prediabetes-diabetes spectrum could provide early time windows for targeted preventive measures to extend precision medicine while avoiding disproportionate healthcare costs. The authors identified a panel of 9 circulating metabolites combined with basic clinical variables that significantly improved the prediction from prediabetes to diabetes. These findings provided insights into the integration of these metabolites into clinical and public health practice. However, the interpretation of these findings should take account of the following limitations.

We appreciate the reviewer’s positive comments and encouragement.

(1) First, the causal relationship between identified metabolites and diabetes or prediabetes deserves to be further examined particularly when the prediabetic status was partially defined. Some metabolites might be the results of prediabetes rather than the casual factors for progression to diabetes.

Thank you for your insightful comments. We agree with you that the panel of metabolites in this study might not be the causal factor for progression from prediabetes to diabetes, which needs further validation in experimental studies. We have added this limitation in the “Discussion” section.

“Fifth, we could not draw any conclusion about the causality between the identified metabolites and the risk for progression to diabetes due to the observational nature, which remained to be validated in further experimental studies.”

(2) The blood samples were taken at random (not all in a non-fasting state) and so the findings were subjected to greater variability. This should be discussed in the limitations.

According to the reviewer’s suggestion, we have added more details to explain the potential influence of non-fasting status on our findings in the “Discussion” section.

“Additionally, the use of non-fasting blood samples might increase inter-individual variation in metabolic biomarker concentrations, however, fasting duration has been reported to account for only a small proportion of variation in plasma metabolic biomarker concentrations5. Therefore, we believe the impact of non-fasting samples on our findings would be minor.”

(3) The strength of NMR in metabolic profiling compared to other techniques (i.e., mass spectrometry [MS], another commonly used metabolic profiling method) could be added in the Discussion section.

According to the reviewer’s suggestion, we have added the strength of NMR in metabolic profiling compared to other techniques in the “Discussion” section.

“Circulating metabolites were quantified via NMR-based metabolome profiling within the UK Biobank, which offers metabolite qualification with relatively lower costs and better reproducibility6.”

(4) Fourth, the applied platform focuses mostly on lipid species which may be a limitation as well.

Thank you for the comment. We acknowledged this limitation that NMR platform within the UK Biobank primarily focused on lipid species and the potential bias from the measuring platform and have added this in the “Discussion” section.

“Third, the Nightingale metabolomics platform primarily focused on lipids and lipoprotein sub-fractions, and thus the predictive value of other metabolites in the progression from prediabetes to diabetes warranted further research using an untargeted metabolomics approach.”

(5) it is a very large group with pre-diabetes, but the results only apply to prediabetes and not to the general population. This should be clear, although the authors have also validated the predictive value of these metabolites in the general population.

Thank you for the comment. We agree with you that the results only apply to prediabetes and not to the general population, though they also showed potential predictive value among participants with normoglycemia. We have accordingly modified the relevant expressions in the “Conclusion” section to restrict these findings to participants with prediabetes.

“In this large prospective study among individuals with prediabetes, we detected a panel of circulating metabolites that were associated with an increased risk of progressing to diabetes.”

References

(1) Janitza S, Hornung R. On the overestimation of random forest's out-of-bag error. PLoS One. 2018;13(8):e0201904.

(2) Tian D, Yan HJ, Huang H, et al. Machine Learning-Based Prognostic Model for Patients After Lung Transplantation. JAMA Netw Open. 2023;6(5):e2312022.

(3) Vickers AJ, van Calster B, Steyerberg EW. A simple, step-by-step guide to interpreting decision curve analysis. Diagn Progn Res. 2019;3:18.

(4) Li J, Xi F, Yu W, Sun C, Wang X. Real-Time Prediction of Sepsis in Critical Trauma Patients: Machine Learning-Based Modeling Study. JMIR Form Res. 2023;7:e42452.

(5) Li-Gao R, Hughes DA, le Cessie S, et al. Assessment of reproducibility and biological variability of fasting and postprandial plasma metabolite concentrations using 1H NMR spectroscopy. PLoS One. 2019;14(6):e0218549.

