Author response:

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

Public Reviews:

Review #1:

Summary:

Jin et al. investigated how the bacterial DNA damage (SOS) response and its regulator protein RecA affect the development of drug resistance under short-term exposure to beta-lactam antibiotics. Canonically, the SOS response is triggered by DNA damage, which results in the induction of error-prone DNA repair mechanisms. These error-prone repair pathways can increase mutagenesis in the cell, leading to the evolution of drug resistance. Thus, inhibiting the SOS regulator RecA has been proposed as a means to delay the rise of resistance. 

In this paper, the authors deleted the RecA protein from E. coli and exposed this ∆recA strain to selective levels of the beta-lactam antibiotic, ampicillin. After an 8-hour treatment, they washed the antibiotic away and allowed the surviving cells to recover in regular media. They then measured the minimum inhibitory concentration (MIC) of ampicillin against these treated strains. They note that after just 8-hour treatment with ampicillin, the ∆recA had developed higher MICs towards ampicillin, while by contrast, wild-type cells exhibited unchanged MICs. This MIC increase was also observed in subsequent generations of bacteria, suggesting that the phenotype is driven by a genetic change.

The authors then used whole genome sequencing (WGS) to identify mutations that accounted for the resistance phenotype. Within resistant populations, they discovered key mutations in the promoter region of the beta-lactamase gene, ampC; in the penicillin-binding protein PBP3 which is the target of ampicillin; and in the AcrB subunit of the AcrAB-TolC efflux machinery. Importantly, mutations in the efflux machinery can impact the resistance towards other antibiotics, not just beta-lactams. To test this, they repeated the MIC experiments with other classes of antibiotics, including kanamycin, chloramphenicol, and rifampicin. Interestingly, they observed that the ∆recA strains pre-treated with ampicillin showed higher MICs towards all other antibiotics tested. This suggests that the mutations conferring resistance to ampicillin are also increasing resistance to other antibiotics.

The authors then performed an impressive series of genetic, microscopy, and transcriptomic experiments to show that this increase in resistance is not driven by the SOS response, but by independent DNA repair and stress response pathways. Specifically, they show that deletion of the recA reduces the bacterium's ability to process reactive oxygen species (ROS) and repair its DNA. These factors drive the accumulation of mutations that can confer resistance to different classes of antibiotics. The conclusions are reasonably well-supported by the data, but some aspects of the data and the model need to be clarified and extended.

We sincerely appreciate your overall summary of the manuscript and their positive evaluation of our work.

Strengths:

A major strength of the paper is the detailed bacterial genetics and transcriptomics that the authors performed to elucidate the molecular pathways responsible for this increased resistance. They systemically deleted or inactivated genes involved in the SOS response in E. coli. They then subjected these mutants to the same MIC assays as described previously. Surprisingly, none of the other SOS gene deletions resulted in an increase in drug resistance, suggesting that the SOS response is not involved in this phenotype. This led the authors to focus on the localization of DNA PolI, which also participates in DNA damage repair. Using microscopy, they discovered that in the RecA deletion background, PolI co-localizes with the bacterial chromosome at much lower rates than wild-type. This led the authors to conclude that deletion of RecA hinders PolI and DNA repair. Although the authors do not provide a mechanism, this observation is nonetheless valuable for the field and can stimulate further investigations in the future.

In order to understand how RecA deletion affects cellular physiology, the authors performed RNA-seq on ampicillin-treated strains. Crucially, they discovered that in the RecA deletion strain, genes associated with antioxidative activity (cysJ, cysI, cysH, soda, sufD) and Base Excision Repair repair (mutH, mutY, mutM), which repairs oxidized forms of guanine, were all downregulated. The authors conclude that down-regulation of these genes might result in elevated levels of reactive oxygen species in the cells, which in turn, might drive the rise of resistance. Experimentally, they further demonstrated that treating the ∆recA strain with an antioxidant GSH prevents the rise of MICs. These observations will be useful for more detailed mechanistic follow-ups in the future.

We are grateful to you for your positive assessment of the strengths of our manuscript and your recognition of its potential future applications.

Weaknesses:

Throughout the paper, the authors use language suggesting that ampicillin treatment of the ∆recA strain induces higher levels of mutagenesis inside the cells, leading to the rapid rise of resistance mutations. However, as the authors note, the mutants enriched by ampicillin selection can play a role in efflux and can thus change a bacterium's sensitivity to a wide range of antibiotics, in what is known as cross-resistance. The current data is not clear on whether the elevated "mutagenesis" is driven ampicillin selection or by a bona fide increase in mutation rate.

We greatly appreciate you for raising this issue, as it is an important premise that must be clearly stated throughout the entire manuscript. To verify that the observed increase in mutation rate is a bona fide increase and not due to experimental error, we used a non-selective antibiotic, rifampicin, to evaluate the mutation frequency after drug induction, as it is a gold-standard method documented in other studies [Heterogeneity in efflux pump expression predisposes antibiotic-resistant cells to mutation, Science, 362, 6415, 686-690, 2018.]. In the absence of ampicillin treatment, the natural mutation rates detected using rifampicin were consistent between the wild-type and the ΔrecA strain. However, after ampicillin treatment, the mutation rate detected using rifampicin was significantly elevated only in the ΔrecA strain (Fig. 1G). We also employed other antibiotics, such as ciprofloxacin and chloramphenicol, in our experiments to treat the cells (data not shown). However, we observed that beta-lactam antibiotics specifically induced the emergence of resistance or altered the MIC in our bacterial populations. If resistance had pre-existed before antibiotic exposure or a bona fide increase in mutation rate, we would expect other antibiotics to exhibit a similar selective effect, particularly given the potential for cross-resistance to multiple antibiotics.

Furthermore, on a technical level, the authors employed WGS to identify resistance mutations in the treated ampicillin-treated wild-type and ∆recA strains. However, the WGS methodology described in the paper is inconsistent. Notably, wild-type WGS samples were picked from non-selective plates, while ΔrecA WGS isolates were picked from selective plates with 50 μg/mL ampicillin. Such an approach biases the frequency and identity of the mutations seen in the WGS and cannot be used to support the idea that ampicillin treatment induces higher levels of mutagenesis.

We appreciate your concern regarding potential inconsistencies in the WGS methodology. However, we would like to clarify that the primary aim of the WGS experiment was to identify the types of mutations present in the wild-type and ΔrecA strains after treatment of ampicillin, rather than to quantify or compare mutation frequencies. This purpose was explicitly stated in the manuscript.

Furthermore, the choice of selective and non-selective conditions was made to ensure the successful isolation of mutants in both strains. Specifically, if selective conditions (50 μg/mL ampicillin) were applied to the wild-type strain, it would have been nearly impossible to recover colonies for WGS analysis, as wild-type cells are highly susceptible to ampicillin at this concentration (Top, Author response image 1). Conversely, under non-selective conditions, ΔrecA mutants carrying resistance mutations may not have been effectively isolated, which would have limited our ability to identify resistance mutations in these strains (Bottom, Author response image 1 Thus, the use of different selection pressures was essential for achieving the objective of mutation identification in this study.

Author response image 1.

After 8 hours of antibiotic treatment, the wild type or the ΔrecA cells were plated on agar plates either without ampicillin or with 50 μg/mL ampicillin and incubated for 24-48 hours. Top: Under selective conditions, no wild type colonies were recovered, indicating high susceptibility to the antibiotic, preventing further analysis. Bottom: In non-selective conditions, both ΔrecA resistant mutants and non-resistant cells grew, making it difficult to distinguish and isolate the mutants carrying resistance mutations.

Finally, it is important to establish what the basal mutation rates of both the WT and ∆recA strains are. Currently, only the ampicillin-treated populations were reported. It is possible that the ∆recA strain has inherently higher mutagenesis than WT, with a larger subpopulation of resistant clones. Thus, ampicillin treatment might not in fact induce higher mutagenesis in ∆recA.

Thanks for this suggestion. The basal mutation frequency of the wild-type and the ∆recA strain have been measured using rifampicin (Fig. 1G), and there is no significant difference between them.

Reviewer #2:

Summary:

This study aims to demonstrate that E. coli can acquire rapid antibiotic resistance mutations in the absence of a DNA damage response. To investigate this, the authors employed a sophisticated experimental framework based on a modified Adaptive Laboratory Evolution (ALE) workflow. This workflow involves numerous steps culminating in the measurement of antibiotic resistance. The study presents evidence that a recA strain develops ampicillin resistance mutations more quickly than the wild-type, as shown by measuring the Minimum Inhibitory Concentration (MIC) and mutation frequency. Whole-genome sequencing of 15 recA-colonies resistant to ampicillin revealed predominantly inactivation of genes involved in the multi-drug efflux pump system, whereas, in the wild-type, mutations appear to enhance the activity of the chromosomal ampC cryptic promoter. By analyzing mutants involved in the SOS response, including a lexA3 mutant incapable of inducing the SOS response, the authors conclude that the rapid evolution of antibiotic resistance occurs in an SOS-independent manner when recA is absent.

Furthermore, RNA sequencing (RNA-seq) of the four experimental conditions suggests that genes related to antioxidative responses drive the swift evolution of antibiotic resistance in the recA-strain.

We greatly appreciate your overall summary of the manuscript and their positive evaluation of our work.

Weaknesses:

However, a potential limitation of this study is the experimental design used to determine the 'rapid' evolution of antibiotic resistance. It may introduce a significant bottleneck in selecting ampicillin-resistant mutants early on. A recA mutant could be more susceptible to ampicillin than the wild-type, and only resistant mutants might survive after 8 hours, potentially leading to their enrichment in subsequent steps. To address this concern, it would be critical to perform a survival analysis at various time points (0h, 2h, 4h, 6h, and 8h) during ampicillin treatment for both recA and wild-type strains, ensuring there is no difference in viability.

We appreciate your suggestion. We measured the survival fraction at 0, 2, 4, 6, and 8 hours after ampicillin treatment. The results show no significant difference in antibiotic sensitivity between the wild-type and ΔrecA strain (Fig. S2). We therefore added a description int the main text, “Meanwhile, after 8 hours of treatment with 50 μg/mL ampicillin, the survival rates of both wild type and ΔrecA strain were consistent (Fig. S2)”.

The observation that promoter mutations are absent in ΔrecA strains could be explained by previous research indicating that amplification of the AmpC genes is a mechanism for E. coli resistance to ampicillin, which does not occur in a recA-deficient background (PMID# 19474201).

We are very grateful to you for providing this reference. We did examine the amplification of the ampC gene in both wild-type and _recA-_deficient strains, but we found no significant changes in its copy number after ampicillin treatment (Author response image 2). Therefore, the results and discussion regarding gene copy number were not included in this manuscript.

Author response image 2.

Copy number variations of genes in the chromosome before and after exposure to ampicillin at 50 µg/mL for 8 hours in the wild type and ΔrecA strain.

The section describing Figure 3 is poorly articulated, and the conclusions drawn are apparent. The inability of a recA strain to induce the SOS response is well-documented (lines 210 and 278). The data suggest that merely blocking SOS induction is insufficient to cause 'rapid' evolution in their experimental conditions. To investigate whether SOS response can be induced independently of lexA cleavage by recA, alternative experiments, such as those using a sulA-GFP fusion, might be more informative.

Thanks for your suggestion. We agree that detecting the expression level of SulA can provide valuable information to reveal the impact of the SOS system on rapid drug resistance. In addition to fluorescence visualization and quantification of SulA expression, regulating the transcription level of the sulA gene can achieve the same objective. Therefore, in our transcriptome sequencing analysis, we focused on evaluating the transcription level of sulA (Fig. 4E).

In Figure 4E, the lack of increased SulA gene expression in the wild-type strain treated with ampicillin is unexpected, given that SulA is an SOS-regulated gene. The fact that polA (Pol I) is going down should be taken into account in the interpretation of Figures 2D and 2E.

Thank you for your observation regarding the lack of increased SulA gene expression in the wild-type strain treated with ampicillin in Figure 4E. We agree that SulA is typically an SOS-regulated gene, and its expression is expected to increase in response to DNA damage induced by antibiotics like ampicillin. However, in our experimental conditions, the observed lack of increased SulA expression could be due to different factors. One possibility is that the concentration of ampicillin used, or the duration of treatment, was not applicable to induce a strong SOS response in the wild type strain under the specific conditions tested. Additionally, differences in experimental setups such as timing, sampling, or cellular stress responses could account for the lack of a pronounced upregulation of SulA.

You may state that the fact that polA (Pol I) is going down should be taken into account in the interpretation of Figures 3D and 3E, and we agree with you.

The connection between compromised DNA repair, the accumulation of Reactive Oxygen Species (ROS) based on RNA-seq data, and accelerated evolution is merely speculative at this point and not experimentally established.

We greatly appreciate your comments. First, the correlation between DNA mutations and the accumulation of reactive oxygen species (ROS) has been experimentally confirmed. As shown in Fig. 4I, after the addition of the antioxidant GSH, DNA resistance mutations were not detected in the ΔrecA strain treated with ampicillin for 8 hours, compared to those without the addition of GSH, proving that the rapid accumulation of ROS induces the enhancement of DNA resistance mutations. Second, the enhancement of DNA resistance mutations in relation to bacterial resistance has been widely validated and is generally accepted. Finally, we appreciate the your suggestion to strengthen the evidence supporting ROS enhancement. To address this, we have added an experiment to measure ROS levels. Through flow cytometry, we found that ROS levels significantly increased in both the wild-type and ΔrecA strain after 8 hours of ampicillin treatment. However, ROS levels in the ΔrecA strain showed a significant further increase compared to the wild-type strain (Fig. 4G). Additionally, with the addition of 50 mM glutathione, no significant change in ROS levels was observed in either the wild-type or ΔrecA strain before and after ampicillin treatment (Fig. 4H). This result further confirms our finding in Fig. 4I, where adding GSH inhibited the development of antibiotic resistance.

Reviewer #3:

Summary:

In the present work, Zhang et al investigate the involvement of the bacterial DNA damage repair SOS response in the evolution of beta-lactam drug resistance evolution in Escherichia coli. Using a combination of microbiological, bacterial genetics, laboratory evolution, next-generation, and live-cell imaging approaches, the authors propose short-term drug resistance evolution that can take place in RecA-deficient cells in an SOS response-independent manner. They propose the evolvability of drug resistance is alternatively driven by the oxidative stress imposed by the accumulation of reactive oxygen species and inhibition of DNA repair. Overall, this is a nice study that addresses a growing and fundamental global health challenge (antimicrobial resistance). However, although the authors perform several multi-disciplinary experiments, there are several caveats to the authors' proposal that ultimately do not fully support their interpretation that the observed antimicrobial resistance evolution phenotype is due to compromised DNA repair.

We greatly appreciate your overall summary of the manuscript and positive evaluation of our work.

Strengths:

The authors introduce new concepts to antimicrobial resistance evolution mechanisms. They show short-term exposure to beta-lactams can induce durably fixed antimicrobial resistance mutations. They propose this is due to comprised DNA repair and oxidative stress. This is primarily supported by their observations that resistance evolution phenotypes only exist for recA deletion mutants and not other genes in the SOS response.

Thanks for your positive comments.

Weaknesses:

The authors do not show any direct evidence (1) that these phenotypes exist in strains harboring deletions in other DNA repair genes outside of the SOS response, (2) that DNA damage is increased, (3) that reactive oxygen species accumulate, (4) that accelerated resistance evolution can be reversed by anything other than recA complementation. The authors do not directly test alternative hypotheses. The conclusions drawn are therefore premature.

We sincerely thank you for your insightful comments. First, in this study, our primary focus is on the role of recA deficiency in bacterial antibiotic resistance evolution. Therefore, we conducted an in-depth investigation on E. coli strains lacking RecA and found that its absence promotes resistance evolution through mechanisms involving increased ROS accumulation and downregulation of DNA repair pathways. While we acknowledge the importance of other DNA repair genes outside of the SOS response, exploring them is beyond the scope of this paper. However, in a separate unpublished study, we have identified the involvement of another DNA recombination protein, whose role in resistance evolution is not yet fully elucidated, in promoting resistance development. This finding is part of another independent investigation.

Regarding DNA damage and repair, our paper emphasizes that resistance-related mutations in DNA are central to the development of antibiotic resistance. These mutations are a manifestation of DNA damage. To demonstrate this, we measured mutation frequency and performed whole-genome sequencing, both of which confirmed an increase in DNA mutations.

We appreciate the reviewer's suggestion to provide additional evidence for ROS accumulation, and we have now supplemented our manuscript with relevant experiments. Through flow cytometry, we found that ROS levels significantly increased in both the wild type and ΔrecA strains after 8 hours of ampicillin treatment. However, ROS levels in the ΔrecA strain showed a significant further increase compared to the wild-type strain (Fig. 4G). Additionally, with the addition of 50 mM glutathione, no significant change in ROS levels was observed in either the wild-type or ΔrecA strain before and after ampicillin treatment (Fig. 4H). This result further confirms our finding in Fig. 4I, where adding GSH inhibited the development of antibiotic resistance.

Finally, in response to your question about reversing accelerated resistance evolution, we would like to highlight that, in addition to recA complementation, we successfully suppressed rapid resistance evolution by supplementing with an antioxidant, GSH (Fig. 4I). This further supports our hypothesis that increased ROS levels play a key role in driving accelerated resistance evolution in the absence of RecA.

Recommendations for the authors:

Reviewer #1:

The author's model asserts that deletion of recA impairs DNA repair in E. coli, leading to an accumulation of ROS in the cell, and ultimately driving the rapid rise of resistance mutations. However, the experimental evidence does not adequately address whether the resistance mutations are true, de novo mutations that arose due to beta-lactam treatment, or mutations that confer cross-resistance enriched by ampicillin selection.

a. Major: In Figure 1F & G, the authors show that the ∆recA strain, following ampicillin treatment, has higher resistance and mutation frequency towards rifampicin than WT. However, it is not clear whether the elevated resistance and mutagenesis are driven by mutations enriched by the ampicillin treatment (e.g. mutations in acrB, as seen in Figure 2) or by "new" mutations in the rpoB gene. As the authors note, the mutants enriched by ampicillin selection can play a role in efflux and can thus change a bacterium's sensitivity to a wide range of antibiotics, including rifampicin, in what is known as cross-resistance. Therefore, the mutation frequency calculation, which relies on quantifying rifampicin-resistant clones, might be confounded by bacteria with mutations that confer cross-resistance. A better approach to calculate mutation frequency would be to employ an assay that does not require antibiotic selection, such as a lac-reversion assay. This would mitigate the confounding effects of cross-resistance of drug-resistant mutations.

We appreciate your thoughtful comments regarding the potential for cross-resistance to confound the mutation frequency calculation based on rifampicin-resistant clones. Indeed, as noted, ampicillin selection can enrich for mutants with enhanced efflux activity, which may confer cross-resistance to a range of antibiotics, including rifampicin.

However, we believe that the current approach of calculating mutation frequency using rifampicin-resistant mutants is still valid in our specific context. Rifampicin targets the RNA polymerase β subunit, and resistance typically arises from specific mutations in the rpoB gene. These mutations are well-characterized and distinct from those typically associated with efflux-related cross-resistance. Thus, the likelihood of cross-resistance affecting our mutation frequency calculation is minimized in this scenario.

Additionally, while the lac-reversion assay could be an alternative, it focuses on specific metabolic pathway mutations (such as those affecting lacZ) and would not necessarily capture the same types of mutations relevant to rifampicin resistance or antibiotic-induced mutagenesis. Given our experimental objective of understanding how ampicillin induces mutations that confer antibiotic resistance, the current approach of using rifampicin selection provides a direct and relevant measurement of mutation frequency under antibiotic stress.

b. Major: It is important to establish what the basal mutation frequencies/rates of both the WT and ∆recA strains are. Currently, only the ampicillin-treated populations were reported. It is possible that the ∆recA strain has an inherently higher mutagenesis than WT. Thus, ampicillin treatment might not in fact induce higher mutagenesis in ∆recA.

Thanks for your suggestion. The basal mutation frequency of the wild-type and the ∆recA strain have been measured using rifampicin (Fig. 1G), and there is no significant difference between them.

c. Major: In the text, the authors write, "To verify whether drug resistance associated DNA mutations have led to the rapid development of antibiotic resistance in recA mutant strain, we randomly selected 15 colonies on non-selected LB agar plates from the wild type surviving isolates, and antibiotic screening plates containing 50 μg/mL ampicillin from the ΔrecA resistant isolates, respectively." Why were the WT clones picked from non-selective plates and the recA mutant from selective ones for WGS? It appears that such a procedure would bias the recA mutant clones to show more mutations (caused by selection on the ampicillin plate). The authors need to address this discrepancy.

We appreciate your concern regarding potential inconsistencies in the WGS methodology. However, we would like to clarify that the primary aim of the WGS experiment was to identify the types of mutations present in the wild-type and ΔrecA strains after treatment of ampicillin, rather than to quantify or compare mutation frequencies. This purpose was explicitly stated in the manuscript.

Furthermore, the choice of selective and non-selective conditions was made to ensure the successful isolation of mutants in both strains. Specifically, if selective conditions (50 μg/mL ampicillin) were applied to the wild type strain, it would have been nearly impossible to recover colonies for WGS analysis, as wild-type cells are highly susceptible to ampicillin at this concentration (Top, Author response image 1). Conversely, under non-selective conditions, ΔrecA mutants carrying resistance mutations may not have been effectively isolated, which would have limited our ability to identify resistance mutations in these strains (Bottom, Author response image 1). Thus, the use of different selection pressures was essential for achieving the objective of mutation identification in this study.

d. Major: In some instances, the authors do not use accurate language to describe their data. In Figure 2A, the authors randomly selected 15 ∆recA clones from a selective plate with 50 µg/mL of ampicillin. These clones were then subjected to WGS, which subsequently identified resistant mutations. Based on the described methods, these mutations are a result of selection: in other words, resistant mutations were preexisting in the bacterial population, and the addition of ampicillin selection killed off the sensitive cells, enabling the proliferation of the resistant clones. However, the in Figure 2 legend and associated text, the authors suggest that these mutations were "induced" by beta-lactam exposure, which is misleading. The data does not support that.

We appreciate your detailed feedback on the language used to describe our data. We understand the concern regarding the use of the term "induced" in relation to beta-lactam exposure. To clarify, we employed not only beta-lactam antibiotics but also other antibiotics, such as ciprofloxacin and chloramphenicol, in our experiments (data not shown). However, we observed that beta-lactam antibiotics specifically induced the emergence of resistance or altered the MIC in our bacterial populations. If resistance had pre-existed before antibiotic exposure, we would expect other antibiotics to exhibit a similar selective effect, particularly given the potential for cross-resistance to multiple antibiotics.

Furthermore, we used two different ∆recA strains, and the results were consistent between the strains (Fig. S3). Given that spontaneous mutations can occur with significant variability in populations, if resistance mutations pre-existed before antibiotic exposure, the selective outcomes should have varied between the two strains.

Most importantly, we found that the addition of anti-oxidative compound GSH prevented the evolution of antibiotic from the treatment of ampicillin in the ΔrecA strain. If we assume that resistant bacteria preexist in the ∆recA strain, then the addition of GSH should not affect the evolution of resistance. Therefore, we believe that the resistance mutations we detected were not simply the result of selection from preexisting mutations but were indeed induced by beta-lactam exposure.

e. Major: For Figure 4J, using WGS the authors show that the addition of GSH to WT and ∆recA cells inhibited the rise of resistance mutations; no resistance mutations were reported. However, in the "Whole genome sequencing" section under "Materials and Methods", they state that "Resistant clones were isolated by selection using LB agar plates with the supplementation of ampicillin at 50 μg/mL". These clones were then genome-extracted and sequenced. Given the methodology, it is surprising that the WGS did not reveal any resistance mutations in the GSH-treated cells. How were these cells able to grow on 50 μg/mL ampicillin plates for isolation in the first place? The authors need to address this.

We sincerely apologize for the confusion caused by the incorrect expression in the "Materials and Methods" section. Indeed, when bacteria were treated with the combination of antibiotics and GSH, resistance was significantly suppressed, and no resistant clones could be isolated from selective plates (i.e., LB agar supplemented with 50 μg/mL ampicillin).

To address this, we instead plated the bacteria treated with antibiotics and GSH onto non-selective plates (without ampicillin) and randomly selected 15 colonies for WGS. None of them showed resistance mutations. We will revise the text in the "Materials and Methods" section to accurately reflect this procedure and provide clarity.

f. Minor: for Figure 1G, it is misleading to have both "mutation frequency" and "mutant rate" in the y-axis; the two are defined and calculated differently. Based on the Materials and Materials, "mutation frequency" would be the appropriate term. Also, for the ∆recA strain, it is a bit unusual to see mutation frequencies that are tightly clustered. Usually, mutation frequencies follow the Luria-Delbruck distribution. Can the authors explain why the ∆recA data looks so different compared to, say, the WT mutation frequencies?

Thank you for your insightful feedback. We agree that having both "mutation frequency" and "mutant rate" on the y-axis is misleading, as these terms are defined and calculated differently. To avoid confusion, we will revise Figure 1G to use only "mutation frequency" as the correct term, in line with the methods described in the Materials and Methods section.

Regarding the ∆recA strain's mutation frequencies, we acknowledge that the data appear more tightly clustered compared to the expected Luria-Delbruck distribution seen in the wild type strain. In fact, the y-axis of the Figure 1G is logarithmic, this causes the data to appear more clustered.

We further added the basal mutation frequency in the wild type and ∆recA strains before the exposure to ampicillin. The basal mutation frequency of the wild-type and the ∆recA strain have been measured using rifampicin (Fig. 1G), and there is no significant difference between them.

g. Minor: It needs to be made clear in the Main Text what the selective antibiotic agar plate used was, rifampicin or ampicillin. I am assuming it was rifampicin, as ampicillin plates would yield resistance frequencies close to 100%, given the prior treatment of the culture with ampicillin.

Thanks for your comments. Depending on the objective, we used different selective plates. For example, when testing the mutation frequency of antibiotic resistance, we used a selective plate containing rifampicin in order to utilize a non-inducing antibiotic, which is the standard method for calculating resistance mutation frequency. In the WGS experiment, to obtain mutations specific to ampicillin resistance, we selected a selective plate containing ampicillin.

Reviewer #2:

The Y-axis label (log10 mutant rate) in Figure 1G is misleading or incorrect.

Thanks for your comments and we apologize for this misleading information. The Figure 1G has been revised accordingly.

In line 393 of the discussion, the authors claim that excessive ROS accumulation drives the evolution of ampicillin resistance, which has not been conclusively demonstrated. Additional experiments are needed to support this statement.

We greatly appreciate your comments. First, the correlation between DNA mutations and the accumulation of reactive oxygen species (ROS) has been experimentally confirmed. As shown in Fig. 4I, after the addition of the antioxidant GSH, DNA resistance mutations were not detected in the ΔrecA strain treated with ampicillin for 8 hours, compared to those without the addition of GSH, proving that the rapid accumulation of ROS induces the enhancement of DNA resistance mutations. Second, the enhancement of DNA resistance mutations in relation to bacterial resistance has been widely validated and is generally accepted. Finally, we appreciate the your suggestion to strengthen the evidence supporting ROS enhancement. To address this, we have added an experiment to measure ROS levels. Through flow cytometry, we found that ROS levels significantly increased in both the wild-type and ΔrecA strain after 8 hours of ampicillin treatment. However, ROS levels in the ΔrecA strain showed a significant further increase compared to the wild-type strain (Fig. 4G). Additionally, with the addition of 50 mM glutathione, no significant change in ROS levels was observed in either the wild-type or ΔrecA strain before and after ampicillin treatment (Fig. 4H). This result further confirms our finding in Fig. 4I, where adding GSH inhibited the development of antibiotic resistance.

The abstract is overly complex and difficult to read, e.g. "Contrary to previous findings, it is shown that this accelerated resistance development process is dependent on the hindrance of DNA repair, which is completely orthogonal to the SOS response").

Thank you for the valuable feedback regarding the complexity of the abstract. We agree that certain sections could be simplified for clarity. In response, we have revised the abstract to make it more concise and easier to understand. For example, the sentence “Contrary to previous findings, it is shown that this accelerated resistance development process is dependent on the hindrance of DNA repair, which is completely orthogonal to the SOS response” has been rewritten as: "Unlike earlier studies, we found that the rapid development of resistance relies on the hindrance of DNA repair, a mechanism that operates independently of the SOS response."

Reviewer #3:

As indicated above, direct evidence is needed to show (1) that these phenotypes exist in strains harboring deletions in other DNA repair genes outside of the SOS response, (2) that DNA damage is increased, (3) that reactive oxygen species accumulate, (4) that accelerated resistance evolution can be reversed by anything other than recA complementation. There are also other resistance evolution mechanisms untested here, including transcription-coupled repair (TCR) mechanisms involving Mfd. These need to be shown in order to draw the conclusions proposed.

We sincerely thank you for your insightful comments. First, in this study, our primary focus is on the role of recA deficiency in bacterial antibiotic resistance evolution. Therefore, we conducted an in-depth investigation on E. coli strains lacking RecA and found that its absence promotes resistance evolution through mechanisms involving increased ROS accumulation and downregulation of DNA repair pathways. While we acknowledge the importance of other DNA repair genes outside of the SOS response and other resistance evolution mechanisms including the TCR mechanism, exploring them is beyond the scope of this paper. However, in a separate unpublished study, we have identified the involvement of another DNA recombination protein, whose role in resistance evolution is not yet fully elucidated, in promoting resistance development. This finding is part of another independent investigation.

Regarding DNA damage and repair, our paper emphasizes that resistance-related mutations in DNA are central to the development of antibiotic resistance. These mutations are a manifestation of DNA damage. To demonstrate this, we measured mutation frequency and performed whole-genome sequencing, both of which confirmed an increase in DNA mutations.

We appreciate the reviewer's suggestion to provide additional evidence for ROS accumulation, and we have now supplemented our manuscript with relevant experiments. Through flow cytometry, we found that ROS levels significantly increased in both the wild type and ΔrecA strains after 8 hours of ampicillin treatment. However, ROS levels in the ΔrecA strain showed a significant further increase compared to the wild-type strain (Fig. 4G). Additionally, with the addition of 50 mM glutathione, no significant change in ROS levels was observed in either the wild-type or ΔrecA strain before and after ampicillin treatment (Fig. 4H). This result further confirms our finding in Fig. 4I, where adding GSH inhibited the development of antibiotic resistance.

Finally, in response to your question about reversing accelerated resistance evolution, we would like to highlight that, in addition to recA complementation, we successfully suppressed rapid resistance evolution by supplementing with an antioxidant, GSH (Fig. 4I). This further supports our hypothesis that increased ROS levels play a key role in driving accelerated resistance evolution in the absence of RecA.

Author response:

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

eLife Assessment 

This useful study reports how neuronal activity in the prefrontal cortex maps time intervals during which animals have to wait until reaching a reward and how this mapping is preserved across days. However, the evidence supporting the claims is incomplete as these sequential neuronal patterns do not necessarily represent time but instead may be correlated with stereotypical behavior and restraint from impulsive decision, which would require further controls (e.g. behavioral analysis) to clarify the main message. The study will be of interest to neuroscientists interested in decision making and motor control.

We thank the editors and reviewers for the constructive comments. In light of the questions mentioned by the reviewers, we have performed additional analyses in our revision, particularly aiming to address issues related to single-cell scalability, and effects of motivation and movement. We believe these additional data will greatly improve the rigor and clarity of our study. We are grateful for the review process of eLife.

Public Reviews:

Reviewer #1 (Public Review): 

Summary:

This paper investigates the neural population activity patterns of the medial frontal cortex in rats performing a nose poking timing task using in vivo calcium imaging. The results showed neurons that were active at the beginning and end of the nose poking and neurons that formed sequential patterns of activation that covaried with the timed interval during nose poking on a trial-by-trial basis. The former were not stable across sessions, while the latter tended to remain stable over weeks. The analysis on incorrect trials suggests the shorter non-rewarded intervals were due to errors in the scaling of the sequential pattern of activity.

Strengths:

This study measured stable signals using in vivo calcium imaging during experimental sessions that were separated by many days in animals performing a nose poking timing task. The correlation analysis on the activation profile to separate the cells in the three groups was effective and the functional dissociation between beginning and end, and duration cells was revealing. The analysis on the stability of decoding of both the nose poking state and poking time was very informative. Hence, this study dissected a neural population that formed sequential patterns of activation that encoded timed intervals. 

We thank the reviewer for the positive comments.

Weaknesses:

It is not clear whether animals had enough simultaneously recorded cells to perform the analyzes of Figures 2-4. In fact, rat 3 had 18 responsive neurons which probably is not enough to get robust neural sequences for the trial-by-trial analysis and the correct and incorrect trial analysis. 

We thank the reviewer for the comment. Our imaging data generally yielded 50-150 cells in each session. The 18 neurons mentioned by the reviewer are from the duration cell category. We have now provided the number of imaged cells from each rat in the new Supplementary figure 1D. In addition, we have plotted the duration cells’ sequential activity of individual trials for each rat in new Supplementary figure 1B and 1C. These data demonstrate robust sequential activities from the duration cells.

In addition, the analysis of behavioral errors could be improved. The analysis in Figure 4A could be replaced by a detailed analysis on the speed, and the geometry of neural population trajectories for correct and incorrect trials.

We thank the reviewer for the suggestions. We have now performed analyses of the neural population trajectories as the reviewer suggested. We have calculated the neural population trajectories using the first two principal components of the neural activities during nose poke events. While both correct and incorrect trials show similar shapes of the trajectories, correct trials show more expanded paths, with longer lengths on average. These new results are now updated in Figure 4. Since type I or type II errors would likely generate trajectories not following the general direction which is different from our observations, these results are consistent with our conclusion that scaling errors contribute to the incorrect behavior timing in these rats.

In the case of Figure 4G is not clear why the density of errors formed two clusters instead of having a linear relation with the produce duration. I would be recommendable to compute the scaling factor on neuronal population trajectories and single cell activity or the computation of the center of mass to test the type III errors. 

To clarify the original Figure 4G, the correct trials tended to show positive time estimation errors while the incorrect trials showed negative time estimation errors. We believe that the polarity switch between these two types suggests a possible use of this neural mechanism to time the action of the rats.

In addition, we have performed the analysis suggested by the reviewer in our revision. We calculated two types of scaling factors. On individual cell level, we computed the peak position of individual trials to the expected positions from averaged template. And on neural population level, we searched for a scaling multiplier to resample the calcium activity data and minimized the differences between scaled activity and the expected template. Using these two factors, we found that correct trials show significantly larger scaling compared to incorrect trials, consistent with our original interpretation that behavior errors are primarily correlated with scaling errors in the neural activities (type III error). These new results are now incorporated in Figure 4 and we have also updated the main text for the descriptions.

Due to the slow time resolution of calcium imaging, it is difficult to perform robust analysis on ramping activity. Therefore, I recommend downplaying the conclusion that: "Together, our data suggest that sequential activity might be a more relevant coding regime than the ramping activity in representing time under physiological conditions." 

We agree with the reviewer, and have now modified this sentence in the abstract.

Reviewer #2 (Public Review):

In this manuscript, Li and collaborators set out to investigate the neuronal mechanisms underlying "subjective time estimation" in rats. For this purpose, they conducted calcium imaging in the prefrontal cortex of water-restricted rats that were required to perform an action (nosepoking) for a short duration to obtain drops of water. The authors provided evidence that animals progressively improved in performing their task. They subsequently analyzed the calcium imaging activity of neurons and identify start, duration, and stop cells associated with the nose poke. Specifically, they focused on duration cells and demonstrated that these cells served as a good proxy for timing on a trial-by-trial basis, scaling their pattern of actvity in accordance with changes in behavioral performance. In summary, as stated in the title, the authors claim to provide mechanistic insights into subjective time estimation in rats, a function they deem important for various cognitive conditions.

This study aligns with a wide range of studies in system neuroscience that presume that rodents solve timing tasks through an explicit internal estimation of duration, underpinned by neuronal representations of time. Within this framework, the authors performed complex and challenging experiments, along with advanced data analysis, which undoubtedly merits acknowledgement. However, the question of time perception is a challenging one, and caution should be exercised when applying abstract ideas derived from human cognition to animals. Studying so-called time perception in rats has significant shortcomings because, whether acknowledged or not, rats do not passively estimate time in their heads. They are constantly in motion. Moreover, rats do not perform the task for the sake of estimating time but to obtain their rewards are they water restricted. Their behavior will therefore reflects their motivation and urgency to obtain rewards. Unfortunately, it appears that the authors are not aware of these shortcomings. These alternative processes (motivation, sensorimotor dynamics) that occur during task performance are likely to influence neuronal activity. Consequently, my review will be rather critical. It is not however intended to be dismissive. I acknowledge that the authors may have been influenced by numerous published studies that already draw similar conclusions. Unfortunately, all the data presented in this study can be explained without invoking the concept of time estimation. Therefore, I hope the authors will find my comments constructive and understand that as scientists, we cannot ignore alternative interpretations, even if they conflict with our a priori philosophical stance (e.g., duration can be explicitly estimated by reading neuronal representation of time) and anthropomorphic assumptions (e.g., rats estimate time as humans do). While space is limited in a review, if the authors are interested, they can refer to a lengthy review I recently published on this topic, which demonstrates that my criticism is supported by a wide range of timing experiments across species (Robbe, 2023). In addition to this major conceptual issue that cast doubt on most of the conclusions of the study, there are also several major statistical issues.

Main Concerns

(1) The authors used a task in which rats must poke for a minimal amount of time (300 ms and then 1500 ms) to be able to obtain a drop of water delivered a few centimeters right below the nosepoke. They claim that their task is a time estimation task. However, they forget that they work with thirsty rats that are eager to get water sooner than later (there is a reason why they start by a short duration!). This task is mainly probing the animals ability to wait (that is impulse control) rather than time estimation per se. Second, the task does not require to estimate precisely time because there appear to be no penalties when the nosepokes are too short or when they exceed. So it will be unclear if the variation in nosepoke reflects motivational changes rather than time estimation changes. The fact that this behavioral task is a poor assay for time estimation and rather reflects impulse control is shown by the tendency of animals to perform nose-pokes that are too short, the very slow improvement in their performance (Figure 1, with most of the mice making short responses), and the huge variability. Not only do the behavioral data not support the claim of the authors in terms of what the animals are actually doing (estimating time), but this also completely annhilates the interpretation of the Ca++ imaging data, which can be explained by motivational factors (changes in neuronal activity occurring while the animals nose poke may reflect a growing sens of urgency to check if water is available). 

We would like to respond to the reviewer’s comments 1, 2 and 4 together, since they all focus on the same issue. We thank the reviewer for the very thoughtful comments and for sharing his detailed reasoning from a recently published review (Robbe, 2023). A lot of discussions go beyond the scope of this study, and we agree that whether there is an explicit representation of time (an internal clock) in the brain is a difficult question to be answer, particularly by using animal behaviors. In fact, even with fully conscious humans and elaborated task design, we think it is still questionable to clearly dissociate the neural substrate of “timing” from “motor”. In the end, it may as well be that as the reviewer cited from Bergson’sarticle, the experience of time cannot be measured.

Studying the neural representation of any internal state may suffer from the same ambiguity. With all due respect, however, we would like to limit our response to the scope of our results. According to the reviewer, two alternative interpretations of the task-related sequential activity exist: 1, duration cells may represent fidgeting or orofacial movements and 2, duration cells may represent motivation or motion plan of the rats. To test the first alternative interpretation, we have now performed a more comprehensive analysis of the behavior data at all the limbs and visible body parts of the experimental rats during nose poke and analyzed its periodicity among different trials. We found that the coding cells (including duration, start and end cells) activities were not modulated by these motions, arguing against this possibility. These data are now included in the new Supp. Figure 2, and we have added corresponding texts in the manuscript.

Regarding the second alternative interpretation, we think our data in the original Figure 4G argues against it. In this graph, we plotted the decoding error of time using the duration cells’ activity against the actual duration of the trials. If the sequential activity of durations cells only represents motivation, then the errors should be linearly modulated by trial durations. The unimodal distribution we observed (Figure 4G and see graph below for a re-plot without signs) suggests that the scaling factor of the sequential activity represents information related to time. And the fact that this unimodal distribution centered at the time threshold of the task provides strong evidence for the active use of scaling factor for time estimation.

In order to further test the relationship to motivation, we have measured the time interval between exiting nose poke to the start of licking water reward as an independent measurement of motivation for each trial. We found that this reward-seeking time was positively correlated with the trial durations, suggesting that the durations were correlated with motivation to some degree. And when we scaled the activities of the duration cells by this reward-seeking time, we found that the patterns of the sequential activities were largely diminished, and showed a significantly lower peak entropy compared to the same activities scaled by trial durations. The remaining sequential pattern may be due to the correlation between trial durations and motivation (Supp. Figure 2), and the sequential pattern reflects timing more prominently. These analyses provide further evidence that the sequential activities were not coding motivations. These data are included in Figure 2F, 2K and supp. Figure 3 in revised manuscript.

Author response image 1.

Regarding whether the scaling sequential activity we report represents behavioral timing or true time estimation, we did not have evidence on this point. However, a previous study has shown that PFC silencing led to disruption of the mouse’s timing behavior without affecting the execution of the task (PMID: 24367075), arguing against the behavior timing interpretation. The main surprising finding of our present study is that these duration cells are different from the start and end cells

in terms of their coding stability. Thus, future studies dissecting the anatomical microcircuit of these duration cells may provide further clues regarding whether they are connected with reward-related or motion-related brain regions. This may help partially resolve the “time” vs.

“motor” debate the reviewer mentioned.

(2) A second issue is that the authors seem to assume that rats are perfectly immobile and perform like some kind of robots that would initiate nose pokes, maintain them, and remove them in a very discretized manner. However, in this kind of task, rats are constantly moving from the reward magazine to the nose poke. They also move while nose-poking (either their body or their mouth), and when they come out of the nose poke, they immediately move toward the reward spout. Thus, there is a continuous stream of movements, including fidgeting, that will covary with timing. Numerous studies have shown that sensorimotor dynamics influence neural activity, even in the prefrontal cortex. Therefore, the authors cannot rule out that what the records reflect are movements (and the scaling of movement) rather than underlying processes of time estimation (some kind of timer). Concretely, start cells could represent the ending of the movement going from the water spout to the nosepoke, and end cells could be neurons that initiate (if one can really isolate any initiation, which I doubt) the movement from the nosepoke to the water spout. Duration cells could reflect fidgeting or orofacial movements combined with an increasing urgency to leave the nose pokes.

(3) The statistics should be rethought for both the behavioral and neuronal data. They should be conducted separately for all the rats, as there is likely interindividual variability in the impulsivity of the animals.

We thank the reviewer for the comment, yet we are not quite sure what specifically was asked by the reviewer. It appears that the reviewer requires we conduct our analysis using each rat individually. In our revised manuscript, we have conducted and reported analyses with individual rat in the original Figure 1C, Figure 2C, G, K, Figure 4F.

(4) The fact that neuronal activity reflects an integration of movement and motivational factors rather than some abstract timing appears to be well compatible with the analysis conducted on the error trials (Figure 4), considering that the sensorimotor and motivational dynamics will rescale with the durations of the nose poke. 

(5) The authors should mention upfront in the main text (result section) the temporal resolution allowed by their Ca+ probe and discuss whether it is fast enough in regard of behavioral dynamics occurring in the task. 

We thank the reviewer for the suggestion. We have originally mentioned the caveat of calcium imaging in the interpretation of our results. We have now incorporated more texts for this purpose during our revision. In terms of behavioral dynamics (start and end of nose poke in this case), we think calcium imaging could provide sufficient kinetics. However, the more refined dynamics related to the reproducibility of the sequential activity or the precise representation of individual cells on the scaled duration may be benefited from improved time resolution.

Recommendations for the authors:  

Reviewer #1 (Recommendations For The Authors): 

(1) Please refer explicitly to the three types of cells in the abstract. 

We have now modified the abstract as suggested during revision.

(2) Please refer to the work of Betancourt et al., 2023 Cell Reports, where a trial-by-trail analysis on the correlation between neural trajectory dynamics in MPC and timing behavior is reported. In that same paper the stability of neural sequences across task parameters is reported. 

We have now cited and discussed the study in the discussion section of the revised manuscript.

(3) Please state the number of studied animals at the beginning of the results section. 

We have now provided this information as requested. The numbers of rats are also plotted in Figure 1D for each analysis.

(4) Why do the middle and right panels of Figure 2E show duration cells. 

Figure 2E was intended to show examples of duration cells’ activity. We included different examples of cells that peak at different points in the scaled duration. We believe these multiple examples would give the readers a straight forward impression of these cells’ activity patterns.

(5) Which behavioral sessions of Figure 1B were analyzed further.

We have now labeled the analyzed sessions in Figure 1B with red color in the revised manuscript.

(6) In Figure 3A-C please increase the time before the beginning of the trial in order to visualize properly the activation patterns of the start cells.

We thank the reviewer for the suggestion and have now modified the figure accordingly in the revised manuscript.

(7) Please state what could be the behavioral and functional effect of the ablation of the cortical tissue on top of mPFC.

We thank the reviewer for the question. In our experience, mice with lens implanted in the mPFC did not show observable difference with mice without surgery in the acquisition of the task and the distribution of the nose-poke durations. In our dataset, rats with the lens implantation showed similar nose-poking behavior as those without lens implantation (Figure 1B). Thus, it seems that the effect of ablation, if any, was quite limited, in the scope of our task.

Author Response

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

We thank the reviewers and appreciate their recommendations to improve this work.

Reviewer 1:

Reviewer 1 recognizes that ‘This is an important finding that is relevant to the actions of VDR on colorectal cancer. The data presented to support the presented conclusion is convincing’.

Reviewer 1 identifies as a major weakness ‘that the site of SIRT1 regulatory lysine acetylation is defined by mutational analysis rather than by direct biochemical analysis.

However, as the reviewer mentions “previous reports of K610 acetylation using mass spec https://www.phosphosite.org/proteinAction.action?id=5946&showAllSites=true), and the absence of SIRT1 mutant K610R in the immunoprecipitates using anti-acetylated lysine antibodies presented in Fig. 4E clearly overcome this weakness”.

In addition, overall SIRT1 acetylation is reduced by vitamin D and by the specific SIRT1 activator SRT1720 as shown by decreased SIRT1 in the anti-acetyl-lysine immunoprecipates, (Fig. 4A and B). The second weakness identified by Reviewer 1 concerns “the use of only one shRNA to deplete VDR in CRC cells.”

We have made efforts to demonstrate that the results are specific, though we do not have results with alternative shRNAs for a variety of reasons. To mitigate this issue, we have compared two colon cancer cells originating from the same patient which differ in the presence/absence of VDR. SW480, derive from the primary tumor and express VDR, whereas SW620 cells were derived from a lung metastasis and lack VDR. Similar, to the comparison of HCT116 with shVDR HCT116 cells presented in this study, VD induced SIRT1 levels in SW480 in contrast to a lack of induction in SW620, as shown in Author response image 1. This result provides support for the specificity of the shVDR.

Author response image 1.

Vitamin D requires the presence of VDR to increase SIRT1 protein levels. SW480 and SW620 cell lines derive from the same patient, from primary tumor and lung metastasis respectively and differ in their VDR content. 1α,25-dihydroxyvitamin D3 (1,25(OH)2D3) was added at 100 nM for 24 h. Representative western-blot, where TBP was used as a loading control, of four biological replicates. Statistical analysis by ANOVA and values represent mean ± SEM; *p<0.05; *** p<0.001.

The referee noticed the inclusion of an siRNA for SIRT1 in Table 1. We apologize for that, since this is an error, and no results are presented in this study with SIRT1 depletion. Table 1 has been modified accordingly.

Concerning the third and fourth weaknesses that Reviewer 1 identifies, we agree that mapping the interacting domains in both VDR and SIRT1 and in vitro reconstitution would improve the present study. However, we believe that these would constitute long-term studies that themselves are not strictly necessary at this stage. Consequently, we favor the publication of the present body of work. In vitro reconstitution of the present work and the putative relevance of the proposed mechanism of vitamin D action via SIRT1 on types of cancer other than colon (eg breast etc), are certainly very interesting and warrant further investigation.

Reviewer 2:

This reviewer acknowledges that “…this study provides very interesting and solid information on the link between vitamin D and colorectal cancer. It is likely that this study will provide insight into the importance of vitamin D in other types of cancer. It may also lead to new therapeutic strategies for specific cases. This article is convincing, although the authors can improve their study as outlined…”

We acknowledge the proposed changes and recommendations, and have changed the text and Figures as suggested the by Reviewer as follows:

Figure 1

Figure 1E and F: the cell lines used were described in the figure legend, but we agree that including the name in the figure brings more clarity and these are now added.

Figure 1G: the statistical analysis was for all panels of Figure 1 as described in the Figure legend (lines 731-32), We have amended the original omission of panels 1G and 1H. In panel G, * represents statistical analysis by ANOVA (comparing the four groups) whereas # was the analysis by Students t test (comparing the two indicated groups), where * or #p<0.05. We hope to have clarified this point now.

Figure 2

Figure 2C: We showed originally the SIRT1/VDR interaction by immunoprecipitation of VDR and detection of SIRT1 in immunoprecipitates. We also showed immunoprecipitation of exogenously expressed Myc-SIRT1 (WT or mutants) and detection of VDR in immunoprecipitates (Figure 4F). The reviewer requests that we perform the inverse IP for endogenous SIRT1, that is immunoprecipitate SIRT1 and detect VDR in the immunoprecipates, which we now supply for the reviewer in Author response image 2.

Author response image 2

Immunoprecipitation of endogenous SIRT1 to show interaction with VDR. 1α,25-dihydroxyvitamin D3 (1,25(OH)2D3) was added at 100 nM for 24 h. Representative western-blots, where TBP was used as a loading control.

Figure 3

• Figure 3D: ‘The authors should indicate the color of the different stainings’. Immunostainings have been revealed with DAB (diaminebenzidine); thus, positiveness is highlighted by light or dark brown according to their low or high protein expression. Counterstaining has been performed with hematoxilin, which stains nuclei in dark blue and cytoplasm in light blue.

Do the authors mean that the secondary antibody marks in brown/red? If so, these results are inconsistent with the text considering that hematoxylin was used for non-tumor tissue. This part needs to be clarified.

We thank the Reviewer for asking us to clarify this issue. Neither the primary nor anti-Ig horseradish peroxidase-conjugated secondary antibodies presented positiveness resulting from these antibodies individually. Therefore, secondary antibody does not mark in any color. Hematoxylin has been used as counterstaining for both non-tumor as well as for tumor tissues.

What about the level of FOXO3A in these tissues/tumors?

We did not prove the tumor sections for specific SIRT1 substrates such as FoxO3A since their levels may not entirely depend on SIRT1 specific deacetylation.

What is the level of 1,25(OH)2D3 in these patients?

We agree with this referee that this information would be very useful, but unfortunately, we do not have data on vitamin D levels for these patients since they were not specifically recruited for this study and vitamin D levels are not routinely measured.

Figure 3D, the following information is missing: "A detailed amplification is shown in the lower left of each micrograph."

We decided not to include the amplification in micrographs because the aim of the manuscript is focused on protein levels, not localization and including the amplification was more confusing than enlightening. This has been amended now in the text.

Figure 3E, it says p=0.325, in the legend p<0.01, and in the text there is a trend. Which is the correct version?

We really apologize for this misunderstanding. As stated in the Figure, p=0.325 and therefore it does not reach statistical significance. We have amended the main text and figure legend to report that differences between SIRT1 expression levels of healthy and cancer human colon samples are not statistically significant.

Figure 4

Figure 4F. The quality of the presented blots is not optimal. It needs to be improved. In addition, the number of independent biological experiments is not indicated.

We have substituted the representative western-blot and included statistical analysis of four independent biological replicates. Since 4F is now a bigger panel, it has required a slight reorganization of the whole Figure, but the rest of panels remain with the originals. Now we indicate in the figure legend that at least three independent biological replicas were analyzed. In addition, we supply below the four experiments for the reviewer in Author response image 3.

Author response image 3

Immunoprecipitation of exogenous myc-tagged SIRT1 to show interaction with VDR of wild type (WT) or mutants. 1α,25-dihydroxyvitamin D3 (1,25(OH)2D3) was added at 100 nM for 24 h. FT: Flow Through. TBP as a loading control.

Regarding the last general comment concerning the number of independent experiments performed, this is indicated in the Figure legends (lines 732-36, 757-58, 82324, 840-41). All the in vitro experiments were performed at least as three independent experiments and not by repeating a western blot. A representative western blot is shown, and the statistical analysis corresponds to the analysis of the three biological replicates. For experiments with patient samples, the number of patients appears clearly indicated in the corresponding panel.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors attempt to validate Fisher Kernels on the top of HMM as a way to better describe human brain dynamics at resting state. The objective criterion was the better prediction of the proposed pipeline of the individual traits.

Strengths:

The authors analyzed rs-fMRI dataset from the HCP providing results also from other kernels.

The authors also provided findings from simulation data.

Weaknesses:

(1) The authors should explain in detail how they applied cross-validation across the dataset for both optimization of parameters, and also for cross-validation of the models to predict individual traits.

Indeed, there were details about the cross-validation for hyperparameter tuning and prediction missing. This problem was also raised by Reviewer #2. We have now rephrased this section in 4.4 and added details: ll. 804-813:

“We used k-fold nested cross-validation (CV) to select and evaluate the models. We used 10 folds for both the outer loop (used to train and test the model) and the inner loop (used to select the optimal hyperparameters) such that 90% were used for training and 10% for testing. The optimal hyperparameters λ (and τ in the case of the Gaussian kernels) were selected using grid-search from the vectors λ=[0.0001,0.001,0.01,0.1,0.3,0.5,0.7,0.9,1] and . In both the outer and the inner loop, we accounted for family structure in the HCP dataset so that subjects from the same family were never split across folds (Winkler et al., 2015). Within the CV, we regressed out sex and head motion confounds, i.e., we estimated the regression coefficients for the confounds on the training set and applied them to the test set (Snoek et al., 2019).“ and ll. 818-820: “We generated the 100 random repetitions of the 10 outer CV folds once, and then used them for training and prediction of all methods, so that all methods were fit to the same partitions.”

(2) They discussed throughout the paper that their proposed (HMM+Fisher) kernel approach outperformed dynamic functional connectivity (dFC). However, they compared the proposed methodology with just static FC.

We would like to clarify that the HMM is itself a method for estimating dynamic (or time-varying) FC, just like the sliding window approach, see also Vidaurre, 2024 (https://direct.mit.edu/imag/article/doi/10.1162/imag_a_00363/124983) for an overview of terminology.

See also our response to Q3.

(3) If the authors wanted to claim that their methodology is better than dFC, then they have to demonstrate results based on dFC with the trivial sliding window approach.

We would like to be clear that we do not claim in the manuscript that our method outperforms other dynamic functional connectivity (dFC) approaches, such as sliding window FC. We have now made changes to the manuscript to make this clearer.

First, we have clarified our use of the term “brain dynamics” to signify “time-varying amplitude and functional connectivity patterns” in this context, as Reviewer #2 raised the point that the former term is ambiguous (ll.33-35: “One way of describing brain dynamics are state-space models, which allow capturing recurring patterns of activity and functional connectivity (FC) across the whole brain.”).

Second, our focus is on our method being a way of using dFC for predictive modelling, since there currently is no widely accepted way of doing this. One reason why dFC is not usually considered in prediction studies is that it is mathematically not trivial how to use the parameters from estimators of dynamic FC for a prediction. This includes the sliding window approach. We do not aim at comparing across different dFC estimators in this paper. To make these points clearer, we have revised the introduction to now say:

Ll. 39-50:

“One reason why brain dynamics are not usually considered in this context pertains to their representation: They are represented using models of varying complexity that are estimated from modalities such as functional MRI or MEG. Although there exists a variety of methods for estimating time-varying or dynamic FC (Lurie et al., 2019), like the commonly used sliding-window approach, there is currently no widely accepted way of using them for prediction problems. This is because these models are usually parametrised by a high number of parameters with complex mathematical relationships between the parameters that reflect the model assumptions. How to leverage these parameters for prediction is currently an open question.

We here propose the Fisher kernel for predicting individual traits from brain dynamics, using information from generative models that do not assume any knowledge of task timings. We focus on models of brain dynamics that capture within-session changes in functional connectivity and amplitude from fMRI scans, in this case acquired during wakeful rest, and how the parameters from these models can be used to predict behavioural variables or traits. In particular, we use the Hidden Markov Model (HMM), which is a probabilistic generative model of time-varying amplitude and functional connectivity (FC) dynamics (Vidaurre et al., 2017).”

Reviewer #2 (Public Review):

Summary:

The manuscript presents a valuable investigation into the use of Fisher Kernels for extracting representations from temporal models of brain activity, with the aim of improving regression and classification applications. The authors provide solid evidence through extensive benchmarks and simulations that demonstrate the potential of Fisher Kernels to enhance the accuracy and robustness of regression and classification performance in the context of functional magnetic resonance imaging (fMRI) data. This is an important achievement for the neuroimaging community interested in predictive modeling from brain dynamics and, in particular, state-space models.

Strengths:

(1) The study's main contribution is the innovative application of Fisher Kernels to temporal brain activity models, which represents a valuable advancement in the field of human cognitive neuroimaging.

(2) The evidence presented is solid, supported by extensive benchmarks that showcase the method's effectiveness in various scenarios.

(3) Model inspection and simulations provide important insights into the nature of the signal picked up by the method, highlighting the importance of state rather than transition probabilities.

(4) The documentation and description of the methods are solid including sufficient mathematical details and availability of source code, ensuring that the study can be replicated and extended by other researchers.

Weaknesses:

(1) The generalizability of the findings is currently limited to the young and healthy population represented in the Human Connectome Project (HCP) dataset. The potential of the method for other populations and modalities remains to be investigated.

As suggested by the reviewer, we have added a limitations paragraph and included a statement about the dataset: Ll. 477-481: “The fMRI dataset we used (HCP 1200 Young Adult) is a large sample taken from a healthy, young population, and it remains to be shown how our findings generalise to other datasets, e.g. other modalities such as EEG/MEG, clinical data, older populations, different data quality, or smaller sample sizes both in terms of the number of participants and the scanning duration”.

We would like to emphasise that this is a methodological contribution, rather than a basic science investigation about cognition and brain-behaviour associations. Therefore, the method would be equally usable on different populations, even if the results vary.

(2) The possibility of positivity bias in the HMM, due to the use of a population model before cross-validation, needs to be addressed to confirm the robustness of the results.

As pointed out by both Reviewers #2 and #3, we did not separate subjects into training and test set before fitting the HMM. To address this issue, we have now repeated the predictions for HMMs fit only to the training subjects. We show that this has no effect on the results. Since this question has consequences for the Fisher kernel, we have also added simulations showing how the different kernels react to increasing heterogeneity between training and test set. These new results are added as results section 2.4 (ll. 376-423).

(3) The statistical significance testing might be compromised by incorrect assumptions about the independence between cross-validation distributions, which warrants further examination or clearer documentation.

We have now replaced the significance testing with repeated k-fold cross-validated corrected tests. Note that this required re-running the models to be able to test differences in accuracies on the level of individual folds, resulting in different plots throughout the manuscript and different statistical results. This does not, however, change the main conclusions of our manuscript.

(4) The inclusion of the R^2 score, sensitive to scale, would provide a more comprehensive understanding of the method's performance, as the Pearson correlation coefficient alone is not standard in machine learning and may not be sufficient (even if it is common practice in applied machine learning studies in human neuroimaging).

We have now added the coefficient of determination to the results figures.

(5) The process for hyperparameter tuning is not clearly documented in the methods section, both for kernel methods and the elastic net.

As mentioned above in the response to Reviewer #1, we have now added details about hyperparameter tuning for the kernel methods and the non-kernelised static FC regression models (see also Reviewer #1 comment 1): Ll.804-813: “We used k-fold nested cross-validation (CV) to select and evaluate the models. We used 10 folds for both the outer loop (used to train and test the model) and the inner loop (used to select the optimal hyperparameters) such that 90% were used for training and 10% for testing. The optimal hyperparameters  (and  in the case of the Gaussian kernels) were selected using grid-search from the vectors λ=[0.0001,0.001,0.01,0.1,0.3,0.5,0.7,0.9,1] and . In both the outer and the inner loop, we accounted for family structure in the HCP dataset so that subjects from the same family were never split across folds (Winkler et al., 2015). Within the CV, we regressed out sex and head motion confounds, i.e., we estimated the regression coefficients for the confounds on the training set and applied them to the test set (Snoek et al., 2019).” and ll. 818-820: “We generated the 100 random repetitions of the 10 outer CV folds once, and then used them for training and prediction of all methods, so that all methods were fit to the same partitions.”, as well as ll.913-917: “All time-averaged FC models are fitted using the same (nested) cross-validation strategy as described above (10-fold CV using the outer loop for model evaluation and the inner loop for model selection using grid-search for hyperparameter tuning, accounting for family structure in the dataset, and repeated 100 times with randomised folds).”

(6) For the time-averaged benchmarks, a comparison with kernel methods using metrics defined on the Riemannian SPD manifold, such as employing the Frobenius norm of the logarithm map within a Gaussian kernel, would strengthen the analysis, cf. Jayasumana (https://arxiv.org/abs/1412.4172) Table 1, log-euclidean metric.

We have now added the log-Euclidean Gaussian kernel proposed by the reviewer to the model comparisons. The additional model does not change our conclusions.

(7) A more nuanced and explicit discussion of the limitations, including the reliance on HCP data, lack of clinical focus, and the context of tasks for which performance is expected to be on the low end (e.g. cognitive scores), is crucial for framing the findings within the appropriate context.

We have now revised the discussion section and added an explicit limitations paragraph: Ll. 475-484:

“We here aimed to show the potential of the HMM-Fisher kernel approach to leverage information from patterns of brain dynamics to predict individual traits in an example fMRI dataset as well as simulated data. The fMRI dataset we used (HCP 1200 Young Adult) is a large sample taken from a healthy, young population, and it remains to be shown how the exhibited performance generalises to other datasets, e.g. other modalities such as EEG/MEG, clinical data, older populations, different data quality, or smaller sample sizes both in terms of the number of participants and the scanning duration. Additionally, we only tested our approach for the prediction of a specific set of demographic items and cognitive scores; it may be interesting to test the framework in also on clinical variables, such as the presence of a disease or the response to pharmacological treatment.”

(8) While further benchmarks could enhance the study, the authors should provide a critical appraisal of the current findings and outline directions for future research, considering the scope and budget constraints of the work.

In addition to the new limitations paragraph (see previous comment), we have now rephrased our interpretation of the results and extended the outlook paragraph: Ll. 485-507:

“There is growing interest in combining different data types or modalities, such as structural, static, and dynamic measures, to predict phenotypes (Engemann et al., 2020; Schouten et al., 2016). While directly combining the features from each modality can be problematic, modality-specific kernels, such as the Fisher kernel for time-varying amplitude and/or FC, can be easily combined using approaches such as stacking (Breiman, 1996) or Multi Kernel Learning (MKL) (Gönen & Alpaydın, 2011). MKL can improve prediction accuracy of multimodal studies (Vaghari et al., 2022), and stacking has recently been shown to be a useful framework for combining static and time-varying FC predictions (Griffin et al., 2024). A detailed comparison of different multimodal prediction strategies including kernels for time-varying amplitude/FC may may be the focus of future work.

In a clinical context, while there are nowadays highly accurate biomarkers and prognostics for many diseases, others, such as psychiatric diseases, remain poorly understood, diagnosed, and treated. Here, improving the description of individual variability in brain measures may have potential benefits for a variety of clinical goals, e.g., to diagnose or predict individual patients’ outcomes, find biomarkers, or to deepen our understanding of changes in the brain related to treatment responses like drugs or non-pharmacological therapies (Marquand et al., 2016; Stephan et al., 2017; Wen et al., 2022; Wolfers et al., 2015). However, the focus so far has mostly been on static or structural information, leaving the potentially crucial information from brain dynamics untapped. Our proposed approach provides one avenue of addressing this by leveraging individual patterns of time-varying amplitude and FC, and it can be flexibly modified or extended to include, e.g., information about temporally recurring frequency patterns (Vidaurre et al., 2016).”

Reviewer #3 (Public Review):

Summary:

In this work, the authors use a Hidden Markov Model (HMM) to describe dynamic connectivity and amplitude patterns in fMRI data, and propose to integrate these features with the Fisher Kernel to improve the prediction of individual traits. The approach is tested using a large sample of healthy young adults from the Human Connectome Project. The HMM-Fisher Kernel approach was shown to achieve higher prediction accuracy with lower variance on many individual traits compared to alternate kernels and measures of static connectivity. As an additional finding, the authors demonstrate that parameters of the HMM state matrix may be more informative in predicting behavioral/cognitive variables in this data compared to state-transition probabilities.

Strengths:

- Overall, this work helps to address the timely challenge of how to leverage high-dimensional dynamic features to describe brain activity in individuals.

- The idea to use a Fisher Kernel seems novel and suitable in this context.

- Detailed comparisons are carried out across the set of individual traits, as well as across models with alternate kernels and features.

- The paper is well-written and clear, and the analysis is thorough.

Potential weaknesses:

- One conclusion of the paper is that the Fisher Kernel "predicts more accurately than other methods" (Section 2.1 heading). I was not certain this conclusion is fully justified by the data presented, as it appears that certain individual traits may be better predicted by other approaches (e.g., as shown in Figure 3) and I found it hard to tell if certain pairwise comparisons were performed -- was the linear Fisher Kernel significantly better than the linear Naive normalized kernel, for example?

We have revised the abstract and the discussion to state the results more appropriately. For instance, we changed the relevant section in the abstract to (ll. 24-26):

“We show here, in fMRI data, that the HMM-Fisher kernel approach is accurate and reliable. We compare the Fisher kernel to other prediction methods, both time-varying and time-averaged functional connectivity-based models.”,

and in the discussion, removing the sentence

“resulting in better generalisability and interpretability compared to other methods”,

and adding (given the revised statistical results) ll. 435-436:

“though most comparisons were not statistically significant given the narrow margin for improvements.”

In conjunction with the new statistical approach (see Reviewer #2, comment 3), we have now streamlined the comparisons. We explained which comparisons were performed in the methods ll.880-890:

“For the main results, we separately compare the linear Fisher kernel to the other linear kernels, and the Gaussian Fisher kernel to the other Gaussian kernels, as well as to each other. We also compare the linear Fisher kernel to all time-averaged methods. Finally, to test for the effect of tangent space projection for the time-averaged FC prediction, we also compare the Ridge regression model to the Ridge Regression in Riemannian space. To test for effects of removing sets of features, we use the approach described above to compare the kernels constructed from the full feature sets to their versions where features were removed or reduced. Finally, to test for effects of training the HMM either on all subjects or only on the subjects that were later used as training set, we compare each kernel to the corresponding kernel constructed from HMM parameters, where training and test set were kept separate.“

Model performance evaluation is done on the level of all predictions (i.e., across target variables, CV folds, and CV iterations) rather than for each of the target variables separately. That means different best-performing methods depending on the target variables are to be expected.

- While 10-fold cross-validation is used for behavioral prediction, it appears that data from the entire set of subjects is concatenated to produce the initial group-level HMM estimates (which are then customized to individuals). I wonder if this procedure could introduce some shared information between CV training and test sets. This may be a minor issue when comparing the HMM-based models to one another, but it may be more important when comparing with other models such as those based on time-averaged connectivity, which are calculated separately for train/test partitions (if I understood correctly).

The lack of separation between training and test set before fitting the HMM was also pointed out by Reviewer #2. We are addressing this issue in the new Results section 2.4 (see also our response to Reviewer #2, comment 2).

Recommendations for the authors:

The individual public reviews all indicate the merits of the study, however, they also highlight relatively consistent questions or issues that ought to be addressed. Most significantly, the authors ought to provide greater clarity surrounding the use of the cross-validation procedures they employ, and the use of a common atlas derived outside the cross-validation loop. Also, the authors should ensure that the statistical testing procedures they employ accommodate the dependencies induced between folds by the cross-validation procedure and give care to ensuring that the conclusions they make are fully supported by the data and statistical tests they present.

Reviewer #1 (Recommendations For The Authors):

Overall, the study is interesting but demands further improvements. Below, I summarize my comments:

(1) The authors should explain in detail how they applied cross-validation across the dataset for both optimization of parameters, and also for cross-validation of the models to predict individual traits.

How did you split the dataset for both parameters optimization, and for the CV of the prediction of behavioral traits?

A review and a summary of various CVs that have been applied on the same dataset should be applied.

We apologise for the oversight and have now added more details to the CV section of the methods, see our response to Reviewer #1 comment 1:

In ll. 804-813:

“We used k-fold nested cross-validation (CV) to select and evaluate the models. We used 10 folds for both the outer loop (used to train and test the model) and the inner loop (used to select the optimal hyperparameters) such that 90% were used for training and 10% for testing. The optimal hyperparameters  (and  in the case of the Gaussian kernels) were selected using grid-search from the vectors λ=[0.0001,0.001,0.01,0.1,0.3,0.5,0.7,0.9,1] and . In both the outer and the inner loop, we accounted for family structure in the HCP dataset so that subjects from the same family were never split across folds (Winkler et al., 2015). Within the CV, we regressed out sex and head motion confounds, i.e., we estimated the regression coefficients for the confounds on the training set and applied them to the test set (Snoek et al., 2019).“ and ll. 818-820: “We generated the 100 random repetitions of the 10 outer CV folds once, and then used them for training and prediction of all methods, so that all methods were fit to the same partitions.”

(2) The authors should explain in more detail how they applied ICA-based parcellation at the group-level.

A. Did you apply it across the whole group? If yes, then this is problematic since it rejects the CV approach. It should be applied within the folds.

B. How did you define the representative time-source per ROI?

A: How group ICA was applied was stated in the Methods section (4.1 HCP imaging and behavioural data), ll. 543-548:

“The parcellation was estimated from the data using multi-session spatial ICA on the temporally concatenated data from all subjects.”

We have now added a disclaimer about the divide between training and test set:

“Note that this means that there is no strict divide between the subjects used for training and the subjects for testing the later predictive models, so that there is potential for leakage of information between training and test set. However, since this step does not concern the target variable, but only the preprocessing of the predictors, the effect can be expected to be minimal (Rosenblatt et al., 2024).”

We understand that in order to make sure we avoid data leakage, it would be desirable to estimate and apply group ICA separately for the folds, but the computational load of this would be well beyond the constraints of this particular work, where we have instead used the parcellation provided by the HCP consortium.

B: This was also stated in 4.1, ll. 554-559: “Timecourses were extracted using dual regression (Beckmann et al., 2009), where group-level components are regressed onto each subject’s fMRI data to obtain subject-specific versions of the parcels and their timecourses. We normalised the timecourses of each subject to ensure that the model of brain dynamics and, crucially, the kernels were not driven by (averaged) amplitude and variance differences between subjects.”

(3) The authors discussed throughout the paper that their proposed (HMM+Fisher) kernel approach outperformed dynamic functional connectivity (dFC). However, they compared the proposed methodology with just static FC.

A. The authors didn't explain how static and dFC have been applied.

B. If the authors wanted to claim that their methodology is better than dFC, then they have to demonstrate results based on dFC with the trivial sliding window approach.

C. Moreover, the static FC networks have been constructed by concatenating time samples that belong to the same state across the time course of resting-state activity.

So, it's HMM-informed static FC analysis, which is problematic since it's derived from HMM applied over the brain dynamics.

I don't agree that connectivity is derived exclusively from the clustering of human brain dynamics!

D. A static approach of using the whole time course, and a dFC following the trivial sliding-window approach should be adopted and presented for comparison with (HMM+Fisher) kernel.

We do not intend to claim our manuscript that our method outperforms other methods for doing dynamic FC. Indeed, we would like to be clear that the HMM itself is a method for capturing dynamic FC. Please see our responses to public review comments 2 and 3 by reviewer #1, copied below, which is intended to clear up this misunderstanding:

We would like to clarify that the HMM is itself a method for estimating dynamic (or time-varying) FC, just like the sliding window approach, see also Vidaurre, 2024 (https://direct.mit.edu/imag/article/doi/10.1162/imag_a_00363/124983) for an overview of terminology.

We would like to be clear that we do not claim in the manuscript that our method outperforms other dynamic functional connectivity (dFC) approaches, such as sliding window FC. We have now made changes to the manuscript to make this clearer.

First, we have clarified our use of the term “brain dynamics” to signify “time-varying amplitude and functional connectivity patterns” in this context, as Reviewer #2 raised the point that the former term is ambiguous.

Second, our focus is on our method being a way of using dFC for predictive modelling, since there currently is no widely accepted way of doing this. One reason why dFC is not usually considered in prediction studies is that it is mathematically not trivial how to use the parameters from estimators of dynamic FC for a prediction. This includes the sliding window approach. We do not aim at comparing across different dFC estimators in this paper. To make these points clearer, we have revised the introduction to now say:

Ll. 39-50:

“One reason why brain dynamics are not usually considered in this context pertains to their representation: They are represented using models of varying complexity that are estimated from modalities such as functional MRI or MEG. Although there exists a variety of methods for estimating time-varying or dynamic FC (Lurie et al., 2019), like the commonly used sliding-window approach, there is currently no widely accepted way of using them for prediction problems. This is because these models are usually parametrised by a high number of parameters with complex mathematical relationships between the parameters that reflect the model assumptions. How to leverage these parameters for prediction is currently an open question.

We here propose the Fisher kernel for predicting individual traits from brain dynamics, using information from generative models that do not assume any knowledge of task timings. We focus on models of brain dynamics that capture within-session changes in functional connectivity and amplitude from fMRI scans, in this case acquired during wakeful rest, and how the parameters from these models can be used to predict behavioural variables or traits. In particular, we use the Hidden Markov Model (HMM), which is a probabilistic generative model of time-varying amplitude and functional connectivity (FC) dynamics (Vidaurre et al., 2017).”

To the additional points raised here:

A: How static and dynamic FC have been estimated is explicitly stated in the relevant Methods sections 4.2 (The Hidden Markov Model), which explains the details of using the HMM to estimate dynamic functional connectivity; and 4.5 (Regression models based on time-averaged FC features), which explains how static FC was computed.

B: We are not making this claim. We have now modified the Introduction to avoid further misunderstandings, as per ll. 33-36: “One way of describing brain dynamics are state-space models, which allow capturing recurring patterns of activity and functional connectivity (FC) across the whole brain.”

C: This is not how static FC networks were constructed; we apologise for the confusion. We also do not perform any kind of clustering. The only “HMM-informed static FC analysis” is the static FC KL divergence model to allow for a more direct comparison with the time-varying FC KL divergence model, but we have included several other static FC models (log-Euclidean, Ridge regression, Ridge regression Riem., Elastic Net, Elastic Net Riem., and Selected Edges), which do not use HMMs. This is explained in Methods section 4.5.

D: As explained above, we have included four (five in the revised manuscript) static approaches using the whole time course, and we do not claim that our method outperforms other dynamic FC models. We also disagree that using the sliding window approach for predictive modelling is trivial, as explained in the introduction of the manuscript and under public review comment 3.

(4) Did you correct for multiple comparisons across the various statistical tests?

All statistical comparisons have been corrected for multiple comparisons. Please find the relevant text in Methods section 4.4.1.

(5) Do we expect that behavioral traits are encapsulated in resting-state human brain dynamics, and on which brain areas mostly? Please, elaborate on this.

While this is certainly an interesting question, our paper is a methodological contribution about how to predict from models of brain dynamics, rather than a basic science study about the relation between resting-state brain dynamics and behaviour. The biological aspects and interpretation of the specific brain-behaviour associations are a secondary point and out of scope for this paper. Our approach uses whole-brain dynamics, which does not require selecting brain areas of interest.

Reviewer #2 (Recommendations For The Authors):

Beyond the general principles included in the public review, here are a few additional pointers to minor issues that I would wish to see addressed.

Introduction:

- The term "brain dynamics" encompasses a broad spectrum of phenomena, not limited to those captured by state-space models. It includes various measures such as time-averaged connectivity and mean EEG power within specific frequency bands. To ensure clarity and relevance for a diverse readership, it would be beneficial to adopt a more inclusive and balanced approach to the terminology used.

The reviewer rightly points out the ambiguity of the term “brain dynamics”, which we use in the interest of readability. The HMM is one of several possible descriptions of brain dynamics. We have now included a statement early in the introduction to narrow this down:

Ll. 32-35:

“… the patterns in which brain activity unfolds over time, i.e., brain dynamics. One way of describing brain dynamics are state-space models, which allow capturing recurring patterns of activity and functional connectivity (FC) across the whole brain.”

And ll. 503-507:

“Our proposed approach provides one avenue of addressing this by leveraging individual patterns of time-varying amplitude and FC, as one of many possible descriptions of brain dynamics, and it can be flexibly modified or extended to include, e.g., information about temporally recurring frequency patterns (Vidaurre et al., 2016).”

Figures:

- The font sizes across the figures, particularly in subpanels 2B and 2C, are quite small and may challenge readability. It is advisable to standardize the font sizes throughout all figures to enhance legibility.

We have slightly increased the overall font sizes, while we are generally following figure recommendations set out by Nature. The font sizes are the same throughout the figures.

- When presenting performance comparisons, a horizontal layout is often more intuitive for readers, as it aligns with the natural left-to-right reading direction. This is not just a personal preference; it is supported by visualization best practices as outlined in resources like the NVS Cheat Sheet (https://github.com/GraphicsPrinciples/CheatSheet/blob/master/NVSCheatSheet.pdf) and Kieran Healy's book (https://socviz.co/lookatdata.html).

We have changed all figures to use horizontal layout, hoping that this will ease visual comparison between the different models.

- In the kernel density estimation (KDE) and violin plot representations, it appears that the data displays may be truncated. It is crucial to indicate where the data distribution ends. Overplotting individual data points could provide additional clarity.

To avoid confusion about the data distribution in the violin plots, we have now overlaid scatter plots, as suggested by the reviewer. Overlaying the fold-level accuracies was not feasible (since this would result in ~1.5 million transparent points for a single figure), so we instead show the accuracies averaged over folds but separate for target variables and CV iterations. Only the newly added coefficient of determination plots had to be truncated, which we have noted in the figure legend.

- Figure 3 could inadvertently suggest that time-varying features correspond to panel A and time-averaged features to panel B. To avoid confusion, consider reorganizing the labels at the bottom into two rows for clearer attribution.

We have changed the layout of the time-varying and time-averaged labels in the new version of the plots to avoid this issue.

Discussion:

- The discussion on multimodal modeling might give the impression that it is more effective with multiple kernel learning (MKL) than with other methods. To present a more balanced view, it would be appropriate to rephrase this section. For instance, stacking, examples of which are cited in the same paragraph, has been successfully applied in practice. The text could be adjusted to reflect that Fisher Kernels via MKL adds to the array of viable options for multimodal modeling. As a side thought: additionally, a well-designed comparison between MKL and stacking methods, conducted by experts in each domain, could greatly benefit the field. In certain scenarios, it might even be demonstrated that the two approaches converge, such as when using linear kernels.

We would like to thank the reviewer for the suggestion about the discussion concerning multimodal modelling. We agree that there are other relevant methods that may lead to interesting future work and have now included stacking and refined the section: ll. 487-494:

“While directly combining the features from each modality can be problematic, modality-specific kernels, such as the Fisher kernel for time-varying amplitude and/or FC, can be easily combined using approaches such as stacking (Breiman, 1996) or Multi Kernel Learning (MKL) (Gönen & Alpaydın, 2011). MKL can improve prediction accuracy of multimodal studies (Vaghari et al., 2022), and stacking has recently been shown to be a useful framework for combining static and time-varying FC predictions (Griffin et al., 2024). A detailed comparison of different multimodal prediction strategies including kernels for time-varying amplitude/FC may be the focus of future work.”

- The potential clinical applications of brain dynamics extend beyond diagnosis and individual outcome prediction. They play a significant role in the context of biomarkers, including pharmacodynamics, prognostic assessments, responder analysis, and other uses. The current discussion might be misinterpreted as being specific to hidden Markov model (HMM) approaches. For diagnostic purposes, where clinical assessment or established biomarkers are already available, the need for new models may be less pressing. It would be advantageous to reframe the discussion to emphasize the potential for gaining deeper insights into changes in brain activity that could indicate therapeutic effects or improvements not captured by structural brain measures. However, this forward-looking perspective is not the focus of the current work. A nuanced revision of this section is recommended to better reflect the breadth of applications.

We appreciate the reviewer’s thoughtful suggestions regarding the discussion of potential clinical applications. We have included the suggestions and refined this section of the discussion: Ll. 495-507:

“In a clinical context, while there are nowadays highly accurate biomarkers and prognostics for many diseases, others, such as psychiatric diseases, remain poorly understood, diagnosed, and treated. Here, improving the description of individual variability in brain measures may have potential benefits for a variety of clinical goals, e.g., to diagnose or predict individual patients’ outcomes, find biomarkers, or to deepen our understanding of changes in the brain related to treatment responses like drugs or non-pharmacological therapies (Marquand et al., 2016; Stephan et al., 2017; Wen et al., 2022; Wolfers et al., 2015). However, the focus so far has mostly been on static or structural information, leaving the potentially crucial information from brain dynamics untapped. Our proposed approach provides one avenue of addressing this by leveraging individual patterns of time-varying amplitude and FC, and it can be flexibly modified or extended to include, e.g., information about temporally recurring frequency patterns (Vidaurre et al., 2016).”

Reviewer #3 (Recommendations For The Authors):

- I wondered if the authors could provide, within the Introduction, an intuitive description for how the Fisher Kernel "preserves the structure of the underlying model of brain dynamics" / "preserves the mathematical structure of the underlying HMM"? Providing more background may help to motivate this study to a general audience.

We agree that this would be helpful and have now added this to the introduction: Ll.61-67:

“Mathematically, the HMM parameters lie on a Riemannian manifold (the structure). This defines, for instance, the relation between parameters, such as: how changing one parameter, like the probabilities of transitioning from one state to another, would affect the fitting of other parameters, like the states’ FC. It also defines the relative importance of each parameter; for example, how a change of 0.1 in the transition probabilities would not be the same as a change of 0.1 in one edge of the states’ FC matrices.”

To communicate the intuition behind the concept, the idea was also illustrated in Figure 1, panel 4 by showing Euclidean distances as straight lines through a curved surface (4a, Naïve kernel), as opposed to the tangent space projection onto the curved manifold (4b, Fisher kernel).

- Some clarifications regarding Figure 2a would be helpful. Was the linear Fisher Kernel significantly better than the linear Naive normalized kernel? I couldn't find whether this comparison was carried out. Apologies if I have missed it in the text. For some of the brackets indicating pairwise tests and their significance values, the start/endpoints of the bracket fall between two violins; in this case, were the results of the linear and Gaussian Fisher Kernels pooled together for this comparison?

We have now streamlined the statistical comparisons and avoided plotting brackets falling between two violin plots. The comparisons that were carried out are stated in the methods section 4.4.1. Please see also our response to above to Reviewer #3 public review, potential weaknesses, point 1, relevant point copied below:

In conjunction with the new statistical approach (see Reviewer #2, comment 3), we have now streamlined the comparisons. We explained which comparisons were performed in the methods ll.880-890:

“For the main results, we separately compare the linear Fisher kernel to the other linear kernels, and the Gaussian Fisher kernel to the other Gaussian kernels, as well as to each other. We also compare the linear Fisher kernel to all time-averaged methods. Finally, to test for the effect of tangent space projection for the time-averaged FC prediction, we also compare the Ridge regression model to the Ridge Regression in Riemannian space. To test for effects of removing sets of features, we use the approach described above to compare the kernels constructed from the full feature sets to their versions where features were removed or reduced. Finally, to test for effects of training the HMM either on all subjects or only on the subjects that were later used as training set, we compare each kernel to the corresponding kernel constructed from HMM parameters, where training and test set were kept separate”.

- The authors may wish to include, in the Discussion, some remarks on the use of all subjects in fitting the group-level HMM and the implications for the cross-validation performance, and/or try some analysis to ensure that the effect is minor.

As suggested by reviewers #2 and #3, we have now performed the suggested analysis and show that fitting the group-level HMM to all subjects compared to only to the training subjects has no effect on the results. Please see our response to Reviewer #2, public review, comment 2.

- The decision to use k=6 states was made here, and I wondered if the authors may include some support for this choice (e.g., based on findings from prior studies)?

We have now refined and extended our explanation and rationale behind the number of states: Ll. 586-594: “The number of states can be understood as the level of detail or granularity with which we describe the spatiotemporal patterns in the data, akin to a dimensionality reduction, where a small number of states will lead to a very general, coarse description and a large number of states will lead to a very detailed, fine-grained description. Here, we chose a small number of states, K=6, to ensure that the group-level HMM states are general enough to be found in all subjects, since a larger number of states increases the chances of certain states being present only in a subset of subjects. The exact number of states is less relevant in this context, since the same HMM estimation is used for all kernels.”

- (minor) Abstract: "structural aspects" - do you mean structural connectivity?

With “structural aspects”, we refer to the various measures of brain structure that are used in predictive modelling. We have now specified: Ll. 14-15: “structural aspects, such as structural connectivity or cortical thickness”.

Author response:

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

Reviewer #1 (Public Review):

Summary:

This study demonstrates a key role of oxLDL in enhancing Ang II-induced Gq signaling by promoting the AT1/LOX1 receptor complex formation. Importantly, Gq-mediated calcium influx was only observed in LOX1 and AT1 both expressing cells, and AT1-LOX1 interaction aggravated renal damage and dysfunction under the condition of a high-fat diet with Ang II infusion, so this study indicated a new therapeutic potential of AT1-LOX1 receptor complex in CKD patients with dyslipidemia and hypertension.

Strengths:

This study is very exciting and the work is also very detailed, especially regarding the mechanism of LOX1-AT1 receptor interaction and its impact on oxidative stress, fibrosis, and inflammation.

Weaknesses:

The direct evidence for the interaction between AT1 and LOX1 receptors in cell membrane localization is relatively weak. Here I raise some questions that may further improve the study.

Major points:

(1) The authors hypothesized that in the interaction of AT1/LOX1 receptor complex in response to ox-LDL and AngII, there should be strong evidence of fluorescence detection of colocalization for these two membrane receptors, both in vivo and in vitro. Although the video evidence for AT1 internalization upon complex activation is shown in Figure S1, the more important evidence should be membrane interaction and enhanced signal of intracellular calcium influx.

Thank you for your valuable feedback. We agree that demonstrating the colocalization and interaction of AT1 and LOX-1 receptors at the membrane is critical to supporting our hypothesis.

In response, we have previously provided visual evidence of membrane co-localization of the AT1/LOX-1 receptor complex using an in situ PLA assay with anti-FLAG and antiV5 antibodies in CHO cells expressing FLAG-tagged AT1 and V5-tagged LOX-1 (Yamamoto et al., FASEB J 2015). This was further supported by immunoprecipitation of membrane proteins in CHO cells co-expressing LOX-1 and AT1, which confirmed the presence of the receptor complex. In the current study, we offer additional evidence of enhanced intracellular calcium influx following simultaneous stimulation with oxLDL and Ang II, confirming the functional activation of the AT1/LOX-1 receptor complex (Fig. 1g-j and Fig. 3e-h). Together, these findings provide substantial support for the colocalization of AT1 and LOX-1 and their influence on downstream signaling in our in vitro experiments.

However, we acknowledge the limitation of direct evidence for membrane co-localization of LOX-1 and AT1 in vivo. This constraint is attributed to the fact that both available anti-AT1 and anti-LOX-1 antibodies are derived from rabbits, making coimmunofluorescence or PLA challenging in our study. To address this, we employed coimmunofluorescent staining with megalin, a well-established marker for proximal renal tubules, as shown in Fig. S10. We found that both AT1 and LOX-1 co-localized with megalin, particularly at the brush borders, indicating their presence in the same renal compartments relevant to AT1/LOX-1 signaling.

We have revised the manuscript to highlight the functional evidence from calcium influx assays, supported by prior PLA results, demonstrating the interaction between LOX-1 and AT1. Additionally, we included a figure showing the co-localization of AT1 and LOX-1 with megalin in proximal renal tubules to reinforce these findings. Lastly, we have emphasized in the discussion the limitation regarding the lack of direct in vivo evidence for membrane co-localization of LOX-1 and AT1.

(2) Co-IP experiment should be provided to prove the AT1/LOX1 receptor interaction in response to ox-LDL and AngII in AT1 and LOX1 both expressing cells but not in AT1 only expressing cells.

We thank the reviewer for the insightful suggestion to validate the AT1/LOX1 receptor interaction under various stimulation conditions. In our previous study (Yamamoto et al., FASEB J 2015), we demonstrated the interaction between AT1 and LOX1 receptors through Co-IP and in situ PLA assays in cells overexpressing both receptors, without stimulation. These experiments provided solid evidence of the receptor interaction under static conditions at the cell membrane.

However, as noted in the previous work, we did not perform Co-IP experiments under AngII or oxLDL stimulation. The primary reason for this is that both AngII and oxLDL trigger internalization of the AT1 and/or LOX1 receptors, which may complicate the detection of receptor interaction at the membrane via Co-IP. This is supported by our realtime imaging, which showed a reduction in AT1 and/or LOX1 puncta following stimulation, indicating internalization of the receptors (Fig. 2a).

While we acknowledge the reviewer’s interest in investigating the interaction under AngII stimulation, we believe that the current data—especially from the PLA and Co-IP assays under static conditions—strongly support the interaction of AT1 and LOX1 receptors at the membrane.

(3) The authors mentioned that the Gq signaling-mediated calcium influx may change gene expression and cellular characteristics, including EMT and cell proliferation. They also provided evidence that oxidative stress, fibrosis, and inflammation were all enhanced after activating both receptors and inhibiting Gq was effective in reversing these changes. However, single stimulation with ox-LDL or AngII also has strong effects on ROS production, inflammation, and cell EMT, which has been extensively proved by previous studies. So, how to distinguish the biased effect of LOX1 or AT1r alone or the enhanced effect of receptor conformational changes mediated by their receptor interaction? Is there any better evidence to elucidate this point?

Thank you for raising this important point regarding the distinction between the individual effects of LOX-1 or AT1R activation and the enhanced effects mediated by their interaction. In our study, the concentration of oxLDL used (2–10 μg/ml) was significantly lower than concentrations typically employed in other studies (which often exceed 20 μg/ml). As a result, oxLDL alone produced minimal effects, aside from a reduction in cell proliferation observed in the BrdU assay. This suggests that oxLDL, at the concentrations used in our experiments, does not elicit a strong cellular response on its own.

The key to distinguishing the effect of the LOX-1/AT1 interaction lies in the amplification of Gq signaling, a pathway specifically activated by AngII. The distinction between the individual effects of LOX-1 or AT1R and the enhanced effects due to their interaction is centered on the increased activation of Gq signaling. In our experiments, co-treatment with oxLDL and AngII led to a significant increase in IP1 levels and calcium influx— both critical indicators of Gq signaling activation. While AngII alone also raised IP1 levels, the combined treatment with oxLDL further amplified the Gq signaling response, as reflected in the enhanced calcium influx. Importantly, oxLDL alone did not alter IP1 levels, even at high concentrations (100 μg/ml) (Takahashi et al., iScience 2021).

This enhancement of Gq signaling provides strong evidence of the synergistic interaction between LOX-1 and AT1, which surpasses the individual effects of either receptor alone. The LOX-1/AT1 interaction is thus crucial for the observed amplification of AngIIspecific signaling pathways. The combination of increased IP1 levels and calcium influx serves as compelling evidence of this interaction, clearly differentiating the effects of individual receptor activation from the enhanced response driven by receptor conformational changes and interaction.

Thank you again for your insightful comment, which has helped us to better articulate the significance of receptor interaction in this study.

(4) How does the interaction between AT1 and LOX1 affect the RAS system and blood pressure? What about the serum levels of rennin, angiotensin, and aldosterone in ND-fed or HFD-fed mice?

Thank you for your insightful question regarding the effects of AT1 and LOX-1 interaction on the renin-angiotensin system (RAS) and blood pressure, as well as the plasma levels of renin, angiotensin, and aldosterone in normal diet (ND)-fed and high-fat diet (HFD)-fed mice.

OxLDL binds to LOX-1, amplifying AT1 receptor activation and Gq signaling, which enhances the effects of Ang II. This interaction between AT1 and LOX-1 can lead to increased vasoconstriction, oxidative stress, and inflammation, which contribute to elevated blood pressure. This pathway may play a crucial role in modulating the RAS, particularly under conditions of elevated oxLDL, such as those induced by a HFD. Regarding the components of the RAS, we focused on plasma aldosterone levels, as this is a direct consequence of Ang II signaling. As shown in Fig. S7, when mice were treated with a pressor dose of Ang II infusion and subjected to a HFD to elevate oxLDL levels, we did not observe a significant increase in plasma aldosterone levels (102.8 ± 11.6pg/mL vs. 141.8 ± 15.0 pg/mL, P = 0.081).

In terms of blood pressure, Fig. 7b shows that no significant changes were observed under these treatment conditions, despite the AT1/LOX-1 interaction. These findings suggest that while oxLDL, via the AT1/LOX-1 interaction, can enhance Ang II signaling, its effect on blood pressure was not apparent in our study. This may be due to several factors, including heterogeneous cellular responses to the combined treatment across different cell types, as shown by the lack of reaction in vascular endothelial cells, vascular smooth muscle cells, and macrophages (Fig. S2). This may also be attributed to the high concentration of angiotensin II used in this study, which could have saturated aldosterone production under our experimental conditions. We have revised the manuscript to reflect these points. 

Thank you again for your thoughtful comment, which has allowed us to expand and refine the discussion on this important aspect of our study.

Reviewer #2 (Public Review):

(1)  Individuals with chronic kidney disease often have dyslipidemia, with the latter both a risk factor for atherosclerotic heart disease and a contributor to progressive kidney disease. Prior studies suggest that oxidized LDL (oxLDL) may cause renal injury through the activation of the LOX1 receptor. The authors had previously reported that LOX1 and AT1 interact to form a complex at the cell surface. In this study, the authors hypothesize that oxLDL, in the setting of angiotensin II, is responsible for driving renal injury by inducing a more pronounced conformational change of the AT1 receptor which results in enhanced Gq signaling.

They go about testing the hypothesis in a set of three studies. In the first set, they engineered CHO cell lines to express AT1R alone, LOX1 in combination with AT1R, or LOX1 with an inactive form of AT1R and indirectly evaluated Gq activity using IP1 and calcium activity as read-outs. They assessed activity after treatment with AngII, oxLDL, or both in combination and found that treatment with both agents resulted in the greatest level of activity, which could be effectively blocked by a Gq inhibitor but not a Gi inhibitor nor a downstream Rho kinase inhibitor targeting G12/13 signaling. These results support their hypothesis, though variability in the level of activation was dramatically inconsistent from experiment to experiment, differing by as much as 20-fold. In contrast, within the experiment, differences between the AngII and AngII/oxLDL treatments, while nominally significant and consistent with their hypothesis, generally were only 10-20%. Another example of unexplained variability can be found in Figures 1g-1j. AngII, at a concentration of 10-12, has no effect on calcium flux in one set of studies (Figure 1g, h) yet has induced calcium activity to a level as great as AngII + oxLDL in another (Figure 1i). The inconsistency of results lessens confidence in the significance of these findings. In other studies with the LOX1-CHO line, they tested for conformational change by transducing AT1 biosensors previously shown to respond to AngII and found that one of them in fact showed enhanced BRET in the setting of oxLDL and AngII compared to AngII alone, which was blocked by an antibody to AT1R. The result is supportive of their conclusions. Limiting enthusiasm for these results is the fact that there isn't a good explanation as to why only 1 sensor showed a difference, and the study should have included a non-specific antibody to control for non-specific effects.

We sincerely appreciate the reviewer’s thorough and insightful feedback, especially regarding the variability observed in our experimental results. As the reviewer pointed out, the differences in activation levels between the calcium influx assay and the IP1 assay, particularly between AngII and AngII/oxLDL co-treatment, were indeed significant. These differences can be attributed to the inherent sensitivity of these assays, which are used to indirectly evaluate Gq activity. Despite the variability, we believe that the reliability of our results is supported by the consistent directional trends across both assays, which align with our hypothesis.

Regarding the inconsistencies in intracellular calcium dynamics observed in Fig. 1i, we have performed additional analysis of calcium kinetics during ligand stimulation, similar to the analysis in Fig. 1g. As shown in Author response image 1, the background signal in the experiment related to Fig. 1i was relatively higher than in Fig. 1g and 1h. This elevated background, which may have been influenced by variations between cells and experimental days, resulted in a higher percent change from baseline in samples treated with AngII alone. However, the combined effect of AngII with oxLDL was still apparent. This clarification further supports the consistency of our findings.

Author response image 1.

In reference to the BRET sensor experiments, we acknowledge the reviewer’s concern regarding the variability in sensor responses. As outlined in Devost et al. (J Biol Chem. 2017), the sensitivity of AT1 intramolecular FlAsH-BRET biosensors in detecting conformational changes induced by AngII is highly dependent on the insertion site of the FlAsH sequence. In our experiments, co-treatment with oxLDL and AngII enhanced AT1 conformational changes, but this effect was only detectable with the CHO-LOX-1-AT1-3p3 sensor (with FlAsH inserted in the third intracellular loop), and not with the CHO-LOX-1-AT1-C-tail P1 sensor (with FlAsH inserted at the C-terminal tail). This differential sensitivity likely explains why only one sensor showed a significant response, highlighting the critical role of FlAsH insertion site selection in these assays. We hope these clarifications address the reviewer’s concerns and improve confidence in the significance of our findings.

(2) The authors then repeated similar studies using publicly available rat kidney epithelial and fibroblast cell lines that have an endogenous expression of AT1R and LOX1. In these studies, oxLDL in combination with AngiI also enhanced Gq signaling, while knocking down either AT1R or LOX1, and treatment with inhibitors of Gq and AT1R blocked the effects. Like the prior set of studies, however, the effects are very modest and there was significant inter-experimental variability, reducing confidence in the significance of the findings. The authors then tested for evidence that the enhanced Gq signaling could result in renal injury by comparing qPCR results for target genes. While the results show some changes, their significance is difficult to assess. A more global assessment of gene expression patterns would have been more appropriate. In parallel with the transcriptional studies, they tested for evidence of epithelial-mesenchymal transition (EMT) using a single protein marker (alpha-smooth muscle actin) and found that its expression increased significantly in cells treated with oxLDL and AngII, which was blocked by inhibition of Gq inhibition and AT1R. While the data are sound, their significance is also unclear since EMT is a highly controversial cell culture phenomenon. Compelling in vivo studies have shown that most if not all fibroblasts in the kidney are derived from interstitial cells and not a product of EMT. In the last set of studies using these cell lines, the authors examined the effects of AngII and oxLDL on cell proliferation as assayed using BrdU. These results are puzzling---while the two agents together enhanced proliferation which was effectively blocked by an inhibitor to either AT1R or Gq, silencing of LOX1 had no effect.

Thank you for your thorough review and comments. We acknowledge your concerns regarding the modest effects observed and the variability in experimental outcomes. We would like to address your points systematically.

(1) Gq signaling and experimental variability:

Regarding the question of Gq signaling in Fig. 3, as previously mentioned, the observed differences in the IP1 assay are likely due to the sensitivity of the assay and the technical issues associated with detecting calcium influx and IP1 levels. While the overall differences between treatments may appear modest, the most critical comparison— between AngII alone and AngII combined with oxLDL—consistently showed significant differences, which aligns with the calcium influx results shown in Fig. 1. Notably, we found that the EC50 for IP1 production decreased by 80% in response to co-treatment with oxLDL and AngII, compared to AngII treatment alone. These findings demonstrate the robustness of Gq signaling enhancement with co-treatment, even if the absolute differences in the IP1 assay appear small.

(2) Gene expression in Fig. 4:

Regarding the gene expression analysis in Fig. 4, we used relatively low concentrations of oxLDL (5 μg/ml) compared to the higher concentrations typically employed in other studies (mostly exceeding 20 μg/ml). This may explain the lack of robust responses in some conditions. However, in combination with AngII, the co-treatment significantly upregulated several genes, particularly pro-inflammatory markers such as IL-6, TNFα, IL1β, and MCP-1 in NRK49F cells. These results suggest that the co-treatment induces a complex response, potentially activating multiple downstream signaling pathways beyond just Gq signaling, which may obscure more straightforward effects.

While we agree that a more global assessment of gene expression would provide further insights, due to cost constraints, we focused on key representative genes that are highly relevant to inflammation and fibrosis in this study.

(3) EMT in renal fibrosis:

We appreciate the reviewer’s insightful comments regarding the role of EMT in renal fibrosis. Regarding full EMT, in which epithelial cells completely transition into mesenchymal cells, previous studies using the unilateral ureteral obstruction (UUO) model suggest that full EMT may not play a significant role (J Clin Invest. 2011 Feb;121(2):468-74). The role of full EMT remains controversial in the context of renal fibrosis, with most kidney fibroblasts thought to originate from interstitial cells rather than through full EMT.

Recent studies, however, suggest that partial epithelial-mesenchymal transition (pEMT) could be involved in CKD, especially in association with inflammation, oxidative stress, and elevated TGF-β levels—conditions also present in our model involving Ang II infusion combined with an HFD. pEMT refers to a state in which epithelial cells acquire mesenchymal traits, such as increased α-SMA expression and secretion of pro-fibrotic cytokines, while remaining attached to the basement membrane without fully transitioning into fibroblasts (Front Physiol. 2020 Sep 15;11:569322). This phenomenon has been observed in kidney fibrosis models, including UUO, which shares inflammatory and oxidative stress conditions with our Ang II and HFD treatment model. The observed increase in α-SMA in our model may thus indicate a pEMT-like state, indirectly contributing to fibrosis through the secretion of growth factors and cytokines.

We are mindful of the importance of not overstating EMT's role. Accordingly, we interpret increased α-SMA expression as a potential marker of the pEMT process rather than definitive evidence of its presence or direct role in fibroblast formation. Furthermore, we acknowledge limitations in providing direct in vivo evidence for pEMT and recognize that further mechanistic studies are needed to elucidate its specific role in renal fibrosis, despite inherent challenges.

In response to the reviewer’s concern, we have revised the manuscript to clarify that our data support the possibility of pEMT contributing to fibrosis in this model, without overstating its impact. We also acknowledge the challenges in translating in vitro pEMT findings to in vivo models, where detecting the subtle effects of pEMT is inherently challenging.

(4) BrdU assay and fibroblast proliferation (Fig. 6b):

In Fig. 6b, the BrdU assay shows that fibroblast proliferation was significantly enhanced by the co-treatment with AngII and oxLDL, and this effect was abolished by LOX-1 knockdown, similar to the results observed with AT1 knockdown. These findings strongly suggest a combinatorial effect of AT1/LOX-1 interaction in promoting fibroblast proliferation, supporting the idea that the co-treatment operates through a coordinated mechanism involving both receptors. Notably, LOX-1 silencing did not affect the proliferation induced by AngII alone, as this response is independent of LOX-1.

We will incorporate these points into the Discussion section of the manuscript, specifically regarding the differences in sensitivity between the Ca influx and IP1 assays, as well as the emerging role of partial EMT in renal fibrosis. This will provide a clearer context for the interpretation of our findings and further strengthen the discussion on the significance of these phenomena.

Thank you again for your valuable feedback, which has helped us improve the clarity and depth of our manuscript.

(3) The final set of studies looked to test the hypothesis in mice by treating WT and Lox1KO mice with different doses of AngII and either a normal or high-fat diet (to induce oxLDL formation). The authors found that the combination of high dose AngII and a highfat diet (HFD) increased markers of renal injury (urinary 8-ohdg and urine albumin) in normal mice compared to mice treated with just AngII or HFD alone, which was blunted in Lox1-KO mice). These results are consistent with their hypothesis. However, there are other aspects of these studies that are either inconsistent or complicating factors that limit the strength of the conclusions. For example, Lox1- KO had no effect on renal injury marker expression in mice treated with low-dose AngII and HFD. It also should be noted that Lox1-KO mice had a lower BP response to AngII, which could have reduced renal injury independent of any effects mediated by the AT1R/LOX1 interaction. Another confounding factor was the significant effect the HFD diet had on body weight. While the groups did not differ based on AngII treatment status, the HFD consistently was associated with lower total body weight, which is unexplained. Next, the authors sought to find more direct evidence of renal injury using qPCR of candidate genes and renal histology. The transcriptional results are difficult to interpret; moreover, there were no significant histologic differences between groups. They conclude the study by showing the pattern of expression of LOX1 and AT1R in the kidney by immunofluorescence and conclude that the proteins overlap in renal tubules and are absent from the glomerulus. Unfortunately, they did not co-stain with any other markers to identify the specific cell types. However, these results are inconsistent with other studies that show AT1R is highly expressed in mesangial cells, renal interstitial cells, near the vascular pole, JG cells, and proximal tubules but generally absent from most other renal tubule segments.

Thank you for your valuable comments and for raising these important points. We appreciate the opportunity to clarify several aspects of our study and address the limitations and inconsistencies you have pointed out.

(1) Renal injury markers (urinary albumin and 8-OHdG) and the effect of LOX-1 loss of- function:

Our results showed that the combination of high-dose AngII and HFD led to a significant increase in renal injury markers, such as urinary albumin and 8-OHdG, in WT mice. In LOX-1 KO mice, this increase was significantly blunted, supporting a protective role of LOX-1 loss-of-function. However, as you noted, at low-dose AngII, there was no significant difference in urinary 8-OHdG between ND-fed and HFD-fed mice. Despite this, we observed a significant increase in urinary albumin in HFD-fed WT mice compared to ND-fed mice under low-dose AngII, and this difference was abolished in LOX-1 KO mice. Moreover, gene expression analysis showed that oxidative stress markers such as p67phox and p91phox (Fig. 8b), as well as p40phox, p47phox (Fig. S8), and inflammatory markers like IL1β (Fig. 8b), were significantly elevated in HFD-fed WT mice even with low-dose AngII, while these increases were absent in LOX-1 KO mice. These results suggest that the LOX-1/AT1 interaction contributes to renal injury under both low- and high-dose AngII conditions.

We acknowledge that the treatment duration may have influenced our results, as urine and renal tissue samples were only examined at a single time point (1.5 months after treatment initiation). The impact of AT1/LOX-1 interaction may evolve over time, and different treatment durations might yield varying outcomes. This is a limitation of our study, which we have addressed in the revised manuscript.

(2) Blood pressure and its effect on renal injury:

As shown in Fig. 7b and Fig S6f, LOX-1 KO mice exhibited a lower blood pressure response to high-dose AngII compared to WT mice, which could indeed have contributed to the reduced renal injury in the LOX-1 KO group, independent of the AT1/LOX-1 interaction. However, it is important to note that the differences in renal injury markers between AngII alone and AngII + HFD were largely abolished in LOX-1 KO mice, suggesting the in vivo relevance of the LOX-1/AT1 interaction observed in vitro. Additionally, as shown in Fig. 7d (urinary albumin), Fig. 8b (p67phox, p91phox), and Fig. S8b (p40phox, p47phox), even under subpressor doses of AngII, where no significant blood pressure differences were observed, HFD-fed WT mice exhibited exacerbated renal injury compared to ND-fed mice. These effects were ameliorated in LOX-1 KO mice, indicating that the protective effects in LOX-1 KO mice are at least partly independent of blood pressure changes and that the AT1/LOX-1 interaction plays a significant role in modulating renal injury under co-treatment with AngII and HFD.