(6) Geng T-T, Chen J-X, Lu Q, et al. Nuclear Magnetic Resonance–Based Metabolomics and Risk of CKD. American Journal of Kidney Diseases. 2023.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The current manuscript by Hajra et al deals with the role of the prominent Sirtuins SIRT1 and -3 during infection of macrophages with Salmonella Typhimurium (ST). Apparently, ST infection induces upregulation of host cell SRTs to aid its own metabolism during the intracellular lifestyle and to help reprogramming macrophage polarization. The manuscript has two parts, namely one part that deals with Salmonella infection in cells, where RAW 264.7 murine macrophage-like cells, sharing some features with primary macrophages, were employed. Infected RAW cells displayed a tendency to polarize towards wound-healing M2 and not inflammatory M1 macrophages, which was dependent on SRT. Consequently, the inflammatory response in RAW was more robust in the absence of SRT. Moreover, loss of SRTs leads to impaired bacterial proliferation in these cells, which was attributed to defects in metabolic adaption of the bacteria in the absence of SRT-activity and to the increased M1 inflammatory response.

Unfortunately, the line of argumentation remains incomplete because corresponding assays in mice showed the opposite result as compared to the experiments using RAW 264.7 cells. i.e. loss of SRTs leads to increased bacterial load in animals (versus impaired proliferation in RAW 264.7 cells). The authors cannot explain this discrepancy.

Strengths:

Extensive analysis of Salmonella infection in RAW macrophage-like cells and mice in the context of SRT1/3 function.

Weaknesses:

Lack of connection between the cell-based and organismic data, which are not supportive of each other.

We are highly grateful for your valuable and insightful comments. Thank you for appreciating the merit of our manuscript. We agree with the opposing phenotypes among the RAW264.7 cell line (Fig. 2A), primary peritoneal macrophages (ex vivo) (Fig.2B), and in vivo mouse model (Fig.8) findings. Both RAW264.7 macrophage and peritoneal macrophage infection show attenuated intracellular bacterial proliferation owing to the heightened proinflammatory burst. This is in sharp contrast to our in vivo mouse model of infection which shows increased organ burden and bacterial dissemination. The higher bacterial load in the organs including the spleen (Fig.8B) is attributed to increased pro-inflammatory cytokine burst and ROS production (Fig.8F-H, Fig.S9) triggering bacterial dissemination. The pro-inflammatory arsenals like IL-6, IL-1β and ROS that limit bacterial proliferation within the macrophages (F4/80+ macrophages within the spleen or in RAW264.7 macrophages or primary peritoneal macrophages) are facilitating bacterial dissemination in blood and to the other organs (Fig. 8I-L, Fig.S3F-G). This is in line with the following previous findings-

Klebsiella pneumoniae infection triggers an inflammatory response via secretion of IL-6 upon HIF-1α activation that induces bacterial dissemination (Holden VI, Breen P, Houle S, Dozois CM, Bachman MA. Klebsiella pneumoniae Siderophores Induce Inflammation, Bacterial Dissemination, and HIF-1α Stabilization during Pneumonia. mBio. 2016 Sep 13;7(5):e01397-16. doi: 10.1128/mBio.01397-16. PMID: 27624128; PMCID: PMC5021805.).

Correlation analysis of immune responses to Salmonella infection revealed that increased innate immune “cassette” opposes the adaptive immune arm leading to increased bacterial load in mice (Hotson AN, Gopinath S, Nicolau M, Khasanova A, Finck R, Monack D, et al. Coordinate actions of innate immune responses oppose those of the adaptive immune system during Salmonella infection of mice. Science signaling. 2016;9(410):ra4). 

In our revised manuscript, we have assessed additional splenic populations including CD45+, Ly6C+, and CD11c+ populations. Our results show that the CD45+ splenic population depicts increased bacterial loads like that of the total splenic population within the SIRT1/3 inhibited cohorts. However, CD45+ monocytes and Ly6C positive splenic population exhibit compromised burden within the SIRT1/3 inhibited cohorts. Moreover, within the CD11c+ population, CD45+ granulocytes or lymphocytes show comparable organ loads to that of the vehicle control or SIRT1 activator-treated mice group (Fig. M-S, Fig.S8). Overall, our data suggest heterogeneous bacterial burden in diverse splenic populations.

Reviewer #2 (Public Review):

Dipasree Hajra et al demonstrated that Salmonella was able to modulate the expression of Sirtuins (Sirt1 and Sirt3) and regulate the metabolic switch in both host and Salmonella, promoting its pathogenesis. The authors found Salmonella infection induced high levels of Sirt1 and Sirt3 in macrophages, which were skewed toward the M2 phenotype allowing Salmonella to hyper-proliferate. Mechanistically, Sirt1 and Sirt3 regulated the acetylation of HIF-1alpha and PDHA1, therefore mediating Salmonella-induced host metabolic shift in the infected macrophages. Interestingly, Sirt1 and Sirt3-driven host metabolic switch also had an effect on the metabolic profile of Salmonella. Counterintuitively, inhibition of Sirt1/3 led to increased pathogen burdens in an in vivo mouse model. Overall, this is a well-designed study. There are a few comments below that would further strengthen the current study.

Major comments:

In the in vivo study (lines 436-446) - the authors noticed increased pathogen burden in the EX-527 or the 3TYP-treated mice cohorts but decreased pathogen burden within the F4/80+ macrophage population. What are the other cell types that have increased pathogen burden in splenocytes from EX-527 or the 3TYP treated? Can this be further explored and explained?

While the authors indicated that IL-6 cytokine storm and elevated ROS production could result in bacterial dissemination in vivo, one could also argue that Sirt1/3 inhibitors might have an impact on gut function and/or gut microbiota (PMID: 22115311). Did Sirt1/3 inhibitors also lead to increased pathogen burdens in the gut? If so, the potential effect of these in vivo treatments on gut microbiota/colonization resistance should be discussed.

Minor comment:

Sirt1 has been shown to be degraded during Salmonella infection (PMID: 28192515), which is different from the current study. An explanation should be provided for this.

We thank you for your encouraging and gracious comments. We deeply appreciate your time and efforts in providing constructive feedback for the betterment of our work. As per your precious suggestions, we have assessed additional splenic populations including CD45+, Ly6C+, and CD11c+ populations apart from F4/80+ macrophage populations. Our analysis suggests that the CD45+ splenic population show increased bacterial loads similar to the total splenic population within the SIRT1/3 inhibited cohorts. However, CD45+ monocytes and Ly6C positive splenic population exhibit compromised burden within the SIRT1/3 inhibited cohorts. Moreover, CD11c+ population, CD45+ granulocytes or lymphocytes show comparable organ loads to that of the vehicle control or SIRT1 activator treated mice group (Fig. 8M-S). Overall, our data suggest heterogeneous bacterial burden in diverse splenic populations.

We immensely appreciate the reviewer for this insightful question about the effect of SIRT1/3 on the gut per se. To answer your question, we observed increased pathogen loads within the mesenteric lymph nodes of the gut in the SIRT1/3 inhibitor-treated mice groups (Fig.8B). In our revised manuscript, we evaluated gut inflammation via IL1-β estimation in the mice's ileal tissues and have observed heightened IL-1β production in the inhibitor-treated mice cohorts in comparison to the vehicle control (Fig. S3G). We have also examined gut epithelial pathology via Haematoxylin-Eosin (H&E) staining of the ileal sections to address the effect of in vivo treatment on gut microbiota and colonization resistance which is appended here. However, the gut microbiota crosstalk and their effect on colonization resistance is a part of another current study and it is being examined in detail there. Therefore, this appended H&E has not been incorporated in the revised manuscript.

Author response image 1.

In line with the reference PMID: 28192515, where Sirt1 has been shown to be degraded during Salmonella infection at later time points of infection, our study also has shown that both SIRT1 mRNA (Fig. 1A) and protein levels (Fig. S1A) show an elevated expression at 2h and 6h post-infection and show a downregulation at 16h in comparison to the 6h time point.  However, SIRT3 expression levels remain elevated even at later time points of infection. Therefore, we speculate that there is a shared role between SIRT1 and SIRT3 that facilitates the phenotypes reported in our study.

Reviewer #3 (Public Review):

Summary:

In this paper, Hajra et al have attempted to identify the role of Sirt1 and Sirt3 in regulating metabolic reprogramming and macrophage host defense. They have performed gene knockdown experiments in RAW macrophage cell lines to show that depletion of Sirt1 or Sirt3 enhances the ability of macrophages to eliminate Salmonella Typhimurium. However, in mice, inhibition of Sirt1 resulted in dissemination of the bacteria but the bacterial burden was still reduced in macrophages. They suggest that the effect they have observed is due to increased inflammation and ROS production by macrophages. They also try to establish a weak link with metabolism. They present data to show that the switch in metabolism from glycolysis to fatty acid oxidation is regulated by acetylation of Hif1a, and PDHA1.

Strengths:

The strength of the manuscript is that the role of Sirtuins in host-pathogen interactions has not been previously explored in-depth making the study interesting. It is also interesting to see that depletion of either Sirt1 or Sirt3 results in a similar outcome.