(3) HFD and body weight changes:

We agree with your observation regarding the effect of HFD on body weight, which was consistently lower in HFD-fed groups, despite no differences in AngII treatment status. This is an atypical presentation compared to previous studies mostly showing increased body weight by feeding of HFD. The HFD used in this study was intended to elevate oxLDL levels, as previously reported (Atherosclerosis 200:303–309 (2008)). As shown in Fig. S6d and S6e, this can be attributed to reduced food intake in HFD-fed mice. Although modest, this weight reduction may influence renal function. This point is added in the limitation.

(4) Histological findings and qPCR results:

As discussed in the manuscript, despite significant changes in urinary markers and gene expression, we did not observe histological evidence of fibrosis or mesangial expansion, even under co-treatment with AngII and HFD. This may be due to the relatively short treatment period of 4 weeks, and a longer duration might be necessary to detect such changes. Additionally, we acknowledge that we did not detect increased Gq signaling in kidney tissue, which is another limitation of the study. Nevertheless, the gene expression data on oxidative stress, fibrosis, inflammation, and renal injury markers (e.g., p67phox, IL1β) are consistent with our hypothesis that the AT1/LOX-1 interaction exacerbates renal injury under AngII and HFD conditions.

(5) Immunostaining for AT1 and LOX-1:

Due to the use of rabbit-derived antibodies for both AT1 and LOX-1, it was technically not feasible to perform co-immunostaining for both receptors simultaneously. Instead, we performed co-immunofluorescent staining using megalin, a well-established marker of proximal renal tubules, to help localize these receptors. As shown in Fig. S10, both AT1 and LOX-1 were co-localized with megalin, particularly at the brush borders of proximal tubules. This pattern suggests the presence of these receptors in renal compartments relevant to AT1/LOX-1 signaling. While we did not perform additional co-staining with other markers to identify specific cell types, the strong localization with megalin provides robust evidence of their expression in proximal renal tubules, which is consistent with the literature on AT1R in this nephron segment. We acknowledge that previous studies have identified AT1R expression in mesangial cells, renal interstitial cells, the vascular pole, juxtaglomerular (JG) cells, and proximal tubules. In our immunofluorescence experiments, we did not detect significant AT1R expression in the glomerulus or mesangium. This finding aligns with other reports showing strong expression of AT1R in proximal tubules (Am J Physiol Renal Physiol. 2021 Apr 1;320(4)), although it does not exclude the possibility of AT1 expression in other compartments, given the sensitivity limitations of the immunofluorescence. Our focus on proximal tubules allowed us to observe clear AT1/LOX-1 co-localization in this region, particularly in the context of oxLDL and AngII signaling. Given that the AT1/LOX-1 interaction is crucial in kidney disease pathogenesis, this co-localization in proximal tubules highlights a key site of action for these receptors in the renal system.

In summary, while our study focused on the co-localization of AT1 and LOX-1 in proximal tubules, we agree that further exploration of AT1R expression in other renal cell types would provide a more comprehensive understanding of its role across different kidney compartments. We have addressed this in the revised discussion.

Reviewer #1 (Recommendations For The Authors):

Minor points:

(1) In this study, AT1/LOX1 receptor complex was mainly observed in some renal cells, how about other types of cells that also highly express LOX1 and AT1r? Such as cardiomyocytes? Vascular endothelial cells?

Thank you for your insightful comment. In our study, we demonstrated that enhanced Gq signaling through co-treatment with AngII and oxLDL was not observed in other cell types, including vascular endothelial cells, smooth muscle cells, and macrophages, as indicated by the lack of an IP1 increase in response to the co-treatment (Fig. S2). The factors contributing to this heterogeneous response remain unclear, and further investigation is needed to explore this observation more thoroughly.

(2) Has the author detected such an effect on the AT2 receptor?

We greatly appreciate the reviewer’s insightful inquiry regarding the potential interaction between the AT2 receptor and LOX-1. In our previous work (Yamamoto et al., FASEB J 2015), we conducted an immunoprecipitation (IP) assay to investigate the interaction between LOX-1 and AT2 on cell membranes. The results of this assay demonstrated that, unlike AT1, LOX-1 exhibits minimal binding to the AT2 receptor under the experimental conditions tested. Specifically, our IP studies showed that while LOX-1 readily coimmunoprecipitated with AT1, indicating a strong interaction, this was not the case with AT2, where the binding was negligible. These findings suggest that the interaction between LOX-1 and AT1 is receptor-specific and that LOX-1 does not significantly associate with AT2 to influence signaling pathways.

(3) Which kind of ARBs are more effective for the inhibition of this AT1/LOX1 receptor conformational change?

Thank you for your insightful question regarding the effectiveness of ARBs in inhibiting the AT1/LOX-1 receptor conformational change. Based on our current understanding, any ARB should similarly block the downstream signaling resulting from the interaction between AT1 and LOX-1. This is because all ARBs function by inhibiting the binding of Ang II to AT1, thereby preventing receptor activation and the conformational changes that facilitate its interaction with LOX-1. Additionally, our previous study (FASEB J. 2015) demonstrated that even in the absence of Ang II, the activation of AT1 via the binding of oxLDL to LOX-1 was similarly blocked by ARBs, including olmesartan, telmisartan, valsartan, and losartan.

When oxLDL and Ang II are co-treated, the Gq signaling pathway is significantly amplified due to the interaction between LOX-1 and AT1. In this setting, all ARBs act by competitively inhibiting Ang II binding to AT1, effectively reducing Gq signaling. 

However, a subtle but important difference arises when considering the inverse agonist activity of certain ARBs. Olmesartan, telmisartan, and valsartan are thought to act not only as competitive inhibitors of Ang II but also as inverse agonists, meaning they reduce the baseline activity of the AT1 receptor by preventing the conformational changes in the absence of Ang II. This inverse agonist property is particularly relevant in pathological conditions where AT1 receptor activation can occur independently of Ang II binding, such as in the presence of oxLDL. In these cases, ARBs with inverse agonist activity may offer an additional therapeutic advantage by reducing receptor activation beyond what is achieved by simple antagonism.

Thus, while the general efficacy of ARBs in blocking the AT1/LOX-1 interaction could be under similar conditions of oxLDL and Ang II co-treatment, ARBs with inverse agonist properties may provide additional benefit by further reducing AT1 activity. 

We have revised the manuscript to clarify these points and to highlight the role of inverse agonist activity in ARB efficacy under these conditions.

Thank you again for your valuable comment, which has allowed us to refine our discussion on the relative efficacy of ARBs in inhibiting AT1/LOX-1 receptor interaction.

Reviewer #2 (Recommendations For The Authors):

My comments were pretty thorough in the public review. The only other comments I would add are the following:

(1) Why are there so few overlapping LOX1 and ATR puncta in Supplementary Figure 1 if the receptors co-localize? The figure would suggest a very small proportion of the receptors actually are co-localized.

Thank you for your insightful comment regarding the apparent scarcity of overlapping LOX-1 and AT1R puncta in Fig. S1. We agree that at first glance, the low number of colocalized puncta may raise questions about the extent of interaction between these receptors. However, based on our previous findings reported in FASEB J 2015, we believe this phenomenon can be explained by the dynamic nature of the LOX-1 and AT1 interaction.

As we reported in FASEB J 2015, the interaction between LOX-1 and AT1 is sensitive to buffer conditions. Specifically, in non-reducing conditions, LOX-1 and AT1 form complexes, whereas in reducing buffer, this interaction is not observed. This suggests that the interaction between these receptors is not stabilized by strong covalent (disulfide) bonds but is instead transient, likely involving non-covalent interactions. Thus, LOX-1 and AT1 may form and dissociate repeatedly, contributing to a dynamic receptor complex rather than a permanent colocalization. This transient interaction could explain the relatively low number of overlapping puncta observed at a given time point in the liveimaging analysis.

Moreover, as you pointed out, it is likely that only a small fraction of LOX-1 and AT1 are physically co-localized at any one moment. However, when these receptors do interact, co-treatment with oxLDL and Ang II has been shown to significantly enhance Gq signaling. This suggests that the functional consequence of the LOX-1/AT1 interaction, particularly in response to stimuli such as oxLDL and Ang II, is more critical than the frequency of receptor colocalization at any one time.

We have revised the manuscript to include this explanation and to clarify the dynamic nature of the LOX-1/AT1 interaction. This revision also highlights the importance of considering not just the number of colocalized receptors but also the functional outcomes of their interaction, such as enhanced Gq signaling in response to co-treatment.

Thank you again for your careful observation, which has allowed us to better communicate the complexity of the receptor dynamics in our study.

(2) Tubulin is misspelled in Figure 5 ("tublin").

Thank you for pointing out the typographical error in Fig. 5. We have corrected the spelling of "tubulin" in the revised figure. We appreciate your attention to detail, and we apologize for the oversight.

(3) Why does the number of replicates differ for some experimental sets (i.e. Figure 1h vs other panels in Figure 1, Figure 2d vs other panels in Figure 2, Figure 7: Lox-1KO treated with High dose AngII and HFD? There aren't obvious reasons why the number of replicates should differ so much within a set of studies.

We are grateful to the reviewer for highlighting the discrepancies in the number of replicates across different figures in our manuscript. We would like to provide detailed explanations for each case.

(1) Fig. 1h vs Other Panels in Fig. 1:

The calcium influx assay (Fig. 1h) required a higher number of replicates due to the inherent biological variability associated with calcium signaling. To achieve statistical significance and account for variability in these measurements, we conducted additional replicates. Other panels, such as those measuring IP1 accumulation (Fig. 1a–f), displayed more consistent and reproducible results, allowing us to use fewer replicates while still maintaining statistical power.

(2) Fig. 2d vs Fig. 2b and 2c: 

The difference in the number of replicates between Fig. 2d (N=8) and Fig. 2b and 2c (N=4) is due to the distinct nature of the measurements and the variability expected in each assay. In Fig. 2d, which measures the effects of a LOX-1 neutralizing antibody on BRET, additional replicates were needed to ensure the robustness of the statistical analysis due to the greater complexity and sensitivity of the assay. The inclusion of an antibody treatment introduces more variability, necessitating a higher number of replicates (N=8) to confidently assess the effects of the neutralizing antibody. In contrast, Fig. 2b and 2c involved BRET measurements of AT1 conformational changes without antibody intervention. These assays are more reproducible and have less experimental variability, allowing for a smaller sample size (N=4) while still achieving reliable and statistically significant results. The differences in sample size across these panels were carefully considered to ensure appropriate statistical power for each specific experimental condition.

(3) Fig. 7: LOX-1 KO Mice Treated with High-dose AngII vs Saline:

We acknowledge the reviewer’s concern regarding the higher number of LOX-1 KO mice treated with high-dose Ang II compared to the saline group. The number of saline-treated mice was indeed sufficient for reliable statistical analysis. However, the decision to increase the number of mice in the high-dose Ang II group was driven by the anticipated higher variability in the physiological responses under these conditions, such as blood pressure and renal injury. To ensure that we captured the full spectrum of responses and to maintain robust statistical power in the high-dose group, we opted to include more mice in this cohort. 

We hope this response provides clarity on the rationale behind the varying number of replicates across different experiments. We have rigorously applied appropriate statistical methods to account for these differences, ensuring that the conclusions drawn are robust and scientifically sound. We appreciate the reviewer’s understanding of the experimental constraints and variations that can arise in complex studies such as these.

Author response:

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

Public Reviews:

Joint Public Review: 

The molecular mechanisms that mediate the regulated exocytosis of neuropeptides and neurotrophins from neurons via large dense-core vesicles (LDCVs) are still incompletely understood. Motivated by their earlier discovery that the Rab3-RIM1 pathway is essential for neuronal LDCV exocytosis, the authors now examined the role of the Rab3 effector Rabphilin-3A in neuronal LDCV secretion. Based on multiple live and confocal imaging approaches, the authors provide evidence for a synaptic enrichment of Rabphilin-3A and for independent trafficking of Rabphilin-3A and LDCVs. Using an elegant NPY-pHluorin imaging approach, they show that genetic deletion of Rabphilin-3A causes an increase in electrically triggered LDCV fusion events and increased neurite length. Finally, knock-out-replacement studies, involving Rabphilin-3A mutants deficient in either Rab3- or SNAP25-binding, indicate that the synaptic enrichment of Rabphilin-3A depends on its Rab3 binding ability, while its ability to bind to SNAP25 is required for its effects on LDCV secretion and neurite development. The authors conclude that Rabphilin-3A negatively regulates LDCV exocytosis and propose that this mechanism also affects neurite growth, e.g. by limiting neurotrophin secretion. These are important findings that advance our mechanistic understanding of neuronal large dense-core vesicle (LDCV) secretion. 

The major strengths of the present paper are: 

(i) The use of a powerful Rabphilin-3A KO mouse model. 

(ii) Stringent lentiviral expression and rescue approaches as a strong genetic foundation of the study. 

(iii) An elegant FRAP imaging approach. 

(iv) A cutting-edge NPY-pHluorin-based imaging approach to detect LDCV fusion events. 

We thank the reviewers for their positive evaluation of our manuscript.

Weaknesses that somewhat limit the convincingness of the evidence provided and the corresponding conclusions include the following: 

(i) The limited resolution of the various imaging approaches introduces ambiguity to several parameters (e.g. LDCV counts, definition of synaptic localization, Rabphilin-3A-LDCV colocalization, subcellular and subsynaptic localization of expressed proteins, AZ proximity of Rabphilin-3A and LDCVs) and thereby limits the reliability of corresponding conclusions. Super-resolution approaches may be required here. 

We thank the reviewer for their constructive suggestion. We fully agree that super-resolution imaging would produce a more precise localization of RPH3A and co-localization with DCVs. We have now repeated our (co)-localization experiments with STED microscopy. We find that RPH3A colocalized with the pre-synaptic marker Synapsin1 and, to a lesser extent, with the post synaptic marker Homer and DCV marker chromogranin B (new Figure 1). This indicates that RPH3A is highly enriched in synapses, mostly the pre-synapse, and that RPH3A partly co-localizes with DCVs.  

(ii) The description of the experimental approaches lacks detail in several places, thus complicating a stringent assessment. 

We apologize for the lack of detail in explaining the experimental approaches. We have included a more detailed description in the revised manuscript. 

(iii) Further analyses of the LDCV secretion data (e.g. latency, release time course) would be important in order to help pinpoint the secretory step affected by Rabphilin-3A. 

We agree. To address this comment, we have now included the duration of the fusion events (new Figure S2D-F). The start time of the fusion events are shown in the cumulative plots in now Figure 3F and I. The kinetics are normal in the RPH3A KO neurons.

(iv) It remains unclear why a process that affects a general synaptic SNARE fusion protein - SNAP25 - would specifically affect LDCV but not synaptic vesicle fusion. 

We agree that we have not addressed this issue systematically enough in the original manuscript. We have now added a short discussion on this topic in the Discussion of the revised manuscript (p 15, line 380-386). In brief, we do not claim full selectivity for the DCV pathway. Some effects of RPH3A deficiency on the synaptic vesicle cycle have been observed. Furthermore, because DCVs typically do not mix in the synaptic vesicle cluster and fuse outside the active zone (and outside the synapse), DCVs might be more accessible to RPH3A regulation.

(v) The mechanistic links between Rabphilin-3A function, LDCV density in neurites, neurite outgrowth, and the proposed underlying mechanisms involving trophic factor release remain unclear. 

We agree that we have not addressed all these links systematically enough in the original manuscript, although we feel that we have at least postulated the best possible working model to link RPH3A function to DCV exocytosis/neurotrophic factor release and neurite outgrowth (p 15-16, line 396-400). Of course, a single study cannot support all these links with sufficient experimental evidence. We have now added a short text on what we can conclude exactly based on our experiments and how we see the links between RPH3A function, DCV exocytosis/neurotrophic factor release, neurite outgrowth and DCV density in neurites (p 13-14, line 317-325).

Reviewer #1 (Public Review): 

Summary:

The manuscript by Hoogstraaten et al. investigates the effect of constitutive Rabphilin 3A (RPH3A) ko on the exocytosis of dense core vesicles (DCV) in cultured mouse hippocampal neurons. Using mCherry- or pHluorin-tagged NPY expression and EGFP- or mCherry tagged RPHA3, the authors first analyse the colocalization of DCVs and RPH3A. Using FRAP, the authors next analyse the mobility of DCVs and RAB3A in neurites. The authors go on to determine the number of exocytotic events of DCVs in response to high-frequency electrical stimulation and find that RPH3A ko increases the number of exocytotic events by a factor 2-3, but not the fraction of released DCVs in a given cell (8x 50Hz stim). In contrast, the release fraction is also increased in RBP3A KOs when doubling the stimulation number (16x 50Hz). They further observe that RPH3A ko increases dendrite and axon length and the overall number of ChgrB-positive DCVs. However, the overall number of DCVs and dendritic length in ko cells directly correlate, indicating that the number of vesicles per dendritic length remains unaffected in the RPH3A KOs. Lentiviral co-expression of tetanus toxin (TeNT) showed a non-significant trend to reduce axon and dendrite length in RPH3a KOs. Finally, the authors use co-expression of RAB3A and SNAP25 constructs to show that RAB3A but not SNAP25 interaction is required to allow the exocytosis-enhancing effect in RPH3A KOs. 

While the authors' methodology is sound, the microscopy results are performed well and analyzed appropriately, but their results in larger parts do not sufficiently support their conclusions. Moreover, the experiments are not always described in sufficient detail (e.g. FRAP; DCV counts vs. neurite length) to fully understand their claims. 

Overall, I thus feel that the manuscript does not provide a sufficient advance in knowledge. 

Strengths: 

- The authors' methodology is sound, and the microscopy results are performed well and analyzed appropriately. 

- Figure 2: The exocytosis imaging is elegant and potentially very insightful. The effect in the RPH3A KOs is convincing. 

- Figure 4: the logic of this experiment is elegant. It shows that the increased number of DCV fusion events in RPH3A KOs is related to the interaction of RPH3A with RAB3A but not with SNAP25. 

We thank the reviewer for their positive evaluation of our manuscript.

Weaknesses: 

- The results in larger parts do not sufficiently support the conclusions. 

- The experiments are not always described in sufficient detail (e.g. FRAP; DCV counts vs. neurite length) to fully understand their claims. 

- Not of sufficient advance in knowledge for this journal 

- The significance of differences in control experiments WT vs. KO) varies between experiments shown in different figures. 

- Axons and dendrites were not analyzed separately in Figures 1 and 2. 

- The colocalization study in Figure 1 would require super-resolution microscopy. 

To address the reviewers’ comments, we have provided a more detailed explanation of our analysis (p 19-20, line 521-542). In addition, we have repeated our colocalization experiments using STED microscopy, see Joint Public Review item (i).  

Reviewer #2 (Public Review): 

Summary: 

Hoogstraaten et al investigated the involvement of rabphilin-3A RPH3A in DCV fusion in neurons during calcium-triggered exocytosis at the synapse and during neurite elongation. They suggest that RPH3A acts as an inhibitory factor for LDV fusion and this is mediated partially via its interaction with SNAP25 and not Rab3A/Rab27. It is a very elegant study although several questions remain to be clarified. 

Strengths: 

The authors use state-of-the-art techniques like tracking NPY-PHluorin exocytosis and FRAP experiments to quantify these processes providing novel insight into LDCs exocytosis and the involvement of RPH3A. 

We thank the reviewer for their positive evaluation of our manuscript.

Weaknesses: 

At the current state of the manuscript, further supportive experiments are necessary to fully support the authors' conclusions. 

We thank the reviewer for their comments and suggestions. We have performed additional experiments to support our conclusions, see Joint Public Review items (i) – (iv)

Reviewer #3 (Public Review): 

Summary: 

The molecular mechanism of regulated exocytosis has been extensively studied in the context of synaptic transmission. However, in addition to neurotransmitters, neurons also secrete neuropeptides and neurotrophins, which are stored in dense core vesicles (DCVs). These factors play a crucial role in cell survival, growth, and shaping the excitability of neurons. The mechanism of release for DCVs is similar, but not identical, to that used for SV exocytosis. This results in slow kinetic and low release probabilities for DCV compared to SV exocytosis. There is a limited understanding of the molecular mechanisms that underlie these differences. By investigating the role of rabphilin-3A (RPH3A), Hoogstraaten et al. uncovered for the first time a protein that inhibits DCV exocytosis in neurons. 

Strengths: 

In the current work, Hoogstraaten et al. investigate the function of rabphilin-3A (RPH3A) in DVC exocytosis. This RAB3 effector protein has been shown to possess a Ca2+ binding site and an independent SNAP25 binding site. Using colocalization analysis of confocal imaging the authors show that in hippocampal neurons RPH3A is enriched at pre- and post-synaptic sites and associates specifically with immobile DCVs. Using site-specific RPH3A mutants they found that the synaptic location was due to its RAB3 interaction site. They further could show that RPH3A inhibits DCV exocytosis due to its interaction with SNAP25. They came to that conclusion by comparing NPY-pHluorin release in WT and RPH3A KO cells and by performing rescue experiments with RPH3A mutants. Finally, the authors showed that by inhibiting stimulated DCV release, RPH3A controlled the axon and dendrite length possibly through the reduced release of neurotrophins. Thereby, they pinpoint how the proper regulation of DCV exocytosis affects neuron physiology. 

We thank the reviewer for their positive evaluation of our manuscript.

Weaknesses: 

Data context 

One of the findings is that RPH3A accumulates at synapses and is mainly associated with immobile DCVs.

However, Farina et al. (2015) showed that 66% of all DCVs are secreted at synapses and that these DCVs are immobile prior to secretion. To provide additional context to the data, it would be valuable to determine if RPH3A KO specifically enhances secretion at synapses. Additionally, the authors propose that RPH3A decreases DCV exocytosis by sequestering SNAP25 availability. At first glance, this hypothesis appears suitable. However, due to RPH3A synaptic localization, it should also limit SV exocytosis, which it does not. In this context, the only explanation for RPH3A's specific inhibition of DCV exocytosis is that RPH3A is located at a synapse site remote from the active zone, thus protecting the pool of SNAP25 involved in SV exocytosis from binding to RPH3A. This hypothesis could be tested using super-resolution microscopy. 

We thank the reviewer for their suggestion. We have now performed super resolution microscopy, see Joint Public Review item (i). However, these new data do not necessarily explain the stronger effect of RP3A deficiency on DCV exocytosis, relative to SV exocytosis. We have added a short discussion on this topic to the revised manuscript, see Joint Public Review item (iv).

Technical weakness 

One technical weakness of this work consists in the proper counting of labeled DCVs. This is significant since most findings in this manuscript rely on this analysis. Since the data was acquired with epi-fluorescence or confocal microscopy, it doesn't provide the resolution to visualize individual DCVs when they are clumped. The authors use a proxy to count the number of DCVs by measuring the total fluorescence of individual large spots and dividing it by the fluorescence intensity of discrete spots assuming that these correspond to individual DCVs. This is an appropriate method but it heavily depends on the assumption that all DCVs are loaded with the same amount of NPY-pHluorin or chromogranin B (ChgB). Due to the importance of this analysis for this manuscript, I suggest that the authors show that the number of DCVs per µm2 is indeed affected by RPH3A KO using super-resolution techniques such as dSTORM, STED, SIM, or SRRF. 

The reviewer is correct that this is a crucial issue, that we have not addressed optimally until now. We have previously devoted a large part of a previous manuscript to this issue, but have not referred to this previous work clearly enough. We have now clarified this (p 7, line 187-190). In brief, we have previously quantified the ratio between fluorescent intensity of ChgB and NPY-pHluorin in confocal microscopy over the number of dSTORM puncta in sparse areas of WT mouse hippocampal neurons (Persoon et al., 2018). This quantification yielded a unitary fluorescence intensity per vesicle that was very stable of different neurons. Although there might be some underestimation of the total number of DCVs when using confocal microscopy, the study of Persoon et al. (2018) has demonstrated that these parameters correlate well and that the estimations are accurate. Considering that the rF/F0 is similar in RPH3A WT and KO neurons (now Figure S2I), meaning that the intensity of NPY-pHluorin of one fusion event is comparable, we can presume that this correlation also applies for the RPH3A KO neurons.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Major points: 

(1) The authors perform an extensive analysis regarding the colocalization of RPH3A and DCVs (Figure 1 upper part). This analysis is hampered by the fact that the recorded data has in relation to vesicle size limited resolution (> 1 µm) to allow making strong claims here. In my view, super-resolution microscopy would be required for the co-localization studies shown in Figure 1. 

We fully agree and have now performed super-resolution microscopy, see Joint Public Review item (i)

(2) The FRAP experiments (Figure 1 lower part) cannot be sufficiently understood from what is presented. The methods say that both laser channels were activated during bleaching but NPY-pHluorin is not bleached in Fig.1E. Explanation of the bleaching is not very circumspect. In 1D, it is rather EGFP-RPH3A that is entering the bleached area than the NPY vesicles. These experiments require a more careful explanation of methodology, observed results, and their interpretation. Overall, the observed effects in the original kymograph traces require a better explanation. 

We acknowledge that NPY-pHluorin in Figure 1E (now Figure 2C) is not completely bleached. NPY-pHluorin appeared to be more difficult to bleach than NPY-mCherry. However, it is important to clarify that we merely bleached the neurites to remove the stationary puncta and facilitate our analysis of DCV/RPH3A dynamics. This bleaching step does not affect the interpretation of our results. We apologize that this was not clearly stated in the text and have made the necessary adjustments in legend, results- and methods section, (p 6-7, line 162-163; p 5, line 140-142 and p 19, line 508-513). Additionally, we apologize for the accidental switch of the kymographs for NPY-mCherry and EGFP-RPH3A in Figure 1D (now Figure 2B, C). We greatly appreciate identifying this error.  

(3) Figure 1: The authors need to mention whether axons, dendrites, or both were analyzed throughout the different panels and how they were identified. Is it possible that axons were wrapping around dendrites in their cultures (compare e.g. Shimojo et al., 2015)? Given the limited spatial resolution and because of this wrapping, interpretation of results could be affected. 

We completely agree with the reviewer’s assessment and conclusion. We are unable to distinguish axons from dendrites using this experimental design. We have made sure to specify in the text that our observation that RPH3A does not co-travel with DCVs is true for both dendrites and axons, (p 5, line 150).

(4) Figure 2: The exocytosis imaging is elegant and potentially very insightful. The effect in the RPH3A KOs is convincing. However, the authors determine the efficacy of exocytosis from NPY-pHluorin unquenching of DCVs only. This is only one of several possible parameters to read out the efficiency of exocytosis. Kinetics like e.g. delay between stimulation and start of exocytosis events or release time course of NPY after DCV fusion were not determined. Such analysis could give a better insight into what process before or after the fusion of DCVs is affected by RPH3A ko. 

We fully agree with the reviewer. We have now included the duration of the fusion events (new Figure S2D-F). The start time of the fusion events are shown in the cumulative plots in now Figure 3F and I. The kinetics are normal in the RPH3A KO neurons.

Moreover, it needs to be mentioned whether 2C and D are from WT or ko cultures. It would be best to show representative examples from both genotypes. 

We have now adjusted this in the new figure (now Figure 3C, D).

The number of fusion events is much increased but the release fraction is not significantly changed. While this is consistent with results in Figure 4C it is at variance with 4F. This raises questions about the reliability of the effects in RPH3A KOs. 

The release fraction indicates the number of fusion events normalized to the total DCV pool. In Figure 4D, we observed a slightly bigger pool size, which explains the lack of significance when analyzing the released fraction. In Figure 4G, however, DCV pool sizes are similar between KO and WT, leading to a statistically significant effect on release fraction in KO neurons. Furthermore, Figures 4B and E distinctly show a substantial increase in fusion events in RPH3A KO neurons. This variability in pool size observed could potentially be attributed to variation in culture or inherent biological variability.

Given the increased number of ChgrB-positive DCVs in RPH3A KOs (shown in Figure 2) and that only the cumulative number of exocytosis events were analysed, how can the authors exclude that the RPH3A ko only affects vesicle number but not release, if the % change in released vesicles is not different to WT? Kinetics of release don't seem to be affected. Importantly, what was the density of NPY-pHluorin vesicles in WT vs. ko? 

In Figure 2 (now Figure 5) we show that RPH3A KO neurons are larger and contain more endogenous ChgB+ puncta than WT neurons. This increased number of ChgrB+ puncta scales with their size as puncta density is not increased. A previous study (Persoon et al., 2018) has demonstrated a strong correlation between DCV number and neuron size. Our data show that RPH3A deficiency increased DCV exocytosis, but the released fraction of vesicles depends on the total number of DCVs, which we determined during live recording by dequenching NPY-pHluorin using NH4+. Considering that this is an overexpression of a heterologous DCV-fusion reporter, and not endogenous staining of DCVs, as in the case of ChgrB+ puncta, some variability is not unexpected.

Also in these experiments, the question arises of whether the authors analyse axons, dendrites, or both throughout the different panels and how they were identified. 

In our experimental design we record all fusion events per cell, including both axons and dendrites but excluding the cell soma. We have clarified this in the method section, (p 19, line 508 and p 19, line 521-522).

(5) Figure 3: in D the authors show that ChgrB-pos. DCV density is slightly increased in KOs. How does this relate to the density of NPY-pHluorin DCVS in Figure 2? 

We do not observe a difference in NPY-pHluorin density (see Author response image 1). However, it is important to note that we relied on tracing neurites in live recording images to determine the neuronal size. In contrast, the ChgB density was based on dendritic length using MAP2 (post-hoc) staining was limited. In addition, Chgr+ puncta represent an endogenous DCV staining, NPY-pHluorin quantification is based on overexpression of a heterologous DCV-fusion reporter. These two factors likely contribute some variability.

Author response image 1.

The authors show a non-significant trend of TeNT coexpression to reduce axon and dendrite lengths in RPH3A KOs. While this trend is visible, I think one cannot draw conclusions from that when not reaching significance. The argument of the authors that the increased axon and dendrite lengths are created by growth factor peptide release from DCV during culture time is interesting. However, the fact that TeNT expression shows a trend toward reducing this effect on axons/dendrites is not sufficient to prove the release of such growth factors. 

We agree. We have toned down this speculation in the revised manuscript, (p 15-16, line 395-400).

Lastly, the authors don't provide insight into the mechanisms, of how RPH3A ko increases the number of DCVs per µm dendritic length in the neurons. In my view, there are too many loose ends in this story of how RPH3A ko first increases spontaneous release of DCVs and then enhances neurite growth and DCV density. Did the authors e.g. measure the spontaneous release of DCVs in their cultures? 

We measured spontaneous release of DCVs during the 30s baseline recording prior to stimulation. We observed no difference in spontaneous release between WT and KO neurons (now Figure S2H). However, baseline recording lasted only 30 seconds. It is possible that this was too short to detect subtle effects.

Other points: 

(1) Figure 4: the logic of this experiment is elegant. It shows that the increased number of DCV fusion events in RPH3A KOs is related to the interaction of RPH3A with RAB3A but not with SNAP25. As mentioned above, it is irritating that the reduction of fusion events in KOs and on the release fraction is sometimes reaching significance, but sometimes it does not. Likewise, the absence of significant effects on DCV numbers is not consistent with the results shown in Figures 3C and D. 

DCV numbers in Figure 3 (now Figure 5) are determined by staining for endogenous ChgB, whereas in Figure 4D and G DCV numbers are determined by overexpressing NPY-pHluorin and counting the dequenched puncta following a NH4+ puff.

(2) Figure 1B: truncation of the y-axis needs to be clearly indicated. 

We have replaced this figure with new Figure 1 and have indicated truncations of the y-axis when needed (new Figure 1E). 

(3) Page 10: "Given that neuropeptides are key modulators of adult neurogenesis (Mu et al., 2010), and that RPH3A depletion leads to increased DCV exocytosis, it is coherent that we observed longer neurites in RPH3A KO neurons." I cannot follow the argument of the authors here: what has neurogenesis to do with neurite length? 

We apologize for the confusion. We have clarified this in the revised text, (p 16, line 398-400).

Minor point: 

There are some typos in the manuscript. e.g., page 8: "... may partially dependent on regulated secretion...); page 6: "...to dequence all...". 

Thank you for noticing, we have corrected the typos.

Reviewer #2 (Recommendations For The Authors): 

(1) Supplementary Figure S1A, in my opinion, should be in Figure 1A as it illustrates all the constructs used in this study and helps the reader to follow it up. 

We thank the reviewer for their suggestion. However, we feel that with the adjustments we have made in Figure 1, the illustrations of the constructs fit better in Figure S1, since new Figure 1 shows the localization of endogenous RPH3A and not that of the constructs.  

(2) One of the conclusions of the manuscript is the synaptic localization of the different RPH3A mutants. The threshold for defining synaptic localization is not clear either from the images nor from the analysis: for example, the Menders coefficient for VGut1-Syn1 which is used as a positive control, ranges from 0.65-0.95 and that of RPH3A and Syn1 ranges from 0.5-0.95. These values should be compared to all mutants and the conclusions should be based on such comparison. 

We agree. We have now repeated our initial co-localization experiment with all the RPH3A mutants (now Figure S1D-F).  

(3) Strengthening this figure with STED/SIM/dSTORM microscopy can verify and add a new understanding of the subtle changes of RPH3A localization. 

We fully agree and have now added super-resolution microscopy data, see Joint Public Review item (i).

(4) As RAB3A/RAB27A (ΔRAB3A/RAB27A) loses the punctate distribution, please clarify how can it function at the synapse and not act as a KO. Is it sorted to the synapse and how does it is sorted to the synapse? 

We used lentiviral delivery to introduce our constructs, resulting in the overexpression of ΔRAB3A/RAB27A mutant RPH3A. This overexpression likely compensates for the loss of the punctate distribution of RPH3A, thereby maintaining its limiting effect on DCV exocytosis. It is plausible that under physiological conditions, the mislocalization of RPH3A would lead to increased exocytosis, similar to what we observed in the KO. 

(5) Is RPH3A expressed in both excitatory and inhibitory neurons? 

We agree this is an important question. Single cell RNA-seq already suggests the protein is expressed in both, but we nevertheless decided to test expression of RPH3A protein in excitatory and inhibitory neurons, using immunocytochemistry with VGAT and VGLUT as markers in hippocampal and striatal WT neurons. We found that RPH3A is expressed in both VGLUT+ hippocampal neurons and VGAT+ striatal neurons (new Figure S1A, B).  

(6) The differential use of ChgB and NPY as markers for DCVs should be clarified and compared as these are used at different stages of the manuscript. 

We have previously addressed the comparison between ChgB and NPY-pHluorin (Persoon et al., 2018). We made sure to indicate this more clearly throughout the manuscript to clarify the use of the two markers. 

(7) FRAP experiments- A graph describing NPY recovery should be added as a reference to 2H and discussed. 

We agree. We have made the necessary adjustments (new Figure 2G).

(8) Figure 2E shows some degree of "facilitation" between the 2 8x50 pulses RPH3A KO neurons. Can the author comment on that? What was the reason for using this dual stimulation protocol? 

There is indeed some facilitation between the two 8 x 50 pulses in KO neurons and to a lesser extent also in the WT neurons, which we have observed before in WT neurons (Baginska et al., 2023). Baginska et al. (2023) showed recently that different stimulation protocols can influence certain fusion dynamics, like the ratio of persistent and transient events and event duration. We used two different stimulation protocols to thoroughly investigate the effect of RPH3A on exocytosis, and assess the robustness of our findings regarding the number of fusion events. Fusion kinetics was similar in WT an KO neurons for both stimulation protocols (new Figure 2D-F).

(9) Figure 3 quantifies dendrites length and then moves to quantify both axon and dendrites for the Tetanus toxin experiment. What are the effects of KO on axon length? In the main figures, it is not mentioned but in S3 it seems not to be affected. How does it reconcile with the main conclusion on neurite length? 

Figure 3H (now Figure 6C) shows the effect of the KO on axon length: the axon length is increased in RPH3A KO neurons compared to WT, similar to dendrite length. Re-expressing RPH3A in KO neurons rescues axonal length to WT levels. In Figure S3, we observe a similar trend as in main Figure 3 (new Figure 6), yet this effect did not reach significance. Based on this, we concluded that neurite length is increased upon RPH3A depletion.

(10) For lay readers, please explain the total pool and how you measured it. However, see the next comment. 

We agree. We have now defined this better in the revised manuscript, (p 19, line 524-527 and p 20, line 535-539).

(11) It is a bit hard to understand if the total number of DCV was increased in the KO and if the pool size was increased and in which figure it is quantified. Some sentences like: "A trend towards a larger intracellular DCV pool in KO compared to WT neurons was observed" do not fit with "No difference in DCV pool size was observed between WT and KO neurons (Figure S2D)" or with "During stronger stimulation (16 bursts of 50 APs at 50 Hz), the total fusion and released fraction of DCVs were increased in KO neurons compared to WT". They are not directly supported, or not related to specific figures. Please indicate if the total DCVs pool, as measured by NH4, was increased and based on that, the fraction of the releasable DCVs following the long stimulation. From Figure 2H, the conclusion is an increase in fusion events. In general, NH4 is not quantified clearly- is it quantified in Figure S2C? And if it is a trend, how can it become significant in Figure 3? 

We agree there has been some inconsistency in the way we describe the data on the total number of DCVs. We have addressed this in the revised text to ensure better clarity. The total DCV pool measured by NPY-pHluorin was not significantly increased in KO neurons, we see a trend towards a bigger DCV pool in the 2x8 50 Hz stimulation paradigm (now Figure S2C), therefore the released fraction of vesicles is not increased in Figure 1G (now Figure 3G). The number of DCV in Figure 3 (now Figure 5) is based on endogenous ChgB staining and not overexpression like the DCV pool measured by NPY-pHluorin. In Figure 3 (now Figure 5) we show that RPH3A KO neurons have slightly more ChgB+ puncta compared to WT.

(12) In Figure 3, the quantification is not clear, discrete puncta are not visible but rather a smear of chromogranin staining. How was it quantified? An independent method to count DCV number, size, and distribution like EM is necessary to support and add further understanding. 

We acknowledge that discrete ChgB puncta are not completely visible in Figure 3 (now Figure 5). Besides the inherent limitation in resolution with confocal imaging, we believe that this is due to ChgB accumulation in the KO neurons, as shown in now Figure 5D. Nonetheless, to address this concern of the reviewer, we have selected other images that represent our dataset (now Figure 5A). Furthermore, the number of ChgB+ DCVs was calculated using SynD software (Schmitz et al., 2011; van de Bospoort et al., 2012) (see previous reply). EM would offer valuable independent confirmation on the total DCV number, size and distribution. However, with the current method we already know that vesicle numbers are at least similar. Does that justify the (major) investment in a quantitative EM study? Moreover, this issue does not affect the central message of the current study.

(13) Can the author discuss if the source of DCVs that are released at the synapse is similar or different from the source of DCVs fused while neurites elongate? 

With our current experimental design, we are unable to draw conclusions regarding this aspect. We are not sure how experiments to identify this source (probably the Golgi?) would be crucial to sustain the central message of our study.

(14) An interesting and related question: what are the expression levels of RPH3A during development and neuronal growth during the nervous system development? 

While we have not specifically examined the expression levels of RPH3A over development, public databases show that RPH3A expression increases over time in mice, consistent with other synaptic proteins (Blake et al., 2021; Baldarelli et al., 2021; Krupke et al., 2017). We have now added this to the revised manuscript (p 2, line 55-56).

(15) The conclusion from Figure 4 about the contribution of SNAP25 interaction to RPH3A inhibitory effect is not convincing. The data are scattered and in many neurons, high levels of fusion events were detected. Further or independent experiments are needed to support this conclusion. For example, is the interaction with SNAP25 important for its inhibitory activity in other DCV-releasing systems like adrenal medulla chromaffin cells? 

We agree that further studies in other DCV-releasing systems like chromaffin cells would provide valuable insight into the role of SNAP25 interaction in RPH3A’s inhibitory effect on exocytosis. However, we believe that starting new series of experiments in another model system is outside of the scope of our current study.

(16) Furthermore, the number of DCVs in the KO is similar in this experiment, raising some more questions about the quantification of the number of vesicles, that differ, in different sections of the manuscript (points # 10,11). 

The total DCV pool in the fusion experiments is measured by overexpression NPY-pHluorin, this cannot be directly compared to the number of endogenous ChgB+ DCV in Figure 3 (now Figure 5), see also item (11)

(17) The statement - "RPH3A is the only negative regulator of DCV" is not completely accurate as other DCV inhibitors like tomosyn were described before. 

We agree. By this statement, we intend to convey that RPH3A is the only negative regulator of DCVs without substantial impact on synaptic vesicle exocytosis, unlike Tomosyns. We have clarified this in the revised text, (p 15, line 366-367).

(18) The support for the effect of KO on the "clustering of DCVs" is not convincing. 

The intensity of endogenous ChgB puncta was decreased in RPH3A KO neurons (now Figure 5E). However, the peak intensity induced by single NPY-pHluorin labeled DCV fusion events (quanta) was unchanged (now Figure S2I). This indicates that the decrease in ChgB puncta intensity must be due to a reduced number of DCVs (quanta) in this specific location. We have interpreted that as ‘clustering’, or maybe ‘accumulation’. However, we only put forward this possibility. We are now more careful in our speculations within the text, (p 11 line 271-277).

(19) Final sentence: "where RPH3A binds available SNAP25, consequently restricting the assembly of SNARE complexes" should be either demonstrated or rephrased as no effect of trans or general SNARE complex formation is shown. 

We agree. We have made the necessary adjustments in the text, (p 15, line 387-389).   

(20) A scheme summarizing RPH3A's interaction with synaptic proteins and its effects on DCVs release, maybe even versus its effects on SVs release, should be considered as a figure or graphic abstract. 

We have included a working model in Figure 7.  

(21) Figure 4 logically should come after Figure 2 to summarize the fusion-related chapter before moving to neurite elongation. 

We have placed Figure 4 after Figure 2 (now Figure 3).

Reviewer #3 (Recommendations For The Authors): 

One important finding of this study is that RPH3A downregulates neuron size, possibly by inhibiting DCV release. Additionally, the authors demonstrated that the number of DCVs is directly proportional to the number of DCVs per µm2, and that RPH3A KO reduces DCV clustering. This conclusion was drawn by comparing ChgB with NPY-pHluorin loading of the DCVs. However, this comparison is not valid as ChgB is expressed at an endogenous level and NPY-pHluorin is over-expressed. In the KO situation where DCV exocytosis is enhanced, the available endogenous ChgB may be depleted faster than the overexpressed NPY-pHluorin. Hoogstraaten et al. should either perform a study in which ChgB is overexpressed to test whether the difference in DCV remains or at least provides an alternative interpretation of their data. 

We thank the reviewer for this comment. The reviewer challenges one or two conclusions in our original manuscript (It is not entirely clear to what exactly “This conclusion” refers): (a) “the number of DCVs is directly proportional to the number of DCVs per µm2”, and (b) “that RPH3A KO reduces DCV clustering”. The reviewer probably means that the number of DCVs per neuron is directly proportional to size of the neuron (a) and states this (these) conclusion(s) are “not valid as ChgB is expressed at an endogenous level and NPY-pHluorin is over-expressed” because “endogenous ChgB may be depleted faster than the overexpressed NPY-pHluorin”. We have three arguments to conclude that faster depletion of ChgB cannot affect these two conclusions: (1) DCVs bud off from the Golgi with newly synthesized (fresh) ChgB. Whether or not a larger fraction of DCVs is released does not influence this initial ChgB loading into DCVs (together with over-expressed NPY-pHluorin); (2) in hippocampal neurons merely 1-6% of the total DCV pool undergoes exocytosis (the current study and also extensively demonstrated in Persoon et al., 2018). RPH3A KO neurons release few percent more of the total DCV pool. Hence, “depletion of ChgB” is only marginally different between experimental groups; and (c) the proposed experiment overexpressing ChgB will not help scrutinize our current conclusions as ChgB overexpression is known to affect DCV biogenesis and the total DCV pool, most likely much more than a few percent more release by RPH3A deficiency.

Hoogstraaten et al. conducted a thorough analysis of the impact of RPH3A KO and its rescue using various mutants on dendrite and axon length (see Supplementary Figure 3). However, they did not test the effect of the ΔSNAP25 mutant. The authors demonstrated that this mutant is the least efficient in rescuing DCV exocytosis (Figure 4E). Hence the neurons expressing this mutant should have a similar size to the KO neurons. This finding would strongly support the argument that DCV exocytosis regulates neuron size. Otherwise, it would suggest that RPH3A may have a function in regulating exocytosis at the growth cones that is independent of SNAP25. Since the authors most probably have the data that allows them to measure the neuron size (acquired for Supplementary Figure 2), I suggest that they perform the required analysis. 

We agree this is important and performed new experiments to determine the dendrite length of RPH3A WT, KO and KO neurons expressing the ΔSNAP25 mutant. We observed that the dendrite length of RPH3A KO neurons expressing ΔSNAP25 mutant is indeed similar to KO neurons (new Figure S3C). Although not significant we observe a clear trend towards bigger neurons compared to WT.  This strengthens our conclusion that increased DCV exocytosis contributes to the observed increased neuronal size.

The authors displayed the result of DCV exocytosis in two ways. One is by showing the number of exocytosis events the other is to display the proportion of DCVs that were secreted. They do the latter by dividing the secreted DCV by the total number of DCVs. These are visualized at the end of the experiment through NH4+ application. While this method works well for synaptic secretion as the marker of SV is localized to the SV membrane and remains at the synapse upon SV exocytosis, it cannot be applied in the same manner when it is the DCV content that is labeled as it is released upon secretion. Hence, the total pool of vesicles should be the number of DCV counted upon NH4+ application in addition to those that are secreted. This way of analyzing the total pool of DCV might also explain the difference in this pool size between KO neurons stimulated two times with 8 stimuli instead of one time with 16 stimuli (Sup Fig 2 C and D). This is an important point as it affects the conclusions drawn from Figure 2. 

We thank the reviewed for this comment. We agree, and we have made the necessary adjustments throughout the manuscript. 

The kymogram of DCV exocytic events displayed in Figure 2D shows a majority of persistent (>20s long) events. This is strange as NPY-pHluori corresponds to the released cargo. Previous work using the same labeling and stimulation technique showed that content release occurs in less than 10s (Baginska et al. 2023). The authors should comment on that difference. 

In Baginska et al. (2023), the authors distinguished between persistent and transient events. The transient events are shorter than 10s for the 2x8 and 16x stimulation paradigms, whereas persistent events can last for more than 10s. In our study we did not make this distinction. However, in response to this reviewer, we have now quantified the fusion duration per cell. These new data show that the mean duration is similar between genotypes for both stimulation paradigms. We have added these new data (new Figure S2D-F).

In Figures 1D and E, some puncta in the kymogram appeared to persist after bleaching. This raises questions about the effectiveness of the bleaching procedure for the FRAP experiment. 

The reviewer is correct that NPY-pHluorin in Figure 1E (now Figure 2C) is not fully bleached. NPY-pHluorin was more resistant to bleaching than NPY-mCherry. However, we merely bleached the neurites to facilitate our analysis by reducing fluorescence of the stationary puncta without causing phototoxicity. Some remaining fluorescence after bleaching does not affect our conclusions in any way.

In the discussion, the paragraph titled "RPH3A does not travel with DCVs in hippocampal neurons" is quite confusing and would benefit from a streamlined explanation. 

We thank the reviewed for this comment. We made the necessary adjustments to make this paragraph clearer, (p 14, line 339-351).

First paragraph of page 8 "TeNT expression in KO neurons restored neurite length to WT levels. When compared to KO neurons without TeNT, neurite length was not significantly decreased but displayed a trend towards WT levels (Figure 3G, H)." These two sentences are confusing as they seem contradictory. 

We agree that this conclusion has been too strong. However, we do not see a contradiction. The significant effect between KO and control neurons on both axon and dendrite length is lost upon TeNT expression (which forms the basis for our conclusions cited by the reviewer, now Figure 6B, C). While the difference between KO neurons +/- TeNT did not reach statistical significance. The (strong) trend is clearly in the same direction. We have refined our original conclusion in the revised manuscript, (p 12, line 304-306).

The data availability statement is missing. 

We have added the data availability statement, (p 21, line 571-572).

Reviewer #2 (Public Review):

Here I submit my previous review and a great deal of additional information following on from the initial review and the response by the authors.

* Initial Review *

Assessment:

This manuscript is based upon the unprecedented identification of an apparently highly unusual trigeminal nuclear organization within the elephant brainstem, related to a large trigeminal nerve in these animals. The apparently highly specialized elephant trigeminal nuclear complex identified in the current study has been classified as the inferior olivary nuclear complex in four previous studies of the elephant brainstem. The entire study is predicated upon the correct identification of the trigeminal sensory nuclear complex and the inferior olivary nuclear complex in the elephant, and if this is incorrect, then the remainder of the manuscript is merely unsupported speculation. There are many reasons indicating that the trigeminal nuclear complex is misidentified in the current study, rendering the entire study, and associated speculation, inadequate at best, and damaging in terms of understanding elephant brains and behaviour at worst.

Original Public Review:

The authors describe what they assert to be a very unusual trigeminal nuclear complex in the brainstem of elephants, and based on this, follow with many speculations about how the trigeminal nuclear complex, as identified by them, might be organized in terms of the sensory capacity of the elephant trunk.<br /> The identification of the trigeminal nuclear complex/inferior olivary nuclear complex in the elephant brainstem is the central pillar of this manuscript from which everything else follows, and if this is incorrect, then the entire manuscript fails, and all the associated speculations become completely unsupported.

The authors note that what they identify as the trigeminal nuclear complex has been identified as the inferior olivary nuclear complex by other authors, citing Shoshani et al. (2006; 10.1016/j.brainresbull.2006.03.016) and Maseko et al (2013; 10.1159/000352004), but fail to cite either Verhaart and Kramer (1958; PMID 13841799) or Verhaart (1962; 10.1515/9783112519882-001). These four studies are in agreement, the current study differs.

Let's assume for the moment that the four previous studies are all incorrect and the current study is correct. This would mean that the entire architecture and organization of the elephant brainstem is significantly rearranged in comparison to ALL other mammals, including humans, previously studied (e.g. Kappers et al. 1965, The Comparative Anatomy of the Nervous System of Vertebrates, Including Man, Volume 1 pp. 668-695) and the closely related manatee (10.1002/ar.20573). This rearrangement necessitates that the trigeminal nuclei would have had to "migrate" and shorten rostrocaudally, specifically and only, from the lateral aspect of the brainstem where these nuclei extend from the pons through to the cervical spinal cord (e.g. the Paxinos and Watson rat brain atlases), the to the spatially restricted ventromedial region of specifically and only the rostral medulla oblongata. According to the current paper the inferior olivary complex of the elephant is very small and located lateral to their trigeminal nuclear complex, and the region from where the trigeminal nuclei are located by others, appears to be just "lateral nuclei" with no suggestion of what might be there instead.

Such an extraordinary rearrangement of brainstem nuclei would require a major transformation in the manner in which the mutations, patterning, and expression of genes and associated molecules during development occurs. Such a major change is likely to lead to lethal phenotypes, making such a transformation extremely unlikely. Variations in mammalian brainstem anatomy are most commonly associated with quantitative changes rather than qualitative changes (10.1016/B978-0-12-804042-3.00045-2).

The impetus for the identification of the unusual brainstem trigeminal nuclei in the current study rests upon a previous study from the same laboratory (10.1016/j.cub.2021.12.051) that estimated that the number of axons contained in the infraorbital branch of the trigeminal nerve that innervate the sensory surfaces of the trunk is approximately 400 000. Is this number unusual? In a much smaller mammal with a highly specialized trigeminal system, the platypus, the number of axons innervating the sensory surface of the platypus bill skin comes to 1 344 000 (10.1159/000113185). Yet, there is no complex rearrangement of the brainstem trigeminal nuclei in the brain of the developing or adult platypus (Ashwell, 2013, Neurobiology of Monotremes), despite the brainstem trigeminal nuclei being very large in the platypus (10.1159/000067195). Even in other large-brained mammals, such as large whales that do not have a trunk, the number of axons in the trigeminal nerve ranges between 400 000 and 500 000 (10.1007/978-3-319-47829-6_988-1). The lack of comparative support for the argument forwarded in the previous and current study from this laboratory, and that the comparative data indicates that the brainstem nuclei do not change in the manner suggested in the elephant, argues against the identification of the trigeminal nuclei as outlined in the current study. Moreover, the comparative studies undermine the prior claim of the authors, informing the current study, that "the elephant trigeminal ganglion ... point to a high degree of tactile specialization in elephants" (10.1016/j.cub.2021.12.051). While clearly the elephant has tactile sensitivity in the trunk, it is questionable as to whether what has been observed in elephants is indeed "truly extraordinary".

But let's look more specifically at the justification outlined in the current study to support their identification of the unusual located trigeminal sensory nuclei of the brainstem.

(1) Intense cytochrome oxidase reactivity<br /> (2) Large size of the putative trunk module<br /> (3) Elongation of the putative trunk module<br /> (4) Arrangement of these putative modules correspond to elephant head anatomy<br /> (5) Myelin stripes within the putative trunk module that apparently match trunk folds<br /> (6) Location apparently matches other mammals<br /> (7) Repetitive modular organization apparently similar to other mammals.<br /> (8) The inferior olive described by other authors lacks the lamellated appearance of this structure in other mammals

Let's examine these justifications more closely.

(1) Cytochrome oxidase histochemistry is typically used as an indicative marker of neuronal energy metabolism. The authors indicate, based on the "truly extraordinary" somatosensory capacities of the elephant trunk, that any nuclei processing this tactile information should be highly metabolically active, and thus should react intensely when stained for cytochrome oxidase. We are told in the methods section that the protocols used are described by Purkart et al (2022) and Kaufmann et al (2022). In neither of these cited papers is there any description, nor mention, of the cytochrome oxidase histochemistry methodology, thus we have no idea of how this histochemical staining was done. In order to obtain the best results for cytochrome oxidase histochemistry, the tissue is either processed very rapidly after buffer perfusion to remove blood or in recently perfusion-fixed tissue (e.g., 10.1016/0165-0270(93)90122-8). Given: (1) the presumably long post-mortem interval between death and fixation - "it often takes days to dissect elephants"; (2) subsequent fixation of the brains in 4% paraformaldehyde for "several weeks"; (3) The intense cytochrome oxidase reactivity in the inferior olivary complex of the laboratory rat (Gonzalez-Lima, 1998, Cytochrome oxidase in neuronal metabolism and Alzheimer's diseases); and (4) The lack of any comparative images from other stained portions of the elephant brainstem; it is difficult to support the justification as forwarded by the authors. It is likely that the histochemical staining observed is background reactivity from the use of diaminobenzidine in the staining protocol. Thus, this first justification is unsupported.<br /> Justifications (2), (3), and (4) are sequelae from justification (1). In this sense, they do not count as justifications, but rather unsupported extensions.

(4) and (5) These are interesting justifications, as the paper has clear internal contradictions, and (5) is a sequelae of (4). The reader is led to the concept that the myelin tracts divide the nuclei into sub-modules that match the folding of the skin on the elephant trunk. One would then readily presume that these myelin tracts are in the incoming sensory axons from the trigeminal nerve. However, the authors note that this is not the case: "Our observations on trunk module myelin stripes are at odds with this view of myelin. Specifically, myelin stripes show no tapering (which we would expect if axons divert off into the tissue). More than that, there is no correlation between myelin stripe thickness (which presumably correlates with axon numbers) and trigeminal module neuron numbers. Thus, there are numerous myelinated axons, where we observe few or no trigeminal neurons. These observations are incompatible with the idea that myelin stripes form an axonal 'supply' system or that their prime function is to connect neurons. What do myelin stripe axons do, if they do not connect neurons? We suggest that myelin stripes serve to separate rather than connect neurons." So, we are left with the observation that the myelin stripes do not pass afferent trigeminal sensory information from the "truly extraordinary" trunk skin somatic sensory system, and rather function as units that separate neurons - but to what end? It appears that the myelin stripes are more likely to be efferent axonal bundles leaving the nuclei (to form the olivocerebellar tract). This justification is unsupported.

(6) The authors indicate that the location of these nuclei matches that of the trigeminal nuclei in other mammals. This is not supported in any way. In ALL other mammals in which the trigeminal nuclei of the brainstem have been reported they are found in the lateral aspect of the brainstem, bordered laterally by the spinal trigeminal tract. This is most readily seen and accessible in the Paxinos and Watson rat brain atlases. The authors indicate that the trigeminal nuclei are medial to the facial nerve nucleus, but in every other species the trigeminal sensory nuclei are found lateral to the facial nerve nucleus. This is most salient when examining a close relative, the manatee (10.1002/ar.20573), where the location of the inferior olive and the trigeminal nuclei matches that described by Maseko et al (2013) for the African elephant. This justification is not supported.

(7) The dual to quadruple repetition of rostro-caudal modules within the putative trigeminal nucleus as identified by the authors relies on the fact that in the neurotypical mammal, there are several trigeminal sensory nuclei arranged in a column running from the pons to the cervical spinal cord, these include (nomenclature from Paxinos and Watson in roughly rostral to caudal order) the Pr5VL, Pr5DM, Sp5O, Sp5I, and Sp5C. But, these nuclei are all located far from the midline and lateral to the facial nerve nucleus, unlike what the authors describe in the elephants. These rostrocaudal modules are expanded upon in Figure 2, and it is apparent from what is shown is that the authors are attributing other brainstem nuclei to the putative trigeminal nuclei to confirm their conclusion. For example, what they identify as the inferior olive in figure 2D is likely the lateral reticular nucleus as identified by Maseko et al (2013). This justification is not supported.

(8) In primates and related species, there is a distinct banded appearance of the inferior olive, but what has been termed the inferior olive in the elephant by other authors does not have this appearance, rather, and specifically, the largest nuclear mass in the region (termed the principal nucleus of the inferior olive by Maseko et al, 2013, but Pr5, the principal trigeminal nucleus in the current paper) overshadows the partial banded appearance of the remaining nuclei in the region (but also drawn by the authors of the current paper). Thus, what is at debate here is whether the principal nucleus of the inferior olive can take on a nuclear shape rather than evince a banded appearance. The authors of this paper use this variance as justification that this cluster of nuclei could not possibly be the inferior olive. Such a "semi-nuclear/banded" arrangement of the inferior olive is seen in, for example, giraffe (10.1016/j.jchemneu.2007.05.003), domestic dog, polar bear, and most specifically the manatee (a close relative of the elephant) (brainmuseum.org; 10.1002/ar.20573). This justification is not supported.

Thus, all the justifications forwarded by the authors are unsupported. Based on methodological concerns, prior comparative mammalian neuroanatomy, and prior studies in the elephant and closely related species, the authors fail to support their notion that what was previously termed the inferior olive in the elephant is actually the trigeminal sensory nuclei. Given this failure, the justifications provided above that are sequelae also fail. In this sense, the entire manuscript and all the sequelae are not supported.

What the authors have not done is to trace the pathway of the large trigeminal nerve in the elephant brainstem, as was done by Maseko et al (2013), which clearly shows the internal pathways of this nerve, from the branch that leads to the fifth mesencephalic nucleus adjacent to the periventricular grey matter, through to the spinal trigeminal tract that extends from the pons to the spinal cord in a manner very similar to all other mammals. Nor have they shown how the supposed trigeminal information reaches the putative trigeminal nuclei in the ventromedial rostral medulla oblongata. These are but two examples of many specific lines of evidence that would be required to support their conclusions. Clearly tract tracing methods, such as cholera toxin tracing of peripheral nerves cannot be done in elephants, thus the neuroanatomy must be done properly and with attention to details to support the major changes indicated by the authors.

So what are these "bumps" in the elephant brainstem?

Four previous authors indicate that these bumps are the inferior olivary nuclear complex. Can this be supported?

The inferior olivary nuclear complex acts "as a relay station between the spinal cord (n.b. trigeminal input does reach the spinal cord via the spinal trigeminal tract) and the cerebellum, integrating motor and sensory information to provide feedback and training to cerebellar neurons" (https://www.ncbi.nlm.nih.gov/books/NBK542242/). The inferior olivary nuclear complex is located dorsal and medial to the pyramidal tracts (which were not labelled in the current study by the authors but are clearly present in Fig. 1C and 2A) in the ventromedial aspect of the rostral medulla oblongata. This is precisely where previous authors have identified the inferior olivary nuclear complex and what the current authors assign to their putative trigeminal nuclei. The neurons of the inferior olivary nuclei project, via the olivocerebellar tract to the cerebellum to terminate in the climbing fibres of the cerebellar cortex.

Elephants have the largest (relative and absolute) cerebellum of all mammals (10.1002/ar.22425), this cerebellum contains 257 x109 neurons (10.3389/fnana.2014.00046; three times more than the entire human brain, 10.3389/neuro.09.031.2009). Each of these neurons appears to be more structurally complex than the homologous neurons in other mammals (10.1159/000345565; 10.1007/s00429-010-0288-3). In the African elephant, the neurons of the inferior olivary nuclear complex are described by Maseko et al (2013) as being both calbindin and calretinin immunoreactive. Climbing fibres in the cerebellar cortex of the African elephant are clearly calretinin immunopositive and also are likely to contain calbindin (10.1159/000345565). Given this, would it be surprising that the inferior olivary nuclear complex of the elephant is enlarged enough to create a very distinct bump in exactly the same place where these nuclei are identified in other mammals?

What about the myelin stripes? These are most likely to be the origin of the olivocerebellar tract and probably only have a coincidental relationship to the trunk. Thus, given what we know, the inferior olivary nuclear complex as described in other studies, and the putative trigeminal nuclear complex as described in the current study, is the elephant inferior olivary nuclear complex. It is not what the authors believe it to be, and they do not provide any evidence that discounts the previous studies. The authors are quite simply put, wrong. All the speculations that flow from this major neuroanatomical error are therefore science fiction rather than useful additions to the scientific literature.

What do the authors actually have?<br /> The authors have interesting data, based on their Golgi staining and analysis, of the inferior olivary nuclear complex in the elephant.

* Review of Revised Manuscript *

Assessment:

There is a clear dichotomy between the authors and this reviewer regarding the identification of specific structures, namely the inferior olivary nuclear complex and the trigeminal nuclear complex, in the brainstem of the elephant. The authors maintain the position that in the elephant alone, irrespective of all the published data on other mammals and previously published data on the elephant brainstem, these two nuclear complexes are switched in location. The authors maintain that their interpretation is correct, this reviewer maintains that this interpretation is erroneous. The authors expressed concern that the remainder of the paper was not addressed by the reviewer, but the reviewer maintains that these sequelae to the misidentification of nuclear complexes in the elephant brainstem renders any of these speculations irrelevant as the critical structures are incorrectly identified. It is this reviewer's opinion that this paper is incorrect. I provide a lot of detail below in order to provide support to the opinion I express.

Public Review of Current Submission:

As indicated in my previous review of this manuscript (see above), it is my opinion that the authors have misidentified, and indeed switched, the inferior olivary nuclear complex (IO) and the trigeminal nuclear complex (Vsens). It is this specific point only that I will address in this second review, as this is the crucial aspect of this paper - if the identification of these nuclear complexes in the elephant brainstem by the authors is incorrect, the remainder of the paper does not have any scientific validity.

The authors, in their response to my initial review, claim that I "bend" the comparative evidence against them. They further claim that as all other mammalian species exhibit a "serrated" appearance of the inferior olive, and as the elephant does not exhibit this appearance, that what was previously identified as the inferior olive is actually the trigeminal nucleus and vice versa.

For convenience, I will refer to IOM and VsensM as the identification of these structures according to Maseko et al (2013) and other authors and will use IOR and VsensR to refer to the identification forwarded in the study under review.<br /> The IOM/VsensR certainly does not have a serrated appearance in elephants. Indeed, from the plates supplied by the authors in response (Referee Fig. 2), the cytochrome oxidase image supplied and the image from Maseko et al (2013) shows a very similar appearance. There is no doubt that the authors are identifying structures that closely correspond to those provided by Maseko et al (2013). It is solely a contrast in what these nuclear complexes are called and the functional sequelae of the identification of these complexes (are they related to the trunk sensation or movement controlled by the cerebellum?) that is under debate.

Elephants are part of the Afrotheria, thus the most relevant comparative data to resolve this issue will be the identification of these nuclei in other Afrotherian species. Below I provide images of these nuclear complexes, labelled in the standard nomenclature, across several Afrotherian species.

(A) Lesser hedgehog tenrec (Echinops telfairi)

Tenrecs brains are the most intensively studied of the Afrotherian brains, these extensive neuroanatomical studies undertaken primarily by Heinz Künzle. Below I append images (coronal sections stained with cresol violet) of the IO and Vsens (labelled in the standard mammalian manner) in the lesser hedgehog tenrec. It should be clear that the inferior olive is located in the ventral midline of the rostral medulla oblongata (just like the rat) and that this nucleus is not distinctly serrated. The Vsens is located in the lateral aspect of the medulla skirted laterally by the spinal trigeminal tract (Sp5). These images and the labels indicating structures correlate precisely with that provide by Künzle (1997, 10.1016/S0168- 0102(97)00034-5), see his Figure 1K,L. Thus, in the first case of a related species, there is no serrated appearance of the inferior olive, the location of the inferior olive is confirmed through connectivity with the superior colliculus (a standard connection in mammals) by Künzle (1997), and the location of Vsens is what is considered to be typical for mammals. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 1.

(B) Giant otter shrew (Potomogale velox)

The otter shrews are close relatives of the Tenrecs. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see hints of the serration of the IO as defined by the authors, but we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 2.

(C) Four-toed sengi (Petrodromus tetradactylus)

The sengis are close relatives of the Tenrecs and otter shrews, these three groups being part of the Afroinsectiphilia, a distinct branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see vague hints of the serration of the IO (as defined by the authors), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 3.

(D) Rock hyrax (Procavia capensis)

The hyraxes, along with the sirens and elephants form the Paenungulata branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per the standard mammalian anatomy. Here we see hints of the serration of the IO (as defined by the authors), but we also see evidence of a more "bulbous" appearance of subnuclei of the IO (particularly the principal nucleus), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 4.

(E) West Indian manatee (Trichechus manatus)

The sirens are the closest extant relatives of the elephants in the Afrotheria. Below I append images of cresyl violet (top) and myelin (bottom) stained coronal sections (taken from the University of Wisconsin-Madison Brain Collection, https://brainmuseum.org, and while quite low in magnification they do reveal the structures under debate) through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see the serration of the IO (as defined by the authors). Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Review image 5.

These comparisons and the structural identification, with which the authors agree as they only distinguish the elephants from the other Afrotheria, demonstrate that the appearance of the IO can be quite variable across mammalian species, including those with a close phylogenetic affinity to the elephants. Not all mammal species possess a "serrated" appearance of the IO. Thus, it is more than just theoretically possible that the IO of the elephant appears as described prior to this study.

So what about elephants? Below I append a series of images from coronal sections through the African elephant brainstem stained for Nissl, myelin, and immunostained for calretinin. These sections are labelled according to standard mammalian nomenclature. In these complete sections of the elephant brainstem, we do not see a serrated appearance of the IOM (as described previously and in the current study by the authors). Rather the principal nucleus of the IOM appears to be bulbous in nature. In the current study, no image of myelin staining in the IOM/VsensR is provided by the authors. However, in the images I provide, we do see the reported myelin stripes in all stains - agreement between the authors and reviewer on this point. The higher magnification image to the bottom left of the plate shows one of the IOM/VsensR myelin stripes immunostained for calretinin, and within the myelin stripes axons immunopositive for calretinin are seen (labelled with an arrow). The climbing fibres of the elephant cerebellar cortex are similarly calretinin immunopositive (10.1159/000345565). In contrast, although not shown at high magnification, the fibres forming the Sp5 in the elephant (in the Maseko description, unnamed in the description of the authors) show no immunoreactivity to calretinin.

Review image 6.

Peripherin Immunostaining

In their revised manuscript the authors present immunostaining of peripherin in the elephant brainstem. This is an important addition (although it does replace the only staining of myelin provided by the authors which is unusual as the word myelin is in the title of the paper) as peripherin is known to specifically label peripheral nerves. In addition, as pointed out by the authors, peripherin also immunostains climbing fibres (Errante et al., 1998). The understanding of this staining is important in determining the identification of the IO and Vsens in the elephant, although it is not ideal for this task as there is some ambiguity. Errante and colleagues (1998; Fig. 1) show that climbing fibres are peripherin-immunopositive in the rat. But what the authors do not evaluate is the extensive peripherin staining in the rat Sp5 in the same paper (Errante et al, 1998, Fig. 2). The image provided by the authors of their peripherin immunostaining (their new Figure 2) shows what I would call the Sp5 of the elephant to be strongly peripherin immunoreactive, just like the rat shown in Errant et al (1998), and more over in the precise position of the rat Sp5! This makes sense as this is where the axons subserving the "extraordinary" tactile sensitivity of the elephant trunk would be found (in the standard model of mammalian brainstem anatomy). Interestingly, the peripherin immunostaining in the elephant is clearly lamellated...this coincides precisely with the description of the trigeminal sensory nuclei in the elephant by Maskeo et al (2013) as pointed out by the authors in their rebuttal. Errante et al (1998) also point out peripherin immunostaining in the inferior olive, but according to the authors this is only "weakly present" in the elephant IOM/VsensR. This latter point is crucial. Surely if the elephant has an extraordinary sensory innervation from the trunk, with 400 000 axons entering the brain, the VsensR/IOM should be highly peripherin-immunopositive, including the myelinated axon bundles?! In this sense, the authors argue against their own interpretation - either the elephant trunk is not a highly sensitive tactile organ, or the VsensR is not the trigeminal nuclei it is supposed to be.

Summary:

(1) Comparative data of species closely related to elephants (Afrotherians) demonstrates that not all mammals exhibit the "serrated" appearance of the principal nucleus of the inferior olive.

(2) The location of the IO and Vsens as reported in the current study (IOR and VsensR) would require a significant, and unprecedented, rearrangement of the brainstem in the elephants independently. I argue that the underlying molecular and genetic changes required to achieve this would be so extreme that it would lead to lethal phenotypes. Arguing that the "switcheroo" of the IO and Vsens does occur in the elephant (and no other mammals) and thus doesn't lead to lethal phenotypes is a circular argument that cannot be substantiated.

(3) Myelin stripes in the subnuclei of the inferior olivary nuclear complex are seen across all related mammals as shown above. Thus, the observation made in the elephant by the authors in what they call the VsensR, is similar to that seen in the IO of related mammals, especially when the IO takes on a more bulbous appearance. These myelin stripes are the origin of the olivocerebellar pathway, and are indeed calretinin immunopositive in the elephant as I show.

(4) What the authors see aligns perfectly with what has been described previously, the only difference being the names that nuclear complexes are being called. But identifying these nuclei is important, as any functional sequelae, as extensively discussed by the authors, is entirely dependent upon accurately identifying these nuclei.

(4) The peripherin immunostaining scores an own goal - if peripherin is marking peripheral nerves (as the authors and I believe it is), then why is the VsensR/IOM only "weakly positive" for this stain? This either means that the "extraordinary" tactile sensitivity of the elephant trunk is non-existent, or that the authors have misinterpreted this staining. That there is extensive staining in the fibre pathway dorsal and lateral to the IOR (which I call the spinal trigeminal tract), supports the idea that the authors have misinterpreted their peripherin immunostaining.

(5) Evolutionary expediency. The authors argue that what they report is an expedient way in which to modify the organisation of the brainstem in the elephant to accommodate the "extraordinary" tactile sensitivity. I disagree. As pointed out in my first review, the elephant cerebellum is very large and comprised of huge numbers of morphologically complex neurons. The inferior olivary nuclei in all mammals studied in detail to date, give rise to the climbing fibres that terminate on the Purkinje cells of the cerebellar cortex. It is more parsimonious to argue that, in alignment with the expansion of the elephant cerebellum (for motor control of the trunk), the inferior olivary nuclei (specifically the principal nucleus) have had additional neurons added to accommodate this cerebellar expansion. Such an addition of neurons to the principal nucleus of the inferior olive could readily lead to the loss of the serrated appearance of the principal nucleus of the inferior olive, and would require far less modifications in the developmental genetic program that forms these nuclei. This type of quantitative change appears to be the primary way in which structures are altered in the mammalian brainstem.

Author response:

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

We are thankful for the handling of our manuscript. The following is a summary of our response and what we have done:

(1) We are most thankful for the very thorough evaluation of our manuscript.

(2) We were a bit shocked by the very negative commentary of referee 2.

(3) We think, what put referee 2 off so much is that we were overconfident in the strength of our conclusions. We consider such overconfidence a big mistake. We have revised the manuscript to fix this problem.

(4) We respond in great depth to all criticism and also go into technicalities.

(5) We consider the possibility of a mistake. Yet, we carefully weighed the evidence advanced by referee 2 and by us and found that a systematic review supports our conclusions. Hence, we also resist the various attempts to crush our paper.

(6) We added evidence (peripherin-antibody staining; our novel Figure 2) that suggests we correctly identified the inferior olive.

(7) The eLife format – in which critical commentary is published along with the paper – is a fantastic venue to publish, what appears to be a surprisingly controversial issue.

eLife assessment

This potentially valuable study uses classic neuroanatomical techniques and synchrotron X-ray tomography to investigate the mapping of the trunk within the brainstem nuclei of the elephant brain. Given its unique specializations, understanding the somatosensory projections from the elephant trunk would be of general interest to evolutionary neurobiologists, comparative neuroscientists, and animal behavior scientists. However, the anatomical analysis is inadequate to support the authors' conclusion that they have identified the elephant trigeminal sensory nuclei rather than a different brain region, specifically the inferior olive.

Comment: We are happy that our paper is considered to be potentially valuable. Also, the editors highlight the potential interest of our work for evolutionary neurobiologists, comparative neuroscientists, and animal behavior scientists. The editors are more negative when it comes to our evidence on the identification of the trigeminal nucleus vs the inferior olive. We have five comments on this assessment. (i) We think this assessment is heavily biased by the comments of referee 2. We show that the referee’s comments are more about us than about our paper. Hence, the referee failed to do their job (refereeing our paper) and should not have succeeded in leveling our paper. (ii) We have no ad hoc knock-out experiments to distinguish the trigeminal nucleus vs the inferior olive. Such experiments (extracellular recording & electrolytic lesions, viral tracing would be done in a week in mice, but they cannot and should not be done in elephants. (iii) We have extraordinary evidence. Nobody has ever described a similarly astonishing match of body (trunk folds) and myeloarchitecture in the brain before. (iv) We show that our assignment of the trigeminal nucleus vs the inferior olive is more plausible than the current hypothesis about the assignment of the trigeminal nucleus vs the inferior olive as defended by referee 2. We think this is why it is important to publish our paper. (v) We think eLife is the perfect place for our publication because the deviating views of referee 2 are published along.

Change: We performed additional peripherin-antibody staining to differentiate the inferior olive and trigeminal nucleus. Peripherin is a cytoskeletal protein that is found in peripheral nerves and climbing fibers. Specifically, climbing fibers of various species (mouse, rabbit, pig, cow, and human; Errante et al., 1998) are stained intensely with peripherin-antibodies. What is tricky for our purposes is that there is also some peripherin-antibody reactivity in the trigeminal nuclei (Errante et al., 1998). Such peripherin-antibody reactivity is weaker, however, and lacks the distinct axonal bundle signature that stems from the strong climbing fiber peripherin-reactivity as seen in the inferior olive (Errante et al., 1998). As can be seen in our novel Figure 2, we observe peripherin-reactivity in axonal bundles (i.e. in putative climbing fibers), in what we think is the inferior olive. We also observe weak peripherin-reactivity, in what we think is the trigeminal nucleus, but not the distinct and strong labeling of axonal bundles. These observations are in line with our ideas but are difficult to reconcile with the views of the referee. Specifically, the lack of peripherin-reactive axon bundles suggests that there are no climbing fibers in what the referee thinks is the inferior olive.

Errante, L., Tang, D., Gardon, M., Sekerkova, G., Mugnaini, E., & Shaw, G. (1998). The intermediate filament protein peripherin is a marker for cerebellar climbing fibres. Journal of neurocytology, 27, 69-84.

Reviewer #1 :

Summary:

This fundamental study provides compelling neuroanatomical evidence underscoring the sensory function of the trunk in African and Asian elephants. Whereas myelinated tracts are classically appreciated as mediating neuronal connections, the authors speculate that myelinated bundles provide functional separation of trunk folds and display elaboration related to the "finger" projections. The authors avail themselves of many classical neuroanatomical techniques (including cytochrome oxidase stains, Golgi stains, and myelin stains) along with modern synchrotron X-ray tomography. This work will be of interest to evolutionary neurobiologists, comparative neuroscientists, and the general public, with its fascinating exploration of the brainstem of an icon sensory specialist. 

Comment: We are incredibly grateful for this positive assessment.

Changes: None.

Strengths: 

- The authors made excellent use of the precious sample materials from 9 captive elephants. 

- The authors adopt a battery of neuroanatomical techniques to comprehensively characterize the structure of the trigeminal subnuclei and properly re-examine the "inferior olive".

- Based on their exceptional histological preparation, the authors reveal broadly segregated patterns of metabolic activity, similar to the classical "barrel" organization related to rodent whiskers. 

Comment: The referee provides a concise summary of our findings.

Changes: None.

Weaknesses: 

- As the authors acknowledge, somewhat limited functional description can be provided using histological analysis (compared to more invasive techniques). 

- The correlation between myelinated stripes and trunk fold patterns is intriguing, and Figure 4 presents this idea beautifully. I wonder - is the number of stripes consistent with the number of trunk folds? Does this hold for both species? 

Comment: We agree with the referee’s assessment. We note that cytochrome-oxidase staining is an at least partially functional stain, as it reveals constitutive metabolic activity. A significant problem of the work in elephants is that our recording possibilities are limited, which in turn limits functional analysis. As indicated in Figure 5 (our former Figure 4) for the African elephant Indra, there was an excellent match of trunk folds and myelin stripes. Asian elephants have more, and less conspicuous trunk folds than African elephants. As illustrated in Figure 7, Asian elephants have more, and less conspicuous myelin stripes. Thus, species differences in myelin stripes correlate with species differences in trunk folds.

Changes: We clarify the relation of myelin stripe and trunk fold patterns in our description of Figure 7.

Reviewer #2 (Public Review): 

The authors describe what they assert to be a very unusual trigeminal nuclear complex in the brainstem of elephants, and based on this, follow with many speculations about how the trigeminal nuclear complex, as identified by them, might be organized in terms of the sensory capacity of the elephant trunk.

Comment: We agree with the referee’s assessment that the putative trigeminal nucleus described in our paper is highly unusual in size, position, vascularization, and myeloarchitecture. This is why we wrote this paper. We think these unusual features reflect the unique facial specializations of elephants, i.e. their highly derived trunk. Because we have no access to recordings from the elephant brainstem, we cannot back up all our functional interpretations with electrophysiological evidence; it is therefore fair to call them speculative.

Changes: None.

The identification of the trigeminal nuclear complex/inferior olivary nuclear complex in the elephant brainstem is the central pillar of this manuscript from which everything else follows, and if this is incorrect, then the entire manuscript fails, and all the associated speculations become completely unsupported. 

Comment: We agree.

Changes: None.

The authors note that what they identify as the trigeminal nuclear complex has been identified as the inferior olivary nuclear complex by other authors, citing Shoshani et al. (2006; 10.1016/j.brainresbull.2006.03.016) and Maseko et al (2013; 10.1159/000352004), but fail to cite either Verhaart and Kramer (1958; PMID 13841799) or Verhaart (1962; 10.1515/9783112519882-001). These four studies are in agreement, but the current study differs.

Comment & Change: We were not aware of the papers of Verhaart and included them in the revised manusript.

Let's assume for the moment that the four previous studies are all incorrect and the current study is correct. This would mean that the entire architecture and organization of the elephant brainstem is significantly rearranged in comparison to ALL other mammals, including humans, previously studied (e.g. Kappers et al. 1965, The Comparative Anatomy of the Nervous System of Vertebrates, Including Man, Volume 1 pp. 668-695) and the closely related manatee (10.1002/ar.20573). This rearrangement necessitates that the trigeminal nuclei would have had to "migrate" and shorten rostrocaudally, specifically and only, from the lateral aspect of the brainstem where these nuclei extend from the pons through to the cervical spinal cord (e.g. the Paxinos and Watson rat brain atlases), the to the spatially restricted ventromedial region of specifically and only the rostral medulla oblongata. According to the current paper, the inferior olivary complex of the elephant is very small and located lateral to their trigeminal nuclear complex, and the region from where the trigeminal nuclei are located by others appears to be just "lateral nuclei" with no suggestion of what might be there instead.

Comment: We have three comments here:

(1) The referee correctly notes that we argue the elephant brainstem underwent fairly major rearrangements. In particular, we argue that the elephant inferior olive was displaced laterally, by a very large cell mass, which we argue is an unusually large trigeminal nucleus. To our knowledge, such a large compact cell mass is not seen in the ventral brain stem of any other mammal.

(2) The referee makes it sound as if it is our private idea that the elephant brainstem underwent major rearrangements and that the rest of the evidence points to a conventional ‘rodent-like’ architecture. This is far from the truth, however. Already from the outside appearance (see our Figure 1B and Figure 7A) it is clear that the elephant brainstem has huge ventral bumps not seen in any other mammal. An extraordinary architecture also holds at the organizational level of nuclei. Specifically, the facial nucleus – the most carefully investigated nucleus in the elephant brainstem – has an appearance distinct from that of the facial nuclei of all other mammals (Maseko et al., 2013; Kaufmann et al., 2022). If both the overall shape and the constituting nuclei of the brainstem are very different from other mammals, it is very unlikely if not impossible that the elephant brainstem follows in all regards a conventional ‘rodent-like’ architecture.

(3) The inferior olive is an impressive nucleus in the partitioning scheme we propose (Figure 2). In fact – together with the putative trigeminal nucleus we describe – it’s the most distinctive nucleus in the elephant brainstem. We have not done volumetric measurements and cell counts here, but think this is an important direction for future work. What has informed our work is that the inferior olive nucleus we describe has the serrated organization seen in the inferior olive of all mammals. We will discuss these matters in depth below.

Changes: None.

Such an extraordinary rearrangement of brainstem nuclei would require a major transformation in the manner in which the mutations, patterning, and expression of genes and associated molecules during development occur. Such a major change is likely to lead to lethal phenotypes, making such a transformation extremely unlikely. Variations in mammalian brainstem anatomy are most commonly associated with quantitative changes rather than qualitative changes (10.1016/B978-0-12-804042-3.00045-2). 

Comment: We have two comments here:

(1) The referee claims that it is impossible that the elephant brainstem differs from a conventional brainstem architecture because this would lead to lethal phenotypes etc. Following our previous response, this argument does not hold. It is out of the question that the elephant brainstem looks very different from the brainstem of other mammals. Yet, it is also evident that elephants live. The debate we need to have is not if the elephant brainstem differs from other mammals, but how it differs from other mammals.

(2) In principle we agree with the referee’s thinking that the model of the elephant brainstem that is most likely to be correct is the one that requires the least amount of rearrangements to other mammals. We therefore prepared a comparison of the model the referee is proposing (Maseko et al., 2013; see Referee Table 1 below) with our proposition. We scored these models on their similarity to other mammals. We find that the referee’s ideas (Maseko et al., 2013) require more rearrangements relative to other mammals than our suggestion.

Changes: Inclusion of Referee Table 1, which we discuss in depth below.

The impetus for the identification of the unusual brainstem trigeminal nuclei in the current study rests upon a previous study from the same laboratory (10.1016/j.cub.2021.12.051) that estimated that the number of axons contained in the infraorbital branch of the trigeminal nerve that innervate the sensory surfaces of the trunk is approximately 400 000. Is this number unusual? In a much smaller mammal with a highly specialized trigeminal system, the platypus, the number of axons innervating the sensory surface of the platypus bill skin comes to 1 344 000 (10.1159. Yet, there is no complex rearrangement of the brainstem trigeminal nuclei in the brain of the developing or adult platypus (Ashwell, 2013, Neurobiology of Monotremes), despite the brainstem trigeminal nuclei being very large in the platypus (10.1159/000067195). Even in other large-brained mammals, such as large whales that do not have a trunk, the number of axons in the trigeminal nerve ranges between 400,000 and 500,000 (10.1007. The lack of comparative support for the argument forwarded in the previous and current study from this laboratory, and that the comparative data indicates that the brainstem nuclei do not change in the manner suggested in the elephant, argues against the identification of the trigeminal nuclei as outlined in the current study. Moreover, the comparative studies undermine the prior claim of the authors, informing the current study, that "the elephant trigeminal ganglion ... point to a high degree of tactile specialization in elephants" (10.1016/j.cub.2021.12.051). While clearly, the elephant has tactile sensitivity in the trunk, it is questionable as to whether what has been observed in elephants is indeed "truly extraordinary".

Comment: These comments made us think that the referee is not talking about the paper we submitted, but that the referee is talking about us and our work in general. Specifically, the referee refers to the platypus and other animals dismissing our earlier work, which argued for a high degree of tactile specialization in elephants. We think the referee’s intuitions are wrong and our earlier work is valid.

Changes: We prepared a Author response image 1 (below) that puts the platypus brain, a monkey brain, and the elephant trigeminal ganglion (which contains a large part of the trunk innervating cells) in perspective.

Author response image 1.

The elephant trigeminal ganglion is comparatively large. Platypus brain, monkey brain, and elephant ganglion. The elephant has two trigeminal ganglia, which contain the first-order somatosensory neurons. They serve mainly for tactile processing and are large compared to a platypus brain (from the comparative brain collection) and are similar in size to a monkey brain. The idea that elephants might be highly specialized for trunk touch is also supported by the analysis of the sensory nerves of these animals (Purkart et al., 2022). Specifically, we find that the infraorbital nerve (which innervates the trunk) is much thicker than the optic nerve (which mediates vision) and the vestibulocochlear nerve (which mediates hearing). Thus, not everything is large about elephants; instead, the data argue that these animals are heavily specialized for trunk touch.

But let's look more specifically at the justification outlined in the current study to support their identification of the unusually located trigeminal sensory nuclei of the brainstem. 

(1) Intense cytochrome oxidase reactivity.

(2) Large size of the putative trunk module.

(3) Elongation of the putative trunk module.

(4) The arrangement of these putative modules corresponds to elephant head

anatomy. 

(5) Myelin stripes within the putative trunk module that apparently match trunk folds. <br /> (6) Location apparently matches other mammals.

(7) Repetitive modular organization apparently similar to other mammals. <br /> (8) The inferior olive described by other authors lacks the lamellated appearance of this structure in other mammals.

Comment: We agree those are key issues.

Changes: None.

Let's examine these justifications more closely.

(1) Cytochrome oxidase histochemistry is typically used as an indicative marker of neuronal energy metabolism. The authors indicate, based on the "truly extraordinary" somatosensory capacities of the elephant trunk, that any nuclei processing this tactile information should be highly metabolically active, and thus should react intensely when stained for cytochrome oxidase. We are told in the methods section that the protocols used are described by Purkart et al (2022) and Kaufmann et al (2022). In neither of these cited papers is there any description, nor mention, of the cytochrome oxidase histochemistry methodology, thus we have no idea of how this histochemical staining was done. To obtain the best results for cytochrome oxidase histochemistry, the tissue is either processed very rapidly after buffer perfusion to remove blood or in recently perfusion-fixed tissue (e.g., 10.1016/0165-0270(93)90122-8). Given: (1) the presumably long post-mortem interval between death and fixation - "it often takes days to dissect elephants"; (2) subsequent fixation of the brains in 4% paraformaldehyde for "several weeks"; (3) The intense cytochrome oxidase reactivity in the inferior olivary complex of the laboratory rat (Gonzalez-Lima, 1998, Cytochrome oxidase in neuronal metabolism and Alzheimer's diseases); and (4) The lack of any comparative images from other stained portions of the elephant brainstem; it is difficult to support the justification as forwarded by the authors. The histochemical staining observed is likely background reactivity from the use of diaminobenzidine in the staining protocol. Thus, this first justification is unsupported. 

Comment: The referee correctly notes the description of our cytochrome-oxidase reactivity staining was lacking. This is a serious mistake of ours for which we apologize very much. The referee then makes it sound as if we messed up our cytochrome-oxidase staining, which is not the case. All successful (n = 3; please see our technical comments in the recommendation section) cytochrome-oxidase stainings were done with elephants with short post-mortem times (≤ 2 days) to brain removal/cooling and only brief immersion fixation (≤ 1 day). Cytochrome-oxidase reactivity in elephant brains appears to be more sensitive to quenching by fixation than is the case for rodent brains. We think it is a good idea to include a cytochrome-oxidase staining overview picture because we understood from the referee’s comments that we need to compare our partitioning scheme of the brainstem with that of other authors. To this end, we add a cytochrome-oxidase staining overview picture (Author response image 3) along with an alternative interpretation from Maseko et al., 2013.

Changes: (1) We added details on our cytochrome-oxidase reactivity staining protocol and the cytochrome-oxidase reactivity in the elephant brain in the manuscript and in our response to the general recommendations.

(2) We provide a detailed discussion of the technicalities of cytochrome-oxidase staining below in the recommendation section, where the referee raised further criticisms.

(3) We include a cytochrome-oxidase staining overview picture (Author response image 2) along with an alternative interpretation from Maseko et al., 2013.

Author response image 2.

Cytochrome-oxidase staining overview. Coronal cytochrome-oxidase staining overview from African elephant cow Indra; the section is taken a few millimeters posterior to the facial nucleus. Brown is putatively neural cytochrome-reactivity, and white is the background. Black is myelin diffraction and (seen at higher resolution, when you zoom in) erythrocyte cytochrome-reactivity in blood vessels (see our Figure 1E-G); such blood vessel cytochrome-reactivity is seen, because we could not perfuse the animal. There appears to be a minimal outside-in-fixation artifact (i.e. a more whitish/non-brownish appearance of the section toward the borders of the brain). This artifact is not seen in sections from Indra that we processed earlier or in other elephant brains processed at shorter post-mortem/fixation delays (see our Figure 1C).

The same structures can be recognized in Author response image 2 and Supplememntary figure 36 of Maseko et al. (2013). The section is taken at an anterior-posterior level, where we encounter the trigeminal nuclei in pretty much all mammals. Note that the neural cytochrome reactivity is very high, in what we refer to as the trigeminal-nuclei-trunk-module and what Maseko et al. refer to as inferior olive. Myelin stripes can be recognized here as white omissions.

At the same time, the cytochrome-oxidase-reactivity is very low in what Maseko et al. refer to as trigeminal nuclei. The indistinct appearance and low cytochrome-oxidase-reactivity of the trigeminal nuclei in the scheme of Maseko et al. (2013) is unexpected because trigeminal nuclei stain intensely for cytochrome-oxidase-reactivity in most mammals and because the trigeminal nuclei represent the elephant’s most important body part, the trunk. Staining patterns of the trigeminal nuclei as identified by Maseko et al. (2013) are very different at more posterior levels; we will discuss this matter below.

Justifications (2), (3), and (4) are sequelae from justification (1). In this sense, they do not count as justifications, but rather unsupported extensions. 

Comment: These are key points of our paper that the referee does not discuss.

Changes: None.

(4) and (5) These are interesting justifications, as the paper has clear internal contradictions, and (5) is a sequelae of (4). The reader is led to the concept that the myelin tracts divide the nuclei into sub-modules that match the folding of the skin on the elephant trunk. One would then readily presume that these myelin tracts are in the incoming sensory axons from the trigeminal nerve. However, the authors note that this is not the case: "Our observations on trunk module myelin stripes are at odds with this view of myelin. Specifically, myelin stripes show no tapering (which we would expect if axons divert off into the tissue). More than that, there is no correlation between myelin stripe thickness (which presumably correlates with axon numbers) and trigeminal module neuron numbers. Thus, there are numerous myelinated axons, where we observe few or no trigeminal neurons. These observations are incompatible with the idea that myelin stripes form an axonal 'supply' system or that their prime function is to connect neurons. What do myelin stripe axons do, if they do not connect neurons? We suggest that myelin stripes serve to separate rather than connect neurons." So, we are left with the observation that the myelin stripes do not pass afferent trigeminal sensory information from the "truly extraordinary" trunk skin somatic sensory system, and rather function as units that separate neurons - but to what end? It appears that the myelin stripes are more likely to be efferent axonal bundles leaving the nuclei (to form the olivocerebellar tract). This justification is unsupported.

Comment: The referee cites some of our observations on myelin stripes, which we find unusual. We stand by the observations and comments. The referee does not discuss the most crucial finding we report on myelin stripes, namely that they correspond remarkably well to trunk folds.

Changes: None.

(6) The authors indicate that the location of these nuclei matches that of the trigeminal nuclei in other mammals. This is not supported in any way. In ALL other mammals in which the trigeminal nuclei of the brainstem have been reported they are found in the lateral aspect of the brainstem, bordered laterally by the spinal trigeminal tract. This is most readily seen and accessible in the Paxinos and Watson rat brain atlases. The authors indicate that the trigeminal nuclei are medial to the facial nerve nucleus, but in every other species, the trigeminal sensory nuclei are found lateral to the facial nerve nucleus. This is most salient when examining a close relative, the manatee (10.1002/ar.20573), where the location of the inferior olive and the trigeminal nuclei matches that described by Maseko et al (2013) for the African elephant. This justification is not supported. 

Comment: The referee notes that we incorrectly state that the position of the trigeminal nuclei matches that of other mammals. We think this criticism is justified.

Changes: We prepared a comparison of the Maseko et al. (2013) scheme of the elephant brainstem with our scheme of the elephant brainstem (see below Referee Table 1). Here we acknowledge the referee’s argument and we also changed the manuscript accordingly.

(7) The dual to quadruple repetition of rostrocaudal modules within the putative trigeminal nucleus as identified by the authors relies on the fact that in the neurotypical mammal, there are several trigeminal sensory nuclei arranged in a column running from the pons to the cervical spinal cord, these include (nomenclature from Paxinos and Watson in roughly rostral to caudal order) the Pr5VL, Pr5DM, Sp5O, Sp5I, and Sp5C. However, these nuclei are all located far from the midline and lateral to the facial nerve nucleus, unlike what the authors describe in the elephants. These rostrocaudal modules are expanded upon in Figure 2, and it is apparent from what is shown that the authors are attributing other brainstem nuclei to the putative trigeminal nuclei to confirm their conclusion. For example, what they identify as the inferior olive in Figure 2D is likely the lateral reticular nucleus as identified by Maseko et al (2013). This justification is not supported.

Comment: The referee again compares our findings to the scheme of Maseko et al. (2013) and rejects our conclusions on those grounds. We think such a comparison of our scheme is needed, indeed.

Changes: We prepared a comparison of the Maseko et al. (2013) scheme of the elephant brainstem with our scheme of the elephant brainstem (see below Referee Table 1).

(8) In primates and related species, there is a distinct banded appearance of the inferior olive, but what has been termed the inferior olive in the elephant by other authors does not have this appearance, rather, and specifically, the largest nuclear mass in the region (termed the principal nucleus of the inferior olive by Maseko et al, 2013, but Pr5, the principal trigeminal nucleus in the current paper) overshadows the partial banded appearance of the remaining nuclei in the region (but also drawn by the authors of the current paper). Thus, what is at debate here is whether the principal nucleus of the inferior olive can take on a nuclear shape rather than evince a banded appearance. The authors of this paper use this variance as justification that this cluster of nuclei could not possibly be the inferior olive. Such a "semi-nuclear/banded" arrangement of the inferior olive is seen in, for example, giraffe (10.1016/j.jchemneu.2007.05.003), domestic dog, polar bear, and most specifically the manatee (a close relative of the elephant) (brainmuseum.org; 10.1002/ar.20573). This justification is not supported. 

Comment: We carefully looked at the brain sections referred to by the referee in the brainmuseum.org collection. We found contrary to the referee’s claims that dogs, polar bears, and manatees have a perfectly serrated (a cellular arrangement in curved bands) appearance of the inferior olive. Accordingly, we think the referee is not reporting the comparative evidence fairly and we wonder why this is the case.

Changes: None.

Thus, all the justifications forwarded by the authors are unsupported. Based on methodological concerns, prior comparative mammalian neuroanatomy, and prior studies in the elephant and closely related species, the authors fail to support their notion that what was previously termed the inferior olive in the elephant is actually the trigeminal sensory nuclei. Given this failure, the justifications provided above that are sequelae also fail. In this sense, the entire manuscript and all the sequelae are not supported.

Comment: We disagree. To summarize:

(1) Our description of the cytochrome oxidase staining lacked methodological detail, which we have now added; the cytochrome oxidase reactivity data are great and support our conclusions.

(2)–(5)The referee does not really discuss our evidence on these points.

(6) We were wrong and have now fixed this mistake.

(7) The referee asks for a comparison to the Maseko et al. (2013) scheme (agreed, see Referee Table 1).

(8) The referee bends the comparative evidence against us.

Changes: None.

A comparison of the elephant brainstem partitioning schemes put forward by Maseko et al 2013 and by Reveyaz et al.

To start with, we would like to express our admiration for the work of Maseko et al. (2013). These authors did pioneering work on obtaining high-quality histology samples from elephants. Moreover, they made a heroic neuroanatomical effort, in which they assigned 147 brain structures to putative anatomical entities. Most of their data appear to refer to staining in a single elephant and one coronal sectioning plane. The data quality and the illustration of results are excellent.

We studied mainly two large nuclei in six (now 7) elephants in three (coronal, parasagittal, and horizontal) sectioning planes. The two nuclei in question are the two most distinct nuclei in the elephant brainstem, namely an anterior ventromedial nucleus (the trigeminal trunk module in our terminology; the inferior olive in the terminology of Maseko et al., 2013) and a more posterior lateral nucleus (the inferior olive in our terminology; the posterior part of the trigeminal nuclei in the terminology of Maseko et al., 2013).

Author response image 3 gives an overview of the two partitioning schemes for inferior olive/trigeminal nuclei along with the rodent organization (see below).

Author response image 3.

Overview of the brainstem organization in rodents & elephants

The strength of the Maseko et al. (2013) scheme is the excellent match of the position of elephant nuclei to the position of nuclei in the rodent (Author response image 3). We think this positional match reflects the fact that Maseko et al. (2013) mapped a rodent partitioning scheme on the elephant brainstem. To us, this is a perfectly reasonable mapping approach. As the referee correctly points out, the positional similarity of both elephant inferior olive and trigeminal nuclei to the rodent strongly argues in favor of the Maseko et al. (2013), because brainstem nuclei are positionally very conservative.

Other features of the Maseko et al. (2013) scheme are less favorable. The scheme marries two cyto-architectonically very distinct divisions (an anterior indistinct part) and a super-distinct serrated posterior part to be the trigeminal nuclei. We think merging entirely distinct subdivisions into one nucleus is a byproduct of mapping a rodent partitioning scheme on the elephant brainstem. Neither of the two subdivisions resemble the trigeminal nuclei of other mammals. The cytochrome oxidase staining patterns differ markedly across the anterior indistinct part (see our Author response image 3) and the posterior part of the trigeminal nuclei and do not match with the intense cytochrome oxidase reactivity of other mammalian trigeminal nuclei (Author response image 2). Our anti-peripherin staining (the novel Figure 2 of our manuscript) indicates that there probably no climbing fibers, in what Maseko et al. think. is inferior olive; this is a potentially fatal problem for the hypothesis. The posterior part of Maseko et al. (2013) trigeminal nuclei has a distinct serrated appearance that is characteristic of the inferior olive in other mammals. Moreover, the inferior olive of Maseko et al. (2013) lacks the serrated appearance of the inferior olive seen in pretty much all mammals; this is a serious problem.

The partitioning scheme of Reveyaz et al. comes with poor positional similarity but avoids the other problems of the Maseko et al. (2013) scheme. Our explanation for the positionally deviating location of trigeminal nuclei is that the elephant grew one of the if not the largest trigeminal systems of all mammals. As a result, the trigeminal nuclei grew through the floor of the brainstem. We understand this is a post hoc just-so explanation, but at least it is an explanation.

The scheme of Reveyaz et al. was derived in an entirely different way from the Maseko model. Specifically, we were convinced that the elephant trigeminal nuclei ought to be very special because of the gigantic trigeminal ganglia (Purkart et al., 2022). Cytochrome-oxidase staining revealed a large distinct nucleus with an elongated shape. Initially, we were freaked out by the position of the nucleus and the fact that it was referred to as inferior olive by other authors. When we found an inferior-olive-like nucleus at a nearby (although at an admittedly unusual) location, we were less worried. We then optimized the visualization of myelin stripes (brightfield imaging etc.) and were able to collect an entire elephant trunk along with the brain (African elephant cow Indra). When we made the one-to-one match of Indra’s trunk folds and myelin stripes (former Figure 4, now Figure 5) we were certain that we had identified the trunk module of the trigeminal nuclei. We already noted at the outset of our rebuttal that we now consider such certainty a fallacy of overconfidence. In light of the comments of Referee 2, we feel that a further discussion of our ideas is warranted.

A strength of the Reveyaz model is that nuclei look like single anatomical entities. The trigeminal nuclei look like trigeminal nuclei of other mammals, the trunk module has a striking resemblance to the trunk and the inferior olive looks like the inferior olive of other mammals.

We evaluated the fit of the two models in the form of a table (Author response table 1; below). Unsurprisingly, Author response table 1 aligns with our views of elephant brainstem partitioning.

Author response table 1

Qualitative evaluation of elephant brainstem partitioning schemes

++ = Very attractive; + = attractive; - = unattractive; -- = very unattractive

We scored features that are clear and shared by all mammals – as far as we know them – as very attractive.

We scored features that are clear and are not shared by all mammals – as far as we know them – as very unattractive.

Attractive features are either less clear or less well-shared features.

Unattractive features are either less clear or less clearly not shared features.

Author response table 1 suggests two conclusions to us. (i) The Reveyaz et al. model has mainly favorable properties. The Maseko et al. (2013) model has mainly unfavorable properties. Hence, the Reveyaz et al. model is more likely to be true. (ii) The outcome is not black and white, i.e., both models have favorable and unfavorable properties. Accordingly, we overstated our case in our initial submission and toned down our claims in the revised manuscript.

What the authors have not done is to trace the pathway of the large trigeminal nerve in the elephant brainstem, as was done by Maseko et al (2013), which clearly shows the internal pathways of this nerve, from the branch that leads to the fifth mesencephalic nucleus adjacent to the periventricular grey matter, through to the spinal trigeminal tract that extends from the pons to the spinal cord in a manner very similar to all other mammals. Nor have they shown how the supposed trigeminal information reaches the putative trigeminal nuclei in the ventromedial rostral medulla oblongata. These are but two examples of many specific lines of evidence that would be required to support their conclusions. Clearly, tract tracing methods, such as cholera toxin tracing of peripheral nerves cannot be done in elephants, thus the neuroanatomy must be done properly and with attention to detail to support the major changes indicated by the authors. 

Comment: The referee claims that Maseko et al. (2013) showed by ‘tract tracing’ that the structures they refer to trigeminal nuclei receive trigeminal input. This statement is at least slightly misleading. There is nothing of what amounts to proper ‘tract tracing’ in the Maseko et al. (2013) paper, i.e. tracing of tracts with post-mortem tracers. We tried proper post-mortem tracing but failed (no tracer transport) probably as a result of the limitations of our elephant material. What Maseko et al. (2013) actually did is look a bit for putative trigeminal fibers and where they might go. We also used this approach. In our hands, such ‘pseudo tract tracing’ works best in unstained material under bright field illumination, because myelin is very well visualized. In such material, we find: (i) massive fiber tracts descending dorsoventrally roughly from where both Maseko et al. 2013 and we think the trigeminal tract runs. (ii) These fiber tracts run dorsoventrally and approach, what we think is the trigeminal nuclei from lateral.

Changes: Ad hoc tract tracing see above.

So what are these "bumps" in the elephant brainstem? 

Four previous authors indicate that these bumps are the inferior olivary nuclear complex. Can this be supported?

The inferior olivary nuclear complex acts "as a relay station between the spinal cord (n.b. trigeminal input does reach the spinal cord via the spinal trigeminal tract) and the cerebellum, integrating motor and sensory information to provide feedback and training to cerebellar neurons" (https://www.ncbi.nlm.nih.gov/books/NBK542242/). The inferior olivary nuclear complex is located dorsal and medial to the pyramidal tracts (which were not labeled in the current study by the authors but are clearly present in Fig. 1C and 2A) in the ventromedial aspect of the rostral medulla oblongata. This is precisely where previous authors have identified the inferior olivary nuclear complex and what the current authors assign to their putative trigeminal nuclei. The neurons of the inferior olivary nuclei project, via the olivocerebellar tract to the cerebellum to terminate in the climbing fibres of the cerebellar cortex.

Comment: We agree with the referee that in the Maseko et al. (2013) scheme the inferior olive is exactly where we expect it from pretty much all other mammals. Hence, this is a strong argument in favor of the Maseko et al. (2013) scheme and a strong argument against the partitioning scheme suggested by us.

Changes: Please see our discussion above.

Elephants have the largest (relative and absolute) cerebellum of all mammals (10.1002/ar.22425), this cerebellum contains 257 x109 neurons (10.3389/fnana.2014.00046; three times more than the entire human brain, 10.3389/neuro.09.031.2009). Each of these neurons appears to be more structurally complex than the homologous neurons in other mammals (10.1159/000345565; 10.1007/s00429-010-0288-3). In the African elephant, the neurons of the inferior olivary nuclear complex are described by Maseko et al (2013) as being both calbindin and calretinin immunoreactive. Climbing fibres in the cerebellar cortex of the African elephant are clearly calretinin immunopositive and also are likely to contain calbindin (10.1159/000345565). Given this, would it be surprising that the inferior olivary nuclear complex of the elephant is enlarged enough to create a very distinct bump in exactly the same place where these nuclei are identified in other mammals? 

Comment: We agree with the referee that it is possible and even expected from other mammals that there is an enlargement of the inferior olive in elephants. Hence, a priori one might expect the ventral brain stem bumps to the inferior olive, this is perfectly reasonable and is what was done by previous authors. The referee also refers to calbindin and calretinin antibody reactivity. Such antibody reactivity is indeed in line with the referee’s ideas and we considered these findings in our Referee Table 1. The problem is, however, that neither calbindin nor calretinin antibody reactivity are highly specific and indeed both nuclei in discussion (trigeminal nuclei and inferior olive) show such reactivity. Unlike the peripherin-antibody staining advanced by us, calbindin nor calretinin antibody reactivity cannot distinguish the two hypotheses debated.

Changes: Please see our discussion above.