Weaknesses:

The major weakness of the paper is the low quality of data, making it harder to substantiate the claims. Also, there are too many pathways and mechanisms being investigated. It would have been better if the authors had focussed on either Sirt1 or Sirt3 and elucidated how it reprograms metabolism to eventually modulate host response against Salmonella Typhimurium. Experimental evidence is also lacking to prove the proposed mechanisms. For instance, they show correlative data that the knockdown of Sirt1-mediated shift in metabolism is due to HIF1a acetylation but this needs to be proven with further experiments.

We appreciate the reviewer’s critical analysis of our work. In the revised manuscript, we aimed to eliminate the low-quality data sets and have tried to substantiate them with better and conclusive ones, as directed in the recommendations for the author section. We agree with the reviewer that the inclusion of both Sirtuins 1 and 3 has resulted in too many pathways and mechanisms and focusing on one SIRT and its mechanism of metabolic reprogramming and immune modulation would have been a less complicated alternative approach. However, as rightly pointed out, our work demonstrated the shared and few overlapping roles of the two sirtuins, SIRT1 and SIRT3, together mediating the immune-metabolic switch upon Salmonella infection. As per the reviewer’s suggestion, we have performed additional experiments with HIF-1α inhibitor treatment in our revised manuscript to substantiate our correlative findings on SIRT1-mediated regulation of host glycolysis (Fig.7G).

Reviewer #1 (Recommendations For The Authors):

The authors state "SIRT1 and SIRT3 inhibition resulted in increased pathogen loads in organs and triggered enhanced bacterial dissemination, together leading to increased susceptibility of the mice to S. Typhimurium infection owing to increased ROS and IL-6 production." How can this be reconciled? To the reviewer, this is not a convincing explanation. The reviewer is not a mouse pathologist, so maybe did not understand the argument in full.

However, in order to clarify whether these phenomena can be brought into context and explained by for instance cell-autonomous (in (RAW) macrophages) versus non-autonomous (in mice) mechanisms, it would be required to bring in context the organismic phenotype with a cellular phenotype, using more physiologic primary macrophages.

(1) The authors show in Figure 8 that in general SRT inhibition leads to increased infection whereas SRT activation results in decreased infection. This is even true for e the spleen (e.g. Figure 8B), which should be full of macrophages upon infection.

(2) Only Figure 8L implies that endogenous primary, splenic macrophages show a higher infection rate upon pharmacologic SRT activation, which would potentially mirror the RAW results. This is however not supportive of their own explanation: Who would now produce more ROS and IL6 if these macrophages are more supportive of intracellular ST? Is there a difference in the roles or SRTs between different types of macrophages and/or neutrophils? And between macrophages and somatic cells concerning ST infection? The reviewer tends to believe that RAW cells display a defective killing response (such as ROS production) as they are highly transformed cells. Therefore, the authors should use cultured peritoneal macrophages or BMDMs in addition to RAW264.7 cells.

The literature cited by the authors also implies that the inflammatory response in mice is higher in the absence of SRTs. This is in line with a role for SRTs in (negatively) regulating M1 inflammatory polarization but probably not with increased bacterial burden in mice. If it was, then increased dissemination could be explained by increased tissue damage. However, the flow cytometry experiments from infected organs then do not confirm that, as the infection of individual cells is higher upon SRT inhibition. Thus there seems a broad gap between the role of SRTs in ST infection in RAW264.7 cells versus non-transformed cells.

I would not discard the RAW results, as I am convinced that they contain valuable data. However, it needs to be clarified what aspect of the host response RAW 264.7 cells represent. Primary macrophages might likely be more aggressive towards the bacteria. Finally, the question arises: what is the role of the metabolic switch in the in vivo setting?

The reviewer recommends repeating some key experiments by in-vitro-infecting BMDMs or isolated peritoneal macrophages (after some days of culturing) to bridge between the present RAW-derived data and the mouse data. How is the bacterial load with and without SRT inhibitor/activator in primary macrophages, when infected outside of the body? Can ex-vivo infection also affect polarization of e.g. peritoneal macrophages or the metabolic switch? If it is possible to find a conclusive explanation for their data, then this story might really add to our understanding of another aspect of how ST manipulates the host to survive.

In case the reviewer understands the mouse experiments correctly, all assays on peritoneal cells were performed after in-vivo-infection and/or treatment.