What about the myelin stripes? These are most likely to be the origin of the olivocerebellar tract and probably only have a coincidental relationship with the trunk. Thus, given what we know, the inferior olivary nuclear complex as described in other studies, and the putative trigeminal nuclear complex as described in the current study, is the elephant inferior olivary nuclear complex. It is not what the authors believe it to be, and they do not provide any evidence that discounts the previous studies. The authors are quite simply put, wrong. All the speculations that flow from this major neuroanatomical error are therefore science fiction rather than useful additions to the scientific literature. 

Comment: It is unlikely that the myelin stripes are the origin of the olivocerebellar tract as suggested by the referee. Specifically, the lack of peripherin-reactivity indicates that these fibers are not climbing fibers (our novel Figure 2). In general, we feel the referee does not want to discuss the myelin stripes and obviously thinks we made up the strange correspondence of myelin stripes and trunk folds.

Changes: Please see our discussion above.

What do the authors actually have? 

The authors have interesting data, based on their Golgi staining and analysis, of the inferior olivary nuclear complex in the elephant.

Comment: The referee reiterates their views.

Changes: None.

Reviewer #3 (Public Review):

Summary: 

The study claims to investigate trunk representations in elephant trigeminal nuclei located in the brainstem. The researchers identified large protrusions visible from the ventral surface of the brainstem, which they examined using a range of histological methods. However, this ventral location is usually where the inferior olivary complex is found, which challenges the author's assertions about the nucleus under analysis. They find that this brainstem nucleus of elephants contains repeating modules, with a focus on the anterior and largest unit which they define as the putative nucleus principalis trunk module of the trigeminal. The nucleus exhibits low neuron density, with glia outnumbering neurons significantly. The study also utilizes synchrotron X-ray phase contrast tomography to suggest that myelin-stripe-axons traverse this module. The analysis maps myelin-rich stripes in several specimens and concludes that based on their number and patterning they likely correspond with trunk folds; however, this conclusion is not well supported if the nucleus has been misidentified.

Comment: The referee gives a concise summary of our findings. The referee acknowledges the depth of our analysis and also notes our cellular results. The referee – in line with the comments of Referee 2 – also points out that a misidentification of the nucleus under study is potentially fatal for our analysis. We thank the referee for this fair assessment.

Changes: We feel that we need to alert the reader more broadly to the misidentification concern. We think the critical comments of Referee 2, which will be published along with our manuscript, will go a long way in doing so. We think the eLife publishing format is fantastic in this regard. We will also include pointers to these concerns in the revised manuscript.

Strengths: 

The strength of this research lies in its comprehensive use of various anatomical methods, including Nissl staining, myelin staining, Golgi staining, cytochrome oxidase labeling, and synchrotron X-ray phase contrast tomography. The inclusion of quantitative data on cell numbers and sizes, dendritic orientation and morphology, and blood vessel density across the nucleus adds a quantitative dimension. Furthermore, the research is commendable for its high-quality and abundant images and figures, effectively illustrating the anatomy under investigation.

Comment: Again, a very fair and balanced set of comments. We are thankful for these comments.

Changes: None.

Weaknesses: 

While the research provides potentially valuable insights if revised to focus on the structure that appears to be the inferior olivary nucleus, there are certain additional weaknesses that warrant further consideration. First, the suggestion that myelin stripes solely serve to separate sensory or motor modules rather than functioning as an "axonal supply system" lacks substantial support due to the absence of information about the neuronal origins and the termination targets of the axons. Postmortem fixed brain tissue limits the ability to trace full axon projections. While the study acknowledges these limitations, it is important to exercise caution in drawing conclusions about the precise role of myelin stripes without a more comprehensive understanding of their neural connections.

Comment: The referee points out a significant weakness of our study, namely our limited understanding of the origin and targets of the axons constituting the myelin stripes. We are very much aware of this problem and this is also why we directed high-powered methodology like synchrotron X-ray tomograms to elucidate the structure of myelin stripes. Such analysis led to advances, i.e., we now think, what looks like stripes are bundles and we understand the constituting axons tend to transverse the module. Such advances are insufficient, however, to provide a clear picture of myelin stripe connectivity.

Changes: We think solving the problems raised by the referee will require long-term methodological advances and hence we will not be able to solve these problems in the current revision. Our long-term plans for confronting these issues are the following: (i) Improving our understanding of long-range connectivity by post-mortem tracing and MR-based techniques such as Diffusion-Tensor-Imaging. (ii) Improving our understanding of mid and short-range connectivity by applying even larger synchrotron X-ray tomograms and possible serial EM.

Second, the quantification presented in the study lacks comparison to other species or other relevant variables within the elephant specimens (i.e., whole brain or brainstem volume). The absence of comparative data for different species limits the ability to fully evaluate the significance of the findings. Comparative analyses could provide a broader context for understanding whether the observed features are unique to elephants or more common across species. This limitation in comparative data hinders a more comprehensive assessment of the implications of the research within the broader field of neuroanatomy. Furthermore, the quantitative comparisons between African and Asian elephant specimens should include some measure of overall brain size as a covariate in the analyses. Addressing these weaknesses would enable a richer interpretation of the study's findings.

Comment: The referee suggests another series of topics, which include the analysis of brain parts volumes or overall brain size. We agree these are important issues, but we also think such questions are beyond the scope of our study.

Changes: We hope to publish comparative data on elephant brain size and shape later this year.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I realize that elephant brains are a limiting resource in this project, along with the ability to perform functional investigations. However, I believe that Prof. Jon Kaas (Vanderbilt University) has one or more series of Nissl-stained brainstems from elephants. These might be of potential interest, as they were previously used to explore general patterns of trigeminal brainstem organization in a comparative manner (see Sawyer and Sarko, 2017, "Comparative Anatomy and Evolution of the Somatosensory Brain Stem" in the Evolution of Nervous System series) and might shed light on the positioning of the trigeminal complex and IO, with parts of the trigeminal nerve itself still attached to these sections.

Comment: The referee suggests adding data from more elephants and we think this is a great suggestion because our ns are small. We followed this advice. We agree we need more comparative neuroanatomy of elephants and the urgency of this matter is palpable in the heated debate we have with Referee 2. Specifically, we need more long-range and short-range analysis of elephant brains.

Changes: We plan to include data in the revised manuscript about cytoarchitectonics (Nissl), cytochrome-oxidase reactivity, and possibly also antibody reactivity from an additional animal, i.e., from the African elephant cow Bibi. The quality of this specimen is excellent and the post-mortem time to brain extraction was very short.

We also have further plans for connectivity analysis (see our response above), but such data will not become available fast enough for the revision.

Other recommendations: 

- A general schematic showing input from trunk to PrV to the trigeminal subnuclei (as well as possibly ascending connections) might be informative to the reader, in terms of showing which neural relay is being examined.

Comment: We think this is a very good suggestion in principle, but we were not satisfied with the schematics we came up with.

Changes: None.

- Perhaps a few more sentences described the significance of synchrotron tomography for those who may be unfamiliar.

Comment & Change: We agree and implement this suggestion.

- "Belly-shaped" trunk module description is unclear on page 9. 

Comment & Change: We clarified this matter.

- Typo on the last sentence of page 9. 

Comment & Change: We fixed this mistake.

Reviewer #2 (Recommendations For The Authors): 

The data is only appropriate a specialized journal and is limited to the Golgi analysis of neurons within the inferior olivary complex of the elephant. This reviewer considers that the remainder of the work is speculation and that the paper in its current version is not salvageable.

Comment: Rather than suggesting changes, the referee makes it clear that the referee does not want to see our paper published. We think this desire to reject is not rooted in a lack of quality of our work. In fact, we did an immense amount of work (detailed cytoarchitectonic analysis of six (now seven) elephant brainstems rather than one as in the case of our predecessors), cell counts, and X-ray tomography. Instead, we think the problem is rooted in the fact that we contradict the referee. To us, such suppression of diverging opinions – provided they are backed up with data – is a scientifically deeply unhealthy attitude. Science lives from the debate and this is why we did not exclude any referees even though we knew that our results do not align with the views of all of the few actors in the field.

Changes: We think the novel eLife publishing scheme was developed to prevent such abuse. We look forward to having our data published along with the harsh comments of the referee. The readers and subsequent scientific work will determine who’s right and who’s wrong.

In order to convince readers of the grand changes to the organization of the brainstem in a species suggested by the authors the data presented needs to be supported. It is not. 

Comment: Again, this looks to us like more of the ‘total-rejection-commentary’ than like an actual recommendation.

Changes: None.

The protocol for the cytochrome oxidase histochemistry is not available in the locations indicated by the authors, and it is very necessary to provide this, as I fully believe that the staining obtained is not real, given the state of the tissue used. 

Comment: We apologize again for not including the necessary details on our cytochrome-oxidase staining.

From these comments (and the initial comments above) it appears that the referee is uncertain about the validity of cytochrome-oxidase staining. We (M.B., the senior author) have been doing this particular stain for approximately three decades. The referee being unfamiliar with cytochrome-oxidase staining is fine, but we can’t comprehend how the referee then comes to the ‘full belief’ that our staining patterns are ‘not real’ when the visual evidence indicates the opposite. We feel the referee does not want to believe our data.

From hundreds of permutations, we can assure the referee that cytochrome-oxidase staining can go wrong in many ways. The most common failure outcome in elephants is a uniform light brown stain after hours or days of the cytochrome-oxidase reaction. This outcome is closely associated with long ≥2 days post-mortem/fixation times and reflects the quenching of cytochrome-oxidases by fixation. Interestingly, cytochrome-oxidase staining in elephant brains is distinctly more sensitive to quenching by fixation than cytochrome-oxidase staining in rodent brains. Another, more rare failure of cytochrome-oxidase staining comes as entirely white or barely colored sections; this outcome is usually associated with a bad reagent (most commonly old DAB, but occasionally also old or bad catalase, in case you are using a staining protocol with catalase). Another nasty cytochrome-oxidase staining outcome is smeary all-black sections. In this case, a black precipitate sticks to sections and screws up the staining (filtering and more gradual heating of the staining solution usually solve this problem). Thus, you can get uniformly white, uniformly light brown, and smeary black sections as cytochrome-oxidase staining failures. What you never get from cytochrome-oxidase staining as an artifact are sections with a strong brown to lighter brown differential contrast. All sections with strong brown to lighter brown differential contrast (staining successes) show one and the same staining pattern in a given brain area, i.e., brownish barrels in the rodent cortex, brownish barrelettes (trigeminal nuclei) in the rodent brainstem, brownish putative trunk modules/inferior olives (if we believe the referee) in the elephant brainstem. Cytochrome-oxidase reactivity is in this regard remarkably different from antibody staining. In antibody staining you can get all kinds of interesting differential contrast staining patterns, which mean nothing. Such differential contrast artifacts in antibody staining arise as a result of insufficient primary antibody specificity, the secondary antibody binding non-specifically, and of what have you not reasons. The reason that the brown differential contrast of cytochrome-oxidase reaction is pretty much fool-proof, relates to the histochemical staining mechanism, which is based on the supply of specific substrates to a universal mitochondrial enzyme. The ability to reveal mitochondrial metabolism and the universal and ‘fool-proof’ staining qualities make the cytochrome-oxidase reactivity a fantastic tool for comparative neuroscience, where you always struggle with insufficient information about antigen reactivity.

We also note that the contrast of cytochrome-oxidase reactivity seen in the elephant brainstem is spectacular. As the Referee can see in our Figure 1C we observe a dark brown color in the putative trunk module, with the rest of the brain being close to white. Such striking cytochrome-oxidase reactivity contrast has been observed only very rarely in neuroanatomy: (i) In the rest of the elephant brain (brainstem, thalamus cortex) we did not observe as striking contrast as in the putative trunk module (the inferior olive according to the referee). (ii) In decades of work with rodents, we have rarely seen such differential activity. For example, cortical whisker-barrels (a classic CO-staining target) in rodents usually come out as dark brown against a light brown background.

What all of this commentary means is that patterns revealed by differential cytochrome-oxidase staining in the elephant brain stem are real.

Changes: We added details on our cytochrome-oxidase reactivity staining protocol and commented on cytochrome-oxidase reactivity in the elephant brain in general.

The authors need to recognize that the work done in Africa on elephant brains is of high quality and should not be blithely dismissed by the authors - this stinks of past colonial "glory", especially as the primary author on these papers is an African female.

Comment: The referee notes that we unfairly dismiss the work of African scientists and that our paper reflects a continuation of our horrific colonial past because we contradict the work of an African woman. We think such commentary is meant to be insulting and prefer to return to the scientific discourse. We are staunch supporters of diversity in science. It is simply untrue, that we do not acknowledge African scientists or the excellent work done in Africa on elephant brains. For example, we cite no less than four papers from the Manger group. We refer countless times in the manuscript to these papers, because these papers are highly relevant to our work. We indeed disagree with two anatomical assignments made by Maseko et al., 2013. Such differences should not be overrated, however. As we noted before, such differences relate to only 2 out of 147 anatomical assignments made by these authors. More generally, discussing and even contradicting papers is the appropriate way to acknowledge scientists. We already expressed we greatly admire the pioneering work of the Manger group. In our view, the perfusion of elephants in the field is a landmark experiment in comparative neuroanatomy. We closely work with colleagues in Africa and find them fantastic collaborators. When the referee is accusing us of contradicting the work of an African woman, the referee is unfairly and wrongly accusing us of attacking a scientist’s identity. More generally, we feel the discussion should focus on the data presented.

Changes: None.

In addition, perfusing elephants in the field with paraformaldehyde shortly after death is not a problem "partially solved" when it comes to collecting elephant tissue (n.b., with the right tools the brain of the elephant can be removed in under 2 hours). It means the problem IS solved. This is evidenced by the quality of the basic anatomical, immuno-, and Golgi-staining of the elephant tissue collected in Africa.

Comment: This is not a recommendation. We repeat: In our view, the perfusion of elephants in the field by the Manger group is a landmark experiment in comparative neuroanatomy. Apart, from that, we think the referee got our ‘partially solved comment’ the wrong way. It is perhaps worthwhile to recall the context of this quote. We first describe the numerous limitations of our elephant material; admitting these limitations is about honesty. Then, we wanted to acknowledge previous authors who either paved the way for elephant neuroanatomy (Shoshani) or did a better job than we did (Manger; see the above landmark experiment). These citations were meant as an appreciation of our predecessors’ work and by far not meant to diminish their work. Why did we say that the problems of dealing with elephant material are only partially solved? Because elephant neuroanatomy is hard and the problems associated with it are by no means solved. Many previous studies rely on single specimen and our possibilities of accessing, removing, processing, and preserving elephant brains are limited and inferior to the conditions elsewhere. Doing a mouse brain is orders of magnitude easier than doing an elephant brain (because the problems of doing mouse anatomy are largely solved), yet it is hard to publish a paper with six elephant brains because the referees expect evidence at least half as good as what you get in mice.

Changes: We replaced the ‘partially solved’ sentence.

The authors need to give credit where credit is due - the elephant cerebellum is clearly at the core of controlling trunk movement, and as much as primary sensory and final stage motor processing is important, the complexity required for the neural programs needed to move the trunk either voluntarily or in response to stimuli, is being achieved by the cerebellum. The inferior olive is part of this circuit and is accordingly larger than one would expect.

Comment: We think it is very much possible that the elephant cerebellum is important in trunk control.

Changes: We added a reference to the elephant cerebellum in the introduction of our manuscript.

Author response:

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

Common comments

(1) Significance of zero mutation rate

Reviewers asked why we included mutation rate even though setting mutation rate to zero doesn’t change results. We think that including non-zero mutation rate makes our results more generalisable, and thus is a strength rather than weakness. To better motivate this choice, we have added a sentence to the beginning of Results:

(2) Writing the mu=0 case first

Reviewers suggested that we should first focus on the mu=0 case, and then generalize the result. The suggestions are certainly good. However, given the large amount of work involved in a re-organization, we have decided to adhere to our current narrative. However, we now only include equations where mu=0 in the main text, and have moved the case of nonzero mutation rate to Supplementary Information.

(3) Making equations more accessible

We have taken three steps to make equations more readable.

● Equations in the main text correspond to the case of zero-mutation rate.

● The original section on equation derivation is now in a box in the main text so that readers have the choice of skipping it but interested readers can still get a gist of where equations came from.

● We have provided a much more detailed interpretation of the equation (see page 10).

(4) Validity of the Gaussian approximation

Reviewers raised concerns about the validity of Gaussian approximation on F frequency𝑓(𝜏). The fact that our calculations closely match simulations suggest that this approximation is reasonable. Still, we added a discussion about the validity of this approximation in Box 1.

We also added to SI with various cases of initial S and F sizes. This figure shows that when either initial S or initial F is small, the distribution of𝑓(𝜏) is not normal. However, if initial S and F are both on the order of hundreds, then the distribution of 𝑓(𝜏) is approximately Gaussian.

Public Reviews:

Summary:

The authors demonstrate with a simple stochastic model that the initial composition of the community is important in achieving a target frequency during the artificial selection of a community.

Strengths:

To my knowledge, the intra-collective selection during artificial selection has not been seriously theoretically considered. However, in many cases, the species dynamics during the incubation of each selection cycle are important and relevant to the outcome of the artificial selection experiment. Stochasticity from birth and death (demographic stochasticity) plays a big role in these species' abundance dynamics. This work uses a simple framework to tackle this idea meticulously.

This work may or may not be hysteresis (path dependency). If this is true, maybe it would be nice to have a discussion paragraph talking about how this may be the case. Then, this work would even attract the interest of people studying dynamic systems.

We have added this clarification in the main text:

“Note that here, selection outcome is path-dependent in the sense of being sensitive to initial conditions. This phenomenon is distinct from hysteresis where path-dependence results from whether a tuning parameter is increased or decreased.

Weaknesses:

(1) Connecting structure and function

In typical artificial selection literature, most of them select the community based on collective function. Here in this paper, the authors are selecting a target composition. Although there is a schematic cartoon illustrating the relationship between collective function (y-axis) and the community composition in the main Figure 1, there is no explicit explanation or justification of what may be the origin of this relationship. I think giving the readers a naïve idea about how this structure-function relationship arises in the introduction section would help. This is because the conclusion of this paper is that the intra-collective selection makes it hard to artificially select a community that has an intermediate frequency of f (or s). If there is really evidence or theoretical derivation from this framework that indeed the highest function comes from the intermediate frequency of f, then the impact of this paper would increase because the conclusions of this stochastic model could allude to the reasons for the prevalent failures of artificial selection in literature.

We have added this to introduction: “This is a common quest: whenever a collective function depends on both populations, collective function is maximised, by definition, at an intermediate frequency (e.g. too little of either population will hamper function [23]).”

(2) Explain intra-collective and inter-collective selection better for readers.

The abstract, the introduction, and the result section use these terms or intra-collective and inter-collective selection without much explanation. For the wide readership of eLife, a clear definition in the beginning would help the audience grasp the importance of this paper, because these concepts are at the core of this work.

This is a great point. We have added in Abstract:

“Such collective selection is dictated by two opposing forces: during collective maturation, intra-collective selection acts like a waterfall, relentlessly driving the S-frequency to lower values, while during collective reproduction, inter-collective selection resembles a rafter striving to reach the target frequency. Due to this model structure, maintaining a target frequency requires the continued action of inter-collective selection.”

and in Introduction

“A selection cycle consists of three stages (Fig. 1). During collective maturation, intra-collective selection favors fast-growing individuals within a collective. At the end of maturation, inter-collective selection acts on collectives and favors those achieving the target composition. Finally during collective reproduction, offspring collectives sample stochastically from the parents, a process dominated by genetic drift.”

(3) Achievable target frequency strongly depending on the degree of demographic stochasticity.

I would expect that the experimentalists would find these results interesting and would want to consider these results during their artificial selection experiments. The main Figure 4 indicates that the Newborn size N0 is a very important factor to consider during the artificial selection experiment. This would be equivalent to how much bottleneck is imposed on the artificial selection process in every iteration step (i.e., the ratio of serial dilution experiment). However, with a low population size, all target frequencies can be achieved, and therefore in these regimes, the initial frequency now does not matter much. It would be great for the authors to provide what the N0 parameter actually means during the artificial selection experiments. Maybe relative to some other parameter in the model. I know this could be very hard. But without this, the main result of this paper (initial frequency matters) cannot be taken advantage of by the experimentalists.

We have added an analytical approximation for N0˘, the Newborn size below which all target frequencies can be achieved in SI.

Also, we have added lines indicating N0˘ in Fig4a.

(4) Consideration of environmental stochasticity.

The success (gold area of Figure 2d) in this framework mainly depends on the size of the demographic stochasticity (birth-only model) during the intra-collective selection. However, during experiments, a lot of environmental stochasticity appears to be occurring during artificial selection. This may be out of the scope of this study. But it would definitely be exciting to see how much environmental stochasticity relative to the demographic stochasticity (variation in the Gaussian distribution of F and S) matters in succeeding in achieving the target composition from artificial selection.

You are correct that our work considers only demographic stochasticity.

Indeed, considering other types of stochasticity will be an exciting future research direction. We added in the main text:

“Overall our model considers mutational stochasticity, as well as demographic stochasticity in terms of stochastic birth and stochastic sampling of a parent collective by offspring collectives. Other types of stochasticity, such as environmental stochasticity and measurement noise, are not considered and require future research.”

(5) Assumption about mutation rates

If setting the mutation rates to zero does not change the result of the simulations and the conclusion, what is the purpose of having the mutation rates \mu? Also, is the unidirectional (S -> F -> FF) mutation realistic? I didn't quite understand how the mutations could fit into the story of this paper.

This is a great point. We have added this to the beginning of Results to better motivate our study:

“We will start with a complete model where S mutates to F at a nonzero mutation rate µ. We made this choice because it is more challenging to attain or maintain the target frequency when the abundance of fast-growing F is further increased via mutations. This scenario is encountered in biotechnology: an engineered pathway will slow down growth, and breaking the pathway (and thus faster growth) is much easier than the other way around. When the mutation rate is set to zero, the same model can be used to capture collectives of two species with different growth rates.

See answer on common question 1.

(6) Minor points

In Figure 3b, it is not clear to me how the frequency difference for the Intra-collective and the Inter-collective selection is computed.

We added a description in caption 3b.

In Figure 5b, the gold region (success) near the FF is not visible. Maybe increase the size of the figure or have an inset for zoom-in. Why is the region not as big as the bottom gold region?

We increased the resolution of Fig 5b so that the gold region near FF is more visible.

We have added Fig 5c and the following explanation to the main text:

“From numerical simulations, we identified two accessible regions: a small region near FF and a band region spanning from S to F (gold in Fig. 5b i). Intuitively, the rate at which FF grows faster than S+F is greater than the rate at which F grows faster than S (see section VIII in Supplementary Information). Thus, the problem can initially be reduced to a two-population problem (i.e. FF versus F+S; Fig. 5c left), and then expanded to a three-population problem (Fig. 5c right).”

Recommendations For The Authors

Since the conclusion of the model greatly depends on the noise (variation) of F and S in the Gaussian distribution, it would be nice to have a plot where the y-axis is the variation in terms of frequency and the x-axis is the s_0 or f_0 (frequency). In the plot, I would love to see how the variation in the frequency depends on the initial frequency of S and F. Maybe this is just trivial.

In the SI, we added Fig6a, as per your request. Previous Fig6 became Fig6b.

Reviewer #2 (Public review):

The authors provide an analytical framework to model the artificial selection of the composition of communities composed of strains growing at different rates. Their approach takes into account the competition between the targeted selection at the level of the meta-community and the selection that automatically favors fast-growing cells within each replicate community. Their main finding is a tipping point or path-dependence effect, whereby compositions dominated by slow-growing types can only be reached by community-level selection if the community does not start and never crosses into a range of compositions dominated by fast growers during the dynamics.

These results seem to us both technically correct and interesting. We commend the authors on their efforts to make their work reproducible even when it comes to calculations via extensive appendices, though perhaps a table of contents and a short description of these appendices at the start of SI would help navigate them.

Thank you for the suggestion. We have added a paragraph at the beginning of SI.

The main limitation in the current form of the article is that it could clarify how its assumptions and findings differ from and improve upon the rest of the literature:

-  Many studies discuss the interplay between community-level evolution and species- or strain-level evolution. But "evolution" can be a mix of various forces, including selection, drift/randomness, and mutation/innovation.

- This work's specificity is that it focuses strictly on constant community-level selection versus constant strain-level selection, all other forces being negligible (neither stochasticity nor innovation/mutation matter at either level, as we try to clarify now).

Note that intra-collective selection is not strictly “constant” in the sense that selection favoring F is the strongest at intermediate F frequency (Fig 3). However, we think that you mean that intra- and inter-collective selection are present in every cycle, and this is correct for our case, and for community selection in general.

-  Regarding constant community-level selection, it is only briefly noted that "once a target frequency is achieved, inter-collective selection is always required to maintain that frequency due to the fitness difference between the two types" [pg. 3 {section sign}2]. In other words, action from the selector is required indefinitely to maintain the community in the desired state. This assumption is found in a fraction of the literature, but is still worth clarifying from the start as it can inform the practical applicability of the results.

This is a good point. We have added to abstract:

“Such collective selection is dictated by two opposing forces: during collective maturation, intra-collective selection acts like a waterfall, relentlessly driving the S-frequency to lower values, while during collective reproduction, inter-collective selection resembles a rafter striving to reach the target frequency. Due to this model structure, maintaining a target frequency requires the continued action of inter-collective selection.”

- More importantly, strain-level evolution also boils down here to pure selection with a constant target, which is less usual in the relevant literature. Here, (1) drift from limited population sizes is very small, with no meaningful counterbalancing of selection, (2) pure exponential regime with constant fitness, no interactions, no density- or frequency-dependence, (3) there is no innovation in the sense that available types are unchanging through time (no evolution of traits such as growth rate or interactions) and (4) all the results presented seem unchanged when mutation rate mu = 0 (as noted in Appendix III), meaning that the conclusions are not "about" mutation in any meaningful way.

With regard to point (1), Figure 4a (reproduced below) shows how Newborn size affects the region of achievable targets. Indeed at large Newborn size (e.g. 5000 and above), no target frequency is achievable (since drift is too small to generate sufficient inter-community variation and consequently all communities are dominated by fast-growing F). However at Newborn size of for example 1000, there are two regions of accessible target frequencies. At smaller Newborn size, all target frequencies become achievable due to drift becoming sufficiently strong.

With regard to points (2) and (3), we have added to Introduction

“To enable the derivation of an analytical expression, we have made the following simplifications.

First, growth is always exponential, without complications such as resource limitation, ecological interactions between the two populations, or density-dependent growth. Thus, the exponential growth equation can be used. Second, we consider only two populations (genotypes or species): the fast-growing F population with size F and the slow-growing S population with size S. We do not consider a spectrum of mutants or species, since with more than two populations, an analytical solution becomes very difficult.”

With regard to point (4), we view this as a strength rather than weakness. We have added the following to the beginning of Results and Discussions:

“We will start with a complete model where S mutates to F at a nonzero mutation rate µ. We made this choice because it is more challenging to attain or maintain the target frequency when the abundance of fast-growing F is further increased via mutations.”

“When the mutation rate is set to zero, the same model can be used to capture collectives of two species with different growth rates.”

See Point 1 of Common comments.

- Furthermore, the choice of mutation mechanism is peculiar, as it happens only from slow to fast grower: more commonly, one assumes random non-directional mutations, rather than purely directional ones from less fit to fitter (which is more of a "Lamarckian" idea). Given that mutation does not seem to matter here, this choice might create unnecessary opposition from some readers or could be considered as just one possibility among others.

We have added the following justification:

“This scenario is encountered in biotechnology: an engineered pathway will slow down growth, and breaking the pathway (and thus faster growth) is much easier than the other way around.”

It would be helpful to have all these points stated clearly so that it becomes easy to see where this article stands in an abundant literature and contributes to our understanding of multi-level evolution, and why it may have different conclusions or focus than others tackling very similar questions.

Finally, a microbial context is given to the study, but the assumptions and results are in no way truly tied to that context, so it should be clear that this is just for flavor.

We have deleted “microbial” from the title, and revised our abstract:

Recommendations For The Authors

(1) More details concerning our main remark above:

- The paragraph discussing refs [24, 33] is not very clear in how they most importantly differ from this study. Our impression is that the resource aspect is not very important for instance, and the main difference is that these other works assume that strains can change in their traits.

We are fairly sure that resource depletion is important in Rainey group’s study, as the attractor only evolved after both strains grew fast enough to deplete resources by the end of maturation. Indeed, evolution occurred in interaction coefficients which dictate the competition between strains for resources.

Regardless, you raised an excellent point. As discussed earlier, we have added the following:

“To enable the derivation of an analytical expression, we have made the following simplifications.

First, growth is always exponential, without complications such as resource limitation, ecological interactions between the two populations, or density-dependent growth. Thus, the exponential growth equation can be used. Second, we consider only two populations (genotypes or species): the fast-growing F population with size F and the slow-growing S population with size S. We do not consider a spectrum of mutants or species, since with more than two populations, an analytical solution becomes very difficult.”

- We would advise the main text to focus on mu = 0, and only say in discussion that results can be generalized.

Your suggestion is certainly good. However, given the large amount of work involved in a reorganisation, we have decided to adhere to our current narrative. However, as discussed earlier, we have added this at the beginning of Results to help orient readers:

“We will start with a complete model where S mutates to F at a nonzero mutation rate µ. We made this choice because it is more challenging to attain or maintain the target frequency when the abundance of fast-growing F is further increased via mutations.”

“When the mutation rate is set to zero, the same model can be used to capture collectives of two species with different growth rates.”

(2) We think the material on pg. 5 "Intra-collective evolution is the fastest at intermediate F frequencies, creating the "waterfall" phenomenon", although interesting, could be presented in a different way. The mathematical details on how to find the probability distribution of the maximum of independent random variables (including Equation 1) will probably be skipped by most of the readers (for experienced theoreticians, it is standard content; for experimentalists, it is not the most relevant), as such I would recommend displacing them to SM and report only the important results.

This is an excellent suggestion. We have put a sketch of our calculations in a box in the main text to help orient interested readers. As before, details are in SI.

Similarly, Equations 2, 3, and 4 are hard to read given the large amount of parameters and the low amount of simplification. Although exploring the effect of the different parameters through Figures 3 and 4 is useful, I think the role of the equations should be reconsidered:

i. Is it possible to rewrite them in terms of effective variables in a more concise way?

See Point 3 of Common comments.

ii. Is it possible to present extreme/particular cases in which they are easier to interpret?

We have focused on the case where the mutation rate is zero. This makes the mathematical expressions much simpler (see above).

(3) Is it possible to explain more in detail why the distribution of f_k+1 conditional to f_k^* is well approximated by a Gaussian? Also, have you explored to what extent the results would change if this were not true (in light of the few universal classes for the maximum of independent variables)?

Despite the appeal to the CLT and the histograms in the Appendix suggesting that the distribution looks a bit like a Gaussian at a certain scale, fluctuations on that scale are not necessarily what is relevant for the results - a rapid (and maybe wrong) attempt at a characteristic function calculation suggests that in your case, one does not obtain convergence to Gaussians unless we renormalize by S(t=0) and F(t=0), so it seems there is a justification missing in the text as is for the validity of this approximation (or that it is simply assumed).

See point 4 of Common comments.

Reviewer #3 (Public Reviews):

The authors address the process of community evolution under collective-level selection for a prescribed community composition. They mostly consider communities composed of two types that reproduce at different rates, and that can mutate one into the other. Due to such differences in 'fitness' and to the absence of density dependence, within-collective selection is expected to always favour the fastest grower, but the collective-level selection can oppose this tendency, to a certain extent at least. By approximating the stochastic within-generation dynamics and solving it analytically, the authors show that not only high frequencies of fast growers can be reproducibly achieved, aligned with their fitness advantage. Small target frequencies can also be maintained, provided that the initial proportion of fast growers is sufficiently small. In this regime, similar to the 'stochastic corrector' model, variation upon which selection acts is maintained by a combination of demographic stochasticity and of sampling at reproduction. These two regions of achievable target compositions are separated by a gap, encompassing intermediate frequencies that are only achievable when the bottleneck size is small enough or the number of communities is (disproportionately) larger.

A similar conclusion, that stochastic fluctuations can maintain the system over evolutionary time far from the prevalence of the faster-growing type, is then confirmed by analyzing a three-species community, suggesting that the qualitative conclusions of this study are generalizable to more complex communities.

I expect that these results will be of broad interest to the community of researchers who strive to improve community-level selection, but are often limited to numerical explorations, with prohibitive costs for a full characterization of the parameter space of such embedded populations. The realization that not all target collective functions can be as easily achieved and that they should be adapted to the initial conditions and the selection protocol is also a sobering message for designing concrete applications.

A major strength of this work is that the qualitative behaviour of the system is captured by an analytically solvable approximation so that the extent of the 'forbidden region' can be directly and generically related to the parameters of the selection protocol.

Thanks so much for these positive comments.

I however found the description of the results too succinct and I think that more could be done to unpack the mathematical results in a way that is understandable to a broader audience. Moreover, the phenomenon the authors characterize is of purely ecological nature. Here, mutations of the growth rate are, in my understanding, neither necessary (non-trivial equilibria can be maintained also when \mu =0) nor sufficient (community-level selection is necessary to keep the system far from the absorbing state) for the phenomenon described. Calling this dynamics community evolution reflects a widespread ambiguity, and is not ascribable just to this work. I find that here the authors have the opportunity to make their message clearer by focusing on the case where the 'mutation' rate \mu vanishes (Equations 39 & 40 of the SI) - which is more easily interpretable, at least in some limits - while they may leave the more general equations 3 & 4 in the SI.

See points 1-4 of Common comments.

Combined with an analysis of the deterministic equations, that capture the possibility of maintaining high frequencies of fast growers, the authors could elucidate the dynamics that are induced by the presence of a second level of selection, and speculate on what would be the result of real open-ended evolution (not encompassed by the simple 'switch mutations' generally considered in evolutionary game theory), for instance discussing the invasibility (or not) of mutant types with slightly different growth rates.

Indeed, evolution is not restricted to two types. However, our main goal here is to derive an analytical expression, and it was difficult for even two types. For three-type collectives, we had to resort to simulations. Investigating the case where fitness effects of mutations are continuously distributed is beyond the scope of this study.

The single most important model hypothesis that I would have liked to be discussed further is that the two types do not interact. Species interactions are not only essential to achieve inheritance of composition in the course of evolution but are generally expected to play a key role even on ecological time scales. I hope the authors plan to look at this in future work.

In our system, the S and F do interact in a competitive fashion: even though S and F are not competing for nutrients (which are always in excess), they are competing for space. This is because a fixed number of cells are transferred to the next cycle. Thus, the presence of F will for example reduce the chance of S being propagated. We have added this clarification to our main text:

“Note that even though S and F do not compete for nutrients, they compete for space: because the total number of cells transferred to the next cycle is fixed, an overabundance of one population will reduce the likelihood of the other being propagated.”

Recommendations For The Authors

I felt the authors could put some additional effort into making their theoretical results meaningful for a population of readers who, though not as highly mathematically educated as they are, can nonetheless appreciate the implications of simple relations or scaling. Below, you find some suggestions:

(1) In order to make it clear that there is a 'natural' high-frequency equilibrium that can be reached even in the absence of selection, the authors could examine first the dynamics of the deterministic system in the absence of mutations, and use its equilibria to elucidate the combined role of the 'fitness' difference \omega and of the generation duration \tau in setting its value. The fact that these parameters always occur in combination (when there are no mutations) is a general and notable feature of the stochastic model as well. Moreover, this model would justify why you only focus on decreasing the frequency in the new generation.

Note that the ‘natural’ high-frequency equilibrium in the absence of collective selection is when fast grower F becomes fixed in the population. Following your suggestion, we have introduced two parameters 𝑅τ and 𝑊τ to reflect the coupling between ‘fitness’ and ‘generation duration’:

(2) Since the phenomenon described in the paper is essentially ecological in nature (as the author states, it does not change significantly if the 'mutation rate' \mu is set to zero), I would put in the main text Equations 39 & 40 of the SI in order to improve intelligibility.

See Point 2 at the beginning of this letter.

These equations can be discussed in some detail, especially in the limit of small f^*_k, where I think it is worth discussing the different dependence of the mean and the variance of the frequency distribution on the system's parameters.

This is a great suggestion. We have added the following:

“In the limit of small , Equation (3) becomes f while Equation (4) becomes . Thus, both Newborn size (N₀) and fold-change in F/S during maturation (W_τ) are important determinants of selection progress.

(3) I would have appreciated an explanation in words of what are the main conceptual steps involved in attaining Equation 2, the underlying hypotheses (notably on community size and distributions), and the expected limits of validity of the approximation.

See points 3 and 4 at the beginning of this letter.

(4) I think that some care needs to be put into explaining where extreme value statistics is used, and why is the median of the conditional distribution the most appropriate statistics to look at for characterizing the evolutionary trajectory (which seems to me mostly reliant on extreme values).

Great point! We added an explanation of using median value in Box 1.

and also added figure 7 to explaining it in SI.

Showing in a figure the different distributions you are considering (for instance, plotting the conditional distribution for one generation in the trajectories displayed in Figure 2) would be useful to understand what information \bar f provides on a sequence of collective generations, where in principle there may be memory effects.

Thanks for this suggestion. We have added to Fig 2d panel to illustrate the shape and position of F frequency distributions in each step in the first two selection cycles.

(5) Similarly, I do not understand why selecting the 5% best communities should push the system's evolution towards the high-frequency solution, instead of just slowing down the improvement (unless you are considering the average composition of the top best communities - which should be justified). I think that such sensitivity to the selection intensity should be appropriately referenced and discussed in the main text, as it is a parameter that experimenters are naturally led to manipulate.

In the main text, we have added this explanation:

“In contrast with findings from an earlier study [23], choosing top 1 is more effective than the less stringent “choosing top 5%”. In the earlier study, variation in the collective trait is partly due to nonheritable factors such as random fluctuations in Newborn biomass. In that context, a less stringent selection criterion proved more effective, as it helped retain collectives with favorable genotypes that might have exhibited suboptimal collective traits due to unfavorable nonheritable factors. However, since this study excludes nonheritable variations in collective traits, selecting the top 1 collective is more effective than selecting the top 5% (see Fig. 11 in Supplementary Information).”

(6) Equation 1 could be explained in simpler terms as the product between the probability that one collective reaches the transmitted value times the probability that all others do worse than that. The current formulation is unclear, perhaps just a matter of English formulation.

We have revised our description to state:

“Equation (1) can be described as the product between two terms related to probability: (i) describes the probability density that any one of the g Adult collectives achieves f given , and (ii) describes the probability that all other g – 1 collectives achieve frequencies above f and thus not selected.”

(7) I think that the discussion of the dependence of the boundaries of the 'waterfall' region with the difference in growth rate \omega is important and missing, especially if one wants to consider open-ended evolution of the growth rate - which can occur at steps of different magnitude.

We added a new chapter and figure in supplementary information on the threshold values when \omega varies. As expected, smaller \omega enlarges the success area.

We have also added a new figure panel to show how maturation time affects selection efficacy.

(8) Notations are a bit confusing and could be improved. First of all, in most equations in the main text and SI, what is initially introduced as \omega appears as s. This is confusing because the letter s is also used for the frequency of the slow type.

The letter S is used to denote an attribute of cells (S cells), the type of cells (Equations 1-3 of the SI) and the number of these cells in the population, sometimes with different meanings in the same sentence. This is confusing, and I suggest referring to slow cells or fast cells instead (or at least to S-cells and F-cells), and keeping S and F as variables for the number of cells of the two types.

All typos related to the notation have been fixed. We use S and F as types, and S and F (italic) and population numbers.

(9) On page 3, when introducing the sampling of newborns as ruled by a binomial distribution, the information that you are just transmitting one collective is needed, while it is conveyed later.

We have added this emphasis:

“At the end of a cycle, a single Adult with the highest function (with F frequency f closest to the target frequency ) is chosen to reproduce g Newborn collectives each with N₀ cells (‘Selection’ and ’Reproduction’ in Fig. 1).”

(10) I found that the abstract talks too early about the 'waterfall' phenomenon. As this is a concept introduced here, I suggest the authors first explain what it is, then use the term. It is a useful metaphor, but it should not obscure the more formal achievements of the paper.

We feel that the “waterfall” analogy offers a gentle helping hand to orient those who have not thought much about the phenomenon. We view abstract as an opportunity to attract readership, and thus the more accessible the better.

(11) In the SI there are numerous typos and English language issues. I suggest the authors read carefully through it, and add line numbers to the next version so that more detailed feedback is possible.

Thank you for going through SI. We have gone through the SI, and fixed problems.

Author Response

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

We sincerely thank and express our appreciation to each of the reviewers for their thorough critique of our manuscript.

Reviewer #1 (Recommendations For The Authors):

1. The analysis of whole study comes from only 4 cells from L2/3 of ferret visual cortex; however, it is well known that there is a high level of functional heterogeneity within the cortical neurons. Do those four neurons have similar or different response properties? If the four neurons are functionally different, the weak or no correlation may result from heterogenous distribution pattern of mitochondria associated with heterogenous functionality.

This is an important consideration and often a limitation of CLEM studies. While cortical neurons do exhibit a high degree of functional heterogeneity (similar to spine activity), the 4 cells examined all had selective (OSI > 0.4) somatic responses to oriented gratings, although they differed in their exact orientation preference. Due to experimental limitations of recording from a large population of dendritic spines, we did not characterize other response properties for which their sensitivity might differ. We did not consider orientation preference a metric of study, but instead characterized the difference in preference from the somatic output, allowing comparisons across spines. In addition, our measurements were limited to proximal, basal dendrites rather than any location in the dendritic tree. Nonetheless, we attempted to address this concern by examining spines with functionally heterogenous visual responses within single cells, as reported in our manuscript: mitochondrial volume within a 1 µm radius was correlated with difference in orientation preference relative to the soma across all 4 cells, the mean r = 0.49 +/- 0.22 s.d.), suggesting that cell-to-cell variability has a minimal impact on our main conclusions.

Even with our limited measurements, there is a large amount of functional heterogeneity in dendritic spine responses (Extended Data Figure 2, Scholl et al. 2021), far greater than the small differences in somatic responses of these 4 cells (Figure 3, Scholl et al. 2021). Moreover, the individual dendrites from these 4 cells exhibited substantial heterogeneity in the distribution of mitochondria. We cannot rule out whether heterogeneity at various scales may obscure certain relationships or result in the weak correlations we observed. We also note that future advancements in volume electron microscopy should allow for greater sample sizes that can better address the role of functional (and structural) heterogeneity. We have added text in the Discussion section about the potential structure-function relationships that might be obscured or revealed by neuron heterogeneity.

1. The authors argued that "mitochondria are not necessarily positioned to support the energy needs of strong spines." However, the overall energy needs of a spine depend not only on the synaptic strength but also on the frequency of synaptic activity. Is there a correlation between the mitochondria volume around a spine and the overall activity of the spine? This data needs to be analyzed to confirm the distribution of mitochondria is independent of local energy needs.

The reviewer is correct, but our experimental paradigm was not optimally designed to measure the ‘frequency’ of synaptic activity in vivo. This could have been accomplished with flashed gratings or, perhaps, presenting drifting gratings at different temporal frequencies. For spines tuned to higher temporal frequencies in V1, we may expect greater energy needs, although as the reviewer suggests, energy needs will depend on synapse (and bouton) size. Because we are not able to directly measure activity frequency as carefully or beautifully as can be done ex vivo or in nerve fibers, we do not feel confident in attempting such analysis in this study. Instead, based on previous studies, we assumed that larger synapses might be able to transmit higher frequencies, and thus have higher energy demands. We believe future in vivo studies will more directly measure synaptic frequency for comparison with mitochondria.

We have added text in the Discussion about this caveat and potential future experiments.

1. In the results section, the authors briefly mentioned that "We also considered other spine response properties related to tuning preference; specifically, orientation selectivity and response amplitude at the preferred orientation. For either metric, we observed no relationship to mitochondria within 1 μm radius (selectivity: 1 μm: r = -0.081, p = 0.269, n = 60; max response amplitude: 1 μm: r = -0.179, p = 0.078, n = 64) but did see a weak, significant relationship to both at a 5 μm radius (selectivity: r = 0.175, p = 0.027, n = 121; max response amplitude: r =-0.166, p = 0.030, n = 129)." Here only statistic results were given while the data were not presented in the figure illustration. Based on the methods and Figure 3B, it seems that the preferred orientations were calculated based on the vector summation. How did the authors calculate the "response amplitude at the preferred orientation"? This needs to be clarified. In addition, given the huge variety of orientation selectivity, using the response amplitude at the preferred orientation may not be the best parameter to correlate with the mitochondria volume which is indicative of energy needs. It might be necessary to include the baseline activity without visual stimulation and the average response for visual stimuli of different orientations in the analysis.

We apologize for this oversight, as the details are present in our previous study (Scholl et al., 2021). Response amplitude and preferred orientation were calculated from a Gaussian curve fitting procedure with specific parameters describing those exact values (see Scholl et al. 2021 or Scholl et al. 2013). Only spines with selective responses (vector strength index > 0.1) and passing our SNR criterion were used for these analyses. We have now added this information to the Methods section and referred to it in the Results. With respect to the reviewer’s other concern, we also examined the average response amplitude (across all visual stimuli). There we found no relationship between the volume of mitochondria within 1 or 5 microns of a spine, however, because spines differ greatly in their selectivity (range = 0 – 0.8) the average response may not be an appropriate metric to compare across spines.

1. A continuation from the former point, do the spines with similar preferred orientation to the somatic Ca signal have similar Ca signal strength, orientation selectivity index and other characteristics to the spines with different preferred orientation? As shown in the examples (Figure 3B), the spine on the right with different orientation preference compared with its soma has considerably larger response in non-preferred orientation compared to the spine on the left. Thus, the overall activity of the spine on the right may be higher than the spine which has similar preferred orientation to the soma. The authors showed that a positive correlation between difference in orientation preference and mitochondria volume (Figure 3C). Could this be simply due to higher spine activity for non-preferred orientation or spontaneous activity? Thus, the mitochondria might be positioned to support spines with higher overall activity rather than diverse response property.

The reviewer brings up an interesting consideration. We examined the response properties of spines co-tuned (∆θpref < 22.5 deg) and differentially-tuned (∆θpref > 67.5 deg) to the soma. The orientation selectivity was not different between the two groups (p = 0.12, Wilcoxon ranksum test), although there was a small trend towards co-tuned inputs being more selective. We found that calcium response amplitudes for the preferred stimulus were also not different (p = 0.58, Wilcoxon ranksum test). These analyses are now included as a sentence in the Results.

We agree with the reviewer that higher spontaneous activity in non-preferred spines may help explain the mitochondrial relationship we observe. However, our current dataset does not have sufficiently long recordings to measure spontaneous synaptic activity. Further, when considering a non-anesthetized preparation, spontaneous activity is highly dependent on brain state and an animal’s self-driven brain activity, which all must be experimentally controlled or measured to accurately address this.

1. In addition, the information about the orientation selectivity of the soma is also missing. Do the four cells shown here all have similar level of orientation selectivity? Or some have relative weak orientation selectivity in the soma?

Yes, all 4 cells have a similar OSI (range = 0.4 – 0.57, mean = 0.46 +/ 0.08 s.d.). This has been added to the Results section.

1. This study focused on only a fraction of spines that are (1) responsive (2) osi > 0.1. However, in theory energy consumption is also related to non-responsive spines and spines with weak orientation tuning. What is the percentage of tuned and untuned spines? What's the correlation of mitochondria volume and spine activity level for untuned spines? I also recommend including the non-responsive spines into the analysis. For example, for each mitochondrion calculate the averaged overall activity of spines within certain distance from the mitochondrion, including the non-responsive spines. I would predict there may be more active spines and higher overall spine activity of dentritic segments near a mitochondrion than segments far from a mitochondrion.

A majority of spines were tuned for orientation (~91%), although we specifically chose to only analyze data from spines with verifiable, independent calcium events. All analyses except those involving measurements of orientation preference use all dendritic spines (i.e. tuned and untuned). We have clarified this in the Results.

These other ‘silent’ (i.e. without resolvable visual activity) spines may significantly contribute to energy demands of a dendrite too, as our methods (GCaMP6s expression) likely only capture synaptic events driving Ca+2 influx through NMDA receptors or VGCCs. We expect that glutamate imaging (e.g. iGlusnfr) may open the door to additional analyses to fully characterize functional relationship between spines and mitochondria.

1. The correlation coefficient for mitochondria volume and difference in orientation preference is relatively low (r=0.3150). With such weak correlation, the explanatory power of this data is limited.

We agree that while the correlation is significant, it is not particularly strong. To better represent the noise surrounding this measurement, we performed a bootstrap correlation analysis, sampling with replacement (1 micron: mean r = 0.31 +/- 0.11 s.e., 5 micron: mean r = 0.02 +/- 0.10 s.e.). We now include this in the Results.

1. Why do the numbers of spines in different figures vary? For example, n=60 for 1micron in Figure 3, 54 in Figure 3c, 31 in Figure 4b, 51 in Figure 4e and so on.

We apologize for the lack of clarity. Each analysis presented different requirements of the data. For example, orientation preference was computed only for selective (OSI > 1) spines (Fig. 3c), but this requirement did not apply to comparisons with selectivity or response amplitude (Fig. 3d). Similarly, as stated in the Results and Methods, measurements of local heterogeneity require a minimum number of neighboring spines (n > 2), limiting the number of usable spines for analysis (Fig. 4). We have clarified this in the text.

1. In Figure 6a, the sample sizes of mito+ spines and mito- spines are extremely unbalanced, which affects the stat power of the analysis. I recommend performing a randomization test.

We thank the reviewer for this suggestion. We ran permutation tests to compare the similarity in mean values between equally sampled values from each distribution. These tests supported our original analysis and conclusions. We have added these tests to the Results.

1. Ca signals are approximations of electrical signals. How well are spinal calcium signals correlated to synaptic strength and local depolarization? This should be put into discussion.

There is unlikely a simple, direct relationship between spine calcium signal and synaptic strength or membrane depolarization, and this has never been addressed in vivo. Koester and Johnston (2005) performed paired recordings in slice and showed that single presynaptic action potentials producing successful transmission generate widely different calcium amplitudes (Fig. 3). Another study from Sobczyk, Scheuss, and Svoboda (2005) used two-photon glutamate uncaging on single spines and showed that micro-EPSC’s evoked are uncorrelated with the spine calcium signal amplitude. We have added a note about this in the discussion.

1. In Figure 4i, the negative correlation may depend on the 4 data points on the right side. How influential are those data points?

Spearman’s correlation coefficient analysis is robust to outliers and it is highly unlikely these datapoints are critical with our sample size (n > 100 spines).

1. Raw data of Ca responses were missing.

Some data has been published with the parent publication (Scholl et al., 2021). As spine imaging data is difficult to obtain and highly unique, we prefer to provide raw data directly upon reasonable request of the corresponding author.

1. What is the temporal frequency of the drifting grating? Was it fixed or the speed of the grating was fixed?

This was fixed to 4 Hz and this is now included in the Methods.

Reviewer #2 (Recommendations For The Authors):

1. Most of the measurements were based on the distance from the base of the spine neck, and "only on spines with measurable mitochondrial volume at each radius" were analyzed. To better understand the causality, it may also be interesting to have an analysis based on the distance from mitochondria. Would the result be different if the measurements are not 1µm / 5µm from spine but 1µm / 5µm from mitochondria? (e.g. total spine volume in 1µm / 5µm from mitochondria).

In fact, our first iteration of this study focused on exactly this metric: measuring the distance to nearest mitochondria. However, after lengthy discussions between the authors, we ultimately decided this metric was inferior to a volumetric one. Our decision was based on several factors: (1) distance to mitochondrion is ill defined (e.g. distance to the a mitochondrion center or nearest membrane edge?), (2) the total amount of mitochondrial volume within a dendritic shaft should allow the greatest amount of energetic support (e.g. more cristae for ATP production, greater capacity for calcium buffering), and (3) we would not account for the geometry of individual mitochondria or their placement near a spine (e.g. when 2 different mitochondria are next to the same spine) We have added further clarification of our reasoning to the Results.

Nonetheless, we present the reviewer some of our original analyses correlating distance to mitochondria (from the base of the spine and including the spine neck length):

Author response image 1.

Here, we examined the relationship to spine head volume, spine-soma orientation preference difference, and the local orientation preference heterogeneity. No relationship showed any significant correlation. Again, this may not be surprising given the drawbacks of measuring ‘distance to mitochondria’.

1. Is there a selection criterion for the spine for the analysis? Are filopodia spines excluded in the analysis?

Spines were analyzed regardless of structural classification; however, they were only analyzed if they had a synaptic density with synaptic vesicle accumulation. In our dataset (including those visualized in vivo and reconstructed from the EM volume) we observed no filopodia.

1. The result states that "56.8% of spines had no mitochondria volume within 1 μm and 12.1% of spines had none within 5 μm.". In other words, around 43% of spines had mitochondria within 1 μm. It would be interesting to show whether there is a correlation between mitochondria size and spine density.

We agree that this is an interesting measurement. It has been reported that mitochondrial unit length along the dendrite co-varies with linear synapse density in the neocortical distal dendrites of mice (Turner et al., 2022). This was specifically true in distal portions of dendrites more than 60 µm from the soma, because mitochondria volume increases as a function of distance roughly up to this point, then remains relatively constant beyond this distance.

To investigate this possibility, we calculated the local spine density around an individual spine and compared to the mitochondria volume within 1 or 5 µm. We found no evidence of a correlation between local spine density and the volume of mitochondria (1 µm: Spearman r = -0.07447, p = 0.2859; 5 µm: r = -0.04447, p = 0.3141). However, the majority of our measurements are more proximal than 60 µm (our median distance of all spines = 49.4 µm, max = 114 µm) and this may be one reason why observe no correlation.

1. In Figure 3B, the drifting grating directions are examined from 0 to 315 degrees in the experiment. However, in Figure 3C and 3D, the spine-soma difference of orientation preference was limited to 0 to 90 degree in the graph. Is the graph trimmed, or is there a cause that limits the spine-soma difference of orientation preference to 90?

Ferret visual cortical neurons are highly sensitive to grating direction and the responses are fit by a double Gaussian curve which estimates the ‘orientation preference’ (0-180 deg). We then calculated the absolute difference in orientation preference and wrapped that value in circular space so the maximum difference possible is 90 deg (e.g. 135 deg -> 45 deg).

1. In Figure 4D-F, how is the temporal correlation of calcium activity determined? Is it based on stimulated activity or basal activity? A brief explanation may be helpful to the readers. Also, scale bars could be added to Fig 4D.

Temporal correlation is computed as the signal correlation between 2 spines over the entire imaging session at that field of view. Specifically, we measured the Pearson correlation between each spine’s ∆F/F trace. To measure the local spatiotemporal correlation, we computed correlations between all neighboring spines within 5 microns and took the average of those values. We have clarified this in the Results section.

1. Figure 3C and Figure 4D displayed a significant correlation in 1µm range and such correlation drastically diminished once the criterion changed to 5µm range. It would be interesting to include the criterion of intermediate ranges. It would be interesting to see if there is a trend or tendency or if there is a "cut-off" limit.

We agree with the reviewer that the drastic change in the correlations between 1 and 5 µm range was surprising to see. While these volumetric measurements are time consuming, we returned to our data and measured an intermediate point of 3 µm. Investigating relationships reported in our study, we found no significant trends for spine-soma similarity (Spearman’s r = -0.011, p = 0.54) or local heterogeneity (Spearman’s r = 0.11, p = 0.23). This suggests that a potential ‘critical distance’ might be less than 3 µm; however, far more additional measurements and analyses would be needed to attempt to identify exactly what this distance is.

1. In Figure 5, it is shown that spines having mitochondrion in the head or neck are larger. However, only 10 spines are found with mitochondria inside. In the current dataset, are mitochondria abundantly found in large spines? Further analysis or justification would be informative to address this.

In our dataset, mitochondria were found in ~5% of all spines. Spines with mitochondria have a median volume of approximately 0.6 µm3, roughly twice as large as than those without mitochondria, as the reviewer suggests. In the entire population of spines without mitochondria, a volume of 0.6 µm3 represents roughly the 82nd percentile. In other words, of the total population of 157 spines without mitochondria, only 29 had equal or greater volume than the median spine with a mitochondrion. We believe this trend is clearly shown in Figure 5A and is supported by our analysis, including new permutation tests suggested by Reviewer 1.

Reviewer #3 (Recommendations For The Authors):

1. The authors state that their unsupervised method "quickly and accurately identified mitochondria," but the methods section only says that segmentations were proofread. Was every segmentation examined and judged to be accurate, or was only a subset of the 324 mitochondria checked?

After deep learning-based extraction, each mitochondrion segmentation was manually proofread. For each dendrite segment, this was ~10-20 mitochondria, so it did not take long to manually inspect and edit each mitochondrion segmentation.

1. The EM image of the mitochondrion in the spine head in Figure 2C is low resolution and does not apply to the bulk of the data. Images more representative of the analyzed data should be added to supplement the cartoons.

Our primary rationale for including this specific image was to show that the mitochondria located within spines are small, round, and to include a view of the synapse as well as the mitochondrion. We now include enlarge and additional EM images to Figure 1C.

1. The majority of spines did not have any mitochondria within a 1 micron radius and were excluded from the correlation analyses, so most of the conclusions are based on a minority of spines. It would be interesting to see comparisons between spines with and without nearby mitochondria. Correlations between the absolute distance to any mitochondrion, synapse size, and mismatch to soma orientation would be especially interesting.

The reviewer brings up a good point. It is true that many spines were excluded from our analysis based on the fact that they did not have nearby mitochondria within 1 or 5 µm (56.8% of spines had no mitochondria volume within 1 μm and 12.1% of spines had none within 5 μm). We compared the distributions of synapse size, mismatch to soma, and orientation selectivity of two groups of spines – those with at least some mitochondria within 1 µm (n = 65) versus spines without any mitochondria within 5 µm (n = 19).

We found no difference in the distributions between spine volume (1 µm: median = 0.29 µm3, IQR = 0.41 µm3; no mitochondria within 5 µm: median = 0.40 µm3, IQR = 0.37 µm3; p = 0.67) or PSD area (1 µm: median = 0.26 µm2, IQR = 0.33 µm2; no mitochondria within 5 µm: median = 0.31 µm2, IQR = 0.36 µm2; p = 0.49). For functional measures, we also saw no difference in orientation selectivity (1 µm: median = 0.29, IQR = 0.28; no mitochondria within 5 µm: median = 0.28, IQR = 0.15; p = 0.74) or mismatch to soma orientation (1 µm: median = 0.54 deg, IQR = 0.86 deg; no mitochondria within 5 µm: median = 0.46 deg, IQR = 0.47 deg; p = 0.75). We now include analyses in the Results.

We also looked at the absolute distances to mitochondria and did not find any significant relationships to spine head volume, spine-soma orientation preference difference, or the local orientation preference heterogeneity (see our response to reviewer #2 for more information).

1. In Figure 1A the mitochondria appear to be taking up a substantial fraction of the dendritic shaft diameter, even for distal dendrites. It would be useful to know the absolute diameter of the dendrites and mitochondria, given that this is not rodent data and there is no reference for either in the ferret.

We agree with the reviewer’s point, although we would like to remind the reviewer that these are basal dendrites of layer 2/3 cells. Basal dendrites tend to be thinner than apical branches. Interestingly, in some cases, the dendrite even swells to accommodate a mitochondrion. We did not incorporate this measurement in our study because it is not trivial; dendrite diameter is variable and dendrites are not perfect cylinders. Although we did not make precise measurements across our dendrites, the diameter is comparable to what has been seen in mouse cortex (Turner et al., 2022), roughly 500-1000 nm, but as small as 100 nm at some pinch points. In terms of mitochondria, many were roughly spherical or oblong, therefore the maximum diameters we report are roughly similar to, if not a bit larger than, those of the cross-sectional diameter.

1. As a rule, PSD area is correlated with spine volume, which makes the observation that spines with mitochondria have larger volume but not PSD area surprising. With n=10 it is difficult to draw conclusions, but it would be interesting to know the PSD area-to-volume ratio of other spines of the same volume and synapse size.

We were also somewhat surprised to see this, but exactly as the reviewer mentioned, we believe it to be a limitation of the sample size. The difference in volume was large enough to be detected despite a small sample size. We saw a trend towards larger synapses when spines have mitochondria (the median was approximately 60% larger), and we would expect with a larger comparison that PSD area would be significantly greater in spines with mitochondria.

We calculated the PSD area-to-spine head volume ratio for spines with or without mitochondria. Spines with mitochondria had a significantly lower ratio compared to those without (Mann-Whitney test, p = 0.0056, mito - = 0.78, n = 10; mito + = 0.53, n = 157). As the reviewer mentions, it is somewhat difficult to draw a conclusion from this, but it appears that the PSD does not scale with the increased spine head size.

Author response image 2.

The only way to definitively address this is to increase the sample size, which is becoming easier to achieve with the progression of volume EM imaging and analysis techniques in recent times. We look forward to addressing this in the future.

1. Nothing is made of the significant fact that these data come from the visual system of a carnivore, not a mouse. Consideration of differences in visual physiology between rodents and carnivores would be worthwhile to put the function of these dendrites in context.

We thank the reviewer for this consideration and have added text to the Discussion.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors aimed to investigate the contribution of antigenic drift in the HA and NA genes of seasonal influenza A(H3N2) virus to their epidemic dynamics. Analyzing 22 influenza seasons before the COVID-19 pandemic, the study explored various antigenic and genetic markers, comparing them against indicators characterizing the epidemiology of annual outbreaks. The central findings highlight the significant influence of genetic distance on A(H3N2) virus epidemiology and emphasize the role of A(H1N1) virus incidence in shaping A(H3N2) epidemics, suggesting subtype interference as a key factor. 

Major Strengths: 

The paper is well-organized, written with clarity, and presents a comprehensive analysis. The study design, incorporating a span of 22 seasons, provides a robust foundation for understanding influenza dynamics. The inclusion of diverse antigenic and genetic markers enhances the depth of the investigation, and the exploration of subtype interference adds valuable insights. 

Major Weaknesses: 

While the analysis is thorough, some aspects require deeper interpretation, particularly in the discussion of certain results. Clarity and depth could be improved in the presentation of findings. Furthermore, the evolving dynamics of H3N2 predominance post-2009 need better elucidation.  

Reviewer #2 (Public Review): 

Summary: This paper aims to achieve a better understanding of how the antigenic or genetic compositions of the dominant influenza A viruses in circulation at a given time are related to key features of seasonal influenza epidemics in the US. To this end, the authors analyze an extensive dataset with a range of statistical, data science and machine learning methods. They find that the key drivers of influenza A epidemiological dynamics are interference between influenza A subtypes and genetic divergence, relative to the previous one or two seasons, in a broader range of antigenically related sites than previously thought. 

Strengths: A thorough investigation of a large and complex dataset. 

Weaknesses: The dataset covers a 21 year period which is substantial by epidemiological standards, but quite small from a statistical or machine learning perspective. In particular, it was not possible to follow the usual process and test predictive performance of the random forest model with an independent dataset. 

Reviewer #3 (Public Review): 

Summary: 

This paper explores the relationships among evolutionary and epidemiological quantities in influenza, using a wide range of datasets and features, and using both correlations and random forests to examine, primarily, what are the drivers of influenza epidemics. It's a strong paper representing a thorough and fascinating exploration of potential drivers, and it makes a trove of relevant data readily available to the community. 

Strengths: 

This paper makes links between epidemiological and evolutionary data for influenza. Placing each in the context of the other is crucial for understanding influenza dynamics and evolution and this paper does a thorough job of this, with many analyses and nuances. The results on the extent to which evolutionary factors relate to epidemic burden, and on interference among influenza types, are particularly interesting. The github repository associated with the paper is clear, comprehensive, and well-documented. 

Weaknesses: 

The format of the results section can be hard to follow, and we suggest improving readability by restructuring and simplifying in some areas. There are a range of choices made about data preparation and scaling; the authors could explore sensitivity of the results to some of these. 

Response to public reviews

We appreciate the positive comments from the reviewers and have implemented or responded to all of the reviewers’ recommendations.

In response to Reviewer 1, we expand on the potential drivers and biological implications of the findings pointed out in their specific recommendations. For example, we now explicitly mention that antigenically distinct 3c.2a and 3c.3a viruses began to co-circulate in 2012 and underwent further diversification during subsequent seasons in our study. We note that, after the 2009 A(H1N1) pandemic, the mean fraction of influenza positive cases typed as A(H3N2) in A(H3N2) dominant seasons is lower compared to A(H3N2) dominant seasons prior to 2009. We propose that the weakening of A(H3N2) predominance may be linked to the diversification of A(H3N2) viruses during the 2010s, wherein multiple antigenically distinct clades with similar fitness circulated in each season, as opposed to a single variant with high fitness.

In response to Reviewer 2, we agree that it would be ideal and best practice to measure model performance with an independent test set, but our dataset includes only ~20 seasons. Predictions of independent test sets of 2-3 seasons had unstable performance, which indicates we do not have sufficient power to measure model performance with a test set this small. In the revised manuscript, we provide more justification and clarification of our methodology. Instead of testing model performance on an independent test set, we use leave-one-season-out cross-validation to train models and measure model performance, wherein each “assessment” set contains one season of data (predicted by the model), and the corresponding “analysis” set (“fold”) contains the remaining seasons. This approach is roughly analogous to splitting data into training and test sets, but all seasons are used at some point in the training of the model (Kuhn & Johnson, 2019).

In response to Reviewer 3, we follow the reviewer’s advice to put the Methods section before the Results section. Concerning Reviewer 3’s question about the sensitivity of our results to data preparation and rescaling, we provide more justification and clarification of our methodology in the revised manuscript. In our study, we adjust influenza type/subtype incidences for differences in reporting between the pre- and post-2009 pandemic periods and across HHS regions. We adjust for differences in reporting between the pre- and post-2009 periods because the US CDC and WHO increased laboratory testing capacity in response to the 2009 A(H1N1) pandemic, which led to substantial, long-lasting improvements to influenza surveillance that are still in place today. Figure 1 - figure supplement 2 shows systematic increases in influenza test volume in all HHS regions after the 2009 pandemic. Given the substantial increase in test volume after 2009, we opted to keep the time trend adjustment for the pre- and post-2009 pandemic periods and evaluate whether adjusting for regional reporting differences affects our results. When estimating univariate correlations between various A(H3N2) epidemic metrics and evolutionary indicators, we found qualitatively equivalent results when adjusting for both pre- and post-2009 pandemic reporting and regional reporting versus only adjusting for the pre- and post-2009 pandemic reporting.

Reviewer #1 (Recommendations For The Authors): 

Specific comments: 

(1) Line 155-156. Request for a reference for: "Given that protective immunity wanes after 1-4 years" 

We now include two references (He et al. 2015 and Wraith et al. 2022), which were cited at the beginning of the introduction when referring to the duration of protective immunity for antigenically homologous viruses. (Lines 640-642 in revised manuscript)

(2) Line 162-163: Request a further explanation of the negative correlation between seasonal diversity of HA and NA LBI values and NA epitope distance. Clarify biological implications to aid reader understanding. 

In the revised manuscript we expand on the biological implications of A(H3N2) virus populations characterized by high antigenic novelty and low LBI diversity.

Lines 649-653:

“The seasonal diversity of HA and NA LBI values was negatively correlated with NA epitope distance (Figure 2 – figure supplements 5 – 6), with high antigenic novelty coinciding with low genealogical diversity. This association suggests that selective sweeps tend to follow the emergence of drifted variants with high fitness, resulting in seasons dominated by a single A(H3N2) variant rather than multiple cocirculating clades.”

(3) Figure S3 legend t-2 may be marked as t-1. 

Thank you for catching this. We have fixed this typo. Note: Figure S3 is now Figure 2 – figure supplement 5.

(4) Lines 201-214. The key takeaways from the analysis of subtype dominance are ultimately not clear. It also misses the underlying dynamics that H3N2 predominance following an evolutionary change has waned since 2009.

In the revised manuscript we elaborate on key takeaways concerning the relationship between antigenic drift and A(H3N2) dominance. We also add a caveat noting that A(H3N2) predominance is weaker during the post-2009 period, which may be linked to the diversification of A(H3N2) lineages after 2012. We do not know of a reference that links the diversification of A(H3N2) viruses in the 2010s to a particular evolutionary change. Therefore, we do not attribute the diversification of A(H3N2) viruses to a specific evolutionary change in A(H3N2) variants circulating at the time (A/Perth/16/2009-like strains (PE09)). Instead, we allude to the potential role of A(H3N2) diversification in creating multiple co-circulating lineages that may have less of a fitness advantage.

Lines 681-703:

“We explored whether evolutionary changes in A(H3N2) may predispose this subtype to dominate influenza virus circulation in a given season. A(H3N2) subtype dominance – the proportion of influenza positive samples typed as A(H3N2) – increased with H3 epitope distance (t – 2) (R2 = 0.32, P = 0.05) and N2 epitope distance (t – 1) (R2 = 0.34, P = 0.03) (regression results: Figure 4; Spearman correlations: Figure 3 – figure supplement 1). Figure 4 illustrates this relationship at the regional level across two seasons in which A(H3N2) was nationally dominant, but where antigenic change differed. In 2003-2004, we observed widespread dominance of A(H3N2) viruses after the emergence of the novel antigenic cluster, FU02 (A/Fujian/411/2002-like strains). In contrast, there was substantial regional heterogeneity in subtype circulation during 2007-2008, a season in which A(H3N2) viruses were antigenically similar to those circulating in the previous season. Patterns in type/subtype circulation across all influenza seasons in our study period are shown in Figure 4 – figure supplement 1. As observed for the 2003-2004 season, widespread A(H3N2) dominance tended to coincide with major antigenic transitions (e.g.,

A/Sydney/5/1997 (SY97) seasons, 1997-1998 to 1999-2000; A/California/7/2004 (CA04) season, 20042005), though this was not universally the case (e.g., A/Perth/16/2009 (PE09) season, 2010-2011). 

After the 2009 A(H1N1) pandemic, A(H3N2) dominant seasons still occurred more frequently than A(H1N1) dominant seasons, but the mean fraction of influenza positive cases typed as A(H3N2) in A(H3N2) dominant seasons was lower compared to A(H3N2) dominant seasons prior to 2009. Antigenically distinct 3c.2a and 3c.3a viruses began to co-circulate in 2012 and underwent further diversification during subsequent seasons in our study (https://nextstrain.org/seasonal-

flu/h3n2/ha/12y@2024-05-13) (Dhanasekaran et al., 2022; Huddleston et al., 2020; Yan et al., 2019). The decline in A(H3N2) predominance during the post-2009 period may be linked to the genetic and antigenic diversification of A(H3N2) viruses, wherein multiple lineages with similar fitness co-circulated in each season.”

(5) Line 253-255: It would be beneficial to provide a more detailed interpretation of the statement that "pre-2009 seasonal A(H1N1) viruses may limit the circulation of A(H3N2) viruses to a greater extent than A(H1N1)pdm09 viruses." Elaborate on the cause-and-effect relationship within this statement.

In the revised manuscript we suggest that seasonal A(H1N1) viruses may interfere with the circulation of A(H3N2) viruses to a greater extent than A(H1N1)pdm09 viruses, because seasonal A(H1N1) viruses and A(H3N2) are more closely related, and thus may elicit stronger cross-reactive T cell responses.

Lines 738-745:

“The internal gene segments NS, M, NP, PA, and PB2 of A(H3N2) viruses and pre-2009 seasonal A(H1N1) viruses share a common ancestor (Webster et al., 1992) whereas A(H1N1)pdm09 viruses have a combination of gene segments derived from swine and avian reservoirs that were not reported prior to the 2009 pandemic (Garten et al., 2009; Smith et al., 2009). Non-glycoprotein genes are highly conserved between influenza A viruses and elicit cross-reactive antibody and T cell responses (Grebe et al., 2008; Sridhar, 2016). Because pre-2009 seasonal A(H1N1) viruses and A(H3N2) are more closely related, we hypothesized that seasonal A(H1N1) viruses could potentially limit the circulation of A(H3N2) viruses to a greater extent than A(H1N1)pdm09 viruses, due to greater T cell-mediated cross-protective immunity.”

(6) In the results section, many statements report statistical results of correlation analyses. Consider providing further interpretations of these results, such as the implications of nonsignificant correlations and how they support or contradict the hypothesis or previous studies. For example, the statement on line 248 regarding the lack of significant correlation between influenza B epidemic size and A(H3N2) epidemic metrics would benefit from additional discussion on what this non-significant correlation signifies and how it relates to the hypothesis or previous research. 

In the Discussion section, we suggest that the lack of an association between influenza B circulation and A(H3N2) epidemic metrics is due to few T and B cell epitopes shared between influenza A and B viruses (Terajima et al., 2013).

Lines 1005-1007 in revised manuscript (Lines 513-515 in original manuscript): 

“Overall, we did not find any indication that influenza B incidence affects A(H3N2) epidemic burden or timing, which is not unexpected, given that few T and B cell epitopes are shared between the two virus types (Terajima et al., 2013).”

Minor comments: 

(1) Line 116-122: Include a summary statistical description of all collected data sets, detailing the number of HA and NA sequence data and their sources. Briefly describe subsampled data sets, specifying preferences (e.g., the number of HA or NA sequence data collected from each region). 

In our revised manuscript we now include supplementary tables that summarize the number of A/H3 and

A/N2 sequences in each subsampled dataset, aggregated by world region, for all seasons combined (Figure 2 - table supplements 1 - 2). We also include supplementary figures showing the number of sequences collected in each month and each season in North America versus the other nine world regions combined (Figure 2 - figure supplements 1 - 2). Subsampled datasets are plotted individually in the figures below but individual time series are difficult to discern due to minor differences in sequence counts across the datasets.

(2) Figure 7A: Due to space limitations, consider rounding numbers on the x-axis to whole numbers for clarity. 

Thank you for this suggestion. In the revised manuscript we round numbers in the axes of Figure 7A (Figure 9A in the revised manuscript) so that the axes are less crowded.

(3) Figure 4C & Figure 4D: Note that Region 10 (purple) data were unavailable for seasons before 2009 (lines 1483-1484). Label each region on the map with its respective region number (1 to 10) and indicate this in the legend for easy identification. 

In our original submission, the legend for Figure 4 included “Data for Region 10 (purple) were not available for seasons prior to 2009” at the end of the caption. We have moved this sentence, as well as other descriptions that apply to both C and D, so that they follow the sentence “C-D. Regional patterns of influenza type and subtype incidence during two seasons when A(H3N2) was nationally dominant.”

In our revised manuscript, Figure 4, and Figure 4 - figure supplement 1 (Figure S10 in original submission) include labels for each HHS region.

We did not receive specific recommendations from Reviewer #2. However, our responses to Reviewer #3 addresses the study’s weaknesses mentioned by Reviewer #2.

Reviewer #3 (Recommendations For The Authors): 

This paper explores the relationships among evolutionary and epidemiological quantities in influenza, using a wide range of datasets and features, and using both correlations and random forests to examine, primarily, what are the drivers of influenza epidemics. 

This is a work horse of paper, in the volumes of data that are analyzed and the extensive analysis that is done. The data that are provided are a treasure trove resource for influenza modelers and for anyone interested in seeing influenza surveillance data in the context of evolution, and evolutionary information in the context of epidemiology. 

L53 - end of sentence "and antigenic drift": not sure this fits, explain? I thought this sentence was in contrast to antigenic drift.

Thank you for catching this. We did not intend to include “and antigenic drift” at the end of this sentence and have removed it (Line 59).

Para around L115: would using primarily US data be a limitation, because it's global immunity that shapes success of strains? Or, how much does each country's immunity and vaccination and so on actually shape what strains succeed there, compared to global/international factors? 

The HA and NA phylogenetic trees in our study are enriched with US sequences because our study focuses on epidemiological dynamics in the US, and we wanted to prioritize A(H3N2) viruses that the US human population encountered in each season. We agree with the reviewer that the world population may be the right scale to understand how immunity, acquired by vaccination or natural infection, may shape the emergence and success of new lineages that will go on to circulate globally. However, our study assesses the overall impact of antigenic drift on regional A(H3N2) epidemic dynamics in the US. In other words, our driving question is whether we can predict the population-level impact of an A(H3N2) variant in the US, conditional on this particular lineage having established in the US and circulating at relatively high levels. We do not assess the global or population-level factors that may influence which A(H3N2) virus lineages are successful in a given location or season.

We have added a clarifying sentence to the end of the Introduction to narrow the scope of the paper for the reader. 

Line 114-116: “Rather than characterize in situ evolution of A(H3N2) lineages circulating in the U.S., we study the epidemiological impacts of antigenic drift once A(H3N2) variants have arrived on U.S. soil and managed to establish and circulate at relatively high levels.”

In the Results section, I found the format hard to follow, because of the extensive methodological details, numbers with CIs and long sentences. Sentences sometimes included the question, definitions of variables, and lists. For example at line 215 we have: "Next, we tested for associations between A(H3N2) evolution and epidemic timing, including onset week, defined as the winter changepoint in incidence [16], and peak week, defined as the first week of maximum incidence; spatiotemporal synchrony, measured as the variation (standard deviation, s.d.) in regional onset and peak timing; and epidemic speed, including seasonal duration and the number of weeks from onset to peak (Table 2, Figure S11)". I would suggest putting the methods section first, using shorter sentences, separating lists from the question being asked, and stating what was found without also putting in all the extra detail. Putting the methods section before the results might reduce the sense that you have to explain what you did and how in the results section too.

Thank you for suggesting how to improve the readability of the Results section. In the revised manuscript, we follow the reviewer’s advice to put the Methods section before the Results section. Although eLife formatting requirements specify the order: Introduction, Results, Discussion, and Methods, the journal allows for the Methods section to follow the Introduction when it makes sense to do so. We agree with the reviewer that putting the Methods section before the Results section makes our results easier to follow because we no longer need to introduce methodological details at the beginning of each set of results.

L285 in the RF you remove variables without significant correlations with the target variables, but isn't one of the aims of RF to uncover relationships where a correlation might not be evident, and in part to reveal combinations of features that give the targeted outcome? Also with the RF, I am a bit concerned that you could not use the leave-one-out approach because it was "unstable" - presumably that means that you obtain quite different results if you leave out a season. How robust are these results, and what are the most sensitive aspects? Are the same variables typically high in importance if you leave out a season, for example? What does the scatterplot of observed vs predicted epidemic size (as in Fig 7) look like if each prediction is for the one that was left out (i.e. from a model trained on all the rest)? In my experience, where the RF is "unstable", that can look pretty terrible even if the model trained on all the data looks great (as does Figure 7). In any case I think it's worth discussing sensitivity.

(1) In response to the reviewer’s first question, we explain our rationale for not including all candidate predictors in random forest and penalized regression models. 

Models trained with different combinations of predictors can have similar performance, and these combinations of predictors can include variables that do not necessarily have strong univariate associations with the target variable. The performance of random forest and LASSO regression models are not sensitive to redundant or irrelevant predictors (see Figure 10.2 in Kuhn & Johnson, 2019). However,  if our goal is variable selection rather than strictly model performance, it is considered best practice to remove collinear, redundant, and/or irrelevant variables prior to training models (see section 11.3 in Kuhn & Johnson, 2019). In both random forest and LASSO regression models, if there are highly collinear variables that are useful for predicting the target variable, the predictor chosen by the model becomes a random selection. In random forest models, these highly collinear variables will be used in all splits across the forest of decision trees, and this redundancy dilutes variable importance scores. Thus, failing to minimize multicollinearity prior to model training could result in some variables having low rankings and the appearance of being unimportant, because their importance scores are overshadowed by those of the highly correlated variables. Our rationale for preprocessing predictor data follows the philosophy of Kuhn & Johnson, 2019, who recommend including the minimum possible set of variables that does not compromise model performance. Even if a particular model is insensitive to extra predictors, Kuhn and John explain that “removing predictors can reduce the cost of acquiring data or improve the throughput of the software used to make predictions.”

In the revised manuscript, we include more details about our steps for preprocessing predictor data. We also follow the reviewer’s suggestion to include all evolutionary predictors in variable selection analyses, regardless of whether they have strong univariate correlations with target outcomes, because the performance of random forest and LASSO regression models is not affected by redundant predictors. 

Including additional predictors in our variable selection analyses does not change our conclusions. As reported in our original manuscript, predictors with strong univariate correlations with various epidemic metrics were the highest ranked features in both random forest and LASSO regression models.

Lines 523-563:

“Preprocessing of predictor data: The starting set of candidate predictors included all viral fitness metrics: genetic and antigenic distances between current and previously circulating strains and the standard deviation and Shannon diversity of H3 and N2 LBI values in the current season. To account for potential type or subtype interference, we included A(H1N1) or A(H1N1)pdm09 epidemic size and B epidemic size in the current and prior season and the dominant IAV subtype in the prior season (Lee et al., 2018). We included A(H3N2) epidemic size in the prior season as a proxy for prior natural immunity to A(H3N2). To account for vaccine-induced immunity, we considered four categories of predictors and included estimates for the current and prior seasons: national vaccination coverage among adults (18-49 years coverage × ≥ 65 years coverage), adjusted A(H3N2) vaccine effectiveness (VE), a combined metric of vaccination coverage and A(H3N2) VE (18-49 years coverage × ≥ 65 years coverage × VE), and H3 and N2 epitope distances between naturally circulating A(H3N2) viruses and the U.S. A(H3N2) vaccine strain in each season. We could not include a predictor for vaccination coverage in children or consider cladespecific VE estimates, because these data were not available for most seasons in our study.

Random forest and LASSO regression models are not sensitive to redundant (highly collinear) features (Kuhn & Johnson, 2019), but we chose to downsize the original set of candidate predictors to minimize the impact of multicollinearity on variable importance scores. For both types of models, if there are highly collinear variables that are useful for predicting the target variable, the predictor chosen by the model becomes a random selection (Kuhn & Johnson, 2019). In random forest models, these highly collinear variables will be used in all splits across the forest of decision trees, and this redundancy dilutes variable importance scores (Kuhn & Johnson, 2019). We first confirmed that none of the candidate predictors had zero variance or near-zero variance. Because seasonal lags of each viral fitness metric are highly collinear, we included only one lag of each evolutionary predictor, with a preference for the lag that had the strongest univariate correlations with various epidemic metrics. We checked for multicollinearity among the remaining predictors by examining Spearman’s rank correlation coefficients between all pairs of predictors. If a particular pair of predictors was highly correlated (Spearman’s 𝜌 > 0.8), we retained only one predictor from that pair, with a preference for the predictor that had the strongest univariate correlations with various epidemic metrics. Lastly, we performed QR decomposition of the matrix of remaining predictors to determine if the matrix is full rank and identify sets of columns involved in linear dependencies. This step did not eliminate any additional predictors, given that we had already removed pairs of highly collinear variables based on Spearman correlation coefficients. 

After these preprocessing steps, our final set of model predictors included 21 variables, including 8 viral evolutionary indicators: H3 epitope distance (t – 2), HI log2 titer distance (t – 2), H3 RBS distance (t – 2), H3 non-epitope distance (t – 2), N2 epitope distance (t – 1), N2 non-epitope distance (t – 1), and H3 and N2 LBI diversity (s.d.) in the current season; 6 proxies for type/subtype interference and prior immunity:

A(H1N1) and B epidemic sizes in the current and prior season, A(H3N2) epidemic size in the prior season, and the dominant IAV subtype in the prior season; and 7 proxies for vaccine-induced immunity: A(H3N2) VE in the current and prior season, H3 and N2 epitope distances between circulating strains and the vaccine strain in each season, the combined metric of adult vaccination coverage × VE in the current and prior season, and adult vaccination coverage in the prior season.”

(2) Next, we clarify our model training methodology to address the reviewer’s second point about using a leave-one-out cross-validation approach.

We believe the reviewer is mistaken; we use a leave-one-season-out validation approach which lends some robustness to the predictions. In our original submission, we stated “We created each forest by generating 3,000 regression trees from 10 repeats of a leave-one-season-out (jackknife) cross-validated sample of the data. Due to the small size of our dataset, evaluating the predictive accuracy of random forest models on a quasi-independent test set produced unstable estimates.” (Lines 813-816 in the original manuscript)

To clarify, we use leave-one-season-out cross-validation to train models and measure model performance, wherein each “assessment” set contains one season of data (predicted by the model), and the corresponding “analysis” set (“fold”) contains the remaining seasons. This approach is roughly analogous to splitting data into training and test sets, but all seasons are used at some point in the training of the model (see Section 3.4 in Kuhn & Johnson, 2019). To reduce noise, we generated 10 bootstrap resamples of each fold and averaged the RMSE and R2 values of model predictions from resamples. 

Although it would be ideal and best practice to measure model performance with an independent test set, our dataset includes only ~20 seasons. We found that predictions of independent test sets of 2-3 seasons had unstable performance, which indicates we do not have sufficient power to measure model performance with a test set this small. Further, we suspect that large antigenic jumps in a small subset of seasons further contribute to variation in prediction accuracy across randomly selected test sets. Our rationale for using cross-validation instead of an independent test set is best described in Section 4.3 of Kuhn and Johnson’s book “Applied Predictive Modeling” (Kuhn & Johnson, 2013):

“When the number of samples is not large, a strong case can be made that a test set should be avoided because every sample may be needed for model building. Additionally, the size of the test set may not have sufficient power or precision to make reasonable judgements. Several researchers (Molinaro 2005; Martin and Hirschberg 1996; Hawkins et al. 2003) show that validation using a single test set can be a poor choice. Hawkins et al. (2003) concisely summarize this point: “holdout samples of tolerable size [...] do not match the cross-validation itself for reliability in assessing model fit and are hard to motivate. “Resampling methods, such as cross-validation, can be used to produce appropriate estimates of model performance using the training set. These are discussed in length in Sect.4.4. Although resampling techniques can be misapplied, such as the example shown in Ambroise and McLachlan (2002), they often produce performance estimates superior to a single test set because they evaluate many alternate versions of the data.”

In our revised manuscript, we provide additional clarification of our methods (Lines 574-590):

“We created each forest by generating 3,000 regression trees. To determine the best performing model for each epidemic metric, we used leave-one-season-out (jackknife) cross-validation to train models and measure model performance, wherein each “assessment” set is one season of data predicted by the model, and the corresponding “analysis” set contains the remaining seasons. This approach is roughly analogous to splitting data into training and test sets, but all seasons are used at some point in the training of each model (Kuhn & Johnson, 2019). Due to the small size of our dataset (~20 seasons), evaluating the predictive accuracy of random forest models on a quasi-independent test set of 2-3 seasons produced unstable estimates. Instead of testing model performance on an independent test set, we generated 10 bootstrap resamples (“repeats”) of each analysis set (“fold”) and averaged the predictions of models trained on resamples (Kuhn & Johnson, 2013, 2019). For each epidemic metric, we report the mean root mean squared error (RMSE) and R2 of predictions from the best tuned model. We used permutation importance (N = 50 permutations) to estimate the relative importance of each predictor in determining target outcomes. Permutation importance is the decrease in prediction accuracy when a single feature (predictor) is randomly permuted, with larger values indicating more important variables. Because many features were collinear, we used conditional permutation importance to compute feature importance scores, rather than the standard marginal procedure (Altmann et al., 2010; Debeer & Strobl, 2020; Strobl et al., 2008; Strobl et al., 2007).”

(3) In response to the reviewer’s question about the sensitivity of results when one season is left out, we clarify that the variable importance scores in Figure 8 and model predictions in Figure 9 were generated by models tuned using leave-one-season-out cross-validation. 

As explained above, in our leave-one-season-out cross-validation approach, each “assessment” set contains one season of data predicted by the model, and the corresponding “analysis” set (“fold”) contains the remaining seasons. We generated predictions of epidemic metrics and variable importance rankings by averaging the model output of 10 bootstrap resamples of each cross-validation fold. 

In Lines 791-806, we describe which epidemic metrics have the highest prediction accuracy and report that random forest models tend to underpredict most epidemic metrics in seasons with high antigenic novelty:

“We measured correlations between observed values and model-predicted values at the HHS region level. Among the various epidemic metrics, random forest models produced the most accurate predictions of A(H3N2) subtype dominance (Spearman’s 𝜌 = 0.95, regional range = 0.85 – 0.97), peak incidence (𝜌 = 0.91, regional range = 0.72 – 0.95), and epidemic size (𝜌 = 0.9, regional range = 0.74 – 0.95), while predictions of effective 𝑅! and epidemic intensity were less accurate (𝜌 = 0.81, regional range = 0.65 – 0.91; 𝜌 = 0.78, regional range = 0.63 – 0.92, respectively) (Figure 9). Random forest models tended to underpredict most epidemic targets in seasons with substantial H3 antigenic transitions, in particular the SY97 cluster seasons (1998-1999, 1999-2000) and the FU02 cluster season (2003-2004) (Figure 9). 

For epidemic size and peak incidence, seasonal predictive error – the root-mean-square error (RMSE) across all regional predictions in a season – increased with H3 epitope distance (epidemic size, Spearman’s 𝜌 = 0.51, P = 0.02; peak incidence, 𝜌 = 0.63, P = 0.004) and N2 epitope distance (epidemic size, 𝜌 = 0.48, P = 0.04; peak incidence, 𝜌 = 0.48, P = 0.03) (Figure 9 – figure supplements 1 – 2). For models of epidemic intensity, seasonal RMSE increased with N2 epitope distance (𝜌 = 0.64, P = 0.004) but not H3 epitope distance (𝜌 = 0.06, P = 0.8) (Figure 9 – figure supplements 1 – 2). Seasonal RMSE of effective 𝑅! and subtype dominance predictions did not correlate with H3 or N2 epitope distance (Figure 9 – figure supplements 1 – 2).”

I think the competition (interference) results are really interesting, perhaps among the most interesting aspects of this work. 

Thank you! We agree that our finding that subtype interference has a greater impact than viral evolution on A(H3N2) epidemics is one of the more interesting results in the study.

Have you seen the paper by Barrat-Charlaix et al? They found that LBI was not good predicting frequency dynamics (see https://pubmed.ncbi.nlm.nih.gov/33749787/); instead, LBI was high for sequences like the consensus sequence, which was near to future strains. LBI also was not positively correlated with epidemic impact in Figure S7.

The local branching index (LBI) measures the rate of recent phylogenetic branching and approximates relative fitness among viral clades, with high LBI values representing greater fitness (Neher et al. 2014).

Two of this study’s co-authors (John Huddleston and Trevor Bedford) are also co-authors of BarratCharlaix et al. 2021. Barrat-Charlaix et al. 2021 assessed the performance of LBI in predicting the frequency dynamics and fixation of individual amino acid substitutions in A(H3N2) viruses. Our study is not focused on predicting the future success of A(H3N2) clades or the frequency dynamics or probability of fixation of individual substitutions. Instead, we use the standard deviation and Shannon diversity of LBI values in each season as a proxy for genealogical (clade-level) diversity. We find that, at a seasonal level, low diversity of H3 or N2 LBI values in the current season correlates with greater epidemic intensity, higher transmission rates, and shorter seasonal duration.

In the Discussion we provide an explanation for these correlation results (Lines 848-857): 

“The local branching index (LBI) is traditionally used to predict the success of individual clades, with high LBI values indicating high viral fitness (Huddleston et al., 2020; Neher et al., 2014). In our epidemiological analysis, low diversity of H3 or N2 LBI in the current season correlated with greater epidemic intensity, higher transmission rates, and shorter seasonal duration. These associations suggest that low LBI diversity is indicative of a rapid selective sweep by one successful clade, while high LBI diversity is indicative of multiple co-circulating clades with variable seeding and establishment times over the course of an epidemic. A caveat is that LBI estimation is more sensitive to sequence sub-sampling schemes than strain-level measures. If an epidemic is short and intense (e.g., 1-2 months), a phylogenetic tree with our sub-sampling scheme (50 sequences per month) may not incorporate enough sequences to capture the true diversity of LBI values in that season.”

Figure 1 - LBI goes up over time. Is that partly to do with sampling? Overall how do higher sampling volumes in later years impact this analysis? (though you choose a fixed number of sequences so I guess you downsample to cope with that). I note that LBI is likely to be sensitive to sequencing density. 

Thank you for pointing this out. We realized that increasing LBI Shannon diversity over the course of the study period was indeed an artefact of increasing sequence volume over time. Our sequence subsampling scheme involves selecting a random sample of up to 50 viruses per month, with up to 25 viruses selected from North America (if available) and the remaining sequences evenly divided across nine other global regions. In early seasons of the study (late 1990s/early 2000s), sampling was often too sparse to meet the 25 viruses/month threshold for North America or for the other global regions combined (H3: Figure 2 - figure supplement 1; N2: Figure 2 - figure supplement 2). Ecological diversity metrics are sensitive to sample size, which explains why LBI Shannon diversity appeared to steadily increase over time in our original submission. In our revised manuscript, we correct for uneven sample sizes across seasons before estimating Shannon diversity and clarify our methodology. 

Lines 443-482: 

“Clade growth: The local branching index (LBI) measures the relative fitness of co-circulating clades, with high LBI values indicating recent rapid phylogenetic branching (Huddleston et al., 2020; Neher et al., 2014). To calculate LBI for each H3 and N2 sequence, we applied the LBI heuristic algorithm as originally described by Neher et al., 2014 to H3 and N2 phylogenetic trees, respectively. We set the neighborhood parameter 𝜏 to 0.4 and only considered viruses sampled between the current season 𝑡 and the previous season 𝑡 – 1 as contributing to recent clade growth in the current season 𝑡.  

Variation in the phylogenetic branching rates of co-circulating A(H3N2) clades may affect the magnitude, intensity, onset, or duration of seasonal epidemics. For example, we expected that seasons dominated by a single variant with high fitness might have different epidemiological dynamics than seasons with multiple co-circulating clades with varying seeding and establishment times. We measured the diversity of clade growth rates of viruses circulating in each season by measuring the standard deviation (s.d.) and Shannon diversity of LBI values in each season. Given that LBI measures relative fitness among cocirculating clades, we did not compare overall clade growth rates (e.g., mean LBI) across seasons.

Each season’s distribution of LBI values is right-skewed and does not follow a normal distribution. We therefore bootstrapped the LBI values of each season in each replicate dataset 1000 times (1000 samples with replacement) and estimated the seasonal standard deviation of LBI from resamples, rather than directly from observed LBI values. We also tested the seasonal standard deviation of LBI from log transformed LBI values, which produced qualitatively equivalent results to bootstrapped LBI values in downstream analyses.

As an alternative measure of seasonal LBI diversity, we binned raw H3 and N2 LBI values into categories based on their integer values (e.g., an LBI value of 0.5 is assigned to the (0,1] bin) and estimated the exponential of the Shannon entropy (Shannon diversity) of LBI categories (Hill, 1973; Shannon, 1948). The Shannon diversity of LBI considers both the richness and relative abundance of viral clades with different growth rates in each season and is calculated as follows:  

where 𝑞 𝐷 is the effective number of categories or Hill numbers of order 𝑞 (here, clades with different growth rates), with 𝑞 defining the sensitivity of the true diversity to rare versus abundant categories (Hill,

1973). exp is the exponential function, 𝑝# is the proportion of LBI values belonging to the 𝑖th category, and 𝑅 is richness (the total number of categories). Shannon diversity 1𝐷 (𝑞 = 1) estimates the effective number of categories in an assemblage using the geometric mean of their proportional abundances 𝑝# (Hill, 1973).  

Because ecological diversity metrics are sensitive to sampling effort, we rarefied H3 and N2 sequence datasets prior to estimating Shannon diversity so that seasons had the same sample size. For each season in each replicate dataset, we constructed rarefaction and extrapolation curves of LBI Shannon diversity and extracted the Shannon diversity estimate of the sample size that was twice the size of the reference sample size (the smallest number of sequences obtained in any season during the study) (iNEXT R package) (Chao et al., 2014). Chao et al. found that their diversity estimators work well for rarefaction and short-range extrapolation when the extrapolated sample size is up to twice the reference sample size. For H3, we estimated seasonal diversity using replicate datasets subsampled to 360 sequences/season; For N2, datasets were subsampled to 230 sequences/season.”

Estimating the Shannon diversity of LBI from datasets with even sampling across seasons removes the previous secular trend of increasing LBI diversity over time (Figure 2 in revised manuscript).

Figure 3 - I wondered what about the co-dominant times? 

In Figure 3, orange points correspond to seasons in which A(H3N2) and A(H1N1) were codominant. We are not sure of the reviewer’s specific question concerning codominant seasons, but if it concerns whether antigenic drift is linked to epidemic magnitude among codominant seasons alone, we cannot perform separate regression analyses for these seasons because there are only two codominant seasons during the 22 season study period.

Figure 4 - Related to drift and epidemic size, dominance, etc. -- when is drift measured, and (if it's measured in season t), would larger populations create more drift, simply by having access to more opportunity (via a larger viral population size)? This is a bit 'devil's advocate' but what if some epidemiological/behavioural process causes a larger and/or later peak, and those gave rise to higher drift?

Seasonal drift is measured as the genetic or antigenic distance between viruses circulating during season t and viruses circulating in the prior season (𝑡 – 1) or two seasons ago (𝑡 – 2).

Concerning the question about whether larger human populations lead to greater rates of antigenic drift, phylogeographic studies have repeatedly found that East-South-Southeast Asia are the source populations for A(H3N2) viruses (Bedford et al., 2015; Lemey et al., 2014), in part because these regions have tropical or subtropical climates and larger human populations, which enable year-round circulation and higher background infection rates. Larger viral populations (via larger host population sizes) and uninterrupted transmission may increase the efficiency of selection and the probability of strain survival and global spread (Wen et al., 2016). After A(H3N2) variants emerge in East-South-Southeast Asia and spread to other parts of the world, A(H3N2) viruses circulate via overlapping epidemics rather than local persistence (Bedford et al., 2015; Rambaut et al., 2008). Each season, A(H3N2) outbreaks in the US (and other temperate regions) are seeded by case importations from outside the US, genetic diversity peaks during the winter, and a strong genetic bottleneck typically occurs at the end of the season (Rambaut et al., 2008).

Due to their faster rates of antigenic evolution, A(H3N2) viruses undergo more rapid clade turnover and dissemination than A(H1N1) and B viruses, despite similar global migration networks across A(H3N2), A(H1N1), and B viruses (Bedford et al., 2015). Bedford et al. speculate that there is typically little geographic differentiation in A(H3N2) viruses circulating in each season because A(H3N2) viruses tend to infect adults, and adults are more mobile than children. Compared to A(H3N2) viruses, A(H1N1) and B viruses tend to have greater genealogical diversity, geographic differentiation, and longer local persistence times (Bedford et al., 2015; Rambaut et al., 2008). Thus, some A(H1N1) and B epidemics are reseeded by viruses that have persisted locally since prior epidemics (Bedford et al., 2015).

Theoretical models have shown that epidemiological processes can influence rates of antigenic evolution (Recker et al., 2007; Wen et al., 2016; Zinder et al., 2013), though the impact of flu epidemiology on viral evolution is likely constrained by the virus’s intrinsic mutation rate. 

In conclusion, larger host population sizes and flu epidemiology can indeed influence rates of antigenic evolution. However, given that our study is US-centric and focuses on A(H3N2) viruses, these factors are likely not at play in our study, due to intrinsic biological characteristics of A(H3N2) viruses and the geographic location of our study.

We have added a clarifying sentence to the end of the Introduction to narrow the scope of the paper for the reader.

Line 114-116: “Rather than characterize in situ evolution of A(H3N2) lineages circulating in the U.S., we study the epidemiological impacts of antigenic drift once A(H3N2) variants have arrived on U.S. soil and managed to establish and circulate at relatively high levels.”

Methods -- 

L 620 about rescaling and pre- vs post-pandemic times : tell us more - how has reporting changed? could any of this not be because of reporting but because of NPIs or otherwise? Overall there is a lot of rescaling going on. How sensitive are the results to it? 

it would be unreasonable to ask for a sensitivity analysis for all the results for all the choices around data preparation, but some idea where there is a reason to think there might be a dependence on one of these choices would be great.

In response to the 2009 A(H1N1) pandemic, the US CDC and WHO increased laboratory testing capacity and strengthened epidemiological networks, leading to substantial, long-lasting improvements to influenza surveillance that are still in place today (https://www.cdc.gov/flu/weekly/overview.htm). At the beginning of the COVID-19 pandemic, influenza surveillance networks were quickly adapted to detect and understand the spread of SARS-CoV-2. The 2009 pandemic occurred over a time span of less than one year, and strict non-pharmaceutical interventions (NPIs), such as lockdowns and mask mandates, were not implemented. Thus, we attribute increases in test volume during the post-2009 period to improved virologic surveillance and laboratory testing capacity rather than changes in care-seeking behavior. In the revised manuscript, we include a figure (Figure 1 - figure supplement 2) that shows systematic increases in test volume in all HHS regions after the 2009 pandemic.

Given the substantial increase in influenza test volume after 2009, we opted to keep the time trend adjustment for the pre- and post-2009 pandemic periods and evaluate whether adjusting for regional reporting differences affects our results. When estimating univariate correlations between various

A(H3N2) epidemic metrics and evolutionary indicators, we found qualitatively equivalent results for Spearman correlations and regression models, when adjusting for the pre- and post-2009 pandemic time periods and regional reporting versus only adjusting for the pre-/post-2009 pandemic time periods. Below, we share adjusted versions of Figure 3 (regression results) and Figure 3 - figure supplement 1 (Spearman correlations). Each figure only adjusts for differences in pre- and post-2009 pandemic reporting.

Author response image 1.

Adjustment for pre- and post-2009 pandemic only

Author response image 2.

Adjustment for pre- and post-2009 pandemic only

L635 - Why discretize the continuous LBI distribution and then use Shannon entropy when you could just use the variance and/or higher moments? (or quantiles)? Similarly, why not use the duration of the peak, rather than Shannon entropy? (though there, because presumably data are already binned weekly, and using duration would involve defining start and stop times, it's more natural than with LBI)

We realize that we failed to mention in the methods that we calculated the standard deviation of LBI in each season, in addition to the exponential of the Shannon entropy (Shannon diversity) of LBI. Both the Shannon diversity of LBI values and the standard deviation of LBI values were negatively correlated with effective Rt and epidemic intensity and positively correlated with seasonal duration. The two measures were similarly correlated with effective Rt and epidemic intensity (Figure 3 - figure supplements 2 - 3), while the Shannon diversity of LBI had slightly stronger correlations with seasonal duration than s.d. LBI (Figure 5). Thus, both measures of LBI diversity appear to capture potentially biologically important heterogeneities in clade growth rates.

Separately, we use the inverse Shannon entropy of the incidence distribution to measure the spread of an A(H3N2) epidemic during the season, following the methods of Dalziel et al. 2018. The peak of an epidemic is a single time point at which the maximum incidence occurs. We have not encountered “the duration of the peak” before in epidemiology terminology, and, to our knowledge, there is not a robust way to measure the “duration of a peak,” unless one were to measure the time span between multiple points of maximum incidence or designate an arbitrary threshold for peak incidence that is not strictly the maximum incidence. Given that Shannon entropy is based on the normalized incidence distribution over the course of the entire influenza season (week 40 to week 20), it does not require designating an arbitrary threshold to describe epidemic intensity.

L642 - again why normalize epidemic intensities, and how sensitive are the results to this? I would imagine given that the RF results were unstable under leave-one-out analysis that some of those results could be quite sensitive to choices of normalization and scaling.

Epidemic intensity, defined as the inverse Shannon entropy of the incidence distribution, measures the spread of influenza cases across the weeks in a season. Following Dalziel et al. 2018, we estimated epidemic intensity from normalized incidence distributions rather than raw incidences so that epidemic intensity is invariant under differences in reporting rates and/or attack rates across regions and seasons. If we were to use raw incidences instead, HHS regions or seasons could have the appearance of greater or lower epidemic intensity (i.e., incidence concentrated within a few weeks or spread out over several weeks), due to differences in attack rates or test volume, rather than fundamental differences in the shapes of their epidemic curves. In other words, epidemic intensity is intended to measure the shape and spread of an epidemic, regardless of the actual volume of cases in a given region or season.

In the methods section, we provide further clarification for why epidemic intensities are based on normalized incidence distributions rather than raw incidences.

Lines 206-209: “Epidemic intensity is intended to measure the shape and spread of an epidemic, regardless of the actual volume of cases in a given region or season. Following the methodology of Dalziel et al. 2018, epidemic intensity values were normalized to fall between 0 and 1 so that epidemic intensity is invariant to differences in reporting rates and/or attack rates across regions and seasons.”  

L643 - more information about what goes into Epidemia (variables, priors) such that it's replicable/understandable without the code would be good. 

We now include additional information concerning the epidemic models used to estimate Rt, including all model equations, variables, and priors (Lines 210-276 in Methods).

L667 did you do breakpoint detection? Why linear models? Was log(incidence) used? 

In our original submission, we estimated epidemic onsets using piecewise regression models (Lines 666674 in original manuscript), which model non-linear relationships with breakpoints by iteratively fitting linear models (Muggeo, 2003). Piecewise regression falls under the umbrella of parametric methods for breakpoint detection.

We did not include results from linear models fit to log(incidence) or GLMs with Gaussian error distributions and log links, due to two reasons. First, models fit to log-transformed data require non-zero values as inputs. Although breakpoint detection does not necessarily require weeks of zero incidence leading up to the start of an outbreak, limiting the time period for breakpoint detection to weeks with nonzero incidence (so that we could use log transformed incidence) substantially pushed back previous more biologically plausible estimates of epidemic onset weeks. Second, as an alternative to limiting the dataset to weeks with non-zero incidence, we tried adding a small positive number to weekly incidences so that we could fit models to log transformed incidence for the whole time period spanning epidemic week 40 (the start of the influenza season) to the first week of maximum incidence. Fitting models to log

transformed incidences produced unrealistic breakpoint locations, potentially because log transformations 1) linearize data, and 2) stabilize variance by reducing the impact of extreme values. Due to the short time span used for breakpoint detection, log transforming incidence diminishes abrupt changes in incidence at the beginning of outbreaks, making it difficult for models to estimate biologically plausible breakpoint locations. Log transformations of incidence may be more useful when analyzing time series spanning multiple seasons, rather than short time spans with sharp changes in incidence (i.e., the exponential growth phase of a single flu outbreak).

As an alternative to piecewise regression, our revised manuscript also estimates epidemic onsets using a Bayesian ensemble algorithm that accounts for the time series nature of incidence data and allows for complex, non-linear trajectories interspersed with change points (BEAST - a Bayesian estimator of Abrupt change, Seasonal change, and Trend; Zhao et al., 2019). Although a few regional onset time times differed across the two methods, our conclusions did not change concerning correlations between viral fitness and epidemic onset timing.

We have rewritten the methods section for estimating epidemic onsets to clarify our methodology and to include the BEAST method (Lines 292-308):

“We estimated the regional onsets of A(H3N2) virus epidemics by detecting breakpoints in A(H3N2) incidence curves at the beginning of each season. The timing of the breakpoint in incidence represents epidemic establishment (i.e., sustained transmission) rather than the timing of influenza introduction or arrival (Charu et al., 2017). We used two methods to estimate epidemic onsets: 1) piecewise regression, which models non-linear relationships with break points by iteratively fitting linear models to each segment (segmented R package) (Muggeo, 2008; Muggeo, 2003), and 2) a Bayesian ensemble algorithm (BEAST – a Bayesian estimator of Abrupt change, Seasonal change, and Trend) that explicitly accounts for the time series nature of incidence data and allows for complex, non-linear trajectories interspersed with change points (Rbeast R package) (Zhao et al., 2019). For each region in each season, we limited the time period of breakpoint detection to epidemic week 40 to the first week of maximum incidence and did not estimate epidemic onsets for regions with insufficient signal, which we defined as fewer than three weeks of consecutive incidence and/or greater than 30% of weeks with missing data. We successfully estimated A(H3N2) onset timing for most seasons, except for three A(H1N1) dominant seasons: 20002001 (0 regions), 2002-2003 (3 regions), and 2009-2010 (0 regions). Estimates of epidemic onset weeks were similar when using piecewise regression versus the BEAST method, and downstream analyses of correlations between viral fitness indicators and onset timing produced equivalent results. We therefore report results from onsets estimated via piecewise regression.”

L773 national indicators -- presumably this is because you don't have regional-level information, but it might be worth saying that earlier so it doesn't read like there are other indicators now, called national indicators, that we should have heard of 

In the revised manuscript, we move a paragraph that was at the beginning of the Results to the beginning of the Methods.

Lines 123-132: 

“Our study focuses on the impact of A(H3N2) virus evolution on seasonal epidemics from seasons 19971998 to 2018-2019 in the U.S.; whenever possible, we make use of regionally disaggregated indicators and analyses. We start by identifying multiple indicators of influenza evolution each season based on changes in HA and NA. Next, we compile influenza virus subtype-specific incidence time series for U.S. Department of Health and Human Service (HHS) regions and estimate multiple indicators characterizing influenza A(H3N2) epidemic dynamics each season, including epidemic burden, severity, type/subtype dominance, timing, and the age distribution of cases. We then assess univariate relationships between national indicators of evolution and regional epidemic characteristics. Lastly, we use multivariable regression models and random forest models to measure the relative importance of viral evolution, heterosubtypic interference, and prior immunity in predicting regional A(H3N2) epidemic dynamics.”

In Lines 484-487 in the Methods, we now mention that measures of seasonal antigenic and genetic distance are at the national level. 

“For each replicate dataset, we estimated national-level genetic and antigenic distances between influenza viruses circulating in consecutive seasons by calculating the mean distance between viruses circulating in the current season 𝑡 and viruses circulating during the prior season (𝑡 – 1 year; one season lag) or two prior seasons ago (𝑡 – 2 years; two season lag).”

L782 Why Beta regression and what is "the resampled dataset" ? 

Beta regression is appropriate for models of subtype dominance, epidemic intensity, and age-specific proportions of ILI cases because these data are continuous and restricted to the interval (0, 1) (Ferrari & Cribari-Neto, 2004). “The resampled dataset” refers to the “1000 bootstrap replicates of the original dataset (1000 samples with replacement)” mentioned in Lines 777-778 of the original manuscript. 

In the revised manuscript, we include more background information about Beta regression models, and explicitly mention that regression models were fit to 1000 bootstrap replicates of the original dataset.

Lines 503-507: 

“For subtype dominance, epidemic intensity, and age-specific proportions of ILI cases, we fit Beta regression models with logit links. Beta regression models are appropriate when the variable of interest is continuous and restricted to the interval (0, 1) (Ferrari & Cribari-Neto, 2004). For each epidemic metric, we fit the best-performing regression model to 1000 bootstrap replicates of the original dataset.”

The github is clear, comprehensive and well-documented, at least at a brief glance. 

Thank you! At the time of resubmission, our GitHub repository is updated to incorporate feedback from the reviewers.

References

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Author response:

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

Reviewer #1 (Public Review): 

Summary: 

The study by Klug et al. investigated the pathway specificity of corticostriatal projections, focusing on two cortical regions. Using a G-deleted rabies system in D1-Cre and A2a-Cre mice to retrogradely deliver channelrhodopsin to cortical inputs, the authors found that M1 and MCC inputs to direct and indirect pathway spiny projection neurons (SPNs) are both partially segregated and asymmetrically overlapping. In general, corticostriatal inputs that target indirect pathway SPNs are likely to also target direct pathway SPNs, while inputs targeting direct pathway SPNs are less likely to also target indirect pathway SPNs. Such asymmetric overlap of corticostriatal inputs has important implications for how the cortex itself may determine striatal output. Indeed, the authors provide behavioral evidence that optogenetic activation of M1 or MCC cortical neurons that send axons to either direct or indirect pathway SPNs can have opposite effects on locomotion and different effects on action sequence execution. The conclusions of this study add to our understanding of how cortical activity may influence striatal output and offer important new clues about basal ganglia function. 

The conceptual conclusions of the manuscript are supported by the data, but the details of the magnitude of afferent overlap and causal role of asymmetric corticostriatal inputs on behavioral outcomes were not yet fully resolved. 

We appreciate the reviewer’s thoughtful understanding and acknowledgment that the conceptual conclusion of asymmetric projections from the cortex to the striatum is well supported by our data. We also recognize the importance of further elucidating the extent of afferent overlap and the causal contributions of asymmetric corticostriatal inputs to behavioral outcomes. However, we respectfully note that current technical limitations pose significant challenges to addressing these questions with high precision.

In response to the reviewer’s comments, we have now clarified the sample size, added proper analysis and elaborated on the experimental design to ensure that our conclusions are presented more transparently and are more accessible to the reader.

After virally labeling either direct pathway (D1) or indirect pathway (D2) SPNs to optogenetically tag pathway-specific cortical inputs, the authors report that a much larger number of "non-starter" D2-SPNs from D2-SPN labeled mice responded to optogenetic stimulation in slices than "non-starter" D1 SPNs from D1-SPN labeled mice did. Without knowing the relative number of D1 or D2 SPN starters used to label cortical inputs, it is difficult to interpret the exact meaning of the lower number of responsive D2-SPNs in D1 labeled mice (where only ~63% of D1-SPNs themselves respond) compared to the relatively higher number of responsive D1-SPNs (and D2-SPNs) in D2 labeled mice. While relative differences in connectivity certainly suggest that some amount of asymmetric overlap of inputs exists, differences in infection efficiency and ensuing differences in detection sensitivity in slice experiments make determining the degree of asymmetry problematic. 

Thank you for highlighting this point. As it lies at the core of our manuscript, we agree that it is essential to present it clearly and convincingly. As shown by the statistics (Fig. 2B-F), non-starter D1- and D2-SPNs appear to receive fewer projections from D1-projecting cortical neurons (Input D1-record D1, 0.63; Input D1-record D2, 0.40) compared to D2-projecting cortical neurons (Input D2 - record D1, 0.73; Input D2 -record D2, 0.79).

While it is not technically feasible to quantify the number of infected cells in brain slices following electrophysiological recordings, we addressed this limitation by collecting data from multiple animals and restricting recordings to cells located within the injection sites. In Figure 2D, we used 7 mice in the D1-projecting to D1 EGFP(+) group, 8 mice in the D1-projecting to D2 EGFP(-) group, 10 mice in the D2-projecting to D2 EGFP(+) group, and 8 mice in the D2-projecting to D1 EGFP(-) group. In Figure 2G, the group sizes were as follows: 8 mice in the D1-projecting to D2 EGFP(+) group, 7 mice in the D1-projecting to D1 EGFP(-) group, 8 mice in the D2-projecting to D1 EGFP(+) group, and 10 mice in the D2-projecting to D2 EGFP(-) group. In both panels, connection ratios were compared using Fisher’s exact test. Comparisons were then made across experimental groups. Furthermore, as detailed in our Methods section (page 20, line 399-401), we assessed cortical expression levels prior to performing whole-cell recordings. Taken together, these precautions help ensure that the calculated connection ratios are unlikely to be confounded by differences in infection efficiency.

It is also unclear if retrograde labeling of D1-SPN- vs D2-SPN- targeting afferents labels the same densities of cortical neurons. This gets to the point of specificity in the behavioral experiments. If the target-based labeling strategies used to introduce channelrhodopsin into specific SPN afferents label significantly different numbers of cortical neurons, might the difference in the relative numbers of optogenetically activated cortical neurons itself lead to behavioral differences? 

Thank you for bringing this concern to our attention. While optogenetic manipulation has become a widely adopted tool in functional studies of neural circuits, it remains subject to several technical limitations due to the nature of its implementation. Factors such as opsin expression efficiency, optic fiber placement, light intensity, stimulation spread, and other variables can all influence the specificity and extent of neuronal activation or inhibition. As such, rigorous experimental controls are essential when interpreting the outcomes of optogenetic experiments.

In our study, we verified both the expression of channelrhodopsin in D1- or D2-projecting cortical neurons and the placement of the optic fiber following the completion of behavioral testing. To account for variability, we compared the behavioral effects of optogenetic stimulation within the same animals, stimulated versus non-stimulated conditions, as shown in Figures 3 and 4. Moreover, Figure S3 includes important controls that rule out the possibility that the behavioral effects observed were due to direct activation of D1- or D2-SPNs in striatum or to light alone in the cortex.

An additional point worth emphasizing is that the behavioral effects observed in the open field and ICSS tests cannot be attributed to differences in the number of neurons activated. Specifically, activation of D1-projecting cortical neurons promoted locomotion in the open field, whereas activation of D2-projecting cortical neurons did not. However, in the ICSS test, activation of both D1- and D2-projecting cortical neurons reinforced lever pressing. Given that only D1-SPN activation, but not D2-SPN activation, supports ICSS behavior, these effects are unlikely to result merely from differences in the number of neurons recruited.

This rationale underlies our use of multiple behavioral paradigms to examine the functions of D1- and D2-projecting cortical neurons. By assessing behavior across distinct tasks, we aimed to approach the question from multiple angles and reduce the likelihood of spurious or confounding effects influencing our interpretation.

In general, the manuscript would also benefit from more clarity about the statistical comparisons that were made and sample sizes used to reach their conclusions.

We thank the reviewer for the valuable suggestion to improve the manuscript. In response, we have made the following changes and provided additional clarification:

(1) In Figure 2D, we used 7 mice in the D1-projecting to D1 EGFP(+) group, 8 mice in the D1-projecting to D2 EGFP(-) group, 10 mice in the D2-projecting to D2 EGFP(+) group, and 8 mice in the D2-projecting to D1 EGFP(-) group. In Figure 2G, the group sizes were as follows: 8 mice in the D1-projecting to D2 EGFP(+) group, 7 mice in the D1-projecting to D1 EGFP(-) group, 8 mice in the D2-projecting to D1 EGFP(+) group, and 10 mice in the D2-projecting to D2 EGFP(-) group. In both panels, connection ratios were compared using Fisher’s exact test.

(2) In Figure 3, we reanalyzed the data in panels O, P, R, and S using permutation tests to assess whether each individual group exhibited a significant ICSS learning effect. The figure legend has been revised accordingly as follows:

(O-P) D1-SPN (red) but not D2-SPN stimulation (black) drives ICSS behavior in both the DMS (O: D1, n = 6, permutation test, slope = 1.5060, P = 0.0378; D2, n = 5, permutation test, slope = -0.2214, P = 0.1021; one-tailed Mann Whitney test, Day 7 D1 vs. D2, P = 0.0130) and the DLS (P: D1, n = 6, permutation test, slope = 28.1429, P = 0.0082; D2, n = 5, permutation test, slope = -0.3429, P = 0.0463; one-tailed Mann Whitney test, Day 7 D1 vs. D2, P = 0.0390). *, P < 0.05. (Q) Timeline of helper virus injections, rabies-ChR2 injections and optogenetic stimulation for ICSS behavior. (R-S) Optogenetic stimulation of the cortical neurons projecting to either D1- or D2-SPNs induces ICSS behavior in both the MCC (R: MCC-D1, n = 5, permutation test, Day1-Day7, slope = 2.5857, P = 0.0034; MCC-D2, n = 5, Day2-Day7, permutation test, slope = 1.4229, P = 0.0344; no significant effect on Day7, MCC-D1 vs. MCC-D2,  two-tailed Mann Whitney test, P = 0.9999) and the M1 (S: M1-D1, n = 5, permutation test, Day1-Day7, slope = 1.8214, P = 0.0259; M1-D2, n = 5, Day1-Day7, permutation test, slope = 1.8214, P = 0.0025; no significant effect on Day7, M1-D1 vs. M1-D2, two-tailed Mann Whitney test, P = 0.3810). n.s., not statistically significant.

(3) In Figure 4, we have added a comparison against a theoretical percentage change of zero to better evaluate the net effect of each manipulation. The results showed that in Figure 4D, optogenetic stimulation of D1-projecting MCC neurons significantly increased the pressing rate, whereas stimulation of D2-projecting MCC neurons did not (MCC-D1: n = 8, one-sample two-tailed t-test, t = 2.814, P = 0.0131; MCC-D2: n = 7, t = 0.8481, P = 0.4117). In contrast, in Figure 4H, optogenetic stimulation of both D1- and D2-projecting M1 neurons significantly increased the sequence press rate (M1-D1: n = 6, one-sample two-tailed Wilcoxon signed-rank test, P = 0.0046; M1-D2: n = 7, P = 0.0479).

Reviewer #2 (Public Review):

Summary: 

Klug et al. use monosynaptic rabies tracing of inputs to D1- vs D2-SPNs in the striatum to study how separate populations of cortical neurons project to D1- and D2-SPNs. They use rabies to express ChR2, then patch D1-or D2-SPNs to measure synaptic input. They report that cortical neurons labeled as D1-SPN-projecting preferentially project to D1-SPNs over D2-SPNs. In contrast, cortical neurons labeled as D2-SPN-projecting project equally to D1- and D2-SPNs. They go on to conduct pathway-specific behavioral stimulation experiments. They compare direct optogenetic stimulation of D1- or D2-SPNs to stimulation of MCC inputs to DMS and M1 inputs to DLS. In three different behavioral assays (open field, intra-cranial self-stimulation, and a fixed ratio 8 task), they show that stimulating MCC or M1 cortical inputs to D1-SPNs is similar to D1-SPN stimulation, but that stimulating MCC or M1 cortical inputs to D2-SPNs does not recapitulate the effects of D2-SPN stimulation (presumably because both D1- and D2-SPNs are being activated by these cortical inputs). 

Strengths: 

Showing these same effects in three distinct behaviors is strong. Overall, the functional verification of the consequences of the anatomy is very nice to see. It is a good choice to patch only from mCherry-negative non-starter cells in the striatum.

Thank you for your profound understanding and appreciation of our manuscript’s design and the methodologies employed. In the realm of neuroscience, quantifying synaptic connections is a formidable challenge. While the roles of the direct and indirect pathways in motor control have long been explored, the mechanism by which upstream cortical inputs govern these pathways remains shrouded in mystery at the circuitry level.

In the ‘Go/No-Go’ model, the direct and indirect pathways operate antagonistically; in contrast, the ‘Co-activation’ model suggests that they work cooperatively to orchestrate movement. These distinct theories raise a compelling question: Do these two pathways receive inputs from the same upstream cortical neurons, or are they modulated by distinct subpopulations? Answering this question could provide vital clues as to whether these pathways collaborate or operate independently.

Previous studies have revealed both differences and similarities in the cortical inputs to direct and indirect pathways at population level. However, our investigation delves deeper to understand how a singular cortical input simultaneously drives these pathways, or might it regulate one pathway through distinct subpopulations? To address this, we employed rabies virus–mediated retrograde tracing from D1- or D2-SPNs and recorded non-starter SPNs to determine if they receive the same inputs as the starter SPNs. This approach allowed us to calculate the connection ratio and estimate the probable connection properties.

Weaknesses: 

One limitation is that all inputs to SPNs are expressing ChR2, so they cannot distinguish between different cortical subregions during patching experiments. Their results could arise because the same innervation patterns are repeated in many cortical subregions or because some subregions have preferential D1-SPN input while others do not.

Thank you for raising this thoughtful concern. It is indeed not feasible to restrict ChR2 expression to a specific cortical region using the first-generation rabies-ChR2 system alone. A more refined approach would involve injecting Cre-dependent TVA and RG into the striatum of D1- or A2A-Cre mice, followed by rabies-Flp infection. Subsequently, a Flp-dependent ChR2 virus could be injected into the MCC or M1 to selectively label D1- or D2-projecting cortical neurons. This strategy would allow for more precise targeting and address many of the current limitations.

However, a significant challenge lies in the cytotoxicity associated with rabies virus infection. Neuronal health begins to deteriorate substantially around 10 days post-infection, which provides an insufficient window for robust Flp-dependent ChR2 expression. We have tested several new rabies virus variants with extended survival times (Chatterjee et al., 2018; Jin et al., 2024), but unfortunately, they did not perform effectively or suitably in the corticostriatal systems we examined.

In our experimental design, the aim is to delineate the connectivity probabilities to D1 or D2-SPNs from cortical neurons. Our hypothesis considered includes the possibility that similar innervation patterns could occur across multiple cortical subregions, or that some subregions might show preferential input to D1-SPNs while others do not, or a combination of both scenarios. This leads us to perform a series behavior test that using optogenetic activation of the D1- or D2-projecting cortical populations to see which could be the case.

In the cortical areas we examined, MCC and M1, during behavioral testing, there is consistency with our electrophysiological results. Specifically, when we stimulated the D1-projecting cortical neurons either in MCC or in M1, mice exhibited facilitated local motion in open field test, which is the same to the activation of D1 SPNs in the striatum along (MCC: Fig 3C & D vs. I; M1: Fig 3F & G vs. L). Conversely, stimulation of D2-projecting MCC or M1 cortical neurons resulted in behavioral effects that appeared to combine characteristics of both D1- and D2-SPNs activation in the striatum (MCC: Fig 3C & D vs. J; M1: Fig 3F & G vs. M). The similar results were observed in the ICSS test. Our interpretation of these results is that the activation of D1-projecting neurons in the cortex induces behavior changes akin to D1 neuron activation, while activation of D2-projecting neurons in the cortex leads to a combined effect of both D1 and D2 neuron activation. This suggests that at least some cortical regions, the ones we tested, follow the hypothesis we proposed.

There are also some caveats with respect to the efficacy of rabies tracing. Although they only patch non-starter cells in the striatum, only 63% of D1-SPNs receive input from D1-SPN-projecting cortical neurons. It's hard to say whether this is "high" or "low," but one question is how far from the starter cell region they are patching. Without this spatial indication of where the cells that are being patched are relative to the starter population, it is difficult to interpret if the cells being patched are receiving cortical inputs from the same neurons that are projecting to the starter population. Convergence of cortical inputs onto SPNs may vary with distance from the starter cell region quite dramatically, as other mapping studies of corticostriatal inputs have shown specialized local input regions can be defined based on cortical input patterns (Hintiryan et al., Nat Neurosci, 2016, Hunnicutt et al., eLife 2016, Peters et al., Nature, 2021).

This is a valid concern regarding anatomical studies. Investigating cortico-striatal connectivity at the single-cell level remains technically challenging due to current methodological limitations. At present, we rely on rabies virus-mediated trans-synaptic retrograde tracing to identify D1- or D2-projecting cortical populations. This anatomical approach is coupled with ex vivo slice electrophysiology to assess the functional connectivity between these projection-defined cortical neurons and striatal SPNs. This enables us to quantify connection ratios, for example, the proportion of D1-projecting cortical neurons that functionally synapse onto non-starter D1-SPNs.

To ensure the robustness of our conclusions, it is essential that both the starter cells and the recorded non-starter SPNs receive comparable topographical input from the cortex and other brain regions. Therefore, we carefully designed our experiments so that all recorded cells were located within the injection site, were mCherry-negative (i.e., non-starter cells), and were surrounded by ChR2-mCherry-positive neurons. This configuration ensured that the distance between recorded and starter cells did not exceed 100 µm, maintaining close anatomical proximity and thereby preserving the likelihood of shared cortical innervation within the examined circuitry.

These methodological details are also described in the section on ex vivo brain slice electrophysiology, specifically in the Methods section, lines 396–399:

“D1-SPNs (eGFP-positive in D1-eGFP mice, or eGFP-negative in D2-eGFP mice) or D2-SPNs (eGFP-positive in D2-eGFP mice, or eGFP-negative in D1-eGFP mice) that were ChR2-mCherry-negative, but in the injection site and surrounded by cells expressing ChR2-mCherry were targeted for recording.”

This experimental strategy was implemented to control for potential spatial biases and to enhance the interpretability of our connectivity measurements.

A caveat for the optogenetic behavioral experiments is that these optogenetic experiments did not include fluorophore-only controls.

Thank you for bringing this to our attention. A fluorophore-only control is indeed a valuable negative control, commonly used to rule out effects caused by light exposure independent of optogenetic manipulation. In this study, however, comparisons were made between light-on and light-off conditions within the same animal. This within-subject design, as employed in recent studies (Geddes et al., 2018; Zhu et al., 2025), is considered sufficient to isolate the effects of optogenetic manipulation.

Furthermore, as shown in Figure S3, we conducted an additional control experiment in which optogenetic stimulation was applied to M1, while ensuring that ChR2 expression was restricted to the striatum via targeted viral infection. This approach serves as a functional equivalent to the control you suggested. Importantly, we observed no effects that could be attributed solely to light exposure, further supporting the conclusion that the observed outcomes in our main experiments are due to targeted optogenetic manipulation, rather than confounding effects of illumination.

Lastly, by employing an in-animal comparison, measuring changes between stimulated and non-stimulated trials, we account for subject-specific variability and strengthen the interpretability of our findings.

Another point of confusion is that other studies (Cui et al, J Neurosci, 2021) have reported that stimulation of D1-SPNs in DLS inhibits rather than promotes movement.

Thank you for bringing the study by Cui and colleagues to our attention. While that study has generated some controversy, other independent investigations have demonstrated that activation of D1-SPNs in DLS facilitates local motion and lever-press behaviors (Dong et al., 2025; Geddes et al., 2018; Kravitz et al., 2010).

It is still worth to clarify. The differences in behavioral outcomes observed between our study and that of Cui et al. may be attributable to several methodological factors, including differences in both the stereotaxic targeting coordinates and the optical fiber specifications used for stimulation.

Specifically, in our experiments, the dorsomedial striatum (DMS) was targeted at coordinates AP +0.5 mm, ML ±1.5 mm, DV –2.2 mm, and the DLS at AP +0.5 mm, ML ±2.5 mm, DV –2.2 mm. In contrast, Cui et al. targeted the DMS at AP +0.9 mm, ML ±1.4 mm, DV –3.0 mm and the DLS at AP +0.7 mm, ML ±2.3 mm, DV –3.0 mm. These coordinates correspond to sites that are slightly more rostral and ventral compared to our own. Even subtle differences in anatomical targeting can result in activation of distinct neuronal subpopulations, which may account for the differing behavioral effects observed during optogenetic stimulation.

In addition, the optical fibers used in the two studies varied considerably. We employed fibers with a 200 µm core diameter and a numerical aperture (NA) of 0.37, whereas Cui et al. used fibers with a 250 µm core diameter and a higher NA of 0.66. The combination of a larger core and higher NA in their setup implies a broader spatial spread and deeper tissue penetration of light, likely resulting in activation of a larger neural volume. This expanded volume of stimulation may have engaged additional neural circuits not recruited in our experiments, further contributing to the divergent behavioral outcomes. Taken together, these differences in targeting and photostimulation parameters are likely key contributors to the distinct effects reported between the two studies.

Reviewer #3 (Public Review): 

In the manuscript by Klug and colleagues, the investigators use a rabies virus-based methodology to explore potential differences in connectivity from cortical inputs to the dorsal striatum. They report that the connectivity from cortical inputs onto D1 and D2 MSNs differs in terms of their projections onto the opposing cell type, and use these data to infer that there are differences in cross-talk between cortical cells that project to D1 vs. D2 MSNs. Overall, this manuscript adds to the overall body of work indicating that there are differential functions of different striatal pathways which likely arise at least in part by differences in connectivity that have been difficult to resolve due to difficulty in isolating pathways within striatal connectivity and several interesting and provocative observations were reported. Several different methodologies are used, with partially convergent results, to support their main points.

However, I have significant technical concerns about the manuscript as presented that make it difficult for me to interpret the results of the experiments. My comments are below.

Major:

There is generally a large caveat to the rabies studies performed here, which is that both TVA and the ChR2-expressing rabies virus have the same fluorophore. It is thus essentially impossible to determine how many starter cells there are, what the efficiency of tracing is, and which part of the striatum is being sampled in any given experiment. This is a major caveat given the spatial topography of the cortico-striatal projections. Furthermore, the authors make a point in the introduction about previous studies not having explored absolute numbers of inputs, yet this is not at all controlled in this study. It could be that their rabies virus simply replicates better in D1-MSNs than D2-MSNs. No quantifications are done, and these possibilities do not appear to have been considered. Without a greater standardization of the rabies experiments across conditions, it is difficult to interpret the results.

We thank the reviewer for raising these questions, which merit further discussion.

Firstly, the primary aim of our study is to investigate the connectivity of the corticostriatal pathway. Given the current technical limitations, it is not feasible to trace all the striatal SPNs connected to a single cortical neuron. Therefore, we approached this from the opposite direction, starting from D1- or D2-SPNs to retrogradely label upstream cortical neurons, and then identifying their connected SPNs via functional synaptic recordings. To achieve this, we employed the only available transsynaptic retrograde method: rabies virus-mediated tracing. Because we crossed D1- or D2-GFP mice with D1- or A2A-Cre mice to identify SPN subtypes during electrophysiological recordings, the conventional rabies-GFP system could not be used to distinguish starter cells without conflicting with the GFP labeling of SPNs. To overcome this, we tagged ChR2 expression with mCherry. In this setup, we recorded from mCherry-negative D1- or D2-SPNs within the injection site and surrounded by mCherry-positive neurons. This ensures that the recorded neurons are topographically matched to the starter cell population and receive input from the same cortical regions. We acknowledge that TVA-only and ChR2-expressing cells are both mCherry-positive and therefore indistinguishable in our system. As such, mCherry-positive cells likely comprise a mixture of starter cells and TVA-only cells, representing a somewhat broader population than starter cells alone. Nevertheless, by restricting recordings to mCherry-negative SPNs within the injection site, it is ensured that our conclusions about functional connectivity remain valid and aligned with the primary objective of this study.

Secondly, if rabies virus replication were significantly more efficient in D1-SPNs than in D2-SPNs, this would likely result in a higher observed connection probability in the D1-projecting group. However, we used consistent genetic strategies across all groups: D1-SPNs were defined as GFP-positive in D1-GFP mice and GFP-negative in D2-GFP mice, with D2-SPNs defined analogously. Recordings from both D1- and D2-SPNs were performed using the same methodology and under the same injection conditions within the same animals. This internal control helps mitigate the possibility that differential rabies infection efficiency biased our results.

With these experimental safeguards in place, we found that 40% of D2-SPNs received input from D1-SPN-projecting cortical neurons, while 73% of D1-SPNs received input from D2-SPN-projecting cortical neurons. Although the ideal scenario would involve an even larger sample size to refine these estimates, the technical demands of post-rabies-infection electrophysiological recordings inherently limit throughput. Nonetheless, our approach represents the most feasible and accurate method currently available, and provides a significant advance in characterizing the functional connectivity within corticostriatal circuits.

The authors claim using a few current clamp optical stimulation experiments that the cortical cells are healthy, but this result was far from comprehensive. For example, membrane resistance, capacitance, general excitability curves, etc are not reported. In Figure S2, some of the conditions look quite different (e.g., S2B, input D2-record D2, the method used yields quite different results that the authors write off as not different). Furthermore, these experiments do not consider the likely sickness and death that occurs in starter cells, as has been reported elsewhere. The health of cells in the circuit is overall a substantial concern that alone could invalidate a large portion, if not all, of the behavioral results. This is a major confound given those neurons are thought to play critical roles in the behaviors being studied. This is a major reason why first-generation rabies viruses have not been used in combination with behavior, but this significant caveat does not appear to have been considered, and controls e.g., uninfected animals, infected with AAV helpers, etc, were not included.

We understand and appreciate the reviewer’s concern regarding the potential cytotoxicity of rabies virus infection. Indeed, this is a critical consideration when interpreting functional connectivity data. We have tested several newer rabies virus variants reported to support extended survival times (Chatterjee et al., 2018; Jin et al., 2024), but unfortunately, these variants did not perform reliably in the corticostriatal circuits we examined.

Given these limitations, we relied on the rabies virus approach originally developed by Osakada et al. (Osakada et al., 2011), which demonstrated that neurons infected with rabies virus expressing ChR2 remain both viable and functional up to at least 10 days post-infection (Fig. 3, cited below). In our own experiments, we further validated the health and viability of cortical neurons, the presynaptic partners of SPNs, particularly around day 7 post-infection.

To minimize the risk of viral toxicity, we performed ex vivo slice recordings within a conservative time window, between 4 and 8 days after infection, when the health of labeled neurons is well maintained. Moreover, the recorded SPNs were consistently mCherry-negative, indicating they were not directly infected by rabies virus, thus further reducing the likelihood of recording from compromised cells.

Taken together, these steps help ensure that our synaptic recordings reflect genuine functional connectivity, rather than artifacts of viral toxicity. We hope this clarifies the rationale behind our experimental design.

For the behavioral tests, including a naïve uninfected group and an AAV helper virus-only group as negative controls could be beneficial to isolate the specific impact of rabies virus infection. However, our primary focus is on the activation of selected presynaptic inputs to D1- or D2-SPNs by optogenetic method. Therefore, comparing stimulated versus non-stimulated trials within the same animal offers more direct and relevant results for our study objectives.

It is also important to note that the ICSS test is particularly susceptible to the potential cytotoxic effects of rabies virus, as it spans a relatively extended period, from Day 4 to Day 12 post-infection. To mitigate this issue, we focused our analysis on the first 7 days of ICSS testing, thereby keeping the behavioral observations within 10 days post-rabies injection. This approach minimizes potential confounds from rabies-induced neurotoxicity while still capturing the relevant behavioral dynamics. Accordingly, we have revised Figure 3 and updated the statistical analyses to reflect this adjustment.

The overall purity (e.g., EnvA-pseudotyping efficiency) of the RABV prep is not shown. If there was a virus that was not well EnvA-pseudotyped and thus could directly infect cortical (or other) inputs, it would degrade specificity.

We agree that anatomical specificity is crucial for accurately labeling inputs to defined SPN populations in our study. The rabies virus strain employed here has been rigorously validated for its specificity in numerous previous studies from our group and others (Aoki et al., 2019; Klug et al., 2018; Osakada et al., 2011; Smith et al., 2016; Wall et al., 2013; Wickersham et al., 2007). For example, in a recent study by Aoki et al. (Aoki et al., 2019), we tested the same rabies virus strain by co-injecting the glycoprotein-deleted rabies virus and the TVA-expressing helper virus, without glycoprotein expressing AAV, into the SNr. As shown in Figure S1 (related to Figure 2), GFP expression was restricted to starter cells within the SNr, with no evidence of transsynaptic labeling in upstream regions such as the striatum, EPN, GPe, or STN (see panels F–H). These findings provide strong evidence that the rabies virus used in our experiments is properly pseudotyped and exhibits high specificity for starter cell labeling without off-target spread.

We appreciate the reviewer’s emphasis on specificity, and we hope this clarification further supports the reliability of our anatomical tracing approach.

While most of the study focuses on the cortical inputs, in slice recordings, inputs from the thalamus are not considered, yet likely contribute to the observed results. Related to this, in in vivo optogenetic experiments, technically, if the thalamic or other inputs to the dorsal striatum project to the cortex, their method will not only target cortical neurons but also terminals of other excitatory inputs. If this cannot be ruled it, stating that the authors are able to selectively activate the cortical inputs to one or the other population should be toned down.

We agree with the reviewer that the thalamus is also a significant source of excitatory input to the striatum. However, current techniques do not allow for precise and exclusive labeling of upstream neurons in a given brain region, such as the cortex or thalamus. This technical limitation indeed makes it difficult to definitively determine whether inputs from these regions follow the same projection rules. Despite this, our findings show that stimulation of defined cortical populations, specifically, D1- or D2-projecting neurons in MCC and M1, elicits behavioral outcomes that closely mirror those observed in our ex vivo slice recordings, providing strong support for the cortical origin of the effects we observed.

In our in vivo optogenetic experiments, we acknowledge that stimulating a specific cortical region may also activate axonal terminals from rabies-infected cortical or thalamic neurons. While somatic stimulation is generally more effective than terminal stimulation, we recognize the possibility that terminals on non-rabies-traced cortical neurons could be activated through presynaptic connections. To address this, we considered the finding of a previous study (Cruikshank et al., 2010), which demonstrated that while brief optogenetic stimulation (0.05 ms) of thalamo-cortical terminals can elicit few action potentials in postsynaptic cortical neurons, sustained terminal stimulation (500 ms) also results in only transient postsynaptic firing rather than prolonged activation (Fig. 3C, cited below). This suggests that cortical neurons exhibit only short-lived responses to continuous presynaptic stimulation of thalamic origin.

In comparison, our behavioral paradigms employed prolonged optogenetic stimulation protocols- 20 Hz, 10 ms pulses for 15 s (open-field test), 1 s (ICSS), and 8 s (FR4/8)—which more closely resemble sustained stimulation conditions. Given these parameters, and the robust behavioral responses observed, it means that the effects are primarily mediated by activation of rabies-labeled, ChR2-expressing D1- or D2-projecting cortical neurons rather than indirect activation through thalamic input.

We appreciate the reviewer’s valuable comment, and we have now incorporated this point into the revised manuscript (page 13, line 265 to 275) to more clearly address the potential contribution of thalamic inputs in our experimental design.

The statements about specificity of connectivity are not well-founded. It may be that in the specific case where they are assessing outside of the area of injections, their conclusions may hold (e.g., excitatory inputs onto D2s have more inputs onto D1s than vice versa). However, how this relates to the actual site of injection is not clear. At face value, if such a connectivity exists, it would suggest that D1-MSNs receive substantially more overall excitatory inputs than D2s. It is thus possible that this observation would not hold over other spatial intervals. This was not explored and thus the conclusions are over-generalized. e.g., the distance from the area of red cells in the striatum to recordings was not quantified, what constituted a high level of cortical labeling was not quantified, etc. Without more rigorous quantification of what was being done, it is difficult to interpret the results. 

We sincerely thank the reviewer for the thoughtful comments and critical insights into our interpretation of connectivity data. These concerns are valid and provide an important opportunity to clarify and reinforce our experimental design and conclusions.

Firstly, as described in our previous response, all patched neurons were carefully selected to be within the injection site and in close proximity to ChR2-mCherry-positive cells. Specifically, the estimated distance from each recorded neuron to the nearest starter cells did not exceed 100 µm. This design choice was made to minimize variability associated with spatial distance or heterogeneity in viral expression, thereby allowing for a more consistent sampling of putatively connected neurons.

Secondly, quantifying both the number of starter and input neurons would, in principle, provide a more comprehensive picture of connectivity. However, given the technical limitations of the current approach particularly when combining rabies tracing with functional recordings it is not feasible to obtain such precise cell counts. Instead, we focused on connection ratios derived from targeted electrophysiological recordings, which offer a reliable and practical means of estimating connectivity within these defined circuits.

Thirdly, regarding the potential influence of rabies-labeled neurons beyond the immediate recording site: while we acknowledge that rabies tracing labels a broad set of upstream neurons, our analysis was confined to a well-defined and localized area. The analogy we find helpful here is that of a spotlight - our recordings were restricted to the illuminated region directly under the beam, where the projection pattern is fixed and interpretable, regardless of what lies outside that area. Although we cannot fully account for all possible upstream connections, our methodology was designed to minimize variability and maintain consistency in the region of interest, which we believe supports the robustness of our conclusions in the ex vivo slice recording experiment.

We hope this additional explanation addresses the reviewer’s concerns and helps clarify the rationale of our experimental strategy.

The results in figure 3 are not well controlled. The authors show contrasting effects of optogenetic stimulation of D1-MSNs and D2-MSNs in the DMS and DLS, results which are largely consistent with the canon of basal ganglia function. However, when stimulating cortical inputs, stimulating the inputs from D1-MSNs gives the expected results (increased locomotion) while stimulating putative inputs to D2-MSNs had no effect. This is not the same as showing a decrease in locomotion - showing no effect here is not possible to interpret.

We apologize for any confusion and appreciate the opportunity to clarify this point. Our electrophysiological recordings demonstrated that D1-projecting cortical neurons preferentially innervate D1-SPNs in the striatum, whereas D2-projecting cortical neurons provide input to both D1- and D2-SPNs, without a clear preference. These synaptic connectivity patterns are further supported by our behavioral experiments: optogenetic stimulation of D1-projecting neurons in cortical areas such as MCC and M1 led to behavioral effects consistent with direct D1-SPN activation. In contrast, stimulation of D2-projecting cortical neurons produced behavioral outcomes that appeared to reflect a mixture of both D1- and D2-SPN activation.

We acknowledge that interpreting negative behavioral findings poses inherent challenges, as it is difficult to distinguish between a true lack of effect and insufficient experimental manipulation. To mitigate this, we ensured that all animals included in the analysis exhibited appropriate viral expression and correctly placed optic fibers in the targeted regions. These controls help to confirm that the observed behavioral effects - or lack thereof - are indeed due to the activation of the intended neuronal populations rather than technical artifacts such as weak expression or fiber misplacement.

As shown in Author response image 1 below, our verification of virus expression and fiber positioning confirms effective targeting in MCC and M1 of A2A-Cre mice. Therefore, we interpret the negative behavioral outcomes as meaningful consequences of specific neural circuit activation.

Author response image 1.

Confocal image from A2A-Cre mouse showing targeted optogenetic stimulation of D2-projecting cortical neurons in MCC or M1. ChR2-mCherry expression highlights D2-projecting neurons, selectively labeled via rabies-mediated tracing. Optic fiber placement is confirmed above the cortical region of interest. Image illustrates robust expression and anatomical specificity necessary for pathway-selective stimulation in behavioral assays.

In light of their circuit model, the result showing that inputs to D2-MSNs drive ICSS is confusing. How can the authors account for the fact that these cells are not locomotor-activating, stimulation of their putative downstream cells (D2-MSNs) does not drive ICSS, yet the cortical inputs drive ICSS? Is the idea that these inputs somehow also drive D1s? If this is the case, how do D2s get activated, if all of the cortical inputs tested net activate D1s and not D2s? Same with the results in figure 4 - the inputs and putative downstream cells do not have the same effects. Given the potential caveats of differences in viral efficiency, spatial location of injections, and cellular toxicity, I cannot interpret these experiments.

We apologize for any confusion in our previous explanation. In our behavioral experiments, the primary objective was to determine whether activation of D1- or D2-projecting cortical neurons would produce behavioral outcomes distinct from those observed with pure D1 or D2 activation.

Our findings show that stimulation of D1-projecting cortical neurons produced behavioral effects closely resembling those of selective D1 activation in both open field and ICSS tests. This is consistent with our slice recording data, which revealed that D1-projecting cortical neurons exhibit a higher connection probability with D1-SPNs than with D2-SPNs.

In contrast, interpreting the effects of D2-projecting cortical neuron stimulation is inherently more nuanced. In the open field test, activation of these neurons did not significantly modulate local motion. This could reflect a balanced influence of D1 activation, which facilitates movement, and D2 activation, which suppresses it - resulting in a net neutral behavioral outcome. In the ICSS test, the absence of a strong reinforcement effect typically associated with D2 activation, combined with partial reinforcement likely due to concurrent D1 activation, suggests that stimulation of D2-projecting neurons produces a mixed behavioral signal. This outcome supports the interpretation that these neurons synapse onto both D1- and D2-SPNs, leading to a blended behavioral response that differs from selective D1 or D2 activation alone.

Together, these two behavioral assays offer complementary perspectives, providing a more complete view of how projection-specific cortical inputs influence striatal output and behavior.

In Figure 4 of the current manuscript (as cited below), we show that optogenetic activation of MCC neurons projecting to D1-SPNs facilitates sequence lever pressing, whereas activation of MCC neurons projecting to D2-SPNs does not induce significant behavioral changes. Conversely, activation of M1 neurons projecting to either D1- or D2-SPNs enhances lever pressing sequences. These observations align with our prior findings (Geddes et al., 2018; Jin et al., 2014), where we demonstrated that in the striatum, D1-SPN activation facilitates ongoing lever pressing, whereas D2-SPN activation is more involved in suppressing ongoing actions and promoting transitions between sub-sequences, shown in Fig. 4 from (Geddes et al., 2018; Jin et al., 2014) and Fig. 5K from (Jin et al., 2014) . Taken together, the facilitation of lever pressing by D1-projecting MCC and M1 neurons is consistent with their preferential connectivity to D1-SPNs and their established behavioral role.

What is particularly intriguing, though admittedly more complex, is the behavioral divergence observed upon activation of D2-SPN-projecting cortical neurons. Activation of D2-projecting MCC neurons does not alter lever pressing, possibly reflecting a counterbalancing effect from concurrent D1- and D2-SPN activation. In contrast, stimulation of D2-projecting M1 neurons facilitates lever pressing, albeit less robustly than their D1-projecting counterparts. This discrepancy may reflect regional differences in striatal targets, DMS for MCC versus DLS for M1, as also supported by our open field test results. Furthermore, our recent findings (Zhang et al., 2025) show that synaptic strength from Cg to D2-SPNs is stronger than to D1-SPNs, whereas the M1 pathway exhibits the opposite pattern. These data suggest that beyond projection ratios, synaptic strength also shapes cortico-striatal functional output. Thus, stronger D2-SPN synapses in the DMS may offset D1-SPN activation during MCC-D2 stimulation, dampening lever pressing increase. Conversely, weaker D2 synapses in the DLS may permit M1-D2 projections to facilitate behavior more readily.

In summary, the behavioral outcomes of our optogenetic manipulations support the proposed asymmetric cortico-striatal connectivity model. While the effects of D2-projecting neurons are not uniform, they reflect varying balances of D1 and D2-SPN influence, which further underscores the asymmetrical connections of cortical inputs to the striatum.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors): 

(1) What are the sample sizes for Fig S2? Some trends that are listed as nonsignificant look like they may just be underpowered. Related to this point, S2C indicates that PPR is statistically similar in all conditions. The traces shown in Figure 2 suggest that PPR is quite different in "Input D1"- vs "Input D2" projections. If there is indeed no difference, the exemplar traces should be replaced with more representative ones to avoid confusion. 

Thank you for your suggestion. The sample size reported in Figure S2 corresponds to the neurons identified as connected in Figure 2. The representative traces shown in Figure 2 were selected based on their close alignment with the amplitude statistics and are intended to reflect typical responses. Given this, it is appropriate to retain the current examples as they accurately illustrate the underlying data.

(2) Previous studies have described that SPN-SPN collateral inhibition is also asymmetric, with D2->D1 SPN connectivity stronger than the other direction. While cortical inputs to D2-SPNs may also strongly innervate D1-SPNs, it would be helpful to speculate on how collateral inhibition may further shape the biases (or lack thereof) reported here. 

This would indeed be an interesting topic to explore. SPN-SPN mutual inhibition and/or interneuron inhibition may also play a role in the functional organization and output of the striatum. In the present study, we focused on the primary layer of cortico-striatal connectivity to examine how cortical neurons selectively connect to the striatal direct and indirect pathways, as these pathways have been shown to have distinct yet cooperative functions. To achieve this, we applied a GABAA receptor inhibitor to isolate only excitatory synaptic currents in SPNs, yielding the relevant results.

To investigate additional circuit organization involving SPN-SPN mutual inhibition, the current available technique would involve single-cell initiated rabies tracing. This approach would help identify the starter SPN and the upstream SPNs that provide input to the starter cell, thereby offering a clearer understanding of the local circuit.

(3) In Fig 3N-S there are no stats confirming that optogenetic stimulation does indeed increase lever pressing in each group (though it obviously looks like it does). It would be helpful to add statistics for this comparison, in addition to the between-group comparisons that are shown. 

We thank the reviewer for this thoughtful suggestion. To assess whether optogenetic stimulation increases lever pressing in each group shown in Figures 3O, 3P, 3R, and 3S, we employed a permutation test (10,000 permutations). This non-parametric statistical method does not rely on assumptions about the underlying data distribution and is particularly appropriate for our analysis given the relatively small sample sizes.

Additionally, in response to Reviewer 3’s concern regarding the potential cytotoxicity of rabies virus affecting behavioral outcomes during in vivo optogenetic stimulation experiments, we focused our analysis on Days 1 through 7 of the ICSS test. This time window remains within 10 days post-rabies infection, a period during which previous studies have reported minimal cytopathic effects (Osakada et al., 2011).

Accordingly, we have updated Figure 3N-S and revised the associated statistical analyses in the figure legend as follows:

(O-P) D1-SPN (red) but not D2-SPN stimulation (black) drives ICSS behavior in both the DMS (O: D1, n = 6, permutation test, slope = 1.5060, P = 0.0378; D2, n = 5, permutation test, slope = -0.2214, P = 0.1021; one-tailed Mann Whitney test, Day 7 D1 vs. D2, P = 0.0130) and the DLS (P: D1, n = 6, permutation test, slope = 28.1429, P = 0.0082; D2, n = 5, permutation test, slope = -0.3429, P = 0.0463; one-tailed Mann Whitney test, Day 7 D1 vs. D2, P = 0.0390). *, P < 0.05. (Q) Timeline of helper virus injections, rabies-ChR2 injections and optogenetic stimulation for ICSS behavior. (R-S) Optogenetic stimulation of the cortical neurons projecting to either D1- or D2-SPNs induces ICSS behavior in both the MCC (R: MCC-D1, n = 5, permutation test, Day1-Day7, slope = 2.5857, P = 0.0034; MCC-D2, n = 5, Day2-Day7, permutation test, slope = 1.4229, P = 0.0344; no significant effect on Day7, MCC-D1 vs. MCC-D2,  two-tailed Mann Whitney test, P = 0.9999) and the M1 (S: M1-D1, n = 5, permutation test, Day1-Day7, slope = 1.8214, P = 0.0259; M1-D2, n = 5, Day1-Day7, permutation test, slope = 1.8214, P = 0.0025; no significant effect on Day7, M1-D1 vs. M1-D2, two-tailed Mann Whitney test, P = 0.3810). n.s., not statistically significant.

We believe this updated analysis and additional context further strengthen the validity of our conclusions regarding the reinforcement effects.

(4) Line 206: mice were trained for "a few more days" is not a very rigorous description. It would be helpful to state the range of additional days of training. 

We thank the reviewer for the suggestion. In accordance with the Methods section, we have now specified the number of days, which is 4 days, in the main text (line 207).

(5) In Fig 4D,H, the statistical comparison is relative modulation (% change) by stimulation of D1- vs D2- projecting inputs. Please show statistics comparing the effect of stimulation on lever presses for each individual condition. For example, is the effect of MCC-D2 stimulation in panel D negative or not significant? 

Thank you for your suggestion. Below are the statistical results, which we have also incorporated into the figure legend for clarity. To assess the net effects of each manipulation, we compared the observed percentage changes with a theoretical value of zero.

In Figure 4D, optogenetic stimulation of D1-projecting MCC neurons significantly increased the pressing rate (MCC-D1, n = 8, one-sample two-tailed t-test, t = 2.814, P = 0.0131), whereas stimulation of D2-projecting MCC neurons did not produce a significant effect (MCC-D2, n = 7, one-sample two-tailed t-test, t = 0.8481, P = 0.4117).

In contrast, Figure 4H shows that optogenetic stimulation of both D1- and D2-projecting M1 neurons significantly increased the sequence press rate (M1-D1, n = 6, one-sample two-tailed Wilcoxon signed-rank test, P = 0.0046; M1-D2, n = 7, one-sample two-tailed Wilcoxon signed-rank test, P = 0.0479).

These analyses help clarify the distinct behavioral effects of manipulating different corticostriatal projections.

(6) Are data in Fig 1G-H from a D1- or A2a- cre mouse? 

The data in Fig 1G-H are from a D1-Cre mouse.

(7) In Fig S3 it looks like there may actually be an effect of 20Hz simulation of D2-SPNs. Though it probably doesn't affect the interpretation. 

As indicated by the statistics, there is a slight, but not statistically significant, decrease in local motion when 20 Hz stimulation is delivered to the motor cortex with ChR2 expression in D2-SPNs in the striatum.

Reviewer #2 (Recommendations For The Authors): 

The rabies tracing is referred to on several occasions as "new" but the reference papers are from 2011, 2013, and 2018. It is unclear what is new about the system used in the paper and what new feature is relevant to the experiments that were performed. Either clarify or remove "new" terminology. 

Thank you for bringing this to our attention. We have revised the relevant text accordingly at line 20 in the Abstract, line 31 in the In Brief, line 69 in the Introduction, line 83 in the Results, and line 226 in the Discussion to improve clarity and accuracy.

In Figure 2 D and G, D1 eGFP (+) and D2 eGFP(-) are plotted separately. These are the same cell type; therefore it may work best to combine that data. This could also be done for 'input to D2- Record D2' in panel D as well as 'input D1-Record D2' and 'input D2-Record D1' in panel G. Combining the information in panel D and G and comparing all 4 conditions to each other would give a better understanding of the comparison of functional connectivity between cortical neurons and D1 and D2 SPNs. 

We thank the reviewer for the thoughtful suggestion. While presenting single bars for each condition (e.g., ‘input D1 - record D1’) might improve visual simplicity, it would obscure an important aspect of our experimental design. Specifically, we aimed to highlight that the comparisons between D1- and D2-projecting neurons to D1 and D2 SPNs were counterbalanced within the same animals - not just across different groups. By showing both D1-eGFP(+) and D2-eGFP(-), or vice versa, within each group and at similar proportions, we provide a more complete picture of the internal control built into our design. This format helps ensure the audience that our conclusions are not biased by group-level differences, but are supported by within-subject comparisons. Therefore, that the current presentation better could serve to communicate the rigor and balance of our experimental approach.

The findings in Figure 2 are stated as D1 projecting excitatory inputs have a higher probability of targeting D1 SPNs while D2 projecting excitatory inputs target both D1 SPNs and D2 SPNs. It may be more clear to say that some cortical neurons project specifically to D1 SPNs while other cortical neurons project to both D1 and D2 SPNs equally. A better summary diagram could also help with clarity. 

Thank you for bringing this up. The data we present reflect the connection probabilities of D1- or D2-projecting cortical neurons to D1 or D2 SPNs. One possible interpretation is like the reviewer said that a subset of cortical neurons preferentially target D1 SPNs, while others exhibit more balanced projections to both D1 and D2 SPNs. However, we cannot rule out alternative explanations - for example, that some D2-projecting neurons preferentially target D2 SPNs, or that the observed differences arise from the overall proportions of D1- and D2-projecting cortical neurons connecting to each striatal subtype.

There are multiple possible patterns of connectivity that could give rise to the observed differences in connection ratios. Based on our current data, we can confidently conclude the existence of asymmetric cortico-striatal projections to the direct and indirect pathways, but the precise nature of this asymmetry will require further investigation.

Figure 4 introduces the FR8 task, but there are similar takeaways to the findings from Figure 3. Is there another justification for the FR8 task or interesting way of interpreting that data that could add richness to the manuscript?

The FR8 task is a self-initiated operant sequence task that relies on motor learning mechanisms, whereas the open field test solely assesses spontaneous locomotion. Furthermore, the sequence task enables us to dissect the functional role of specific neuronal populations in the initiation, maintenance, and termination of sequential movements through closed-loop optogenetic manipulations integrated into the task design. These methodological advantages underscore the rationale for including Figure 4 in the manuscript, as it highlights the unique insights afforded by this experimental paradigm.

I am somewhat surprised to see that D1-SPN stimulation in DLS gave the results in Figure 3 F and P, as mentioned in the public review. These contrast with some previous results (Cui et al, J Neurosci, 2021). Any explanation? Would be useful to speculate or compare parameters as this could have important implications for DLS function.

Thank you for raising this point. While Cui’s study has generated some debate, several independent investigations have consistently demonstrated that stimulation of D1-SPNs in the dorsolateral striatum (DLS) facilitates local motion and lever-press behaviors (Dong et al., 2025; Geddes et al., 2018; Kravitz et al., 2010). These findings support the functional role of D1-SPNs in promoting movement and motivated actions.

The differences in behavioral outcomes observed between our study and that of Cui et al. may stem from several methodological factors, particularly related to anatomical targeting and optical stimulation parameters.

Specifically, our experiments targeted the DMS at AP +0.5 mm, ML ±1.5 mm, DV –2.2 mm, and the DLS at AP +0.5 mm, ML ±2.5 mm, DV –2.2 mm. In contrast, Cui’s study targeted the DMS at AP +0.9 mm, ML ±1.4 mm, DV –3.0 mm, and the DLS at AP +0.7 mm, ML ±2.3 mm, DV –3.0 mm. These differences indicate that their targeting was slightly more rostral and more ventral than ours, which could have led to stimulation of distinct neuronal populations within the striatum, potentially accounting for variations in behavioral effects observed during optogenetic activation.

In addition, the optical fibers used in the two studies differed markedly. We employed optical fibers with a 200 µm core diameter and a numerical aperture (NA) of 0.37. Cui’s study used fibers with a larger core diameter (250 µm) and a higher NA (0.66), which would produce a broader spread and deeper penetration of light. This increased photostimulation volume may have recruited a more extensive network of neurons, possibly including off-target circuits, thus influencing the behavioral outcomes in a manner not seen in our more spatially constrained stimulation paradigm.

Taken together, these methodological differences, both in anatomical targeting and optical stimulation parameters, likely contribute to the discrepancies in behavioral results observed between the two studies. Our findings, consistent with other independent reports, support the role of D1-SPNs in facilitating movement and reinforcement behaviors under more controlled and localized stimulation conditions.

Reviewer #3 (Recommendations For The Authors): 

Minor: 

The authors repeatedly state that they are using a new rabies virus system, but the system has been in widespread use for 16 years, including in the exact circuits the authors are studying, for over a decade. I would not consider this new. 

Thank you for bringing this to our attention. We have revised the relevant text accordingly at line 20 in the Abstract, line 31 in the In Brief, line 69 in the Introduction, line 83 in the Results, and line 226 in the Discussion to improve clarity and accuracy.

Figure 2G, how many mice were used for recordings?

In Fig. 2G, we used 8 mice in the D1-projecting to D2 EGFP(+) group, 7 mice in the D1-projecting to D1 EGFP(-) group, 8 mice in the D2-projecting to D1 EGFP(+) group, and 10 mice in the D2-projecting to D2 EGFP(-) group.

The amplitude of inputs was not reported in figure 2. This is important, as the strength of the connection matters. This is reported in Figure S2, but how exactly this relates to the presence or absence of connections should be made clearer.

The amplitude data presented in Figure S2 summarize all recorded currents from confirmed connections, as detailed in the Methods section. A connection is defined by the presence of a detectable and reliable postsynaptic current with an onset latency of less than 10 ms following laser stimulation.

Reference in the reply-to-review comments:

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Kravitz, A.V., Freeze, B.S., Parker, P.R.L., Kay, K., Thwin, M.T., Deisseroth, K., and Kreitzer, A.C. (2010). Regulation of parkinsonian motor behaviours by optogenetic control of basal ganglia circuitry. Nature 466, 622-626.

Osakada, F., Mori, T., Cetin, A.H., Marshel, J.H., Virgen, B., and Callaway, E.M. (2011). New Rabies Virus Variants for Monitoring and Manipulating Activity and Gene Expression in Defined Neural Circuits. Neuron 71, 617-631.

Smith, J.B., Klug, J.R., Ross, D.L., Howard, C.D., Hollon, N.G., Ko, V.I., Hoffman, H., Callaway, E.M., Gerfen, C.R., and Jin, X. (2016). Genetic-Based Dissection Unveils the Inputs and Outputs of Striatal Patch and Matrix Compartments. Neuron 91, 1069-1084.

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Author response:

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

Life Assessment

This valuable study builds on previous work by the authors by presenting a potentially key method for correcting optical aberrations in GRIN lens-based micro endoscopes used for imaging deep brain regions. By combining simulations and experiments, the authors show that the obtained field of view is significantly increased with corrected, versus uncorrected microendoscopes. The evidence supporting the claims of the authors is solid, although some aspects of the manuscript should be clarified and missing information provided. Because the approach described in this paper does not require any microscope or software modifications, it can be readily adopted by neuroscientists who wish to image neuronal activity deep in the brain.

We thank the Referees for their interest in the paper and for the constructive feedback. We have taken the time necessary to address all of their comments, acquiring new data and performing additional analyses. With the inclusion of these new results, we modified four main figures (Figures 1, 6, 7, and 8), added three new Supplementary Figures (Supplementary Figures 1, 2, and 3), and significantly edited the text. Based on the additional work suggested by the Referees, we believe that we have improved our manuscript, provided missing information, and clarified some aspects of the manuscript, which the Referees pointed our attention to.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Referee’s comment: Sattin, Nardin, and colleagues designed and evaluated corrective microlenses that increase the useable field of view of two long (>6mm) thin (500 um diameter) GRIN lenses used in deep-tissue two-photon imaging. This paper closely follows the thread of earlier work from the same group (e.g. Antonini et al, 2020; eLife), filling out the quiver of available extended-fieldof-view 2P endoscopes with these longer lenses. The lenses are made by a molding process that appears practical and easy to adopt with conventional two-photon microscopes.

Simulations are used to motivate the benefits of extended field of view, demonstrating that more cells can be recorded, with less mixing of signals in extracted traces, when recorded with higher optical resolution. In vivo tests were performed in the piriform cortex, which is difficult to access, especially in chronic preparations.

The design, characterization, and simulations are clear and thorough, but not exhaustive (see below), and do not break new ground in optical design or biological application. However, the approach shows much promise, including for applications not mentioned in the present text such as miniaturized GRIN-based microscopes. Readers will largely be interested in this work for practical reasons: to apply the authors' corrected endoscopes.

Strengths:

The text is clearly written, the ex vivo analysis is thorough and well-supported, and the figures are clear. The authors achieved their aims, as evidenced by the images presented, and were able to make measurements from large numbers of cells simultaneously in vivo in a difficult preparation.

Weaknesses:

Referee’s comment: (1) The novelty of the present work over previous efforts from the same group is not well explained. What needed to be done differently to correct these longer GRIN lenses?

We thank the Referee for the positive evaluation of our work. The optical properties of GRIN lenses depend on the geometrical and optical features of the specific GRIN lens type considered, i.e. its diameter, length, numerical aperture, pitch, and radial modulation of the refractive index. Our approach is based on the addition of a corrective optical element at the back end of the GRIN lens to compensate for aberrations that light encounters as it travels through the GRIN lens. The corrective optical element must, therefore, be specifically tailored to the specific GRIN lens type we aim to correct the aberrations of. The novelty of the present article lies in the successful execution of the ray-trace simulations and two-photon lithography fabrication of corrective optical elements necessary to achieve aberration correction in the two novel and long GRIN lens types, i.e. NEM-050-25-15-860-S-1.5p and NEM-050-23-15-860-S-2.0p (GRIN length, 6.4 mm and 8.8 mm, respectively). Our previous work (Antonini et al. eLife 2020) demonstrated aberration correction with GRIN lenses shorter than 4.1 mm. The design and fabrication of a single corrective optical element suitable to enlarge the field-of-view (FOV) in these longer GRIN lenses is not obvious, especially because longer GRIN lenses are affected by stronger aberrations. To better clarify this point, we revised the Introduction at page 5 (lines 3-10 from bottom) as follows:

“Recently, a novel method based on 3D microprinting of polymer optics was developed to correct for GRIN aberrations by placing specifically designed aspherical corrective lenses at the back end of the GRIN lens 7. This approach is attractive because it is built-in on the GRIN lens and corrected microendoscopes are ready-to-use, requiring no change in the optical set-up. However, previous work demonstrated the feasibility of this method only for GRIN lenses of length < 4.1 mm 7, which are too short to reach the most ventral regions of the mouse brain. The applicability of this technology to longer GRIN lenses, which are affected by stronger optical aberrations 19, remained to be proven.”

(2) Some strong motivations for the method are not presented. For example, the introduction (page 3) focuses on identifying neurons with different coding properties, but this can be done with electrophysiology (albeit with different strengths and weaknesses). Compared to electrophysiology, optical methods more clearly excel at genetic targeting, subcellular measurements, and molecular specificity; these could be mentioned.

Thank you for the comment. We added a paragraph in the Introduction (page 3, lines 2-8) according to what suggested by the Reviewer:

“High resolution 2P fluorescence imaging of the awake brain is a fundamental tool to investigate the relationship between the structure and the function of brain circuits 1. Compared to electrophysiological techniques, functional imaging in combination with genetically encoded indicators allows monitoring the activity of genetically targeted cell types, access to subcellular compartments, and tracking the dynamics of many biochemical signals in the brain (2). However, a critical limitation of multiphoton microscopy lies in its limited (< 1 mm) penetration depth in scattering biological media 3”.

Another example, in comparing microfabricated lenses to other approaches, an unmentioned advantage is miniaturization and potential application to mini-2P microscopes, which use GRIN lenses.

We added the concept suggested by the Reviewer in the Discussion (page 21, lines 4-7 from bottom). The text now reads:

“Another advantage of long corrected microendoscopes described here over adaptive optics approaches is the possibility to couple corrected microendoscopes with portable 2P microscopes 42-44, allowing high resolution functional imaging of deep brain circuits on an enlarged FOV during naturalistic behavior in freely moving mice”.

(3) Some potentially useful information is lacking, leaving critical questions for potential adopters:

How sensitive is the assembly to decenter between the corrective optic and the GRIN lens?

Following the Referee’s comment, we conducted new optical simulations to evaluate the decrease in optical performance of the corrected endoscopes as a function of the radial shift of the corrective lens from the optical axis of the GRIN rod (decentering, new Supplementary Figure 3), using light rays passing either off- or on-axis. For off-axis rays, we found that the Strehl ratio remained above 0.8 (Maréchal criterion) for positive translations in the range 6-11.5 microns and 16-50 microns for the 6.4 mm- and the 8.8 mm-long corrected microendoscope, respectively, while the Strehl ratio decreased below 0.8 for negative translations of amplitude ~ 5 microns. Please note that for the most marginal rays, a negative translation produces a mismatch between the corrective microlens and the GRIN lens such that the light rays no longer pass through the corrective lens. In contrast, rays passing near the optical axis were still focused by the corrected probe with Strehl ratio above 0.8 in a range of radial shifts of -40 – 40 microns for both microendoscope types. Altogether, these novel simulations suggest that decentering between the corrective microlens and the GRIN lens < 5 microns do not majorly affect the optical properties of the corrected endoscopes. These new results are now displayed in Supplementary Figure 3 and described on page 7 (lines 3-5 from bottom).

What is the yield of fabrication and of assembly?

The fabrication yield using molding was ~ 90% (N > 30 molded lenses). The main limitation of this procedure was the formation of air bubbles between the mold negative and the glass coverslip. Molded lenses were visually inspected with a stereomicrscope and, in case of air bubble formation, they were discarded.

The assembly yield, i.e. correct positioning of the GRIN lens with respect to the coverslip, was 100 % (N = 27 endoscopes).

We added this information in the Methods at page 29 (lines 1-12), as follows:

“After UV curing, the microlens was visually inspected at the stereomicroscope. In case of formation of air bubbles, the microlens was discarded (yield of the molding procedure: ~ 90 %, N > 30 molded lenses). The coverslip with the attached corrective lens was sealed to a customized metal or plastic support ring of appropriate diameter (Fig. 2C). The support ring, the coverslip and the aspherical lens formed the upper part of the corrected microendoscope, to be subsequently coupled to the proper GRIN rod (Table 2) using a custom-built opto-mechanical stage and NOA63 (Fig. 2C) 7. The GRIN rod was positioned perpendicularly to the glass coverslip, on the other side of the coverslip compared to the corrective lens, and aligned to the aspherical lens perimeter (Fig. 2C) under the guidance of a wide field microscope equipped with a camera. The yield of the assembly procedure for the probes used in this work was 100 % (N = 27 endoscopes). For further details on the assembly of corrected microendoscope see(7)”. 

Supplementary Figure 1: Is this really a good agreement between the design and measured profile? Does the figure error (~10 um in some cases on average) noticeably degrade the image?

As the Reviewer correctly noticed, the discrepancy between the simulated profile and the experimentally measured profile can be up to 5-10 microns at specific radial positions. This discrepancy could be due to issues with: (i) the fabrication of the microlens; (ii) the experimental measurement of the lens profile with the stylus profilometer. To discriminate among these two possibilities, we asked what would be the expected optical properties of the corrected endoscope should the corrective lens have the experimentally measured (not the simulated) profile. To this aim, we performed new optical simulations of the point spread function (PSF) of the corrected probe using, as corrective microlens profile, the average, experimentally measured, profile of a fabricated corrective lens. For both microendoscope types, we first fitted the mean experimentally measured profile of the fabricated lens with the aspherical function reported in equation (1) of the main text:

where:

-                is the radial distance from the optical axis;

-                is equal to 1⁄ , where R is the radius of curvature;

-                is the conic constant;

-                − are asphericity coefficients;

-                is the height of the microlens profile on-axis.

The fitting values of the parameters of equation (1) for the two lenses are reported for the Referee’s inspection here below (variables describing distances are expressed in mm):

Author response table 1.

Fitting values for the parameters of Equation (1) describing the profile of corrective microlens replicas measured with the stylus profilometer. Distances are expressed in mm.

We then assumed that the profile of the corrective microlenses were equal to the mean experimentally measured profiles and used the aspherical fitting functions in the optical simulations to compute the performance of corrected microendoscopes. For both microendoscope types, we found that the Strehl ratio was lower than 0.35, well below the theoretical diffractionlimited threshold of 0.8 (Maréchal criterion) at moderate distances from the optical axis (68 μm94 μm and 67 μm-92 μm on the focal plane in the object space, after the front end of the GRIN lens, for the 6.4 mm- and the 8.8 mm-long corrected microendoscope, respectively, Author response image 1A, C), and the PSF was strongly distorted (Author response image 1B, D).

Author response image 1.

Simulated optical performance of corrected probes with profiles of corrective microlenses equal to the mean experimentally measured profiles of fabricated corrective lenses. A) The Strehl ratio for the 6.4 mm-long corrected microendoscope with measured microlens profile (black dots) is computed on-axis (distance from the center of the FOV d = 0 µm) and at two radial distances off-axis (d = 68 μm and 94 μm on the focal plane in the object space) and compared to the Strehl ratio of the uncorrected (red line) and corrected (blue line) microendoscopes. B) Lateral (x,y) and axial (x,z) fluorescence intensity (F) profiles of simulated PSFs on-axis (left) and off-axis (right, at the indicated distance d computed on the focal plane in the object space) for the 6.4 mm-long corrected microendoscope with measured microlens profile. C) Same as in (A) for the 8.8 mm-long corrected microendoscope (off-axis d = 67 μm and 92 μm on the focal plane in the object space). D) Same as in (B) for the 8.8 mm-long corrected microendoscope.

These simulated findings are in contrast with the experimentally measured optical properties of our corrected endoscopes (Figure 3). In other words, these novel simulated results show that experimentally measured profiles of the corrected lenses are incompatible with the experimental measurements of the optical properties of the corrected endoscopes. Therefore, our experimental recording of the lens profile shown in Supplementary Figure 1 of the first submission (now Supplementary Figure 4) should be used only as a coarse measure of the lens shape and cannot be used to precisely compare simulated lens profiles with measured lens profiles.

How do individual radial profiles compare to the presented means?

We provide below a modified version of Supplementary Figure 4 (Supplementary Figure 1 in the first submission), where individual profiles measured with the stylus profilometer and the mean profile are displayed for both microendoscope types (Author response image 2). In the manuscript (Supplementary Figure 4), we would suggest to keep showing mean profiles ± standard errors of the mean, as we did in the original submission.

Author response image 2.

Characterization of polymeric corrective lens replicas. A) Stylus profilometer measurements were performed along the radius of the corrective polymer microlens replica for the 6.4 mm-long corrected microendoscope. Individual measured profiles (grey solid lines) obtained from n = 3 profile measurements on m = 3 different corrective lens replicas, plus the mean profile (black solid line) are displayed. B) Same as (A) for the 8.8 mm-long microendoscope.

What is the practical effect of the strong field curvature? Are the edges of the field, which come very close to the lens surface, a practical limitation?

A first practical effect of the field curvature is that structures at different z coordinates are sampled. The observed field curvature of corrected endoscopes may therefore impact imaging in brain regions characterized by strong axially organized anatomy (e.g., the pyramidal layer of the hippocampus), but would not significantly affect imaging in regions with homogeneous cell density within the axial extension of the field curvature (< 170 µm, see more details below). A second consequence of the field curvature, as the Referee correctly points out, is that cell at the border of the FOV are closer to the front end of the GRIN lens. In measurements of subresolved fluorescent layers (Figure 3A-D), we observed that the field curvature extends in the axial direction to ~ 110 μm and ~170 μm for the 6.4 mm- and the 8.8 mm-long microendoscopes, respectively. Considered that the nominal working distances on the object side of the 6.4 mm- and the 8.8 mm-long microendoscopes were, respectively, 210 μm and 178 μm (Table 3), structures positioned at the very edge of the FOV were ~ 100 μm and ~ 8 μm away from the GRIN front end for the 6.4 mm-long and for the 8.8 mm-long probe, respectively. Previous studies have shown that brain tissue within 50-100 μm from the GRIN front end may show signs of tissue reaction to the implant (Curreli et al. PLOS Biology 2022, Attardo et al. Nature 2015). Therefore, structures at the very edge of the FOV of the 8.8 mm-long endoscopes, but not those at the edge of the 6.4 mm-long endoscopes, may be within the volume showing tissue reaction. We added a paragraph in the text to discuss these points (page 18 lines 10-14).

The lenses appear to be corrected for monochromatic light; high-performance microscopes are generally achromatic. Is the bandwidth of two-photon excitation sufficient to warrant optimization over multiple wavelengths?

Thanks for this comment. All optical simulations described in the first submission were performed at a fixed wavelength (λ = 920 nm). Following the Referee’s request, we explored the effect of changing wavelength on the Strehl ratio using new optical simulations. We found that the Strehl ratio remains > 0.8 at least within ± 10 nm from λ = 920 nm (new Supplementary Figure 1A-D, left panels), which covers the limited bandwidth of our femtosecond laser. Moreover, these simulations demonstrate that, on a much wider wavelength range (800 - 1040 nm), high Strehl ratio is obtained, but at different z planes (new Supplementary Figure 1A-D, right panels). This means that the corrective lens is working as expected also for wavelengths which are different from 920 nm, with different wavelengths having the most enlarged FOV located at different working distances. These new results are now described on page 7 (lines 8-10).

GRIN lenses are often used to access a 3D volume by scanning in z (including in this study). How does the corrective lens affect imaging performance over the 3D field of view?

The optical simulations we did to design the corrective lenses were performed maximizing aberration correction only in the focal plane of the endoscope. Following the Referee’s comment, we explored the effect of aberration correction outside the focal plane using new optical simulations. In corrected endoscopes, we found that for off-axis rays (radial distance from the optical axis > 40 μm) the Strehl ratio was > 0.8 (Maréchal criterion) in a larger volume compared to uncorrected endoscopes (new Supplementary Figure 2), demonstrating that the aberration correction method developed in this study does extend beyond the focal plane for short distances. For example, at a radial distance of ~ 90 μm from the optical axis, the axial range in which the Strehl ratio was > 0.8 in corrected endoscopes was 28 μm and 19 μm for the 6.4 mm- and the 8.8 mm-long microendoscope, respectively. These new results are now described on page 7 (10-19).

(4) The in vivo images (Figure 7D) have a less impressive resolution and field than the ex vivo images (Figure 4B), and the reason for this is not clear. Given the difference in performance, how does this compare to an uncorrected endoscope in the same preparation? Is the reduced performance related to uncorrected motion, field curvature, working distance, etc?

In comparing images in Figure 4B with images shown in Figure 7D, the following points should be considered:

(1) Figure 4B is a maximum fluorescence intensity projection of multiple axial planes of a z-stack acquired through a thin brain slice (slice thickness: 50 µm) using 8 frame averages for each plane. In contrast, images in Figure 7D are median projection of a t-series acquired on a single plane in the awake mouse at 30 Hz resonant scanning imaging (8 min, 14,400 frames).

(2) Images of the fixed brain slice in Figure 4B were acquired at 1024 pixels x 1024 pixels resolution, nominal pixel size 0.45 µm/pixel, and with objective NA = 0.50, whereas in vivo images in Figure 7D were acquired at 512 pixels x 512 pixels resolution, nominal pixel size 0.72 - 0.84 µm/pixel, and with objective NA = 0.45.

(3) In the in vivo preparation (Figure 7D), excitation and emission light travel through > 180 µm of scattering and absorbing brain tissue, reducing spatial resolution and the SNR of the collected fluorescence signal.

(4) By shifting the sample in the x, y plane, in Figure 4B we could chose a FOV containing homogenously stained cells. x, y shifting and selecting across multiple FOVs was not possible in vivo, as the GRIN lens was cemented on the animal skull.

(5) Images in Figure 7D were motion corrected, but we cannot exclude that part of the decrease in resolution observed in Figure 7D when compared to images in Figure 4B are due to incomplete correction of motion artifacts.

For all the reasons listed above, we believe that it is expected to see smaller resolution and contrast in images recorded in vivo (Figure 7D) compared to images acquired in fixed tissue (Figure 4B).

Regarding the question of how do images from an uncorrected and a corrected endoscopes compared in vivo, we think that this comparison is better performed in fixed tissue (Figure 4) or in simulated calcium data (Figure 5-6), rather than in vivo recordings (Figure 7). In fact, in the brain of living mice motion artifacts, changes in fluorophore expression level, variation in the optical properties of the brain (e.g., the presence of a blood vessel over the FOV) may make the comparison of images acquired with uncorrected and corrected microendoscopes difficult, requiring a large number of animals to cancel out the contributions of these factors. Comparing optical properties in fixed tissue is, in contrast, devoid of these confounding factors. Moreover, the major advantage of quantifying how the optical properties of uncorrected and corrected endoscopes impact on the ability to extract information about neuronal activity in simulated calcium data is that, under simulated conditions, we can count on a known ground truth as reference (e.g., how many neurons are in the FOV, where they are, and which is their electrical activity). This is clearly not possible in the in vivo recordings.

Regarding Figure 7, there is no analysis of the biological significance of the calcium signals or even a description of where olfactory stimuli were presented.

We appreciate the Reviewer pointing out the lack of detailed analysis regarding the biological significance of the calcium signals and the presentation of olfactory stimuli in Figure 7. Our initial focus was on demonstrating the effectiveness of the optimized GRIN lenses for imaging deep brain areas like the piriform cortex, with an emphasis on the improved signal-tonoise ratio (SNR) these lenses provide. However, we agree that including more context about the experimental conditions would enhance the manuscript. To address this point, we added a new panel (Figure 7F) showing calcium transients aligned with the onset of olfactory stimulus presentations, which are now indicated by shaded light blue areas. Additionally, we have specified the timing of each stimulus presented in Figure 7E. This revision allows readers to better understand the relationship between the calcium signals and the olfactory stimuli.

The timescale of jGCaMP8f signals in Figure 7E is uncharacteristically slow for this indicator (compared to Zhang et al 2023 (Nature)), though perhaps this is related to the physiology of these cells or the stimuli.

Regarding the timescale of the calcium signals observed in Figure 7E, we apologize for the confusion caused by a mislabeling we inserted in the original manuscript. The experiments presented in Figure 7 were conducted using jGCaMP7f, not jGCaMP8f as previously stated (both indicators were used in this study but in separate experiments). We have corrected this error in the Results section (caption of Figure 7D, E). It is important to note that jGCaMP7f has a longer half-decay time compared to jGCaMP8f, which could in part account for the slower decay kinetics observed in our data. Furthermore, the prolonged calcium signals can be attributed to the physiological properties of neurons in the piriform cortex. Upon olfactory stimulation, these neurons often fire multiple action potentials, resulting in extended calcium transients that can last several seconds. This sustained activity has been documented in previous studies, such as Roland et al. (eLife 2017, Figure 1C therein) in anesthetized animals and Wang et al. (Neuron 2020, Figure 1E therein) in awake animals, which report similar durations for calcium signals.

(5) The claim of unprecedented spatial resolution across the FOV (page 18) is hard to evaluate and is not supported by references to quantitative comparisons. The promises of the method for future studies (pages 18-19) could also be better supported by analysis or experiment, but these are minor and to me, do not detract from the appeal of the work.

GRIN lens-based imaging of piriform cortex in the awake mouse had already been done in Wang et al., Neuron 2020. The GRIN lens used in that work was NEM-050-50-00920-S-1.5p (GRINTECH, length: 6.4 mm; diameter: 0.5 mm), similar to the one that we used to design the 6.4 mm-long corrected microendoscope. Here we used a microendoscope specifically design to correct off-axis aberrations and enlarge the FOV, in order to maximize the number of neurons recorded with the highest possible spatial resolution, while keeping the tissue invasiveness to the minimum. Following the Referee’s comments, we revised the sentence at page 19 (lines 68 from bottom) as follows:

“We used long corrected microendoscopes to measure population dynamics in the olfactory cortex of awake head-restrained mice with unprecedented combination of high spatial resolution across the FOV and minimal invasiveness(17)”.

(6) The text is lengthy and the material is repeated, especially between the introduction and conclusion. Consolidating introductory material to the introduction would avoid diluting interesting points in the discussion.

We thank the Reviewer for this comment. As suggested, we edited the Introduction and shortened the Discussion.

Reviewer #2 (Public review):

In this manuscript, the authors present an approach to correct GRIN lens aberrations, which primarily cause a decrease in signal-to-noise ratio (SNR), particularly in the lateral regions of the field-of-view (FOV), thereby limiting the usable FOV. The authors propose to mitigate these aberrations by designing and fabricating aspherical corrective lenses using ray trace simulations and two-photon lithography, respectively; the corrective lenses are then mounted on the back aperture of the GRIN lens.

This approach was previously demonstrated by the same lab for GRIN lenses shorter than 4.1 mm (Antonini et al., eLife, 2020). In the current work, the authors extend their method to a new class of GRIN lenses with lengths exceeding 6 mm, enabling access to deeper brain regions as most ventral regions of the mouse brain. Specifically, they designed and characterized corrective lenses for GRIN lenses measuring 6.4 mm and 8.8 mm in length. Finally, they applied these corrected long micro-endoscopes to perform high-precision calcium signal recordings in the olfactory cortex.

Compared with alternative approaches using adaptive optics, the main strength of this method is that it does not require hardware or software modifications, nor does it limit the system's temporal resolution. The manuscript is well-written, the data are clearly presented, and the experiments convincingly demonstrate the advantages of the corrective lenses.

The implementation of these long corrected micro-endoscopes, demonstrated here for deep imaging in the mouse olfactory bulb, will also enable deep imaging in larger mammals such as rats or marmosets.

We thank the Referee for the positive comments on our study. We address the points indicated by the Referee in the “Recommendation to the authors” section below.

Reviewer #3 (Public review):

Summary:

This work presents the development, characterization, and use of new thin microendoscopes (500µm diameter) whose accessible field of view has been extended by the addition of a corrective optical element glued to the entrance face. Two micro endoscopes of different lengths (6.4mm and 8.8mm) have been developed, allowing imaging of neuronal activity in brain regions >4mm deep. An alternative solution to increase the field of view could be to add an adaptive optics loop to the microscope to correct the aberrations of the GRIN lens. The solution presented in this paper does not require any modification of the optical microscope and can therefore be easily accessible to any neuroscience laboratory performing optical imaging of neuronal activity.

Strengths:

(1) The paper is generally clear and well-written. The scientific approach is well structured and numerous experiments and simulations are presented to evaluate the performance of corrected microendoscopes. In particular, we can highlight several consistent and convincing pieces of evidence for the improved performance of corrected micro endoscopes:

a) PSFs measured with corrected micro endoscopes 75µm from the centre of the FOV show a significant reduction in optical aberrations compared to PSFs measured with uncorrected micro endoscopes.

b) Morphological imaging of fixed brain slices shows that optical resolution is maintained over a larger field of view with corrected micro endoscopes compared to uncorrected ones, allowing neuronal processes to be revealed even close to the edge of the FOV.

c) Using synthetic calcium data, the authors showed that the signals obtained with the corrected microendoscopes have a significantly stronger correlation with the ground truth signals than those obtained with uncorrected microendoscopes.

(2) There is a strong need for high-quality micro endoscopes to image deep brain regions in vivo. The solution proposed by the authors is simple, efficient, and potentially easy to disseminate within the neuroscience community.

Weaknesses:

(1) Many points need to be clarified/discussed. Here are a few examples:

a) It is written in the methods: “The uncorrected microendoscopes were assembled either using different optical elements compared to the corrected ones or were obtained from the corrected

probes after the mechanical removal of the corrective lens.”

This is not very clear: the uncorrected microendoscopes are not simply the unmodified GRIN lenses?

We apologize for not been clear enough on this point. Uncorrected microendoscopes are not simply unmodified GRIN lenses, rather they are GRIN lenses attached to a round glass coverslip (thickness: 100 μm). The glass coverslip was included in ray-trace optical simulations of the uncorrected system and this is the reason why commercial GRIN lenses and corresponding uncorrected microendoscopes have different working distances, as reported in Tables 2-3. To make the text clearer, we added the following sentence at page 27 (last 4 lines):

“To evaluate the impact of corrective microlenses on the optical performance of GRIN-based microendoscopes, we also simulated uncorrected microendoscopes composed of the same optical elements of corrected probes (glass coverslip and GRIN rod), but in the absence of the corrective microlens”.

b) In the results of the simulation of neuronal activity (Figure 5A, for example), the neurons in the center of the FOV have a very large diameter (of about 30µm). This should be discussed.

Thanks for this comment. In synthetic calcium imaging t-series, cell radii were randomly sampled from a Gaussian distribution with mean = 10 µm and standard deviation (SD) = 3 µm. Both values were estimated from the literature (ref. no. 28: Suzuki & Bekkers, Journal of Neuroscience, 2011) as described in the Methods (page 35). In the image shown in Figure 5A, neurons near to the center of the FOV have radius of ~ 20 µm corresponding to the right tail of the distribution (mean + 3SD = 19 µm). It is also important to note that, for corrected microendoscopes, neurons in the central portion of the FOV appear larger than cells located near the edges of the FOV, because the magnification depends on the distance from the optical axis (see Figure 3E, F) and near the center the magnification is > 1 for both microendoscope types.

Also, why is the optical resolution so low on these images?

Images shown in Figure 5 are median fluorescence intensity projections of 5 minute-long simulated t-series. Simulated calcium data were generated with pixel size 0.8 μm/pixel and frame rate 30 Hz, similarly to in vivo recordings. In the simulations, pixels not belonging to any cell soma were assigned a value of background fluorescence randomly sampled from a normal distribution with mean and standard deviation estimated from experimental data, as described in the Methods section (page 37). To simulate activity, the mean spiking rate of neurons was set to 0.3 Hz, thus in a large fraction of frames neurons do not show calcium transients. Therefore, the median fluorescence intensity value of somata will be close to their baseline fluorescence value (_F_0). Since in simulations F0 values (~ 45-80 a.u.) were not much higher than the background fluorescence level (~ 45 a.u.), this may generate the appearance of low contrast image in Figure 5A. Finally, we suspect that PDF rendering also contributed to degrade the quality of those images. We will now submit high resolution images alongside the PDF file.

c) It seems that we can't see the same neurons on the left and right panels of Figure 5D. This should be discussed.

The Referee is correct. When we intersected the simulated 3D volume of ground truth neurons with the focal surface of microendoscopes, the center of the FOV for the 8.8 mmlong corrected microendoscope was located at a larger depth than the FOV of the 8.8 mm uncorrected microendoscope. This effect was due to the larger field curvature of corrected 8.8 mmlong endoscopes compared to 8.8 mm-long uncorrected endoscopes. This is the reason why different neurons were displayed for uncorrected and corrected endoscopes in Figure 5D. We added this explanation in the text at page 37 (lines 1-4). The text reads:

“Due to the stronger field curvature of the 8.8 mm-long corrected microendoscope (Figure 1C) compared to 8.8 mm-long uncorrected microendoscopes, the center of the corrected imaging focal surface resulted at a larger depth in the simulated volume compared to the center of the uncorrected focal surface(s). Therefore, different simulated neurons were sampled in the two cases”.

d) It is not very clear to me why in Figure 6A, F the fraction of adjacent cell pairs that are more correlated than expected increases as a function of the threshold on peak SNR. The authors showed in Supplementary Figure 3B that the mean purity index increases as a function of the threshold on peak SNR for all micro endoscopes. Therefore, I would have expected the correlation between adjacent cells to decrease as a function of the threshold on peak SNR. Similarly, the mean purity index for the corrected short microendoscope is close to 1 for high thresholds on peak SNR: therefore, I would have expected the fraction of adjacent cell pairs that are more correlated than expected to be close to 0 under these conditions. It would be interesting to clarify these points.

Thanks for raising this point. We defined the fraction of adjacent cell pairs more correlated than expected as the number of adjacent cell pairs more correlated than expected divided by the number of adjacent cell pairs. The reason why this fraction raises as a function of the SNR threshold is shown in Supplementary Figure 2 in the first submission (now Supplementary Figure 5). There, we separately plotted the number of adjacent cell pairs more correlated than expected (numerator) and the number of adjacent cell pairs (denominator) as a function of the SNR threshold. For both microendoscope types, we observed that the denominator more rapidly decreased with peak SNR threshold than the numerator. Therefore, the fraction of adjacent cell pairs more correlated than expected increases with the peak SNR threshold.

To understand why the denominator decreases with SNR threshold, it should be considered that, due to the deterioration of spatial resolution and attenuation of fluorescent signal collection as a function of the radial distance from the optical axis (see for example fluorescent film profiles in Figure 3A, C), increasing the threshold on the peak SNR of extracted calcium traces implies limiting cell detection to those cells located within smaller distance from the center of the FOV. This information is shown in Figure 5C, F.

In the manuscript text, this point is discussed at page 12 (lines 1-3 from bottom) and page 13 (lines 1-4):

“The fraction of pairs of adjacent cells (out of the total number of adjacent pairs) whose activity correlated significantly more than expected increased as a function of the SNR threshold for corrected and uncorrected microendoscopes of both lengths (Fig. 6A, F). This effect was due to a larger decrease of the total number of pairs of adjacent cells as a function of the SNR threshold compared to the decrease in the number of pairs of adjacent cells whose activity was more correlated than expected (Supplementary Figure 5)”.

e) Figures 6C, H: I think it would be fairer to compare the uncorrected and corrected endomicroscopes using the same effective FOV.

To address the Reviewer’s concern, we repeated the linear regression of purity index as a function of the radial distance using the same range of radial distances for the uncorrected and corrected case of both microendoscope types. Below, we provide an updated version of Figure 6C, H for the referee’s perusal. Please note that the maximum value displayed on the x-axis of both graphs is now corresponding to the minimum value between the two maximum radial distance values obtained in the uncorrected and corrected case (maximum radial distance displayed: 151.6 µm and 142.1 μm for the 6.4 mm- and the 8.8 mm-long GRIN rod, respectively). Using the same effective FOV, we found that the purity index drops significantly more rapidly with the radial distance for uncorrected microendoscopes compared to the corrected ones, similarly to what observed in the original version of Figure 6. The values of the linear regression parameters and statistical significance of the difference between the slopes in the uncorrected and corrected cases are stated in the Author response image 3 caption below for both microendoscope types. In the manuscript, we would suggest to keep showing data corresponding to all detected cells, as we did in the original submission.

Author response image 3.

Linear regression of purity index as a function of the radial distance. A) Purity index of extracted traces with peak SNR > 10 was estimated using a GLM of ground truth source contributions and plotted as a function of the radial distance of cell identities from the center of the FOV for n = 13 simulated experiments with the 6.4 mm-long uncorrected (red) and corrected (blue) microendoscope. Black lines represent the linear regression of data ± 95% confidence intervals (shaded colored areas). Maximum value of radial distance displayed: 151.6 μm. Slopes ± standard error (s.e.): uncorrected, (-0.0015 ± 0.0002) µm-1; corrected, (-0.0006 ± 0.0001) μm-1. Uncorrected, n = 991; corrected, n = 1156. Statistical comparison of slopes, p < 10^-10, permutation test. B) Same as (A) for n = 15 simulated experiments with the 8.8 mm-long uncorrected and corrected microendoscope. Maximum value of radial distance displayed: 142.1 μm. Slopes ± s.e.: uncorrected, (-0.0014 ± 0.0003) μm-1; corrected, (-0.0010 ± 0.0002) µm-1. Uncorrected, n = 718; corrected, n = 1328. Statistical comparison of slopes, p = 0.0082, permutation test.

f) Figure 7E: Many calcium transients have a strange shape, with a very fast decay following a plateau or a slower decay. Is this the result of motion artefacts or analysis artefacts?

Thank you for raising this point about the unusual shapes of the calcium transients in Figure 7E. The observed rapid decay following a plateau or a slower decay is indeed a result of how the data were presented in the original submission. Our experimental protocol consisted of 22 s-long trials with an inter-trial interval of 10 s (see Methods section, page 44). In the original figure, data from multiple trials were concatenated, which led to artefactual time courses and apparent discontinuities in the calcium signals. To resolve this issue, we revised Figure 7E to accurately represent individual concatenated trials. We also added a new panel (please see new Figure 7F) showing examples of single cell calcium responses in individual trials without concatenation, with annotations indicating the timing and identity of presented olfactory stimuli.

Also, the duration of many calcium transients seems to be long (several seconds) for GCaMP8f. These points should be discussed.

Author response: regarding the timescale of the calcium signals observed in Figure 7E, we apologize for the confusion caused by a mislabeling we inserted in the manuscript. The experiments presented in Figure 7 were conducted using jGCaMP7f, not jGCaMP8f as previously stated (both indicators were used in this study, but in separate experiments). We have corrected this error in the Results section (caption of Figure 7D, E). It is important to note that jGCaMP7f has a longer half-decay time compared to jGCaMP8f, which could in part account for the slower decay kinetics observed in our data. Furthermore, the prolonged calcium signals can be attributed to the physiological properties of neurons in the piriform cortex. Upon olfactory stimulation, these neurons often fire multiple action potentials, resulting in extended calcium transients that can last several seconds. This sustained activity has been documented in previous studies, such as Roland et al. (eLife 2017, Figure 1C therein) in anesthetized animals and Wang et al. (Neuron 2020, Figure 1E therein) in awake animals, which report similar durations for calcium signals. We cite these references in the text. We believe that these revisions and clarifications address the Reviewer's concern and enhance the overall clarity of our manuscript.

g) The authors do not mention the influence of the neuropil on their data. Did they subtract the neuropil's contribution to the signals from the somata? It is known from the literature that the presence of the neuropil creates artificial correlations between neurons, which decrease with the distance between the neurons (Grødem, S., Nymoen, I., Vatne, G.H. et al. An updated suite of viral vectors for in vivo calcium imaging using intracerebral and retro-orbital injections in male mice. Nat Commun 14, 608 (2023). https://doi.org/10.1038/s41467-023-363243; Keemink SW, Lowe SC, Pakan JMP, Dylda E, van Rossum MCW, Rochefort NL. FISSA: A neuropil decontamination toolbox for calcium imaging signals. Sci Rep. 2018 Feb 22;8(1):3493.

doi: 10.1038/s41598-018-21640-2. PMID: 29472547; PMCID: PMC5823956)

This point should be addressed.

We apologize for not been clear enough in our previous version of the manuscript. The neuropil was subtracted from calcium traces both in simulated and experimental data. Please note that instead of using the term “neuropil”, we used the word “background”. We decided to use the more general term “background” because it also applies to the case of synthetic calcium tseries, where neurons were modeled as spheres devoid of processes. The background subtraction is described in the Methods on page 39:

“F(t) was computed frame-by-frame as the difference between the average signal of pixels in each ROI and the background signal. The background was calculated as the average signal of pixels that: i) did not belong to any bounding box; ii) had intensity values higher than the mean noise value measured in pixels located at the corners of the rectangular image, which do not belong to the circular FOV of the microendoscope; iii) had intensity values lower than the maximum value of pixels within the boxes”.

h) Also, what are the expected correlations between neurons in the pyriform cortex? Are there measurements in the literature with which the authors could compare their data?

We appreciate the reviewer's interest in the correlations between neurons in the piriform cortex. The overall low correlations between piriform neurons we observed (Figure 8) are consistent with a published study describing ‘near-zero noise correlations during odor inhalation’ in the anterior piriform cortex of rats, based on extracellular recordings (Miura et al., Neuron 2013). However, to the best of our knowledge, measurements directly comparable to ours have not been described in the literature. Recent analyses of the correlations between piriform neurons were restricted to odor exposure windows, with the goal to quantify odor-specific activation patterns (e.g. Roland et al., eLife 2017; Bolding et al., eLife 2017, Pashkovski et al., Nature 2020; Wang et al., Neuron 2020). Here, we used correlation analyses to characterize the technical advancement of the optimized GRIN lens-based endoscopes. We showed that correlations of pairs of adjacent neurons were independent from radial distance (Figure 8B), highlighting homogeneous spatial resolution in the field of view.

(2) The way the data is presented doesn't always make it easy to compare the performance of corrected and uncorrected lenses. Here are two examples:

a) In Figures 4 to 6, it would be easier to compare the FOVs of corrected and uncorrected lenses if the scale bars (at the centre of the FOV) were identical. In this way, the neurons at the centre of the FOV would appear the same size in the two images, and the distances between the neurons at the centre of the FOV would appear similar. Here, the scale bar is significantly larger for the corrected lenses, which may give the illusion of a larger effective FOV.

We appreciate the Referee’s comment. Below, we explain why we believe that the way we currently present imaging data in the manuscript is preferable:

(1) current figures show images of the acquired FOV as they are recorded from the microscope (raw data), without rescaling. In this way, we exactly show what potential users will obtain when using a corrected microendoscope.

(2) In the current version of the figures, the fact that the pixel size is not homogeneous across the FOV, nor equal between uncorrected and corrected microendoscopes, is initially shown in Figure 3E, F and then explicitly stated throughout the manuscript when images acquired with a corrected microendoscope are shown.

(3) Rescaling images acquired with the corrected endoscopes gives the impression that the acquisition parameters were different between acquisitions with the corrected and uncorrected microendoscopes, which was not the case.

Importantly, the larger FOV of the corrected microendoscope, which is one of the important technological achievements presented in this study, can be appreciated in the images regardless of the presentation format.

b) In Figures 3A-D it would be more informative to plot the distances in microns rather than pixels. This would also allow a better comparison of the micro endoscopes (as the pixel sizes seem to be different for the corrected and uncorrected micro endoscopes).

The Referee is correct that the pixel size is different between the corrected and uncorrected probes. This is because of the different magnification factor introduced by the corrective microlens, as described in Figure 3E, F. The rationale for showing images in Figure 3AD in pixels rather than microns is the following:

(1) Optical simulations in Figure 1 suggest that a corrective optical element is effective in compensating for some of the optical aberrations in GRIN microendoscopes.

(2) After fabricating the corrective optical element (Figure 2), in Figure 3A-D we conduct a preliminary analysis of the effect of the corrective optical element on the optical properties of the GRIN lens. We observed that the microfabricated optical element corrected for some aberrations (e.g., astigmatism), but also that the microfabricated optical element was characterized by significant field curvature. This can be appreciated showing distances in pixels.

(3) The observed field curvature and the aspherical profile of the corrected lens prompted us to characterize the magnification factor of the corrected endoscopes as a function of the radial distance. We found that the magnification factor changed as a function of the radial distance (Figure 3E-F) and that pixel size was different between uncorrected and corrected endoscopes. We also observed that, in corrected endoscopes, pixel size was a function of the radial distance (Figure 3E-F).

(4) Once all of the above was established and quantified, we assigned precise pixel size to images of uncorrected and corrected endoscopes and we show all following images of the study (Figure 3G on) using a micron (rather than pixel) scale.

(3) There seems to be a discrepancy between the performance of the long lenses (8.8 mm) in the different experiments, which should be discussed in the article. For example, the results in Figure 4 show a considerable enlargement of the FOV, whereas the results in Figure 6 show a very moderate enlargement of the distance at which the person's correlation with the first ground truth emitter starts to drop.

Thanks for raising this point and helping us clarifying data presentation. Images in Figure 4B are average z-projections of z-stacks acquired through a mouse fixed brain slice and they were taken with the purpose of showing all the neurons that could be visualized from the same sample using an uncorrected and a corrected microendoscope. In Figure 4B, all illuminated neurons are visible regardless of whether they were imaged with high axial resolution (e.g., < 10 µm as defined in Figure 3J) or poor axial resolution. In contrast, in Figure 6J we evaluated the correlation between the calcium trace extracted from a given ROI and the real activity trace of the first simulated ground truth emitter for that specific ROI. The moderate increase in the correlation for the corrected microendoscope compared to the uncorrected microendoscope (Figure 6J) is consistent with the moderate improvement in the axial resolution of the corrected probe compared to the uncorrected probe at intermediate radial distances (60-100 µm from the optical axis, see Figure 3J). We added a paragraph in the Results section (page 14, lines 8-18) to summarize the points described above.

a) There is also a significant discrepancy between measured and simulated optical performance, which is not discussed. Optical simulations (Figure 1) show that the useful FOV (defined as the radius for which the size of the PSF along the optical axis remains below 10µm) should be at least 90µm for the corrected microendoscopes of both lengths. However, for the long microendoscopes, Figure 3J shows that the axial resolution at 90µm is 17µm. It would be interesting to discuss the origin of this discrepancy: does it depend on the microendoscope used?

As the Reviewer correctly pointed out, the size of simulated PSFs at a given radial distance (e.g., 90 µm) tends to be generally smaller than that of the experimentally measured PSFs. This might be due to multiple reasons:

(1) simulated PSFs are excitation PSFs, i.e. they describe the intensity spatial distribution of focused excitation light. On the contrary, measured PSFs result from the excitation and emission process, thus they are also affected by aberrations of light emitted by fluorescent beads and collected by the microscope.

(2) in the optical simulations, the Zemax file of the GRIN lenses contained first-order aberrations. High-order aberrations were therefore not included in simulated PSFs.

(3) intrinsic variability of experimental measurements (e.g., intrinsic variability of the fabrication process, alignment of the microendoscope to the optical axis of the microscope, the distance between the GRIN back end and the objective…) are not considered in the simulations.

We added a paragraph in the Discussion section (page 17, lines 9-18) summarizing the abovementioned points.

Are there inaccuracies in the construction of the aspheric corrective lens or in the assembly with the GRIN lens? If there is variability between different lenses, how are the lenses selected for imaging experiments?

The fabrication yield, i.e. the yield of generating the corrective lenses, using molding was ~ 90% (N > 30 molded lenses). The main limitation of this procedure was the formation of air bubbles between the mold negative and the glass coverslip. Molded lenses were visually inspected with the stereoscope and, in case of air bubble formation, they were discarded.

The assembly yield, i.e. the yield of correct positioning of the GRIN lens with respect to the coverslip, was 100 % (N = 27 endoscopes).

We added this information in the Methods at page 29 (lines 1-12), as follows:

“After UV curing, the microlens was visually inspected at the stereomicroscope. In case of formation of air bubbles, the microlens was discarded (yield of the molding procedure: ~ 90 %, N > 30 molded lenses). The coverslip with the attached corrective lens was sealed to a customized metal or plastic support ring of appropriate diameter (Fig. 2C). The support ring, the coverslip and the aspherical lens formed the upper part of the corrected microendoscope, to be subsequently coupled to the proper GRIN rod (Table 2) using a custom-built opto-mechanical stage and NOA63 (Fig. 2C) 7. The GRIN rod was positioned perpendicularly to the glass coverslip, on the other side of the coverslip compared to the corrective lens, and aligned to the aspherical lens perimeter (Fig. 2C) under the guidance of a wide field microscope equipped with a camera. The yield of the assembly procedure for the probes used in this work was 100 % (N = 27 endoscopes). For further details on the assembly of corrected microendoscope see(7)”.

Reviewer #1 (Recommendations for the authors):

(1) Page 4, what is meant by 'ad-hoc" in describing software control?

With “ad-hoc” we meant “specifically designed”. We revised the text to make this clear.

(2) It was hard to tell how the PSF was modeled for the simulations (especially on page 34, describing the two spherical shells of the astigmatic PSF and ellipsoids modeled along them). Images or especially videos that show the modeling would make this easier to follow.

Simulated calcium t-series were generated following previous work by our group (Antonini et al., eLife 2020), as stated in the Methods on page 37 (line 5). In Figure 4A of Antonini et al. eLife 2020, we provided a schematic to visually describe the procedure of simulated data generation. In the present paper, we decided not to include a similar drawing and cite the eLife 2020 article to avoid redundancy.

(3) Some math symbols are missing from the methods in my version of the text (page 36/37).

We apologize for the inconvenience. This issue arose in the PDF conversion of our Word document and we did not spot it at the time of submission. We will now make sure the PDF version of our manuscript correctly reports symbols and equations.

(4) The Z extent of stacks (i.e. number of steps) used to generate images in Figure 4 is missing.

We thank the Reviewer for the comment and we now revised the caption of Figure 4 and the Methods section as follows:

“Figure 4. Aberration correction in long GRIN lens-based microendoscopes enables highresolution imaging of biological structures over enlarged FOVs. A) jGCaMP7f-stained neurons in a fixed mouse brain slice were imaged using 2PLSM (λexc = 920 nm) through an uncorrected (left) and a corrected (right) microendoscope based on the 6.4 mm-long GRIN rod. Images are maximum fluorescence intensity (F) projections of a z-stack acquired with a 5 μm step size. Number of steps: 32 and 29 for uncorrected and corrected microendoscope, respectively. Scale bars: 50 μm. Left: the scale applies to the entire FOV. Right, the scale bar refers only to the center of the FOV; off-axis scale bar at any radial distance (x and y axes) is locally determined multiplying the length of the drawn scale bar on-axis by the corresponding normalized magnification factor shown in the horizontal color-coded bar placed below the image (see also Fig. 3, Supplementary Table 3, and Materials and Methods for more details). B) Same results for the microendoscope based on the 8.8 mm-long GRIN rod. Number of steps: 23 and 31 for uncorrected and corrected microendoscope, respectively”.

We also modified the text in the Methods (page 35, lines 1-2):

“(1024 pixels x 1024 pixels resolution; nominal pixel size: 0.45 µm/pixel; axial step: 5 µm; number of axial steps: 23-32; frame averaging = 8)”.

(5) Overall, the text is wordy and a bit repetitive and could be cut down significantly in length without loss of clarity. This is true throughout, but especially when comparing the introduction and discussion.

We edited the text (Discussion and Introduction), as suggested by the Reviewer.

(6) Although I don't think it's necessary, I would advise including comparison data with an uncorrected endoscope in the same in vivo preparation.

We thank the Referee for the suggestion. Below, we list the reasons why we decided not to perform the comparison between the uncorrected and corrected endoscopes in the in vivo preparation:

(1) We believe that the comparison between uncorrected and corrected endoscopes is better performed in fixed tissue (Figure 4) or in simulated calcium data (Figure 5-6), rather than in vivo recordings (Figure 7). In fact, in the brain of living mice motion artifacts, changes in fluorophore expression level, variation in the optical properties of the brain (e.g., the presence of a blood vessel over the FOV) may make the comparison of images acquired with uncorrected and corrected microendoscopes difficult, requiring a large number of animals to cancel out the contributions of all these factors. Comparing optical properties in fixed tissue is, in contrast, devoid of these confounding factors.

(2) A major advantage of quantifying how the optical properties of uncorrected and corrected endoscope impact on the ability to extract information about neuronal activity in simulated calcium data is that, under simulated conditions, we can count on a known ground truth as reference (e.g., how many neurons are in the FOV, where they are, and which is their electrical activity). This is clearly not possible under in vivo conditions.

(3) The proposed experiment requires to perform imaging in the awake mouse with a corrected microendoscope, then anesthetize the animal to carefully remove the corrective microlens using forceps, and finally repeat the optical recordings in awake mice with the uncorrected microendoscope. Although this is feasible (we performed the proposed experiment in Antonini et al. eLife 2020 using a 4.1 mm-long microendoscope), the yield of success of these experiments is low. The low yield is due to the fact that the mechanical force applied on top of the microendoscope to remove the corrective microlens may induce movement of the GRIN lens inside the brain, both in vertical and horizontal directions. This can randomly result in change of the focal plane, death or damage of the cells, tissue inflammation, and bleeding. From our own experience, the number of animals used for this experiment is expected to be high.

Reviewer #2 (Recommendations for the authors):

Below, I provide a few minor corrections and suggestions for the authors to consider before final submission.

(1) Page 5: when referring to Table 1 maybe add "Table 1 and Methods".

Following the Reviewer’s comment, we revised the text at page 6 (lines 4-5 from bottom) as follows:

“(see Supplementary Table 1 and Materials and Methods for details on simulation parameters)”.

(2) Page 8: "We set a threshold of 10 µm on the axial resolution to define the radius of the effective FOV (corresponding to the black triangles in Fig. 3I, J) in uncorrected and corrected microendoscopes. We observed an enlargement of the effective FOV area of 4.7 times and 2.3 times for the 6.4 mm-long micro endoscope and the 8.8 mm-long micro endoscope, respectively (Table 1). These findings were in agreement with the results of the ray-trace simulations (Figure 1) and the measurement of the subresolved fluorescence layers (Figure 3AD)." I could not find the information given in this paragraph, specifically:

a) Upon examining the black triangles in Figure 3I and J, the enlargement of the effective FOV does not appear to be 4.7 and 2.3 times.

In Figure 3I, J, black triangles mark the intersections between the curves fitting the data and the threshold of 10 µm on the axial resolution. The values on the x-axis corresponding to the intersections (Table 1, “Effective FOV radius”) represent the estimated radius of the effective FOV of the probes, i.e. the radius within which the microendoscope has spatial resolution below the threshold of 10 μm. The ratios of the effective FOV radii are 2.17 and 1.53 for the 6.4 mm- and the 8.8 mm-long microendoscope, respectively, which correspond to 4.7 and 2.3 times larger FOV (Table 1). To make this point clearer, we modified the indicated sentence as follows (page 10, lines 3-11 from bottom):

“We set a threshold of 10 µm on the axial resolution to define the radius of the effective FOV (corresponding to the black triangles in Fig. 3I, J) in uncorrected and corrected microendoscopes. We observed a relative increase of the effective FOV radius of 2.17 and 1.53 for the 6.4 mm- and the 8.8 mm-long microendoscope, respectively (Table 1). This corresponded to an enlargement of the effective FOV area of 4.7 times and 2.3 times for the 6.4 mm-long microendoscope and the 8.8

mm-long microendoscope, respectively (Table 1). These findings were in agreement with the results of the ray-trace simulations (Figure 1) and the measurement of the subresolved fluorescence layers (Figure 3A-D)."

b) I do not understand how the enlargements in Figure 3I and J align with the ray trace simulations in Figure 1, indicating an enlargement of 5.4 and 5.6.