Together, RAW 264.7 murine macrophage-like cells might not be the right model to understand the phenotypes in full. As far as the reviewer knows, these cells are not capable of killing bacteria as effectively as activated primary macrophages or neutrophils.

A few of the key findings of RAW264.7 macrophages have been replicated in primary peritoneal macrophages (Fig. 2B, S3E-F, S6B, S7B-D). We wanted to clarify that the peritoneal macrophage experiments were performed ex vivo, wherein peritoneal macrophages were isolated from mice were then subjected to SIRT1/3 inhibitor treatments and Salmonella infection and not after in vivo treatment or infection. In ex vivo setting, we have examined the effect of SIRTs on the metabolic switch during Salmonella infection (Fig. S7B-D) which resembled our RAW264.7 macrophage data. Additionally, in in vivo setting, we have analyzed the transcript level expression of host metabolic genes and corresponding bacterial metabolic genes in infected mice liver and spleen tissue under SIRT1/3 inhibitor treatment (Fig.S7E-F, Fig.6C-D). Our primary peritoneal macrophage data exactly mirrors the RAW264.7 macrophage findings showing attenuated intracellular bacterial proliferation owing to the heightened proinflammatory burst upon SIRT1/3 knockdown or inhibition (Fig.2A-B). This is opposite to our in vivo mouse model of infection which shows increased organ burden and bacterial dissemination (Fig.8A-H). The pro-inflammatory arsenals that limit bacterial proliferation within the macrophages (F4/80+ macrophages within the spleen or in RAW264.7 macrophages or primary peritoneal macrophages) are facilitating bacterial dissemination in blood and to the other organs owing to tissue damage (Fig.8E-L). This is in line with the following previous findings-

Klebsiella pneumoniae infection triggers an inflammatory response via secretion of IL-6 upon HIF-1α activation that induces bacterial dissemination (Holden VI, Breen P, Houle S, Dozois CM, Bachman MA. Klebsiella pneumoniae Siderophores Induce Inflammation, Bacterial Dissemination, and HIF-1α Stabilization during Pneumonia. mBio. 2016 Sep 13;7(5):e01397-16. doi: 10.1128/mBio.01397-16. PMID: 27624128; PMCID: PMC5021805.).

Correlation analysis of immune responses to Salmonella infection revealed that increased innate immune “cassette” opposes the adaptive immune arm leading to increased bacterial load in mice (Hotson AN, Gopinath S, Nicolau M, Khasanova A, Finck R, Monack D, et al. Coordinate actions of innate immune responses oppose those of the adaptive immune system during Salmonella infection of mice. Science Signaling. 2016;9(410):ra4). 

As per the reviewer’s suggestions, we have analyzed other populations apart from F4/80+ macrophages and have observed that the CD45+ splenic population depicts increased bacterial loads like that of the total splenic population within the SIRT1/3 inhibited cohorts. However, CD45+ monocytes and Ly6C positive splenic population exhibit compromised burden within the SIRT1/3 inhibited cohorts. Moreover, the CD1c+ population, CD45+ granulocytes, or lymphocytes show comparable organ loads to that of the vehicle control or SIRT1 activator-treated mice group (Fig.8M-S, Fig.S8). Overall, our data suggest heterogeneous bacterial burden in diverse splenic populations.

Reviewer #3 (Recommendations For The Authors):

Abstract

The authors state that perturbing Sirt1 and Sirt3 results in a shift in Salmonella's metabolism. On the contrary, the data reflects the metabolism in the host cell and not the bacteria. This statement is wrong. They only show increased expression of some of the glycolytic genes in Salmonella, which is not sufficient to make the claim that the switch to fatty acid oxidation in macrophages is due to utilisation of glucose by the bacteria.

We value the reviewer’s response and have accordingly reframed our sentence in the abstract (Line 24-25).

Fig 1: Expression of Sirt1 - The data needs to be supported with a western blot for Sirt1 and Sirt3 but the Western blots shown in the supplementary figure are of very poor quality and do not support the authors' claim.

We have repeated the western blot and have supplemented the previous blot with an alternate blot in Fig. S1A as per your precious input.

Why haven't the authors shown any representative blots for Sirt1 and Sirt3 upon infection with Salmonella mutants? They need to italicize the genes when they describe mRNA expression.

Previously we had only performed transcript-level expression of Sirt1 and Sirt3 upon infection with Salmonella mutants and therefore representative blot image was absent. The gene names have been duly italicized while describing mRNA expression (Line 126-154). We regret the inconvenience caused. We have performed the western blotting to assess the protein expression profile upon infection with Salmonella mutants as per the reviewer’s suggestion and the representative blot image has been duly appended in the revised manuscript (Fig. S1B).