In Figure 1C, E of the first submission we showed the Strehl ratio of focal spots focalized after the microendoscope, in the object plane, as a function of radial distance from the optical axis of focal spots focalized in the focal plane at the back end of the GRIN rod (“Objective focal plane” in Figure 1A, B), before the light has traveled along the GRIN lens. After reading the Referee’s comment, we realized this choice does not facilitate the comparison between Figure 1 and Figure 3I, J. We therefore decided to modify Figure 1C, E by showing the Strehl ratio of focal spots focalized after the microendoscope as a function of their radial distance from the optical axis in the objet plane (where the Strehl ratio is computed), after the light has traveled through the GRIN lens (radial distances are still computed on a plane, not along the curved focal surface represented by the “imaging plane” in Figure 1 A, B). Computing radial distances in the object space, we found that the relative increase in the radius of the FOV due to the correction of aberrations was 3.50 and 3.35 for the 6.4 mm- and the 8.8 mm-long microendoscope, respectively. We also revised the manuscript text accordingly (page 7, lines 6-8):

“The simulated increase in the radius of the diffraction-limited FOV was 3.50 times and 3.35 times for the 6.4 mm-long and 8.8 mm-long probe, respectively (Fig. 1C, E)”. We believe this change should facilitate the comparison of the data presented in Figure 1 and Figure 3.

Moreover, in comparing results in Figure 1 and Figure 3, it is important to keep in mind that:

(1) the definitions of the effective FOV radius were different in simulations (Figure 1) and real measurements (Figure 3). In simulations, we considered a theoretical criterion (Maréchal criterion) and set the lower threshold for a diffraction-limited FOV to a Strehl ratio value of 0.8. In real measures, the effective FOV radius obtained from fluorescent bead measurements was defined based on the empirical criterion of setting the upper threshold for the axial resolution to 10 µm.

(2) the Zemax file of the GRIN lenses contained low-order aberrations and not high-order aberrations.

(3) the small variability in some of the experimental parameters (e.g., the distance between the GRIN back end and the focusing objective) were not reflected in the simulations.

Given the reasons listed above, it is expected that the prediction of the simulations do not perfectly match the experimental measurements and tend to predict larger improvements of aberration correction than the experimentally measured ones.

c) Finally, how can the enlargement in Figure 3I be compared to the measurements of the sub-resolved fluorescence layers in Figures 3A-D? Could the authors please clarify these points?

When comparing measurements of subresolved fluorescent films and beads it is important to keep in mind that the two measures have different purposes and spatial resolution. We used subresolved fluorescent films to visualize the shape and extent of the focal surface of microendoscopes in a continuous way along the radial dimension (in contrast to bead measurements that are quantized in space). This approach comes at the cost of spatial resolution, as we are using fluorescent layers, which are subresolved in the axial but not in the radial dimension. Therefore, fluorescent film profiles are not used in our study to extract relevant quantitative information about effective FOV enlargement or spatial resolution of corrected microendoscopes. In contrast, to quantitatively characterize axial and lateral resolutions we used measurements of 100 nm-diameter fluorescent beads (therefore subresolved in the x, y, and z dimensions) located at different radial distances from the center of the FOV, using a much smaller nominal pixel size compared to the fluorescent films (beads, lateral resolution: 0.049 µm/pixel, axial resolution: 0.5 µm/pixel; films, lateral resolution: 1.73 µm/pixel, axial resolution: 2 µm/pixel).

(3) On page 15, the statement "significantly enlarge the FOV" should be more specific by providing the actual values for the increase. It would also be good to mention that this is not a xy lateral increase; rather, as one moves further from the center, more of the imaged cells belong to axially different planes.

The values of the experimentally determined FOV enlargements (4.7 times and 2.3 times for 6.4 mm- and 8.8 mm-long microendoscope, respectively) are provided in Table 1 and are now referenced on page 10. Following the Referee’s request, we added the following sentence in the discussion (page 18, lines 10-14) to underline that the extended FOV samples on different axial positions because of the field curvature effect:

“It must be considered, however, that the extended FOV achieved by our aberration correction method was characterized by a curved focal plane. Therefore, cells located in different radial positions within the image were located at different axial positions and cells at the border of the FOV were closer to the front end of the microendoscope”.

(4) On page 36, most of the formulas appear to be corrupted. This may have occurred during the conversion to the merged PDF. Please verify this and check for similar problems in other equations throughout the text as well.

We apologize for the inconvenience. This issue arose in the PDF conversion of our Word document and we did not spot it upon submission. We will now make sure the PDF version of our manuscript correctly reports symbols and equations.

(5) In the discussion, the authors could potentially add comments on how the verified performance of the corrective lenses depends on the wavelength and mention the range within which the wavelength can be changed without the need to redesign a new corrective lens.

Following this comments and those of other Reviewers, we explored the effect of changing wavelength on the Strehl ratio using new Zemax simulations. We found that the Strehl ratio remains > 0.8 within ± at least 10 nm from λ = 920 nm (new Supplementary Figure 1A-D, left panels), which covers the limited bandwidth of our femtosecond laser. Moreover, these simulations demonstrate that, on a much wider wavelength range (800 - 1040 nm), high Strehl ratio is obtained but at different z planes (new Supplementary Figure 1A-D, right panels). These new results are now described on page 7 (lines 8-10).

(6) Also, they could discuss if and how the corrective lens could be integrated into fiberscopes for freely moving experiments.

Following the Referee’s suggestion, we added a short text in the Discussion (page 21, lines 4-7 from bottom). It reads:

“Another advantage of long corrected microendoscopes described here over adaptive optics approaches is the possibility to couple corrected microendoscopes with portable 2P microscopes(42-44), allowing high resolution functional imaging of deep brain circuits on an enlarged FOV during naturalistic behavior in freely moving mice”.

(7) Finally, since the main advantage of this approach is its simplicity, the authors should also comment on or outline the steps to follow for potential users who are interested in using the corrective lenses in their systems.

Thanks for this comment. The Materials and Methods section of this study and that of Antonini et al. eLife 2020 describe in details the experimental steps necessary to reproduce corrective lenses and apply them to their experimental configuration.

Reviewer #3 (Recommendations for the authors):

(1) Suggestions for improved or additional experiments, data, or analyses, and Recommendations for improving the writing and presentation:

See Public Review.

Please see our point-by-point response above.

(2) Minor corrections on text and figures: a) Figure 6A: is the fraction of cells expressed in %?

Author response: yes, that is correct. Thank you for spotting it. We added the “%” symbol to the y label.

b) Figurer 8A, left: The second line is blue and not red dashed. In addition, it could be interesting to also show a line corresponding to the 0 value.

Thank you for the suggestions. We modified Figure 8 according to the Referee’s comments.

c) Some parts of equation (1) and some variables in the Material and Methods section are missing

We apologize for the inconvenience. This issue arose in the PDF conversion of our Word document and we did not spot it upon submission. We will now make sure the PDF version of our manuscript correctly reports symbols and equations.

d) In the methods, the authors mention a calibration ruler with ticks spaced every 10 µm along two orthogonal directions and refer to the following product: 4-dot calibration slide, Cat. No. 1101002300142, Motic, Hong Kong. However, this product does not seem to correspond to a calibration ruler.

We double check. The catalog number 1101002300142 is correct and product details can be found at the following link:

https://moticmicroscopes.com/products/calibration-slide-4-dots-1101002300142?srsltid=AfmBOorGYx9PcXtAlIMmSs_tEpxS4nX21qIcV8Kfn4qGwizQK3LYOQn3

Author Response

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

We are grateful to the reviewers for their appreciation of our study and thoughtful comments. In response to the main concern raised by all reviewers regarding the potential influences of external noise factors on intuitive inference, such as external disturbances or imperfect observations, we have conducted three new experiments suggested by the reviewers. These experiments were designed to: (1) assess the influence of external forces on humans’ judgments by implementing a wall to block wind disturbances from one direction, (2) examine human accuracy in predicting the landing position of a falling ball when its trajectory is obscured, and (3) evaluate the effect of object geometry on human judgment of stability. The findings from these experiments consistently support our proposal of the stochastic world model on gravity embedded in human mind. Besides, we have also addressed the rest comments from the reviewers in a one-by-one fashion.

Reviewer #1 (Recommendations For The Authors):

As mentioned in the public review, I did not find it entirely convincing that the study shows evidence for a Gaussian understanding of gravity. There are two studies that would bolster this claim: 1. Replicate experiment 1, but also ask people to infer whether there was a hidden force. If people are truly representing gravity as proposed in the paper, you should get no force inferences. However, if the reason the Gaussian gravity model works is that people infer unseen forces, this should come out clearly in this study.

Author response image 1.

Wall experiment to test the impact of external forces on the measurement of stochastic gravity. (a) Experimental setting. We replicated the original setup with the addition of a wall implemented on one side. Left: the overall experimental scene; Right, the scene shown to participants. (b) Human behaviors. Three participants conducted this experiment, and their responses consistently showed normal distributions without any skewness, suggesting that their judgments were not affected by the presence of the wall. These results support our claim that humans’ judgments on stability were not affected by potential concerns regarding external forces.

R1: We thank the reviewer for this suggestion. To directly test whether participants’ judgments were influenced by their implicit assumptions about external forces, we duplicated the original experimental setup with the addition of a wall implemented on one side (Supplementary Figure 4A). Before the start of the experiment, we explicitly informed the participants that the wall was designed to block wind, ensuring that any potential wind forces from the direction of the wall would not influence the collapse. If participants’ judgments were affected by external noise, we would expect to observe a skewed angle distribution. Contrary to this prediction, our results showed a normal distribution across all three participants tested (1 female; ages: 24-30), similar to the experiment without the wall (Supplementary Figure 4B). Therefore, the stochastic nature of intuitive inference on objects’ stability is embedded in the mind, not shaped by external forces or explicit instructions.

This new experiment has been added to the revised manuscript

Line 166-168: “…, and remained unchanged with the addition of a wall on one side to block potential external disturbances from wind (Supplementary Figure 4).”

(2) Similarly, you can imagine a simple study where you drop an object behind a floating occluder and you check where people produce an anticipatory fixation (i.e., where do they think the object will come out?). If people have a stochastic representation of gravity, this should be reflected in their fixations. But my guess is that everyone will look straight down.

Author response image 2.

Trajectory experiment to test the stochastic nature of gravity represented in the mind. (a) Experiment design. In this experiment, participants were required to use a mouse to determine the landing point of a parabolic trajectory (marked by the green dot), obscured by a grey rectangle. Note that the parabolic trajectory was determined only by gravity, and no external disturbances were introduced. The parameters used in this experiment are detailed in the upper right corner. (b) Predictive errors from three participants. The predictive errors from all three participants conform to Gaussian distributions with non-negligible variances. These results suggest the notion of an inherent stochastic property of gravity represented in the mind.

R2: We thank the reviewer for suggesting this thought experiment. However, when predicting the landing point of a falling object, participants may rely more on learned knowledge that an unimpeded object continues to fall in a straight line, rather than drawing on their intuitive physics. To avoid this potential confounding factor, we designed a similar experiment where participants were asked to predict the landing point of a parabolic trajectory, obscured by an occluder (Author response image 2A). In each trial, participants used a mouse (clicking the left button) to predict the landing point of each parabolic trajectory, and there were 100 trials in total. This design not only limits the impact of direct visual cues but also actively engages the mental simulation of intuitive physics. All three participants (1 female; ages: 24-30) were unable to accurately predict the landing points of the trajectories, and the predictive errors conformed to Gaussian distributions with different variances (Author response image 2B). Therefore, this new experiment confirms the stochastic nature of intuitive physics.

(3) I believe the correct alternative model should be the one that has uncertainty over unseen forces, which better captures current proposals in the field, and controls for the amount of uncertainty in the models.

R3: We thank the reviewers for the above-mentioned suggestions, and the findings from these two new experiments reinforce our proposal regarding the inherent stochastic characteristic of how the mind represents gravity.

(4) I was not convinced that the RL framework was set up correctly to tackle the questions it claims to tackle. What this shows is that you can evolve a world model with Gaussian gravity in a setup that has no external perturbations. That does not imply that that is how humans evolved their intuitive physics, particularly when creatures have evolved in a world full of external perturbations. Showing that when (1) there are hidden perturbations, and (2) these perturbations are learnable, but (3) the model nonetheless just learns stochastic gravity, would be a more convincing result.

R4: We completely agree with the reviewer that the RL framework serves primarily as a theoretic model to explain the stochastic nature of the world model on gravity, rather than as a demonstration of the developmental origins of intuitive physics abilities. The genesis of such abilities is multifaceted and unlikely to be fully replicated through a simple simulation like RL. Therefore, the purpose of incorporating the RL framework in our study is to demonstrate that external perturbances are not necessary for the development of a stochastic representation of gravity. In fact, introducing additional external noise into the RL framework likely heightens the uncertainty in learning gravity’s direction, potentially amplifying, rather than diminishing, the stochastic nature of mental gravity.

In revision, we have clarified the role of the RL framework

Line 265-277: “While the cognitive impenetrability and the self-consistency observed in this study, without resorting to an external perturbation, favor the stochastic model over the deterministic one, the origin of this stochastic feature of the world model is unclear.

Here we used a reinforcement learning (RL) framework to unveil this origin, because our intelligence emerges and evolves under the constraints of the physical world. Therefore, the stochastic feature may emerge as a biological agent interacts with the environment, where the mismatches between external feedback from the environment and internal expectations from the world model are in turn used to fine-tune the world model (Friston et al., 2021; MacKay, 1956; Matsuo et al., 2022). Note that a key aspect of the framework is determining whether the stochastic nature of the world model on gravity emerges through this interaction, even in the absence of external noise.”

(5) Some comments on the writing:

The word 'normality' is used to refer to people's judgments about whether a tower collapsed looked 'normal'. I was a bit confused by this because normality can also mean 'Gaussian' and the experiments are also sampling from Gaussian distributions. There were several points where it took me a second to figure out which sense of 'normality' the paper was using. I would recommend using a different term.

R5: We are sorry for the confusion. In revision, the term “normality” has been replaced with “confidence level about normal trajectory”.

(6) One small comment is that Newton's laws are not a faithful replica of the "physical laws of the world" they are a useful simplification that only works at certain timescales. I believe some people propose Newtonian physics as a model of intuitive physics in part because it is a rapid and useful approximation of complex physical systems, and not because it is an untested assumption of perfect correspondence.

R6: We are sorry for the inaccurate expression. We have revised our statements in the manuscript Line 15-16: “We found that the world model on gravity was not a faithful replica of the physical laws, but instead encoded gravity’s vertical direction as a Gaussian distribution.”

(7) Line 49-50: Based on Fig 1d, lower bound of possible configurations for 10 blocks is ~17 in log-space, which is about 2.5e7. But the line here says it's 3.72e19, which is much larger. Sorry if I am missing something.

R7: We thank the reviewer to point out this error. We re-calculated the number of possible configurations using the formula (3) in the appendix, and the number of configurations with 10 blocks is:

Thus,

This estimated number is much larger than that in our previous calculation, which has been corrected in the revised text.

Line 827-829: “d) The lower bound of configurations’ possible number and the number of blocks in a stack followed an exponential relationship with a base of 10. The procedure can create at least 1.14×1050 configurations for stacks consisting of 10 blocks.”

Line 49-50: “… but the universal cardinality of possible configurations is at least 1.14×1050 (Supplementary Figure 1), …”

Line 1017-1018: “… the number of configurations can be estimated with formula (9), which is 1.14×1050.”

(8) Lines 77-78: "A widely adopted but not rigorously tested assumption is that the world model in the brain is a faithful replica of the physical laws of the world." This risks sounding like you are asserting that colleagues in the field do not rigorously test their models. I think you meant to say that they did not 'directly test', rather than 'rigorously test'. If you meant rigorous, you might want to say more to justify why you think past work was not rigorous.

R8: We apologize for the inappropriate wording, the sentence has been revised and we illustrate the motivation more comprehensively in the revised text,

Line 76-92: “A prevailing theory suggests that the world model in the brain accurately mirrors the physical laws of the world (Allen et al., 2020; Battaglia et al., 2013; Zhou et al., 2022). For example, the direction of gravity encoded in the world model, a critical factor in stability inference, is assumed to be straight downward, aligning with its manifestation in the physical world. To explain the phenomenon that tall and thin objects are subjectively perceived as more unstable compared to short and fat ones (Supplementary Figure 2), external noise, such as imperfect perception and assumed external forces, is introduced to influence the output of the model. However, when the brain actively transforms sensory data into cognitive understanding, these data can become distorted (Kriegeskorte and Douglas, 2019; Naselaris et al., 2011), hereby introducing uncertainty into the representation of gravity’s direction. In this scenario, the world model inherently incorporates uncertainty, eliminating the need for additional external noise to explain the inconsistency between subjective perceptions of stability and the actual stability of objects. Note that this distinction of these two theories is nontrivial: the former model implies a deterministic representation of the external world, while the latter suggests a stochastic approach.”

(9) Lines 79-84 States that past models encode gravity downward. It then says that alternatively there is consensus that the brain uses data from sensory organs and adds meaning to them. I think there might be a grammatical error here because I did not follow why saying there is 'consensus' on something is a theoretical alternative. I also had trouble following why those two statements are in opposition. Is any work on physics engines claiming the brain does not take data from sensory organs and add meaning to them?

R9: We are sorry for the confusion. Here we intend to contrast the deterministic model (i.e., the uncertainty comes from outside the model) with the stochastic model (i.e., the uncertainty is inherently built into the model). In revision, we have clarified the intention. For details, please see R8.

(10) Lines 85-88: Following on the sentence above, you then conclude that the representation of the world may therefore not be the same as reality. I did not understand why this followed. It seems you are saying that, because the brain takes data from sensory organs, therefore its representations may differ from reality.

R10: Again, we are sorry about the confusion. Please see the revised text in R8.

(11) Lines 190-191: I had trouble understanding this sentence. I believe you are missing an adjective to clarify that participants were more inclined to judge taller stacks as more likely to collapse.

R11: We are sorry for the confusion. What we intended to state here is that participants’ judgment was biased, showing a tendency to predict a collapse for stacks regardless of their actual stability. We have revised this confusing sentence in the revision. Line 202–204: “However, the participants showed an obvious bias towards predicting a collapse for stacks regardless of their actual stability, as the dots in Fig 2b are more concentrated on the lower side of the diagonal line.”

(12) Line 201: I don't think it's accurate to say that MGS "perfectly captured participants' judgments" unless the results are actually perfect.

R12: We agree, and in revision we have toned down the statement Line 213–214: “…, the MGS, in contrast to the NGS, more precisely reflected participants’ judgments of stability …”

Reviewer #2 (Recommendations For The Authors):

I think this is an impressive set of experiments and modeling work. The paper is nicely written and I appreciate the poetic license the authors took at places in the manuscript. I only have clarification points and suggest a simple experiment that could lend further support to their conclusions. 1. In my opinion, the impact of this work is twofold. First, the suggestion that gravity is represented as a distribution of the world and not a result of (inferred) external perturbations. Second, that the distribution is advantageous as it balances speed and accuracy, and lessens computational processing demands (i.e., number of simulations). The second point here is contingent on the first point, which is really only supported by the RL model and potentially the inverted scene condition. I am somewhat surprised that the RL model does not converge on a width much smaller than ~20 degrees after 100,000 simulations. From my understanding, it was provided feedback with collapses based on natural gravity (deterministically downward). Why is learning so slow and the width so large? Could it be the density of the simulated world model distribution? If the model distribution of Qs was too dense, then Q-learning would take forever. If the model distribution was too sparse, then its final estimate would hit a floor of precision. Could the authors provide more details on the distribution of the Qs for the RL model?

Author response image 3.

RL learning curves as a function of θ angle with different sampling densities and learning rates. Learning rates were adjusted to low (a), intermediate (b) and high (c) settings, while sampling densities were chosen at four levels: 5x5, 11x11, 31x31, and 61x61 shown from the left to the right. Two key observations emerged from the simulations as the reviewer predicted. First, higher learning rates resulted in a more rapid decline in learning curves but introduced larger variances. Second, increased sampling density necessitated more iterations for convergence. Note that in all simulations, we limited the iterations to 1,000 times (as opposed to 100,000 times reported in the manuscript) to demonstrate the trend without excessive computational demands.

R1: To illustrate the distribution of the Q-values for the RL model, we re-ran the RL model with various learning rates and sampling densities (Author response image 3). These results support the reviewer’s prediction that higher learning rates resulted in a more rapid decline in learning curves but introduced larger variances, and increased sampling density requires more iterations for convergence.

This simulation also elucidates the slower learning observed in the experiment described in the text, where the force sphere was divided into 61x61 angle pairs, and the learning rate was set to 0.15. This set of parameters ensured convergence within a reasonable brief timeframe while maintaining high-resolution force assessments.

Besides, the width of the Gaussian distribution is mainly determined by the complexity of stacks. As shown in Figure 3c and Supplementary Figure 9, stacks with fewer blocks (i.e., less complex) caused a larger width, whereas those with more blocks resulted in a narrower spread. In the study, we used a collection of stacks varying from 2 to 15 blocks to simulate the range of stacks humans typically encounter in daily life.

In revision, we have incorporated these insights suggested by the reviewer to clarify the performance of the RL framework:

Line 634-639: “The angle density and learning rate are two factors that affect the learning speed. A larger angle density prolongs the time to reach convergence but enables a more detailed force space; a higher learning rate accelerates convergence but incurs larger variance during training. To balance speed and convergence, we utilized 100,000 configurations for the training.”

Line 618-619: “…, separately divided them into 61 sampling angles across the spherical force space (i.e., the angle density).”

(2) Along similar lines, the authors discuss the results of the inverted science condition as reflecting cognitive impenetrability. However, do they also interpret it as support for an intrinsically noisy distribution of gravity? I would be more convinced if they created a different scene that could have the possibility of affecting the direction of an (inferred) external perturbation - a previously held explanation of the noisy world model. For example, a relatively simple experiment would be to have a wall on one side of the scene such that an external perturbation would be unlikely to be inferred from that direction. In the external perturbation account, phi would then be affected resulting in a skewed distribution of angle pairs. However, in the authors' stochastic world model phi would remain unaffected resulting in the same uniform distribution of phi the authors observed. In my opinion, this would provide more compelling evidence for the stochastic world model.

Author response image 4.

Wall experiment to test the impact of external forces on the measurement of stochastic gravity. (a) Experimental setting. We replicated the original setup with the addition of a wall implemented on one side. Left: the overall experimental scene; Right, the scene shown to participants. (b) Human behaviors. Three participants conducted this experiment, and their responses consistently showed normal distributions without any skewness, suggesting that their judgments were not affected by the presence of the wall. These results support our claim that humans’ judgments on stability were not affected by potential concerns regarding external forces.

R2: We thank the reviewer for this suggestion. Following the reviewer’s concern, we designed the experiment with the addition of a wall implemented on one side (Supplementary figure 4A). We explicitly informed the participants that the wall was designed to block wind before the start of the experiment, ensuring no potential wind forces from the direction of the wall to influence the collapse trajectory of configurations. Participants need to judge if the trajectory was normal. If participants’ judgments were influenced by external noises, we would expect to observe a skewed angle distribution. However, our results still showed a normal distribution across all participants tested, consistent with the experiment without the wall (Supplementary figure 4B). This experiment suggested the stochastic nature of intuitive inference on objects’ stability is embedded in the mind, rather than shaped by external forces or explicit instructions.

We revised the original manuscript, and added this new experiment

Line 166-168: “…, and remained unchanged with the addition of a wall on one side to block potential external disturbances from wind (Supplementary Figure 4).”

(3) I didn't completely follow the authors' explanation for the taller objects illusion. On lines 229-232, the authors state that deviations from gravity's veridical direction are likely to accumulate with the height of the objects. Is this because, in the stochastic world model account, each block gets its own gravity vector that is sampled from the distribution? The authors should clarify this more explicitly. If this is indeed the author's claim, then it would seem that it could be manipulated by varying the dimensions of the blocks (or whatever constitutes an object).

R3: We are sorry for the confusion caused by the use of the term ‘accumulate’. In the study, there is only one gravity vector sampled from the distribution for the entire structure, rather than each block having a unique gravity vector. The height illusion is attributed to the fact that the center of gravity in taller objects is more susceptible to influence when gravity deviates slightly from a strictly downward direction. This is especially true for objects consisting of multiple blocks stacked atop one another. In revision, we have removed the confusing term ‘accumulate’ for clarification.

Line 242-244: “…, because the center of gravity in taller objects is more susceptible to influence when gravity deviates slightly from a strictly downward direction during humans’ internal simulations.”

(4) The authors refer to the RL simulations as agent-environment interactions, but in reality, the RL model does not interact with the blocks. Would experience-dependent or observation be more apropos?

R4: We completely agree. Indeed, the RL model did not manipulate stacks; rather, it updated its knowledge of natural gravity based on the discrepancies between the RL model’s predictions and observed outcomes. In revision, we have removed the confusing term ‘agent-environment interactions’ and clarified its intended meaning.

Line 19-22: “Furthermore, a computational model with reinforcement learning revealed that the stochastic characteristic likely originated from experience-dependent comparisons between predictions formed by internal simulations and the realities observed in the external world, …”

Reviewer #3 (Public Review):

(1) In spite of the fact that the Mental Gravity Simulation (MGS) seems to predict the data of the two experiments, it is an untenable hypothesis. I give the main reason for this conclusion by illustrating a simple thought experiment. Suppose you ask subjects to determine whether a single block (like those used in the simulations) is about to fall. We can think of blocks of varying heights. No matter how tall a block is, if it is standing on a horizontal surface it will not fall until some external perturbation disturbs its equilibrium. I am confident that most human observers would predict this outcome as well. However, the MSG simulation would not produce this outcome. Instead, it would predict a non-zero probability of the block to tip over. A gravitational field that is not perpendicular to the base has the equivalent effect of a horizontal force applied on the block at the height corresponding to the vertical position of the center of gravity. Depending on the friction determined by the contact between the base of the block and the surface where it stands there is a critical height where any horizontal force being applied would cause the block to fall while pivoting about one of the edges at the base (the one opposite to where the force has been applied). This critical height depends on both the size of the base and the friction coefficient. For short objects this critical height is larger than the height of the object, so that object would not fall. But for taller blocks, this is not the case. Indeed, the taller the block the smaller the deviation from a vertical gravitational field is needed for a fall to be expected. The discrepancy between this prediction and the most likely outcome of the simple experiment I have just outlined makes the MSG model implausible. Note also that a gravitational field that is not perpendicular to the ground surface is equivalent to the force field experienced by the block while standing on an inclined plane. For small friction values, the block is expected to slide down the incline, therefore another prediction of this MSG model is that when we observe an object on a surface exerting negligible friction (think of a puck on ice) we should expect that object to spontaneously move. But of course, we don't, as we do not expect tall objects that are standing to suddenly fall if left unperturbed. In summary, a stochastic world model cannot explain these simple observations.

Author response image 5.

Differentiating Subjectivity from Objectivity. In both Experiment 1 (a) and Experiment 2 (b), participants were instructed to determine which shape appeared most stable. Objectively, in the absence of external forces, all shapes possess equal stability. Yet, participants typically perceived the shape on the left as the most stable because of its larger base area. The discrepancy between objective realities and subjective feelings, as we propose, is attributed to the human mind representing gravity’s direction as a Gaussian distribution, rather than as a singular value pointing directly downward.

R1: We agree with the reviewer that objects will remain stable until disturbed by external forces. However, in many cases, this is a clear discrepancy between objective realities and subjective feelings. For example, electromagnetic waves associated with purple and red colors are the farthest in the electromagnetic space, yet purple and red are the closest colors in the color space. Similarly, as shown in Supplementary Figure 4, in reality all shapes possess equal stability in the absence of external forces. Yet, humans typically perceive the shape on the left as more stable because of its larger base area. In this study, we tried to explore the mechanism underlying this discrepancy by proposing that the human mind represents gravity’s direction as a Gaussian distribution, rather than as a singular value pointing directly downward.

In revision, we have clarified the rationale of this study

Line 76-98: “A prevailing theory suggests that the world model in the brain accurately mirrors the physical laws of the world (Allen et al., 2020; Battaglia et al., 2013; Zhou et al., 2022). For example, the direction of gravity encoded in the world model, a critical factor in stability inference, is assumed to be straight downward, aligning with its manifestation in the physical world. To explain the phenomenon that tall and thin objects are subjectively perceived as more unstable compared to short and fat ones (Supplementary Figure 2), external noise, such as imperfect perception and assumed external forces, is introduced to influence the output of the model. However, when the brain actively transforms sensory data into cognitive understanding, these data can become distorted (Kriegeskorte and Douglas, 2019; Naselaris et al., 2011), hereby introducing uncertainty into the representation of gravity’s direction. In this scenario, the world model inherently incorporates uncertainty, eliminating the need for additional external noise to explain the inconsistency between subjective perceptions of stability and the actual stability of objects. Note that this distinction of these two theories is nontrivial: the former model implies a deterministic representation of the external world, while the latter suggests a stochastic approach. Here, we investigated these two alternative hypotheses regarding the construction of the world model in the brain by examining how gravity’s direction is represented in the world model when participants judged object stability.”

(2) The question remains as to how we can interpret the empirical data from the two experiments and their agreement with the predictions of the stochastic world model if we assume that the brain has internalized a vertical gravitational field. First, we need to look more closely at the questions posed to the subjects in the two experiments. In the first experiment, subjects are asked about how "normal" a fall of a block construction looks. Subjects seem to accept 50% of the time a fall is normal when the gravitational field is about 20 deg away from the vertical direction. The authors conclude that according to the brain, such an unusual gravitational field is possible. However, there are alternative explanations for these findings that do not require a perceptual error in the estimation of the direction of gravity. There are several aspects of the scene that may be misjudged by the observer. First, the 3D interpretation of the scene and the 3D motion of the objects can be inaccurate. Indeed, the simulation of a normal fall uploaded by the authors seems to show objects falling in a much weaker gravitational field than the one on Earth since the blocks seem to fall in "slow motion". This is probably because the perceived height of the structure is much smaller than the simulated height. In general, there are even more severe biases affecting the perception of 3D structures that depend on many factors, for instance, the viewpoint.

R2: We thank the reviewer for highlighting several potential confounding factors in our study. We address each of these concerns point-by-point:

(a) Misinterpretation of the 3D scene and motion. In Response Figure 4 shown above, there is no 3D structure, yet participants’ judgment on stability still deviated from objective realities. In addition, the introduction of 3D motion was to aid in understanding the stacks’ 3D structure. Previous studies without 3D motion have reported similar findings (Allen et al., 2020). Therefore, regardless of whether objects are presented in 2D or 3D, or in static or in motion formats, humans’ judgment on object stability appears consistent.

(b) Errors in perceived height. While there might be discrepancies between perceived and simulated heights, such errors are systematic across all conditions. Therefore, they may affect the width of the Gaussian distribution but do not fundamentally alter its existence.

(c) The viewpoint. In one experiment, we inverted gravity’s direction to point upward, diverging from common daily experience. Despite this change in viewpoint, the Gaussian distribution was still observed. That is, the viewpoint appears not a key factor in influencing how gravity’s direction is represented as a Gaussian distribution in our mental world.

In summary, both our and previous studies (Allen et al., 2020; Battaglia et al., 2013) agree that humans’ subjective assessments of objects’ stability deviate from actual stability due to noise in mental simulation. Apart from previous studies, we suggest that this noise is intrinsic, rather than stemming from external forces or imperfect observations.

(3) Second, the distribution of weight among the objects and the friction coefficients acting between the surfaces are also unknown parameters. In other words, there are several parameters that depend on the viewing conditions and material composition of the blocks that are unknown and need to be estimated. The authors assume that these parameters are derived accurately and only that assumption allows them to attribute the observed biases to an error in the estimate of the gravitational field. Of course, if the direction of gravity is the only parameter allowed to vary freely then it is no surprise that it explains the results. Instead, a simulation with a titled angle of gravity may give rise to a display that is interpreted as rendering a vertical gravitational field while other parameters are misperceived. Moreover, there is an additional factor that is intentionally dismissed by the authors that is a possible cause of the fall of a stack of cubes: an external force. Stacks that are initially standing should not fall all of a sudden unless some unwanted force is applied to the construction. For instance, a sudden gust of wind would create a force field on a stack that is equivalent to that produced by a tilted gravitational field. Such an explanation would easily apply to the findings of the second experiment. In that experiment subjects are explicitly asked if a stack of blocks looks "stable". This is an ambiguous question because the stability of a structure is always judged by imagining what would happen to the structure if an external perturbation is applied. The right question should be: "do you think this structure would fall if unperturbed". However, if stability is judged in the face of possible external perturbations then a tall structure would certainly be judged as less stable than a short structure occupying the same ground area. This is what the authors find. What they consider as a bias (tall structures are perceived as less stable than short structures) is instead a wrong interpretation of the mental process that determines stability. If subjects are asked the question "Is it going to fall?" then tall stacks of sound structure would be judged as stable as short stacks, just more precarious.

R3: Indeed, the external forces suggested by the reviewer certainly influence judgments of objects’ stability. The critical question, however, is whether humans’ judgments on objects’ stability accurately mirror the actual stability of objects in the absence of external forces. To address this question, we designed two new experiments.

Experiment 1: we duplicated the original experimental setup with the addition of a wall implemented on one side (Supplementary Figure 4A). We explicitly informed the participants that the wall could block wind, ensuring that no potential wind from the direction of the wall could influence the configuration. If participants’ judgments were affected by external noise, we would expect to observe a skewed angle distribution. Contrary to this prediction, our results showed a normal distribution across all three participants (Age: 25-30, two females), which is similar to the experiment without the wall (Supplementary Figure 4B).

Author response image 6.

Wall experiment to test the impact of external forces on the measurement of stochastic gravity. (a) Experimental setting. We replicated the original setup with the addition of a wall implemented on one side. Left: the overall experimental scene; Right, the scene shown to participants. (b) Human behaviors. Three participants conducted this experiment, and their responses consistently showed normal distributions without any skewness, suggesting that their judgments were not affected by the presence of the wall. These results support our claim that humans’ judgments on stability were not affected by potential concerns regarding external forces.

Experiment 2: The second experiment adopted another paradigm to test the hypothesis of stochastic mental simulation. Consider humans to infer the landing point of a parabolic trajectory that was obscured by an occlude (Author response image 2A), the stochastic mental simulation predicted that humans’ behavior follows a Gaussian distribution. However, if humans’ judgments were influenced by external noise, the landing points could not be Gaussian. The experiment consists of 100 trials in total, and in each trial participants used a mouse to predict the landing point of each trajectory by clicking the left button. Our results found all three participants (1 female; ages: 24-30) were unable to accurately predict the landing points of the trajectories, and the predictive errors conformed to Gaussian distributions with different variances (Author response image 2B). Therefore, this new experiment confirms the stochastic nature of intuitive physics.

Author response image 7.

Trajectory experiment to test the stochastic nature of gravity represented in the mind. (a) Experiment design. In this experiment, participants were required to use a mouse to determine the landing point of a parabolic trajectory (marked by the green dot), obscured by a grey rectangle. Note that the parabolic trajectory was determined only by gravity, and no external disturbances were introduced. The parameters used in this experiment are detailed in the upper right corner. (b) Predictive errors from three participants. The predictive errors from all three participants conform to Gaussian distributions with non-negligible variances. These results suggest the notion of an inherent stochastic property of gravity represented in the mind.

(4) The RL model used as a proof of concept for how the brain may build a stochastic prior for the direction of gravity is based on very strong and unverified assumptions. The first assumption is that the brain already knows about the force of gravity, but it lacks knowledge of the direction of this force of gravity. The second assumption is that before learning the brain knows the effect of a gravitational field on a stack of blocks. How can the brain simulate the effect of a non-vertical gravitational field on a structure if it has never observed such an event?

R4: We agree with the reviewer that the RL framework serves primarily as a theoretic model to explain the stochastic nature of the world model on gravity, rather than as a demonstration of the developmental origins of intuitive physics abilities. The genesis of such abilities is multifaceted and unlikely to be fully replicated through a simple simulation like RL. Therefore, the purpose of incorporating the RL framework in our study is to demonstrate that external perturbances are not necessary for the development of a stochastic representation of gravity.

In revision, we have clarified the role of the RL framework

Line 265-277: “While the cognitive impenetrability and the self-consistency observed in this study, without resorting to an external perturbation, favor the stochastic model over the deterministic one, the origin of this stochastic feature of the world model is unclear.

Here we used a reinforcement learning (RL) framework to unveil this origin, because our intelligence emerges and evolves under the constraints of the physical world. Therefore, the stochastic feature may emerge as a biological agent interacts with the environment, where the mismatches between external feedback from the environment and internal expectations from the world model are in turn used to fine-tune the world model (Friston et al., 2021; MacKay, 1956; Matsuo et al., 2022). Note that a key aspect of the framework is determining whether the stochastic nature of the world model on gravity emerges through this interaction, even in the absence of external noise.”

(5) The third assumption is that from the visual input, the brain is able to figure out the exact 3D coordinates of the blocks. This has been proven to be untrue in a large number of studies. Given these assumptions and the fact that the only parameters the RL model modifies through learning specify the direction of gravity, I am not surprised that the model produces the desired results.

Author response image 8.

Perception Uncertainty in 3D stacks structures. (a) Experimental design. A pair of two stacks with similar placements of blocks were presented sequentially to participants, who were instructed to judge whether the stacks were identical and to rate their confidence in this judgment. Each stack was presented on the screen for 2 seconds. (b) Behavior Performance. Three participants (2 males, age range: 24-30) were recruited to the experiment. The confidence in determining whether a pair of stacks remained unchanged rapidly decreased when each block had a very small displacement, suggesting humans could keenly perceive trivial changes in configurations. The x-axis denotes the difference in block placement between stacks, with the maximum value (0.4) corresponding to the length of a block’s short side. The Y-axis denotes humans’ confidence in reporting no change. The red curve illustrates the average confidence level across 4 runs, while the yellow curve is the confidence level of each run.

R5: Indeed, uncertainty is inevitable when perceiving the external world, because our perception is not a faithful replica of external reality. A more critical question pertains to the accuracy of our perception in representing the 3D coordinates of a stack’s blocks. To address this question, we designed a straightforward experiment (Author response image 5a), where participants were instructed to determine whether a pair of stacks were identical. The position of each block was randomly changed horizontally. We found that all participants were able to accurately identify even minor positional variations in the 3D structure of the stacks (Author response image 5b). This level of perceptual precision is adequate for locating the difference between predictions from mental simulations and actual observations of the external world.

(6）Finally, the argument that the MGS is more efficient than the NGS model is based on an incorrect analysis of the results of the simulation. It is true that 80% accuracy is reached faster by the MGS model than the 95% accuracy level is reached by the NGS model. But the question is: how fast does the NGS model reach 80% accuracy (before reaching the plateau)?

R6: Yes. The NGS model achieved 80% accuracy as rapidly as the MGS model. However, the NGS model required a significantly longer period to reach the plateau crucial for decision-making. In revision, this information is now included.

Line 348-350: “…, while the initial growth rates of both models were comparable, the MGS reached the plateau crucial for decision-making sooner than the NGS.”

We greatly appreciate the thorough and insightful review provided by all three reviewers, which has considerably improved our manuscript, especially in terms of clarity in the presentation of the approach and further validation of the robustness implications of our results.

Reference: Allen KR, Smith KA, Tenenbaum JB. 2020. Rapid trial-and-error learning with simulation supports flexible tool use and physical reasoning. Proceedings of the National Academy of Sciences 117:29302–29310.

Battaglia PW, Hamrick JB, Tenenbaum JB. 2013. Simulation as an engine of physical scene understanding. Proceedings of the National Academy of Sciences 110:18327–18332.

Friston K, Moran RJ, Nagai Y, Taniguchi T, Gomi H, Tenenbaum J. 2021. World model learning and inference. Neural Networks 144:573–590.

Kriegeskorte N, Douglas PK. 2019. Interpreting encoding and decoding models. Current opinion in neurobiology 55:167–179.

MacKay DM. 1956. The epistemological problem for automataAutomata Studies.(AM-34), Volume 34. Princeton University Press. pp. 235–252.

Matsuo Y, LeCun Y, Sahani M, Precup D, Silver D, Sugiyama M, Uchibe E, Morimoto J. 2022. Deep learning, reinforcement learning, and world models. Neural Networks.

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Zhou L, Smith K, Tenenbaum J, Gerstenberg T. 2022. Mental Jenga: A counterfactual simulation model of physical support.

Author response:

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

eLife assessment:

This study presents an important finding on the implicit and automatic emotion perception from biological motion (BM). The evidence supporting the claims of the authors is solid, although inclusion of a larger number of samples and more evidence for the discrepancy between Intact and local emotional BMs would have strengthened the study. The work will be of broad interest to perceptual and cognitive neuroscience.

We express our sincere gratitude for the positive and constructive evaluation of our manuscript. We have now included more participants and conducted a replication experiment to strengthen our results.

Reviewer #1 (Public Review):

Summary:

Tian et al. investigated the effects of emotional signals in biological motion on pupil responses. In this study, subjects were presented with point-light biological motion stimuli with happy, neutral, and sad emotions. Their pupil responses were recorded with an eye tracker. Throughout the study, emotion type (i.e., happy/sad/neutral) and BM stimulus type (intact/inverted/non-BM/local) were systematically manipulated. For intact BM stimuli, happy BM induced a larger pupil diameter than neutral BM, and neutral BM also induced a larger pupil diameter than sad BM. Importantly, the diameter difference between happy and sad BM correlated with the autistic trait of individuals. These effects disappeared for the inverted BM and non-BM stimuli. Interestingly, both happy and sad emotions show superiority in pupil diameter.

Strengths:

(1) The experimental conditions and results are very easy to understand.

(2) The writing and data presentation are clear.

(3) The methods are sound. I have no problems with the experimental design and results.

Weaknesses:

(1) My main concern is the interpretation of the intact and local condition results. The processing advantage of happy emotion is not surprising given a number of existing studies. However, the only difference here seems to be the smaller (or larger) pupil diameter for sad compared to neutral in the intact (or local, respectively) condition. The current form only reports this effect but lacks in-depth discussions and explanations as to why this is the case.

Thanks for pointing this out, our apology for not making this point clear. It has long been documented that pupil size reflects the degree of cognitive effort and attention input (Joshi & Gold, 2019; van der Wel & van Steenbergen, 2018), and indexes the noradrenalin activity in emotion processing structures like amygdala (Dal Monte et al., 2015; Harrison et al., 2006; Liddell et al., 2005). Accordingly, we proposed that the smaller pupil response observed under the sad condition as compared to the neutral condition is because the sad biological motion (BM) could be less efficient in attracting visual attention and evoking emotional arousal. In line with this, it has been found that infants looked more at the neutral point-light walker when displayed in pair with the sad walker (Ogren et al., 2019), suggesting that the sad BM is less effective in capturing visual attention than the neutral BM. Besides, neural studies have revealed that, compared with other emotions (anger, happiness, disgust, and fear), the processing of sad emotion failed to evoke heightened activities in any emotionally relevant brain regions including the amygdala, the extrastriate body area (EBA) and the fusiform body area (FBA) (Peelen et al., 2007)(Peelen et al., 2007). The current study echoed with these previous findings by demonstrating a disadvantage for intact sad BM in evoking pupil responses. Notably, different from the intact sad BM, the local sad BM would instead induce stronger pupil responses than the neutral local BM. This distinctive pupil modulation effect observed in intact and local sad BM could be explained as a multi-level emotion processing model of BM. Specifically, even though both the intact and local BM conveyed important life information (Chang & Troje, 2008, 2009; Simion et al., 2008), the latter is deprived of the global form feature. Hence, the processing of emotions in local BM may occur at a more basic and preliminary level, responding to the general affective salient emotion information (happy and sad) without detailed analysis. In fact, similar dissociated emotion processing phenomenon has been observed in another important type of emotional signal with analogous function (i.e., facial expression). For example, happy and fearful faces elicited differential amygdala activations when perceived consciously. However, they elicited comparable amygdala activations when suppressed (Williams et al., 2004). Moreover, it has been proposed that there exist two parallel routes for facial expression processing: a quick but coarse subcortical route that detects affective salient information without detailed analysis, and a fine-grained but slow cortical route that discriminates the exact emotion type. Similarly, the dissociated emotion processing in local and intact BM may function in the same manner, with the former serving as a primary emotion detection mechanism and the latter serving as a detailed emotion discrimination mechanism. Still, future studies adopting more diverse experimental paradigms and neuroimaging techniques were needed to further investigate this issue. We have added these points and more thoroughly discussed the potential mechanism in the revised text (see lines 329-339, 405-415, 418-420).

References:

Chang, D. H. F., & Troje, N. F. (2008). Perception of animacy and direction from local biological motion signals. Journal of Vision, 8(5), 3. https://doi.org/10.1167/8.5.3

Chang, D. H. F., & Troje, N. F. (2009). Characterizing global and local mechanisms in biological motion perception. Journal of Vision, 9(5), 8–8. https://doi.org/10.1167/9.5.8

Dal Monte, O., Costa, V. D., Noble, P. L., Murray, E. A., & Averbeck, B. B. (2015). Amygdala lesions in rhesus macaques decrease attention to threat. Nature Communications, 6(1). https://doi.org/10.1038/ncomms10161

Harrison, N. A., Singer, T., Rotshtein, P., Dolan, R. J., & Critchley, H. D. (2006). Pupillary contagion: central mechanisms engaged in sadness processing. Social Cognitive and Affective Neuroscience, 1(1), 5–17. https://doi.org/10.1093/scan/nsl006

Joshi, S., & Gold, J. I. (2019). Pupil size as a window on neural substrates of cognition. Trends in Cognitive Sciences, 24(6), 466–480. https://doi.org/10.31234/osf.io/dvsme

Liddell, B. J., Brown, K. J., Kemp, A. H., Barton, M. J., Das, P., Peduto, A., Gordon, E., & Williams, L. M. (2005). A direct brainstem–amygdala–cortical ‘alarm’ system for subliminal signals of fear. NeuroImage, 24(1), 235–243.

Ogren, M., Kaplan, B., Peng, Y., Johnson, K. L., & Johnson, S. P. (2019). Motion or emotion: infants discriminate emotional biological motion based on low-level visual information. Infant Behavior and Development, 57, 101324. https://doi.org/10.1016/j.infbeh.2019.04.006

Peelen, M. V., Atkinson, A. P., Andersson, F., & Vuilleumier, P. (2007). Emotional modulation of body-selective visual areas. Social Cognitive and Affective Neuroscience, 2(4), 274–283. https://doi.org/10.1093/scan/nsm023

Simion, F., Regolin, L., & Bulf, H. (2008). A predisposition for biological motion in the newborn baby. Proceedings of the National Academy of Sciences, 105(2), 809–813. https://doi.org/10.1073/pnas.0707021105

van der Wel, P., & van Steenbergen, H. (2018). Pupil dilation as an index of effort in cognitive control tasks: a review. Psychonomic Bulletin & Review, 25(6), 2005–2015. https://doi.org/10.3758/s13423-018-1432-y

Williams, M. A., Morris, A. P., McGlone, F., Abbott, D. F., & Mattingley, J. B. (2004). Amygdala responses to fearful and happy facial expressions under conditions of binocular suppression. Journal of Neuroscience, 24(12), 2898-2904.

(2) I also found no systematic discussion and theoretical contributions regarding the correlation with the autistic traits. If the main point of this paper is to highlight an implicit and objective behavioral marker of the autistic trait, more interpretation and discussion of the links between the results and existing findings in ASD are needed.

We thank the reviewer for this insightful suggestion. The perception of biological motion (BM) has long been considered an important hallmark of social cognition. Abundant studies reported that individuals with social cognitive deficits (e.g., ASD) were impaired in BM perception (Blake et al., 2003; Freitag et al., 2008; Klin et al., 2009; Nackaerts et al., 2012). More recently, it has been pointed out that the extraction of more complex social information (e.g., emotions, intentions) from BM, as compared to basic BM recognitions, could be more effective in detecting ASDs (Federici et al., 2020; Koldewyn et al., 2009; Parron et al., 2008; Todorova et al., 2019). Specifically, a meta-analysis found that the effect size expanded nearly twice when the task required emotion recognition as compared to simple perception/detection (Todorova et al., 2019). However, for the high-functioning ASD individuals, it has been reported that they showed comparable performance with the control group in explicitly labelling BM emotions, while their responses were rather delayed (Mazzoni et al., 2021). This suggested that ASD individuals could adopt compensatory strategies to complete the explicit BM labelling task, while their automatic behavioural responses remained impaired. This highlights the importance of using more objective measures that do not rely on active reports to investigate the intrinsic perception of emotions from BM and its relationship with ASD-related social deficits. The current study thus introduced the pupil size measurement to this field, and we combined it with the passive viewing task to investigate the more automatic aspect of BM emotion processing. More importantly, in addition to diagnostic ASDs, the non-clinical general population also manifested autistic tendencies that followed normal distribution and demonstrated substantial heritability (Hoekstra et al., 2007). Here, we focused on the autistic tendencies in the general population, and our results showed that pupil modulations by BM emotions were indicative of individual autistic traits. Specifically, passively viewing the happy BMs evoked larger pupil responses than the sad BMs, while such emotional modulation diminished with the increase of autistic tendencies. More detailed test-retest examination further illustrated such a correlation was driven by the general diminishment in pupil modulation effects by emotional BM (happy or sad) for individuals with high autistic tendencies. This finding demonstrated that the automatic emotion processing of BM stimuli was impaired in individuals with high autistic tendencies, lending support to previous studies (Hubert et al., 2006; Nackaerts et al., 2012; Parron et al., 2008). This indicated the utility of emotional BM stimuli and pupil measurement in identifying ASD-related tendencies in both clinical and non-clinical populations. We have added these points to the revised text (see lines 347-375).

References:

Blake, R., Turner, L. M., Smoski, M. J., Pozdol, S. L., & Stone, W. L. (2003). Visual recognition of biological motion is impaired in children with autism. Psychological Science, 14(2), 151–157. https://doi.org/10.1111/1467-9280.01434

Federici, A., Parma, V., Vicovaro, M., Radassao, L., Casartelli, L., & Ronconi, L. (2020). Anomalous perception of biological motion in autism: a conceptual review and meta-analysis. Scientific Reports, 10(1). https://doi.org/10.1038/s41598-020-61252-3

Freitag, C. M., Konrad, C., Häberlen, M., Kleser, C., von Gontard, A., Reith, W., Troje, N. F., & Krick, C. (2008). Perception of biological motion in autism spectrum disorders. Neuropsychologia, 46(5), 1480–1494. https://doi.org/10.1016/j.neuropsychologia.2007.12.025

Hoekstra, R. A., Bartels, M., Verweij, C. J. H., & Boomsma, D. I. (2007). Heritability of autistic traits in the general population. Archives of Pediatrics & Adolescent Medicine, 161(4), 372. https://doi.org/10.1001/archpedi.161.4.372

Hubert, B., Wicker, B., Moore, D. G., Monfardini, E., Duverger, H., Fonséca, D. D., & Deruelle, C. (2006). Brief report: recognition of emotional and non-emotional biological motion in individuals with autistic spectrum disorders. Journal of Autism and Developmental Disorders, 37(7), 1386–1392. https://doi.org/10.1007/s10803-006-0275-y

Klin, A., Lin, D. J., Gorrindo, P., Ramsay, G., & Jones, W. (2009). Two-year-olds with autism orient to non-social contingencies rather than biological motion. Nature, 459(7244), 257–261. https://doi.org/10.1038/nature07868

Koldewyn, K., Whitney, D., & Rivera, S. M. (2009). The psychophysics of visual motion and global form processing in autism. Brain, 133(2), 599–610. https://doi.org/10.1093/brain/awp272

Mazzoni, N., Ricciardelli, P., Actis-Grosso, R., & Venuti, P. (2021). Difficulties in recognising dynamic but not static emotional body movements in autism spectrum disorder. Journal of Autism and Developmental Disorders, 52(3), 1092–1105. https://doi.org/10.1007/s10803-021-05015-7

Nackaerts, E., Wagemans, J., Helsen, W., Swinnen, S. P., Wenderoth, N., & Alaerts, K. (2012). Recognizing biological motion and emotions from point-light displays in autism spectrum disorders. PLoS ONE, 7(9), e44473. https://doi.org/10.1371/journal.pone.0044473

Parron, C., Da Fonseca, D., Santos, A., Moore, D. G., Monfardini, E., & Deruelle, C. (2008). Recognition of biological motion in children with autistic spectrum disorders. Autism, 12(3), 261–274. https://doi.org/10.1177/1362361307089520

Todorova, G. K., Hatton, R. E. M., & Pollick, F. E. (2019). Biological motion perception in autism spectrum disorder: a meta-analysis. Molecular Autism, 10(1). https://doi.org/10.1186/s13229-019-0299-8

Reviewer #2 (Public Review):

Summary:

Through a series of four experiments, Yuan, Wang and Jiang examined pupil size responses to emotion signals in point-light motion stimuli. Experiment 1 examined upright happy, sad and neutral point-light biological motion (BM) walkers. The happy BM induced a significantly larger pupil response than the neutral, whereas the sad BM evoked a significantly smaller pupil size than the neutral BM. Experiment 2 examined inverted BM walkers. Experiment 3 examined BM stimuli with acceleration removed. No significant effects of emotion were found in neither Experiment 2 nor Experiment 3. Experiment 4 examined scrambled BM stimuli, in which local motion features were preserved while the global configuration was disrupted. Interestingly, the scrambled happy and sad BM led to significantly greater pupil size than the scrambled neutral BM at a relatively early time, while no significant difference between the scrambled happy and sad BM was found. Thus, the authors argue that these results suggest multi-level processing of emotions in life motion signals.

Strengths:

The experiments were carefully designed and well-executed, with point-light stimuli that eliminate many potential confounding effects of low-level visual features such as luminance, contrast, and spatial frequency.

Weaknesses:

Correlation results with limited sample size should be interpreted with extra caution.

Thanks for pointing this out. To strengthen the correlation results, we have conducted a replication experiment (Exp.1b) and added a test-retest examination to further assess the reliability of our measurements. Specifically, a new group of 24 participants (16 females, 8 males) were recruited to perform the identical experiment procedure as in Experiment 1. Then, after at least seven days, they were asked to return to the lab for a retest. The results successfully replicated the previously reported main effect of emotional condition in both the first test (F(2, 46) = 12.0, p < .001, ηp2 = 0.34, Author response image 1A) and the second test (F(2, 46) = 14.8, p < .001, ηp2 = 0.39, Author response image 1B). The happy BM induced a significantly larger pupil response than the neutral BM (First Test: t(23) = 2.60, p = .022, Cohen’s d = 0.53, 95% CI for the mean difference = [0.02, 0.14], Holm-corrected, p = .048 after Bonferroni correction, Author response image 1A; Second Test: t(23) = 3.36, p = .005, Cohen’s d = 0.68, 95% CI for the mean difference = [0.06, 0.24], Holm-corrected, p = .008 after Bonferroni correction, Author response image 1B). On the contrary, the sad BM induced a significantly smaller pupil response than the neutral BM (First Test: t(23) = -2.77, p = .022, Cohen’s d = 0.57, 95% CI for the mean difference = [-0.19, -0.03], Holm-corrected, p = .033 after Bonferroni correction; Second Test: t(23) = -3.19, p = .005, Cohen’s d = 0.65, 95% CI for the mean difference = [-0.24, -0.05], Holm-corrected, p = .012 after Bonferroni correction, Author response image 1B). Besides, the happy BM induced significantly larger pupil response than the sad BM (first test: t(23) = 4.23, p < .001, Cohen’s d = 0.86, 95% CI for the mean difference = [0.10, 0.28], Holm-corrected, p < .001 after Bonferroni correction, Author response image 1A; second test: t(23) = 4.26, p < .001, Cohen’s d = 0.87, 95% CI for the mean difference = [0.15, 0.44], Holm-corrected, p < .001 after Bonferroni correction, Author response image 1B). The results of the cluster-based permutation analysis were also similar (see Supplementary Material for more details).

Author response image 1.

Normalized mean pupil responses in the replication experiment (Experiment 1b) of Experiment 1a and its retest, using the neutral condition as baseline, plotted against happy and sad conditions. (A) In the first test, the group average pupil response to happy intact BM is significantly larger than that to sad and neutral BM, while the pupil response induced by sad BM is significantly smaller than that evoked by neutral BM, replicating the results of Experiment 1a. (B) Moreover, such results were similarly found in the second test.

Notably, we successfully replicated the negative correlation between the happy over sad dilation effect and individual autistic traits in the first test (r(23) = -0.46, p = .023, 95% CI for the mean difference = [-0.73, -0.07], Author response image 2A). No other significant correlations were found (see Author response image 2B-C). Moreover, in the second test, such a correlation was similarly found and was even stronger (r(23) = -0.61, p = .002, 95% CI for the mean difference = [-0.81, -0.27], Author response image 2D). We‘ve also performed a test-retest reliability analysis on the happy over sad pupil dilation effect and the AQ score. The results showed robust correlations. See Author response table 1 for more details.

Author response table 1.

Reliability of pupil size and AQ indices.

Importantly, in the second test, we’ve also observed a significant negative correlation between AQ and the happy minus neutral pupil dilation effect (r(23) = -0.44, p = .032, 95% CI for the mean difference = [-0.72, -0.04], Author response image 2E), and a significant positive correlation between the sad minus neutral pupil size and AQ (r(23) = 0.50, p = .014, 95% CI for the mean difference = [0.12, 0.75], Author response image 2F). This indicated that the overall correlation between happy over sad dilation effect and AQ was driven both by the diminished happy dilation effect as well as the sad constriction effect. Overall, our replication experiment consistently found a significant negative correlation between AQ and happy over sad dilation effect both in the test and the retest. Moreover, it revealed that such an effect was contributed by both a negative correlation between AQ and happy-neutral pupil response and a positive correlation between AQ and sad-neutral pupil response, demonstrating a general impairment in BM emotion perception (happy or sad) for individuals with high autistic tendencies. This also indicated the utility of adopting a test-retest pupil examination to more precisely detect individual autistic tendencies. We have added these points in the revised text (see lines 135-173, lines 178-180).

Author response image 2.

Correlation results for pupil modulation effects and AQ scores in the replication experiment (Experiment 1b) of Experiment 1a and its retest. (A) We replicated the negative correlation between the happy over sad pupil dilation effect and AQ in the first test. (B-C) No other significant correlations were found. (D) In the second test, the negative correlation between the happy over sad pupil dilation effect and AQ was similarly observed and even stronger. (E-F) Moreover, the happy vs. neutral pupil dilation effect and the sad vs. neutral pupil constriction effect respectively correlate with AQ in the second test.

It would be helpful to add discussions as a context to compare the current results with pupil size reactions to emotion signals in picture stimuli.

Thanks for this this thoughtful comment. The modulation of emotional information on pupil responses has been mostly investigated using picture stimuli. Bradley et al. (2008) first demonstrated that humans showed larger pupil responses towards emotional images as compared to neutral images, while no difference was observed between the positive and negative images. This was regarded as the result of increased sympathetic activity induced by emotional arousal that is independent of the emotional valence. Similar results have been replicated with different presentation durations, repetition settings, and tasks (Bradley & Lang, 2015; Snowden et al., 2016). However, the emotional stimuli adopted in these studies were mostly complicated scene images that conveyed rather general emotional information. When it comes to the specific emotion cues (e.g., fear, anger, happy, sad) delivered by our conspecifics through biologically salient signals (e.g., faces, gestures, voices), the results became intermixed. Some studies demonstrated that fearful, disgusted, and angry static faces induced larger pupil sizes than the neutral face, while sad and happy faces failed to induce such pupil dilatory effects (Burley et al., 2017). In contrast, other studies observed larger pupil responses for happy faces as compared to sad and fearful faces (Aktar et al., 2018; Burley & Daughters, 2020; Jessen et al., 2016). These conflicting results could be due to the low-level confounds of emotional faces (e.g., eye size) (Carsten et al., 2019; Harrison et al., 2006). Similar to faces, BM also conveyed salient clues concerning the emotional states of our interactive partners. However, they were highly simplified, deprived of various irrelevant visual confounders (e.g., body shape). Here, we reported that the happy BM induced a stronger pupil response than the neutral and sad BM, lending support to the happy dilation effect observed with faces (Burley & Daughters, 2020; Prunty et al., 2021). Moreover, it helps ameliorate the concern regarding the low-level confounding factors by identifying similar pupil modulations in another type of social signal with distinctive perceptual features. We have added these points to the revised text (see lines 301-321).

References:

Aktar, E., Mandell, D. J., de Vente, W., Majdandžić, M., Oort, F. J., van Renswoude, D. R., Raijmakers, M. E. J., & Bögels, S. M. (2018). Parental negative emotions are related to behavioral and pupillary correlates of infants’ attention to facial expressions of emotion. Infant Behavior and Development, 53, 101–111. https://doi.org/10.1016/j.infbeh.2018.07.004

Bradley, M. M., & Lang, P. J. (2015). Memory, emotion, and pupil diameter: repetition of natural scenes. Psychophysiology, 52(9), 1186–1193. https://doi.org/10.1111/psyp.12442

Bradley, M. M., Miccoli, L., Escrig, M. A., & Lang, P. J. (2008). The pupil as a measure of emotional arousal and autonomic activation. Psychophysiology, 45(4), 602–607. https://doi.org/10.1111/j.1469-8986.2008.00654.x

Burley, D. T., & Daughters, K. (2020). The effect of oxytocin on pupil response to naturalistic dynamic facial expressions. Hormones and Behavior, 125, 104837. https://doi.org/10.1016/j.yhbeh.2020.104837

Burley, D. T., Gray, N. S., & Snowden, R. J. (2017). As far as the eye can see: relationship between psychopathic traits and pupil response to affective stimuli. PLOS ONE, 12(1), e0167436. https://doi.org/10.1371/journal.pone.0167436

Carsten, T., Desmet, C., Krebs, R. M., & Brass, M. (2019). Pupillary contagion is independent of the emotional expression of the face. Emotion, 19(8), 1343–1352. https://doi.org/10.1037/emo0000503

Harrison, N. A., Singer, T., Rotshtein, P., Dolan, R. J., & Critchley, H. D. (2006). Pupillary contagion: central mechanisms engaged in sadness processing. Social Cognitive and Affective Neuroscience, 1(1), 5–17. https://doi.org/10.1093/scan/nsl006

Jessen, S., Altvater-Mackensen, N., & Grossmann, T. (2016). Pupillary responses reveal infants’ discrimination of facial emotions independent of conscious perception. Cognition, 150, 163–169. https://doi.org/10.1016/j.cognition.2016.02.010

Prunty, J. E., Keemink, J. R., & Kelly, D. J. (2021). Infants show pupil dilatory responses to happy and angry facial expressions. Developmental Science, 25(2). https://doi.org/10.11<br /> 11/desc.13182

Snowden, R. J., O’Farrell, K. R., Burley, D., Erichsen, J. T., Newton, N. V., & Gray, N. S. (2016). The pupil’s response to affective pictures: role of image duration, habituation, and viewing mode. Psychophysiology, 53(8), 1217–1223. https://doi.org/10.1111/psyp.12668

Overall, I think this is a well-written paper with solid experimental results that support the claim of the authors, i.e., the human visual system may process emotional information in biological motion at multiple levels. Given the key role of emotion processing in normal social cognition, the results will be of interest not only to basic scientists who study visual perception, but also to clinical researchers who work with patients of social cognitive disorders. In addition, this paper suggests that examining pupil size responses could be a very useful methodological tool to study brain mechanisms underlying emotion processing.

Reviewer #3 (Public Review):

Summary:

The overarching goal of the authors was to understand whether emotional information conveyed through point-light biological motion can trigger automatic physiological responses, as reflected in pupil size.

Strengths:

This manuscript has several noticeable strengths: it addresses an intriguing research question that fills that gap in existing literature, presents a clear and accurate presentation of the current literature, and conducts a series of experiments and control experiments with adequate sample size. Yet, it also entails several noticeable limitations - especially in the study design and statistical analyses.

Weaknesses:

(1) Study design:

(1.1) Dependent variable:

Emotional attention is known to modulate both microsaccades and pupil size. Given the existing pupillometry data that the authors have collected, it would be both possible and valuable to determine whether the rate of microsaccades is also influenced by emotional biological motion.

We thank the reviewer for this advice. Microsaccades functioned as a mechanism to maintain visibility by continuously shifting the retinal image to overcome visual adaptation (Martinez-Conde et al., 2006). Moreover, it was found to be sensitive to attention processes (Baumeler et al., 2020; Engbert & Kliegl, 2003b; Meyberg et al., 2017), and could reflect the activity of superior colliculus (SC) and other related brain areas (Martinez-Conde et al., 2009, 2013). Previous studies have found that, compared with neutral and pleasant images, unpleasant images significantly inhibit early microsaccade rates (Kashihara, 2020; Kashihara et al., 2013). This is regarded as the result of retaining previous crucial information at the sacrifice of updating new visual input. We agree with the reviewer that it would be valuable to investigate whether emotional information conveyed by BM could modulate microsaccades. However, it should be noted that our data collection and experimental design are not optimized for this purpose. This is because we have only recorded the left eye’s data, while abundant methodological studies have doubted the reliability of using only one eye’s data to analyze microsaccades (Fang et al., 2018; Hauperich et al., 2020; Nyström et al., 2017) and suggested that the microsaccades should be defined by spontaneous binocular eye movement (Engbert & Kliegl, 2003a, 2003b). Besides, according to Kashihara et al. (2013), participants showed differential microsaccade rates after the stimuli disappeared so as to maintain the previously observed different emotional information. However, in the current study, we discarded the data after the stimuli disappeared, making it impossible to analyze the microsaccade data after the stimuli disappeared. Despite these disadvantages, we have attempted to analyze the microsaccade rate during the stimuli presentation using only the left eye’s data. Specifically, we applied the algorithm developed by Otero-Millan et al. (2014) (minimum duration =6 ms, maximum amplitude = 1.5 degrees, maximum velocity = 150 degrees/sec) to the left eye’s data from 100 ms before to 4000 ms after stimulus onset. Subsequently, we calculated the microsaccade rates using a moving window of 100 ms (stepped in 1 ms) (Engbert & Kliegl, 2003b; Kashihara et al., 2013). The microsaccade rate displayed a typical curve, with suppression shortly after stimulus appearance (inhibition phase), followed by an increased rate of microsaccade occurrence (rebound phase). The cluster-based permutation analysis was then applied to explore the modulation of BM emotions on microsaccade rates. However, no significant differences among different emotional conditions (happy, sad, neutral) were found for the four experiments.

Author response image 3.

Time-series change in the microsaccade rates to happy, sad, and neutral BM in Experiments 1-4. Solid lines represent microsaccade rates under each emotional condition as a function of time (happy: red; sad: blue; neutral: gray); shaded areas represent the SEM between participants. No significant differences were found after cluster-based permutation correction for the four experiments.

It is important to note that the microsaccade rate analysis was conducted on only the left eye’s data and that the experiment design is not optimized for this analysis, thus, extra caution should be exercised in interpreting the results. Still, we found it very innovative and important to combine the microsaccade index with the pupil size to holistically investigate the processing of emotional information in BM, and future studies are highly needed to adopt more suitable recording techniques and experiment designs to further probe this issue. We have discussed this issue in the revised text (see lines 339-344).

References:

Baumeler, D., Schönhammer, J. G., & Born, S. (2020). Microsaccade dynamics in the attentional repulsion effect. Vision Research, 170, 46–52. https://doi.org/10.1016/j.visres.2020.03.009

Engbert, R., & Kliegl, R. (2003a). Binocular coordination in microsaccades. In The Mind’s Eye (pp. 103–117). Elsevier. https://doi.org/10.1016/b978-044451020-4/50007-4

Engbert, R., & Kliegl, R. (2003b). Microsaccades uncover the orientation of covert attention. Vision Research, 43(9), 1035–1045. https://doi.org/10.1016/s0042-6989(03)00084-1

Fang, Y., Gill, C., Poletti, M., & Rucci, M. (2018). Monocular microsaccades: do they really occur? Journal of Vision, 18(3), 18. https://doi.org/10.1167/18.3.18

Hauperich, A.-K., Young, L. K., & Smithson, H. E. (2020). What makes a microsaccade? a review of 70 years research prompts a new detection method. Journal of Eye Movement Research, 12(6). https://doi.org/10.16910/jemr.12.6.13

Kashihara, K. (2020). Microsaccadic modulation evoked by emotional events. Journal of Physiological Anthropology, 39(1). https://doi.org/10.1186/s40101-020-00238-6

Kashihara, K., Okanoya, K., & Kawai, N. (2013). Emotional attention modulates microsaccadic rate and direction. Psychological Research, 78(2), 166–179. https://doi.org/10.1007/s00426-013-0490-z

Martinez-Conde, S., Macknik, S. L., Troncoso, X. G., & Dyar, T. A. (2006). Microsaccades counteract visual fading during fixation. Neuron, 49(2), 297–305. https://doi.org/10.1016/j.neuron.2005.11.033

Martinez-Conde, S., Macknik, S. L., Troncoso, X. G., & Hubel, D. H. (2009). Microsaccades: a neurophysiological analysis. Trends in Neurosciences, 32(9), 463–475. https://doi.org/10.1016/j.tins.2009.05.006

Martinez-Conde, S., Otero-Millan, J., & Macknik, S. L. (2013). The impact of microsaccades on vision: towards a unified theory of saccadic function. Nature Reviews Neuroscience, 14(2), 83–96. https://doi.org/10.1038/nrn3405

Meyberg, S., Sinn, P., Engbert, R., & Sommer, W. (2017). Revising the link between microsaccades and the spatial cueing of voluntary attention. Vision Research, 133, 47–60. https://doi.org/10.1016/j.visres.2017.01.001

Nyström, M., Andersson, R., Niehorster, D. C., & Hooge, I. (2017). Searching for monocular microsaccades – a red hering of modern eye trackers? Vision Research, 140, 44–54. https://doi.org/10.1016/j.visres.2017.07.012

Otero-Millan, J., Castro, J. L. A., Macknik, S. L., & Martinez-Conde, S. (2014). Unsupervised clustering method to detect microsaccades. Journal of Vision, 14(2), 18–18. https://doi.org/10.1167/14.2.18

(1.2) Stimuli:

It appears that the speed of the emotional biological motion stimuli mimics the natural pace of the emotional walker. What is the average velocity of the biological motion stimuli for each condition?

Thanks for pointing out this issue. The neutral and emotional (sad or happy) BM stimuli are equal in walking speed (one step for one second, 1Hz). We have also computed their physical velocity by calculating the Euclidean distance in pixel space of each key point between adjacent frames (Poyo Solanas et al., 2020). The velocity was 5.76 pixels/frame for the happy BM, 4.14 pixels/frame for the neutral BM, and 3.21 pixels/frame for the sad BM. This difference in velocity profile was considered an important signature for conveying emotional information, as the happy walker was characterized by a larger step pace and longer arm swing and the sad walker would instead exhibit a slouching gait with short slow strides and smaller arm movement (Barliya et al., 2012; Chouchourelou et al., 2006; Halovic & Kroos, 2018; Roether et al., 2009). More importantly, our current results could not be explained by the differences in velocities. This is because the inverted emotional BM with identical velocity characteristics failed to induce any modulations on pupil responses. Furthermore, the local sad and happy BM differed the most in velocity feature, while they induced similar modulations on pupil sizes. We have added these points in the revised text (see lines 254-257, 484-491).

References:

Barliya, A., Omlor, L., Giese, M. A., Berthoz, A., & Flash, T. (2012). Expression of emotion in the kinematics of locomotion. Experimental Brain Research, 225(2), 159–176. https://doi.org/10.1007/s00221-012-3357-4

Chouchourelou, A., Matsuka, T., Harber, K., & Shiffrar, M. (2006). The visual analysis of emotional actions. Social Neuroscience, 1(1), 63–74. https://doi.org/10.1080/17470910600630599

Halovic, S., & Kroos, C. (2018). Not all is noticed: kinematic cues of emotion-specific gait. Human Movement Science, 57, 478–488. https://doi.org/10.1016/j.humov.2017.11.008

Poyo Solanas, M., Vaessen, M. J., & de Gelder, B. (2020). The role of computational and subjective features in emotional body expressions. Scientific Reports, 10(1). https://doi.org/10.1038/s41598-020-63125-1

Roether, C. L., Omlor, L., Christensen, A., & Giese, M. A. (2009). Critical features for the perception of emotion from gait. Journal of Vision, 9(6), 15–15. https://doi.org/10.1167/9.6.15

When the authors used inverted biological motion stimuli, they didn't observe any modulation in pupil size. Could there be a difference in microsaccades when comparing inverted emotional biological motion stimuli?

Thanks for this consideration. Both microsaccades and pupil size can provide valuable insights into the underlying neural dynamics of attention and cognitive control (Baumeler et al., 2020; Engbert & Kliegl, 2003; Meyberg et al., 2017). Notably, previous studies have shown that the microsaccades and pupil sizes could be similar and highly correlated in reflecting various cognitive processes, such as multisensory integration, inhibitory control, and cognitive load (Krejtz et al., 2018; Wang et al., 2017; Wang & Munoz, 2021). Moreover, the generation of both microsaccades and pupil responses would involve shared neural circuits, including the midbrain structure superior colliculus (SC) and the noradrenergic system (Hafed et al., 2009; Hafed & Krauzlis, 2012; Wang et al., 2012). However, the pupil size could be more sensitive than microsaccade rates in contexts such as affective priming (Krejtz et al., 2020) and decision formation (Strauch et al., 2018). Moreover, abundant former studies have all shown that inversion would significantly disrupt the perception of emotions from BM (Atkinson et al., 2007; Dittrich et al., 1996; Spencer et al., 2016; Yuan et al., 2022, 2023). Overall, it is unlikely for the microsaccade rates to show significant differences when comparing inverted emotional biological motion stimuli. Besides, we have attempted to analyze the microsaccade rate in the inverted BM situation, while our results showed no significant differences (see also Point 1.1, Author response image 3). Still, it is needed for future studies to combine the microsaccade index and pupil size to provide a thorough understanding of BM emotion processing. We have discussed this issue in the revised text (see lines 339-344).

References:

Atkinson, A. P., Tunstall, M. L., & Dittrich, W. H. (2007). Evidence for distinct contributions of form and motion information to the recognition of emotions from body gestures. Cognition, 104(1), 59–72. https://doi.org/10.1016/j.cognition.2006.05.005

Baumeler, D., Schönhammer, J. G., & Born, S. (2020). Microsaccade dynamics in the attentional repulsion effect. Vision Research, 170, 46–52. https://doi.org/10.1016/j.visres.2020.03.009

Dittrich, W., Troscianko, T., Lea, S., & Morgan, D. (1996). Perception of emotion from dynamic point-light displays represented in dance. Perception, 25(6), 727–738. https://doi.org/10.1068/p250727

Engbert, R., & Kliegl, R. (2003). Microsaccades uncover the orientation of covert attention. Vision Research, 43(9), 1035–1045. https://doi.org/10.1016/s0042-6989(03)00084-1

Hafed, Z. M., Goffart, L., & Krauzlis, R. J. (2009). A neural mechanism for microsaccade generation in the primate superior colliculus. Science, 323(5916), 940–943. https://doi.org/10.1126/science.1166112

Hafed, Z. M., & Krauzlis, R. J. (2012). Similarity of superior colliculus involvement in microsaccade and saccade generation. Journal of neurophysiology, 107(7), 1904-1916.

Krejtz, K., Duchowski, A. T., Niedzielska, A., Biele, C., & Krejtz, I. (2018). Eye tracking cognitive load using pupil diameter and microsaccades with fixed gaze. Plos One, 13(9), e0203629. https://doi.org/10.1371/journal.pone.0203629

Krejtz, K., Żurawska, J., Duchowski, A., & Wichary, S. (2020). Pupillary and microsaccadic responses to cognitive effort and emotional arousal during complex decision making. Journal of Eye Movement Research, 13(5). https://doi.org/10.16910/jemr.13.5.2

Meyberg, S., Sinn, P., Engbert, R., & Sommer, W. (2017). Revising the link between microsaccades and the spatial cueing of voluntary attention. Vision Research, 133, 47–60. https://doi.org/10.1016/j.visres.2017.01.001

Spencer, J. M. Y., Sekuler, A. B., Bennett, P. J., Giese, M. A., & Pilz, K. S. (2016). Effects of aging on identifying emotions conveyed by point-light walkers. Psychology and Aging, 31(1), 126–138. https://doi.org/10.1037/a0040009

Strauch, C., Greiter, L., & Huckauf, A. (2018). Pupil dilation but not microsaccade rate robustly reveals decision formation. Scientific Reports, 8(1). https://doi.org/10.1038/s41598-018-31551-x

Wang, C.-A., Blohm, G., Huang, J., Boehnke, S. E., & Munoz, D. P. (2017). Multisensory integration in orienting behavior: pupil size, microsaccades, and saccades. Biological Psychology, 129, 36–44. https://doi.org/10.1016/j.biopsycho.2017.07.024

Wang, C.-A., Boehnke, S. E., White, B. J., & Munoz, D. P. (2012). Microstimulation of the monkey superior colliculus induces pupil dilation without evoking saccades. Journal of Neuroscience, 32(11), 3629–3636. https://doi.org/10.1523/jneurosci.5512-11.2012

Wang, C.-A., & Munoz, D. P. (2021). Differentiating global luminance, arousal and cognitive signals on pupil size and microsaccades. European Journal of Neuroscience, 54(10), 7560–7574. https://doi.org/10.1111/ejn.15508

Yuan, T., Ji, H., Wang, L., & Jiang, Y. (2022). Happy is stronger than sad: emotional information modulates social attention. Emotion. https://doi.org/10.1037/emo0001145

Yuan, T., Wang, L., & Jiang, Y. (2023). Cross-channel adaptation reveals shared emotion representation from face and biological motion. In Emotion (p. In Press).

(2) Statistical analyses

(2.1) Multiple comparisons:

There are many posthoc comparisons throughout the manuscript. The authors should consider correction for multiple comparisons. Take Experiment 1 for example, it is important to note that the happy over neutral BM effect and the sad over neutral BM effect are no longer significant after Bonferroni correction, which is worth noting.

Thanks for this suggestion. In our original analysis, we applied the Holm post-hoc corrections for multiple comparisons. The Holm correction is a step-down correction method and is more powerful but less conservative than the Bonferroni correction. We have now conducted the stricter Bonferroni post-hoc correction. In Experiment 1, the happy over neutral, and happy over sad BM effect is still significant after the Bonferroni post-hoc correction (happy vs. neutral: p = .036; happy vs. sad: p = .009), and the sad over neutral comparison remains marginally significant after the Bonferroni post-hoc correction (p = .071). Importantly, the test-retest replication experiment also yielded significant results for the comparisons between happy and neutral (First Test: p = .022, Holm-corrected, p = .048, Bonferroni-corrected; Second Test: p = .005,  Holm-corrected, p = .008, Bonferroni-corrected), sad and neutral (First Test: p = .022, Holm-corrected, p = .033, Bonferroni-corrected; Second Test: p = .005, Holm-corrected, p = .012, Bonferroni-corrected, Author response image 1B), and happy and sad BM  (First test: p < .001, Holm-corrected, p < .001, Bonferroni-corrected; Second test: p < .001, Holm-corrected, p < .001, Bonferroni-corrected). These results provided support for the replicability and consistency of the reported significant contrasts. See also Point 2.3.

In Experiment 4, the significance levels of all comparisons remained the same after Bonferroni post-hoc correction (happy vs. neutral: p = .011; sad vs. neutral: p = .007; happy vs. sad: p = 1.000). We have now added these results in the main text (See lines 119, 122, 124, 143, 145, 148, 150, 153, 155, 248, 251, 254).

(2.2) The authors present the correlation between happy over sad dilation effect and the autistic traits in Experiment 1, but do not report such correlations in Experiments 2-4. Did the authors collect the Autistic Quotient measure in Experiments 2-4? It would be informative if the authors could demonstrate the reproducibility (or lack thereof) of this happy-sad index in Experiments 2-4.

We apologize for not making it clear. We have collected the AQ scores in Experiments 2-4. However, it should be pointed out that the happy over sad pupil dilation effect was only observed in Experiment 1. Moreover, we’ve again identified such happy over sad pupil dilation effect in the replication experiment (Experiment 1b) as well as its correlation with AQ. Instead, no significant correlations between AQ and the happy-sad pupil index were found in Experiments 2-4, see Author response image 4 for more details. We have reported these correlations in the main text (see lines 157-173, 190-194, 212-216, 257-262).

Author response image 4.

Correlations between the happy over sad pupil dilation effect and AQ scores. (A)  The happy over sad pupil dilation effect correlated negatively with individual autistic scores. (B-C) Such correlation was similarly observed in the test and retest of the replication experiment. (D-F) No such correlations were found for the inverted, nonbiological, and local BM stimuli.

(2.3) The observed correlation between happy over sad dilation effect and the autistic traits in Experiment 1 seems rather weak. It could be attributed to the poor reliability of the Autistic Quotient measure or the author-constructed happy-sad index. Did the authors examine the test-retest reliability of their tasks or the Autistic Quotient measure?

Thanks for this suggestion. We have now conducted a test-retest replication study to further confirm the observed significant correlations. Specifically, we recruited a new group of 24 participants (16 females, 8 males) to perform the identical procedure as in Experiment 1, and they were asked to return to the lab for a retest after at least seven days. We’ve replicated the significant main effect of emotional conditions in both the first test (F(2, 46) = 12.0, p < .001, ηp2 = 0.34) and the second test (F(2, 46) = 14.8, p < .001, ηp2 = 0.39). Besides, we also replicated the happy minus neutral pupil dilation effect (First Test: t(23) = 2.60, p = .022, Cohen’s d = 0.53, 95% CI for the mean difference = [0.02, 0.14], Holm-corrected, p = .048 after Bonferroni correction; Second Test: t(23) = 3.36, p = .005, Cohen’s d = 0.68, 95% CI for the mean difference = [0.06, 0.24], Holm-corrected, p = .008 after Bonferroni correction), and the sad minus neutral pupil constriction effect (First Test: t(23) = -2.77, p = .022, Cohen’s d = 0.57, 95% CI for the mean difference = [-0.19, -0.03], Holm-corrected, p = .033 after Bonferroni correction; Second Test: t(23) = -3.19, p = .005, Cohen’s d = 0.65, 95% CI for the mean difference = [-0.24, -0.05], Holm-corrected, p = .012 after Bonferroni correction). Additionally, the happy BM still induced a significantly larger pupil response than the sad BM (first test: t(23) = 4.23, p < .001, Cohen’s d = 0.86, 95% CI for the mean difference = [0.10, 0.28], Holm-corrected, p < .001 after Bonferroni correction; second test: t(23) = 4.26, p < .001, Cohen’s d = 0.87, 95% CI for the mean difference = [0.15, 0.44], Holm-corrected, p < .001 after Bonferroni correction).

Notably, we’ve successfully replicated the negative correlation between the happy over sad dilation effect and individual autistic traits (r(23) = -0.46, p = .023, 95% CI for the mean difference = [-0.73, -0.07]). Such a correlation was similarly found and was even stronger in the retest (r(23) = -0.61, p = .002, 95% CI for the mean difference = [-0.81, -0.27]). A test-retest reliability analysis was conducted on the happy over sad pupil dilation effect and the AQ score. The results showed robust correlations (r(happy-sad pupil size)= 0.56; r(AQ)= 0.90) and strong test-retest reliabilities (α(happy-sad pupil size)= 0.60; α(AQ)= 0.82). We have added these results to the main text (see lines 135-173). See also Response to Reviewer #2 Response 1 for more details.

(2.4) Relatedly, the happy over sad dilation effect is essentially a subtraction index. Without separately presenting the pipul size correlation with happy and sad BM in supplemental figures, it becomes challenging to understand what's primarily driving the observed correlation.

Thanks for pointing this out. We have now presented the separate correlations between AQ and the pupil response towards happy and sad BM in Experiment 1 (see Author response image 5A), and the test-retest replication experiment of Experiment 1 (see Author response image 5B-C). No significant correlations were found. This is potentially because the raw pupil response is a mixed result of BM perception and emotion perception, while the variations in pupil sizes across emotional conditions could more faithfully reflect individual sensitivities to emotions in BM (Burley et al., 2017; Pomè et al., 2020; Turi et al., 2018).  

Author response image 5.

No significant correlations between AQ and pupil response towards happy and sad intact BM were found in Experiment 1a and the test-retest replication experiment (Experiment 1b).

To probe what's primarily driving the observed correlation between happy-sad pupil size and AQ, we instead used the neutral as the baseline and separately correlated AQ with the happy-neutral and the sad-neutral pupil modulation effects. No significant correlation was found in Experiment 1a (Author response image 6A-B) and the first test of the replication experiment (Experiment 1b) (Author response image 6C-D). Importantly, in the second test of the replication experiment, we found a significant negative correlation between AQ and the happy-neutral pupil size (r(23) = -0.44, p = .032, 95% CI for the mean difference = [-0.72, -0.04], Author response image 6E), and a significant positive correlation between AQ and the sad-neutral pupil size (r(23) = 0.50, p = .014, 95% CI for the mean difference = [0.12, 0.75], Author response image 6F). This suggested that the overall correlation between AQ and the happy over sad dilation effect was driven by diminished pupil modulations towards both the happy and sad BM for high AQ individuals, demonstrating a general deficiency in BM emotion perception (happy or sad) among individuals with high autistic tendencies. It further revealed the potential of adopting a test-retest pupil examination to more precisely detect individual autistic tendencies. We have reported these results in the main text (see lines 166-173).

Author response image 6.

Correlation results for pupil modulations and AQ scores. (A-B) In Experiment 1a, no significant correlation was observed between AQ and the happy pupil modulation effect, as well as between AQ and the sad pupil modulation effect. (C-D) Similarly, no significant correlations were found in the first test of the replication experiment (Experiment 1b). (E-F) Importantly, in the second test of Experiment 1b, the happy vs. neutral pupil dilation effect was positively correlated with AQ, and the sad vs. neutral pupil constriction effect was positively correlated with AQ.

References:

Burley, D. T., Gray, N. S., & Snowden, R. J. (2017). As Far as the Eye Can See: Relationship between Psychopathic Traits and Pupil Response to Affective Stimuli. PLOS ONE, 12(1), e0167436. https://doi.org/10.1371/journal.pone.0167436

Pomè, A., Binda, P., Cicchini, G. M., & Burr, D. C. (2020). Pupillometry correlates of visual priming, and their dependency on autistic traits. Journal of vision, 20(3), 3-3.

Turi, M., Burr, D. C., & Binda, P. (2018). Pupillometry reveals perceptual differences that are tightly linked to autistic traits in typical adults. eLife, 7. https://doi.org/10.7554/elife.32399

(2.5) For the sake of transparency, it is important to report all findings, not just the positive results, throughout the paper.

Thanks for this suggestion. We have now reported all the correlations results between AQ and pupil modulation effects (happy-sad, happy-neutral, sad-neutral) in the main text (see lines 130-131, 157-162, 166-170, 190-194, 212-216, 257-262). Given that no significant correlations were observed between AQ and the raw pupil responses across four experiments, we reported their correlations with AQ in the supplementary material. We have stated this point in the main text (see lines 132-134).

(3) Structure

(3.1) The Results section immediately proceeds to the one-way repeated measures ANOVA. This section could be more reader-friendly by including a brief overview of the task procedures and variables, e.g., shifting Fig. 3 to this section.

Thanks for this advice. We have now added a brief overview of the task procedures and variables and we have also shifted the figure position (see lines 101-103).

Reviewer #1 (Recommendations For The Authors):

(1) I suggest that the authors first explain the task (i.e., Fig. 3) at the beginning of the results. And it seems more appropriate to show the time course figures (Fig. 2) and before the bar plots (Fig. 1). If I understand correctly, the bar plots reflect the averaged data from the time course plots. Also, please clearly state the time window used to average the data. The results of the correlation analysis can be displayed in the last step.

Thanks for this suggestion. We have now added a concise explanation of the task at the beginning of the results (see lines 101-103). We have also adjusted the figure positions and adjusted the order of our results according to the reviewer’s suggestion. The time window we used to average the data was from the onset of the stimuli until the end of the stimuli presentation. We have now clearly stated these issues in the revised text (see lines 111-112).

(2) According to the above, I think a more reasonable arrangement should be Fig. 3, 2, and 1.

Thanks for this suggestion. We have adjusted the figure positions accordingly.

(3) Please include each subject's data points in the bar plots in Fig. 1.

We have now presented each subject’s individual data point in the bar plot.

(4) Lines 158-160 and 199-202 report interaction effects of the two-way ANOVA. This is good, but the direction of interaction effect should also be reported.

We thank the reviewer for this suggestion. We have now reported the direction of the interaction effect. The significant interaction observed across Experiment 1 and Experiment 2 was mainly due to the diminishment of emotional modulation in inverted BM. The significant interaction crossing Experiment 1 and Experiment 3 was similarly caused by the lack of emotional modulation in nonbiological stimuli. With regard to the significant interaction across Experiment 1 and Experiment 4, it could be primarily attributed to the vanishment of pupil modulation effect between happy and sad local BM. We have specified these points in the revised text, see lines 198-199, 219-220, 267-269.

Reviewer #3 (Recommendations For The Authors):

(1) Number of experiments:

As stated in the Methods section, this study seems to consist of five experiments (120/24=5) according to the description below. However, the current manuscript only reports findings from four of these experiments. Can the authors clarify on this matter?

"A total of 120 participants (44 males, 76 females) ranging from 18 to 29 years old (M ± SD = 23.1 ± 2.5) were recruited, with 24 in each experiment."

We apologize for not making it clear. This referred to a pure behavior explicit emotion classification experiment (N=24) that served as a prior test to confirm that the local BM stimuli conveyed recognizable emotional information. We have now more carefully stated this issue in the revised text, see lines 456-458.

(2) Emotion processing mechanism of BM

"Mechanism" is a very strong word, suggesting a causal relationship. In the setting of a passive viewing task that lacks any behavioral report, it is possible that the observed changes in pupil size could be epiphenomenal, rather than serving as the underlying mechanism.

Thanks for this suggestion. We have now either changed “mechanism” into “phenomenon” or deleted it. We have also carefully discussed the potential implications for future studies to incorporate variant behavioral, physiological and neural indexes to yield more robust causal evidence to unveil the potential mechanism serving the observed multi-level BM emotion processing phenomenon.

(3) Data sharing

The authors could improve their efforts in promoting data transparency to ensure a comprehensive view of the results. This implies sharing deidentified raw data instead of summary data in an Excel spreadsheet.

Thanks for this suggestion. We have now uploaded the deidentified raw data. (https://doi.org/10.57760/sciencedb.psych.00125).

Author Response

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

eLife assessment

This valuable work provides new insights into history-dependent biases in human perceptual decisionmaking. It provides compelling behavioral and MEG evidence that humans adapt their historydependent to the correlation structure of uncertain sensory environments. Further neural data analyses would strengthen some of the findings, and the studied bias would be more accurately framed as a stimulus- or outcome-history bias than a choice-history bias because tested subjects are biased not by their previous choice, but by the previous feedback (indicating the category of the previous stimulus).

Thank you for your constructive evaluation of our manuscript. We have followed your suggestion to frame the studied bias as ‘stimulus history bias’. We now use this term whenever referring to our current results. Please note that we instead use the generic term ‘history bias’ when referring to the history biases studied in the previous literature on this topic in general. This is because these biases were dependent on previous choice(s), previous stimuli, or previous outcomes, or combinations of some (or all) of these factors. We have also added several of your suggested neural data analyses so as to strengthen the support for our conclusions, and we have elaborated on the Introduction so as to clarify the gaps in the literature that our study aims to fill. Our revisions are detailed in our replies below. We also took the liberty to reply to some points in the Public Review, which we felt called for clarification of the main aims (and main contribution) of our study.

Reviewer #1 (Public Review):

This paper aims to study the effects of choice history on action-selective beta band signals in human MEG data during a sensory evidence accumulation task. It does so by placing participants in three different stochastic environments, where the outcome of each trial is either random, likely to repeat, or likely to alternate across trials. The authors provide good behavioural evidence that subjects have learnt these statistics (even though they are not explicitly told about them) and that they influence their decision-making, especially on the most difficult trials (low motion coherence). They then show that the primary effect of choice history on lateralised beta-band activity, which is well-established to be linked to evidence accumulation processes in decision-making, is on the slope of evidence accumulation rather than on the baseline level of lateralised beta.

The strengths of the paper are that it is: (i) very well analysed, with compelling evidence in support of its primary conclusions; (ii) a well-designed study, allowing the authors to investigate the effects of choice history in different stochastic environments.

Thank you for pointing out these strengths of our study.

There are no major weaknesses to the study. On the other hand, investigating the effects of choice/outcome history on evidence integration is a fairly well-established problem in the field. As such, I think that this provides a valuable contribution to the field, rather than being a landmark study that will transform our understanding of the problem.

Your evaluation of the significance of our work made us realize that we may have failed to bring across the main gaps in the literature that our current study aimed to fill. We have now unpacked this in our revised Introduction.

Indeed, many previous studies have quantified history-dependent biases in perceptual choice. However, the vast majority of those studies used tasks without any correlation structure; only a handful of studies have quantified history biases in tasks entailing structured environments, as we have done here (Abrahamyan et al., 2016; Kim et al., 2017; Braun et al., 2018; Hermoso-Mendizabal et al., 2020). The focus on correlated environments matters from an ecological perspective, because (i) natural environments are commonly structured rather than random (a likely reason for history biases being so prevalent in the first place), and (ii) history biases that change flexibly with the environmental structure are a hallmark of adaptive behavior. Critically, the few previous studies that have used correlated environments and revealed flexible/adaptive history biases were purely behavioral. Ours is the first to characterize the neural correlates of adaptive history biases.

Furthermore, although several previous studies have identified neural correlates of history biases in standard perceptual choice tasks in unstructured environments (see (Talluri et al., 2021) for a brief overview), most have focused on static representations of the bias in ongoing activity preceding the new decision; only a single monkey physiology study has tested for both a static bias in the pre-stimulus activity and a dynamic bias building up during evidence accumulation (Mochol et al., 2021). Ours is the first demonstration of a dynamic bias during evidence accumulation in the human brain.

The authors have achieved their primary aims and I think that the results support their main conclusions. One outstanding question in the analysis is the extent to which the source-reconstructed patches in Figure 2 are truly independent of one another (as often there is 'leakage' from one source location into another, and many of the different ROIs have quite similar overall patterns of synchronisation/desynchronisation.).

We do not assume (and nowhere state) that the different ROIs are “truly independent” of one another. In fact, patterns of task-related power modulations of neural activity would be expected to be correlated between many visual and action-related cortical areas even without leakage (due to neural signal correlations). So, one should not assume independence even for intracortically recorded local field potential data, fMRI data, or other data with minimal spatial leakage effects. That said, we agree that filter leakage will add a (trivial) component to the similarity of power modulations across ROIs, which can and should be quantified with the analysis you propose.

A possible way to investigate this further would be to explore the correlation structure of the LCMV beamformer weights for these different patches, to ask how similar/dissimilar the spatial filters are for the different reconstructed patches.

Thank you for suggesting this analysis, which provides a very useful context for interpreting the pattern of results shown in our Figure 2. We have now computed (Pearson) correlation coefficients of the LCMV beamformer weights across the regions of interest. The results are shown in the new Figure 2 – figure supplement 1. This analysis provided evidence for minor leakage between the source estimates for neighboring cortical regions (filter correlations <= than 0.22 on average across subjects) and negligible leakage for more distant regions. We now clearly state this when referring to Figure 2.

That said, we would also like to clarify our reasoning behind Figure 2. Our common approach to these source-reconstructed MEG data is to focus on the differences, rather than the similarities between ROIs, because the differences cannot be accounted for by leakage. Our analyses show clearly distinct, and physiologically plausible functional profiles across ROIs (motion coherence encoding in visual regions, action choice coding in motor regions), in line with other work using our general approach (Wilming et al., 2020; Murphy et al., 2021; Urai and Donner, 2022).

Most importantly, our current analyses focus on the impact of history bias on the build-up of actionselective activity in downstream, action-related areas; and we chose to focus on M1 only in order to avoid hard-to-interpret comparisons between neighboring action-related regions. Figure 2 is intended as a demonstration of the data quality (showing sensible signatures for all ROIs) and as a context for the interpretation of our main neural results from M1 shown in the subsequent figures. So, all our main conclusions are unaffected by leakage between ROIs.

We have now clarified these points in the paper.

Reviewer #2 (Public Review):

In this work, the authors use computational modeling and human neurophysiology (MEG) to uncover behavioral and neural signatures of choice history biases during sequential perceptual decision-making. In line with previous work, they see neural signatures reflecting choice planning during perceptual evidence accumulation in motor-related regions, and further show that the rate of accumulation responds to structured, predictable environments suggesting that statistical learning of environment structure in decision-making can adaptively bias the rate of perceptual evidence accumulation via neural signatures of action planning. The data and evidence show subtle but clear effects, and are consistent with a large body of work on decision-making and action planning.

Overall, the authors achieved what they set out to do in this nice study, and the results, while somewhat subtle in places, support the main conclusions. This work will have impact within the fields of decisionmaking and motor planning, linking statistical learning of structured sequential effects in sense data to evidence accumulation and action planning.

Strengths:

• The study is elegantly designed, and the methods are clear and generally state-of-the-art

• The background leading up to the study is well described, and the study itself conjoins two bodies of work - the dynamics of action-planning processes during perceptual evidence accumulation, and the statistical learning of sequential structure in incoming sense data

• Careful analyses effectively deal with potential confounds (e.g., baseline beta biases)

Thank you for pointing out these strengths of our study.

Weaknesses:

• Much of the study is primarily a verification of what was expected based on previous behavioral work, with the main difference (if I'm not mistaken) being that subjects learn actual latent structure rather than expressing sequential biases in uniform random environments.

As we have stated in our reply to the overall assessment above, we realize that we may have failed to clearly communicate the novelty of our current results, and we have revised our Introduction accordingly. It is true that most previous studies of history biases in perceptual choice have used standard tasks without across-trial correlation structure. Only a handful of studies have quantified history biases in tasks entailing structured environments that varied from one condition to the next (Abrahamyan et al., 2016; Kim et al., 2017; Braun et al., 2018; Hermoso-Mendizabal et al., 2020), and showed that history biases change flexibly with the environmental structure. Our current work adds to this emerging picture, using a specific task setting analogous to one of these previous studies done in rats (Hermoso-Mendizabal et al., 2020).

Critically, all the previous studies that have revealed flexible/adaptive history biases in correlated environments were purely behavioral. Ours is the first to characterize the neural correlates of adaptive history biases. And it is also the very first demonstration of a dynamic history-dependent bias (i.e., one that gradually builds up during evidence accumulation) in the human brain.

Whether this difference - between learning true structure or superstitiously applying it when it's not there - is significant at the behavioral or neural level is unclear. Did the authors have a hypothesis about this distinction? If the distinction is not relevant, is the main contribution here the neural effect?

We are not quite sure what exactly you mean with “is significant”, so we will reply to two possible interpretations of this statement.

The first is that you may be asking for evidence for any difference between the estimated history biases in the structured (i.e., Repetitive, Alternating) vs. the unstructured (i.e., Neutral) environments used in our experiment. We do, in fact, provide quantitative comparisons between the history biases in the structured and Neutral environments at the behavioral level. Figure 1D and Figure 1 – figure supplement 2A and accompanying text show a robust and statistically significant difference in history biases. Specifically, the previous stimulus weights differ between each of the biased environments and the Neutral environment and the weights shifted in expected and opposite directions for both structured environments, indicating a tendency to repeat the previous stimulus category in Repetitive and vice versa in Alternating (Figure1D). Going further, we also demonstrate that the adjustment of the history is behaviorally relevant in that it improves performance in the two structured environments, but not in the unstructured environment (Figure 1F and Figure 1 – figure supplement 2A and figure supplement 3).

The second is that you refer to the question of whether the history biases are generated via different computations in structured vs. random environments. Indeed, this is a very interesting and important question. We cannot answer this question based on the available results, because we here used a statistical (i.e., descriptive) model. Addressing this question would require developing and fitting a generative model of the history bias and comparing the inferred latent learning processes between environments. This is something we are doing in ongoing work.

• The key effects (Figure 4) are among the more statistically on-the-cusp effects in the paper, and the Alternating group in 4C did not reliably go in the expected direction. This is not a huge problem per se, but does make the key result seem less reliable given the clear reliability of the behavioral results

The model-free analyses in Figure 3C and 4B, C from the original version of our manuscript were never intended to demonstrate the “key effects”, but only as supplementary to the results from the modelbased analyses in Figures 3C and 4D, E in our current version of the manuscript. The latter show the “key effects” because they are a direct demonstration of the shaping of build-up of action-selective activity by history bias.

To clarify this, we now decided to focus Figures 3 and 4 on the model-based analyses only. This decision was further supported by noticing a confound in our model-independent analyses in new control analyses prompted by Reviewer #3.

Please note that the alternating bias in the Alternating environment is also less strong at the behavioral level compared to the bias in the Repetitive condition (see Figure 1D). A possible explanation is that a sequence of repetitive stimuli produces stronger prior expectations (for repetition) than an equally long sequence of alternating stimuli (Meyniel et al., 2016). This might also induce the bias to repeat the previous stimulus category in the Neutral condition (Figure 1D). Moreover, this intrinsic repetition bias might counteract the bias to alternate the previous stimulus category in Alternating.

• The treatment of "awareness" of task structure in the study (via informal interviews in only a subsample of subjects) is wanting

Agreed. We have now removed this statement from Discussion.

Reviewer #3 (Public Review):

This study examines how the correlation structure of a perceptual decision making task influences history biases in responding. By manipulating whether stimuli were more likely to be repetitive or alternating, they found evidence from both behavior and a neural signal of decision formation that history biases are flexibly adapted to the environment. On the whole, these findings are supported across an impressive range of detailed behavioral and neural analyses. The methods and data from this study will likely be of interest to cognitive neuroscience and psychology researchers. The results provide new insights into the mechanisms of perceptual decision making.

The behavioral analyses are thorough and convincing, supported by a large number of experimental trials (~600 in each of 3 environmental contexts) in 38 participants. The psychometric curves provide clear evidence of adaptive history biases. The paper then goes on to model the effect of history biases at the single trial level, using an elegant cross-validation approach to perform model selection and fitting. The results support the idea that, with trial-by-trial accuracy feedback, the participants adjusted their history biases due to the previous stimulus category, depending on the task structure in a way that contributed to performance.

Thank you for these nice words on our work.

The paper then examines MEG signatures of decision formation, to try to identify neural signatures of these adaptive biases. Looking specifically at motor beta lateralization, they found no evidence that starting-level bias due to the previous trial differed depending on the task context. This suggests that the adaptive bias unfolds in the dynamic part of the decision process, rather than reflecting a starting level bias. The paper goes on to look at lateralization relative to the chosen hand as a proxy for a decision variable (DV), whose slope is shown to be influenced by these adaptive biases.

This analysis of the buildup of action-selective motor cortical activity would be easier to interpret if its connection with the DV was more explicitly stated. The motor beta is lateralized relative to the chosen hand, as opposed to the correct response which might often be the case. It is therefore not obvious how the DV behaves in correct and error trials, which are combined together here for many of the analyses.

We have now unpacked the connection of the action-selective motor cortical activity and decision variable in the manuscript, as follows:

“This signal, referred to as ‘motor beta lateralization’ in the following, has been shown to exhibit hallmark signatures of the DV, specifically: (i) selectivity for choice and (ii) ramping slope that depends on evidence strength (Siegel et al., 2011; Murphy et al., 2021; O’Connell and Kelly, 2021).”

Furthermore, we have added a figure of the time course of the motor beta lateralization separately for correct and error trials, locked to both stimulus onset and to motor response (Figure 2 – figure supplement 2). This signal reached statistical significance earlier for correct than error trials, and during the stimulus interval it ramped to a larger (i.e., more negative) amplitude for correct trials (Figure 2 – figure supplement 2, left). But the signal was indistinguishable in amplitude between correct and error trials around the time of the motor response (Figure 2 – figure supplement 2, right). This pattern matches what would be expected for a neural signature of the DV, because errors are more frequently made on weak-evidence trials than correct choices and because even for matched evidence strength, the DV builds up more slowly before error trials in accumulator models (Ratcliff and McKoon, 2008).

--

As you will see, all three reviewers found your work to provide valuable insights into history-dependent biases during perceptual decision-making. During consultation between reviewers, there was agreement that what is referred as a choice-history bias in the current version of the manuscript should rather be framed as a stimulus- or outcome-history bias (despite the dominant use of the term 'choicehistory' bias in the existing literature), and the reviewers pointed toward further analyses of the neural data which they thought would strengthen some of the claims made in the preprint. We hope that these comments will be useful if you wish to revise your preprint.

We are pleased to hear that the reviewers think our work provides valuable insights into historydependent biases in perceptual decision-making. We thank you for your thoughtful and constructive evaluation of our manuscript.

We have followed your suggestion to frame the studied bias as ‘stimulus history bias’. We now use this term whenever referring to our current results. Please note that we instead use the generic term ‘history bias’ when referring to the history biases studied in the previous literature on this topic in general. This is because these biases were dependent on previous choice(s), previous stimuli, or previous outcomes, or combinations of some (or all) of these factors.

We have also performed several of your suggested neural data analyses so as to strengthen the support for our conclusions.

Reviewer #1 (Recommendations For The Authors):

One suggestion is to explore the correlation structure of the LCMV beam former weights for the regions of interest in the study, for the reasons outlined in my public review.

Again, thank you for suggesting this analysis, which provides a very useful context for interpreting the pattern of results shown in our Figure 2. We have now computed (Pearson) correlation coefficients of the LCMV beamformer weights across the regions of interest. The results are shown in the new Figure 2 – figure supplement 1. This analysis provided evidence for minor leakage between the source estimates for neighboring cortical regions (filter correlations <= than 0.22 on average across subjects) and negligible leakage for more distant regions. We now clearly state this when referring to Figure 2.

That said, we would also like to clarify our reasoning behind Figure 2. Our common approach to these source-reconstructed MEG data is to focus on the differences, rather than the similarities between ROIs, because the differences cannot be accounted for by leakage. Our analyses show clearly distinct, and physiologically plausible functional profiles across ROIs (motion coherence encoding in visual regions, action choice coding in motor regions), in line with other work using our general approach (Wilming et al., 2020; Murphy et al., 2021; Urai and Donner, 2022).

Most importantly, our current analyses focus on the impact of history bias on the build-up of actionselective activity in downstream, action-related areas; and we chose to focus on M1 only in order to avoid hard-to-interpret comparisons between neighboring action-related regions. Figure 2 is intended as a demonstration of the data quality (showing sensible signatures for all ROIs) and as a context for the interpretation of our main neural results from M1 shown in the subsequent figures. So, all our main conclusions are unaffected by leakage between ROIs.

We have now clarified also these points in the paper.

I also wondered if the authors had considered:

(i) the extent to which the bias changes across time, as the transition probabilities are being learnt across the experiment? given that these are not being explicitly instructed to participants, is any modelling possible of how the transition structure is itself being learnt over time, and whether this makes predictions of either behaviour or neural signals?