What is the rationale for examining Sirt1 and Sirt3 mRNA in M1 and M2 macrophages? Salmonella infection on its own will polarise the macrophages towards M1. How long were these macrophages infected? The time points are missing.

The rationale behind the examination of Sirt1 and Sirt3 mRNA in M1 and M2 polarized was to ascertain whether indeed M1 polarized macrophages exhibit decreased expression of Sirt1 or Sirt3 and polarization of macrophages toward M2 state show upregulation of Sirt1 and Sirt3 upon Salmonella infection. After confirming these above-mentioned findings through this preliminary experiment, we then hypothesized whether Salmonella infection on its own will polarise the macrophages toward an immunosuppressive M2 state at a later time course of infection as infection drives the induction of SIRT expression and whether this is mediated by Sirt1 and Sirt3 (Fig. 3). We are extremely apologetic for not mentioning the 16h time-point in the figure and the missing time point has been duly documented in the revised manuscript (Line 155).

Fig S2 knockdown of Sirt1 and Sirt3 are not convincing.

We are extremely sorry for the inconclusive knockdown blot. An alternative blot has been substantiated in the revised manuscript (Fig. S2,C-D).

Fig 2A and 2B the time point post infection has not been mentioned. Although it is stated that 2h and 16h post-infection samples were analysed. Only one time point has been shown.

We are sorry for the confusion. We wanted to clarify that Fig.2A and Fig. 2B show the fold proliferation where fold proliferation was calculated as CFU at 16hr divided by CFU at 2hr as mentioned in the materials and methods section under the heading of Intracellular proliferation or gentamicin protection assay.

Fold Proliferation= [CFU at 16h]/[CFU at 2h]

The cytokines data are intriguing in that the increase in IL-6 relative to control is seen only at 2h and 20h but not at 6h. Il-6 at 20h in untransfected cells is comparable to uninfected cells. Did the authors investigate cell death? Salmonella induces various forms of cell death which could account for the decreased cytokine production at later time points.

We have investigated the cell death upon Salmonella infection via MTT assay. At later time points of infection, we indeed observed around 16 percent decrease in cell survival compared to the initial time point of 2h. The results have been appended here and it supports our eminent reviewer’s reasoning for the decreased cytokine production at later time points.

Author response image 2.

Additional cytokines such as IL-1b would be helpful. Also, not sure how uninfected macrophages produce nearly 200pg of IL-10.

As per the author’s critical suggestion, we have assessed the IL-1b cytokine production at 16h post-infection in RAW264.7 macrophages and peritoneal macrophages and mice serum samples at 5th day post-infection (Fig.S3C, S3E-F). Our results indicate increased production of IL-b in the infected SIRT1/3 knockdown RAW264.7 macrophages, SIRT1/3 inhibitor-treated peritoneal macrophages and in mice serum samples under SIRT1/3 inhibitor treatment in comparison to the vehicle control. Additionally, we have quantified IL-1b in mice ileal tissues under SIRT1/3 inhibitor treatment (Fig.S3G) and have obtained heightened intestinal IL-1b production in the inhibitor-treated cohorts. We thank the reviewer for raising the concern for 200pg of IL-10 in the uninfected macrophages. We have repeated the experiment and have provided an alternative representative graph for the experiment wherein the IL-10 levels in the uninfected cohorts range between 20-40pg/ml (Fig. S3B).

It is surprising that the authors have found increased Sirt1 binding to NFkB, however there is no change in acetylated NFkB upon infection (Fig 4B). Acetylated p65 is equally high in uninfected Scrambled siRNA, UI shSirt1, STM Scr, and STM shSirt1. Furthermore, increased binding of Sirt1 with NFkb would mean decreased acetylation hence decreased inflammation. However, Salmonella induces profound inflammation.

We thank the reviewers for their insightful and critical questioning. We truly acknowledge that due to oversaturation there was no apparent change in the acetylated p65 among the different sample sets. Therefore, in the revised manuscript we have provided an image at lower exposure where the changes in the acetylation of the p65 subunit are apparent. Salmonella induces inflammation upon challenge similar to any other pathogens and induces acute inflammatory responses. This heightened acute inflammation at the initial phases of infection subsides at a later phase of infection. Here, we have performed the Sirt1 interaction with NFκB at 16hr post-infection where increased binding of Sirt1 with NFκB facilitates the resolution of the Salmonella-_induced acute inflammation. This is in line with previous reports that suggest SIRT1 suppresses acute inflammation through the promotion of p65 acetylation and inhibition of NFκB activity. (Yang H, Zhang W, Pan H, et al. SIRT1 activators suppress inflammatory responses through promotion of p65 deacetylation and inhibition of NF-κB activity. _PLoS One. 2012;7(9):e46364. doi:10.1371/journal.pone.0046364, Liu TF, Yoza BK, El Gazzar M, Vachharajani VT, McCall CE. NAD+-dependent SIRT1 deacetylase participates in epigenetic reprogramming during endotoxin tolerance. J Biol Chem. 2011;286(11):9856–64., Liu TF, Vachharajani V, Millet P, Bharadwaj MS, Molina AJ, McCall CE. Sequential actions of SIRT1-RELB-SIRT3 coordinate nuclear-mitochondrial communication during immunometabolic adaptation to acute inflammation and sepsis. J Biol Chem. 2015;290(1):396–408.)

Please explain how the acetylated p65 was analysed.

Total endogenous p65 subunit was immunoprecipitated using Anti-NFκB p65 antibody and the immunoprecipitated fraction was probed with Anti-Acetylated Lysine antibody to assess acetylated p65.

An increase in ROS production is seen in a relatively small percentage of cells- not more than 4% of cells. How does this contribute to such a significant difference in intracellular bacterial burden? Also, it is not clear how the authors calculated the fold change in proliferation. It is better to show the actual bacterial burden logarithmically.

We strongly agree with the reviewer’s concerns, and we have reanalyzed the flow cytometric data set. The revised data have been presented in Fig. S5 which shows a considerable increase in DCFDA positive population. For instance, the infected scrambled control shows around 2.44% of ROS-producing cells, however knockdown of SIRT1 and SIRT3 increases the ROS-producing cells to 27.34% and 28.64% respectively.

Fold proliferation was calculated as CFU at 16hr divided by CFU at 2hr as mentioned in the materials and methods section under the heading of Intracellular proliferation or gentamicin protection assay. Fold proliferation has been calculated as opposed to absolute CFU values to nullify the differential phagocytosis of bacteria to the macrophages among the samples.

Fold Proliferation= [CFU at 16h]/[CFU at 2h]

An increase in metabolic genes is not sufficient to show that the macrophages are metabolically reprogrammed.

We thank the reviewer for the valuable comment. We agree that an increase in metabolic gene profile is not sufficient to claim metabolic reprogramming. Therefore, in addition to the metabolic gene profile, we have estimated lactate production (end-product of glycolysis) as an indicator of glycolysis (Fig. 5 C-E) and have performed the fatty acid β oxidation activity (Fig. 5G-H) to support our claims.

Figure 5F the band intensities do not visually match the bands shown for PFK. For instance, shSIRT1 STM (1.00) and shSIRT3 STM (0.81).

We are extremely sorry for the erroneous band intensity for shSIRT3. Upon reanalysis of the band intensities, we have corrected the band intensity for shSIRT3 to 2.28 (Fig.5F).

It is surprising that HADHA is not expressed in uninfected samples.

We are extremely apologetic for the inappropriate representative blot. We feel that the discrepancy might have arisen due to the usage of old antibodies. We have provided an alternate blot for the HADHA gene where fresh antibody staining solution was used for probing which shows expression even in the uninfected samples (Fig.5F).

Figure 6A - What is the significance of PFA fixed samples (PI) compared to SI samples? This has not been discussed.

PFA-fixed samples are paraformaldehyde-treated bacterial samples that harbor the immune signals or Pattern Associated Molecular Patterns (PAMPs). The rationale for using PI in addition to SI samples was to show whether the phenomena is driven by live metabolically active pathogens or is mediated by PAMPs.

I understand that the hypothesis is that during the later phase of infection, there is an increase in fatty acid oxidation which correlates with a decrease in inflammation. However, at 6h there is no increase in genes regulating fatty acid oxidation. Why did the authors choose 6h when the previous experiments have been done at 16h?