We refer to this point in the discussion. The learning of the transition probabilities which can and should be addressed. This requires generative models that capture the learning of the transition structure over time (Yu and Cohen, 2009; Meyniel et al., 2016; Glaze et al., 2018; Hermoso-Mendizabal et al., 2020).

The fact that our current statistical modeling approach successfully captures the bias adjustment between environments implies that the learning must be sufficiently fast. Tracking this process explicitly would be an exciting and important endeavor for the future. We think it is beyond the scope of the present study focusing on the trial-by-trial effect of history bias (however generated) on the build-up of action-selective activity.

(ii) neural responses at the time of choice outcome - given that so much of the paper is about the update of information in different statistical environments, it seems a shame that no analyses are included of feedback processing, how this differs across the different environments, and how might be linked to behavioural changes at the next trial.

We agree that the neural responses to feedback are a very interesting topic. We currently analyze these in another ongoing project on (outcome) history bias in a foraging task. We will consider re-analyzing the feedback component in the current data set, in this new study as well.

However, this is distinct from the main question that is in the focus of our current paper – which, as elaborated above, is important to answer: whether and how adaptive history biases shape the dynamics of action-selective cortical activity in the human brain. While interesting and important, neural responses to feedback were not part of this question. So, we prefer to keep the focus of our paper on our original question.

Reviewer #2 (Recommendations For The Authors):

Minor:

-pg. 7: "inconstant"

-some citations (e.g., Barbosa 2020) are missing from the bibliography

Thank you for pointing this out. We have fixed these.

-figure S2 is very useful! could probably go in main text.

We agree that this figure is important. But we decided to show it in the Supplement (now Figure 1 – figure supplement 2) after careful consideration for two reasons. First, we wanted to put the reader’s focus on the stimulus weights, because it is those weights, which are flexibly adjusted to the statistics of the environment rather than the choice weights, which seem less adaptive (i.e., stereotypical across environments) and idiosyncratic. Second, plotting the previous stimulus weights only enabled to add the individual weights in the Neutral condition, which would have been to cluttered to add to figure S2.

For these reasons, we feel that this Figure is more suitable for expert readers with a special interest in the details of the behavioral analyses and would be better placed in the Supplement. These readers will certainly be able to find and interpret that information in the Supplement.

Reviewer #3 (Recommendations For The Authors):

I would suggest that a more in depth description of the previous literature that explains exactly how the features of the lateralized beta--as it is formulated here-- reflect the decision variable would assist with the readers' understanding. A demonstration of how the lateralized beta behaves under different coherence conditions, or for corrects vs errors, for example, might be helpful for readers.

We now provide a more detailed description of how/why the motor beta lateralization is a valid proxy of DV in the revised paper.

We have demonstrated the dependence of the ramping of the motor beta lateralization on the motion coherence using a regression model with current signed motion coherence as well as single trial bias as regressors. The beta weights describing the impact of the signed motion coherence on the amplitude as well as on the slope of the motor beta lateralization are shown in Figure 4G (now 4E). As expected, stronger motion coherence induces a steeper downward slope of the motor beta lateralization.

Furthermore, we have added a figure of the time course of the motor beta lateralization separately for correct and error trials, locked to both stimulus onset and to motor response (Figure 2 – figure supplement 2). This signal reached statistical significance earlier for correct than error trials, and during the stimulus interval it ramped to a larger (i.e., more negative) amplitude for correct trials (Figure 2 – figure supplement 2, left). But the signal was indistinguishable in amplitude between correct and error trials around the time of the motor response (Figure 2 – figure supplement 2, right).This pattern matches what would be expected for a neural signature DV, because errors are more frequently made on weakevidence trials than correct choices and because even for matched evidence strength, the DV builds up more slowly before error trials in accumulator models (Ratcliff and McKoon, 2008).

Finally, please note that our previous studies have demonstrated that the time course of the beta lateralization during the trial closely tracks the time course of a normative model-derived DV (Murphy et al., 2021) and that the motor beta ramping slope is parametrically modulated by motion coherence (de Lange et al., 2013), which is perfectly in line with the current results.

Along similar lines, around figures 3c and 4B, some control analyses may be helpful to clarify whether there are differences between the groups of responses consistent and inconsistent with the previous trial (e.g. correctness, coherence) that differ between environments, and also could influence the lateralized beta.

Thank you for pointing us to this important control analysis. We have done this, and indeed, it identified accuracy and motion strength as possible confounds (Author response image 1). Specifically, proportion correct as well as motion coherence were larger for consistent vs. inconsistent conditions in Repetitive and vice versa in Alternating. Those differences in accuracy and coherence might indeed influence the slope of the motor beta lateralization that our model-free analysis had identified, rendering the resulting difference between consistent and inconsistent difficult to interpret unambiguously in terms of bias. Thus, we have decided to drop the consistency (i.e., model-independent) analysis and focus completely on the modelbased analyses.

Author response image 1.

Proportion correct and motion coherence split by environment and consistency of current choice and previous stimulus. In the Repetitive environment (Rep.), accuracy and motion coherence are larger for current choice consistent vs. inconsistent with previous stimulus category and vice versa in the Alternating environment (Alt.).

Importantly, this decision has no implications for the conclusions of our paper: The model-independent analyses in the original versions of Figure 3 and 4 were only intended as a supplement to the most conclusive and readily interpretable results from the model-based analyses (now in Figs. 3C and 4D, E. The latter are the most direct demonstration of a shaping of build-up of action-selective activity by history bias, and they are unaffected by these confounds.

In addition, I wondered whether the bin subsampling procedure to match trial numbers for choice might result in unbalanced coherences between the up and down choices.

The subsampling itself did not cause any unbalanced coherences between the up and down choices, which we now show in Figure 4 – figure supplement 1. There was only a slight imbalance in coherences between up and down choices before the subsampling which then translated into the subsampled trials but the coherences were equally distributed before as compared to after the subsampling.

Also, please note that the purpose of this analysis was to make the neural bias directly “visible” in the beta lateralization data, rather than just regression weights. The issue does not pertain to the critical single-trial regression analysis, which yielded consistent results.

References

Abrahamyan A, Silva LL, Dakin SC, Carandini M, Gardner JL (2016) Adaptable history biases in human perceptual decisions. Proceedings of the National Academy of Sciences 113:E3548–E3557.

Braun A, Urai AE, Donner TH (2018) Adaptive History Biases Result from Confidence-weighted Accumulation of Past Choices. The Journal of Neuroscience:2189–17. de Lange FP, Rahnev DA, Donner TH, Lau H (2013) Prestimulus Oscillatory Activity over Motor Cortex Reflects Perceptual Expectations. Journal of Neuroscience 33:1400–1410.

Glaze CM, Filipowicz ALS, Kable JW, Balasubramanian V, Gold JI (2018) A bias–variance trade-off governs individual differences in on-line learning in an unpredictable environment. Nat Hum Behav 2:213–224.

Hermoso-Mendizabal A, Hyafil A, Rueda-Orozco PE, Jaramillo S, Robbe D, de la Rocha J (2020) Response outcomes gate the impact of expectations on perceptual decisions. Nat Commun 11:1057.

Kim TD, Kabir M, Gold JI (2017) Coupled Decision Processes Update and Maintain Saccadic Priors in a Dynamic Environment. The Journal of Neuroscience 37:3632–3645.

Meyniel F, Maheu M, Dehaene S (2016) Human Inferences about Sequences: A Minimal Transition Probability Model Gershman SJ, ed. PLOS Computational Biology 12:e1005260.

Mochol G, Kiani R, Moreno-Bote R (2021) Prefrontal cortex represents heuristics that shape choice bias and its integration into future behavior. Current Biology 31:1234-1244.e6.

Murphy PR, Wilming N, Hernandez-Bocanegra DC, Prat-Ortega G, Donner TH (2021) Adaptive circuit dynamics across human cortex during evidence accumulation in changing environments. Nat Neurosci 24:987–997.

O’Connell RG, Kelly SP (2021) Neurophysiology of Human Perceptual Decision-Making. Annu Rev Neurosci 44:495–516.

Ratcliff R, McKoon G (2008) The Diffusion Decision Model: Theory and Data for Two-Choice Decision Tasks. Neural Computation 20:873–922.

Siegel M, Engel AK, Donner TH (2011) Cortical Network Dynamics of Perceptual Decision-Making in the Human Brain. Frontiers in Human Neuroscience 5 Available at: http://journal.frontiersin.org/article/10.3389/fnhum.2011.00021/abstract [Accessed April 8, 2017].

Talluri BC, Braun A, Donner TH (2021) Decision making: How the past guides the future in frontal cortex. Current Biology 31:R303–R306.

Urai AE, Donner TH (2022) Persistent activity in human parietal cortex mediates perceptual choice repetition bias. Nat Commun 13:6015.

Wilming N, Murphy PR, Meyniel F, Donner TH (2020) Large-scale dynamics of perceptual decision information across human cortex. Nat Commun 11:5109.

Yu A, Cohen JD (2009) Sequential effects: Superstition or rational behavior. Advances in neural information processing systems 21:1873–1880.

Author response:

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

We have specifically addressed the points of uncertainty highlighted in eLife's editorial assessment, which concerned the lack of low-level acoustics control, limitations of experimental design, and in-depth analysis. Regarding “the lack of low-level acoustics control, limitations of experimental design”, in response to Reviewer #1, we clarify that our study aimed to provide a broad perspective —which includes both auditory and higher-level processes— on the similarities and distinctions in processing natural speech and music within an ecological context. Regarding “the lack of in-depth analysis”, in response to Reviewer #1 and #2, we have clarified that while model-based analyzes are valuable, they pose fundamental challenges when comparing speech and music. Non-acoustic features inherently differ between speech and music (such as phonemes and pitch), making direct comparisons reliant on somewhat arbitrary choices. Our approach mitigates this challenge by analyzing the entire neural signal, thereby avoiding potential pitfalls associated with encoding models of non-comparable features. Finally, we provide some additional analyzes suggested by the Reviewers.

We sincerely appreciate your thoughtful and thorough consideration throughout the review process.

eLife assessment

This study presents valuable intracranial findings on how two important types of natural auditory stimuli - speech and music - are processed in the human brain, and demonstrates that speech and music largely share network-level brain activities, thus challenging the domain-specific processing view. The evidence supporting the claims of the authors is solid but somewhat incomplete since although the data analysis is thorough, the results are robust and the stimuli have ecological validity, important considerations such as low-level acoustics control, limitations of experimental design, and in-depth analysis, are lacking. The work will be of broad interest to speech and music researchers as well as cognitive scientists in general.

Reviewer #1 (Public Review):

Summary:

In this study, the authors examined the extent to which the processing of speech and music depends on neural networks that are either specific to a domain or general in nature. They conducted comprehensive intracranial EEG recordings on 18 epilepsy patients as they listened to natural, continuous forms of speech and music. This enabled an exploration of brain activity at both the frequency-specific and network levels across a broad spectrum. Utilizing statistical methods, the researchers classified neural responses to auditory stimuli into categories of shared, preferred, and domain-selective types. It was observed that a significant portion of both focal and network-level brain activity is commonly shared between the processing of speech and music. However, neural responses that are selectively responsive to speech or music are confined to distributed, frequency-specific areas. The authors highlight the crucial role of using natural auditory stimuli in research and the need to explore the extensive spectral characteristics inherent in the processing of speech and music.

Strengths:

The study's strengths include its high-quality sEEG data from a substantial number of patients, covering a majority of brain regions. This extensive cortical coverage grants the authors the ability to address their research questions with high spatial resolution, marking an advantage over previous studies. They performed thorough analyses across the entire cortical coverage and a wide frequency range of neural signals. The primary analyses, including spectral analysis, temporal response function calculation, and connectivity analysis, are presented straightforwardly. These analyses, as well as figures, innovatively display how neural responses, in each frequency band and region/electrode, are 'selective' (according to the authors' definition) to speech or music stimuli. The findings are summarized in a manner that efficiently communicates information to readers. This research offers valuable insights into the cortical selectivity of speech and music processing, making it a noteworthy reference for those interested in this field. Overall, this research offers a valuable dataset and carries out extensive yet clear analyses, amounting to an impressive empirical investigation into the cortical selectivity of speech and music. It is recommended for readers who are keen on understanding the nuances of selectivity and generality in the processing of speech and music to refer to this study's data and its summarized findings.

Weaknesses:

The weakness of this study, in my view, lies in its experimental design and reasoning:

(1) Despite using longer stimuli, the study does not significantly enhance ecological validity compared to previous research. The analyses treat these long speech and music stimuli as stationary signals, overlooking their intricate musical or linguistic structural details and temporal variation across local structures like sentences and phrases. In previous studies, short, less ecological segments of music were used, maintaining consistency in content and structure. However, this study, despite employing longer stimuli, does not distinguish between neural responses to the varied contents or structures within speech and music. Understanding the implications of long-term analyses, such as spectral and connectivity analyses over extended periods of around 10 minutes, becomes challenging when they do not account for the variable, sometimes quasi-periodical or even non-periodical, elements present in natural speech and music. When contrasting this study with prior research and highlighting its advantages, a more balanced perspective would have been beneficial in the manuscript.

Regarding ecological validity, we respectfully hold a differing perspective from the reviewer. In our view, a one-second music stimulus lacks ecological validity, as real-world music always extends much beyond such a brief duration. While we acknowledge the trade-off in selecting longer stimuli, limiting the diversity of musical styles, we maintain that only long stimuli afford participants an authentic musical listening experience. Conversely, shorter stimuli may lead participants to merely "skip through" musical excerpts rather than engage in genuine listening.

Regarding the critique that we "did not distinguish between neural responses to the varied contents or structures within speech and music," we partly concur. Our TRF (temporal response function) analyzes incorporate acoustic content, particularly the acoustic envelope, thereby addressing this concern to some extent. However, it is accurate to note that we did not model non-acoustic features. In acknowledging this limitation, we would like to share an additional thought with the reviewer regarding model comparison for speech and music. Specifically, comparing results from a phonetic (or syntactic) model of speech to a pitch-melodic (or harmonic) model for music is not straightforward, as these models operate on fundamentally different dimensions. In other words, while assuming equivalence between phonemes and pitches may be a reasonable assumption, it in essence relies on a somewhat arbitrary choice. Consequently, comparing and interpreting neuronal population coding for one or the other model remains problematic. In summary, because the models for speech and music are different (except for acoustic models), direct comparison is challenging, although still commendable and of interest.

Finally, we did take into account the reviewer’s remark and did our best to give a more balanced perspective of our approach and previous studies in the discussion.

“While listening to natural speech and music rests on cognitively relevant neural processes, our analytical approach, extending over a rather long period of time, does not allow to directly isolate specific brain operations. Computational models -which can be as diverse as acoustic (Chi et al., 2005), cognitive (Giordano et al., 2021), information-theoretic (Di Liberto et al., 2020), or self-supervised neural network (Donhauser & Baillet, 2019 ; Millet et al., 2022) models- are hence necessary to further our understanding of the type of computations performed by our reported frequency-specific distributed networks. Moreover, incorporating models accounting for musical and linguistic structure can help us avoid misattributing differences between speech and music driven by unmatched sensitivity factors (e.g., arousal, emotion, or attention) as inherent speech or music selectivity (Mas-Herrero et al., 2013; Nantais & Schellenberg, 1999).”

(2) In contrast to previous studies that employed short stimulus segments along with various control stimuli to ensure that observed selectivity for speech or music was not merely due to low-level acoustic properties, this study used longer, ecological stimuli. However, the control stimuli used in this study, such as tone or syllable sequences, do not align with the low-level acoustic properties of the speech and music stimuli. This mismatch raises concerns that the differences or selectivity between speech and music observed in this study might be attributable to these basic acoustic characteristics rather than to more complex processing factors specific to speech or music.

We acknowledge the reviewer's concern. Indeed, speech and music differ on various levels, including acoustic and cognitive aspects, and our analyzes do not explicitly distinguish them. The aim of this study was to provide an overview of the similarities and differences between natural speech and music processing, in ecological context. Future work is needed to explore further the different hierarchical levels or networks composing such listening experiences. Of note, however, we report whole-brain results with high spatial resolution (thanks to iEEG recordings), enabling the distinction between auditory, superior temporal gyrus (STG), and higher-level responses. Our findings clearly highlight that both auditory and higher-level regions predominantly exhibit shared responses, challenging the interpretation that our results can be attributed solely to differences in 'basic acoustic characteristics'.

We have now more clearly pointed out this reasoning in the results section:

“The spatial distribution of the spectrally-resolved responses corresponds to the network typically involved in speech and music perception. This network encompasses both ventral and dorsal auditory pathways, extending well beyond the auditory cortex and, hence, beyond auditory processing that may result from differences in the acoustic properties of our baseline and experimental stimuli.“

(3) The concept of selectivity - shared, preferred, and domain-selective - increases the risks of potentially overgeneralized interpretations and theoretical inaccuracies. The authors' categorization of neural sites/regions as shared, preferred, or domain-selective regarding speech and music processing essentially resembles a traditional ANOVA test with post hoc analysis. While this categorization gives meaningful context to the results, the mere presence of significant differences among control stimuli, a segment of speech, and a piece of music does not necessarily imply that a region is specifically selective to a type of stimulus like speech. The manuscript's narrative might lead to an overgeneralized interpretation that their findings apply broadly to speech or music. However, identifying differences in neural responses to a few sets of specific stimuli in one brain region does not robustly support such a generalization. This is because speech and music are inherently diverse, and specificity often relates more to the underlying functions than to observed neural responses to a limited number of examples of a stimulus type. See the next point.

Exactly! Here, we present a precise operational definition of these terms, implemented with clear and rigorous statistical methods. It is important to note that in many cognitive neuroscience studies, the term "selective" is often used without a clear definition. By establishing operational definitions, we identified three distinct categories based on statistical testing of differences from baseline and between conditions. This approach provides a framework for more accurate interpretation of experimental findings, as now better outlined in the introduction:

“Finally, we suggest that terms should be operationally defined based on statistical tests, which results in a clear distinction between shared, selective, and preferred activity. That is, be A and B two investigated cognitive functions, “shared” would be a neural population that (compared to a baseline) significantly and equally contributes to the processing of both A and B; “selective” would be a neural population that exclusively contributes to the processing of A or B (e.g. significant for A but not B); and “preferred” would be a neural population that significantly contributes to the processing of both A and B, but more prominently for A or B (Figure 1A).”

Regarding the risk of over-generalization, we want to clarify that our manuscript does not claim that a specific region or frequency band is selective to speech or music. As indeed we focus on testing excerpts of speech and music, we employ the reverse logical reasoning: "if 10 minutes of instrumental music activates a region traditionally associated with speech selectivity, we can conclude that this region is NOT speech-selective." Our conclusions revolve around the absence of selectivity rather than the presence of selective areas or frequency bands. In essence, "one counterexample is enough to disprove a theory." We now further elaborated on this point in the discussion section:

“In this context, in the current study we did not observe a single anatomical region for which speech-selectivity was present, in any of our analyzes. In other words, 10 minutes of instrumental music was enough to activate cortical regions classically labeled as speech (or language) -selective. On the contrary, we report spatially distributed and frequency-specific patterns of shared, preferred, or selective neural responses and connectivity fingerprints. This indicates that domain-selective brain regions should be considered as a set of functionally homogeneous but spatially distributed voxels, instead of anatomical landmarks.”

(4) The authors' approach, akin to mapping a 'receptive field' by correlating stimulus properties with neural responses to ascertain functional selectivity for speech and music, presents issues. For instance, in the cochlea, different stimuli activate different parts of the basilar membrane due to the distinct spectral contents of speech and music, with each part being selective to certain frequencies. However, this phenomenon reflects the frequency selectivity of the basilar membrane - an important function, not an inherent selectivity for speech or music. Similarly, if cortical regions exhibit heightened responses to one type of stimulus over another, it doesn't automatically imply selectivity or preference for that stimulus. The explanation could lie in functional aspects, such as a region's sensitivity to temporal units of a specific duration, be it music, speech, or even movie segments, and its role in chunking such units (e.g., around 500 ms), which might be more prevalent in music than in speech, or vice versa in the current study. This study does not delve into the functional mechanisms of how speech and music are processed across different musical or linguistic hierarchical levels but merely demonstrates differences in neural responses to various stimuli over a 10-minute span.

We completely agree with the last statement, as our primary goal was not to investigate the functional mechanisms underlying speech and music processing. However, the finding of a substantial portion of the cortical network as being shared between the two domains constrains our understanding of the underlying common operations. Regarding the initial part of the comment, we would like to clarify that in the framework we propose, if cortical regions show heightened responses to one type of stimulus over another, this falls into the ‘preferred’ category. The ‘selective’ (exclusive) category, on the other hand, would require that the region be unresponsive to one of the two stimuli.

Reviewer #2 (Public Review):

Summary:

The study investigates whether speech and music processing involve specific or shared brain networks. Using intracranial EEG recordings from 18 epilepsy patients, it examines neural responses to speech and music. The authors found that most neural activity is shared between speech and music processing, without specific regional brain selectivity. Furthermore, domain-selective responses to speech or music are limited to frequency-specific coherent oscillations. The findings challenge the notion of anatomically distinct regions for different cognitive functions in the auditory process.

Strengths:

(1) This study uses a relatively large corpus of intracranial EEG data, which provides high spatiotemporal resolution neural recordings, allowing for more precise and dynamic analysis of brain responses. The use of continuous speech and music enhances ecological validity compared to artificial or segmented stimuli.

(2) This study uses multiple frequency bands in addition to just high-frequency activity (HFA), which has been the focus of many existing studies in the literature. This allows for a more comprehensive analysis of neural processing across the entire spectrum. The heterogeneity across different frequency bands also indicates that different frequency components of the neural activity may reflect different underlying neural computations.

(3) This study also adds empirical evidence towards distributed representation versus domain-specificity. It challenges the traditional view of highly specialized, anatomically distinct regions for different cognitive functions. Instead, the study suggests a more integrated and overlapping neural network for processing complex stimuli like speech and music.

Weaknesses:

While this study is overall convincing, there are still some weaknesses in the methods and analyses that limit the implication of the work.

The study's main approach, focusing primarily on the grand comparison of response amplitudes between speech and music, may overlook intricate details in neural coding. Speech and music are not entirely orthogonal with each other at different levels of analysis: at the high-level abstraction, these are two different categories of cognitive processes; at the low-level acoustics, they overlap a lot; at intermediate levels, they may also share similar features. The selected musical stimuli, incorporating both vocals and multiple instrumental sounds, raise questions about the specificity of neural activation. For instance, it's unclear if the vocal elements in music and speech engage identical neural circuits. Additionally, the study doesn't adequately address whether purely melodic elements in music correlate with intonations in speech at a neural level. A more granular analysis, dissecting stimuli into distinct features like pitch, phonetics, timbre, and linguistic elements, could unveil more nuanced shared, and unique neural processes between speech and music. Prior research indicates potential overlap in neural coding for certain intermediate features in speech and music (Sankaran et al. 2023), suggesting that a simple averaged response comparison might not fully capture the complexity of neural encoding. Further delineation of phonetic, melodic, linguistic, and other coding, along with an analysis of how different informational aspects (phonetic, linguistic, melodic, etc) are represented in shared neural activities, could enhance our understanding of these processes and strengthen the study's conclusions.

We appreciate the reviewer's acknowledgment that delving into the intricate details of neural coding of speech and music was beyond the scope of this work. To address some of the more precise issues raised, we have clarified in the manuscript that our musical stimuli do not contain vocals and are purely instrumental. We apologize if this was not clear initially.

“In the main experimental session, patients passively listened to ~10 minutes of storytelling (Gripari, 2004); 577 secs, La sorcière de la rue Mouffetard, (Gripari, 2004) and ~10 minutes of instrumental music (580 secs, Reflejos del Sur, (Oneness, 2006) separated by 3 minutes of rest.”

Furthermore, we now acknowledge the importance of modeling melodic, phonetic, or linguistic features in the discussion, and we have referenced the work of Sankaran et al. (2024) and McCarty et al. (2023) in this regard. However, we would like to share an additional thought with the reviewer regarding model comparison for speech and music. Specifically, comparing results from a phonetic (or syntactic) model of speech to a pitch-melodic (or harmonic) model for music is not straightforward, as these models operate on fundamentally different dimensions. In other words, while assuming equivalence between phonemes and pitches may be a reasonable assumption, it in essence relies on a somewhat arbitrary choice. Consequently, comparing and interpreting neuronal population coding for one or the other model remains problematic. In summary, because the models for speech and music are different (except for acoustic models), direct comparison is challenging, although still commendable and of interest.

“These selective responses, not visible in primary cortical regions, seem independent of both low-level acoustic features and higher-order linguistic meaning (Norman-Haignere et al., 2015), and could subtend intermediate representations (Giordano et al., 2023) such as domain-dependent predictions (McCarty et al., 2023; Sankaran et al., 2023).”

References:

McCarty, M. J., Murphy, E., Scherschligt, X., Woolnough, O., Morse, C. W., Snyder, K., Mahon, B. Z., & Tandon, N. (2023). Intraoperative cortical localization of music and language reveals signatures of structural complexity in posterior temporal cortex. iScience, 26(7), 107223.

Sankaran, N., Leonard, M. K., Theunissen, F., & Chang, E. F. (2023). Encoding of melody in the human auditory cortex. bioRxiv. https://doi.org/10.1101/2023.10.17.562771

The paper's emphasis on shared and overlapping neural activity, as observed through sEEG electrodes, provides valuable insights. It is probably true that domain-specificity for speech and music does not exist at such a macro scale. However, it's important to consider that each electrode records from a large neuronal population, encompassing thousands of neurons. This broad recording scope might mask more granular, non-overlapping feature representations at the single neuron level. Thus, while the study suggests shared neural underpinnings for speech and music perception at a macroscopic level, it cannot definitively rule out the possibility of distinct, non-overlapping neural representations at the microscale of local neuronal circuits for features that are distinctly associated with speech and music. This distinction is crucial for fully understanding the neural mechanisms underlying speech and music perception that merit future endeavors with more advanced large-scale neuronal recordings.

We appreciate the reviewer's concern, but we do not view this as a weakness for our study's purpose. Every method inherently has limitations, and intracranial recordings currently offer the best possible spatial specificity and temporal resolution for studying the human brain. Studying cell assemblies thoroughly in humans is ethically challenging, and examining speech and music in non-human primates or rats raises questions about cross-species analogy. Therefore, despite its limitations, we believe intracranial recording remains the best option for addressing these questions in humans.

Regarding the granularity of neural representation, while understanding how computations occur in the central nervous system is crucial, we question whether the single neuron scale provides the most informative insights. The single neuron approach seem more versatile (e.g., in term of cell type or layer affiliation) than the local circuitry they contribute to, which appears to be the brain's building blocks (e.g., like the laminar organization; see Mendoza-Halliday et al.,2024). Additionally, the population dynamics of these functional modules appear crucial for cognition and behavior (Safaie et al. 2023; Buzsáki and Vöröslakos, 2023). Therefore, we emphasize the need for multi-scale research, as we believe that a variety of approaches will complement each other's weaknesses when taken individually. We clarified this in the introduction:

“This approach rests on the idea that the canonical computations that underlie cognition and behavior are anchored in population dynamics of interacting functional modules (Safaie et al. 2023; Buzsáki and Vöröslakos, 2023) and bound to spectral fingerprints consisting of network- and frequency-specific coherent oscillations (Siegel et al., 2012).”

Importantly, we focus on the macro-scale and conclude that, at the anatomical region level, no speech or music selectivity can be observed during natural stimulation. This is stated in the discussion, as follow:

“In this context, in the current study we did not observe a single anatomical region for which speech-selectivity was present, in any of our analyses. In other words, 10 minutes of instrumental music was enough to activate cortical regions classically labeled as speech (or language) -selective. On the contrary, we report spatially distributed and frequency-specific patterns of shared, preferred, or selective neural responses and connectivity fingerprints. This indicates that domain-selective brain regions should be considered as a set of functionally homogeneous but spatially distributed voxels, instead of anatomical landmarks.”

References :

Mendoza-Halliday, D., Major, A.J., Lee, N. et al. A ubiquitous spectrolaminar motif of local field potential power across the primate cortex. Nat Neurosci (2024).

Safaie, M., Chang, J.C., Park, J. et al. Preserved neural dynamics across animals performing similar behaviour. Nature 623, 765–771 (2023).

Buzsáki, G., & Vöröslakos, M. (2023). Brain rhythms have come of age. Neuron, 111(7), 922-926.

While classifying electrodes into 3 categories provides valuable insights, it may not fully capture the complexity of the neural response distribution to speech and music. A more nuanced and continuous approach could reveal subtler gradations in neural response, rather than imposing categorical boundaries. This could be done by computing continuous metrics, like unique variances explained by each category, or ratio-based statistics, etc. Incorporating such a continuum could enhance our understanding of the neural representation of speech and music, providing a more detailed and comprehensive picture of cortical processing.

To clarify, the metrics we are investigating (coherence, power, linear correlations) are continuous. Additionally, we conduct a comprehensive statistical analysis of these results. The statistical testing, which includes assessing differences from baseline and between the speech and music conditions using a statistical threshold, yields three categories. Of note, ratio-based statistics (a continuous metric) are provided in Figures S9 and S10 (Figures S8 and S9 in the original version of the manuscript).

Reviewer #3 (Public Review):

Summary:

Te Rietmolen et al., investigated the selectivity of cortical responses to speech and music stimuli using neurosurgical stereo EEG in humans. The authors address two basic questions: 1. Are speech and music responses localized in the brain or distributed; 2. Are these responses selective and domain-specific or rather domain-general and shared? To investigate this, the study proposes a nomenclature of shared responses (speech and music responses are not significantly different), domain selective (one domain is significant from baseline and the other is not), domain preferred (both are significant from baseline but one is larger than the other and significantly different from each other). The authors employ this framework using neural responses across the spectrum (rather than focusing on high gamma), providing evidence for a low level of selectivity across spectral signatures. To investigate the nature of the underlying representations they use encoding models to predict neural responses (low and high frequency) given a feature space of the stimulus envelope or peak rate (by time delay) and find stronger encoding for both in the low-frequency neural responses. The top encoding electrodes are used as seeds for a pair-wise connectivity (coherence) in order to repeat the shared/selective/preferred analysis across the spectra, suggesting low selectivity. Spectral power and connectivity are also analyzed on the level of the regional patient population to rule out (and depict) any effects driven by a select few patients. Across analyses the authors consistently show a paucity of domain selective responses and when evident these selective responses were not represented across the entire cortical region. The authors argue that speech and music mostly rely on shared neural resources.

Strengths:

I found this manuscript to be rigorous providing compelling and clear evidence of shared neural signatures for speech and music. The use of intracranial recordings provides an important spatial and temporal resolution that lends itself to the power, connectivity, and encoding analyses. The statistics and methods employed are rigorous and reliable, estimated based on permutation approaches, and cross-validation/regularization was employed and reported properly. The analysis of measures across the entire spectra in both power, coherence, and encoding models provides a comprehensive view of responses that no doubt will benefit the community as an invaluable resource. Analysis of the level of patient population (feasible with their high N) per region also supports the generalizability of the conclusions across a relatively large cohort of patients. Last but not least, I believe the framework of selective, preferred, and shared is a welcome lens through which to investigate cortical function.

Weaknesses:

I did not find methodological weaknesses in the current version of the manuscript. I do believe that it is important to highlight that the data is limited to passively listening to naturalistic speech and music. The speech and music stimuli are not completely controlled with varying key acoustic features (inherent to the different domains). Overall, I found the differences in stimulus and lack of attentional controls (passive listening) to be minor weaknesses that would not dramatically change the results or conclusions.

Thank you for this positive review of our work. We added these points as limitations and future directions in the discussion section:

“Finally, in adopting here a comparative approach of speech and music – the two main auditory domains of human cognition – we only investigated one type of speech and of music also using a passive listening task. Future work is needed to investigate for instance whether different sentences or melodies activate the same selective frequency-specific distributed networks and to what extent these results are related to the passive listening context compared to a more active and natural context (e.g. conversation).”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The concepts of activation and deactivation within the study's context of selectivity are not straightforward to comprehend. It would be beneficial for the authors to provide more detailed explanations of how these phenomena relate to the selectivity of neural responses to speech and music. Such elaboration would aid readers in better understanding the nuances of how certain brain regions are selectively activated or deactivated in response to different auditory stimuli.

The reviewer is right that the reported results are quite complex to interpret. The concepts of activation and deactivation are generally complex to comprehend as they are in part defined by an approach (e.g., method and/or metric) and the scale of observation (Pfurtscheller et al., 1999). The power (or the magnitude) of time-frequency estimate is by definition a positive value. Deactivation (or desynchronization) is therefore related to the comparison used (e.g., baseline, control, condition). This is further complexified by the scale of the measurement, for instance, when it comes to a simple limb movement, some brain areas in sensory motor cortex are going to be activated, yet this phenomenon is accompanied at a finer scale by some desynchonization of the mu-activity, and such desynchronization is a relative measure (e.g., before/after motor movement). At a broader scale it is not rare to see some form of balance between brain networks, some being ‘inhibited’ to let some others be activated like the default mode network versus sensory-motor networks. In our case, when estimating selective responses, it is the strength of the signal that matters. The type of selectivity is then defined by the sign/direction of the comparison/subtraction. We now provide additional details about the sign of selectivity between domains and frequencies in the Methods and Results section:

Methods:

“In order to explore the full range of possible selective, preferred, or shared responses, we considered both responses greater and smaller than the baseline. Indeed, as neural populations can synchronize or desynchronize in response to sensory stimulation, we estimated these categories separately for significant activations and significant deactivations compared to baseline.”

Results:

“We classified, for each canonical frequency band, each channel into one of the categories mentioned above, i.e. shared, selective, or preferred (Figure 1A), by examining whether speech and/or music differ from baseline and whether they differ from each other. We also considered both activations and deactivations, compared to baseline, as both index a modulation of neural population activity, and have been linked with cognitive processes (Pfurtscheller & Lopes da Silva, 1999; Proix et al., 2022). However, because our aim was not to interpret specific increase or decrease with respect to the baseline, we here simply consider significant deviations from the baseline. In other words, when estimating selectivity, it is the strength of the response that matters, not its direction (activation, deactivation).”

“Both domains displayed a comparable percentage of selective responses across frequency bands (Figure 4, first values of each plot). When considering separately activation (Figure 2) and deactivation (Figure 3) responses, speech and music showed complementary patterns: for low frequencies (<15 Hz) speech selective (and preferred) responses were mostly deactivations and music responses activations compared to baseline, and this pattern reversed for high frequencies (>15 Hz).”

References :

J.P. Lachaux, J. Jung, N. Mainy, J.C. Dreher, O. Bertrand, M. Baciu, L. Minotti, D. Hoffmann, P. Kahane,Silence Is Golden: Transient Neural Deactivation in the Prefrontal Cortex during Attentive Reading, Cerebral Cortex, Volume 18, Issue 2, February 2008, Pages 443–450

Pfurtscheller, G., & Da Silva, F. L. (1999). Event-related EEG/MEG synchronization and desynchronization: basic principles. Clinical neurophysiology, 110(11), 1842-1857

(2) The manuscript doesn't easily provide information about the control conditions, yet the conclusion significantly depends on these conditions as a baseline. It would be beneficial if the authors could clarify this information for readers earlier and discuss how their choice of control stimuli influences their conclusions.

We added information in the Results section about the baseline conditions:

“[...] with respect to two baseline conditions, in which patients passively listened to more basic auditory stimuli: one in which patients passively listened to pure tones (each 30 ms in duration), the other in which patients passively listened to isolated syllables (/ba/ or /pa/, see Methods).”

Of note, while the choice of different ‘basic auditory stimuli’ as baseline can change the reported results in regions involved in low-level acoustical analyzes (auditory cortex), it will have no impact on the results observed in higher-level regions, which predominantly also exhibit shared responses. We have now more clearly pointed out this reasoning in the results section:

“The spatial distribution of the spectrally-resolved responses corresponds to the network typically involved in speech and music perception. This network encompasses both ventral and dorsal auditory pathways, extending well beyond the auditory cortex and, hence, beyond auditory processing that may result from differences in the acoustic properties of our baseline and experimental stimuli.“

(3) The spectral analyses section doesn't clearly explain how the authors performed multiwise correction. The authors' selectivity categorization appears similar to ANOVAs with posthoc tests, implying the need for certain corrections in the p values or categorization. Could the authors clarify this aspect?

We apologize that this was not in the original version of the manuscript. In the spectral analyzes, the selectivity categorization depended on both (1) the difference effects between the domains and the baseline, and (2) the difference effect between domains. Channels were marked as selective when there was (1) a significant difference between domains and (2) only one domain significantly differed from the baseline. All difference effects were estimated using the paired sample permutation tests based on the t-statistic from the mne-python library (Gramfort et al., 2014) with 1000 permutations and the build-in tmax method to correct for the multiple comparisons over channels (Nichols & Holmes, 2002; Groppe et al. 2011). We have now more clearly explained how we controlled family-wise error in the Methods section:

“For each frequency band and channel, the statistical difference between conditions was estimated with paired sample permutation tests based on the t-statistic from the mne-python library (Gramfort et al., 2014) with 1000 permutations and the tmax method to control the family-wise error rate (Nichols and Holmes 2002; Groppe et al. 2011). In tmax permutation testing, the null distribution is estimated by, for each channel (i.e. each comparison), swapping the condition labels (speech vs music or speech/music vs baseline) between epochs. After each permutation, the most extreme t-scores over channels (tmax) are selected for the null distribution. Finally, the t-scores of the observed data are computed and compared to the simulated tmax distribution, similar as in parametric hypothesis testing. Because with an increased number of comparisons, the chance of obtaining a large tmax (i.e. false discovery) also increases, the test automatically becomes more conservative when making more comparisons, as such correcting for the multiple comparison between channels.”

References :

Gramfort, A., Luessi, M., Larson, E., Engemann, D. A., Strohmeier, D., Brodbeck, C., Parkkonen, L., & Hämäläinen, M. S. (2014). MNE software for processing MEG and EEG data. NeuroImage, 86, 446–460.

Groppe, D. M., Bickel, S., Dykstra, A. R., Wang, X., Mégevand, P., Mercier, M. R., Lado, F. A., Mehta, A. D., & Honey, C. J. (2017). iELVis: An open source MATLAB toolbox for localizing and visualizing human intracranial electrode data. Journal of Neuroscience Methods, 281, 40–48.

Nichols, T. E., & Holmes, A. P. (2002). Nonparametric permutation tests for functional neuroimaging: a primer with examples. Human Brain Mapping, 15(1), 1–25.

Reviewer #2 (Recommendations For The Authors):

Other suggestions:

(1) The authors need to provide more details on how the sEEG electrodes were localized and selected. Are all electrodes included or only the ones located in the gray matter? If all electrodes were used, how to localize and label the ones that are outside of gray matter? In Figures 1C & 1D it seems that a lot of the electrodes were located in depth locations, how were the anatomical labels assigned for these electrodes

We apologize that this was not clear in the original version of the manuscript. Our electrode localization procedure was based on several steps described in detail in Mercier et al., 2022. Once electrodes were localized in a post-implant CT-scan and the coordinates projected onto the pre-implant MRI, we were able to obtain the necessary information regarding brain tissues and anatomical region. That is, first, the segmentation of the pre-impant MRI with SPM12 provided both the tissue probability maps (i.e. gray, white, and cerebrospinal fluid (csf) probabilities) and the indexed-binary representations (i.e., either gray, white, csf, bone, or soft tissues) that allowed us to dismiss electrodes outside of the brain and select those in the gray matter. Second, the individual's brain was co-registered to a template brain, which allowed us to back project atlas parcels onto individual’s brain and assign anatomical labels to each electrode. The result of this procedure allowed us to group channels by anatomical parcels as defined by the Brainnetome atlas (Figure 1D), which informed the analyses presented in section Population Prevalence (Methods, Figures 4, 9-10, S4-5). Because this study relies on stereotactic EEG, and not Electro-Cortico-Graphy, recording sites include both gyri and sulci, while depth structures were not retained.

We have now updated the “General preprocessing related to electrodes localisation” section in the Methods. The relevant part now states:

“To precisely localize the channels, a procedure similar to the one used in the iELVis toolbox and in the fieldtrip toolbox was applied (Groppe et al., 2017; Stolk et al., 2018). First, we manually identified the location of each channel centroid on the post-implant CT scan using the Gardel software (Medina Villalon et al., 2018). Second, we performed volumetric segmentation and cortical reconstruction on the pre-implant MRI with the Freesurfer image analysis suite (documented and freely available for download online http://surfer.nmr.mgh.harvard.edu/). This segmentation of the pre-implant MRI with SPM12 provides us with both the tissue probability maps (i.e. gray, white, and cerebrospinal fluid (CSF) probabilities) and the indexed-binary representations (i.e., either gray, white, CSF, bone, or soft tissues). This information allowed us to reject electrodes not located in the brain. Third, the post-implant CT scan was coregistered to the pre-implant MRI via a rigid affine transformation and the pre-implant MRI was registered to MNI152 space, via a linear and a non-linear transformation from SPM12 methods (Penny et al., 2011), through the FieldTrip toolbox (Oostenveld et al., 2011). Fourth, applying the corresponding transformations, we mapped channel locations to the pre-implant MRI brain that was labeled using the volume-based Human Brainnetome Atlas (Fan et al., 2016).”

Reference:

Mercier, M. R., Dubarry, A.-S., Tadel, F., Avanzini, P., Axmacher, N., Cellier, D., Vecchio, M. D., Hamilton, L. S., Hermes, D., Kahana, M. J., Knight, R. T., Llorens, A., Megevand, P., Melloni, L., Miller, K. J., Piai, V., Puce, A., Ramsey, N. F., Schwiedrzik, C. M., … Oostenveld, R. (2022). Advances in human intracranial electroencephalography research, guidelines and good practices. NeuroImage, 260, 119438.

(2) From Figures 5 and 6 (and also S4, S5), is it true that aside from the shared response, lower frequency bands show more music selectivity (blue dots), while higher frequency bands show more speech selectivity (red dots)? I am curious how the authors interpret this.

The reviewer is right in noticing the asymmetric selective response to music and speech in lower and higher frequency bands. However, while this effect is apparent in the analyzes wherein we inspected stronger synchronization (activation) compared to baseline (Figures 2 and S1), the pattern appears to reverse when examining deactivation compared to baseline (Figures 3 and S2). In other words, there seems to be an overall stronger deactivation for speech in the lower frequency bands and a relatively stronger deactivation for music in the higher frequency bands.

We now provide additional details about the sign of selectivity between domains and frequencies in the Results section:

“Both domains displayed a comparable percentage of selective responses across frequency bands (Figure 4, first values of each plot). When considering separately activation (Figure 2) and deactivation (Figure 3) responses, speech and music showed complementary patterns: for low frequencies (<15 Hz) speech selective (and preferred) responses were mostly deactivations and music responses activations compared to baseline, and this pattern reversed for high frequencies (>15 Hz).”

Note, however, that this pattern of results depends on only a select number of patients, i.e. when ignoring regional selective responses that are driven by as few as 2 to 4 patients, the pattern disappears (Figures 5-6). More precisely, ignoring regions explored by a small number of patients almost completely clears the selective responses for both speech and music. For this reason, we do not feel confident interpreting the possible asymmetry in low vs high frequency bands differently encoding (activation or deactivation) speech and music.

Minor:

(1) P9 L234: Why only consider whether these channels were unresponsive to the other domain in the other frequency bands? What about the responsiveness to the target domain?

We thank the reviewer for their interesting suggestion. The primary objective of the cross-frequency analyzes was to determine whether domain-selective channels for a given frequency band remain unresponsive (i.e. exclusive) to the other domain across frequency bands, or whether the observed selectivity is confined to specific frequency ranges (i.e.frequency-specific). In other words, does a given channel exclusively respond to one domain and never—in whichever frequency band—to the other domain? The idea behind this question is that, for a channel to be selectively involved in the encoding of one domain, it does not necessarily need to be sensitive to all timescales underlying that domain as long as it remains unresponsive to any timescale in the other domain. However, if the channel is sensitive to information that unfolds slowly in one domain and faster in the other domain, then the channel is no longer globally domain selective, but the selectivity is frequency-specific to each domain.

The proposed analyzes answer a slightly different, albeit also meaningful, question: how many frequencies (or frequency bands) do selective responses span? From the results presented below, the reviewer can appreciate the overall steep decline in selective response beyond the single frequency band with only few channels remaining selectively responsive across maximally four frequency bands. That is, selective responses globally span one frequency band.

Author response image 1.

Cross-frequency channel selective responses. The top figure shows the results for the spectral analyzes (baselined against the tones condition, including both activation and deactivation). The bottom figure shows the results for the connectivity analyzes. For each plot, the first (leftmost) value corresponds to the percentage (%) of channels displaying a selective response in a specific frequency band. In the next value, we remove the channels that no longer respond selectively to the target domain for the following frequency band. The black dots at the bottom of the graph indicate which frequency bands were successively included in the analysis.

(2) P21 L623: "Population prevalence." The subsection title should be in bold.

Done.

Reviewer #3 (Recommendations For The Authors):

The authors chose to use pure tone and syllables as baseline, I wonder if they also tried the rest period between tasks and if they could comment on how it differed and why they chose pure tones, (above and beyond a more active auditory baseline).

This is an interesting suggestion. The reason for not using the baseline between speech and music listening (or right after) is that it will be strongly influenced by the previous stimulus. Indeed, after listening to the story it is likely that patients keep thinking about the story for a while. Similarly after listening to some music, the music remains in “our head” for some time.

This is why we did not use rest but other auditory stimulation paradigms. Concerning the choice of pure tones and syllables, these happen to be used for clinical purposes to assess functioning of auditory regions. They also corresponded to a passive listening paradigm, simply with more basic auditory stimuli. We clarified this in the Results section:

“[...] with respect to two baseline conditions, in which patients passively listened to more basic auditory stimuli: one in which patients passively listened to pure tones (each 30 ms in duration), the other in which patients passively listened to isolated syllables (/ba/ or /pa/, see Methods).”

Discussion - you might want to address phase information in contrast to power. Your encoding models map onto low-frequency (bandpassed) activity which includes power and phase. However, the high-frequency model includes only power. The model comparison is not completely fair and may drive part of the effects in Figure 7a. I would recommend discussing this, or alternatively ruling out the effect with modeling power separately for the low frequency.

We thank the reviewer for their recommendation. First, we would like to emphasize that the chosen signal extraction techniques that we used are those most frequently reported in previous papers (e.g. Ding et al., 2012; Di Liberto et al., 2015; Mesgarani and Chang, 2012).

Low-frequency (LF) phase and high-frequency (HFa) amplitude are also known to track acoustic rhythms in the speech signal in a joint manner (Zion-Golumbic et al., 2013; Ding et al., 2016). This is possibly due to the fact that HFa amplitude and LF phase dynamics have a somewhat similar temporal structure (see Lakatos et al., 2005 ; Canolty and Knight, 2010).

Still, the reviewer is correct in pointing out the somewhat unfair model comparison and we appreciate the suggestion to rule out a potential confound. We now report in Supplementary Figure S8, a model comparison for LF amplitude vs. HFa amplitude to complement the findings displayed in Figure 7A. Overall, the reviewer can appreciate that using LF amplitude or phase does not change the results: LF (amplitude or phase) always better captures acoustic features than HFa amplitude.

Author response image 2.

TRF model comparison of low-frequency (LF) amplitude and high-frequency (HFa) amplitude. Models were investigated to quantify the encoding of the instantaneous envelope and the discrete acoustic onset edges (peakRate) by either the low frequency (LF) amplitude or the high frequency (HFa) amplitude. The ‘peakRate & LF amplitude’ model significantly captures the largest proportion of channels, and is, therefore, considered the winning model. Same conventions as in Figure 7A.

References:

Canolty, R. T., & Knight, R. T. (2010). The functional role of cross-frequency coupling. Trends in Cognitive Sciences, 14(11), 506–515.

Di Liberto, G. M., O’sullivan, J. A., & Lalor, E. C. (2015). Low-frequency cortical entrainment to speech reflects phoneme-level processing. Current Biology, 25(19), 2457-2465.

Ding, N., & Simon, J. Z. (2012). Emergence of neural encoding of auditory objects while listening to competing speakers. Proceedings of the National Academy of Sciences, 109(29), 11854-11859.

Ding, N., Melloni, L., Zhang, H., Tian, X., & Poeppel, D. (2016). Cortical tracking of hierarchical linguistic structures in connected speech. Nature Neuroscience, 19(1), 158–164.

Golumbic, E. M. Z., Ding, N., Bickel, S., Lakatos, P., Schevon, C. A., McKhann, G. M., ... & Schroeder, C. E. (2013). Mechanisms underlying selective neuronal tracking of attended speech at a “cocktail party”. Neuron, 77(5), 980-991.

Lakatos, P., Shah, A. S., Knuth, K. H., Ulbert, I., Karmos, G., & Schroeder, C. E. (2005). An oscillatory hierarchy controlling neuronal excitability and stimulus processing in the auditory cortex. Journal of Neurophysiology, 94(3), 1904–1911.

Mesgarani, N., & Chang, E. F. (2012). Selective cortical representation of attended speaker in multi-talker speech perception. Nature, 485(7397), 233-236.

Similarly, the Coherence analysis is affected by both power and phase and is not dissociated. i.e. if the authors wished they could repeat the coherence analysis with phase coherence (normalizing by the amplitude). Alternatively, this issue could be addressed in the discussion above

We agree with the Reviewer. We have now better clarified our choice in the Methods section:

“Our rationale to use coherence as functional connectivity metric was three fold. First, coherence analysis considers both magnitude and phase information. While the absence of dissociation can be criticized, signals with higher amplitude and/or SNR lead to better time-frequency estimates (which is not the case with a metric that would focus on phase only and therefore would be more likely to include estimates of various SNR). Second, we choose a metric that allows direct comparison between frequencies. As, at high frequencies phase angle changes more quickly, phase alignment/synchronization is less likely in comparison with lower frequencies. Third, we intend to align to previous work which, for the most part, used the measure of coherence most likely for the reasons explained above.“

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):

Summary:

This valuable study by Wu and Zhou combined neurophysiological recordings and computational modelling to investigate the neural mechanisms that underpin the interaction between sensory evaluation and action selection. The neurophysiological results suggest non-linear modulation of decision-related LIP activity by action selection, but some further analysis would be helpful in order to understand whether these results can be generalised to LIP circuitry or might be dependent on specific spatial task configurations. The authors present solid computational evidence that this might be due to projections from choice target representations. These results are of interest for neuroscientists investigating decision-making.

Strengths:

Wu and Zhou combine awake behaving neurophysiology for a sophisticated, flexible visual-motion discrimination task and a recurrent network model to disentangle the contribution of sensory evaluation and action selection to LIP firing patterns. The correct saccade response direction for preferred motion direction choices is randomly interleaved between contralateral and ipsilateral response targets, which allows the dissociation of perceptual choice from saccade direction.

The neurophysiological recordings from area LIP indicate non-linear interaction between motion categorisation decisions and saccade choice direction.

The careful investigation of a recurrent network model suggests that feedback from choice target representations to an earlier sensory evaluation stage might be the source for this non-linear modulation and that it is an important circuit component for behavioural performance.

The paper presents a possible solution to a central controversy about the role of LIP in perceptual decision-making, but see below.

Weaknesses:

The paper presents a possible solution to a central controversy about the role of LIP in perceptual decision-making. However, the authors could be more clear and upfront about their interpretational framework and potential alternative interpretations.

Centrally, the authors' model and experimental data appears to test only that LIP carries out sensory evaluation in its RFs. The model explicitly parks the representation of choice targets outside the "LIP" module receiving sensory input. The feedback from this separate target representation provides then the non-linear modulation that matches the neurophysiology. However, they ignore the neurophysiological results that LIP neurons can also represent motor planning to a saccade target.

The neurophysiological results with a modulation of the direction tuning by choice direction (contralateral vs ipsilateral) are intriguing. However, the evaluation of the neurophysiological results are difficult, because some of the necessary information is missing to exclude alternative explanations. It would be good to see the actual distributions and sizes of the RF, which were determined based on visual responses not with a delayed saccade task. There might be for example a simple spatial configuration, for example, RF and preferred choice target in the same (contralateral) hemifield, for which there is an increase in firing. It is a shame that we do not see what these neurons would do if only a choice target would be put in the RF, as has been done in so many previous LIP experiments. The authors exclude also some spatial task configurations (vertical direction decisions), which makes it difficult to judge whether these data and models can be generalised. The whole section is difficult to follow, partly also because it appears to mix reporting results with interpretation (e.g. "feedback").

The model and its investigation is very interesting and thorough, but given the neurophysiological literature on LIP, it is not clear that the target module would need to be in a separate brain area, but could be local circuitry within LIP between different neuron types.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors recorded activity in the posterior parietal cortex (PPC) of monkeys performing a perceptual decision-making task. The monkeys were first shown two choice dots of two different colors. Then, they saw a random dot motion stimulus. They had to learn to categorize the direction of motion as referring to either the right or left dot. However, the rule was based on the color of the dot and not its location. So, the red dot could either be to the right or left, but the rule itself remained the same. It is known from past work that PPC neurons would code the learned categorization. Here, the authors showed that the categorization signal depended on whether the executed saccade was in the same hemifield as the recorded PPC neuron or in the opposite one. That is, if a neuron categorized the two motion directions such that it responded stronger for one than the other, then this differential motion direction coding effect was amplified if the subsequent choice saccade was in the same hemifield. The authors then built a computational RNN to replicate the results and make further tests by simulated "lesions".

Strengths:

Linking the results to RNN simulations and simulated lesions.

Weaknesses:

Potential interpretational issues due to a lack of evidence on what happens at the time of the saccades.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The neurophysiological results with a modulation of the direction tuning by choice direction are intriguing. However, the evaluation of the neurophysiological results are difficult because some of the necessary information is missing to exclude alternative explanations.

We thank the reviewer for the helpful comments. We have addressed this point in detail in the following response.

(a) Clearly state in the results how the response field "RF", where the stimulus was placed, was mapped. The methods give as "MGS"" (i.e., spatial selectivity during stimulus presentation and delay)" task rather than the standard delayed saccade. And also "while for those neurons which did not show a clear RF during the MGS task, we presented motion stimuli in the positions (always in the visual field contralateral to the recorded hemisphere) in which neurons exhibited the strongest response to the motion stimuli." All this sounds more like a sensory receptive field not an eye movement response filed". What was the exact task and criterion?

We agree with the reviewer that the original description of how we mapped the response fields (RFs) of LIP neurons lacked sufficient detail. In this study, we used the memory-guided saccade (MGS) task to map the RFs of all isolated LIP neurons. Both MGS and delayed saccade tasks are commonly used to map a neuron's response field in previous decision-making studies.

In the MGS task, monkeys initially fixate on the center of the screen. Subsequently, a dot randomly flashes at one of the eight possible locations surrounding the fixation dot with an eccentricity of 8 degree, requiring the monkeys to memorize the location of the flashed dot. After a delay of 1000 ms, the monkeys are instructed to saccade to the remembered location once the fixation dot disappears. The MGS task is a standard behavior task for mapping visual, memory, and motor RFs, particularly in brain regions involved in eye movement planning and control, such as LIP, FEF, and the superior colliculus.

We believe the reviewer's confusion may stem from whether we mapped the visual, memory, or motor RFs of LIP neurons in the current study, as these "RFs" are not always consistent across individual neurons. In our study, we primarily mapped the visual and memory RFs of each LIP neuron by analyzing their activity during both the target presentation and delay periods. To focus on sensory evaluation-related activity, we presented the visual motion stimulus within the visual-memory RF of each neuron. For neurons that did not show a significant visual-memory RF, we used a different approach: we tested the neurons with the main task by altering the spatial configuration of the task stimuli to identify the visual field that elicited the strongest response when the motion stimulus was presented within it. This approach was used to guide the placement of the stimulus during the recording sessions.

Following the reviewer’s suggestion, we have added the following clarification to the results section to better describe how we mapped the RF of LIP neurons:

‘We used the memory-guided saccade (MGS) task, which is commonly employed in LIP studies, to map the receptive fields (RFs) of all isolated LIP neurons. Specifically, we mapped both the visual and memory RFs of each neuron by analyzing their activity during the target presentation and delay periods of the MGS task (see Methods).’.

(b) l.85 / l126: What do you mean by "orthogonal to the axis of the neural RF" - was the RF shape asymmetric, if so how did you determine this? OR do you mean the motion direction axis? Please explain.

We realized that the original description of this point may have been unclear and could lead to confusion. The axis of the neural RF refers to the line connecting the center of the RF (which coincides with the center of the motion stimulus) to the fixation dot. We have revised this sentence in the revised manuscript as follows:

‘To examine the neural activity related to the evaluation of stimulus motion, we presented the motion stimuli within the RF of each neuron, while positioning the saccade targets at locations orthogonal to the line connecting the center of the RF (which also marks the center of the motion stimulus) and the fixation dot.’

(c) Behavioural task. Figure 1 - are these example session? Please state this clearly. Can you show the examples (psychometric function and reaction times) separated for trials where correct choice direction aligning with the motion preference (within 90 degrees) and those that did not?

Figure 1 shows the averaged behavioral results from all recording sessions. We have added this detail in the revised legend of Figure 1.

We are uncertain about the reviewer’s reference to the “correct choice direction aligning with the motion preference,” as the term “motion preference” is specific to the neuron response, which are different for different neurons recorded simultaneously using multichannel recording probe.

Nonetheless, following the reviewer’s suggestion, we grouped the trials in each recording session into two groups based on the relationship between the saccade direction and the preferred motion direction of the identified LIP neuron during one example single-channel recording. Both the RT and the performance accuracy during one example session were shown in the following figure.

Author response image 1.

Give also the performance averaged across all sites included in this study and range.<br /> If performance does differ for different configuration, please, show that the main modulatory effect does not align with this distinction.

To clarify this point, we have plotted performance accuracy and RTs for horizontal, oblique, and vertical target position configurations separately, which are shown for both monkeys in the following figures. We did not observe any systematic influences of task configurations on the monkeys' performance accuracy. While the RTs did differ across different configurations, we believe these differences are likely attributable to several factors, such as varying levels of familiarity introduced by our training process and the intrinsic RT difference between different saccade directions.

Author response image 2.

(d) Show the distribution of RF positions and the direction preferences for the recording sites included in the quantitative analysis of this study. (And if available, separately those excluded).

Following the reviewer’s suggestion, we have plotted the centers of the RFs for all neurons with identifiable RFs, categorizing them by their preferred motion directions. To determine each neuron’s RF, we analyzed the average firing rates from both the target presentation and delay periods during each trial of the memory-guided saccade (MGS) task. The RF centers of neurons with significant RFs were determined through a two-step process. First, we selected neurons that exhibited significant RFs in the MGS based on the following criteria: 1) there must be a significant activity difference between the eight target locations, and 2) the mean activity during the selected periods should be significantly greater than the baseline activity during the fixation period. Second, we fitted the activity data from the eight conditions to a Gaussian distribution, using the center of the fitted distribution as the RF center. A significant proportion of neurons from both monkeys that exhibited significant response to motion stimuli did not exhibited notable RFs based our current method. The following figures show the distributions of RFs and motion direction preference for all LIP neurons with identifiable RFs separately for each monkey. Since this is not the focus of the current study, we are not planning to include this result in the revised manuscript.

Author response image 3.

(e) Following on from d), was there a systematic relationship between RF position or direction preference and modulation by choice direction? For instance could the responses be simply explained by an increase in modulation for choices into the same (contralateral) hemifield as where the stimulus was placed?

The reviewer raised a good point. To address whether there was a systematic relationship between RF position or direction preference and modulation by choice direction, we calculated a modulation index for each neuron to quantify the influence of saccade direction on neuronal responses to motion stimuli. We then plotted the modulation index against the RF position for each LIP neuron, shown as following:

Author response image 4.

As shown in the figures above, neurons with RFs farther from the horizontal meridian were more likely to exhibit stronger modulation by the saccade direction, while neurons with RFs closer to the horizontal meridian showed inconsistent and weaker modulation. This is because when the RFs was on the horizontal meridian, saccade directions were aligned with the vertical axis (with no contralateral or ipsilateral directions). This is consistent with the finding in Figure S3—no significant differences in direction selectivity between the CT and IT conditions in the data sessions where the saccade targets were aligned close to the vertical direction. Since fewer than half of the identified neurons showed clear receptive fields using our method, the figure above did not include all the neurons used in the analysis in the manuscript. Therefore, we chose not to include this figure in the revised manuscript.

Additionally, we quantified the relationship between the modulation index and direction preference for neurons in sessions where the monkeys’ saccades were aligned to either horizontal or oblique directions. As shown in the following figure, no systematic relationship was found between direction preference and modulation by the choice direction for LIP neurons at the population level.

Author response image 5.

We have added this result as Figure S 2 in the revised manuscript.

Notably, the observed modulation of saccade direction on LIP neurons’ response to motion stimuli cannot be simply explained by saccade direction selectivity. We presented two more evidence to rule out such possibility in the original manuscript. First, the modulation effect we observed was nonlinear; specifically, the firing rate of neurons increased for the preferred motion direction but decreased for the non-preferred motion direction (Figure 2i and Figure S1A-D). This phenomenon is unlikely to be attributed to a linear gain modulation driven by saccade directions. Second, we plotted the averaged neural activity for contralateral and ipsilateral saccade directions separately, and found that LIP neurons showed similar levels of activity between two saccade directions (revised Figure 2L).

Additionally, we added a paragraph in the Methods section to describe the way we calculated modulation index as follows:

“We have calculated a modulation index for each neuron to reflect the influence of saccade direction on neuron’s response to visual stimuli. The modulation index is calculated as:

where represents the average firing rate from 50ms to 250ms after sample onset for all contralateral saccade trails with a neuron’s preferred moving direction of visual stimuli. The naming conventions are the same for , , and . An MI value between 0 and 1 indicate higher modulation in contralateral saccade trials, and an MI value between -1 and 0 indicates higher modulation in ipsilateral saccade trials.”

Please split Figures 2G,H,I J,K, by whether the RF was located contralaterally or ipsilaterally. If there are only a small number of ipsilateral RFs, please show these examples, perhaps in an appendix.

This is a reasonable suggestion; however, it is not applicable to our study. Among all the neurons included in our analysis, only one neuron from each monkey exhibited ipsilateral receptive fields (RFs). Therefore, we believe it may not be necessary to plot the result for this outlier.

(f) Were the choice targets always equi-distant from the stimulus and at what distance was this? Please give quantitative details in methods.

The review was correct that the choice targets were always equidistant form the stimulus. The distance between the motion stimulus and the target was typically 12-15 degree. We have added the details in the revised Methods section as follows:

‘Therefore, the two saccade targets were equidistant from the stimulus, with the distance typically ranging from 12 to 15 degrees.

(2) For Figure 3E, how do you explain that there is an up regulation of for contralateral choices before the stimulus onset, i.e. before the animal can make a decision? Is this difference larger for error trials?

This is a good question, which we have attempted to clarify in the revised manuscript. We believe that the observed upregulation in neural activity for contralateral choices may reflect the monkeys’ internal choice bias or expectation (choice between two motion directions) prior to stimulus presentation, which could influence their subsequent decisions. In Figure 3E, we calculated the r-choice to assess the correlation between the neuron’s direction selectivity and the monkeys’ decisions on motion stimuli, separately for contralateral and ipsilateral choice conditions. The increased r-decision during the pre-stimulus period indicates stronger neural activity for trials in which the monkeys later reported that the upcoming stimulus was in the preferred direction, and weaker activity for trials where the stimulus was judged to be in the non-preferred direction. This correlation was more pronounced for contralateral choices than for ipsilateral ones. It is important to note that while the monkeys cannot predict the upcoming stimulus direction with greater-than-chance accuracy, these results suggest that pre-stimulus neural activity in LIP is correlated with the monkeys’ eventual decision for that trial. Furthermore, LIP neural activity was more strongly correlated with the monkeys’ decisions in the contralateral choice condition compared to the ipsilateral one.

Additionally, we clarify that the r-decision was calculated using both correct and error trials. When comparing Figure 2J with Figure 2K, the correlation between neural activity and the monkeys’ upcoming decision during the pre-stimulus period was most prominent in low- and zero-coherence trials, where the monkeys either made more errors or based decisions on guesswork. We infer that the monkeys' confidence in these decisions was likely lower compared to high-coherence trials. Thus, the decision process appears to be influenced by pre-stimulus neural activity, particularly in low-coherence and zero-coherence trials.

Although it is unclear precisely what covert process this pre-stimulus activity reflects, similar patterns of choice-predictive pre-stimulus activity have been observed in LIP and other brain areas (Shadlen, M.N. and Newsome,T.W., 2001; Coe, B., at al. 2002; Baso, M.A. and Wurtz, R.H., 1998; Z. M. Williams at al. 2003). We have clarified this point in the revised manuscript, including a revision of the relevant sentence in the Results section for clarity, shown as follows:

“Furthermore, we used partial correlation analysis to examine decision- and stimulus-related components of DS (i.e., r-decision and r-stimulus, Figure 3E and 3F) using all four coherence levels. The decision-related component of LIP DS was significantly greater in the CT condition than in the IT condition (Figure 3E; nested ANOVA: P = 1.07e-6, F= 25.72), and this difference emerged even before motion stimulus onset. This suggests that the LIP DS was more closely correlated with monkeys’ decisions in the CT condition than in the IT condition. The upregulation in r-decision for contralateral choices may reflect the monkeys’ internal choice bias or expectation (choice between two motion directions) prior to stimulus presentation, which could influence their subsequent decisions more in the CT condition”

(3) Figure 2K: what is the very large condition-independent contribution? It almost seems as most of what these neurons code for is neither saccade or motion related.

The condition-independent contribution is the time-dependent component that is unrelated to saccade, motion, or their interaction. Our findings are consistent with previous methodological studies, where this time-dependent component was shown to account for a significant portion of the variance in population activity (Kobak, D. et al., 2016)

(4) Abstract:

a) "We found that the PPC activity related to monkeys' abstract decisions about visual stimuli was nonlinearly modulated by monkeys' following saccade choices directing outside each neuron's response field."

This sentence is not clear/precise in two regards:

Should "directing" be "directed"?

Also, it is not just saccades directed outside the RF, but towards the contralateral hemifield.

We thank the reviewer for the suggestion. We agree that ‘directing’ should be ‘directed’ and revised it accordingly. However, we do not believe that ‘directed outside each neuron's response field’ should be replaced with “towards the contralateral hemifield”. There are two major reasons. First, the modulation effect was identified as the difference between contralateral and ipsilateral saccade directions. We cannot conclude that the modulation mainly happened in the contralateral saccade direction. Second, we used ‘directed outside each neuron's response field’ to emphasize that this modulation cannot be simply explained by saccade direction selectivity, whereas ‘towards the contralateral hemifield’ cannot fulfill this purpose.

(b) " Recurrent neural network modeling indicated that the feedback connections, matching the learned stimuli-response associations during the task, mediated such feedback modulation."

- should be "that feedback connection .... might mediate". A model can only ever give a possible explanation.

Thanks for the help on the writing again! We have revised this sentence as following: “Recurrent neural network modeling indicated that the feedback connections, matching the learned stimuli-response associations during the task, might mediate such feedback modulation.”

(c) "thereby increasing the consistency of flexible decisions." I am not sure what is really meant by increasing the consistency of flexible decisions? More correct or more the same?

We apologize for the confusion. In the manuscript, "decision consistency" refers to the degree of agreement in the model's decisions under specific conditions. A higher decision consistency indicates that the model is more likely to produce the same choice when encountering encounters a stimulus in that condition. We have incorporated your suggestion and revise this sentence as “thereby increasing the reliability of flexible decisions”. We also clarified the definition of consistency in the main text as follows:

“These disrupted patterns of saccade DS observed in the target module following projection-specific inactivation aligned with the decreased decision consistency of RNNs, where decision consistency reflects the degree of agreement in the model's choices under specific task conditions. This suggests a diminished reliance on sensory input and an increased dependence on internal noise in the decision-making process.”.

(5) Results: headers should be changed to reflect the actual results, not the interpretation:

"Nonlinear feedback modulation of saccade choice on visual motion selectivity in LIP"

"Feedback modulation specifically impacted the decision-correlated activity in LIP"

These first parts of the results describe neurophysiological modulations of LIP activity, the source cannot be known from the presented data alone. I thought that this feedback is suggested by the modelling results in the last part of the results. It is confusing to the reader that the titles already refer to the source of the modulation as "feedback". The titles should more accurelty describe what is found, not pre-judge the interpretation.

We thank the reviewer for those valuable suggestions. We have updated the subtitles to: “Nonlinear modulation of saccade choice on visual motion selectivity in LIP” and “Decision-correlated but not stimulus-correlated activity was modulated in LIP.”

(6) page 8, l366-380. Can you link the statements more directly to panels in Figure 6. For Figure 6H-K, it needs to be clarified that the headers for 6D-G also apply to H-K.

­We have added headers for Figure 6H-K in the revised version, and revised the corresponding results section as follows.

‘We further examined how the energy landscape in the 1-D subspace changed in relation to task difficulty (motion coherence). Consistent with prior findings, trials with lower decision consistency (trials using lower motion coherence) exhibited shallower attractor basins at the time of decision for all types of RNNs (Fig. 6H-K). However, both the depth and the positional separation of attractor basins in the network dynamics significantly decreased for all non-zero motion coherence levels after the ablation of all feedback connections (comparing Figure 6I with Figure 6H; P(depth) = 5.20e-25, F = 122.80; P(position) = 1.82e-27, F = 137.75; two-way ANOVA). Notably, this reduction in basin depth and separation was more pronounced in the specific group compared to the nonspecific groups after ablating the feedback connections (comparing Figure 6J with Figure 6K; P(depth) = 2.65e-13, F =57.35; P(position) = 3.73e-14, F = 61.79; two-way ANOVA). These results might underlie the computational mechanisms that explain the observed reduction in the decision consistency of RNNs following projection-specific inactivation: the shallower and closer attractor basins after ablating feedback connections resulted in less consistent decisions. This happened because the variability in neural activity made it more likely for population activity to stochastically shift out of the shallower basins and into nearby alternative ones.’

(7) line 556-557: Please provide a reference or data for the assertion that nearby recording sites in LIP (100 microns apart) have similar RFs.

The reviewer raised an interesting question that we are unable to address in depth with the current data, as we lack information on the specific cortical location for each recording session. In the original manuscript, we suggested that nearby recording sites in LIP have similar receptive fields (RFs), based on both our own experience with LIP recordings and previous studies. Specifically, we observed that neurons recorded within a single penetration using a single-channel electrode typically exhibited similar RFs. Similarly, the majority of neurons recorded from the same multichannel linear probe within a single session also showed comparable RFs. Additionally, several studies (both electrophysiological and fMRI) have reported topographic organization of RFs in LIP (Gaurav H. Patel et al., 2010; S. Ben Hamed et al., 2001; Gene J. Blatt et al., 1990).

(8) Line 568, Methods: a response criterion of a maximum firing rate of 2 spikes/s seems very low, especially for LIP. How do the results change if this lifted to something more realistic like 5 spikes/s or 10 spikes/s?

We chose this criterion to ensure we included as many neurons as possible in our analysis. To further clarify, we have plotted the distribution of maximum firing rates across all neurons. Based on our findings, relaxing this criterion is unlikely to affect the results, as the majority of neurons exhibit maximum firing rates well above 5 spikes/s, and many exceed 10 spikes/s. We hope this explanation addresses the concern.

Author response image 6.

Reviewer #2 (Recommendations For The Authors):

In this manuscript, the authors recorded activity in the posterior parietal cortex (PPC) of monkeys performing a perceptual decision-making task. The monkeys were first shown two choice dots of two different colors. Then, they saw a random dot motion stimulus. They had to learn to categorize the direction of motion as referring to either the right or left dot. However, the rule was based on the color of the dot and not its location. So, the red dot could either be to the right or left, but the rule itself remained the same. It is known from past work that PPC neurons would code the learned categorization. Here, the authors showed that the categorization signal depended on whether the executed saccade was in the same hemifield as the recorded PPC neuron or in the opposite one. That is, if a neuron categorized the two motion directions such that it responded stronger for one than the other, then this differential motion direction coding effect was amplified if the subsequent choice saccade was in the same hemifield. The authors then built a computational RNN to replicate the results and make further tests by simulated "lesions".

The data are generally interesting, and the manuscript is generally well written (but see some specific comments below on where I was confused). However, I'm still not sure about the conclusions. The way the experiment is setup, the "contra" saccade target is essentially in the same hemifield as the motion patch stimulus. Given that the RF's can be quite large, isn't it important to try to check whether the saccade itself contributed to the effects? i.e. if the RF is on the left side, and the "contra" saccade is to the left, then even if it is orthogonal to the location of the stimulus motion patch itself, couldn't the saccade still be part of a residual edge of the RF? This could potentially contribute to elevating the firing rate on the preferred motion direction trials. I think it would help to align the data on saccade onset to see what happens. It would also help to have fully mapped the neurons' movement fields by asking the monkeys to generate saccades to all screen locations in the monitor. The authors mention briefly that they used a memory-guided saccade task to map RF's, but it is also important to map with a visual target. And, in any case, it would be important to show the mapping results aligned on saccade onset.

Another comment is that the authors might want to mention this other recent related paper by the Pack group: https://www.biorxiv.org/content/10.1101/2023.08.03.551852v2.full.pdf

We thank the reviewer for the comments and realized that we did not explain our results clearly in the original manuscript. We agree with the reviewer that saccade direction selectivity might be a confounding factor for the modulation of the saccade choice direction onto LIP neurons’ activity responded to visual motion stimuli. Because the RFs of LIP neurons might be large and the saccade target might be presented within the edge of the RFs. However, we believe that the observed modulation of saccade direction on LIP neurons’ response to motion stimuli cannot be simply explained by saccade direction selectivity. We presented several pieces of evidence to rule out such possibility. First, the modulation effect we observed was not linear; specifically, the firing rate of neurons increased for the preferred motion direction but decreased for the non-preferred motion direction (Figure 2i and Figure S1A-D). This phenomenon is unlikely to be attributed to a linear gain modulation driven by saccade directions. Second, we plotted the averaged neural activity for contralateral and ipsilateral saccade directions separately, aligned the activity to either motion stimulus onset or saccade onset, and found that LIP neurons showed similar levels of activity between the contralateral and ipsilateral directions (revised Figure 2L), which is not consistent with obvious saccade direction selectivity.

To better control for this confound, we have added figures plotting the mean neural activity aligned to saccade onset for both contralateral and ipsilateral saccades, which are now included in the revised main Figure 2. These figures are presented in the detailed response below. Additionally, we have revised the corresponding results section to clarify our points, as outlined below:

“Figure 2A-2F shows three example LIP neurons that exhibited significant motion coherence correlated DS. Surprisingly, LIP neurons showed greater DS in the CT condition than in the IT condition, even though the same motion stimuli were used in the same spatial location for both conditions. The averaged population activity showed this DS difference between CT and IT conditions for all four coherence levels (Figure 2G, 2H). During presentation of their preferred motion direction, LIP neurons showed significantly elevated activity in the CT relative to the IT at all coherence levels (Figure S1A, S1B, nested ANOVA: P(high) = 0.0326, F = 4.65; P(medium) = 0.0088, 142 F = 7.03; P(low) = 0.0076, F = 7.32; P(zero) = 0.0124, F = 6.4), and a trend toward lower activity to the nonpreferred direction for CT vs. IT (Figure S1C, S1D, nested ANOVA: P(high) = 0.0994, F = 2.75; P(medium) = 0.0649, F = 3.12; P(low) = 0.0311, F = 4.73; P(zero) = 0.0273, F = 4.96). Most of the LIP neurons (48 of 83) showed such opposing trends in activity modulation between the preferred and nonpreferred directions (Figure 2I). These results indicated a nonlinear modulation of saccade choice on motion DS in LIP, aligned precisely with the response property of each neuron. This is unlikely to be driven by a linear gain modulation of saccade direction selectivity. Receiver operating characteristic (ROC) analysis further confirmed significantly greater motion DS in the CT condition than in the IT condition (Figure 2J 148 and 2K; nested ANOVA: P(high) = 5.0e-4, F= 12.44; P(medium) = 9.53e-6, F = 20.91; P(low) = 9.33e-7, F 149 = 26.03; P(zero) = 2.56e-8, F= 34.3). Such DS differences were observed even before stimulus onset. Moreover, LIP neurons exhibited similar levels of mean activity between different saccade directions (CT vs. IT) before monkeys’ saccade choice (Figure 2L), further supporting that saccade direction selectivity did not significantly contribute to the observed modulation of LIP neurons’ responses to motion stimuli.

We also thank the reviewer for pointing out the missing of this relevant study, we have added the suggested refence in the revised discussion section as follows:

‘A recent study demonstrated that neurons in the middle temporal area responded more strongly to motion stimuli when monkeys saccaded toward their RFs in a standard decision task with a fixed mapping between motion stimuli and saccade directions. This modulation emerged through the training process and contributed causally to the monkeys' following saccade choices. Consistently, we found that the response of LIP neurons to motion stimuli was more strongly correlated with the monkeys' decisions in the CT condition (saccades toward RFs) than in the IT condition, in a more flexible decision task. Together, these results suggest that the modulation of action selection on sensory processing may be a general process in perceptual decision-making. However, the observed modulation of saccade direction on LIP neurons' responses to motion stimuli cannot be simply explained by saccade direction selectivity. Several lines of evidence argue against this possibility. First, the modulation effect was nonlinear; specifically, neuronal firing rates increased for preferred motion directions but decreased for non-preferred directions (Figure 2I and Figure S1). This pattern is unlikely to be driven by a linear gain modulation based on saccade directions. Second, we found that LIP neurons exhibited similar levels of activity in both the CT and IT conditions (Figure 2L), which is inconsistent with the presence of clear saccade direction selectivity.

Some more specific comments are below:

- I had a bit of a hard time with the abstract. It does not appear to be crystal clear to me, and it is the first thing that I am reading after the title. For example, if there is a claim about both perceptual decision-making and later target selection, then I feel that the task should be explained a bit more clearly than saying "flexible decision" task. Also, "..modulated by monkeys' following saccade choices directing outside each neuron's response field" was hard to read. It needs to be rewritten. Maybe just say "...modulated by the subsequent eye movement choices, even when these eye movement choices always directed the eyes away from the recorded neuron's response field". Also, I don't fully understand what "selectivity-specific feedback" means. Then, the concept of "consistency" in flexible decisions is brought up, again without much context. The above are examples of why I had a hard time with the abstract.

We realize that our original statement may have been unclear and potentially caused confusion for the readers. Following the reviewer’s suggestions, we have revised the abstract as follows:

‘Neural activity in the primate brain correlates with both sensory evaluation and action selection aspects of decision-making. However, the intricate interaction between these distinct neural processes and their impact on decision behaviors remains unexplored. Here, we examined the interplay of these decision processes in posterior parietal cortex (PPC) when monkeys performed a flexible decision task, in which they chose between two color targets based on a visual motion stimulus. We found that the PPC activity related to monkeys’ abstract decisions about visual stimuli was nonlinearly modulated by their subsequent saccade choices, which were directed outside each neuron’s response field. Recurrent neural network modeling indicated that the feedback connections, matching the learned stimuli-response associations during the task, might mediate such feedback modulation. Further analysis on network dynamics revealed that selectivity-specific feedback connectivity intensified the attractor basins of population activity underlying saccade choices, thereby increasing the reliability of flexible decisions. These results highlight an iterative computation between different decision processes, mediated primarily by precise feedback connectivity, contributing to the optimization of flexible decision-making.’

Specifically, selectivity-specific feedback refers to the feedback connections with positive or negative weights between selectivity-matched and selectivity-nonmatched unit pairs, respectively.

Regarding "decision consistency," we define it as the degree to which the model’s decisions remain congruent under specific conditions. A higher level of decision consistency indicates that the model is more likely to produce the same choice each time it is presented with a stimulus under those conditions, in another words, decision reliability. We have revised the corresponding results section to make these concepts clearer.

- Line 69: I'm not fully sure, but I think that some people might suggest that superior colliculus is also involved in the sensory aspect of the evaluation. But, I guess the sentence itself is correct as you write it. So, I don't think anyone should argue with it. However, if someone does argue with it, then they would flag the next sentence, since if the colliculus does both, then do the sensory and motor parts really employ distinct neural processes? Anyway, I think this is very minor.

This is an interesting point. We have also noticed a recent study that demonstrates that the superior colliculus is causally involved in the sensory aspect of decision-making, specifically in visual categorization. However, the study also distinguishes between neural activity related to categorical decisions and that related to saccade planning. This suggests that the sensory and motor aspects of decision-making likely involve distinct neural processing, even within the same brain region—potentially reflecting separate populations of neurons. Therefore, we stand by our statement in the ‘next sentence’.

- Line 79-80: you might want to look at this work because I feel that it is relevant to cite here: https://www.biorxiv.org/content/10.1101/2023.08.03.551852v2

We have discussed this reference in the revised discussion section of the manuscript, please refer to the above response.

- For a result like that shown in Fig. 2, I feel that it is important to show RF mapping with a saccade task alone. i.e. for the same neurons, have a monkey make a delayed visually guided saccade task to all possible locations on the display, and demonstrate that there is no modulation by saccades to the targets. Otherwise, the result in Fig. 2 could reflect first an onset response by a motion, and then the saccade-related response that would happen anyway, even without the decision task. So, I feel that now, it is not entirely clear whether the result reflects this so-called feedback modulation, or whether simply planning the saccade to the target itself activates the neurons. With large RF's, this is a distinct possibility in my opinion.

- Line 174: this would also be predicted if the neuron's were responding based on the saccade target plan independent of the motion stimulus

- On a related note, I would recommend plotting all data also aligned on saccade onset. This can help establish what the cause of the effects described is

We understand the reviewer’s concern that the modulation might be related to saccade planning, and we acknowledge that the original manuscript might not adequately address this potential confound. Unfortunately, we did not map the LIP neurons' receptive fields (RFs) using a saccade-only task. However, as mentioned earlier, we believe that the modulation of LIP neurons' responses to motion stimuli based on saccade choice direction cannot be simply attributed to saccade direction selectivity. Several lines of evidence support this conclusion. First, the modulation we observed was nonlinear: the firing rate of neurons increased for the preferred motion direction but decreased for the non-preferred motion direction (Figure 2i and Figure S1A-D). This pattern is inconsistent with a simple linear gain modulation driven by saccade direction selectivity. Second, we directly compared LIP neuronal activity for contralateral and ipsilateral target conditions, and found no significant differences between the two. This suggests that saccade direction selectivity is unlikely to be the primary contributor to the observed modulation. In the revised figure, we added a plot (Figure 2L) that aligns neural activity to saccade onset, in addition to the original alignment to motion stimulus onset (Figure S1E). This new analysis further supports our interpretation.

Author response image 7.

- Even when reading the simulation results, I'm still not 100% sure I understand what is meant by this idea of "consistency" of flexible decision-making

We have addressed this issue in a previous comment and please refer to the response above.

Author Response

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

We would like to thank you and the two reviewers for their constructive feed-back on our manuscript entitled: "Substrate evaporation drives collective construction in termites".

Here, we submit a revised version in which -we believe- we fill the missing details identified by the reviewers and we clarify the presentation of our results.

From the eLife assessment we can identify a few main points that the reviewers found unclear or not well developed in our previous manuscript:

• Insufficient details about computer simulation models. Is the match between simulations and experiments qualitative or quantitative?

• Request for clarifications related to the wall stimulus: is evaporation stronger at the high-curvature wall corners or similar along all the wall edge? Why is there less consistency in the experimental results with the wall stimulus, with a minority of wall experiments in which something different happens?

• Quantitative estimation of the humidity gradients in our experimental setup.

• "Confirmation" that termites can sense humidity gradients of magnitude and scale comparable with those encountered in our experiments.

• Request for additional background information about the considered termite species and their construction habits.

The reviewers also made a number of interesting suggestions and other comments:

• Suggestion of possible explanations and interpretations for a purported discrepancy with a previous work by Calovi and collaborators.

• Suggestion of alternative experimental approaches (array of probes, alternative experimental setups).

We address all these points below.

Details about computer simulation models

There are two different types of computer simulations in our experiments: 1. simulations of evaporation on the initial structure, and 2. simulations of structure growth based on curvature.

1) Simulations of evaporation We recall that these simulations rely on the hypothesis that humidity transport happens in a diffusive way, that is evaporation rate is proportional to the humidity gradient. New details on the implementation of these diffusive simulations are now added in section S.VI. We also adapted figures 4A and 4B which are now expressed in units more comparable to the expected humidity field in experiments. Essentially, we show that the model under-estimates the absolute magnitude of the humidity gradient |∇ℎ| in our setup while it correctly predicts the relative importance of the same field across the topography.

First, it is instructive to report the value of |∇ℎ| predicted by diffusive simulations with the bottom boundary at 100% humidity (like the clay disk), and the top boundary of the simulation box at 70% like our experimental room. Note that, at a given temperature, relative humidity and absolute humidity are proportional, so we will assume here that temperature is constant and always refer to relative humidity. Thus, humidity gradient will be measured in 𝑚𝑚−1 exactly like curvature. One than has:

• flat disk, |∇ℎ| ∼0.01mm−1

• wall tips, |∇ℎ| ∼0.13mm−1

• wall top edge |∇ℎ| ∼0.1mm−1

• pillar tips |∇ℎ| ∼0.19mm−1,

First we remark, that the value of |∇ℎ| on the flat portion of the disk is 10 times smaller of the estimation |∇ℎ|0 ∼0.5mm−1 of the same quantity in our experiments, which is now given in the manuscript and discussed in a specific paragraph below. This discrepancy is due to the fact that our simulations overestimate the size of the diffusive region (i.e. the simulation box) to 18mm while we expect the diffusive layer to be much thinner (i.e. 𝛿 ∼2mm). Note also that, as in all diffusive problems, the humidity gradient on any point of the bottom boundary (i.e. on the clay surface) depends on the distance of that point from the top boundary, for example the closer are the boundaries the stronger is the gradient. This is a very general feature of diffusive problems: the gradient of the diffusing field depends on the distance from the boundaries, where the value of the field is given. Note also that, in principle, the size of the simulation box does not only affect the overall magnitude of the humidity gradient but also its shape. However, one observes that in our simulations the topographic cues are only 30% closer to the top boundary compared to the flat, bottom, surface, but the local gradient is 10 to 20 times larger. This evidence suggests that the ’curvature’ effect is much stronger than the ’distance’ effect, and supports the fact that our approximation does not affect in a significant way the estimation of the relative importance of the humidity gradient at the bottom surface. We then conclude that our diffusive simulations do not provide a correct estimation of the order of magnitude of |∇ℎ|, but well capture its relative variations across the topography.

2) Structure growth based on curvature. As observed by the reviewer, the dynamical simulations included here refer to a model that was developed in a previous study, thus we chose to not include all the details of the simulations in the present one. At this stage, that model is still phenomenological: for example we cannot provide a physical estimation of the dimensionless parameter 𝑑 which controls the typical size of the structure produced by the simulations of the model. Thus in principle, the comparisons with real experiments cannot be other than "qualitative". Indeed, to push such a comparison further is not necessarily of interest, given the minimal and mean field character of our model, and the extreme complexity of the natural system which is studied here. However, our experimental setup was specifically designed to overcome this limit, which is designing topographies where the curvature cues where modulated in a way which is almost discrete, with flat regions, and regions where curvature is strong ’for termites’, i.e. the curvature radius is of the order of termite body size. Our experimental results greatly validate our choice because deposition patterns also show an almost ’discrete’ shape, with specific regions attracting most of the depositing actions. Thus, we claim that the significance of the agreement is strong, and we suggest that when stimuli and response both behave in a quasi-discrete manner, the difference between qualitative and quantitative is not well defined. Finally, we recall that in all the discussion above curvature and humidity gradient can be exchanged, as we already pointed out in the manuscript. Consistently, the humidity gradient show a strong variation between the curved regions and the flat ones.

Results with the wall stimulus One important point coming out from the reviews is that we did not clearly present the results with the wall stimulus. These concerns are best summarized by a comment from reviewer 2, who states: “evaporation rates seem inconclusive in the wall geometry, yet the termites still deposit material at the high-curvature wall corners”.

We acknowledge that the interpretation of results of experiments with the wall stimulus must address three key points: 1- Salt deposition experiment are inconclusive in showing variation of the evaporation rate, across the top of the wall; 2- A portion (4/11) of termite experiments do not show a clear pellet deposition pattern by termites; 3- Conversely, in the remaining portion (7/11), most experiments still show a clear pellet deposition on the corners of the wall, in spite of small differences in evaporation between the corners and the top edge (like in our Fig. 3B). These points are now addressed in the manuscript and discussed below.

The variation of the humidity gradient between the corners of the wall, and the wall’s top edge is relatively small while both are regions of relatively high curvature and higher evaporation as compared to the the flat surface of the clay disk. We now report precise values of the humidity gradient from numerical simulations, as discussed above. These indicate that humidity gradient at the wall corners and upper edge is respectively 10 and 7 times larger than on the flat bottom, but evaporation at the wall tips is only 0.3 times larger than on the wall upper edge.

Experiments with the saline solution qualitatively confirm the same result of an evaporation pattern more evenly distributed on the wall stimulus (point 1) than on the pillars.

Taken together, these results might explain why not all wall experiments end up with depositions at the tips (point 2): simply, in the wall experiments the relative importance of the deposition cue between tips and wall upper edge is not high enough to always guide termite behavior in a deterministic way.

But we should also point to the fact that the evaporation simulations presented in figure 4 and the experiments with the saline solution both reflect the humidity field on the clay templates before termite construction has started. As soon as termites start adding pellets to the wall, effectively starting to build a pillar, the humidity gradient will be reinforced at the locations of pellet deposition, and a self-reinforcing process is initiated, similar to our dynamical simulations based on local curvature. This explains why eventually termite activity can result in clear and localized depositions (point 3) also with the wall stimulus.

Incidentally, we would like to include here another consideration: the nest of Coptotermes termites comprise a “scaffold” with multiple interconnected pillars. In other termite genera, the prevalent nest structure is one made by surfaces, rather than pillars, such as in Nasutitermes nests, Apicotermes, Psammotermes, or again some fungus growing structures in Macrotermes and Synacanthotermes). The fact that the wall stimulus presents some potential to stimulate construction everywhere on its edge is intriguing as it might provide some cues on the construction of different nest architectures.

Quantitative estimation of the humidity gradient in our setup The moisture gradients in our experiments and simulations was only presented in a non-quantitative manner, because we were mainly interested in identifying locations of high and low evaporation. But, combining scaling arguments already discussed in S.IX and the the results of our evaporation simulations, one can produce a lower boundary for the magnitude of the humidity gradient |∇ℎ|, predict its higher value at key positions on our setup, and compare it with humidity variations experienced by termites in their natural environment. These considerations are now included in the manuscript and discussed below.

First, we define a reference value |∇ℎ|0 for the humidity gradient on the (flat) clay disk, which can be estimated using the boundary layer thickness 𝛿 ∼2mm (see section IX.A of the SI) and the variation of relative humidity Δℎ between the clay disk surface and the exterior which was Δℎ =30% (the difference between the fully wetted substrate, and room air humidity at 70% saturation). Note that |∇ℎ|0 constitutes a lower boundary for the expected values of the humidity gradient in our setup, as confirmed by our experiments with saline solution. We can then write:

Next, the results of diffusive simulations shown in figure 4A and 4B indicate that the humidity gradient at highly curved regions of the topographic cues is at least 10 times larger than |∇ℎ|0 which allows to estimate an upper boundary for |∇ℎ| in our experimental setup, say |∇ℎ|𝑚𝑎𝑥 ∼1mm−1. Humidity sensing capabilities of termites Our hypothesis that humidity gradients could guide termite building behavior implicitly assumes that termites can sense humidity gradients comparable with those existing in our experiments.

Humidity is important to all termites because of their small size and unsclerotized body. Coptotermes termites in particular are wetwood termites that can only survive in high-humidity environments such as moist wood or soil. It is well documented that coptotermes termites (like other termites and cockroaches) have humidity receptors in their antennae, and behavioral studies indicate that they can discriminate between chambers with different humidity content.

For example, a study by Gautam and Henderson (2011, Environmental entomology, 40:1232) provided chambers with different relative humidity and, after 12 hours, almost all termites were in the highest humidity chamber (98% RH), leaving the other chambers with 75% or less RH empty. These results (which are similar also to other results testing termite response to chambers with different soil moisture) indicate that -given a sufficient amount of time- termites can detect a difference of humidity from 75% to 98% over a spatial scale of centimeters.

The quantitative estimation of the humidity gradient described above indicates that in our experimental setup termites can experience humidity variations of 15% over a distance of only 1mm and even shorter, while the length of a single termite antenna is about 1.5 mm.

In other words, the humidity gradients that we estimate for our experiments are well above those that termites were able to discriminate in previous experiments. Future experiments should aim to test the exact limits of resolution of the humidity-sensing ability of termites (e.g. in an environment where humidity is close to 100% everywhere), and the mechanisms how they sense the gradient (e.g. comparing information from the two antennae, or by integrating humidity information over time).

By definition, |∇ℎ|0 corresponds to a variation of humidity between a fully saturated atmosphere (i.e. 100%), comparable to the nest interior, and a "humid" atmosphere (i.e. 70%) comparable to the natural environment where termites live (say the nest exterior), occurring over a distance (2mm) which is comparable with their body size.

We can then conclude that even the lower boundary |∇ℎ|0 of the humidity gradient corresponds to an atmosphere variation to which termites must be used, i.e. nest interior vs nest exterior, happening across one body length. If we add that the upper boundary |∇ℎ|𝑚𝑎𝑥 is one order of magnitude higher, it appears extremely unlikely that they could not detect these gradients.

Additional background information about our considered termite species and their construction habits

We have now added some details about the life history and nesting habits of termites in the Coptotermes genus in a new paragraph in section SI. Essentially, these are wetwood termites that nest in moist wood or soil, and their nests present a typical structure comprising a scaffold of interconnected pillars (we now show a picture of a typical structure from one of our lab-reared colonies).

After the initial submission of our manuscript we have also obtained a more precise taxonomic identification of the termites we used, which indicated that our termites are better identified as Coptotermes gestroi than Coptotermes formosanus. The two species are extremely close and can also interbreed in the areas where they co-occur, but in this case C. gestroi is a better match. Hence, we have amended the name in the manuscript and in the supplementary material.

Differences with previous results by Calovi and collaborators

We believe that there is no real discrepancy between our results and those described by Calovi et al. (2019, Phil. Trans. Roy. Soc. B 374:20180374). What they measure-termite aggregation and activity- is similar to what we also observe in our experiments: termites aggregate in concave regions, such as at the base of the wall in our experiments, and they collect pellets at the locations that they visit more often. And, above all, we observe that concavities promote digging activity, which in turns promote aggregation as already observed in previous studies like Green et al. (2017, Proc. Roy. Soc. B 284:20162730). The main difference is that in our analyses we treat separately the three measurements of termite occupancy, pellet collection and pellet deposition, and in this way we identify a role of convexity for pellet deposition.

It is possible that, apart from the differences in language and interpretations between our study and the study by Calovi, there were also real differences in termite building behavior between the two studies that we couldn’t fully appreciate from our own reading of the article by Calovi, but which the reviewer has spotted. The reviewer makes a very interesting suggestion that some of these differences might be due to the different humidity level used in our experiment, compared to the experiment by Calovi and collaborators. Room humidity was high, at around 70% in our experiments. The humidity in Calovi’s experiments was possibly even higher as they performed their experiments in a closed box, but we could not find precise reported information on the humidity level in their publication.

Given that it is not clear that the building behavior in our experiments was qualitatively different from the building behavior in Calovi and collaborators’ experiments, and given that we don’t know the precise humidity value used in Calovi’s experiments (plus, we worked on different termite species that could have different sensitivity to humidity) we decided that -based on the information that we have- we could not meaningfully expand our discussion of similarities and differences with Calovi’s study in our manuscript.

It is clear, though, and we completely agree with the referee on this point, that in light of Calovi’s and our own new results, it would now be extremely interesting if future experiments could characterize termite construction activity across a range of finely controlled air humidity values. Anecdotally, in preliminary experiments we did include some trials in which termites were hosted in a completely closed box, and we observed much reduced construction activity in those conditions. However, the fact that we could not easily track termite activity and pellet collections / depositions in those conditions (because of the box), together with the fact that the building activity itself was reduced, made us to converge towards the open arena experiments that we describe here.

Suggestion of alternative experimental approaches One reviewer made interesting suggestions for alternative experiments, including using an array of humidity probes for measuring humidity, or a different experimental setup -analogous to those used in previous experiments by Bardunias and collaborators-. It is often the case that only at the end of a series of experiments we identify an alternative, and possibly better, way of doing the same experiment. In future, if we have the opportunity to run other similar experiments again, we will likely experiment with these suggestions. When we first designed our own experiments, one of our priorities was to be able to film all termites in the arena at all time, so that potentially we could also study individual termite behavior and task specialization. This partly constrained the type of experimental setups that we could use.

One aspect that clearly emerged from our work and from the revision process is that any future experiments related to this topic should achieve a very precise control of air humidity, and test a wider range of stimuli of more varied and controlled size, humidity and curvature. Since our own experiments were conducted, three of us have moved to different institutions, which imposes practical constraints for us on working on the same termites in a similar way, but the suggestions from the reviewers will be helpful as we are planning our future research.

We hope that the explanations above and the details that we have changed in the manuscript itself have contributed to clarify unclear aspects of our study.

Author response:

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

We thank the reviewers for their time and thoughtful comments. We believe that the further analyses suggested have made the results clearer and more robust. Below, we briefly highlight the key points addressed in the revision and the new evidence supporting them. Then, we address each reviewer’s critiques point-by-point.

- Changes in variability with respect to time/experience

Both reviewers #1 and #3 asked whether the variability in grid properties observed was dependent on time or experience. This is an important point, given that such a dependence on time could lead to interesting hypotheses about the underlying dynamics of the grid code. However, in the new analyses we performed, we do not observe changes in grid variability within a session (Fig S5 of the revised manuscript), suggesting that the grid variability seen is constant within the timescale of the data set.

- The assumption of constant grid parameters in the literature

Reviewer #2 pointed out that it had been appreciated by experimentalists that grid properties are variable within a module. We agree that we may have overstated the universality of this assumption in the original manuscript, and we have toned down the language in the revision. However, we note that many previous theoretical studies assumed these properties to be constant, within a given module. We provide some examples below, and have added evidence of this assertion, with citations to the theoretical literature, to the revised manuscript .

- Additional sources of variability

Reviewer #3 pointed out additional sources that might explain the variability observed in the paper (beyond time and experience). These sources include: field width, border location, and the impact of conjunctive cells. We have run additional analyses and have found no significant impact on the observed variability from any of these factors. We believe that these are important controls, and have added them to the manuscript (Fig S4-S7 of the revised manuscript)

- Analysis of computational models

Reviewer #3 noted that our results could be strengthened by performing similar analyses on the output of computational models of grid cells. This is a good idea. We have now measured the variability of grid properties in a recent normative recurrent neural network (RNN) model that develops grid cells when trained to perform path integration (Sorscher et al., 2019). This model has been shown to develop signatures of a 2D toroidal attractor (Sorscher et al., 2023) and achieves a high accuracy on a simple path integration task. Interestingly, the units with the greatest grid scores also exhibit a range of grid spacings and grid orientations (Fig S8 of the revised manuscript). Furthermore, by decreasing the amount of sparsity (through decreasing the weight decay regularization), we found an increase in the variability of the grid properties. This analysis demonstrates a heretofore unknown similarity between the RNN models trained to perform path integration and recorded grid cells from MEC. It additionally provides a framework for computational analysis of the emergence of grid property variability.

Reviewer #1:

(1) Is the variability in grid spacing and orientation that the authors found intrinsically organized or is it shaped by experience? Previous research has shown that grid representations can be modified through experience (e.g., Boccara et al., Science 2019). To understand the dynamics of the network, it would be important to investigate whether robust variability exists from the beginning of the task period (recording period) or whether variability emerges in an experience-dependent manner within a session.

This is an interesting question that was not addressed in the paper. To test this, we performed additional analysis to resolve whether the variability changes across a session.

Using a sliding window, we have measured changes in variability with respect to recording time (Fig S5A). To this end, we compute grid orientation and spacing over a time-window whose length is half the total length of the recording. From the population distribution of orientation and spacing values, we compute the standard deviation as a measure of variability. We repeat the same procedure, sliding the window forward until the variability for the second half of the recording is computed.

We applied this approach to recording ID R12 (the same as in Figs 2-4) given that this recording session was significantly longer than the rest (nearly two hours). Results are shown in Fig S5B-C. For both orientation and spacing, no changes of variability with respect to time can be observed. Similar results were found for other modules (see caption of Fig S5 for statistics).

We also note that the rats were already familiarized with the environment for 10-20 sessions prior to the recordings, so there may not be further learning during the period of the grid cell recordings. No changes in variability can be seen in Rat R across days (e.g., in Fig 5B R12 and R22 have similar distributions of variability). However, we note that it may be possible that there are changes in grid properties at time-scales greater than the recordings.

(2) It is important to consider the optimal variability size. The larger the variability, the better it is for decoding. On the other hand, as the authors state in the

Discussion, it is assumed that variability does not exist in the continuous attractor model. Although this study describes that it does not address how such variability fits the attractor theory, it would be better if more detailed ideas and suggestions were provided as to what direction the study could take to clarify the optimal size of variability.

We appreciate this suggestion and agree that more discussion is warranted on how our results can be reconciled with previously observed attractor dynamics. To explore this, we studied the recurrent neural network (RNN) model from Sorscher et al. (2019), which develops grid responses when trained on path integration. This network has previously been found to develop signatures of toroidal topology (Sorscher et al., 2023), yet we find its grid responses also contain heterogeneity in grid properties (Fig S8). By decreasing the strength of the weight decay regularization (which leads to denser connectivity in the recurrent layer), we find an increase in the grid property variability. Interestingly, decreasing the weight decay regularization has been previously found to lead to weaker grid responses and worse ability of the RNN to perform path integration on environments larger than it was trained on. This approach not only provides preliminary evidence to our claim that too much variability can lead to weaker continuous attractor structure, but also provides a modeling framework with which future work can explore this question in more detail. We have added discussion of this issue to the manuscript text (Discussion).

Reviewer #2:

(1) Even though theoreticians might have gotten the mistaken impression that grid cells are highly regular, this might be due to an overemphasis on regularity in a subset of papers. Most experimentalists working with grid cells know that many if not most grid cells show high variability of firing fields within a single neuron, though this analysis focuses on between neurons. In response to this comment, the reviewers should tone down and modify their statements about what are the current assumptions of the field (and if possible provide a short supplemental section with direct quotes from various papers that have made these assumptions).

We agree that some experimentalists are aware of variability in the recorded grid response patterns and that this work may not come as a complete surprise to them. We have toned down our language in the Introduction, changing “our results challenge a long-held assumption” to “our results challenge a frequently made assumption in the theoretical literature”. Additionally, we have added a caveat that “experimentalists have been aware” of the observed variability in grid properties.

We would like to emphasize that the lack of work carefully examining the robustness of this variability has prevented a firm understanding of whether this is an inherent property of grid cells or due to measurement noise. The impact of this can be seen in theoretical neuroscience work where a considerable number of articles (including recent publications) start with the assumption that all grid cells within a module have identical properties, with the exception of phase shift and noise. We have now cited a number of these papers in the Introduction, to provide specific references. To further illustrate the pervasiveness of this assumption being explicitly made in theoretical neuroscience, below we provide quotes from a few important papers:

“Cells with a common spatial period also share a common grid orientation; their responses differ only by spatial translations, or different preferred firing phases, with respect to their common response period” (Sreenivasan and Fiete, 2011)”

“Grid cells are organized into discrete modules; within each module, the spatial scale and orientation of the grid lattice are the same, but the lattice for different cells is shifted in space.” (Stemmler et al., 2015)”

“Recently, it was shown that grid cells are organized in discrete modules within which cells share the same orientation and periodicity but vary randomly in phase” (Wei et al., 2015)”

“...cells within one module have receptive fields that are translated versions of one another, and different modules have firing lattices of different scales and orientations” (Dorrell et al., 2023)”

In these works, this assumption is used to derive properties relating to the computational properties of grid cells (e.g., error correction, optimal scaling between grid spacings in different modules).

In addition, since grid cells are assumed to be identical in the computational neuroscience community, there has been little work on quantifying how much variability a given model produces. This makes it challenging to understand how consistent different models are with our observations. This is illustrated in our analysis of a recent recurrent neural network (RNN) model of grid cells (Fig S8), which does exhibit variability.

(2) The authors state that "no characterization of the degree and robustness of variability in grid properties within individual modules has been performed." It is always dangerous to speak in absolute terms about what has been done in scientific studies. It is true that few studies have had the number of grid cells necessary to make comparisons within and between modules, but many studies have clearly shown the distribution of spacing in neuronal data (e.g. Hafting et al., 2005; Barry et al., 2007; Stensola et al., 2012; Hardcastle et al., 2015) so the variability has been visible in the data presentations. Also, most researchers in the field are well aware that highly consistent grid cells are much rarer than messy grid cells that have unevenly spaced firing fields. This doesn't hurt the importance of the paper, but they need to tone down their statements about the lack of previous awareness of variability (specific locations are noted in the specific comments).

We have toned down our language in the Introduction. However, we note that our point that no detailed analysis had been done on measuring the robustness of this variability stands. Thus, for the general community, it has not been clear whether this previously observed variability is noise or a real feature of the grid code.

(3) The methods section needs to have a separate subheading entitled: How grid cells were assigned to modules" that clearly describes how the grid cells were assigned to a module (i.e. was this done by Gardner et al., or done as part of this paper's post-processing?

We thank the reviewer for pointing out this missing information. We have added a new subsection in the Materials and Methods section, entitled “Grid module classification” to clarify how the grid cells are assigned to modules. In short, this was done by Gardner et al. (2022) using an unsupervised clustering approach that was viewed as enabling a less biased identification of modules. We did not perform any additional processing steps on module identity.

Reviewer #3:

(1) One possible explanation of the dispersion in lambda (not in theta) could be variability in the typical width of the field. For a fixed spacing, wider fields might push the six fields around the center of the autocorrelogram toward the outside, depending on the details of how exactly the position of these fields is calculated. We recommend authors show that lambda does not correlate with field width, or at least that the variability explained by field width is smaller than the overall lambda variability.

We agree that this option had not been carefully ruled out by our previous analyses. To tackle this question, we compute the field width of a given cell using the value at the minima of its spatial autocorrelogram (Fig S4A-B). For all cells in recording ID R12, there is a non-significant negative linear correlation between grid field width and between-cell variability (Fig S4C) . The variability explained by the width of the field is 4% of the variability, as indicated by the R² value of the linear fit. Similar results were found for all other modules (see caption of Fig S4C for statistics). Therefore, we do not think that grid field width explains spacing variability.