We indeed agree with the reviewer’s understanding of our hypothesis that there is an increase in fatty acid oxidation along the progression of infection which correlates with a decrease in inflammation. The Salmonella intracellular replication has been reported to commence at 6h post-internalization when SPI-2 effector expression is fully established (Helaine S, Thompson JA, Watson KG, Liu M, Boyle C, Holden DW. Dynamics of intracellular bacterial replication at the single cell level. Proc Natl Acad Sci U S A. 2010;107(8):3746-3751. doi:10.1073/pnas.1000041107). Therefore, we have assessed the 6h timepoint post-infection in addition to the initial and later timepoints of 2h and 16h respectively. Additionally, the nanostring gene profiling data of both host and bacterial genes indicate the onset of both metabolic (Fig. 5A, 6A) and immune genes (Fig. 3A) modulation at 6h post-infection. We have validated these results via qPCR studies and have observed an upregulation in the transcript level of fatty acid oxidation genes as depicted in Fig. S7A in RAW264.7 macrophages.

Line 355 it is mentioned that Sirt1 and Sirt3 abrogate metabolic shift by reducing glycolytic flux. This is incorrect as experiments such as carbon chase assays have not been performed to investigate glycolytic flux.

As per the reviewer’s valuable suggestion, we have removed the word ‘flux’ from the above-mentioned statement(Line 351, Line 353).

Lines 392-393: "We immunoprecipitated PDHA1 and checked for its interaction with SIRT3 or SIRT1 under knockdown condition of SIRT3 or upon SIRT3 inhibitor treatment (Fig.7 G-H)"

What is the rationale for checking PDHA1 interaction with Sirt under Sirt knockdown conditions?

We are thankful to the reviewer for the critical comments. The rationale for checking PDHA1 interaction with Sirt was to ascertain that indeed Sirt interacted with PDHA1 under S. Typhimurium infection and abrogation of either protein expression (knockdown) or their enzymatic activity (inhibitor treatment) diminished the interaction.

Moreover, the blots are very confusing and do not represent the authors' claims.

(1) In the input blot I do not see Sirt3 depletion in shSirt3 knockdown sample.

The knockdown has been quantified in the input blot as per your suggestion. A knockdown of 40% has been obtained in the uninfected dataset whereas a knockdown of 47.1% has been obtained in the infected data set at 16h post-infection (Fig.7H).

(2) Why does Sirt1 interact with PDHA1 similar to Sirt3. Do both the proteins bind to PDHA1 at the same time/ competitively? If so do they both deacetylate?

In literature, Sirt3 has been shown to interact with PDHA1 and deacetylate PDHA1. However, the interaction of Sirt1 with PDHA1 has not been reported previously and therefore we are unable to comment on the exact dynamics of the interaction. Future studies need to be performed to explore these phenomena in depth. However, SIRT1 agonist SRT1720 has been shown to impact PDH phosphorylation and its activity (Han Y, Sun W, Ren D, Zhang J, He Z, Fedorova J, Sun X, Han F, Li J. SIRT1 agonism modulates cardiac NLRP3 inflammasome through pyruvate dehydrogenase during ischemia and reperfusion. Redox Biol. 2020 Jul;34:101538).

(3) Figure 7I in the IP: IgG samples Sirt3 seem to bind to IgG non-specifically, which questions the specificity of Sirt3 binding to PDHA1.

We appreciate the reviewer for pointing out this concern. The immunoprecipitation experiment has been repeated and the same has been appended in the revised manuscript and we observe no non-specific binding of Sirt3 antibody to IgG.

(4) In Figure 7I all the bands Ac PDHA1, PDHA1, and Sirt3 look similar with double bands, which has not been seen in other blots. How is this possible?

This cannot explain the increase in beta-oxidation observed.

We thank the reviewer for raising this concern. We have repeated the experiment and provided the alternative blot as per the reviewer’s suggestion.

The rationale for performing this experiment was to show that SIRT plays an important role in the activation of downstream TCA cycle pathways via PDHA1 deacetylation during Salmonella infection. The deacetylation of PDHA1 has been previously reported to cause transcriptional activation of the downstream TCA cycle and oxidative phosphorylation (Zhang Y, Wen P, Luo J, et al., Cell Death Dis.,2021). Additionally, PDHA1 hyperacetylation has been reported to cause lactate overproduction (An, S., Yao, Y., Hu, H. et al. PDHA1 hyperacetylation-mediated lactate overproduction promotes sepsis-induced acute kidney injury via Fis1 lactylation. Cell Death Dis 14, 457 (2023)). In our study, increased lactate production and PDHA1 hyperacetylation have been observed during SIRT3 inhibition conditions upon Salmonella infection.