(2) An alternative explanation could be related to what happens at the borders. The authors tackle this issue in Figure S2 but introduce a different way of measuring lambda based on three fields, which in our view is not optimal. We recommend showing that the dispersions in lambda and theta remain invariant as one removes the border-most part of the maps but estimating lambda through the autocorrelogram of the remaining part of the map. Of course, there is a limit to how much can be removed before measures of lambda and theta become very noisy.

We have performed additional analysis to explore the role of borders in grid property variability. To do so, we have followed the suggestion by the reviewer and have re-analyzed grid properties from the autocorrelogram when the border-most part of the maps are removed (Fig S6A-B). For all modules, we do not see any changes in variability (computed as the standard deviation of the population distribution) for either orientation or spacing. As predicted by the reviewer, after removing about 25% of the border-most part of the environment we start seeing changes in variability, as measures of theta and lambda become noisy and computed over a smaller spatial range. This result holds for all other modules (Fig S6C-D).

(3) A third possibility is slightly more tricky. Some works (for example Kropff et al, 2015) have shown that fields anticipate the rat position, so every time the rat traverses them they appear slightly displaced opposite to the direction of movement. The amount of displacement depends on the velocity. Maps that we construct out of a whole session should be deformed in a perfectly symmetric way if rats traverse fields in all directions and speeds. However, if the cell is conjunctive, we would expect a deformation mainly along the cell's preferred head direction. Since conjunctive cells have all possible preferred directions, and many grid cells are not conjunctive at all, this phenomenon could create variability in theta and lambda that is not a legitimate one but rather associated with the way we pool data to construct maps. To rule away this possibility, we recommend the authors study the variability in theta and lambda of conjunctive vs non-conjunctive grid cells. If the authors suspect that this phenomenon could explain part of their results, they should also take into account the findings of Gerlei and colleagues (2020) from the Nolan lab, that add complexity to this issue.

We appreciate the reviewer pointing out the possible role conjunctive cells may play. To investigate how conjunctive cells may affect the observed grid property variability, we have performed additional analyses taking into account if the grid cells included in the study are conjunctive. Comparing within- and between-cell variability of conjunctive vs. non-conjunctive cells in recording R12, we do not see any qualitative differences for either orientation or spacing (Fig S7A-B). When excluding conjunctive cells from the between-variability comparison, we do not see any significant difference compared to when these cells are included (Fig S7C-D). As such, it does not appear that conjunctive cells are the source of variability in the population.

We further note that the number of putative conjunctive cells varied across modules and recordings. For instance, in recording Q1 and Q2, Gardner et al. (2022) reported 3 (out of 97) and 1 (out of 66) conjunctive cells, respectively. Given that we see variability robustly across recordings (Fig 5), we do not believe that conjunctive cells can explain the presence of variability we observe.

(4) The results in Figure 6 are correct, but we are not convinced by the argument. The fact that grid cells fire in the same way in different parts of the environment and in different environments is what gives them their appeal as a platform for path integration since displacement can be calculated independently of the location of the animal. Losing this universal platform is, in our view, too much of a price to pay when the only gain is the possibility of decoding position from a single module (or non-adjacent modules) which, as the authors discuss, is probably never the case. Besides, similar disambiguation of positions within the environment would come for free by adding to the decoding algorithm spatial cells (non-hexagonal but spatially stable), which are ubiquitous across the entorhinal cortex. Thus, it seems to us that - at least along this line of argumentation - with variability the network is losing a lot but not gaining much.

We agree that losing the continuous attractor network (CAN) structure and the ability to path integrate would be a very large loss. However, we do not believe that the variability we observe necessarily destroys either the CAN or path integration. We argue this for two reasons. First, the data we analyzed [from Gardner et al. (2022)] is exactly the data set that was found to have toroidal topology and therefore viewed to be consistent with a major prediction of CANs. Thus, the amount of variability in grid properties does not rule out the underlying presence of a continuous attractor. Second, path integration may still be possible with grid cells that have variable properties. To illustrate this, we analyzed data from Sorscher et al. (2019) recurrent neural network model (RNN) that was trained explicitly on path integration, and found that the grid representations that emerged had variability in spacing and orientation (see point #6 below).

(5) In Figure 4 one axis has markedly lower variability. Is this always the same axis? Can the authors comment more on this finding?

We agree that in Fig 4 the first axis has lower variability. We believe that this is specific to the module R12 and does not reflect any differences in axis or bias in the methods used to compute the axis metrics. To test this, we have performed the same analyses for other modules, finding that other recordings do not exhibit the same bias. Results for the modules with the most cells are shown below (Author response image 1).

Author response image 1.

Grid propertied along Axis 1 are not less variable for many recorded grid modules. Same as Fig.4C-D, but for four other recorded modules. Note that the variability along each axis is similar.

(6) The paper would gain in depth if maps coming out of different computational models could be analyzed in the same way.

We agree with the reviewer that examining computational models using the same approach would strengthen our results and we appreciate the suggestion. To address this, we have analyzed the results from a previous normative model for grid cells [Sorscher et al., (2019)] that trained a recurrent neural network (RNN) model to perform path integration and found that units developed grid cell like responses. These models have been found to exhibit signatures of toroidal attractor dynamics [Sorscher et al. (2023)] and exhibit a diversity of responses beyond pure grid cells, making them a good starting point for understanding whether models of MEC may contain uncharacterized variability in grid properties.

We find that RNN units in these normative models exhibit similar amounts of variability in grid spacing and orientation as observed in the real grid cell recordings (Fig S8A-D). This provides additional evidence that this variability may be expected from a normative framework, and that the variability does not destroy the ability to path integrate (which the RNN is explicitly trained to perform).

The RNN model offers possibilities to assess what might cause this variability. While we leave a detailed investigation of this to future work, we varied the weight decay regularization hyper-parameter. This value controls how sparse the weights in the hidden recurrent layer are. Large weight decay regularization strength encourages sparser connectivity, while small weight decay regularization strength allows for denser connectivity. We find that increasing this penalty (and enforcing sparser connectivity) decreases the variability of grid properties (Fig S8E-F). This suggests that the observed variability in the Gardner et al. (2022) data set could be due to the fact that grid cells are synaptically connected to other, non-grid cells in MEC.

(7) Similarly, it would be very interesting to expand the study with some other data to understand if between-cell delta_theta and delta_lambda are invariant across environments. In a related matter, is there a correlation between delta_theta (delta_lambda) for the first vs for the second half of the session? We expect there should be a significant correlation, it would be nice to show it.

We agree this would be interesting to examine. For this analysis, it is essential to have a large number of grid cells, and we are not aware of other published data sets with comparable cell numbers using different environments.

Using a sliding window analysis, we have characterized changes in variability with respect to the recording time (Figure S5A). To do so, we compute grid orientation and spacing over a time-window whose length is half of the total length of the recording. From the population distribution of orientation and spacing values, we compute the standard deviation as a measure of between-cell variability. We repeat the same procedure, sliding the window forward until the variability for the second half of the recording is computed.

We applied this approach to recording ID R12 (the same as in Figs 2-4) given that this recording session was significantly longer than the rest (almost two hours). Results are shown in Fig S5 B-C. For both orientation and spacing, no systematic changes of variability with respect to time were observed. Similar results were found for other modules (see caption of Fig S5 for statistics).

We also note that the rats were already familiarized with the environment for 10-20 sessions prior to the recordings, so there may not be further learning during the period of the grid cell recordings. No changes in variability can be seen in Rat R across days (e.g., in Fig 5B R12 and R22 have similar distributions of variability). However, we note that it may be possible that there are changes in grid properties at time-scales greater than the recordings.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In this manuscript entitled "Hexokinase regulates Mondo-mediated longevity via the PPP and organellar dynamics", Laboy and colleagues investigated upstream regulators of MML-1/Mondo, a key transcription factor that regulates aging and metabolism, using the nematode C. elegans and cultured mammalian cells. By performing a targeted RNAi screen for genes encoding enzymes in glucose metabolism, the authors found that two hexokinases, HXK-1 and HXK-2, regulate nuclear localization of MML-1 in C. elegans. The authors showed that knockdown of hxk-1 and hxk-2 suppressed longevity caused by germline-deficient glp-1 mutations. The authors demonstrated that genetic or pharmacological inhibition of hexokinases decreased nuclear localization of MML-1, via promoting mitochondrial β-oxidation of fatty acids. They found that genetic inhibition of hxk-2 changed the localization of MML-1 from the nucleus to mitochondria and lipid droplets by activating pentose phosphate pathway (PPP). The authors further showed that the inhibition of PPP increased the nuclear localization of mammalian MondoA in cultured human cells under starvation conditions, suggesting the underlying mechanism is evolutionarily conserved. This paper provides compelling evidence for the mechanisms by which novel upstream metabolic pathways regulate MML-1/Mondo, a key transcription factor for longevity and glucose homeostasis, through altering organelle communications, using two different experimental systems, C. elegans and mammalian cells. This paper will be of interest to a broad range of biologists who work on aging, metabolism, and transcriptional regulation. 

Reviewer #2 (Public Review):

Raymond Laboy et.al explored how transcriptional Mondo/Max-like complex (MML-1/MXL-2) is regulated by glucose metabolic signals using germ-line removal longevity model. They believed that MML-1/MXL-2 integrated multiple longevity pathways through nutrient sensing and therefore screened the glucose metabolic enzymes that regulated MML-1 nuclear localization. Hexokinase 1 and 2 were identified as the most vigorous regulators, which function through mitochondrial beta-oxidation and the pentose phosphate pathway (PPP), respectively. MML-1 localized to mitochondria associated with lipid droplets (LD), and MML-1 nuclear localization was correlated with LD size and metabolism. Their findings are interesting and may help us to further explore the mechanisms in multiple longevity models, however, the study is not complete and the working model remains obscure. For example, the exact metabolites that account for the direct regulation of MML-1 were not identified, and more detailed studies of the related cellular processes are needed. 

The identification of responsible metabolites is necessary since multiple pieces of evidence from the study suggests that lipid other than glucose metabolites may be more likely to be the direct regulator of MML-1 and HXK regulate MML-1 indirectly by affecting the lipid metabolism: 1) inhibiting the PPP is sufficient to rescue MML-1 function independent of G6P levels; 2) HXK-1 regulates MML-1 by increasing fatty acid beta-oxidation; 3) LD size correlates with MML-1 nuclear localization and LD metabolism can directly regulate MML-1. The identification of metabolites will be helpful for understanding the mechanism. 

Beta-oxidation and the PPP are involved in the regulation of MML-1 by HXK-1 and HXK-2, respectively. But how these two pathways participate in the regulation is not clear. Is it the beta-oxidation rate or the intermediate metabolites that matters? As for the PPP, it provides substrates for nucleotide synthesis and also its product NADPH is essential for redox balance. Is one of the metabolites or the NADPH levels involved in MML-1 regulation? More studies are needed to provide answers to these concerns. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Following are my comments that the authors may want to address to further improve this excellent paper.

Major comments 

(1) Although the authors provided evidence that hexokinases in glucose metabolism are associated with germline-deficient glp-1(-) mutants, they did not mention why they focused on glp-1(-) mutants rather than other longevity mutants. In their previous study (Nakamura et al., 2016), they showed that MML-1 is required for multiple longevity pathways in C. elegans, including reduced mitochondrial respiration and insulin/IGF-1 signaling. Please discuss why the authors focused on glp-1(-) mutants in this paper. It will be even better if the authors test the roles of hexokinases in some other longevity regimens. 

Many thanks for this astute comment. Previously we had shown that mml-1 is required for glp-1, daf-2, and isp-1 longevity, and Johnson et al. had shown a requirement for eat-2, hence the idea that MML-1 is a convergent transcription factor. We first focused on glp-1 because that was the starting point of our screen, and the result was clear and simple: hexokinases regulate MML‑1 nuclear localization and activity in glp-1 and are required for longevity. Naturally, the question arises: do hexokinases behave like MML-1 as convergent longevity regulators across pathways? To address this, we examined the interaction of hxk-1 and hxk-2 with isp-1, daf-2, and raga-1.  Specifically, we now show that:

A. Like glp-1(e2141) mutants, isp-1(qm150) mutants stimulate MML-1 nuclear localization, and the hexokinases are required for isp-1 longevity (Figure 1G-H).

B. daf-2(e1370) mutants do not further stimulate MML-1 nuclear localization beyond basal levels, yet MML-1 is strongly required for daf-2 longevity (Nakamura et al., 2016, Supplementary Figure 1L-M). However, the hexokinases are not required for daf-2 longevity (Supplementary Figure 1M), suggesting that the signaling pathway is wired differently in daf-2, and that other pathways regulate MML-1 activity.

C. raga-1(ok701) mutants stimulate MML-1 nuclear localization and mml-1 is required for raga-1 longevity, suggesting that MML-1 acts downstream of TORC1 signaling (Supplementary Figure 1N-O). However, hexokinases are not required for raga-1 longevity, suggesting that raga-1 acts downstream or parallel to hexokinase signaling (Supplementary Figure 1P).

D. We performed untargeted metabolomics in glp-1, daf-2, and mml-1 single and double mutants and observed that hexose phosphates, which have been shown to regulate MML-1 human homologs MondoA/ChREBP, were differentially regulated between mutants.

Author response image 1.

E. Altogether these experiments reveal that though MML-1 promotes longevity in most pathways, the hexokinases are only required in some (glp-1, isp-1), but not others (raga-1, daf-2). Furthermore, strong MML-1 nuclear localization is often but not always associated with longevity (e.g. daf-2), and the wiring of the signaling pathway is different for various longevity regimens. Consistently, mTOR and Insulin signaling are more functionally linked and therefore may show a more similar genetic profile. Differences in hexose phosphate between glp-1 and daf-2 could explain why MML-1 requires hexokinase function in glp-1 to promote longevity but not in daf-2. However, considerably more work is required to rigorously validate this hypothesis.

(2) In figure 5, the authors investigated whether the association between PPP and MML‑1/MondoA, tested in C. elegans, is conserved in mammals under starvation conditions. The authors should clarify why they tested the MondoA localization upon starvation in cultured human cells. This comment is related to my comment #1 as the authors could determine the roles of hexokinases under dietary restriction (DR)-conditions or in DR-mimetic in eat-2(-) mutants. 

In this case, the actual translatability to a worm longevity pathway was not our goal. Rather, we examined MondoA in cell culture under contrasting conditions of MondoA subcellular localization, where high glucose media had cytosolic/nuclear localization and starvation conditions cytosolic localization. We then showed that similar to our data in worms, PPP inhibition with 6-AN induced MondoA nuclear localization and activity. We now mention this rationale in the results section, lines 352-356.

(3) In figure 2, the authors showed that HXK-2 regulates mitochondrial localization of MML-1, and HXK-1 regulates nuclear localization of MML-1 through mitochondrial β-oxidation in glp‑1(-) mutants. Can the authors test whether mitochondrial β-oxidation affects the effects of hxk RNAi on longevity of glp-1(-) mutants? 

Excellent suggestion. We tried to test this idea and found that acs-2 RNAi alone abolished glp-1 longevity, making epistasis experiments difficult to interpret. This is consistent with published data showing that glp-1 longevity requires NHR-49, a transcription factor that regulates mitochondrial b‑oxidation, that drives acs-2 expression (Ratnappan et al., 2014). It could well be that b‑oxidation inhibition promotes MML-1 nuclear localization but abolishes lifespan extension because of epistatic effects on other transcription factors or processes. Further investigation would be required to elucidate the exact mechanism that goes beyond the scope of the paper.

(4) The authors showed that 2-deoxy-glucose, which decreases the activity of HXK, decreased the nuclear localization of MML-1, and this is consistent with their genetic data. Based on these data, 2-deoxy-glucose is expected to decrease longevity. Interestingly, however, 2-deoxy-glucose has been reported to increase lifespan by restricting glucose, whereas extra glucose intake decreases lifespan in C. elegans, shown by multiple research groups, including M. Ristow, C. Kenyon, and S.J.V. Lee labs. This is seemingly paradoxical and worth discussing with key references, especially because MondoA and Chrebp are known as glucose-responsive transcription factors. 

Thank you for this important comment. 2-DG has been shown to extend lifespan by suppressing glucose metabolism at concentrations ranging from 0.1 to 5 mM, higher concentrations ranging from 20 to 50 mM had the opposite effect decreasing lifespan (Schulz et al., 2007). The concentration we tested was 50 mM 2-DG and observed decreased MML-1 nuclear localization, which is consistent with the previous data showing decreased longevity. We now raise this point in the discussion suggesting that mild inhibition of glucose metabolism has beneficial effects on longevity, while strong suppression causes a shortening of the lifespan (lines 411-414).

Minor comments 

(1) The current Introduction does not include the explicit statement about that MML-1 and MondoA are homologs. Please clarify this as naive readers may be confused.

Thank you for pointing this out. We now say in the intro that MondoA and MML-1 are homologs (lines 59-60).

(2) In figure 1, the effects of hxk-3 on nuclear localization of MML-1 is small compared to those of hxk-1 and hxk-2. Please add speculation about why HXK-3 has different roles in nuclear localization of MML-1 compared to HXK-1 and HXK-2. 

According to GExplore 1.4 (Hutter & Suh, 2016), hxk-3 expression declines during larval development and is low expressed in the adult. Perhaps it has little effect in the young adult, and the other hexokinases suffice to support MML-1 nuclear localization. It also remains possible that hxk-3 is not required in glp-1, but required in other longevity pathways.

(3) The authors tested the effects of genetic inhibition of hxk-1 and hxk-2 on the regulation of MML-1 localization and lifespan of glp-1(-) mutants by using RNAi. I wonder whether the authors can perform the experiments with hxk-1 or hxk-2 loss (or reduction) of function mutants. If they cannot, please discuss the reason and the limitations of RNAi. 

This is an important point raised by the reviewer. We found that RNAi was most effective for phenotypes related to MML-1 nuclear localization and longevity, likely because it results in acute knockdown. We also showed that pharmacological inhibition of hexokinase function with 3BrP and 2‑DG (Supplementary Figure 1B and 1C) and the PPP with 6-AN (Figure 3B) had consistent results with our observation with RNAi.

We generated hexokinase KO mutants by deleting the coding sequence of each hexokinase by CRISPR/Cas9. First, we measured the expression of each hexokinase isozyme in each mutant. Notably, hxk-1(syb1271) null mutant had higher expression of hxk-2 and hxk-3, hxk-2(syb1261) did not significantly affect the expression of hxk-1 and hxk-3, and hxk-3(syb1267) had a mild increase in hxk-2 expression. We followed up on the hxk-1(syb1271) and hxk-2(syb1261) and crossed these mutants with our MML-1::GFP reporter. We observed a modest but significant reduction in MML-1 nuclear localization in both strains. The effect with RNAi is much stronger in comparison to the null mutants, potentially due to a compensatory upregulation of the other hexokinases in the mutants that we do not observe with RNAi (Supplementary Figure 1D-E). Another alternative is that there is a threshold in the effects of hexokinase function on MML-1 nuclear localization. We tried to generate a hxk-1; hxk-2 double mutant but it was lethal and therefore did not pursue this further.

Author response image 2.

(4) Please correct minor typos throughout the manuscript. Following are some examples. <br /> - On page 4, line 111, please correct "Supplementary Figure D-E" to "Supplementary Figure 1D-E". 

- On page 9, line 272, please correct "3A-B" to "4A-B". 

- On page 9, line 275, please correct "S4" to "4". 

- On page 10, line 309, please correct "4A" to "4B" 

Corrected.

(5) In Fig. 3E, please add the information about the scale bars in figure legends.

Corrected.

Reviewer #2 (Recommendations For The Authors):

Here are some detailed suggestions for the authors:

(1) Since MML-1/MXL-2 complex functions in multiple longevity models, e.g. DR, ILS, what are the roles of HXK-1 and HXK-2 in these models? 

We now show that although mml-1 is required in most longevity pathways, hxk-1 and hxk-2 are required in some pathways (glp-1, isp-1) but not others (daf-2, raga-1). See above for more details.

(2) As for the metabolites screening, the lipid metabolic genes can be included. Not only for the above reasons, also previous study had found that the mml-1 mRNA levels and MML-1 GFP nuclear localization were all increased in the glp-1 model, while mml-1 mRNA levels were unaffected by hxk knockdown, suggesting more pathways be involved. 

We agree with the reviewer that understanding what metabolites regulate MML-1 nuclear localization and activity is an important, yet challenging question. Our studies demonstrate a role of glucose metabolism, in particular, hexokinase in this process, consistent with hexose-p being activators of MondoA. Our data also suggest mechanisms beyond hexose-p regulate MML-1, since knockdown of the PPP components stimulates MML-1 even when hxk-2 is depleted and low G6P, and inhibition of the PPP with 6-AN stimulates MondoA nuclear localization under starvation conditions in mammalian cell culture. We tested redox regulation, nucleoside, and lipid metabolism as candidate processes (see below). Notably, our data suggest this other mechanism is tied to lipid metabolism through droplet size since various perturbations that impact LD size and number (atgl-1, dgat-2, tkt-1, Figure 4) affected MML-1 nuclear localization. It remains an open question whether MML-1 is regulated by other metabolites through a ligand-protein interaction or not. We cannot exclude that beyond lipid droplet regulation, specific lipids, other metabolites, or metabolic modules linked to the PPP might regulate MML-1 nuclear localization and activity.

We employed genetic manipulation and pharmacological inhibition to understand the upstream signals that regulate MML-1. These approaches will not be sufficient to determine whether other metabolite(s) are involved in MML-1/MondoA translocation to the nucleus through a direct interaction. Novel technologies that determine protein-metabolite interactions (e.g. MIDAS) will help us answer this question in future work, and go beyond the scope of this paper. As a compromise, we discuss possible metabolites that may orchestrate this based on our observations based on MML‑1 subcellular localization at LD/mitochondria (including PPP and TCA cycle intermediates).

(3) Line 238, it should be "NADPH". 

Corrected.

(4) RNAi targeting enzymes of different branches of PPP can be performed

In our initial screen, we examined the effect of various enzymes of the PPP on MML-1 nuclear localization (Figure 1A, Supplementary Table S1) and found that knockdown of enzymes in both the oxidative phase (PGDH/T25B9.9) and non-oxidative phase (transketolase/TKT-1) affect MML-1 nuclear localization. In line, 6-AN treatment, which affects the oxidative phase, also stimulated MML‑1 nuclear localization (Figure 3B). We also observed that knockdown of enzymes involved in ribose 5P conversion to ribose, ribose 1P, and phosphoribosyl pyrophosphate, an intermediate in nucleotide biosynthesis, decreased MML-1 nuclear localization (rpia-1, F07A11._5, _Y43F4B.5, _R151._2; Supplementary Table S1). Whether MML‑1/MondoA responds to nucleotide pool remains elusive.

(5) As for PPP, these are many possibilities that can be tested. For example, as PPP supplies NADPH for oxidative balance, does MML-1 respond to ROS? Also, it appears the genes in the non-oxidative arm of PPP regulate MML-1, so is nucleotide synthesis involved? 

Thank you for the suggestion. We tested other enzymes involved in NADPH production from the folate cycle and observed a mild but significant reduction of MML-1 nuclear localization upon dao-3i (Supplementary Table S1). Moreover, we tested whether MML-1 nuclear localization is responsive to ROS. While paraquat exposure induced oxidative stress by measuring the transcriptional reporter gst‑4p::GFP (Supplementary Figure 3A), paraquat exposure did not significantly affect MML-1 nuclear localization (Supplementary Figure 3B). Therefore we think it less likely that NADPH production acting through redox regulation is the main effect.

We also tried supplementation with some of the metabolite outputs of PPP including ribose, ribulose, and xylulose, as well as nucleosides (see below), but saw no effect on MML-1 nuclear localization. We agree that further studies are required to pinpoint whether there is another metabolic moiety regulating MML-1 at the protein-ligand level, but this goes beyond the scope of the current investigation.

Author response image 2.

Author response:

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

Reviewer #1:

“EGFRvIII is mainly associated with the classical subtype, so the mesenchymal subtype might be unexpected here. This could be commented on.” 

We acknowledge that EGFRvIII is most often associated with the classical subtype of glioblastoma and agree that mesenchymal subtype classification may be unexpected given the use of her4.1:EGFRvIII as a driver in our model. We would like to highlight the fact that our brain tumors do also express certain markers associated with the classical subtype including neural precursor and neural stem cell markers like sox2, ascl1b, and gli2 (Supplementary Fig 4, 5; Supplementary Table 1-3). However, our transcriptomic data was not found to significantly enrich for classical subtype gene expression, compared to normal brains. This could be due to a significant contribution of normal brain tissue to our analyses (bulk tumor burdened brains were harvested for RNA sequencing), as well as the significant contribution of mesenchymal subtype signatures and/or inflammatory gene expression in our brain tumor-positive samples. Because signatures associated with inflammation consist of some of the most highly upregulated genes in our samples, this could potentially dilute out and/or lessen alterative subtype and/or signature gene expression. Importantly, it is now widely appreciated that patient tumors simultaneously consist of heterogenous tumor cells reflecting multiple molecular subtypes (Couturier et al., 2020; Darmanis et al., 2017; Neftel et al., 2019), providing glioblastoma with a high level of phenotypic plasticity. We also demonstrate that the contribution of additional drivers not always present with EGFRvIII in patient glioblastoma enhances primary brain tumors in vivo. This result is consistent with more aggressive glioblastomas seen in patients with EGFRvIII variants and TP53 loss-of-function mutations (Ruano et al., 2009). It will therefore be interesting in the future to consider how single or multiple driver mutations contribute to subtype-specific gene expression in our model, as well as histopathology, relative to patients. We have included some of these discussion points to our revised manuscript.     

“Some more histologic characterization of the tumors would be helpful. Are they invasive, do larger tumors show necrosis and microvascular proliferation? This would help with understanding the full potential of the new model.”

We have updated our manuscript to include more histolopathological characterization and images (Supplementary Fig 2).

“Current thinking in established glioblastoma is that the M1/M2 designations for macrophages are not relevant, with microglia macrophage populations showing a mixture of pre- and anti-inflammatory features. Ideally, there would be a much more detailed characterization of the intratumoral microglia/macrophage population here, as single markers can’t be relied upon.”

We performed additional gene set enrichment analyses (GSEA) using our sequencing datasets and compared p53EPS gene expression to M1/M2 macrophage expression signatures and expression signatures from MCSF-stimulated macrophages at early and late (M2 polarized) time-points. From this analysis, we detected enrichment for markers of both pro- and antiinflammatory features, however, with stronger and significant enrichment for gene expression signatures associated with classical pro-inflammatory M1 macrophages. We have included these GSEA plots and gene set enrichment lists as supplementary materials (Supplementary Fig 6, Supplementary Table 6). We also performed GSEA against a broad curated set of immunologic gene sets (C7: immunologic signature gene sets, Molecular Signatures Database, (Liberzon et al., 2011)) and have included the list of signatures and enrichment scores as a supplementary table (Supplementary Table 6). 

“Phagocytosis could have anti-tumor effects through removal of live cancer cells or could be cancer-promoting if apoptotic cells are being rapidly cleared with concomitant activation of an immunosuppressive phenotype in the phagocytes (ie. efferocytosis).” 

We looked at efferocytosis-associated gene expression in our sequencing dataset (124 “efferocytosis” genes, GeneCards), and while we detected upregulation of certain genes associated with efferocytosis in p53EPS brains, we did not detect significant enrichment for the entire gene set. Furthermore, we did not detect up-regulation of key efferocytosis receptors including Axl and Tyro3 (Supplementary Table 1, 2), compared to normal brains. While efferocytosis may contribute to tumor growth and evolution, this GSEA combined with our functional data supporting an inhibitory role for phagocytes in p53EPS tumor initiation and engraftment following transplantation (Fig 4, Fig 5, Supplementary Fig 7), suggests that efferocytosis is not a major driver of tumor formation in our model. However, how efferocytosis affects tumor progression in our model and/or relapse following therapy will be an interesting feature to explore in the future using temporal manipulations of phagocytes and/or treatments with chemical inhibitors.

Author response image 1.

Gene Set Enrichment Analysis (GSEA) for efferocytosis-associated gene expression (124 “efferocytosis” genes in GeneCards) in tp53EPS tumor brains, compared to normal zebrafish brains. Normalized enrichment score (NES) and p-value are indicated. 

“Do the irf7/8 and chlodronate experiments distinguish between effects on microglia/macrophages and dendritic cells?”

In addition to microglia/macrophages, the IRF8 transcription factor has been shown to control survival and function of dendritic cells (Sichien et al., 2016). Chlodronate treatments are also used to deplete both macrophages and dendritic cells in vivo. Therefore, we cannot distinguish the effects of these manipulations in our experiments and have updated our manuscript throughout to reflect this.     

Reviewer #2:

“The authors state that oncogenic MAPK/AKT pathway activation drives glial-derived tumor formation. It would be important to include a wild-type or uninjected control for the pERK and pAKT staining shown in Fig1 I-K to aid in the interpretation of these results. Likewise, quantification of the pERK and pAKT staining would be useful to demonstrate the increase over WT, and would also serve to facilitate comparison with the similar staining in the KPG model (Supp Fig 2D).”

We have updated Fig 1 and Supplementary Fig 3D (formerly Fig 2D), to include histology from tumor-free uninjected control animals, as well as quantifications of p-ERK and p-AKT staining to highlight increased MAPK/AKT signaling pathway activation in our tumor model.  

“The authors use a transplantation assay to further test the tumorigenic potential of dissociated cells from glial-derived tumors. Listing the percentage of transplants that generate fluorescent tumor would be helpful to fully interpret these data. Additionally, it was not clear based on the description in the results section that the transplantation assay was an “experimental surrogate” to model the relapse potential of the tumor cell. This is first mentioned in the discussion. The authors may consider adding a sentence for clarity earlier in the manuscript as it helps the reader better understand the logic of the assay.” 

We have clarified in the text the percentage of transplants that generated fluorescent tumor (1625%, n=3 independent screens). This is also represented in Fig 5C,D. We also added text when introducing the transplantation assay, explaining that transplantation is frequently used as an experimental surrogate to assess relapse potential, and that our objective was to assess tumor cell propagation in the context of specific manipulations within the TME.  

“The authors nicely show high levels of immune cell infiltration and associations between microglia/macrophages and tumor cells. However, a quantification of the emergence of macrophages over time in relation to tumor initiation and growth would provide significant support to the observations of tumor suppressive activity of the phagocytes. Along these lines, the inclusion of a statement about when leukocytes emerge during normal development would be informative for those not familiar with the zebrafish model.”

In zebrafish, microglia colonize the neural retina by 48 hpf, and the optic tectum by 84 hpf (Herbomel et al., 2001), prior to when we typically observe lesions in our p53EPS brains. To validate the emergence of microglia prior to tumor formation in p53EPS, we have now used live confocal imaging through the brains of uninjected control and p53EPS injected zebrafish at 5, 7 and 9 dpf. As expected, microglia were present throughout the cephalic region and in the brain at 5 dpf (120 hpf). At this stage, p53EPS injected zebrafish brains displayed mosaic cellular expression of her4.1:mScarlet; however, cells were sparse and diffuse, and no large intensely fluorescent tumor-like clusters were detected at this stage (n=12/12 tumor negative). At 7 dpf, microglia were observed in the brains of control and p53EPS zebrafish; however, at this stage we detected clusters of her4.1:mScarlet+ cells (n=5/9), indicative of tumor formation. Lesions were found to be surrounded and/or infiltrated by mpeg:_EGFP+ microglia. Finally, at 9 dpf _her4.1:mScarlet+ expression became highly specific to tumor lesions, and these lesions were associated with _mpeg:_EGFP+ microglia/macrophages (n=8/8 of tumor-positive zebrafish). These descriptions along with representative images has been added to Figure 3.

“From the data provided in Figure 4G and Supp Fig 7b, the authors suggest that “increased p53EPS tumor initiation following Irf gene knock-down is a consequence of irf7 and irf8 loss-of-function in the TME.” Given the importance of the local microenvironment highlighted in this study, spatial information on the form of in situ hybridization to identify the relevant location of the expression change would be important to support this conclusion.”

We performed fluorescent in situ hybridization (using HCR RNA-FISH, Molecular Instruments) on whole mount control and irf7 CRISPR-injected p53EPG animals (her4.1:EGFRvIII +her4.1:PI3KCAH1047R + her4.1:GFP, GFP was used in this case because of probe availability).

Representative confocal projections through tumors, as well as single optical sections are presented and discussed in Figure 4, highlighting the location of irf7 expression change following gene knock-down. We found significant irf7 signal in and surrounding p53EPS tumors at early stages of tumor formation_. This expression was reduced and/or lost following _irf7 CRISPR gene targeting, consistent with RT-PCR data (Supplementary Fig 7).          

“The authors used neutral red staining that labels lysosomal-rich phagocytes to assess enrichment at the early stages of tumor initiation. The images in Figure 3 panel A should be labeled to denote the uninjected controls to aid in the interpretation of the data. In Supplemental Figure 6, the neutral red staining in the irf8 CRISPR-injected larvae looks to be increased, counter to the quantification. Can the authors comment if the image is perhaps not representative?”

We have updated Figure 3 and Supplementary Figure 6 to aid in the interpretation of our results. In Fig 3A, we used tumor-negative controls from our injected cohorts. This was done to control for exogenous transgene presence and/or over-expression prior to (or in the absence of) malignant transformation. In Supplementary Fig 6, our images are representative, but we have now used unprocessed images with arrowheads to highlight neutral-red positive foci for clarity. In our original manuscript the images contained software generated markers, which could have obscured and/or confused the neutral red staining we were trying the highlight.    

Recommendations For the Authors:

Reviewer #1: 

“The PI 3-kinase does a lot more than just activating mTOR and Akt – I would suggest modifying that sentence in the introduction.”

We have adjusted text in the introduction to reflect the broad role for PI3K signaling.

Reviewer #2:

“In Supplemental Fig 1, it would be helpful for the authors to provide a co-stain, such as DAPI to label all nuclei, which would allow the reader to assess the morphology of the cells in the context of the surrounding tissue.”

We have included brightfield images in Supplementary Fig 1, that together with her4.1:mScarlet fluorescence, should help readers assess tumor location and morphology in the context of surrounding tissue. Tumor cell morphology at high-resolution can be visualized in Fig 3, Movie 1 and Movie 2.

“The authors state that oncogenic MAPK/AKT pathway activation drives glial-derived tumor formation. The authors may consider testing if the addition of an inhibitor of MAPK signaling may prevent or decrease the formation of glial-derived tumors in this context to further support their results.” 

To further assess the role for MAPK activation, we decided to test the effect of 50uM AZD6244 MAPK inhibitor following transplantation of dissociated primary p53EPS cells into syngeneic CG1 strain zebrafish embryos, similar to as previously described (Modzelewska et al., 2016). Following 5 days of drug treatments, we did not detect significant differences in tumor engraftment or in tumor size between DMSO control and AZD6244-treated cohorts, suggesting that MAPK inhibition is not sufficient to prevent p53EPS engraftment and growth in our model. In the future, assessments of on-target drug effects, possible resistance mechanisms, and/or testing MAPK inhibitors in combination with other targeted agents including Akt and/or mTOR inhibitors (Edwards et al., 2006; McNeill et al., 2017; Schreck et al., 2020) will enhance our understanding of potential therapeutic strategies.

Author response image 2.

Dorsal views of 8 dpf zebrafish larvae engrafted with her4.1:mScarlet+ p53EPS tumor cells following treatment from 3-8dpf with 0.1% DMSO (control) or 50uM AZD6244. Tumor cell injections were performed at 2 dpf into syngeneic CG1 strain embryos. The percentage of total animals with persisting engraftment following drug treatments, as well as tumor size (microns squared, quantified using Carl Zeiss ZEN software) are shown for control and AZD6244 treated larvae. 

“Have the authors tested if EGFR and PI3KCA driven by other neural promoters produce similar results, or not? This would help support the specificity of her4.1 neural progenitors and glia as the cell of origin in this model.”

At this time, we have not tested other neural promoters. However, previous reports describe a zebrafish zic4-driven glioblastoma model with mesenchymal-like gene expression (Mayrhofer et al., 2017), supporting neural progenitors as a cell of origin. In the future it will be interesting to test sox2, nestin, and gfap promoters to further define and support her4.1-expressing neural progenitors and glia as the cell of origin in our model.

“Other leukocyte populations, such as neutrophils, can also respond to inflammatory cues. Can the authors comment if neutrophils are also observed in the TME?”

We performed initial assessments of neutrophils in the TME using our expression datasets as well as her4.1:EGFRvIII + her4.1:PI3KCAH1047R co-injection into Tg(mpx:EGFP) strain zebrafish. We observed tumor formation without significant infiltration of mpx:EGFP+ neutrophils. Future investigations will be important to assess differences in the contributions of different myeloidderived lineages in the TME of p53EPS, as well as how heterogeneity may be altered depending on different oncogenic drivers and/or stage of tumor progression, as seen in human glioblastoma (Friedmann-Morvinski and Hambardzumyan, 2023). We have added text in the disscussion section of our manuscript to indicate the possibility of neutrophils and/or other immune cell types contributing to p53EPS tumor biology. 

Author response image 3.

Control-injected tumornegative and tumor-positive Tg(mpx:EGFP) zebrafish at 10 dpf. Tg(mpx:EGFP) strain embryos were injected at the one-cell stage with her4.1:EGFRvIII + her4.1:PI3KCAH1047R + her4.1:mScarlet.

“It is not clear if the transcriptomics data has been deposited in a publicly available database, such as the Gene Expression Omnibus (GEO). Sharing of these data would be a benefit to the field and facilitate use in other studies.”

We have uploaded all transcriptomic data to GEO under accession GSE246295.

Author Response

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

We thank all three Reviewers for their comments and have revised the manuscript accordingly.

Reviewer #1 (Public Review):

The main objective of this paper is to report the development of a new intramuscular probe that the authors have named Myomatrix arrays. The goal of the Myomatrix probe is to significantly advance the current technological ability to record the motor output of the nervous system, namely fine-wire electromyography (EMG). Myomatrix arrays aim to provide large-scale recordings of multiple motor units in awake animals under dynamic conditions without undue movement artifacts and maintain long-term stability of chronically implanted probes. Animal motor behavior occurs through muscle contraction, and the ultimate neural output in vertebrates is at the scale of motor units, which are bundles of muscle fibers (muscle cells) that are innervated by a single motor neuron. The authors have combined multiple advanced manufacturing techniques, including lithography, to fabricate large and dense electrode arrays with mechanical features such as barbs and suture methods that would stabilize the probe's location within the muscle without creating undue wiring burden or tissue trauma. Importantly, the fabrication process they have developed allows for rapid iteration from design conception to a physical device, which allows for design optimization of the probes for specific muscle locations and organisms. The electrical output of these arrays is processed through a variety of means to try to identify single motor unit activity. At the simplest, the approach is to use thresholds to identify motor unit activity. Of intermediate data analysis complexity is the use of principal component analysis (PCA, a linear second-order regression technique) to disambiguate individual motor units from the wide field recordings of the arrays, which benefits from the density and numerous recording electrodes. At the highest complexity, they use spike sorting techniques that were developed for Neuropixels, a large-scale electrophysiology probe for cortical neural recordings. Specifically, they use an estimation code called kilosort, which ultimately relies on clustering techniques to separate the multi-electrode recordings into individual spike waveforms.

The biggest strength of this work is the design and implementation of the hardware technology. It is undoubtedly a major leap forward in our ability to record the electrical activity of motor units. The myomatrix arrays trounce fine-wire EMGs when it comes to the quality of recordings, the number of simultaneous channels that can be recorded, their long-term stability, and resistance to movement artifacts.

The primary weakness of this work is its reliance on kilosort in circumstances where most of the channels end up picking up the signal from multiple motor units. As the authors quite convincingly show, this setting is a major weakness for fine-wire EMG. They argue that the myomatrix array succeeds in isolating individual motor unit waveforms even in that challenging setting through the application of kilosort.

Although the authors call the estimated signals as well-isolated waveforms, there is no independent evidence of the accuracy of the spike sorting algorithm. The additional step (spike sorting algorithms like kilosort) to estimate individual motor unit spikes is the part of the work in question. Although the estimation algorithms may be standard practice, the large number of heuristic parameters associated with the estimation procedure are currently tuned for cortical recordings to estimate neural spikes. Even within the limited context of Neuropixels, for which kilosort has been extensively tested, basic questions like issues of observability, linear or nonlinear, remain open. By observability, I mean in the mathematical sense of well-posedness or conditioning of the inverse problem of estimating single motor unit spikes given multi-channel recordings of the summation of multiple motor units. This disambiguation is not always possible. kilosort's validation relies on a forward simulation of the spike field generation, which is then truth-tested against the sorting algorithm. The empirical evidence is that kilosort does better than other algorithms for the test simulations that were performed in the context of cortical recordings using the Neuropixels probe. But this work has adopted kilosort without comparable truth-tests to build some confidence in the application of kilosort with myomatrix arrays.

Kilosort was developed to analyze spikes from neurons rather than motor units and, as Reviewer #1 correctly points out, despite a number of prior validation studies the conditions under which Kilosort accurately identifies individual neurons are still incompletely understood. Our application of Kilosort to motor unit data therefore demands that we explain which of Kilosort’s assumptions do and do not hold for motor unit data and explain how our modifications of the Kilosort pipeline to account for important differences between neural and muscle recording, which we summarize below and have included in the revised manuscript.

Additionally, both here and in the revised paper we emphasize that while the presented spike sorting methods (thresholding, PCA-based clustering, and Kilosort) robustly extract motor unit waveforms, spike sorting of motor units is still an ongoing project. Our future work will further elaborate how differences between cortical and motor unit data should inform approaches to spike sorting as well as develop simulated motor unit datasets that can be used to benchmark spike sorting methods.

For our current revision, we have added detailed discussion (see “Data analysis: spike sorting”) of the risks and benefits of our use of Kilosort to analyze motor unit data, in each case clarifying how we have modified the Kilosort code with these issues in mind:

“Modification of spatial masking: Individual motor units contain multiple muscle fibers (each of which is typically larger than a neuron’s soma), and motor unit waveforms can often be recorded across spatially distant electrode contacts as the waveforms propagate along muscle fibers. In contrast, Kilosort - optimized for the much more local signals recorded from neurons - uses spatial masking to penalize templates that are spread widely across the electrode array. Our modifications to Kilosort therefore include ensuring that Kilosort search for motor unit templates across all (and only) the electrode channels inserted into a given muscle. In this Github repository linked above, this is accomplished by setting parameter nops.sigmaMask to infinity, which effectively eliminates spatial masking in the analysis of the 32 unipolar channels recorded from the injectable Myomatrix array schematized in Supplemental Figure 1g. In cases including chronic recording from mice where only a single 8-contact thread is inserted into each muscle, a similar modification can be achieved with a finite value of nops.sigmaMask by setting parameter NchanNear, which represents the number of nearby EMG channels to be included in each cluster, to equal the number of unipolar or bipolar data channels recorded from each thread. Finally, note that in all cases Kilosort parameter NchanNearUp (which defines the maximum number of channels across which spike templates can appear) must be reset to be equal to or less than the total number of Myomatrix data channels.”

“Allowing more complex spike waveforms: We also modified Kilosort to account for the greater duration and complexity (relative to neural spikes) of many motor unit waveforms. In the code repository linked above, Kilosort 2.5 was modified to allow longer spike templates (151 samples instead of 61), more spatiotemporal PCs for spikes (12 instead of 6), and more left/right eigenvector pairs for spike template construction (6 pairs instead of 3). These modifications were crucial for improving sorting performance in the nonhuman primate dataset shown in Figure 3, and in a subset of the rodent datasets (although they were not used in the analysis of mouse data shown in Fig. 1 and Supplemental Fig. 2a-f).”

Furthermore, as the paper on the latest version of kilosort, namely v4, discusses, differences in the clustering algorithm is the likely reason for kilosort4 performing more robustly than kilosort2.5 (used in the myomatrix paper). Given such dependence on details of the implementation and the use of an older kilosort version in this paper, the evidence that the myomatrix arrays truly record individual motor units under all the types of data obtained is under question.

We chose to modify Kilosort 2.5, which has been used by many research groups to sort spike features, rather than the just-released Kilosort 4.0. Although future studies might directly compare the performance of these two versions on sorting motor unit data, we feel that such an analysis is beyond the scope of this paper, which aims primarily to introduce our electrode technology and demonstrate that a wide range of sorting methods (thresholding, PCA-based waveform clustering, and Kilosort) can all be used to extract single motor units. Additionally, note that because we have made several significant modifications to Kilosort 2.5 as described above, it is not clear what a “direct” comparison between different Kilosort versions would mean, since the procedures we provide here are no longer identical to version 2.5.

There is an older paper with a similar goal to use multi-channel recording to perform sourcelocalization that the authors have failed to discuss. Given the striking similarity of goals and the divergence of approaches (the older paper uses a surface electrode array), it is important to know the relationship of the myomatrix array to the previous work. Like myomatrix arrays, the previous work also derives inspiration from cortical recordings, in that case it uses the approach of source localization in large-scale EEG recordings using skull caps, but applies it to surface EMG arrays. Ref: van den Doel, K., Ascher, U. M., & Pai, D. K. (2008). Computed myography: three-dimensional reconstruction of motor functions from surface EMG data. Inverse Problems, 24(6), 065010.

We thank the Reviewer for pointing out this important prior work, which we now cite and discuss in the revised manuscript under “Data analysis: spike sorting” [lines 318-333]:

“Our approach to spike sorting shares the same ultimate goal as prior work using skin-surface electrode arrays to isolate signals from individual motor units but pursues this goal using different hardware and analysis approaches. A number of groups have developed algorithms for reconstructing the spatial location and spike times of active motor units (Negro et al. 2016; van den Doel, Ascher, and Pai 2008) based on skin-surface recordings, in many cases drawing inspiration from earlier efforts to localize cortical activity using EEG recordings from the scalp (Michel et al. 2004). Our approach differs substantially. In Myomatrix arrays, the close electrode spacing and very close proximity of the contacts to muscle fibers ensure that each Myomatrix channel records from a much smaller volume of tissue than skin-surface arrays. This difference in recording volume in turn creates different challenges for motor unit isolation: compared to skin-surface recordings, Myomatrix recordings include a smaller number of motor units represented on each recording channel, with individual motor units appearing on a smaller fraction of the sensors than typical in a skin-surface recording. Because of this sensordependent difference in motor unit source mixing, different analysis approaches are required for each type of dataset. Specifically, skin-surface EMG analysis methods typically use source-separation approaches that assume that each sensor receives input from most or all of the individual sources within the muscle as is presumably the case in the data. In contrast, the much sparser recordings from Myomatrix are better decomposed using methods like Kilosort, which are designed to extract waveforms that appear only on a small, spatially-restricted subset of recording channels.”

The incompleteness of the evidence that the myomatrix array truly measures individual motor units is limited to the setting where multiple motor units have similar magnitude of signal in most of the channels. In the simpler data setting where one motor dominates in some channel (this seems to occur with some regularity), the myomatrix array is a major advance in our ability to understand the motor output of the nervous system. The paper is a trove of innovations in manufacturing technique, array design, suture and other fixation devices for long-term signal stability, and customization for different muscle sizes, locations, and organisms. The technology presented here is likely to achieve rapid adoption in multiple groups that study motor behavior, and would probably lead to new insights into the spatiotemporal distribution of the motor output under more naturally behaving animals than is the current state of the field.

We thank the Reviewer for this positive evaluation and for the critical comments above.

Reviewer #2 (Public Review):

Motoneurons constitute the final common pathway linking central impulse traffic to behavior, and neurophysiology faces an urgent need for methods to record their activity at high resolution and scale in intact animals during natural movement. In this consortium manuscript, Chung et al. introduce highdensity electrode arrays on a flexible substrate that can be implanted into muscle, enabling the isolation of multiple motor units during movement. They then demonstrate these arrays can produce high-quality recordings in a wide range of species, muscles, and tasks. The methods are explained clearly, and the claims are justified by the data. While technical details on the arrays have been published previously, the main significance of this manuscript is the application of this new technology to different muscles and animal species during naturalistic behaviors. Overall, we feel the manuscript will be of significant interest to researchers in motor systems and muscle physiology, and we have no major concerns. A few minor suggestions for improving the manuscript follow.

We thank the Reviewer for this positive overall assessment.

The authors perhaps understate what has been achieved with classical methods. To further clarify the novelty of this study, they should survey previous approaches for recording from motor units during active movement. For example, Pflüger & Burrows (J. Exp. Biol. 1978) recorded from motor units in the tibial muscles of locusts during jumping, kicking, and swimming. In humans, Grimby (J. Physiol. 1984) recorded from motor units in toe extensors during walking, though these experiments were most successful in reinnervated units following a lesion. In addition, the authors might briefly mention previous approaches for recording directly from motoneurons in awake animals (e.g., Robinson, J. Neurophys. 1970; Hoffer et al., Science 1981).

We agree and have revised the manuscript to discuss these and other prior use of traditional EMG, including here [lines 164-167]:

“The diversity of applications presented here demonstrates that Myomatrix arrays can obtain highresolution EMG recordings across muscle groups, species, and experimental conditions including spontaneous behavior, reflexive movements, and stimulation-evoked muscle contractions. Although this resolution has previously been achieved in moving subjects by directly recording from motor neuron cell bodies in vertebrates (Hoffer et al. 1981; Robinson 1970; Hyngstrom et al. 2007) and by using fine-wire electrodes in moving insects (Pfluger 1978; Putney et al. 2023), both methods are extremely challenging and can only target a small subset of species and motor unit populations. Exploring additional muscle groups and model systems with Myomatrix arrays will allow new lines of investigation into how the nervous system executes skilled behaviors and coordinates the populations of motor units both within and across individual muscles…

For chronic preparations, additional data and discussion of the signal quality over time would be useful. Can units typically be discriminated for a day or two, a week or two, or longer?

A related issue is whether the same units can be tracked over multiple sessions and days; this will be of particular significance for studies of adaptation and learning.

Although the yields of single units are greatest in the 1-2 weeks immediately following implantation, in chronic preparations we have obtained well-isolated single units up to 65 days post-implant. Anecdotally, in our chronic mouse implants we occasionally see motor units on the same channel across multiple days with similar waveform shapes and patterns of behavior-locked activity. However, because data collection for this manuscript was not optimized to answer this question, we are unable to verify whether these observations actually reflect cross-session tracking of individual motor units. For example, in all cases animals were disconnected from data collection hardware in between recording sessions (which were often separated by multiple intervening days) preventing us from continuously tracking motor units across long timescales. We agree with the reviewer that long-term motor unit tracking would be extremely useful as a tool for examining learning and plan to address this question in future studies.

We have added a discussion of these issues to the revised manuscript [lines 52-59]:

“…These methods allow the user to record simultaneously from ensembles of single motor units (Fig. 1c,d) in freely behaving animals, even from small muscles including the lateral head of the triceps muscle in mice (approximately 9 mm in length with a mass of 0.02 g 23). Myomatrix recordings isolated single motor units for extended periods (greater than two months, Supp. Fig. 3e), although highest unit yield was typically observed in the first 1-2 weeks after chronic implantation. Because recording sessions from individual animals were often separated by several days during which animals were disconnected from data collection equipment, we are unable to assess based on the present data whether the same motor units can be recorded over multiple days.”

Moreover, we have revised Supplemental Figure 3 to show an example of single motor units recorded >2 months after implantation:

Author response image 1.

Longevity of Myomatrix recordings In addition to isolating individual motor units, Myomatrix arrays also provide stable multi-unit recordings of comparable or superior quality to conventional fine wire EMG…. (e) Although individual motor units were most frequently recorded in the first two weeks of chronic recordings (see main text), Myomatrix arrays also isolate individual motor units after much longer periods of chronic implantation, as shown here where spikes from two individual motor units (colored boxes in bottom trace) were isolated during locomotion 65 days after implantation. This bipolar recording was collected from the subject plotted with unfilled black symbols in panel (d).

It appears both single-ended and differential amplification were used. The authors should clarify in the Methods which mode was used in each figure panel, and should discuss the advantages and disadvantages of each in terms of SNR, stability, and yield, along with any other practical considerations.

We thank the reviewer for the suggestion and have added text to all figure legends clarifying whether each recording was unipolar or bipolar.

Is there likely to be a motor unit size bias based on muscle depth, pennation angle, etc.?

Although such biases are certainly possible, the data presented here are not well-suited to answering these questions. For chronic implants in small animals, the target muscles (e.g. triceps in mice) are so small that the surgeon often has little choice about the site and angle of array insertion, preventing a systematic analysis of this question. For acute array injections in larger animals such as rhesus macaques, we did not quantify the precise orientation of the arrays (e.g. with ultrasound imaging) or the muscle fibers themselves, again preventing us from drawing strong conclusions on this topic. This question is likely best addressed in acute experiments performed on larger muscles, in which the relative orientations of array threads and muscle fibers can be precisely imaged and systematically varied to address this important issue.

Can muscle fiber conduction velocity be estimated with the arrays?

We sometimes observe fiber conduction delays up to 0.5 msec as the spike from a single motor unit moves from electrode contact to electrode contact, so spike velocity could be easily estimated given the known spatial separation between electrode contacts. However (closely related to the above question) this will only provide an accurate estimate of muscle fiber conduction velocity if the electrode contacts are arranged parallel to fiber direction, which is difficult to assess in our current dataset. If the arrays are not parallel, this computation will produce an overestimate of conduction velocity, as in the extreme case where a line of electrode contacts arranged perpendicular to the fiber direction might have identical spike arrival times, and therefore appear to have an infinite conduction velocity. Therefore, although Myomatrix arrays can certainly be used to estimate conduction velocity, such estimates should be performed in future studies only in settings where the relative orientation of array threads and muscle fibers can be accurately measured.

The authors suggest their device may have applications in the diagnosis of motor pathologies. Currently, concentric needle EMG to record from multiple motor units is the standard clinical method, and they may wish to elaborate on how surgical implantation of the new array might provide additional information for diagnosis while minimizing risk to patients.

We thank the reviewer for the suggestion and have modified the manuscript’s final paragraph accordingly [lines 182-188]:

“Applying Myomatrix technology to human motor unit recordings, particularly by using the minimally invasive injectable designs shown in Figure 3 and Supplemental Figure 1g,i, will create novel opportunities to diagnose motor pathologies and quantify the effects of therapeutic interventions in restoring motor function. Moreover, because Myomatrix arrays are far more flexible than the rigid needles commonly used to record clinical EMG, our technology might significantly reduce the risk and discomfort of such procedures while also greatly increasing the accuracy with which human motor function can be quantified. This expansion of access to high-resolution EMG signals – across muscles, species, and behaviors – is the chief impact of the Myomatrix project.”

Reviewer #3 (Public Review):

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

Strengths:

They presented convincing examples of EMG recordings with high signal quality using this new technology from a wide array of animal species, muscles, and behavior.

• The design included suture holes and pull-on tabs that facilitate implantation and ensure stable recordings over months.

• Clear presentation of specifics of the fabrication and implantation, recording methods used, and data analysis.

We thank the Reviewer for these comments.

Weaknesses:

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

We thank the Reviewer for the suggestion and have modified the manuscript accordingly [lines 170-174]:

“…how the nervous system executes skilled behaviors and coordinates the populations of motor units both within and across individual muscles. These approaches will be particularly valuable in muscles in which each motor neuron controls a very small number of muscle fibers, allowing fine control of oculomotor muscles in mammals as well as vocal muscles in songbirds (Fig. 2g), in which most individual motor neurons innervate only 1-3 muscle fibers (Adam et al. 2021).”

Reviewer #1 (Recommendations for The Authors):

I would urge the authors to consider a thorough validation of the spike sorting piece of the workflow. Barring that weakness, this paper has the potential to transform motor neuroscience. The validation efforts of kilosort in the context of Neuropixels might offer a template for how to convince the community of the accuracy of myomatrix arrays in disambiguating individual motor unit waveforms.

I have a few minor detailed comments, that the authors may find of some use. My overall comment is to commend the authors for the precision of the work as well as the writing. However, exercising caution associated with kilosort could truly elevate the paper by showing where there is room for improvement.

We thank the Reviewer for these comments - please see our summary of our revisions related to Kilosort in our reply to the public reviews above.

L6-7: The relationship between motor unit action potential and the force produced is quite complicated in muscle. For example, recent work has shown how decoupled the force and EMG can be during nonsteady locomotion. Therefore, it is not a fully justified claim that recording motor unit potentials will tell us what forces are produced. This point relates to another claim made by the authors (correctly) that EMG provides better quality information about muscle motor output in isometric settings than in more dynamic behaviors. That same problem could also apply to motor unit recordings and their relationship to muscle force. The relationship is undoubtedly strong in an isometric setting. But as has been repeatedly established, the electrical activity of muscle is only loosely related to its force output and lacks in predictive power.

This is an excellent point, and our revised manuscript now addresses this issue [lines 174-176]:

“…Of further interest will be combining high-resolution EMG with precise measurement of muscle length and force output to untangle the complex relationship between neural control, body kinematics, and muscle force that characterizes dynamic motor behavior. Similarly, combining Myomatrix recordings with high-density brain recordings….”

L12: There is older work that uses an array of skin mounted EMG electrodes to solve a source location problem, and thus come quite close to the authors' stated goals. However, the authors have failed to cite or provide an in-depth analysis and discussion of this older work.

As described above in the response to Reviewer 1’s public review comments, we now cite and discuss these papers.

L18-19: "These limitations have impeded our understanding of fundamental questions in motor control, ..." There are two independently true statements here. First is that there are limitations to EMG based inference of motor unit activity. Second is that there are gaps in the current understanding of motor unit recruitment patterns and modification of these patterns during motor learning. But the way the first few paragraphs have been worded makes it seem like motor unit recordings is a panacea for these gaps in our knowledge. That is not the case for many reasons, including key gaps in our understanding of how muscle's electrical activity relates to its force, how force relates to movement, and how control goals map to specific movement patterns. This manuscript would in fact be strengthened by acknowledging and discussing the broader scope of gaps in our understanding, and thus more precisely pinpointing the specific scientific knowledge that would be gained from the application of myomatrix arrays.

We agree and have revised the manuscript to note this complexity (see our reply to this Reviewer’s other comment about muscle force, above).

L140-143: The estimation algorithms yields potential spikes but lacking the validation of the sorting algorithms, it is not justifiable to conclude that the myomatrix arrays have already provided information about individual motor units.

Please see our replies to Reviewer #1s public comments (above) regarding motor unit spike sorting.

L181-182: "These methods allow very fine pitch escape routing (<10 µm spacing), alignment between layers, and uniform via formation." I find this sentence hard to understand. Perhaps there is some grammatical ambiguity?

We have revised this passage as follows [lines 194-197]:

"These methods allow very fine pitch escape routing (<10 µm spacing between the thin “escape” traces connecting electrode contacts to the connector), spatial alignment between the multiple layers of polyimide and gold that constitute each device, and precise definition of “via” pathways that connect different layers of the device.”

L240: What is the rationale for choosing this frequency band for the filter?

Individual motor unit waveforms have peak energy at roughly 0.5-2.0 kHz, although units recorded at very high SNR often have voltage waveform features at higher frequencies. The high- and lowpass cutoff frequencies should reflect this, although there is nothing unique about the 350 Hz and 7,000 Hz cutoffs we describe, and in all recordings similar results can be obtained with other choices of low/high frequency cutoffs.

L527-528: There are some key differences between the electrode array design presented here and traditional fine-wire EMG in terms of features used to help with electrode stability within the muscle. A barb-like structure is formed in traditional fine-wire EMG by bending the wire outside the canula of the needle used to place it within the muscle. But when the wire is pulled out, it is common for the barb to break off and be left behind. This is because of the extreme (thin) aspect ratio of the barb in fine wire EMG and low-cycle fatigue fracture of the wire. From the schematic shown here, the barb design seems to be stubbier and thus less prone to breaking off. This raises the question of how much damage is inflicted during the pull-out and the associated level of discomfort to the animal as a result. The authors should present a more careful statement and documentation with regard to this issue.

We have updated the manuscript to highlight the ease of inserting and removing Myomatrix probes, and to clarify that in over 100 injectable insertions/removal there have been zero cases of barbs (or any other part) of the devices breaking off within the muscle [lines 241-249]:

“…Once the cannula was fully inserted, the tail was released, and the cannula slowly removed. After recording, the electrode and tail were slowly pulled out of the muscle together. Insertion and removal of injectable Myomatrix devices appeared to be comparable or superior to traditional fine-wire EMG electrodes (in which a “hook” is formed by bending back the uninsulated tip of the recording wire) in terms of both ease of injection, ease of removal of both the cannula and the array itself, and animal comfort. Moreover, in over 100 Myomatrix injections performed in rhesus macaques, there were zero cases in which Myomatrix arrays broke such that electrode material was left behind in the recorded muscle, representing a substantial improvement over traditional fine-wire approaches, in which breakage of the bent wire tip regularly occurs (Loeb and Gans 1986).”

Reviewer #2 (Recommendations For The Authors):

The Abstract states the device records "muscle activity at cellular resolution," which could potentially be read as a claim that single-fiber recording has been achieved. The authors might consider rewording.

The Reviewer is correct, and we have removed the word “cellular”.

The supplemental figures could perhaps be moved to the main text to aid readers who prefer to print the combined PDF file.

After finalizing the paper we will upload all main-text and supplemental figures into a single pdf on biorXiv for readers who prefer a single pdf. However, given that the supplemental figures provide more technical and detailed information than the main-text figures, for the paper on the eLife site we prefer the current eLife format in which supplemental figures are associated with individual main-text figures online.

Reviewer #3 (Recommendations For The Authors):

• The work could be strengthened by showing examples of simultaneous recordings from different muscles.

Although Myomatrix arrays can indeed be used to record simultaneously from multiple muscles, in this manuscript we have decided to focus on high-resolution recordings that maximize the number of recording channels and motor units obtained from a single muscle. Future work from our group with introduce larger Myomatrix arrays optimized for recording from many muscles simultaneously.

• The implantation did not include mention of testing the myomatrix array during surgery by using muscle stimulation to verify correct placement and connection.

As the Reviewer points out electrical stimulation is a valuable tool for confirming successful EMG placement. However we did not use this approach in the current study, relying instead on anatomical confirmation of muscle targeting (e.g. intrasurgical and postmortem inspection in rodents) and by implanting large, easy-totarget arm muscles (in primates) where the risk of mis-targeting is extremely low. Future studies will examine both electrical stimulation and ultrasound methods for confirming the placement of Myomatrix arrays.

References cited above

Adam, I., A. Maxwell, H. Rossler, E. B. Hansen, M. Vellema, J. Brewer, and C. P. H. Elemans. 2021. 'One-to-one innervation of vocal muscles allows precise control of birdsong', Curr Biol, 31: 3115-24 e5.

Hoffer, J. A., M. J. O'Donovan, C. A. Pratt, and G. E. Loeb. 1981. 'Discharge patterns of hindlimb motoneurons during normal cat locomotion', Science, 213: 466-7.

Hyngstrom, A. S., M. D. Johnson, J. F. Miller, and C. J. Heckman. 2007. 'Intrinsic electrical properties of spinal motoneurons vary with joint angle', Nat Neurosci, 10: 363-9.

Loeb, G. E., and C. Gans. 1986. Electromyography for Experimentalists, First edi (The University of Chicago Press: Chicago, IL).

Michel, C. M., M. M. Murray, G. Lantz, S. Gonzalez, L. Spinelli, and R. Grave de Peralta. 2004. 'EEG source imaging', Clin Neurophysiol, 115: 2195-222.

Negro, F., S. Muceli, A. M. Castronovo, A. Holobar, and D. Farina. 2016. 'Multi-channel intramuscular and surface EMG decomposition by convolutive blind source separation', J Neural Eng, 13: 026027.

Pfluger, H. J.; Burrows, M. 1978. 'Locusts use the same basic motor pattern in swimming as in jumping and kicking', Journal of experimental biology, 75: 81-93.

Putney, Joy, Tobias Niebur, Leo Wood, Rachel Conn, and Simon Sponberg. 2023. 'An information theoretic method to resolve millisecond-scale spike timing precision in a comprehensive motor program', PLOS Computational Biology, 19: e1011170.

Robinson, D. A. 1970. 'Oculomotor unit behavior in the monkey', J Neurophysiol, 33: 393-403.

van den Doel, Kees, Uri M Ascher, and Dinesh K Pai. 2008. 'Computed myography: three-dimensional reconstruction of motor functions from surface EMG data', Inverse Problems, 24: 065010.

Author Response

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

Reviewer #1 (Recommendations For The Authors):

1. Experiments regarding the inducible expression of MukBEF: The authors should provide western blots or rt-qPCR for MukBEF expression at 40 min and 2H.

We provide now a western blot of MukB in non-induced and induced conditions as Figure 1-figure supplement 1D.

1. Experiments with RiTer and LiTer constructs:<br /> a. Authors compare the mukB deletion against wild type (Fig. 2C). It would be additionally informative if these comparisons are made for matP deletion and wild type as well. This will strengthen the conclusion that long-range interactions in ter do increase in the absence of matP.

We agree that the matP mutant may help the reader to compare the effect of the translocation in different backgrounds and have added it to the figure. This strengthens the conclusion that longrange interactions in ter do increase in the absence of matP in a rearranged chromosome, as observed in the WT configuration (Lioy et al., 2018).

b. Additionally, in Fig. 2C, it appears that there is some decrease in long-range interactions in the absence of mukB in ter1 (Riter). Is this a significant change?

The change observed is not significant. The results shown in Fig. 2C have been obtained using a 3C approach, which generated slightly more variability than Hi-C. Furthermore, we measured the range of contacts for the segment corresponding to Ter1 in RiTer (matS12-matS28), in different genetic contexts and different configurations. The results show that this level of variation is not significant (see graph below reporting two independent experiments).

Author response image 1.

Range of interactions measured on the interval matS12-matS18 in different genetic contexts and different configurations (MG1655 WT(1 and 2), ∆mukB, RiTer, RiTer ∆mukB).

1. Experiments with various matS organizations: These experiments are interesting and an important part of the paper. However, it is rather hard to visualize the chromosome conformations in the strains after transposition. To aid the reader (particularly with panel E), authors can provide schematics of the chromosome conformations and anticipated/ observed chromosomal interactions. Circular interaction plots would be useful here.

We thank the reviewer for this interesting remark; we have tried in the past to represent these interactions using a circular representation (see for example the web site of Ivan Junier; https://treetimc.github.io/circhic/index.html). However, this representation is not trivial to apprehend for nonspecialists, especially in strains with a rearranged chromosome configuration. Nonetheless, we have added graphical circular representations of the chromosome configurations to help the reader.

1. ChIP experiments:<br /> a. This section of the manuscript needs to be further strengthened. It is not clear whether the ChIP signal observed is significant (for example at T10 or T20 min, the peak value does not appear to go above 1.1 fold. Can the authors be sure that this small increase is not simply a consequence of increase in copy number of the loci around the origin, as replication has initiated?

The basal value of the ChIP on the non-replicated sequences (between 0-3.5 Mb for 10 minutes and 0-3 Mb for 20 minutes) is 0.8 and 0.7, respectively, whereas the mean value of the replicated sequence is 1.6 and 1.45. So the enrichment observed for these two points is about 2-fold, not 1.1 and it is 4 fold for t40min. These values were obtained by dividing the number of normalized reads in the ChIP (the number of reads at each position divided by the total number of reads) by the normalized reads of the input. Therefore, the increase in copy number is considered in the calculation. Furthermore, we added a supplementary figure (Figure Sup9) in which we performed a ChIP without tags on synchronized cells, and in this case, we did not observe any enrichment triggered by replication.

b. Authors make a conclusion that MukB loads behind the replication fork. However, the time resolution of the presented experiments is not sufficient to be certain of this. Authors would need to perform more time-resolved experiments for the same.

Reviewer 1 is correct; we attempted to discriminate whether the observed enrichment is (i) associated with the replication fork since we observed a decrease in the center of the enrichment at oriC as the maximum enrichment moves away with the replication fork after 20 and 40 minutes, or (ii) associated with the newly replicated sequence. To investigate this, we attempted to induce a single round of replication by shifting the cells back to 40°C after 10 minutes at 30°C. Unfortunately, replication initiation is not immediately halted by shifting the cells to 40°C, and we were unable to induce a single round of replication. To clarify our conclusions, we modified our manuscript to

“Altogether, these findings indicate that MukBEF is loaded into regions newly replicated either at the replication fork or even further behind it, except in the Ter region from which it would be excluded.”

c. Authors conclude that in the LiTer7 strain, MukB signal is absent from Ter2. However, when compared with the ChIP profiles by eye across panels in A and B, this does not seem to be significant. In the same results sections, authors state that there is a 3-fold increase in MukB signal in other regions. The corresponding graph does not show the same.

Rather than relying solely on the enrichment levels, which can be challenging to compare across different strains due to slight variations in replication levels, we believe there is a clear disruption in this profile that corresponds to the Ter2 sequence. Furthermore, this discontinuity in enrichment relative to the replication profile is also observable in the WT configuration. At T40min, MukB ChIPseq signals halt at the Ter boundary, even though Ter is actively undergoing replication, as evidenced by observations in the input data.

Regarding the fold increase of MukB, Reviewer 1 is correct; we overestimated this enrichment in the text and have now corrected it.

d. Authors should provide western blot of MukB-Flag.

We have added Supplementary Figure 1 D, which contains a Western blot of MukB-Flag.

1. The bioinformatic analysis of matS site distribution is interesting, but this is not followed upon. The figure (Fig 5) is better suited in the supplement and used only as a discussion point.

We acknowledge the reviewer's point, but we used this section to attempt to extend our findings to other bacteria and emphasize the observation that even though a few matS sites are necessary to inhibit MukBEF, the Ter domains are large and centered on dif even in other bacteria.

1. The discussion section is lacking many references and key papers have not been cited (paragraph 1 of discussion for example has no references).

The possibility that SMC-ScpAB and MukBEF can act independent of replication has been suggested previously, but are not cited or discussed. Similarly, there is some evidence for SMC-ScpAB association with newly replicated DNA (PMID 21923769).

We have added references to the suggested paragraph and highlighted the fact that MukBEF's activity independent of replication was already known. However, we believe that the situation is less clear for SMC-ScpAB in B. subtilis or C. crescentus. In a similar manner, we found no clear evidence that SMCScpAB is associated with newly replicated DNA in the referenced studies.

To clarify and enrich the discussion section, we have added a paragraph that provides perspective on the loading mechanisms of SMC-ScpAB and MukBEF.

1. There are minor typographical errors that should be corrected. Some are highlighted here:

a. Abstract: L5: "preferentially 'on' instead of 'in'"

b. Introduction: Para 1 L8: "features that determine"

c. Introduction: Para 2 L1: please check the phrasing of this line

d. Results section 2: L1: Ter "MD" needs to be explained

e. Page 8: Para 2: L6: "shows that 'a'"

g. Page 13: Para 2: "MukBEF activity...". This sentence needs to be fixed.

i. Figure 4: "input" instead of "imput"

We thank Reviewer 1 for pointing out all these grammatical or spelling mistakes. We have corrected them all.

f. Page 12: Para 2: "Xer" instead of "XDS"? *We added a reference to clarify the term.

h. Methods: ChIP analysis: Authors state "MatP peaks", however, reported data is for MukB

This description pertains to the matP peak detection shown in Supplementary Figure 3. We have incorporated this clarification into the text.

j. Supplementary figure legends need to be provided (currently main figure legends appear to be pasted twice)

Supplementary figure legends are provided at the end of the manuscript, and we have edited the manuscript to remove one copy of the figure legends.

k. Authors should ensure sequencing data are deposited in an appropriate online repository and an accession number is provided.

We waited for the appropriate timing in the editing process to upload our data, which we have now done. Additionally, we have added a data availability section to the manuscript, including sequence references on the NCBI.

Reviewer #2 (Recommendations For The Authors):

The authors largely avoid speculation on what might be the physiological relevance of the exclusion of MukBEF (and Smc-ScpAB) from the replication termination region (and the coordination with DNA replication). At this stage it would be helpful to present possible scenarios even if not yet supported by data. The authors should for example consider the following scenario: loop extrusion of a dif site in a chromosome dimer followed by dimer resolution by dif recombination leads to two chromosomes that are linked together by MukBEF (equivalent to cohesin holding sister chromatids together in eukaryotes but without a separase). This configuration (while rare) will hamper chromosome segregation. Is MatP particularly important under conditions of elevated levels of chromosome dimers? Could this even be experimentally tested? Other scenarios might also be entertained.

Even though we prefer to avoid speculations, we agree that we may attempt to propose some hypotheses to the reader. To do so, we have added a few sentences at the end of our discussion. “We may speculate, based on in vitro observations (Kumar et al., 2022), that MukBEF could interfere with TopIV activity and delay potential chromosome decatenation. Another possibility is that chromosome dimers resolved at the dif site may become trapped in loops formed by MukBEF, thus delaying segregation. But none of these possible scenarios are supported by data yet, and a major challenge for the future is to determine whether and how MukBEF may interfere with one or both of these processes.”

The manuscript text is well written. However, the labeling of strains in figures and text is sometimes inconsistent which can be confusing (LiTer Liter liter; e.g Riter Fig 2C). For consistency, always denote the number of matS sites in LiTer strains and also in the RiTer strain. The scheme denoting LiTer and RiTer strains should indicate the orientation of DNA segments so it is clear that the engineering does not involve inversion (correct?). Similarly: Use uniform labelling for time points: see T40mn vs 40mn vs T2H vs 2H

We have reviewed the manuscript to standardize our labeling. Additionally, we have included a schema in Figure 2, indicating the matS numbers at the Ter border to emphasize that the transposition events do not involve inversion.

matS sites do not have identical sequences and bind different levels of MatP (suppl fig 3). Does this possibly affect the interpretation of some of the findings (when altering few or only a single matS site). Maybe a comment on this possibility can be added.

We agree with the referee; we do not want to conclude too strongly about the impact of matS density, so we have added this sentence at the end of the section titled 'matS Determinants to Prevent MukBEF Activity':

“Altogether, assuming that differences in the matS sequences do not modify MatP's ability to bind to the chromosome and affect its capacity to inhibit MukBEF, these results suggested that the density of matS sites in a small chromosomal region has a greater impact than dispersion of the same number of matS sites over a larger segment”

Figure 5: show selected examples of matS site distribution in addition to the averaged distribution (as in supplemental figure)?

Figure 5 shows the median of the matS distribution based on the matS positions of 16 species as displayed in the supplementary figure. We believe that this figure is interesting as it represents the overall matS distribution across the Enterobacterales, Pasteurellales, and Vibrionales.

How do authors define 'background levels' (page 9)in their ChIP-Seq experiments? Please add a definition or reword.

We agree that the term 'background level' here could be confusing, so we have modified it to 'basal level' to refer to the non-replicating sequence. The background level can be observed in Supplementary Figure 9 in the ChIP without tags, and, on average, the background level is 1 throughout the entire chromosome in these control experiments.

This reviewer would naively expect the normalized ChIP-Seq signals to revolve around a ratio of 1 (Fig. 4)? They do in one panel (Figure 4B) but not in the others (Figure 4A). Please provide an explanation.

We thank the referee for this pertinent observation. An error was made during the smoothing of the data in Figure 4A, which resulted in an underestimation of the input values. This mistake does not alter the profile of the ChIP (it's a division by a constant) and our conclusions. We provide a revised version of the figure.

Inconsistent axis labelling: e.g Figure 4

Enterobacterals should be Enterobacterales (?)

KB should be kb

MB should be Mb

Imput should be Input

FlaG should be Flag

We have made the suggested modifications to the text.

'These results unveiled that fluorescent MukBEF foci previously observed associated with the Ori region were probably not bound to DNA' Isn't the alternative scenario that MukBEF bound to distant DNA segments colocalize an equally likely scenario? Please rephrase.

Since we lack evidence regarding what triggers the formation of a unique MukB focus associated with the origin and what this focus could represent, we have removed this sentence.

Reviewer #3 (Recommendations For The Authors):

The text is well-written and easy to follow, but I would suggest several improvements to make things clearer:

1. Many plots are missing labels or legends. (I) All contact plots such as Fig. 1C should have a color legend. It is not clear how large the signal is and whether the plots are on the same scale. (II)<br /> Ratiometric contact plots such as in Fig. 1D should indicate what values are shown. Is this a log ratio?

As indicated in the materials and methods section, the ratio presented on this manuscript was calculated for each point on the map by dividing the number of contacts in one condition by the number of contacts in the other condition. The Log2 of the ratio was then plotted using a Gaussian filter.

1. Genotypes and strain names are often inconsistent. Sometimes ΔmukB, ΔmatP, ΔmatS is used, other times it is just mukB, matP, matS; There are various permutations of LiTer, Liter, liter etc.

These inconsistencies have been corrected.

1. The time notation is unconventional. I recommend using 0 min, 40 min, 120 min etc. instead of T0, T40mn, T2H.

As requested, we have standardized and used conventional annotations.

1. A supplemental strain table listing detailed genotypes would be helpful.

A strain table has been added, along with a second table recapitulating the positions of matS in the different strains.

1. Fig. 1A: Move the IPTG labels to the top? It took me a while to spot them.

We have moved the labels to the top of the figure and increased the font size to make them more visible.

1. Fig 1C: Have these plots been contrast adjusted? If so, this should be indicated. The background looks very white and the transitions from diagonal to background look quite sharp.

No, these matrices haven't been contrast-adjusted. They were created in MATLAB, then exported as TIFF files and directly incorporated into the figure. Nevertheless, we noticed that the color code of the matrix in Figure 3 was different and subsequently adjusted it to achieve uniformity across all matrices.

7, Fig 1C: What is the region around 3 Mb and 4 Mb? It looks like the contacts there are somewhat MukBEF-independent.

The referee is right. In the presence of the plasmid pPSV38 (carrying the MukBEF operon or not), we repeatedly observed an increase of long range contacts around 3 Mb. The origin of these contacts is unknown.

1. Fig 1D: Have the log ratios been clipped at -1 and 1 or was some smoothing filter applied? I would expect the division of small and noisy numbers in the background region to produce many extreme values. This does not appear to be the case.

The referee is right, dividing two matrices generates a ratio with extreme values. To avoid this, the Log2 of the ratio is plotted with a Gaussian filter, as described before (Lioy et al., 2018).

1. Fig 1E: I recommend including a wild-type reference trace as a point of reference.

We have added the WT profile to the figure.

1. Fig 2: I feel the side-by-side cartoon from Supplemental Fig. 2A could be included in the main figure to make things easier to grasp.

We added a schematic representation of the chromosome configuration on top of the matrices to aid understanding.

1. Fig. 2C: One could put both plots on the same y-axis scale to make them comparable.

We have modified the axes as required.

1. Fig. 3C: The LiTer4 ratio plot has two blue bands in the 3-4.5 Mb region. I was wondering what they might be. These long-range contacts seem to be transposition-dependent and suppressed by MatP, is that correct?

The referee is right. This indicates that in the absence of MatP, one part of the Ter was able to interact with a distal region of the chromosome, albeit with a low frequency. The origin is not yet known.

1. Fig. 3E: It is hard to understand what is a strain label and what is the analyzed region of interest. The plot heading and figure legend say Ter2 (but then, there are different Ter2 variants), some labels say Ter, others say Ter2, sometimes it doesn't say anything, some labels say ΔmatS or ΔmatP, others say matS or matP, and so on.

We have unified our notation and add more description on the legend to clarify this figure :

“Ter” corresponds to the range of contacts over the entire Ter region, in the WT strain (WT Ter) or in the ΔmatP strain (ΔmatP Ter). The column WT matSX-Y corresponds to the range of contacts between the designated matS sites in the WT configuration. This portion of the Ter can be compared with the same Ter segment in the transposed strain (Ter2). Additionally, the matS20-28 segment corresponds to Ter2 in LiTer9, just as matS22-28 corresponds to Ter2 in LiTer7, and matS25-28 to Ter2 in LiTer4. The range of contacts of this segment was also measured in a ΔmatP or ΔmatS background.”

1. Fig. 4 and p.9: "Normalized ChIP-seq experiments were performed by normalizing the quantity of immuno-precipitated fragments to the input of MukB-Flag and then divide by the normalized ChIP signals at t0 to measure the enrichment trigger by replication."

This statement and the ChIP plots in Fig. 4A are somewhat puzzling. If the data were divided by the ChIP signal at t0, as stated in the text, then I would expect the first plot (t0) to be a flat line at value 1. This is not the case. I assume that normalized ChIP is shown without the division by t0, as stated in the figure legend.

The referee is right. This sentence has been corrected, and as described in the Methods section, Figure 4 shows the ChIP normalized by the input.

If that's true and the numbers were obtained by dividing read-count adjusted immunoprecipitate by read-count adjusted input, then I would expect an average value of 1. This is also not the case. Why are the numbers so low? I think this needs some more details on how the data was prepared.

The referee is right; we thank him for this remark. Our data are processed using the following method: the value of each read is divided by the total number of reads. A sliding window of 50 kb is applied to these normalized values to smooth the data. Then, the resulting signal from the ChIP is divided by the resulting signal from the input. This is what is shown in Figure 4. Unfortunately, for some of our results, the sliding window was not correctly applied to the input data. This did not alter the ChIP profile but did affect the absolute values. We have resolved this issue and corrected the figure.

Another potential issue is that it's not clear what the background signal is and whether it is evenly distributed. The effect size is rather small. Negative controls (untagged MukB for each timepoint) would help to estimate the background distribution, and calibrator DNA could be used to estimate the signal-to-background ratio. There is the danger that the apparent enrichment of replicated DNA is due to increased "stickiness" rather than increased MukBEF binding. If any controls are available, I would strongly suggest to show them.

To address this remark, a ChIP experiment with a non-tagged strain under comparable synchronization conditions has been performed. The results are presented as Supplementary Figure 9; they reveal that the enrichment shown in Figure 4 is not attributed to nonspecific antibody binding or 'stickiness’.

1. Fig. 4A, B: The y-axes on the right are unlabeled and the figure legends mention immunoblot analysis, which is not shown.

We labeled the y-axes as 'anti-Flag ChIP/input' and made corrections to the figure legend.

1. Fig. 4B: This figure shows a dip in enrichment at the Ter2 region of LiTer7, which supports the authors' case. Having a side-by-side comparison with WT at 60 min would be good, as this time point is not shown in Fig. 4A.

Cell synchronization can be somewhat challenging, and we have observed that the timing of replication restart can vary depending on the genetic background of the cells. This delay is evident in the case of LiTer7. To address this, we compared LiTer7 after 60 minutes to the wild type strain (WT) after 40 minutes of replication. Even though the duration of replication is 20 minutes longer in LiTer7, the replication profiles of these two strains under these two different conditions (40 minutes and 60 minutes) are comparable and provide a better representation of similar replication progression.

1. Fig. 4C: Highlighting the position of the replication origin would help to interpret the data.

We highlight oriC position with a red dash line

1. Fig. 4C: One could include a range-of-contact plot that compares the three conditions (similar to Fig. 1E).

We have added this quantification to Supplemental Figure 8

1. Supplemental Fig. 2A: In the LiTer15 cartoon, the flanking attachment sites do not line up. Is this correct? I would also recommend indicating the direction of the Ter1 and Ter2 regions before and after recombination.

In this configuration, attB and attR, as well as attL and attB', should be aligned but the remaining attR attL may not. We have corrected this misalignment. To clarify the question of sequence orientation, we have included in the figure legend that all transposed sequences maintain their original orientation.

1. Supplemental Fig. 3: One could show where the deleted matS sites are.

We added red asterisks to the ChIP representation to highlight the positions of the missing matS.

1. Supplemental Fig. 3B: The plot legend is inconsistent with panel A (What is "WT2")?

We have corrected it.

1. Supplemental Fig. 3C: The E-value notation is unusual. Is this 8.9 x 10^-61?

The value is 8.9 x 10-61; we modified the annotation.

23) Abstract: "While different features for the activity of the bacterial canonical SMC complex, SmcScpAB, have been described in different bacteria, not much is known about the way chromosomes in enterobacteria interact with their SMC complex, MukBEF."

Could this be more specific? What features are addressed in this manuscript that have been described for Smc-ScpAB but not MukBEF? Alternatively, one could summarize what MukBEF does to capture the interest of readers unfamiliar with the topic.

We modified these first sentences.

1. p.5 "was cloned onto a medium-copy number plasmid under control of a lacI promoter" Is "lacI promoter" correct? My understanding is that the promoter of the lacI gene is constitutive, whereas the promoter of the downstream lac operon is regulated by LacI. I would recommend providing an annotated plasmid sequence in supplemental material to make things clearer.

We modified it and replaced “ lacI promoter” with the correct annotation, pLac.

1. p. 5 heading "MukBEF activity does not initiate at a single locus" and p. 6 "Altogether, the results indicate that the increase in contact does not originate from a specific position on the chromosome but rather appears from numerous sites". Although this conclusion is supported by the follow-up experiments, I felt it is perhaps a bit too strong at this point in the text. Perhaps MukBEF loads slowly at a single site, but then moves away quickly? Would that not also lead to a flat increase in the contact plots? One could consider softening these statements (at least in the section header), and then be more confident later on.

We used 'indicate' and 'suggesting' at the end of this results section, and we feel that we have not overreached in our conclusions at this point. While it's true that we can consider other hypotheses, we believe that, at this stage, our suggestion that MukBEF is loaded over the entire chromosome is the simplest and more likely explanation.

1. p.7: "[these results] also reveal that MukBEF does not translocate from the Ori region to the terminus of the chromosome as observed with Smc-ScpAB in different bacteria."

This isn't strictly true for single molecules, is it? Some molecules might translocate from Ori to Ter. Perhaps clarify that this is about the bulk flux of MukBEF?

At this point, our conclusion that MukBEF does not travel from the ori to Ter is global and refers to the results described in this section. However, the referee is correct in pointing out that we cannot exclude the possibility that in a WT configuration (without a Ter in the middle of the right replicore), a specific MukBEF complex can be loaded near Ori and travel all along the chromosome until the Ter. To clarify our statement, we have revised it to 'reveal that MukBEF does not globally translocate from the Ori region to the terminus of the chromosome.' This change is intended to highlight the fact that we are drawing a general conclusion about the behavior of MukBEF and to facilitate its comparison with Smc-ScpAB in B. subtilis.

1. p. 10: The section title "Long-range contacts correlate with MukBEF binding" and the concluding sentence "Altogether, these results indicate that MukBEF promotes long-range DNA contacts independently of the replication process even though it binds preferentially in newly replicated regions" seem to contradict each other. I would rephrase the title as "MukBEF promotes long-range contacts in the absence of replication" or similar.

We agree with this suggestion and have used the proposed title.

1. p. 13: I recommend reserving the name "condensin" for the eukaryotic condensin complex and using "MukBEF" throughout.

We used MukBEF throughout.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary: 

Beyond what is stated in the title of this paper, not much needs to be summarized. eIF2A in HeLa cells promotes translation initiation of neither the main ORFs nor short uORFs under any of the conditions tested. 

Strengths: 

Very comprehensive, in fact, given the huge amount of purely negative data, an admirably comprehensive and well-executed analysis of the factor of interest. 

Weaknesses: 

The study is limited to the HeLa cell line, focusing primarily on KO of eIF2A and neglecting the opposite scenario, higher eIF2A expression which could potentially result in an increase in non-canonical initiation events. 

We thank the reviewer for the positive evaluation. As suggested by the reviewer in the detailed recommendations, we will clarify in the title, abstract and text that our conclusions are limited to HeLa cells. Furthermore, as suggested we will test the effect of eIF2A overexpression on the luciferase reporter constructs, and will upload a revised manuscript.

Reviewer #2 (Public review):

Summary 

Roiuk et al describe a work in which they have investigated the role of eIF2A in translation initiation in mammals without much success. Thus, the manuscript focuses on negative results. Further, the results, while original, are generally not novel, but confirmatory, since related claims have been made before independently in different systems with Haikwad et al study recently published in eLife being the most relevant. 

Despite this, we find this work highly important. This is because of a massive wealth of unreliable information and speculations regarding eIF2A role in translation arising from series of artifacts that began at the moment of eIF2A discovery. This, in combination with its misfortunate naming (eIF2A is often mixed up with alpha subunit of eIF2, eIF2S1) has generated a widespread confusion among researchers who are not experts in eukaryotic translation initiation. Given this, it is not only justifiable but critical to make independent efforts to clear up this confusion and I very much appreciate the authors' efforts in this regard.  

Strengths 

The experimental investigation described in this manuscript is thorough, appropriate and convincing. 

Weaknesses 

However, we are not entirely satisfied with the presentation of this work which we think should be improved. 

We thank the reviewer for the positive evaluation. We will revise the manuscript according to the reviewer's suggestions made in the detailed recommendations.

Reviewer #3 (Public review):

Summary: 

This is a valuable study providing solid evidence that the putative non-canonical initiation factor eIF2A has little or no role in the translation of any expressed mRNAs in cultured human (primarily HeLa) cells. Previous studies have implicated eIF2A in GTP-independent recruitment of initiator tRNA to the small (40S) ribosomal subunit, a function analogous to canonical initiation factor eIF2, and in supporting initiation on mRNAs that do not require scanning to select the AUG codon or that contain near-cognate start codons, especially upstream ORFs with non-AUG start codons, and may use the cognate elongator tRNA for initiation. Moreover, the detected functions for eIF2A were limited to, or enhanced by, stress conditions where canonical eIF2 is phosphorylated and inactivated, suggesting that eIF2A provides a back-up function for eIF2 in such stress conditions. CRISPR gene editing was used to construct two different knockout cell lines that were compared to the parental cell line in a large battery of assays for bulk or gene-specific translation in both unstressed conditions and when cells were treated with inhibitors that induce eIF2 phosphorylation. None of these assays identified any effects of eIF2A KO on translation in unstressed or stressed cells, indicating little or no role for eIF2A as a back-up to eIF2 and in translation initiation at near-cognate start codons, in these cultured cells. 

The study is very thorough and generally well executed, examining bulk translation by puromycin labeling and polysome analysis and translational efficiencies of all expressed mRNAs by ribosome profiling, with extensive utilization of reporters equipped with the 5'UTRs of many different native transcripts to follow up on the limited number of genes whose transcripts showed significant differences in translational efficiencies (TEs) in the profiling experiments. They also looked for differences in translation of uORFs in the profiling data and examined reporters of uORF-containing mRNAs known to be translationally regulated by their uORFs in response to stress, going so far as to monitor peptide production from a uORF itself. The high precision and reproducibility of the replicate measurements instil strong confidence that the myriad of negative results they obtained reflects the lack of eIF2A function in these cells rather than data that would be too noisy to detect small effects on the eIF2A mutations. They also tested and found no evidence for a recent claim that eIF2A localizes to the cytoplasm in stress and exerts a global inhibition of translation. Given the numerous papers that have been published reporting functions of eIF2A in specific and general translational control, this study is important in providing abundant, high-quality data to the contrary, at least in these cultured cells. 

Strengths: 

The paper employed two CRISPR knock-out cell lines and subjected them to a combination of high-quality ribosome profiling experiments, interrogating both main coding sequences and uORFs throughout the translatome, which was complemented by extensive reporter analysis, and cell imaging in cells both unstressed and subjected to conditions of eIF2 phosphorylation, all in an effort to test previous conclusions about eIF2A functioning as an alternative to eIF2. 

Weaknesses: 

There is some question about whether their induction of eIF2 phosphorylation using tunicamycin was extensive enough to state forcefully that eIF2A has little or no role in the translatome when eIF2 function is strongly impaired. Also, similar conclusions regarding the minimal role of eIF2A were reached previously for a different human cell line from a study that also enlisted ribosome profiling under conditions of extensive eIF2 phosphorylation; although that study lacked the extensive use of reporters to confirm or refute the identification by ribosome profiling of a small group of mRNAs regulated by eIF2A during stress. 

We thank the reviewer for the positive evaluation. We will revise the manuscript according to the recommendations made in the detailed recommendations. Regarding the two points mentioned here:

(1) The reason eIF2alpha phosphorylation does not increase appreciably is because unfortunately the antibody is very poor. The fact that the Integrated Stress Response (ISR) is induced by our treatment can be seen, for instance, by the fact that ATF4 protein levels increase strongly (in the very same samples where eIF2alpha phosphorylation does not increase much, in Suppl. Fig. 5E). We will strengthen the conclusion that the ISR is indeed activated with additional experiments/data as suggested by the reviewer.

(2) We agree that our results are in line with results from the previous study mentioned by the reviewer, so we will revise the manuscript to mention this other study more extensively in the discussion.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I suggest to state (already in the abstract, but perhaps also even in the title, definitely in the rest of the paper) that this analysis is limited to the HeLa cell line. 

As suggested, we have now specified in both the title and the abstract that the work is done in HeLa cells.

(2) In my view, it is a pity that the authors - given the tools are available - did not check the impact of high eIF2A levels on expression of individual mRNAs under normal and stress conditions. I am not suggesting to repeat ribo-seq in this setup, it would be too much to ask for, but re-examining some of the many reporters the authors generated with eIF2A overexpressed may point to some function, e.g. increased number of non-canonical initiation events (non-AUG-initiated)? If anything, the use of HeLa and the primary focus on eIF2A KO neglecting the prospective impact of eIF2A overexpression should be mentioned as two main limitations of this study. 

We thank the reviewer for the good suggestion to test our synthetic reporters with eIF2A overexpression. New Suppl. Fig. 4G now shows that overexpression of eIF2A does not affect translation of synthetic reporters carrying an ATG start codon in different initiation contexts, or carrying near-cognate start codons, in agreement with a lack of effect on translation which we previously observed with loss of eIF2A.

(3) Ribo-seq with eIF2A. Did the authors focus on ORFs that are known, or whose isoforms are known, to be non-AUG initiated? Would the loss of eIF2A decrease FPs in their CDSes under at least some conditions?

We have now assessed the read distribution on the eIF4G2 transcript in both the control and tunicamycin conditions ( Author response image 1). In our hands, eIF4G2 is one of the best examples of non-AUG initiation in human cells, since the main coding sequence starts with GTG and the CDS is well translated. Nonetheless, we do not observe any significant changes in read distribution (panels A-B) or overall translation efficiency of eIF4G2 upon eIF2A loss (panels C-D).

Author response image 1.

(A-B) Average reads occupancy on the eIF4G2 (ENST0000339995) transcript in DMSO treated (panel A, n=3) or tunicamycin treated samples (panel B, n=2) derived from either control (black) or eIF2A-KO (red) HeLa cells. Reads counts were normalized to sequencing depth and averaged between either 3 (DMSO-treated) or 2 (tunicamycin-treated) replicates. Graphs were then smoothened with a sliding window of 3 nt. (C-D) The total number of reads mapping to the eIF4G2 CDS, normalized to library sequencing depth per replica was quantified. No significant difference between control and eIF2A-KO cells was observed in either DMSO treated (panel C) or tunicamycin treated (panel D) cells. Significance by unpaired, two-sided, t-test. ns = not significant.

Thank you for giving me the opportunity to review this article.

Reviewer #2 (Recommendations for the authors):

While some of our suggestions below may be considered subtle, in our opinion they are important and it would be good if the authors consider them for their revision, we also have a couple of technical suggestions. 

(1) Abstract. 

The authors failed to identify the role of eIF2A in translation initiation and have provided compelling evidence that eIF2A is not involved in recognition of non-AUG codons as start codons nor in recruitment of initiator tRNA during stress conditions which are two activities most commonly misattributed to eIF2A. However, they have not exhausted all possible potential functions of eIF2A, see below, it is also possible that eIF2A may have a role not yet suggested by anyone and it may function in translation initiation in special circumstances that have not been tested yet. The authors indeed discuss such possibility in the Discussion section. Given that there is genetic evidence (that is unaffected by biochemical impurities) linking eIF2A to other initiation factors (5B and 4E), we are not yet convinced that eIF2A does not have any role in translation initiation and therefore we find the last sentence of the abstract premature. We suggest to soften this statement into something like this: whether eIF2A has any role in translation remains unknown, it may even have a role in a different aspect of RNA Biology. 

We agree with the reviewer. We changed the last sentence of the abstract to read as follows:

“It is possible that eIF2A plays a role in translation regulation in specific conditions that we have not tested here, or that it plays a role in a different aspect of RNA biology.”

(2) Recently eIF2A has been implicated in ribosomal frameshifting, see Wei et al 2023 DOI: 10.1016/j.celrep.2023.112987 

Could authors look into PEG10 mRNA ribosome profile to see if there are detectable statistically significant changes in footprint density downstream of frameshift site between WT and eIF2A Kos? It is likely that the coverage will be insufficient to give a definitive answer, but it is worth checking, it would be a pity to miss it. 

We thank the reviewer for this suggestion. We have now looked at the distribution of ribosome footprints on the PEG10 transcript variant that is expressed in HeLa cells (ENST00000482108) and indeed observe coverage downstream of the annotated stop codon, consistent with a frameshifting event that results in an extended protein isoform being translated. Visual assessment of the read distribution between the main ORF and the "ORF extension" does not show a substantial difference between control and eIF2A knock-out cells ( Author response image 2A-B). Additionally, we quantified the ratio of reads mapping to the PEG10 ORF upstream of the slippery site versus those mapping downstream, extending into the predicted longer protein. Nonetheless, we could not detect significant changes between control and eIF2A-KO cells in either tested condition ( Author response image 2C-D).

Author response image 2.

(A-B) Average reads occupancy on the PEG10 (ENST00000482108) transcript in DMSO treated (panel A, n=3) or tunicamycin treated samples (panel B, n=2) derived from either control (black) or eIF2A-KO (red) HeLa cells are shown. Reads counts were normalized to sequencing depth and averaged between either 3 (DMSO-treated) or 2 (tunicamycin-treated) replicates. Graphs were then smoothened with a sliding window of 3 nt. (C-D) The ratio of reads mapping to the ORF upstream of the slippery site to reads mapping to the predicted extended protein downstream to the slippery site is shown. Reads counts were normalized to the sequencing depth. Neither DMSO treated samples (panel C) nor tunicamycin treated samples (panel D) had a significant difference between control and eIF2A-KO cells. Significance by unpaired, two-sided, t-test. ns = not significant.

(3) Introduction 

Given the volume of unreliable claims regarding eIF2A in the literature and the overall confusion it is very difficult (may even be impossible) to write a clear coherent introduction into the topic. Nonetheless, there are few points that need to be taken into account. 

The authors state that eIF2A is capable to recruit initiator tRNA citing Zoll et al 2002. This activity was later shown to be a biochemical artefact (which was most likely reproduced by Kim et al 2018), eIF2A fraction was contaminated with eIF2D which does bind tRNAs in GTP-independent manner. eIF2A purified from RRL separates from initiator tRNA binding activity, see Dmitriev et al 2010 DOI: 10.1074/jbc.M110.119693. This point is also relevant to the second paragraph of Discussion, it should be acknowledged that it has been shown previously that eIF2A does not bind the initiator tRNA.

We appreciate the advice provided by the reviewer. We have modified both the introduction and the 2nd paragraph of the discussion to reflect that the tRNA-binding activity is due to contaminating eIF2D rather than eIF2A.

In many cases the authors describe certain claims as facts even though they refute them themselves. For example 

"Such eIF2A-driven non-AUG initiation events were shown to play a crucial role in different aspects of cell physiology and disease progression: cellular adaptation during the integrated stress response (Chen et al., 2019; Starck et al., 2016)"  While non-AUG initiation events do play crucial roles in different aspects of cell physiology (reviewed in Andreev et al 2023 doi: 10.1186/s13059-022-02674-2) eIF2A has nothing to do with it as the authors show themselves. Therefore different language should be used, e.g.. "eIF2A has been suggested (or proposed or reported) to be responsible for non-AUG initiation events that were shown to play ..." 

The word "shown" is used in many other instances for the claims that the authors refute. "Shown" is only appropriate for strong evidence that leaves little doubt. 

We agree with the reviewer and made the suggested changes in the text.

(4) Supplementary Fig. 1. 

Panel C is used to argue that eIF2A has a higher concentration than in the nucleus, perhaps it is worth explaining how this conclusion was drawn. If levels in cytoplasm are comparable to GAPDH and Tubulin but less than c-Myc in nucleus does it really mean that there is less eIF2A in the nucleus than in cytoplasm? This is not obvious to us. Also, presumably WCL stands for Whole Cell Lysate, it would be nice to introduce this abbreviation somewhere. 

To compare levels of eIF2A in the nuclear and cytosolic fractions, we lysed the two fractions in equal volumes of buffer (i.e. the cytosolic fraction was extracted in 200 µl of hypotonic buffer, and the nuclear fraction was extracted in 200 µl of cell extraction buffer). This assures that per microliter of lysate we have the same number of "cytosols" or nuclei. Hence, equal intensity bands in the cytosolic and nuclear fractions would mean that half of the protein is in the nucleus and half is in the cytosol. We originally described this in the Methods section, but now also mention it in the Results and in the figure legend.

We replaced WCL with "whole cell" in the figure. 

(5) The differential translation analysis is described very briefly "To obtain values of translation efficiency, log2 fold changes, and adjusted p values the DESeq2 software package was used". Was TE calculated based on ribosome footprint to RNA-seq ratios? How exactly DESeq2 was used here? TE measured in this way spuriously correlates with RNA-seq values, see Larsson et al 2010 DOI: 10.1073/pnas.1006821107, perhaps it would be worse assessing differential translation with anota2seq (Oertlin et al 2019 doi: 10.1093/nar/gkz223.)? Anota2seq avoids calculating the ratios and enables comprehensive analysis of differential translation including detection of buffered translation which might be the case here while avoiding artefacts that may arise from varying RNA levels.  

We now specified in more detail in the Methods section how we analyzed the data. Indeed, the DeSeq2 was used on translation efficiency values, which we calculated as the ratio of ribosome footprints to RNA-seq. 

As suggested, we have now also performed the analysis using anota2seq (Suppl. Fig. 3C) and this analysis identified zero transcripts that are translationally regulated, in agreement with our analysis.

(6) Section "eIF2a-inactivating stresses do not redirect tRNA delivery function to eIF2A." 

The description of ISR mechanism is a bit inaccurate. Strictly speaking eIF2alpha phosphorylation does not inactivate it eIF2alpha. It results in formation of a very stable eIF2*GDP*eIF2B complex, thus severely depleting eIF2B which serves as a GEF for eIF2. This in turn reduces the ternary complex (eIF2*GTP*tRNAi) concentration since there is no free eIF2B to exchange GDP for GTP. Without getting into much detail, we think it would be more accurate to say that eIF2alpha phosphorylation leads to ternary complex depletion instead of saying that stress inactivates eIF2alpha. 

We agree with the reviewer - we were trying to use simple, compact wording. We have now reworded the section title to "No detectable role for eIF2A in translation when eIF2 is inhibited" and rephrased the subsequent text to be correct.

Also the subtitle uses eIF2a with small a that stands for alpha which potentially could lead to substantial confusion since in this case the difference between eIF2alpha and eIF2A is only in capitalisation of the last letter, many text-mining engines such as modern LLMs may not be able to pick the differences. Perhaps it would be better to refer to eIF2alpha by the HGNC approved name of its gene - eIF2S1 to avoid further confusions. For clarity it may be stated at the beginning that eIF2S1 is commonly known as eIF2alpha. 

We thank the reviewer for this point. We have removed all instances of eIF2a (with lowercase a) from the manuscript to avoid this source of confusion. In the first instance of eIF2a we also added the official HGNC gene name. However, we prefer to use eIF2a instead of eIF2S1 because people outside the translation field tend to know the subunit as eIF2a, and we think it is important that also people outside the translation field read this manuscript, since some of the questionable papers on eIF2A come from labs working at the interface between translation and other fields.

Minor 

Introduction 

(7) "uses the CAT anticodon" change CAT to CAU 

We corrected CAT to CAU

(8) "In the canonical initiation pathway", change "canonical" to "most common", canonical is somewhat a judgemental statement that originates in theology. Same applies to numerous occurrences of "canonical AUG", simply using "AUG" would be simpler and more accurate as you will avoid giving impression that there are "non-canonical AUGs".  

Done.

(9) "eIF2A was initially considered to be a functional analogue of prokaryotic IF2 (Merrick and Anderson, 1975), however later this role was reassigned to the above-mentioned heterotrimeric factor eIF2 (a,b,g) (Levin et al., 1973)." - there is a chronological contradiction within this sentence, the initial consideration is attributed to 1975 while its later reassignment to 1973. 

We are grateful to the reviewer for spotting this mistake. There was a citation problem; we fixed it and now cite the correct paper for the initial discovery of eIF2A to PMID 5472357 (Shafritz et al 1970).

(10) "On the other hand, studies on the role of eIF2A on viral IRES translation have arrived at conflicting results." Remove "On the other hand" since conflicting results have been mentioned above. In fact the entire sentence is somewhat redundant given prior "For example, eIF2A has been studied in the context of internal ribosome entry sites (IRES), where it was found to act both as a suppressor and an activator of IRESmediated initiation."  

We have rewritten the paragraph to make it more coherent.

(11) Fig. 1. C-D. is using CHX abbreviation for cycloheximide, this need to be mentioned on the legend or elsewhere in the text. Otherwise CHX may not be clear for a reader uninitiated in ribosome profiling. 

We now mention in the figure legend that CHX stands for cycloheximide and indicate that it was used as a negative control to block translation. 

(12) Page 7, section "Ribosome profiling reveals a few eIF2Adependent transcripts" 

In this section you describe ribosome profiling experiments and identify few transcripts whose translation seems to be changing based on ribosome profiling data. Then you attempt to verify them using gene expression reporters and reasonably suggest that these are false positives. In essence this section argues that there are no eIF2A-dependent transcripts, therefore the title of this subsection is misleading, it makes sense to rename it so that it better reflects the content of this section. 

We agree and have renamed the section to "Ribosome profiling identifies no eIF2Adependent transcripts"

(13) Page 8, top. Rephrase "To do this, we performed ribosome profiling on control and eIF2AKO cells, which sequences the mRNA footprints protected by ribosomes."  

Fixed.

(14) Page 10, bottom. "Several studies have reported that eIF2A can delivery alternative initiator tRNAs to uORFs with nearcognate start codons". Change "delivery" to "deliver". 

Thanks for spotting it. We corrected to “deliver”

(15) Page 13 "This suggests that, as in non-stressed conditions, eIF2A has a minimal effect on global translation also when eIF2a activity is low." - rephrase to avoid impression that eIF2alpha activity is low in normal conditions, also please see comment #6 above. 

We fixed this sentence to read: “This suggests that, as in non-stressed conditions, eIF2A has a minimal effect on global translation also when the integrated stress response is active.”

Reviewer #3 (Recommendations for the authors):

- The experimental data in Fig. S5E do not support the claim of increased eIF2 phosphorylation on TM treatment; although, comparing Fig. S5A with Fig. 1B supports a marked reduction in bulk translation and the reporter data in Fig. 4A show the expected induction of the uORF-containing reporters by TM. Because these are the conditions employed for ribosome profiling in stress conditions shown in Fig. 4B, it would be reassuring to document TM-induced translational efficiencies of ATF4 and the other known mRNAs resistant to eIF2 phosphorylation in the ribosome profiling data, including gene browser images of the replicate experiments. If the induction of TEs by TM for such mRNAs was not robust, it would be valuable to repeat the analysis using arsenite (SA) treatment, which produces a greater inhibition of bulk translation. 

Unfortunately, the eIF2alpha antibody is not very good and also detects the nonphosphorylated protein, causing high background and poor apparent induction in response to tunicamycin. The fact that the ISR was activated is visible from the induction of ATF that was assessed by western blot in the Suppl. Fig. 5E. To ensure that our ribosome profiling libraries also recorded the activation of ISR we built single gene plots for ATF4 both in control and HeLa eIF2A-KO cell. As shown in  Author response image 3 A&B in both cell lines tunicamycin treatment led to the induction of ATF4. This can also be seen by the 4-fold induction in ATF4 translation efficiency in response to tunicamycin in both WT and eIF2A-KO cells ( Author response image 3C). Additionally, we checked that another marker induced by tunicamycin, HSPA5, is also translationally upregulated in both cell lines, as well as the downstream target of ATF4 – PPP1R15B. ( Author response image 3C). 

Author response image 3.

(A-B) Average read occupancy on the ATF4 (ENST00000674920) transcript in DMSO treated (n=3) or tunicamycin treated samples (n=2) derived from either control (panel A) or eIF2A-KO (panel B) HeLa cells are shown. Read counts were normalized to sequencing depth and averaged between either 3 (DMSO-treated) or 2 (tunicamycin-treated) replicates. Graphs were then smoothened with a sliding window of 3 nt. (C) Scatter plot of log2(fold change) of Translation Efficiency TM/DMSO for control cells on the xaxis versus eIF2AKO cells on the y-axis. The induction of ATF4 as well as the downstream target PPP1R15B are shown. The upregulation of HSP5A translation, the other hallmark of ER-stress induced by tunicamycin treatment is shown.

- It should be pointed out in the text that in both published studies being cited here of cells lacking eIF2A, that by Gaikwad et al. on a yeast eIF2A deletion mutant, and that by Ichihara et al. on human HEK293 CRISPR KO cells, the analyses included stress conditions in which eIF2 phosphorylation is induced (amino acid starvation or SA treatment, respectively), as was conducted here.  

Good point - we added this information into the introduction: 

"Furthermore, loss of eIF2A in several systems did not recapitulate these effects on non-AUG initiation in either non-stressed or stress conditions (caused either by amino acid depletion or sodium arsenate treatment) (Gaikwad et al., 2024; Ichihara et al., 2021)."

- The Ichihara et al. (2021) study just mentioned reached some of the same conclusions for HEK cells obtained here by conducting ribosome profiling in untreated and SA-treated cells, finding only 1 mRNA (untreated) or four mRNAs (SA-treated cells) that showed significantly reduced TEs in the eIF2A knockout vs. parental cells. It seems appropriate for the authors to expand their treatment of this prior work by summarizing its findings in some detail and also noting how their study goes beyond this previous one. 

We have added a paragraph to the discussion pointing out that our data agree fully with Ichihara et al. (2021), and that Ichihara et al. (2021) also found only very few mRNAs that change in TE upon loss of eIF2A in either non-stressed or stressed conditions.

Author response:

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

Reviewer #1

Summary:

In this paper, the authors performed molecular dynamics (MD) simulations to investigate the molecular basis of the association of alpha-synuclein chains under molecular crowding and salt conditions. Aggregation of alpha-synuclein is linked to the pathogenesis of Parkinson's disease, and the liquid-liquid phase separation (LLPS) is considered to play an important role in the nucleation step of the alpha-synuclein aggregation. This paper re-tuned the Martini3 coarse-grained force field parameters, which allows long-timescale MD simulations of intrinsically disordered proteins with explicit solvent under diverse environmental perturbation. Their MD simulations showed that alpha-synuclein does not have a high LLPS-forming propensity, but the molecular crowding and salt addition tend to enhance the tendency of droplet formation and therefore modulate the alpha-synuclein aggregation. The MD simulation results also revealed important intra- and inter-molecule conformational features of the alpha-synuclein chains in the formed droplets and the key interactions responsible for the stability of the droplets. These MD simulation data add biophysical insights into the molecular mechanism underlying the association of alpha-synuclein chains, which is important for understanding the pathogenesis of Parkinson's disease.

Strengths:

(1) The re-parameterized Martini 3 coarse-grained force field enables the large-scale MD simulations of the intrinsically disordered proteins with explicit solvent, which will be useful for a more realistic description of the molecular basis of LLPS.

(2) This paper showed that molecular crowding and salt contribute to the modulation of the LLPS through different means. The molecular crowding minimally affects surface tension, but adding salt increases surface tension. It is also interesting to show that the aggregation pathway involves the disruption of the intra-chain interactions arising from C-terminal regions, which potentially facilitates the formation of inter-chain interactions.

We thank the reviewer for pointing out the strengths of our study.

Weaknesses:

(1) Although the authors emphasized the advantage of the Martini3 force field for its explicit description of solvent, the whole paper did not discuss the water's role in the aggregation and LLPS.

We thank the reviewer for pointing this out. We agree that we have not explored or discussed the role of water in aS aggregation or LLPS. We would like to convey that we would like to explore that in detail in a separate study altogether. However we have updated the “Discussion” section with the following lines to convey to the readers the importance water plays in aggregation and LLPS of aS.

Page 24: “The significance of the solvent in alpha-synuclein (αS) aggregation remains underexplored. Recent studies [26, 55] underscore the pivotal role of water as a solvent in LLPS. It suggests that comprehending the solvent’s role, particularly water, is essential for attaining a deeper grasp of the thermodynamic and physical aspects of αS LLPS and aggregation. By delving into the solvent’s contribution, researchers can uncover additional factors influencing αS aggregation. Such insights hold the potential to advance our comprehension of protein aggregation phenomena, crucial for devising strategies to address diseases linked to protein misfolding and aggregation, notably Parkinson’s disease. Future investigations focusing on elucidating the interplay between αS, solvent (especially water), and other environmental elements could yield valuable insights into the mechanisms underlying LLPS and aggregation. Ultimately, this could aid in the development of therapeutic interventions or preventive measures for Parkinson’s and related diseases.”

(2) This paper discussed the effects of crowders and salt on the surface tension of the droplets.

The calculation of the surface tension relies on the droplet shape. However, for the formed clusters in the MD simulations, the typical size is <10, which may be too small to rigorously define the droplet shape. As shown in previous work cited by this paper [Benayad et al., J. Chem. Theory Comput. 2021, 17, 525−537], the calculated surface tension becomes stable when the chain number is larger than 100.

We appreciate the insightful feedback from the reviewer. However, we would like to emphasize that the αS droplets exhibit a highly liquid-like behavior, characterized by frequent exchanges of chains between the dense and dilute phases, alongside a slow aggregation process. In the study by Benayad et al. (2020, JCTC) [ref. 30], FUS-LCD was the protein of choice at concentrations in the (mM) range. FUS-LCD is known to undergo very rapid LLPS at concentrations lower than 100 (μM) where for αS the critical concentration for LLPS is 500 (μM) and undergoes slower aggregation than FUS. Moreover, the diffusion constant of αS inside newly formed droplets (no liquid to solid phase transition has occurred) has been estimated to be 0.23-0.58 μm2/s (Ray et al, 2020, Nat. Comm.). The value of diffusion constant for FUS-LCD inside LLPS droplets has been estimated to be 0.17 μm2/s (Murthy et al. 2023, Nat. Struct. and Mol. Biol.). These prove that αS forms droplets that are less viscous than that formed by FUS-LCD. This dynamic nature impedes the formation of large droplets in the simulations, making it challenging to rigorously calculate surface tension from interfacial width, which, in turn, necessitates the computation of g(r) between water and the droplet.

Furthermore, it's essential to note that our primary aim in calculating surface tension was not to determine its absolute value. Rather, we aimed to compare surface tensions obtained for the three distinct environments explored in this study. Hence, our primary objective is to compare the distributions of surface tensions rather than focusing solely on the mean values obtained. The distributions shown in Figure 4a clearly show a trend which we have stated in the article.

(3) In this work, the Martini 3 force field was modified by rescaling the LJ parameters \epsilon and \sigma with a common factor \lambda. It has not been very clearly described in the manuscript why these two different parameters can be rescaled by a common factor and why it is necessary to separately tune these two parameters, instead of just tuning the coefficient \epsilon as did in a previous work [Larsen et al., PLoS Comput Biol 16: e1007870].

We thank the reviewer for the comment. We think that the distance of the first hydration layer also should have an impact on aggregation/LLPS. Here we are scaling both the epsilon and sigma. A higher epsilon of water-protein interactions mean higher the energy required for removal of water molecules (dehydration) when a chain goes from the dilute to the dense phase. A higher sigma on the other hand means that the hydration shell will also be at a larger distance making dehydration easier. Moreover, tuning both (either by same or different parameter) required a change of the overall protein-water interaction by only 1%, thereby requiring only considerably minimal change in forcefield parameters (compared to the case where only epsilon is being tuned which required 6-10% change in epsilon from its original values.) . Thus we think one of the ways of tuning water-protein interactions which requires minimal retuning of Martini 3 is by optimizing both epsilon and sigma. However whether a single scaling parameter is good enough requires further exploration and is outside the scope of the current study. More importantly it would introduce another free parameter into the system and the lesser the number of free parameters, the better. For this study, a single parameter sufficed as depicted in Figure 9. To inform the readers of why we chose to scale both sigma and epsilon, we have added the following in the main text:

Page 25-26: “Increasing the ϵ value of water-protein interactions results in a higher energy demand for removing water molecules (dehydration) as a chain transitions from the dilute to the dense phase. Conversely, a higher σ value implies that the hydration shell will be at a greater distance, facilitating dehydration if a chain moves into the dilute phase. Therefore, adjusting water-protein interactions based on the protein’s single-chain behavior may not significantly influence the protein’s phase behavior. Furthermore, fine-tuning both ϵ and σ parameters only requires a minimal change in the overall protein-water interaction (1%). As a result, this adjustment minimally alters the force field parameters.”

(4) Both the sizes and volume fractions of the crowders can affect the protein association. It will be interesting to perform MD simulations by adding crowders with various sizes and volume fractions. In addition, in this work, the crowders were modelled by fullerenes, which contribute to protein aggregation mainly by entropic means as discussed in the manuscript. It is not very clear how the crowder effect is sensitive to the chemical nature of the crowders (e.g., inert crowders with excluded volume effect or crowders with non-specific attractive interactions with proteins, etc) and therefore the force field parameters.

We thank the reviewer for a potential future direction. In this investigation our main focus was to simulate the inertness features of crowders only, to ensure that only entropic effect of the crowders are explored. Although this study focuses on the factors that enable aS to form an aggregates/LLPS under different environmental conditions, it would be interesting to explore in a systematic way the mechanism of action of crowders of varying shapes, sizes and interactions. Therefore we added the following lines in the “Discussion” section to let the readers know that this is also a future prospect of investigation.

Page 22: “Under physiological conditions, crowding effects emerge prominently. While crowders are commonly perceived to be inert, as has been considered in this investigation, the morphology, dimensions, and chemical interactions of crowding agents with αS in both dilute and dense phases may potentially exert considerable influence on its LLPS. Hence, a comprehensive understanding through systematic exploration is another avenue that warrants extensive investigation.”

Reviewer #1 (Recommendations For The Authors):

(1) Figure S1. The title of the figure and the description in the figure caption are inconsistent?

We thank the reviewer for the comment and we have updated the article with the correct caption.

(2) Page 14, line 3, the authors may want to provide more descriptions of the "ms1", "ms2", and "ms3" for better understanding.

We are grateful to the reviewer for pointing this out. We have added a line describing in brief what “ms1”, “ms2” and “ms3” represent. It reads “Subsequent to the investigation, we utilize three representative conformations, each corresponding to one of the macrostates. We designate these macrostates as 1 (ms1), 2 (ms2), and 3 (ms3) (Figure S7)” (Page 28)

(3) Page 20, the authors may want to briefly explain how the normalized Shannon entropy was calculated.

We thank the reviewer for pointing this out. This is plain Shannon Entropy and the word “normalized” should not have been there. To avoid confusion we have provided the equation we have used to calculate the Shannon entropy (Eq 8) (Page 21).

Reviewer #2 (Public Review):

In the manuscript "Modulation of α-Synuclein Aggregation Amid Diverse Environmental Perturbation", Wasim et al describe coarse-grained molecular dynamics (cgMD) simulations of α-Synuclein (αS) at several concentrations and in the presence of molecular crowding agents or high salt. They begin by bench-marking their cgMD against all-atom simulations by Shaw. They then carry 2.4-4.3 µs cgMD simulations under the above-noted conditions and analyze the data in terms of protein structure, interaction network analysis, and extrapolated fluid mechanics properties. This is an interesting study because a molecular scale understanding of protein droplets is currently lacking, but I have a number of concerns about how it is currently executed and presented.

We thank the reviewer for finding our study interesting.

(1) It is not clear whether the simulations have reached a steady state. If they have not, it invalidates many of their analysis methods and conclusions.

We have used the last 1 μs (1.5-2.5 1 μs) from each simulation for further analysis in this study. To understand whether the simulations have reached steady state or not, we plot the time profile of the concentration of the protein in the dilute phase for all three cases.

Author response image 1.

Except for the scenario of only αS (Figures a and b), the rest show very steady concentrations across various sections of the trajectory (Figures c-f). The larger sudden fluctuations observed inFigures a and b are due to the fact that only αS undergo very slow spontaneous aggregation and owing to the fact that the dense phase itself is very fluxional, addition/removal of a few chains to/from the dense to dilute phase register themselves as large fluctuations in the protein concentration in the dilute phase. For the other two scenarios (Figures c-f) aggregation has been accelerated due to the presence of crowders/salt. This causes larger aggregates to be formed. Therefore addition/removal of one or two chains does not significantly affect the concentration and we do not see such sudden large jumps. In summary, the large jumps seen in Figures a and b are due to slow, fluxional aggregation of pure αS and finite size effects. However as these still are only fluctuations, we posit that the systems have reached steady states. This claim is further supported by the following figure where the time profile of a few useful system wide macroscopic properties show no change between 1.5-2.5 µs.

We also have added a brief discussion in the Methods section (Page 29-30) with these figures in the Supplementary Information.

Author response image 2.

“In this study, we utilized the final 1 µs from each simulation for further analysis. To ascertain whether the simulations have achieved a steady state, we plotted the time profile of protein concentration in the dilute phase for all three cases. Except for minor intermittent fluctuation involving only αS in neat water (Figures S8a and S8b), the remaining cases exhibit notably stable concentrations throughout various segments of the trajectory (Figures S8 c-f). The relatively higher fluctuations observed in Figures S8a and b stem from the slow, spontaneous aggregation of αS alone, compounded by the inherently ambiguous nature of the dense phase.

Consequently, the addition or removal of a few chains from the dense to the dilute phase results in significant fluctuations in protein concentration within the dilute phase. Conversely, in the other two scenarios (Figures S8c-f), aggregation is expedited by the presence of crowders/salt, leading to the formation of larger aggregates. Consequently, the addition or removal of one or two chains has negligible impact on concentration, thereby mitigating sudden large jumps. In summary, the conspicuous jumps depicted in Figures S8a and b arise from the gradual, fluctuating aggregation of pure αS and finite size effects. However, since these remain within the realm of fluctuations, we assert that the systems have indeed reached steady states. This assertion is bolstered by the subsequent figure, where the time profile of several pertinent system-wide macroscopic properties reveals no discernible change between 1.5-2.5 µs (Figures S9).”

(2) The benchmarking used to validate their cgMD methods is very minimal and fails to utilize a large amount of available all-atom simulation and experimental data.

We disagree with the reviewer on this point. We have cited multiple previous studies [26, 27] that have chosen Rg as a metric of choice for benchmarking coarse-grained model and have used a reference (experimental or otherwise) to tune Martini force fields. Majority of the notable literature where Rg was used as a benchmark during generation of new coarse-grained force fields are works by Dignon et al. (PLoS Comp. Biol.) [ref. 25], Regy et al (Protein Science. 2021) [ref. 26], Joseph et al.(Nature Computational Science. 2021) [ref. 27] and Tesei et al (Open Research Europe, 2022) [ref. 28]. From a polymer physics perspective, tuning water-protein interactions is simply changing the solvent characteristics for the biopolymer and Rg has been generally considered a suitable metric in the case of coarse-grained model. Moreover we try to match the distribution of the Rg rather than only the mean value. This suggests that at a single molecule level, the cgMD simulations at the optimum water of water-protein interactions would allow the protein to sample the conformations present in the reference ensemble. We use the extensively sampled 70 μs all-atom data from DE Shaw Research to obtain the reference Rg distribution. Also we perform a cross validation by comparing the fraction of bound states in all-atom and cgMD dimer simulations which also seem to corroborate well with each other at optimum water-protein interactions. To let the readers understand the rationale behind choosing Rg we have added a section in the Methods section (Page 25) that explains why Rg is plausibly a good metric for tuning water-protein interactions in Martini 3, at least when dealing with IDPs.

Our optimized model is further supported by the FRET experiments by Ray et al. [6]. They found that interchain NAC-NAC interactions drive LLPS. Residue level contact maps obtained from our simulations also show decreased intrachain NAC-NAC interactions with an increased interchain NAC-NAC interactions inside the droplet. This corroborates well with the experimental observations and furthermore validates the metrics we have used for optimization of the water-protein interactions. However the comparison with the FRET data by Ray et al. was not present earlier and we have added the following lines in the updated draft.

Page17: “Thus we observed that increased inter-chain NAC-NAC regions facilitate the formation of αS droplets which also have previously been seen from FRET experiments on αS LLPS

droplets[6].”

(3) They also miss opportunities to compare their simulations to experimental data on aSyn protein droplets.

We thank the reviewer for pointing this out. We have tried to compare the results from our simulations to existing experimental FRET data on αS. Please see the previous response where we have described our comparison with FRET observations.

(4) Aspects such as network analysis are not contextualized by comparison to other protein condensed phases.

For a proper comparison between other protein condensed phases, we would require the position phase space of such condensates which is not readily available. Therefore we tried to explain it in a simpler manner to paint a picture of how αS forms an interconnecting network inside the droplet phase.

(5) Data are not made available, which is an emerging standard in the field.

We thank the reviewer for mentioning this. We have provided the trajectories between 1.5-2.5 μs, which we used for the analysis presented in the article, via a zenodo repository along with other relevant files related to the simulations (https://zenodo.org/records/10926368).

Firstly, it is not clear that these systems are equilibrated or at a steady state (since protein droplets are not really equilibrium systems). The authors do not present any data showing time courses that indicate the system to be reaching a steady state. This is problematic for several of their data analysis procedures, but particularly in determining free energy of transfer between the condensed and dilute phases based on partitioning.

We have addressed this concern as stated previously in the response. We have updated the article accordingly.

Secondly, the benchmarking that they perform against the 73 µs all-atom simulation of aSyn monomer by Shaw and coworkers provides only very crude validation of their cgMD models based on reproducing Rg for the monomer. The authors should make more extensive comparisons to the specific conformations observed in the DE Shaw work. Shaw makes the entire trajectory publicly available. There are also a wealth of experimental data that could be used for validation with more molecular detail. See for example, NMR and FRET data used to benchmark Monte Carlo simulations of aSyn monomer (as well as extensive comparisons to the Shaw MD trajectory) in Ferrie at al: A Unified De Novo Approach for Predicting the Structures of Ordered and Disordered Proteins, J. Phys. Chem. B 124 5538-5548 (2020)

DOI:10.1021/acs.jpcb.0c02924

I note that NMR measurements of aSyn in liquid droplets are available from Vendruscolo: Observation of an α-synuclein liquid droplet state and its maturation into Lewy body-like assemblies, Journal of Molecular Cell Biology, Volume 13, Issue 4, April 2021, Pages 282-294, https://doi.org/10.1093/jmcb/mjaa075.

In addition, there are FRET studies by Maji: Spectrally Resolved FRET Microscopy of α-Synuclein Phase-Separated Liquid Droplets, Methods Mol Biol 2023:2551:425-447. doi: 10.1007/978-1-0716-2597-2_27.

So the authors are missing opportunities to better validate the simulations and place their structural understanding in greater context. This is just based on my own quick search, so I am sure that additional and possibly better experimental comparisons can be found.

We have performed a comparison with existing FRET measurements by Ray et al. (2020) as discussed in a previous response and also updated the same in the article. The doi (10.1007/978-1-0716-2597-2_27) provided by the reviewer is however for a book on Methods to characterize protein aggregates and does not contain any information regarding the observations from FRET experiments. The other doi (https://doi.org/10.1093/jmcb/mjaa075) for the article from Vendrusculo group does not contain information directly relevant to this study. Moreover NMR measurements cannot be predicted from cgMD since full atomic resolution is lost upon coarse-graining of the protein . A past literature survey by the authors found very little scientific literature on molecular level characterization of αS LLPS droplets.

Thirdly, the small word network analysis is interesting, but hard to contextualize. For instance, the 8 Å cutoff used seems arbitrary. How does changing the cutoff affect the value of S determined? Also, how does the value of S compare to other condensed phases like crystal packing or amyloid forms of aSyn?

The 8 Å cutoff is actually arbitrary since a distance based clustering always requires a cutoff which is empirically decided. However 8 Å is quite large compared to other cutoffs used for distance based clustering. For example in ref 26, 5 Å was used as a cutoff for calculation of protein clusters. Larger cutoffs will lead to sparser network structures. However we used the same cutoff for all distance based clustering which makes the networks obtained comparable. We wanted to perform a comparison among the networks formed by αS under different environmental conditions.

Fourthly, I see no statement on data availability. The emerging standard in the computational field is to make all data publicly available through Github or some similar mechanism.

We thank the reviewer for pointing this out and we have provided the raw data between 1.5-2.5 μs for each scenario along with other relevant files via a zenodo repository (https://zenodo.org/records/10926368).

Finally, on page 16, they discuss the interactions of aSyn(95-110), but the sequence that they give is too long (seeming to contain repeated characters, but also not accurate). aSyn(95-110) = VKKDQLGKNEEGAPQE. Presumably this is just a typo, but potentially raises concerns about the simulations (since without available data, one cannot check that the sequence is accurate) and data analysis elsewhere.

This indeed is a typographical error. We have updated the article with the correct sequence. The validity of the simulations can be verified from the data we have shared via the zenodo repository (https://zenodo.org/records/10926368).

Author response:

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

Public Reviews:

Reviewer #1:

Mehrdad Kashefi et al. investigated the availability of planning future reaches while simultaneously controlling the execution of the current reach. Through a series of experiments employing a novel sequential arm reaching paradigm they developed, the authors made several findings: 1) participants demonstrate the capability to plan future reaches in advance, thereby accelerating the execution of the reaching sequence, 2) planning processes for future movements are not independent one another, however, it's not a single chunk neither, 3) Interaction among these planning processes optimizes the current movement for the movement that comes after for it.

The question of this paper is very interesting, and the conclusions of this paper are well supported by data. However, certain aspects require further clarification and expansion.

We thank reviewer one for their evaluation of the work.

(1) The question of this study is whether future reach plans are available during an ongoing reach. In the abstract, the authors summarized that "participants plan at least two future reaches simultaneously with an ongoing reach and that the planning processes of the two future reaches are not independent of one another" and showed the evidence in the next sentences. However the evidence is about the relationship about ongoing reach and future plans but not about in between future plans (Line 52-55). But the last sentence (Line 55-58) mentioned about interactions between future plans only. There are some discrepancies between sentences. Could you make the abstract clear by mentioning interference between 1) ongoing movement and future plans and 2) in between future plans?

We thank Reviewer for their comment. We have separated the longer sentence in the original abstract into two shorter ones. This should clarify that the two pieces of evidence pertain to the interaction of planning processes.

(2) I understood the ongoing reach and future reaches are not independent from the results of first experiment (Figure 2). A target for the current reach is shown at Horizon 1, on the other hand, in Horizon 2, a current and a future target are shown on the screen. Inter-reach-interval was significantly reduced from H1 to H2 (Figure 2). The authors insist that "these results suggest that participants can plan two targets (I guess +1 and +2) ahead of the current reach (I guess +0)". But I think these results suggest that participants can plan a target (+1) ahead of the current reach (+0) because participants could see the current (+0) and a future target (+1) in H2. Could the authors please clarify this point?

We thank Reviewer for raising this point. Our conclusion that “participants can plan two targets ahead of the current reach” is supported by the reduction in Inter-Response Interval (IRI) observed when comparing H2 to H3 in the 75 ms Dwell time condition. Specifically, on average, participants were 16 ms faster when they could see two future targets on the screen (H3) than when they could see only one (H2). To clarify this in the paper, we have revised the wording in line 124 to explicitly state that the conclusion pertains to the 75 ms Dwell time condition. Additionally, we emphasize that the strongest evidence for planning two future targets comes from the experiment shown in Figure 3.

(3) Movement correction for jump of the +1 target takes longer time in H3 compared to H2 (Figure 4). Does this perturbation have any effect on reaching for +2 target? If the +1 jump doesn't affect reaching for +2 target, combined with the result that jump of the +2 target didn't affect the movement time of +1 target (Figure 3C), perturbation (target jump) only affects the movement directly perturbed. Is this implementation correct? If so, does these results support to decline future reaches are planned as motor chunk? I would like to know the author's thoughts about this.

In the experiment presented in Figure 4, once we jumped the +1 target, the reach to that target was changed and participants replaned a corrective movement to the new location of the +1 target. This usually was followed by a longer-than-usual pause at the new location of +1 target for resuming the sequence and finishing the trial. Consequently, in these jump trials, it was impossible to compare the +2 reach to no-jump trials, as the normal sequence of movement was disrupted, and the reach to the +2 target originated from a different starting location. Nevertheless, we addressed the possibility that the two future reaches were planned as a chunk by the analysis shown in figure 5: There we showed that a displacement of the +2 target did not influence the reach to the +1 target, indicating that the movement plans could be updated independently.

(4) Any discussion about Saccade position (Figure 7)?

We thank reviewer 1 for this important comment. The following discussion section is added for the gaze position results.

In our sequence task, participants switched their gaze location only once per reach, suggesting that information about the location of the next target is perceived parafoveally (Figure 7A). This observation aligns with previous studies (Clavagnier et al., 2007; González-Alvarez et al., 2007; Sivak and MacKenzie, 1990) that found participants keep their visual attention on the current sequence item and can perceive the location of spatial targets even when foveal vision is occluded. However, when comparing gaze locations for conditions Horizon >1, we observed that participants systematically biased their gaze location based on the sequence context. The gaze position shifted toward the next target, potentially allowing for more accurate location estimation (Figures 7C-D). Notably, changes in gaze location were observed even in Horizon 2, despite no changes in the curvature of hand movements in this horizon (Figure 6B). This suggests that information about the next target may first be available in the circuitry that controls eye movements and later in the cortical areas that control voluntary upper limb movements. Further control studies are required to investigate this hypothesis.

Reviewer #2:

Summary:

In this work, Kashefi et al. investigate the planning of sequential reaching movements and how the additional information about future reaches affects planning and execution. This study, carried out with human subjects, extends a body of research in sequential movements to ask important questions: How many future reaches can you plan in advance? And how do those future plans interact with each other?

The authors designed several experiments to address these questions, finding that information about future targets makes reaches more efficient in both timing and path curvature. Further, with some clever target jump manipulations, the authors show that plans for a distant future reach can influence plans for a near future reach, suggesting that the planning for multiple future reaches is not independent. Lastly, the authors show that information about future targets is acquired parafoveally--that is, subjects tend to fixate mainly on the target they are about to reach to, acquiring future target information by paying attention to targets outside the fixation point.

The study opens up exciting questions about how this kind of multi-target planning is implemented in the brain. As the authors note in the manuscript, previous work in monkeys showed that preparatory neural activity for a future reaching movement can occur simultaneously with a current reaching movement, but that study was limited to the monkey only knowing about two future targets. It would be quite interesting to see how neural activity partitions preparatory activity for a third future target, given that this study shows that the third target's planning may interact with the second target's planning.

Strengths:

A major strength of this study is that the experiments and analyses are designed to answer complementary questions, which together form a relatively complete picture of how subjects act on future target information. This complete description of a complex behavior will be a boon to future work in understanding the neural control of sequential, compound movements.

We thank the reviewer for their thorough reading of our work.

Weaknesses:

I found no real glaring weaknesses with the paper, though I do wish that there had been some more discussion of what happens to planning with longer dwell times in target. In the later parts of the manuscript, the authors mention that the co-articulation result (where reaches are curved to make future target acquisition more efficient) was less evident for longer dwell times, likely because for longer dwell times, the subject needs to fully stop in target before moving to the next one. This result made me wonder if the future plan interaction effect (tested with the target jumps) would have been affected by dwell time. As far as I can tell, the target jump portion only dealt with the shorter dwell times, but if the authors had longer dwell time data for these experiments, I would appreciate seeing the results and interpretations.

We thank the reviewer for raising this point. In our time (Figure 2) and curvature analysis (Figure 6), we collected data with five levels of the horizon and three levels of dwell time to explore the space of parameters and to see if there is any interaction between dwell time and the horizon of planning the future targets. Apriori, we expected that the full stop in each target imposed by the 400 ms dwell time would be long enough to remove any effect of future targets on how the current move is executed. In line with our initial hypothesis, the systematic curvature of reaches based on the future target was smaller in longer dwell times (Figure 6E). Nevertheless, we observed a significant curvature even in 400 ms dwell time. Based on this observation, we expect running the jump experiments (Figures 4 and 5) in longer dwell times will lead to the same pattern of results but with a smaller effect size since longer dwells break the interdependence of sequence elements (Kalidindi & Crevecoeur, 2023). In the end, for the jump experiments, we limited our experimental conditions to the fastest dwell time (75 ms dwell) since we were conceptually interested in situations where movements in the sequence are maximally dependent on each other.

Beyond this , the authors also mentioned in the results and discussion the idea of "neural resources" being assigned to replan movements, but it's not clear to me what this might actually mean concretely. I wonder if the authors have a toy model in mind for what this kind of resource reassignment could mean. I realize it would likely be quite speculative, but I would greatly appreciate a description or some sort of intuition if possible.

Our use of the term "neural resources" is inspired by classic psychology literature on how cognitive resources such as attention and working memory are divided between multiple sequence components. Early studies on working memory suggest that human participants can retain and manipulate a fixed number of abstract items in working memory (Miller, 1956). However, more recent literature postulates that a specific number of items does not limit working memory, rather, it is limited by a finite attentional resource that is softly allocated to task items.

Here we borrowed the same notion of soft distribution of resources for the preparation of multiple sequence items. A large portion of our observation in this paper and also previous work on sequence production can be explained by a simple model that assumes one central planning resource that is “softly” divided between sequence elements when participants see future items of the sequence (Author Response Image 1). The first sequence element receives the majority of the resources and is planned the most. The rest of the sequence receives the remaining planning resources in an exponentially decaying manner for preparation of the movement during the execution of the ongoing movement. Once the ongoing movement is over, the resource is then transferred to the next sequence item and this process is repeated until the sequence is over. Assignment of planning resources to future items explains why participants are faster when seeing future items (Figure 2). But this comes with a cost – if the ongoing movement is perturbed, the replanning process is delayed since some of the resources are occupied by future planning (Figure 4). This naturally leads to the question of how this resource allocation is implemented in neural tissue. To address this, we are conducting the same sequence task with the horizon in non-human primates (NHPs), and the investigation of these neural implementation questions will be the focus of future studies.

Author response image 1.

Basic diagram showing a soft distribution of a limited planning resource. The diagram shows a Horizon 3 condition in which two future reaches (+1 and +2) are planned while executing a movement (+0). The majority of resources is assigned to the execution of the ongoing movement while the reset is distributed for planning future movements. Once the movement is over, the chain of preparation and execution moves forward.

Recommendations for the author:

Reviewer #1

We thank reviewer one for these comments regarding the clarity and consistency of figures and terminology.

(1) Figure 3. Are "+1 Move" in Fig. 3B and "+ 1 Movement" in Fig. 3C as same as "E + 1" in Fig. 3A? Also does "Dwell" in Fig. 3B mean same as "+1 Dwell" in Fig. 3C? Consistent terminology would help readers to understand the figure.

“+1 Move” in Figure 3B is the same as +1 movement in Figure 3C. “Dwell” in Figure 3B is the same as +1 Dwell in Figure 3C. We changed the figure for more consistency.

(2) Figure 3. A type in the second last line in the legend, "pre-jump target for no-jump and jump and condition". The second "and" isn't necessary.

The typo is corrected. Thank you.

(3) Figure 4C. Is "Movement time" equivalent with "E + 1"?

“Movement time” is equivalent to E+1 only in no-jump conditions. When the jump occurs,

Movement time contains all the

(4) Figure 6B. Is the gray circle in between the graph and target positions there by mistake?

We fixed this typo. Thank you.

(5) Figure 6E. It's hard to distinguish H2-H5 from the color differences.

We changed the H5 to full white with a black stroke to improve the contrast. Thank you.

(6) Figure 7A. Blue dots are almost invisible.

We added a black stroke to blue circles for more visibility. Thank you.

Reviewer #2

I found this manuscript to be engaging and well written--many of the questions I had while reading were answered promptly in the next section. As such, my comments are mostly minor and primarily geared towards improving clarity in the manuscript.

(1) One major recurring confusion I had while reading the manuscript was how to think about H1, H2, and H3. It was clearly explained in the text, and the explanations of the results were generally clear once I read through it all, but I found it strangely confusing at times when trying to interpret the figures for myself (e.g., in H2, 2 targets are on screen, but the second target can only be planned during the reach toward the first target). This confusion may just be me reading the manuscript over two days, but I wonder if it could be made clearer with some semantic iconography associated with each horizon added to the later figures alongside the H labels. As one option, perhaps the planning timeline part of Fig 1D could be simplified and shrunk down to make an icon for each horizon that clearly shows when planning overlaps for each horizon.

(Please see the response to point #2 below)

(2) Regarding Fig 1D: I like this figure, but it's unclear to me how the exact preparation and execution times are determined. Is this more of a general schematic of overlaps, or is there specific information about timing in here?

We thank reviewer 2 for their important feedback. The role of Figure 1D was to summarize the timing of the experiments for different horizons. That is, to clarify the relative timing of the targets appearing on the screen (shown with a small circle above the horizontal line) and targets being captured by participants (the ticks and their associated number on the line). Execution is shown as the time interval that the hand is moving between the targets and planning is the potential planning time for participants from the target appearing on the screen until initiation of the reach to that target. We added the relevant parts of Figure 1D to the subplots for each subsequent experiment, to summarize the timing of other experiments and their analyses. For the experiments with target jump, a small vertical arrow shows the time of the target jump relative to other events.

However, this figure will be less useful, if the connection between the timing dots and ticks is not communicated. We agree that in the original manuscript, this important figure was only briefly explained in the caption of Figure 1. We expanded the explanation in the caption of Figure 1 and referenced the dots and ticks in the main text.

(3) Fig 6B - for some reason I got confused here: I thought the central target in this figure was the start target, and it took me embarrassingly long to figure out that the green target was the start target. This is likely because I'm used to seeing center-out behavioral figures. Incidentally, I wasn't confused by 7c (in fact, seeing 7c is what made me understand 6b), so maybe the solution is to clearly mark a directionality to the reach trajectories, or to point an arrow at the green target like in previous figures. Also, the bottom left gray target in the figure blends into the graph on the left--I didn't notice it until rereading. Because there's white space between that target and the green one, it might be good to introduce some white space to separate the graph from the targets more. The target arrangement makes more sense in panel C, but by the time I got there, I had already been a bit confused.

Thanks for raising this point. As shown in Figure 6C, we used the reach to the +1 target for the curvature analysis. The confusion about Figure 6B is probably due to continuing the reach trajectories after the +1 target. That also explains why Figure 7C seemed more straightforward. To solve this issue we modified Figure 6B such that the reaches are shown with full opacity right until the +1 target and then shown with more transparency. We believe this change focuses the reader's attention to the reach initiated from the +0 target to the +1 target.

As for the gray target in Figure 6B, we originally had the gray target as it is a potential start location for the reach to the +0 target, and for having similar visuals between the plots. The gray target is now removed from Figure 6B.

(4) Line 253 - I'm not sure I understand the advantage over simple averaging that the authors mention here--would be nice to get a bit more intuition.

Thanks for raising this point. We used a two-factor model in our analysis, with each factor representing the angle of the last and next target, respectively. Both factors had five levels: -120, -60, 0, 60, and 120 degrees relative to the +1 reach. In a balanced two-factor design, where each combination of factor levels has an equal number of trials, using a linear model and simple averaging would yield equivalent results. However, when the number of trials for the combinations of the two factors is unbalanced, simple averaging can lead to misleading differences in the levels of the second factor. Additionally, the linear model allows us to investigate potential interactions between the two factors, which is not possible with simple averaging.

(5) Fig 7a - I would have liked to see the traces labeled in figure (i.e. hand trajectory vs. eye trajectory)

Hand and eye trajectories are now labeled in the figure.

(6) Fig 7c - very minor, but the hexagon of targets is rotated 30 degrees from all previous hexagons shown (also, this hex grid target arrangement can't lead to the trajectory shown in 7a, so it can't be that this was a different experimental grid). I'm guessing this was a simple oversight.

We used the same grid in the eye-tracking experiment. The targets are to visually match the previous plots. Thank you for raising this point.

Reference

Clavagnier, S., Prado, J., Kennedy, H., & Perenin, M.-T. (2007). How humans reach: distinct cortical systems for central and peripheral vision. The Neuroscientist: A Review Journal Bringing Neurobiology, Neurology and Psychiatry, 13(1), 22–27.

González-Alvarez, C., Subramanian, A., & Pardhan, S. (2007). Reaching and grasping with restricted peripheral vision. Ophthalmic & Physiological Optics: The Journal of the British College of Ophthalmic Opticians , 27(3), 265–274.

Kalidindi, H. T., & Crevecoeur, F. (2023). Task dependent coarticulation of movement sequences (p.2023.12.15.571847). https://doi.org/10.1101/2023.12.15.571847

Miller, G. A. (1956). The magical number seven plus or minus two: some limits on our capacity for processing information. Psychological Review, 63(2), 81–97.

Sivak, B., & MacKenzie, C. L. (1990). Integration of visual information and motor output in reaching and grasping: the contributions of peripheral and central vision. Neuropsychologia, 28(10), 1095–1116.

Author Response

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

eLife Assessment

This useful study could potentially represent a step forward towards personalized medicine by combining cell-based data and a prior-knowledge network to derive Boolean-based predictive logic models to uncover altered protein/signaling networks within cancer cells. However, the level of evidence supporting the conclusions is inadequate, and further validation of the reported approach is required. If properly validated, these findings could be of interest to medical biologists working in the field of cancer and would inform drug development and treatment choices in the field of oncology.

We thank the editor and the reviewer for their constructive comments, which helped us to improve our story. We have now performed new analyses and experiments to further support our proposed approach.

Public Reviews:

Reviewer #1 (Public Review):

(1) The authors deploy a combination of their own previously developed computational methods and databases (SIGNOR and CellNOptR) to model the FLT3 signaling landscape in AML and identify synergistic drug combinations that may overcome the resistance AML cells harboring ITD mutations in the TKI domain of FLT3 to FLT3 inhibitors. I did not closely evaluate the details of these computational models since they are outside of my area of expertise and have been previously published. The manuscript has significant issues with data interpretation and clarity, as detailed below, which, in my view, call into question the main conclusions of the paper.

The authors train the model by including perturbation data where TKI-resistant and TKIsensitive cells are treated with various inhibitors and the activity (i.e. phosphorylation levels) of the key downstream nodes are evaluated. Specifically, in the Results section (p. 6) they state "TKIs sensitive and resistant cells were subjected to 16 experimental conditions, including TNFa and IGF1 stimulation, the presence or absence of the FLT3 inhibitor, midostaurin, and in combination with six small-molecule inhibitors targeting crucial kinases in our PKN (p38, JNK, PI3K, mTOR, MEK1/2 and GSK3)". I would appreciate more details on which specific inhibitors and concentrations were used for this experiment. More importantly, I was very puzzled by the fact that this training dataset appears to contain, among other conditions, the combination of midostaurin with JNK inhibition, i.e. the very combination of drugs that the authors later present as being predicted by their model to have a synergistic effect. Unless my interpretation of this is incorrect, it appears to be a "self-fulfilling prophecy", i.e. an inappropriate use of the same data in training and verification/test datasets.

We thank the reviewer for this comment. We have now extensively revised the Figure 2B and edited the text to clarify and better describe the experimental conditions of our multiparametric analysis. As the reviewer stated, we have used different combinations of drugs, including midostaurin and JNK inhibitor to generate two cell-specific predictive models recapitulating the main signal transduction events, down-stream FLT3, occurring in resistant (FLT3ITD-TKD) and sensitive (FLT3ITD-JMD) cells. These experiments were performed by treating cells at very early time points to obtain a picture of the signaling response of FLT3-ITD positive cells. Indeed, we have measured the phosphorylation level of signaling proteins, because at these early time points (90 minutes) we do not expect a modulation of downstream crucial phenotypes, including apoptosis or proliferation. To infer perturbations impacting the apoptosis or proliferation phenotypes, we applied a computational two-steps strategy:

(1) We extracted key regulators of ‘apoptosis’ and ‘proliferation’ hallmarks from SIGNOR database.

(2) We applied our recently developed ProxPath algorithm to retrieve significant paths linking nodes of our two optimized models to ‘proliferation’ and ‘apoptosis’ phenotypes.

This allowed us to evaluate in silico the “proliferation” and “apoptosis” rate upon inactivation of each node of the network. With the proposed approach, we identified JNK as a potential drug target to use in combination with FLT3 to restore sensitivity (i.e. in silico inducing apoptosis and reducing proliferation) of FLT3 ITD-TKD cells. We here want to stress once more that although the first piece of information (the effect of JNK and FLT3 inhibition) on sentinel readouts was provided in the training dataset, the second piece of information (the effect on this treatment over the entire model and, as a consequence, on the cellular phenotype) was purely the results of our computational models. As such, we hope that the reviewer will agree that this could not represent a “self-fulfilling prophecy".

That said, we understand that this aspect was not clearly defined in the manuscript. For this reason, we have now 1) extensively revised the Figure 2B; 2) edited the text (pg. 6) to clarify the purpose and the results of our approach; and 3) described in further detail (pg. 16-18) the experimental conditions of our multiparametric analysis.

(2) My most significant criticism is that the proof-of-principle experiment evaluating the combination effects of midostaurin and SP600125 in FLT3-ITD-TKD cell line model does not appear to show any synergism, in my view. The authors' interpretation of the data is that the addition of SP600125 to midostaurin rescues midostaurin resistance and results in increased apoptosis and decreased viability of the midostaurin-resistant cells. Indeed, they write on p.9: "Strikingly, the combined treatment of JNK inhibitor (SP600125) and midostaurin (PKC412) significantly increased the percentage of FLT3ITD-TKD cells in apoptosis (Fig. 4D). Consistently, in these experimental conditions, we observed a significant reduction of proliferating FLT3ITD- TKD cells versus cells treated with midostaurin alone (Fig. 4E)." However, looking at Figs 4D and 4E, it appears that the effects of the midostaurin/SP600125 combination are virtually identical to SP600125 alone, and midostaurin provides no additional benefit. No p-values are provided to compare midostaurin+SP600125 to SP600125 alone but there seems to be no appreciable difference between the two by eye. In addition, the evaluation of synergism (versus additive effects) requires the use of specialized mathematical models (see for example Duarte and Vale, 2022). That said, I do not appreciate even an additive effect of midostaurin combined with SP600125 in the data presented.

We agree with the reviewer that the JNK inhibitor and midostaurin do not have neither a synergic nor additive effect and we have now revised the text accordingly. It is highly discussed in the scientific community whether FLT3ITD-TKD AML cells benefit from midostaurin treatments. In a recently published retroprospective study of K. Dohner et al. (Rücker et al., 2022), the authors investigated the prognostic and predictive impact of FLT3-ITD insertion site (IS) in 452 patients randomized within the RATIFY trial, which evaluated midostaurin additionally to intensive chemotherapy. Their study clearly showed that “Midostaurin exerted a significant benefit only for JMDsole” patients. In agreement with this result, we have demonstrated that midostaurin treatment had no effects on apoptosis of blasts derived from FLT3ITD-TKD patients (Massacci et al., 2023). On the other hand, we and others observed that midostaurin triggers apoptosis in FLT3ITD-TKD cells to a lesser extent as compared to FLT3ITDJMD cells (Arreba-Tutusaus et al., 2016). The data presented here (Fig. 4) and our previously published papers (Massacci et al., 2023; Pugliese et al., 2023) pinpoint that hitting cell cycle regulators (WEE1, CDK7, JNK) induce a significant apoptotic response of TKI resistant FLT3ITD-TKD cells. Prompted by the reviewer comment, we have now revised the text and discussion (pg.9; 14) highlighting the crucial role of JNK in apoptosis induction.

(3) In my view, there are significant issues with clarity and detail throughout the manuscript. For example, additional details and improved clarity are needed, in my view, with respect to the design and readouts of the signaling perturbation experiments (Methods, p. 15 and Fig 2B legend). For example, the Fig 2B legend states: "Schematic representation of the experimental design: FLT3 ITD-JMD and FLT3 ITD-JMD cells were cultured in starvation medium (w/o FBS) overnight and treated with selected kinase inhibitors for 90 minutes and IGF1 and TNFa for 10 minutes. Control cells are starved and treated with PKC412 for 90 minutes, while "untreated" cells are treated with IGF1 100ng/ml and TNFa 10ng/ml with PKC412 for 90 minutes.", which does not make sense to me. The "untreated" cells appear to be treated with more agents than the control cells. The logic behind cytokine stimulation is not adequately explained and it is not entirely clear to me whether the cytokines were used alone or in combination. Fig 2B is quite confusing overall, and it is not clear to me what the horizontal axis (i.e. columns of "experimental conditions", as opposed to "treatments") represents. The Method section states "Key cell signaling players were analyzed through the X-Map Luminex technology: we measured the analytes included in the MILLIPLEX assays" but the identities of the evaluated proteins are not given in the Methods. At the same time, the Results section states "TKIs sensitive and resistant cells were subjected to 16 experimental conditions" but these conditions do not appear to be listed (except in Supplementary data; and Fig 2B lists 9 conditions, not 16). In my subjective view, the manuscript would benefit from a clearer explanation and depiction of the experimental details and inhibitors used in the main text of the paper, as opposed to various Supplemental files/Figures. The lack of clarity on what exactly were the experimental conditions makes the interpretation of Fig 2 very challenging. In the same vein, in the PCA analysis (Fig 2C) there seems to be no reference to the cytokine stimulation status while the authors claim that PC2 stratifies cells according to IGF1 vs TNFalpha. There are numerous other examples of incomplete or confusing legends and descriptions which, in my view, need to be addressed to make the paper more accessible.

We thank the reviewer for his/her comment. We have now extensively revised the text of the manuscript (pg. 6), revised Fig. 2B (now Fig 2C) and methods (pg. 16-18) to improve the clarity of our manuscript, making the take-home messages more accessible. We believe that the revised versions of text and of Figure 2 better explain our strategy and clarify the experimental set up, we added details on the choices of the experimental conditions, and we proposed a better graphic representation of the analysis.

(4) I am not sure that I see significant value in the patient-specific logic models because they are not supported by empirical evidence. Treating primary cells from AML patients with relevant drug combinations would be a feasible and convincing way to validate the computational models and evaluate their potential benefit in the clinical setting.

We thank the reviewer for this comment. We have now performed additional experiments in a small cohort of FLT3-ITD positive patient-derived primary blasts. Specifically, we have treated blasts from 2 FLT3ITD-TKD patients and 3 FLT3ITD-JMD+TKD patients with PKC412 (100nM) 24h and/or 10μM SP600125 (JNK inhibitor). After 24h of treatment we have measured the apoptotic rate. As shown below and in the new Fig. 4F (see pg.10, main text), midostaurin triggers higher levels of apoptosis in FLT3ITD-JMD+TKD blasts as compared to FLT3ITD-TKD blasts. Importantly, treatment with the JNK inhibitor SP600125 alone triggers apoptosis in FLT3ITD-TKD blasts, validating the crucial role of JNK in FLT3ITD-TKD cell survival and TKI resistance. The combined treatment of midostaurin and SP600125 increases the percentage of apoptotic cells as compared to midostaurin treatment alone but to a lesser extent than single agent treatment. This result is in agreement with the current debate in the scientific community on the actual beneficial effect of midostaurin treatment in FLT3ITD-TKD AML patients.

Author response image 1.

Primary samples from AML patients with the FLT3ITD-TKD mutation (n=2, yellow bars) or the FLT3ITD-JMD/TKD mutation (n=3, blue bars) were exposed to Midostaurin (100nM, PKC412), and JNK inhibitor (10µM, SP600125) for 48 hours, or combinations thereof. The specific cell death of gated AML blasts was calculated to account for treatment-unrelated spontaneous cell death. The bars on the graph represent the mean values with standard errors.

Reviewer #2 (Public Review):

Summary:

This manuscript by Latini et al describes a methodology to develop Boolean-based predictive logic models that can be applied to uncover altered protein/signalling networks in cancer cells and discover potential new therapeutic targets. As a proof-of-concept, they have implemented their strategy on a hematopoietic cell line engineered to express one of two types of FLT3 internal tandem mutations (FLT3-ITD) found in patients, FLT3-ITD-TKD (which are less sensitive to tyrosine kinase inhibitors/TKIs) and FLT3-ITD-JMD (which are more sensitive to TKIs).

Strengths:

This useful work could potentially represent a step forward towards personalised targeted therapy, by describing a methodology using Boolean-based predictive logic models to uncover altered protein/signalling networks within cancer cells. However, the weaknesses highlighted below severely limit the extent of any conclusions that can be drawn from the results.

Weaknesses:

While the highly theoretical approach proposed by the authors is interesting, the potential relevance of their overall conclusions is severely undermined by a lack of validation of their predicted results in real-world data. Their predictive logic models are built upon a set of poorlyexplained initial conditions, drawn from data generated in vitro from an engineered cell line, and no attempt was made to validate the predictions in independent settings. This is compounded by a lack of sufficient experimental detail or clear explanations at different steps. These concerns considerably temper one's enthusiasm about the conclusions that could be drawn from the manuscript.

We thank the reviewer for the thorough review and kind comments about our manuscript. We hope the changes and new data we provide further strengthen it in his or her eyes.

Some specific concerns include:

(1) It remains unclear how robust the logic models are, or conversely, how affected they might be by specific initial conditions or priors that are chosen. The authors fail to explain the rationale underlying their input conditions at various points. For example: - at the start of the manuscript, they assert that they begin with a pre-PKN that contains "76 nodes and 193 edges", though this is then ostensibly refined with additional new edges (as outlined in Fig 2A). However, why these edges were added, nor model performance comparisons against the basal model are presented, precluding an evaluation of whether this model is better.

We understand the reviewer’s concern. We have now complemented the manuscript with an extended version of the proposed modelling strategy offering a detailed description of the pipeline and the rationale behind each choice (Supplementary material, pg.14-19). Furthermore, we also referenced the manuscript to a GitHub repository where users can follow and reproduce each step of the pipeline (https://github.com/SaccoPerfettoLab/FLT3ITD_driven_AML_Boolean_models).

• At a later step (relevant to Fig S4 and Fig 3), they develop separate PKNs, for each of the mutation models, that contain "206 [or] 208 nodes" and "756 [or] 782 edges", without explaining how these seemingly arbitrary initial conditions were arrived at. Their relation to the original parameters in the previous model is also not investigated, raising concerns about model over-fitting and calling into question the general applicability of their proposed approach. The authors need to provide a clearer explanation of the logic underlying some of these initial parameter selections, and also investigate the biological/functional overlap between these sets of genes (nodes).

We thank the reviewer for raising this question. Very briefly, the proposed optimization strategy falls in a branch of the modelling, where the predictive model is, indeed, driven by the data (Blinov and Moraru, 2012). From a certain point of view, the scope of optimization is the one of fitting the experimental data in the best way possible. To achieve this, we followed standard practices (Dorier et al., 2016; Traynard et al., 2017). To address the issue of “calling into question the general applicability of their proposed approach”, we have compared the activity status of nodes in the models with ‘real data’ extracted from cell lines and patients’ samples to reassure about the robustness and scalability of the strategy (please see below, response to point 3 pg. 9).

Finally, as mentioned in the previous point, we have now provided a detailed supplementary material, where we have described all the aspects mentioned by the reviewer: step-by-step changes in the PKN, the choice of the parameters and other details can be traced over the novel text and are also available in the GitHub repository (https://github.com/SaccoPerfettoLab/FLT3-ITD_driven_AML_Boolean_models).

(2) There is concern about the underlying experimental data underpinning the models that were generated, further compounded by the lack of a clear explanation of the logic. For example, data concerning the status of signalling changes as a result of perturbation appears to be generated from multiplex LUMINEX assays using phosphorylation-specific antibodies against just 14 "sentinel" proteins. However, very little detail is provided about the rationale underlying how these 14 were chosen to be "sentinels" (and why not just 13, or 15, or any other number, for that effect?). How reliable are the antibodies used to query the phosphorylation status? What are the signal thresholds and linear ranges for these assays, and how would these impact the performance/reliability of the logic models that are generated from them?

We thank the reviewer for this comment as it gives us the opportunity to clarify and better explain the criteria behind the experimental data generation.

Overall, we revised the main text at page 6 and the Figure 2B to improve the clarity of our experimental design. Specifically, the sentinels were chosen because they were considered indirect or direct downstream effectors of the perturbations and were conceived to serve as both a benchmarking system of the study and a readout of the global perturbation of the system. To clarify this aspect, we have added a small network (compressed PKN) in Figure 2B to show that the proteins (green nodes) we chose to measure in the LUMINEX multiplex assay are “sentinels” of the activity of almost all the pathways included in the Prior knowledge network. Moreover, we implemented the methods section “Multiparametric experiment of signaling perturbation” (pg. 16-18), where we added details about the antibodies used in the assay paired with the target phosphosites and their functional role (Table 3). We also better specified the filtering process based on the number of beads detected per each antibody used (pg. 18). About the reliability of the measurements, we can say that the quality of the perturbation data impacts greatly on the logic models’ performance. xMAP technology been already used by the scientific community to generate highly reproducible and reliable multiparametric dataset for model training (Terfve et al., 2012). Additionally, we checked that for each sentinel we could measure a fully active state, a fully inactive state and intermediate states. Modulation of individual analytes are displayed in Figure S3.

Author response image 2.

Partial Figure of normalization of analytes activity through Hill curves. Experimental data were normalized and scaled from 0 to 1 using analyte-specific Hill functions. Raw data are reported as triangles, normalized data and squares. Partial Figure representing three plots of the FLT3 ITD-JMD data (Complete Figure in Supplementary material Fig S3).

(3) In addition, there are publicly available quantitative proteomics datasets from FLT3-mutant cell lines and primary samples treated with TKIs. At the very least, these should have been used by the authors to independently validate their models, selection of initial parameters, and signal performance of their antibody-based assays, to name a few unvalidated, yet critical, parameters. There is an overwhelming reliance on theoretical predictions without taking advantage of real-world validation of their findings. For example, the authors identified a set of primary AML samples with relevant mutations (Fig 5) that could potentially have provided a valuable experimental validation platform for their predictions of effective drug combination. Yet, they have performed Boolean simulations of the predicted effects, a perplexing instance of adding theoretical predictions on top of a theoretical prediction!

Additionally, there are datasets of drug sensitivity on primary AML samples where mutational data is also known (for example, from the BEAT-AML consortia), that could be queried for independent validation of the authors' models.

We thank the reviewer for this comment that helped us to significantly strengthen our story. Prompted by his/her comment, we have now queried three different datasets for independent validation of our logic models. Specifically, we have taken advantage of quantitative phosphoproteomics datasets of FLT3-ITD cell lines treated with TKIs (Massacci et al., 2023), phosphoproteomic data of FLT3-ITD positive patients-derived primary blast (Kramer et al., 2022) and of drug sensitivity data on primary FLT3-ITD positive AML samples (BEAT-AML consortia)

• Comparison with phosphoproteomic data of FLT3-ITD cell lines treated with TKIs (Massacci et al., 2023)

Here, we compared the steady state of our model upon FLT3 inhibition with the phosphoproteomic data describing the modulation of 16,319 phosphosites in FLT3-ITD BaF3 cells (FLT3ITD-TKD and FLT3ITD-JMD) upon TKI treatment (i.e. quizartinib, a highly selective FLT3 inhibitor). As shown in the table below and new Figure S5A, the activation status of the nodes in the two generated models is highly comparable with the level of regulatory phosphorylations reported in the reference dataset. Briefly, to determine the agreement between each model and the independent dataset, we focused on the phosphorylation level of specific residues that (i) regulate the functional activity of sentinel proteins (denoted in the ‘Mode of regulation’ column) and (ii) that were measured in this work to train the model. So, we cross-referenced the sentinel protein status in FLT3 inhibition simulation (as denoted in the 'Model simulation of FLT3 inhibition' column) with the functional impact of phosphorylation measured in Massacci et. al dataset (as denoted in the 'Functional impact in quizartinib dataset' column). Points of congruence were summarized in the 'Consensus' column. As an example, if the phosphorylation level of an activating residue decreases (e.g., Y185 of Mapk1), we can conclude that the protein is inhibited (‘Down-reg’) and this is coherent with model simulation in which Mapk1 is ‘Inactive’.

Author response image 3.

• Comparison with phosphoproteomic data of FLT3-ITD patient-derived primary blasts (Kramer et al., 2022)

Using the same criteria, we extended our validation efforts by comparing the activity status of the proteins in the “untreated” simulation (i.e. reproducing the tumorigenic state where FLT3, IGF1R and TNFR are set to be active) with their phosphorylation levels in the dataset by Kramer et al. (Kramer et al., 2022). Briefly, this dataset gathers phosphoproteomic data from a cohort of 44 AML patients and we restricted the analysis to 11 FLT3-ITD-positive patients. Importantly, all patients carry the ITD mutation in the juxta membrane domain (JMD), thus allowing for the comparison with FLT3 ITD-JMD specific Boolean model, exclusively.

The results are shown in the heatmap below. Each cell in the heatmap reports the phosphorylation level of sentinel proteins’ residues in the indicated patient (red and blue indicate up- or- down-regulated phosphoresidues, respectively). Patients were clustered according to Pearson correlation. We observed a good level of agreement between the patients’ phosphoproteomics data and our model (reported in the column “Tumor simulation steady state”) for a subset of patients highlighted within the black rectangle. However, for the remaining patients, the level of agreement is poor. The main reason is that our work focuses on FLT3-ITD signaling and a systematic translation of the Boolean modeling approach to the entire cohort of AML patients would require the inclusion of the impact of other driver mutations in the network. This is actually a current and a future line of investigation of our group. We have revised the discussion, taking this result into consideration.

Author response image 4.

• Comparison with drug sensitivity data on primary FLT3-ITD positive AML samples (BEAT-AML consortia)

Here we took advantage of the Beat AML programme on a cohort of 672 tumour specimens collected from 562 patients. The BEAT AML consortium provides whole-exome sequencing, RNA sequencing and analyses of ex vivo drug sensitivity of this large cohort of patient-derived primary blasts. We focused on drug sensitivity screening on 134 patients carrying the typical FLT3-ITD mutation in the JMD region. Unfortunately, the ITD insertion in the TKD region is less characterized and additional in-depth sequencing studies are required to identify in this cohort FLT3ITD-TKD positive blasts. Next, we focused on those compounds hitting nodes present in the FLT3ITD-JMD Boolean model. Specifically, we selected drugs inhibiting FLT3, PI3K, mTOR, JNK and p38 and we calculated the average IC50 of FLT3ITD-JMD patient-derived primary blasts for each drug. These results are reported as a bar graph in the new Fig. S5B and below (upper panel) and were compared with the apoptotic and proliferation rate measured in silico simulation of the FLT3ITD-JMD Boolean model. Drug sensitivity screening on primary FLT3ITD-JMD blasts revealed that inhibition of FLT3, PI3K and mTOR induces cell death at low drug concentrations in contrast with JNK and p38 inhibitors showing higher IC50 values. These observations are consistent with our simulation results of the FLT3ITD-JMD model. As expected, in silico inhibition of FLT3 greatly impacts apoptosis and proliferation. Additionally, in silico suppression of mTOR and to a lesser extent PI3K and p38 affect apoptosis and proliferation. Of note, JNK inhibition neither in silico nor in vitro seems to affect viability of FLT3ITD-JMD cells.

Author response image 5.

Altogether these publicly available datasets independently validate our models, strengthening the reliability and robustness of our approach.

We have now revised the main text (pg. 8; 9) and added a new Figure (Fig. S5) in the supplementary material; we collected the results of the analysis in TableS6.

(4) There are additional examples of insufficient experimental detail that preclude a fuller appreciation of the relevance of the work. For example, it is alluded that RNA-sequencing was performed on a subset of patients, but the entire methodological section detailing the RNA-seq amounts to just 3 lines! It is unclear which samples were selected for sequencing nor where the data has been deposited (or might be available for the community - there are resources for restricted/controlled access to deidentified genomics/transcriptomics data).

We apologize for the lack of description regarding the RNA sequencing of patient samples. We have now added details of this approach in the method section (pg. 24), clearly explained in text how we selected the patients for the analysis. Additionally, data has now been deposited in the GEO database (accession number: GSE247483).

The sentences we have rephrased are below:

“We analyzed the mutational and expression profiles of 262 genes (Table S7), relevant to hematological malignancies in a cohort of 14 FLT3-ITD positive de novo AML patients (Fig. 5A, panel a). Since, follow-up clinical data were available for 10 out of 14 patients (Fig. 5B, Table S9), we focused on this subset of patients. Briefly, the classification of these 10 patients according to their ITD localization (see Methods) was as follows: 8 patients with FLT3ITD-JMD, 4 with FLT3ITD-JMD+TKD, and 2 with FLT3ITD-TKD (Fig. 5A, panel b). The specific insertion sites of the ITD in the patient cohort are shown in Table S8.

Similarly, in the "combinatory treatment inference" methods, it states "...we computed the steady state of each cell line best model....." and "Then we inferred the activity of "apoptosis" and "proliferation" phenotypes", without explaining the details of how these were done. The outcomes of these methods are directly relevant to Fig 4, but with such sparse methodological detail, it is difficult to independently assess the validity of the presented data.

Overall, the theoretical nature of the work is hampered by real-world validation, and insufficient methodological details limit a fuller appreciation of the overall relevance of this work.

We thank the reviewer for the insightful feedback regarding the methodology in our paper.<br /> About ‘real-world validation’ we have extensively replied to this issue in point 3 (pg. 9-14 of this document). For what concerns the ‘insufficient methodological details’, we have made substantial improvements to enhance clarity and reproducibility, that encompass: (i) revisions in the main text and in the Materials and Methods section; (ii) detailed explanation of each step and decisions taken that can be accessed either as an extended Materials and Methods section (Supplementary material, pg. 14-19) and through our GitHub repository (https://github.com/SaccoPerfettoLab/FLT3-ITD_driven_AML_Boolean_models). We sincerely hope this addition addresses concerns and facilitates a more thorough and independent assessment of our work.

Reviewer #3 (Public Review):

Summary:

The paper "Unveiling the signaling network of FLT3-ITD AML improves drug sensitivity prediction" reports the combination of prior knowledge signaling networks, multiparametric cell-based data on the activation status of 14 crucial proteins emblematic of the cell state downstream of FLT3 obtained under a variety of perturbation conditions and Boolean logic modeling, to gain mechanistic insight into drug resistance in acute myeloid leukemia patients carrying the internal tandem duplication in the FLT3 receptor tyrosine kinase and predict drug combinations that may reverse pharmacoresistant phenotypes. Interestingly, the utility of the approach was validated in vitro, and also using mutational and expression data from 14 patients with FLT3-ITD positive acute myeloid leukemia to generate patient-specific Boolean models.

Strengths:

The model predictions were positively validated in vitro: it was predicted that the combined inhibition of JNK and FLT3, may reverse resistance to tyrosine kinase inhibitors, which was confirmed in an appropriate FLT3 cell model by comparing the effects on apoptosis and proliferation of a JNK inhibitor and midostaurin vs. midostaurin alone.

Whereas the study does have some complexity, readability is enhanced by the inclusion of a section that summarizes the study design, plus a summary Figure. Availability of data as supplementary material is also a high point.

We thank the reviewer for his/her constructive comments about our manuscript. We believe that our story has been significantly strengthened by the changes and new data we provided.

Weaknesses:

(1) Some aspects of the methodology are not properly described (for instance, no methodological description has been provided regarding the clustering procedure that led to Figs. 2C and 2D).

We apologize for the lack of proper description of the methodology. We have extensively revised the methods section and worked to improve the clarity. We have now added a description of the clustering procedures in the methods section (pg. 19) of new Fig. S2D., Fig. S2E.

It is not clear in the manuscript whether the patients gave their consent to the use of their data in this study, or the approval from an ethical committee. These are very important points that should be made explicit in the main text of the paper.

We thank the reviewer for this comment. We have now added the following sentence (pg. 24): “Peripheral blood (PB) samples from 14 AML patients were obtained upon patient’s informed consent.”

The authors claim that some of the predictions of their models were later confirmed in the follow-up of some of the 14 patients, but it is not crystal clear whether the models helped the physicians to make any decisions on tailored therapeutic interventions, or if this has been just a retrospective exercise and the predictions of the models coincide with (some of) the clinical observations in a rather limited group of patients. Since the paper presents this as additional validation of the models' ability to guide personalized treatment decisions, it would be very important to clarify this point and expand the presentation of the results (comparison of observations vs. model predictions).

As described in the introduction section, this study was inspired by an urgent clinical problem in AML research: patients carrying the ITD in the TKD domain of the FLT3 receptor display poor prognosis and do not respond to current therapy: Midostaurin (which on the other hand is effective in patients with the ITD in the JMD domain).

To fill this gap, we gathered a team of 18 participants, of which 7 have a clinical background and have expertise in the diagnosis, treatment and management of AML patients and 5 are experts in Boolean modeling. The scope of the project is the development of a computational approach to identify possible alternative solutions for FLT3ITD-TKD AML patients, generating future lines of investigations. Drug combinations are currently under investigation as a potential means of avoiding drug resistance and achieving more effective and durable treatment responses. However, it is impractical to test for potential synergistic properties among all available drugs using empirical experiments alone. With our approach, we developed models that recreated in silico the main differences in the signaling of sensitive and resistant cells to support the prioritization of novel therapies. Prompted by the reviewer suggestions, we have now extended the validation of our models, through the comparison with publicly available cell lines and patient-derived dataset. We have also confirmed our results by performing in vitro experiments in patient-derived primary blasts treated with midostaurin and/or JNK inhibitor. Importantly, we have already demonstrated that hitting cell cycle regulators in FLT3ITD-TKD cells can be an effective approach to kill resistant leukemia cells (Massacci et al., 2023; Pugliese et al., 2023). We are aware that changing the clinical practice and the therapies for patients require a proper clinical study which goes far beyond the scope of this manuscript.

However, we hope that our results can be translated soon from “bench-to-bed”. Importantly, we believe that our study can open lines of investigations aimed at the application of our approach to identify promising therapeutic strategies in other clinical settings.

Recommendations for the authors

The reviewers have highlighted significant issues regarding the inadequate level of evidence to support some of the conclusions, plus lack of an exhaustive methodological description that may jeopardize reproducibility.

We hope that the editor and the reviewers will appreciate the extensive revision we made and new data and analysis we provided to strengthen our story.

Reviewer #1 (Recommendations For The Authors):

(1) In Fig 2D the hierarchical tree is off-set in relation to the treatment symbols and names in the middle of the Figure. In addition, I do not see FLT3i combination with JNKi in the JMD cells (perhaps, a coloring error?).

We thank the reviewer for this observation. We have now revised the hierarchical tree, which is now in Figure S2D, we have aligned the tree with the symbols and names and corrected the colouring error for the sample FLT3i+JNKi in JMD cells.

(2) Midostaurin and PKC412 refer to the same drug and are used interchangeably in the manuscript. Using one name consistently would improve readability.

We have now improved the readability of the text and the Figures by choosing “Midostaurin” when we refer to the FLT3 inhibitor.

(3) It is not clear to me why the FLT3-ITD-JMD cells are not presented in Fig. 4B. Perhaps their values are 0? In that case, the readability would be improved by including a thin blue line representing zero values. Additionally, on p.8 the authors state "Interestingly, in the FLT3ITDTKD model, the combined inhibition of JNK and FLT3, exclusively, in silico restores the TKI sensitivity, as revealed by the evaluation of the apoptosis and proliferation levels (Fig. 4B-C)." but Fig. 4C shows no differential effects of JNK inhibition in sensitive versus resistant cells.

To address the reviewer's point, we’ve added a thin blue line representing the zero values of the FLT3ITD-JMD in the results of the simulations in Figure 4B. Regarding the Figure 4C, the reviewer is right in saying that there is no difference in terms of proliferation between sensitive and resistant cells upon JNKi and FLT3i co-inhibition. However, we can see lower proliferation levels in both cell lines as compared to the “untreated” condition. Indeed, the simulation suggests that by combining JNK and FLT3 inhibition we restore the resistant phenotype lowering the proliferation rate of the resistant cells to the TKI-sensitive levels.

Reviewer #2 (Recommendations For The Authors):

I have addressed a number of concerns in the public review. Much better effort needs to be made to provide sufficient methodological detail (to permit independent validation by a sufficiently capable and motivated party) and explain the rationale of important parameter selections. Furthermore, I urge the authors to take advantage of the plethora of publicly available real-world data to validate their predicted outcomes.

We are grateful to the reviewer for the careful revisions. All the aspects raised have been discussed in the specific sections of the public review. In summary, we have provided more methodological details, by revising the text, the methods session, by adding a new step-by-step description of the modelling strategy, the parameters and the criteria adopted in each phase (supplementary methods) and by referring to the entire code developed. Prompted by the reviewer suggestions, we have performed a novel and extensive comparison of our model with three different publicly available datasets. This analysis significantly strengthens our story, and a new supplementary Figure (Fig. S5) summarizes our findings (pg. 9-14 of this document).

Reviewer #3 (Recommendations For The Authors):

(1) At first sight, the distribution of the data points in the PCA space does not really seem to speak of nice clustering. Have the authors computed any clustering validation metric to assess if their clustering strategy is adequate and how informative the results are? Further analysis of this point of the article is precluded by the absence of a clear methodological description.

Here we have used the PCA analysis to obtain a global view of our complex multiparametric data. We have now worked on the PCA to improve its readability. As shown in the new Figure 2D, PCA analysis showed that the activity level of sentinel proteins stratifies cells according to FLT3 activation status (component 1: presence vs absence of FLT3i) and cytokine stimulation (component 2: IGF1 vs TNF⍺). We have now added new experimental details on this part in the methods section (pg. 19) and we deposited the code used for the clustering strategy on the GitHub repository (https://github.com/SaccoPerfettoLab/FLT3ITD_driven_AML_Boolean_models).

(2) Whereas scientists and medical professionals who work in the field of oncology may be familiar with some of the abbreviations used here, it would be good for improved readability by a more general audience to make sure that all the abbreviations (e.g., TKI) are properly defined the first time that they appear in the text.

We thank the reviewer for this observation. To improve the readability of the text, we properly defined all the abbreviations in their first appearance, and we added the “Abbreviation” paragraph at page 15 of the manuscript to summarize them all.

(3) How were the concentrations of the combined treatments chosen in the cell assays used as validation?

We thank the reviewer for giving us the chance to clarify this point. We implemented the Methods with additional information about the treatments used in the validations. We detailed the SP600125 IC50 evaluation and usage in our cell lines (pg.22): IC50 values are approximately 1.5 µM in FLT3-ITD mutant cell lines; the SP600125 treatment affects cell viability, reaching a plateau phase of cell death and at about 2 µM. I used the minimal dose of SP600125 (10µM) to properly inhibit JNK. (Kim et al., 2010; Moon et al., 2009).

We also specified (pg.22) that the concentration of Midostaurin was chosen based on the previously published work (Massacci et al., 2022): FLT3 ITD-TKD cells treated with Midostaurin 100nM show lower apoptotic rate and higher cell viability compared to FLT3 ITD-JMD cells.

The concentration of SB203580 and UO126 was chosen based on previous data available in the lab and set up experiments (pg.22).

(4) The authors say that "we were able to derive patient-specific signaling features and enable the identification of potential tailored treatments restoring TKI resistance" and that "our predictions were confirmed by follow-up clinical data for some patients". However, the results section on this part of the manuscript is rather scarce (the main text should be much more descriptive about the results summarized in Fig. 5, which are not self-explanatory).

We thank the reviewer for this observation. We have now expanded the text to provide a more comprehensive description of the results about personalized Boolean model generation and usage and the content presented in Fig. 5 (pg.10-12).

(5) I do not really agree with the final conclusion about this paper being "the proof of concept that our personalized informatics approach described here is clinically valid and will enable us to propose novel patient-centered targeted drug solutions". First, the clinical data used here belongs to a rather low number of patients. Second, as mentioned before, it is not clear if the models have been used to make any prospective decision or if this conclusion is drawn from an in vitro assay plus a retrospective analysis on a limited number of patients. Moreover, a description of the results and the discussion of the part of the manuscript dealing with patientspecific models is rather scarce, and it is difficult to see how the authors support their conclusions. Also, the statement " In principle, the generalization of our strategy will enable to obtain a systemic perspective of signaling rewiring in different cancer types, driving novel personalized approaches" may be a bit overoptimistic if one considers that so far, the approach has only been applied to a single type of drug-resistant cancer.

We thank the reviewer for this comment. We agree with the referees that the clinical data we used belongs to a rather low number of patients. However, during the revision we have extensively worked to support the clinical relevance of our models and our discoveries. Specifically, we have compared our Boolean logic models with two different publicly available datasets on phosphoproteomics and drug sensitivity of FLT3ITD-JMD and FLT3ITD-TKD cell lines and blasts (FigS5 and answer to reviewer 2, point 3). Importantly, these datasets independently validated our models, highlighting that our approach has a translational value. Additionally, we have performed novel experiments by measuring the apoptotic rate of patient-derived primary blasts upon pharmacological suppression of JNK (Fig. 4H, pg. 10 of main text). Our data highlights that our approach has the potential to suggest novel effective treatments.

That said, we have now revised the discussion to avoid overstatements.

References

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Author Response

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

We thank you for the time you took to review our work and for your feedback!

The major changes to the manuscript are:

1) Promoted by multiple reviewers, we have replaced the statistical analysis in Figure 1L with a bootstrap analysis, added an ANOVA (in Table S1), and have also added the same analysis with mice as a statistical unit as Figure S4J to the manuscript.

2) In response to reviewer 1, comment 3, we have replaced the response latency maps previously shown in Figures 3B, 3C, 3E and 3F with response amplitude maps.

3) In response to reviewer 2, comment 1, we have added a variant of the response traces shown in Figures 3B, 3C, 3E and 3F with mice as the statistical unit as Figures S2C and S2D.

4) In response to reviewer 2, public review, we have added data from additional experiments as Figures S6F-S6H, that control for the effect of a saline injection.

A detailed point-by-point response to all reviewer concerns is provided in the following.  

Reviewer #1 (Public Review):

The authors present a study of visuo-motor coupling primarily using wide-field calcium imaging to measure activity across the dorsal visual cortex. They used different mouse lines or systemically injected viral vectors to allow imaging of calcium activity from specific cell-types with a particular focus on a mouse-line that expresses GCaMP in layer 5 IT (intratelencephalic) neurons. They examined the question of how the neural response to predictable visual input, as a consequence of self-motion, differed from responses to unpredictable input. They identify layer 5 IT cells as having a different response pattern to other cell-types/layers in that they show differences in their response to closed-loop (i.e. predictable) vs open-loop (i.e. unpredictable) stimulation whereas other cell-types showed similar activity patterns between these two conditions. They analyze the latencies of responses to visuomotor prediction errors obtained by briefly pausing the display while the mouse is running, causing a negative prediction error, or by presenting an unpredicted visual input causing a positive prediction error. They suggest that neural responses related to these prediction errors originate in V1, however, I would caution against overinterpretation of this finding as judging the latency of slow calcium responses in wide-field signals is very challenging and this result was not statistically compared between areas. Surprisingly, they find that presentation of a visual grating actually decreases the responses of L5 IT cells in V1. They interpret their results within a predictive coding framework that the last author has previously proposed. The response pattern of the L5 IT cells leads them to propose that these cells may act as 'internal representation' neurons that carry a representation of the brain's model of its environment. Though this is rather speculative. They subsequently examine the responses of these cells to anti-psychotic drugs (e.g. clozapine) with the reasoning that a leading theory of schizophrenia is a disturbance of the brain's internal model and/or a failure to correctly predict the sensory consequences of self-movement. They find that anti-psychotic drugs strongly enhance responses of L5 IT cells to locomotion while having little effect on other cell-types. Finally, they suggest that anti-psychotics reduce long-range correlations between (predominantly) L5 cells and reduce the propagation of prediction errors to higher visual areas and suggest this may be a mechanism by which these drugs reduce hallucinations/psychosis.

This is a large study containing a screening of many mouse-lines/expression profiles using wide-field calcium imaging. Wide-field imaging has its caveats, including a broad point-spread function of the signal and susceptibility to hemodynamic artifacts, which can make interpretation of results difficult. The authors acknowledge these problems and directly address the hemodynamic occlusion problem. It was reassuring to see supplementary 2-photon imaging of soma to complement this data-set, even though this is rather briefly described in the paper. Overall the paper's strengths are its identification of a very different response profile in the L5 IT cells compared other layers/cell-types which suggests an important role for these cells in handling integration of self-motion generated sensory predictions with sensory input. The interpretation of the responses to anti-psychotic drugs is more speculative but the result appears robust and provides an interesting basis for further studies of this effect with more specific recording techniques and possibly behavioral measures.

We thank the reviewer for the feedback and the help with improving the manuscript. We agree, the findings presented in this study are merely a starting point. The two questions we are currently pursuing in follow up work are:

1) Do the findings generalize to all known antipsychotic drugs?

2) What is the mechanism by which these drugs induce a decorrelation of activity, specifically in layer 5 neurons?

But we suspect these questions will take at least a few more years of research to answer.

Reviewer #2 (Public Review):

Summary:

This work investigates the effects of various antipsychotic drugs on cortical responses during visuomotor integration. Using wide-field calcium imaging in a virtual reality setup, the researchers compare neuronal responses to self-generated movement during locomotion-congruent (closed loop) or locomotionincongruent (open loop) visual stimulation. Moreover, they probe responses to unexpected visual events (halt of visual flow, sudden-onset drifting grating). The researchers find that, in contrast to a variety of excitatory and inhibitory cell types, genetically defined layer 5 excitatory neurons distinguish between the closed and the open loop condition and exhibit activity patterns in visual cortex in response to unexpected events, consistent with unsigned prediction error coding. Motivated by the idea that prediction error coding is aberrant in psychosis, the authors then inject the antipsychotic drug clozapine, and observe that this intervention specifically affects closed loop responses of layer 5 excitatory neurons, blunting the distinction between the open and closed loop conditions. Clozapine also leads to a decrease in long-range correlations between L5 activity in different brain regions, and similar effects are observed for two other antipsychotics, aripripazole and haloperidol, but not for the stimulant amphetamine. The authors suggest that altered prediction error coding in layer 5 excitatory neurons due to reduced longrange correlations in L5 neurons might be a major effect of antipsychotic drugs and speculate that this might serve as a new biomarker for drug development.

Strengths:

• Relevant and interesting research question:

The distinction between expected and unexpected stimuli is blunted in psychosis but the neural mechanisms remain unclear. Therefore, it is critical to understand whether and how antipsychotic drugs used to treat psychosis affect cortical responses to expected and unexpected stimuli. This study provides important insights into this question by identifying a specific cortical cell type and long-range interactions as potential targets. The authors identify layer 5 excitatory neurons as a site where functional effects of antipsychotic drugs manifest. This is particularly interesting as these deep layer neurons have been proposed to play a crucial role in computing the integration of predictions, which is thought to be disrupted in psychosis. This work therefore has the potential to guide future investigations on psychosis and predictive coding towards these layer 5 neurons, and ultimately improve our understanding of the neural basis of psychotic symptoms.

• Broad investigation of different cell types and cortical regions:

One of the major strengths of this study is quasi-systematic approach towards cell types and cortical regions. By analysing a wide range of genetically defined excitatory and inhibitory cell types, the authors were able to identify layer 5 excitatory neurons as exhibiting the strongest responses to unexpected vs. expected stimuli and being the most affected by antipsychotic drugs. Hence, this quasi-systematic approach provides valuable insights into the functional effects of antipsychotic drugs on the brain, and can guide future investigations towards the mechanisms by which these medications affect cortical neurons.

• Bridging theory with experiments

Another strength of this study is its theoretical framework, which is grounded in the predictive coding theory. The authors use this theory as a guiding principle to motivate their experimental approach connecting visual responses in different layers with psychosis and antipsychotic drugs. This integration of theory and experimentation is a powerful approach to tie together the various findings the authors present and to contribute to the development of a coherent model of how the brain processes visual information both in health and in disease.

Weaknesses:

• Unclear relevance for psychosis research

From the study, it remains unclear whether the findings might indeed be able to normalise altered predictive coding in psychosis. Psychosis is characterised by a blunted distinction between predicted and unpredicted stimuli. The results of this study indicate that antipsychotic drugs further blunt the distinction between predicted and unpredicted stimuli, which would suggest that antipsychotic drugs would deteriorate rather than ameliorate the predictive coding deficit found in psychosis. However, these findings were based on observations in wild-type mice at baseline. Given that antipsychotics are thought to have little effects in health but potent antipsychotic effects in psychosis, it seems possible that the presented results might be different in a condition modelling a psychotic state, for example after a dopamine-agonistic or a NMDA-antagonistic challenge. Therefore, future work in models of psychotic states is needed to further investigate the translational relevance of these findings.

• Incomplete testing of predictive coding interpretation

While the investigation of neuronal responses to different visual flow stimuli Is interesting, it remains open whether these responses indeed reflect internal representations in the framework of predictive coding. While the responses are consistent with internal representation as defined by the researchers, i.e., unsigned prediction error signals, an alternative interpretation might be that responses simply reflect sensory bottom-up signals that are more related to some low-level stimulus characteristics than to prediction errors. Moreover, This interpretational uncertainty is compounded by the fact that the used experimental paradigms were not suited to test whether behaviour is impacted as a function of the visual stimulation which makes it difficult to assess what the internal representation of the animal actual was. For these reasons, the observed effects might reflect simple bottom-up sensory processing alterations and not necessarily have any functional consequences. While this potential alternative explanation does not detract from the value of the study, future work would be needed to explain the effect of antipsychotic drugs on responses to visual flow. For example, experimental designs that systematically vary the predictive strength of coupled events or that include a behavioural readout might be more suited to draw from conclusions about whether antipsychotic drugs indeed alter internal representations.

• Methodological constraints of experimental design

While the study findings provide valuable insights into the potential effects of antipsychotic drugs, it is important to acknowledge that there may be some methodological constraints that could impact the interpretation of the results. More specifically, the experimental design does not include a negative control condition or different doses. These conditions would help to ensure that the observed effects are not due to unspecific effects related to injection-induced stress or time, and not confined to a narrow dose range that might or might not reflect therapeutic doses used in humans. Hence, future work is needed to confirm that the observed effects indeed represent specific drug effects that are relevant to antipsychotic action.

Conclusion:

Overall, the results support the idea that antipsychotic drugs affect neural responses to predicted and unpredicted stimuli in deep layers of cortex. Although some future work is required to establish whether this observation can indeed be explained by a drug-specific effect on predictive coding, the study provides important insights into the neural underpinnings of visual processing and antipsychotic drugs, which is expected to guide future investigations on the predictive coding hypothesis of psychosis. This will be of broad interest to neuroscientists working on predictive coding in health and in disease.

We thank the reviewer for the feedback and the help with improving the manuscript.

Regarding the concern of a lack of a negative control, we have repeated the correlation measurement experiments in a cohort of Tlx3-Cre x Ai148 mice that received injections of saline. This analysis is now shown in Figure S6F-S6H. Saline injections did not change correlations in L5 IT neurons. Combined with the absence of changes in the L5 IT correlation structure following amphetamine injections (Figures 7G – 7I), this suggests that unspecific effects related to stress of injection, or simply time, cannot explain the observed decorrelation effect of the antipsychotic drugs.

And we fully agree, a lot more work is needed to confirm that the observed effects are specific and relevant to antipsychotic action.

Reviewer #3 (Public Review):

The study examines how different cell types in various regions of the mouse dorsal cortex respond to visuomotor integration and how antipsychotic drugs impacts these responses. Specifically, in contrast to most cell types, the authors found that activity in Layer 5 intratelencephalic neurons (Tlx3+) and Layer 6 neurons (Ntsr1+) differentiated between open loop and closed loop visuomotor conditions. Focussing on Layer 5 neurons, they found that the activity of these neurons also differentiated between negative and positive prediction errors during visuomotor integration. The authors further demonstrated that the antipsychotic drugs reduced the correlation of Layer 5 neuronal activity across regions of the cortex, and impaired the propagation of visuomotor mismatch responses (specifically, negative prediction errors) across Layer 5 neurons of the cortex, suggesting a decoupling of long-range cortical interactions.

The data when taken as a whole demonstrate that visuomotor integration in deeper cortical layers is different than in superficial layers and is more susceptible to disruption by antipsychotics. Whilst it is already known that deep layers integrate information differently from superficial layers, this study provides more specific insight into these differences. Moreover, this study provides a first step into understanding the potential mechanism by which antipsychotics may exert their effect.

Whilst the paper has several strengths, the robustness of its conclusions is limited by its questionable statistical analyses. A summary of the paper's strengths and weaknesses follow.

Strengths:

The authors perform an extensive investigation of how different cortical cell types (including Layer 2/3, 4 , 5, and 6 excitatory neurons, as well as PV, VIP, and SST inhibitory interneurons) in different cortical areas (including primary and secondary visual areas as well as motor and premotor areas), respond to visuomotor integration. This investigation provides strong support to the idea that deep layer neurons are indeed unique in their computational properties. This large data set will be of considerable interest to neuroscientists interested in cortical processing.

The authors also provide several lines of evidence that visuomotor information is differentially integrated in deep vs. superficial layers. They show that this is true across experimental paradigms of visuomotor processing (open loop, closed loop, mismatch, drifting grating conditions) and experimental manipulations, with the demonstration that Layer 5 visuomotor integration is more sensitive to disruption by the antipsychotic drug clozapine, compared with cortex as a whole.

The study further uses multiple drugs (clozapine, aripiprazole and haloperidol) to bolster its conclusion that antipsychotic drugs disrupt correlated cortical activity in Layer 5 neurons, and further demonstrates that this disruption is specific to antipsychotics, as the psychostimulant amphetamine shows no such effect.

In widefield calcium imaging experiments, the authors effectively control for the impact of hemodynamic occlusions in their results, and try to minimize this impact using a crystal skull preparation, which performs better than traditional glass windows. Moreover, they examine key findings in widefield calcium imaging experiments with two-photon imaging.

Weaknesses:

A critical weakness of the paper is its statistical analysis. The study does not use mice as its independent unit for statistical comparisons but rather relies on other definitions, without appropriate justification, which results in an inflation of sample sizes. For example, in Figure 1, independent samples are defined as locomotion onsets, leading to sample sizes of approx. 400-2000 despite only using 6 mice for the experiment. This is only justified if the data from locomotion onsets within a mouse is actually statistically independent, which the authors do not test for, and which seems unlikely. With such inflated sample sizes, it becomes more likely to find spurious differences between groups as significant. It also remains unclear how many locomotion onsets come from each mouse; the results could be dominated by a small subset of mice with the most locomotion onsets. The more disciplined approach to statistical analysis of the dataset is to average the data associated with locomotion onsets within a mouse, and then use the mouse as an independent unit for statistical comparison. A second example, for instance, is in Figure 2L, where the independent statistical unit is defined as cortical regions instead of mice, with the left and right hemispheres counting as independent samples; again this is not justified. Is the activity of cortical regions within a mouse and across cortical hemispheres really statistically independent? The problem is apparent throughout the manuscript and for each data set collected. An additional statistical issue is that it is unclear if the authors are correcting for the use of multiple statistical tests (as in for example Figure 1L and Figure 2B,D). In general, the use of statistics by the authors is not justified in the text.

Finally, it is important to note that whilst the study demonstrates that antipsychotics may selectively impact visuomotor integration in L5 neurons, it does not show that this effect is necessary or sufficient for the action of antipsychotics; though this is likely beyond the scope of the study it is something for readers to keep in mind.

We thank the reviewer for the feedback and the help with improving the manuscript.

Regarding the concerns of statistical analysis, this may partially be a misunderstanding. We apologize for the lack of clarity. For example, the data in Figures 1F-1K is indeed shown as averaged over locomotion onsets, but there is no statistical analysis performed in these panels. The unit for the statistical analysis shown in Figure 1L is brain area (not locomotion onset). A central tenet of the analysis shown in Figures 1L and 2 is that the effect of differential activation during closed and open loop locomotion onsets is not specific to visual areas of cortex. In visual areas of cortex, one would expect to find a difference. In essence, the surprising finding here is the lack of a difference in other cell types but L5 IT neurons. Thus, in the analyses of those figure panels we are testing whether the effect is present on average across all cortical areas. Hence, we chose the statistical unit of Figure 1L to be cortical areas, not mice. We have added the same analysis with mice as a statistical unit as Figure S4J.

Reviewer #1 (Recommendations For The Authors):

I have a few concerns and questions that I would like to see addressed:

1) Figure 1L - the statistics are a little unusual here as the errors are across visual areas rather than across mice or hemispheres. This isn't ideal as ideally, we want to generalize the results across animals, not areas, and the results seem to be driven mostly by V1/RSC. I would like to see comparisons using mice as the statistical unit either in an ANOVA with areas as factors or post-hoc comparisons per area.

Based on the assumption that visual cortex should respond to visual stimuli, we would have expected to find a difference between closed and open loop locomotion onset responses in all cell types in visual areas of cortex (a closed loop locomotion onset being the combination of locomotion and visual flow onset, while an open loop locomotion onset lacks the visual flow component). Thus, the first surprise was that in most cell types we found very little difference between these two locomotion onset types. Conversely, in Tlx3-positive L5 IT neurons the difference was apparent well outside of the visual areas of cortex (even though the difference was indeed strongest in V1/RSC). To quantify the extent to which closed and open loop locomotion onsets result in different activity patterns across dorsal cortex we performed the analyses shown in Figures 1L and 2. To make the point that the effect was observable on average across cortical areas, we used cortical area as a unit in Figure 1L. We have added the analysis shown in Figure 1L with mice as the statistical unit as Figure S4J and have added the ANOVA information to Table S1, as suggested.

2) The reduction of activity of L5 IT cells in V1 after the presentation of gratings is curious. The authors suggest it might have been due to one population of cells tuned for the orientation of the presented grating suppressing the remaining cells leading to an aggregate negative response. However, they also observed this negative response in the 2p signal for individual somata. Presumably in the 2p data they could check their hypothesis - is there a group of cells that were tuned for the grating? Is it possible that for some reason the L5 IT cells in the 2p were not being activated by the grating because of their RF locations? How large were the gratings - I didn't see this in the methods section?

We can certainly identify neurons that selectively increase activity to one particular grating. See Author response image 1, for vertical and horizontal gratings. The gratings were presented full-field on a toroidal screen that surrounded the mouse (240 degrees horizontal and 100 degrees vertical coverage of the visual field). This covered a large fraction of the field of view of the mouse. While we did not map receptive fields of individual neurons in this study, it is unlikely that the receptive fields of the neurons recorded were outside the stimulated area. We have made this clearer in the manuscript.

Author response image 1.

The population L5 IT neuron response to full-field drifting grating stimuli was a decrease of activity, yet there were increasing responses in a subset of neurons. (A) Heatmap of responses of all L5 IT neuron somata recorded with two-photon imaging in 7 Tlx3-Cre x Ai148 mice to drifting gratings of vertical orientation, sorted by their response. Data were sorted on odd trials and plotted on even trials to avoid regression to the mean artifacts. Dashed black box marks the top 10% responsive neurons. The data are a subset of the data shown in Figure S3D. (B) As in A, but for responses to drifting gratings of horizontal orientation. (C) Responses of top 10% vertical grating responsive neurons (dashed black box in A) to vertical (orange) or horizontal gratings (green). Neurons were selected on odd trials, and the average response of even trials is shown. (D) As in A, but sorted to the response of horizontal drifting gratings. (E) As in D, but for the horizontal grating stimulus. (F) As in C, but for the top 10% horizontal grating responsive neurons.

3) I would caution against over-interpretation of latencies from wide-field GCaMP activity (Figure 3). A weaker response in a smaller population of neurons that has the same latency as a strong response in a large population of neurons will appear to have different latencies when convolved with the GCaMP kernel. Also there doesn't appear to be any statistical support for different latencies in different cortical areas. Either this should be correctly treated (ideally with linear mixed effects models to account for the increased correlation within animals) or the latency conclusions should be removed from the manuscript (my recommendation).

We suspect that by “latency conclusions” the reviewer means “latency analysis”. The only time we mention latency differences is to state that: “In C57BL/6 mice that expressed GCaMP brain wide, both visuomotor mismatch and grating stimuli resulted in increases of activity that were strongest and appeared first in visual regions of dorsal cortex (Figures 3A-3C).”

Nevertheless, we agree with the reviewer that response latency and response amplitude are not independent in our measurements and have replaced the latency plots in Figures 3B, 3C, 3E and 3F with average response maps.

4) Given that the data is baseline corrected, is it possible that the effects of the anti-psychotic drugs on L5IT cells was due to a change in the baseline activity of this population?

While we do find a small increase in average activity as a result of antipsychotic drug injections (Author response image 2), these effects are much smaller than those on locomotion onset responses.

Author response image 2.

On average, activity was increased in dorsal cortex after administration of antipsychotic drugs. Average calcium activity over the entire recording session before (naïve) and after (antipsy.) the administration of antipsychotic drugs. Colored lines indicate paired data for individual mice (Blue: 5 mice that had received clozapine, green: 3 mice that had received aripiprazole, red: 3 mice that had received haloperidol).

To illustrate that the clozapine induced change in locomotion related activity cannot be explained by baseline activity differences, we have replotted the responses shown in Figures 4D and 4E, S3B, S5F without baseline subtraction (Author response image 3).

Author response image 3.

Antipsychotic drug injection only modestly shifts the baseline before locomotion onsets. (A) Average response expressed as F/F0 (wherein F0 was defined as the median of a recording session) during closed (solid line, 1101 onsets) and open loop (dashed line, 348 onsets) locomotion onsets in 5 Tlx3-Cre x Ai148 mice that expressed GCaMP6 in layer L5 IT neurons. Shading indicates SEM over onsets. Dashed horizontal line marks a value of F/F0 of 1.005 for comparison with panel B. Underlying data were the same as in Figures 4D and 4E. (B) As in A, but after a single intraperitoneal injection of the drug clozapine and for 707 closed and 350 open loop locomotion onsets. (C) Average response expressed as F/F0 (wherein F0 was defined as the median of a recording session) of L5 soma in V1, recorded with two-photon imaging in 7 Tlx3-Cre x Ai148 mice that expressed GCaMP6 in L5 IT neurons, during either closed (solid) or open loop (dashed) locomotion onsets. Shading indicates SEM over 8434 neurons. Dashed horizontal line marks a value of F/F0 of 1.045 for comparison with panel D. Underlying data were the same as in Figure S3B. (D) As in C, but for the 3 Tlx3 x Ai148 mice that had received a single intraperitoneal injection of clozapine. Underlying data were from Figure S5F.

5) Figure 5/Figure S6 - Do the results really reflect an effect of distance or is it driven by areas from different hemispheres. Does the result hold if they factor out the effect of hemisphere or calculate the results within hemisphere?

The effect appears qualitatively unchanged when we exclude interhemispheric connections from the analysis (Author response image 4).

Author response image 4.

As in Figures 6D-6F, but with the exclusion of interhemispheric connections. The decorrelation effect appears qualitatively unchanged.

Reviewer #2 (Recommendations For The Authors):

In addition to my public review, I only have one statistics-related and a few minor editing suggestions for the abstract. I hope that these might help the authors to improve their manuscript.

1) It seems that the researchers are combining observations across different subjects, as seen in Figure 1F-L as well as in all of the other figures. While this has been a common practice in their field, it is now widely recognized that this approach can result in biased statistical inferences since it violates the assumptions of most statistical tests (see this recent discussion: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7906290/). As such, it may be beneficial for the authors to consider utilizing statistical tests that are designed to accurately deal with hierarchical data sets, like linear mixed models or hierarchical bootstrap, to confirm their key results. Additionally or alternatively, presenting data grouped by subject would help demonstrate the consistency of their findings across subjects.

Please note, in Figures 1F-1K, there are no statistical tests – but the data are indeed averaged over locomotion onsets across all mice. We could use hierarchical sampling to calculate a bootstrap estimate of the mean response curves and show those instead, but that is also not standard practice in the field. We suspect this is also not what the reviewer is suggesting. In Figure 1L, the unit is indeed brain areas (see also our response to comment 1 of reviewer 1), but it is not areas x mice (i.e., the analysis is not hierarchical).

We have now added a supplementary panel (Figure S4J) that shows the data of Figure 1L with mouse as the statistical unit (note, this is also not hierarchical). We have replaced the statistical test data using bootstrapping, as the reviewer suggests. This information can be found in Table S1.<br /> In Figures 2B and 2D, we have replaced the statistical test with hierarchical bootstrap, and updated the corresponding information in Table S1.

For Figure 3, in which we show mismatch and grating onset responses averaged using onsets as the base unit, we have added supplementary panels (Figure S2) that show the same analysis using mice as the statistical unit. This did not change any of the conclusions. Note, there was no statistical testing in Figure 3.

For the decorrelation effect of the different antipsychotic drugs that we show in Figures 6 and 7 the statistical unit is mice x region pairs (that is, while the structure is hierarchical, all mice contribute the same number of pairs). Our data are underpowered to use hierarchical bootstrap for testing the drug effects individually. However, if we combine all antipsychotic drug data (clozapine, aripiprazole, and haloperidol) we reach the same conclusions with hierarchical bootstrap as with the statistical tests (ttest and ranksum) used in the paper (Author response image 5).

Author response image 5.

Hierarchical bootstrap of the combined distribution of correlation values shown in Figures 6F, 7C and 7F did not change the conclusion that administration of antipsychotic drugs reduces L5 IT neuron correlations. Statistical comparisons using hierarchical bootstrap: Short-range vs no change, p < 0.001; long-range vs no change, p < 0.001; short-range vs longrange, p < 0.05.

2) Given the impressive amount of data, I found it sometimes a little difficult to follow the manuscript. The authors might want to consider including a high-level overview of their results and rationales at the end of the introduction, and start each Results subsection with a sentence referring back to that highlevel overview ("To test whether X, we did Y and present it in this section.")

We have attempted to improve the writing along these lines.

3) Some suggestions that might further improve the clarity of writing.

Abstract: Does the brain really distinguish between different "activity patterns", or would externallygenerated and self-generated "stimuli" be a slightly more accurate term to describe the observed alterations in schizophrenia?

We would argue that (outside of sensory organs) the brain only has access to activity patterns, not stimuli directly. We would prefer to keep the phrasing with activity patterns here.

Line 12: It might be easier to follow if the authors explicitly related that sentence back to the previous sentence "their ability to identify self-generated activity patterns" -> "their ability to distinguish between externally and self/internally generated ..."

Absolutely correct – we have improved the writing here.

Line 14: It remains unclear how visuomotor integration relates to the problem of distinguishing between self- and externally generated stimuli.

We have attempted to expand on this in the abstract.

Line 26: it remains unclear how the results support the activation of "internal representations" as this term has not been defined previously

We have removed “internal representation” from the abstract.

Results, line 80ff: I was confused by the description of all the different investigated cell types, as the first figure panels then only talk about brain wide and L5. Maybe the authors might find that shortening this with a reference to the methods might improve the flow.

We have moved the list of cell types and mouse lines to the methods, as suggested.  

Reviewer #3 (Recommendations For The Authors):

The authors should strongly consider reassessing their statistics as outlined in the Public Review.

Specifically:

1) They should justify their definition of independent statistical unit; if this is not the mouse, they should justify why another definition (i.e. locomotion onset) is used, and show that their defined statistical unit achieves the requirements of being statistically independent (i.e. variance of the unit within a mouse is statistically indistinguishable from variance found between mice; more formally they could calculate the intraclass correlation (ICC)).

We assume the reviewer is referring mainly to Figure 1 and therein to panel 1L.

Since we did not perform statistical tests on the calcium traces, we are not sure why we would need to justify the choice of the unit we were showing. Moreover, Figure S2 shows the data of the V1 ROI averaged over mice to address this concern. As also mentioned to reviewer 2, we have amended this Figure S2 for the mouse-averaged traces of the V1 ROI data shown in main Figure 3.

3) They should justify the statistical tests they use and whether they corrected for multiple comparisons; why for example was an ANOVA not used for Figure 1L and Figure 2B,D?

We did not rely on ANOVA statistics for Figure 1L because we were mainly interested in carving out that Tlx3- (and Ntsr1-) positive mice inhabit a unique space when comparing the similarity of activity during closed and open loop locomotion onsets. We appreciate the reviewer taking a slightly different point of view on the data and now additionally report the ANOVA test result in Table S1. We have also opted to replace the statistical test in Figure 1L with bootstrapping. Lastly, we added Figure S4J which now shows the data in Figure 1L but with mice as the statistical unit.

With similar logic, in Figure 2, we were not interested in comparing how the correlation of activity in cortical regions with locomotion behavior evolves over regions within a visuomotor feedback condition (closed loop, open loop or dark) but rather how a given region compares across feedback conditions.

Still, we have opted to replace the statistical test in Figures 2B and 2D with hierarchical bootstrap, as also suggested by reviewer #2, comment 1. This did not change the significance indicator bars. We have accordingly updated Table S1 in which we report the full statistics.

Author response:

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

Response to eLife Assessment:

We sincerely appreciate your recognition of the novelty and potential significance of our study, and we are grateful for your constructive and valuable comments.

With regard to your concern that cast immobilization (CI) may itself act as a stressor—potentially influencing skeletal muscle, brown adipose tissue (BAT), and locomotor energy expenditure—we fully recognize this as a highly important issue. In our study, we sought to interpret the findings in light of oxygen consumption and activity data; however, it is inherently difficult to disentangle systemic stress responses and the increased energetic costs associated with CI. We have therefore revised the manuscript to explicitly acknowledge this point as a limitation, and to identify it as a subject for future investigation.

We also greatly value your suggestion concerning the potential involvement of branched-chain amino acids (BCAAs) derived from adipose tissue in BAT thermogenesis. While our present work primarily focused on muscle-derived amino acids, previous studies have reported that impaired BCAA catabolism in white adipose tissue (WAT) is associated with elevated circulating BCAA levels and metabolic dysfunction [1]. Thus, the possibility that adipose tissue contributes to the BCAA pool used by BAT cannot be disregard. We fully agree that directly addressing this possibility would be highly valuable, and in future work we plan to locally administer isotope-labeled BCAAs into skeletal muscle or adipose tissue and analyze their contribution to circulating BCAA levels and BAT utilization. Although such experiments could not be performed within the timeframe of this resubmission, we have explicitly stated this limitation in the revised manuscript.

In summary, we have revised the text to acknowledge the limitations highlighted in your comments and to better clarify future research directions. We believe these revisions more accurately position our current study within the broader context. Once again, we are deeply grateful for your recognition of the originality of our work and for your constructive guidance in refining it.

Response to Reviewers:

We sincerely appreciate the reviewers’ thoughtful evaluations and constructive comments, and we are grateful for their recognition of the novelty and significance of our study.

Response to Reviewer 1:

We thank the reviewer for the detailed and thoughtful comments regarding the potential systemic effects of CI, including stress responses, energy balance, and tissue wasting. These factors are indeed critical when interpreting our findings, and we agree that CI is not merely a passive loss-of-function model but also introduces stress-related influences.

The principal aim of our study was to investigate the “physiological compensatory mechanisms” that are triggered by loss of muscle function induced by CI. Although CI inevitably elicits systemic metabolic alterations—including stress-related responses—our study is, to our knowledge, the first to demonstrate that a compensatory thermogenic pathway, mediated by the supply of amino acids from skeletal muscle to BAT, is activated under such conditions. We regard this as the central novelty of our work, and it is consistent with the reviewer’s observation that CI results in a “gain of function.”

Our intention is not to exclude stress as a contributing factor. Rather, we emphasize that under physiological stress conditions requiring BAT thermogenesis—such as reduced energy stores or decreased heat production from skeletal muscle—amino acid supply from muscle to BAT is induced. Importantly, this mechanism is not unique to CI, as we have confirmed similar metabolic crosstalk under acute cold exposure.

At the same time, we acknowledge that our current data do not allow us to conclude that “stress is not a primary driver” of BAT thermogenesis induced by CI. Chronic stress induced by CI appeared to be limited in our study (Fig. 2_figure supplement 2), but we cannot fully exclude stress-related effects. Accordingly, we now describe the potential triggers of BAT thermogenesis in the manuscript as either decreased body temperature due to muscle functional loss or stress, explicitly noting in the Discussion that stress and reductions in energy reserves may both contribute, as the reviewer suggested. We also modified the original overstatement that “suppression of muscle thermogenesis induces hypothermia,” and now limit the description to the observed phenomenon that “CI-induced restriction of muscle activity leads to reduced cold tolerance,” while recognizing that multiple factors—including stress, substrate availability, and BAT functional capacity—may underlie this effect.

We further appreciate the reviewer’s comment regarding the energetic burden imposed by CI. The cast weighed less than 2 g (5–10% of body weight), and thus increased locomotor costs cannot be excluded. However, locomotor activity during the dark phase was reduced by approximately 50%, making the net energetic effect difficult to quantify. In the manuscript, we now present oxygen consumption data and restrict our description to “an increase in oxygen consumption per body weight.” Moreover, as food intake remained almost unchanged compared with controls, the animals appear to have compensated for additional energetic demands, supporting the interpretation that the observed effects were not solely attributable to starvation.

We also find the reviewer’s suggestion—that CI induces BAT overactivation but impairs its functional capacity—extremely important. Indeed, although CI increased thermogenic gene expression in BAT, body temperature maintenance was impaired. We interpret this reduction in thermoregulation as reflecting decreased heat production from skeletal muscle; however, as the reviewer noted, under prolonged CI, depletion of energy stores could further prevent BAT from fully exerting its thermogenic function.

We have clarified in the revised Discussion that BAT activation under CI is transient, and that long-term outcomes may be influenced by contributions from other thermogenic organs, and that we recognize the impact of energy depletion as an important issue to be addressed in future studies. We also agree that detailed analyses of metabolic changes and BCAA dynamics following prolonged CI will be an important next step.

Regarding the reviewer’s concern about potential anesthesia effects on acute cold exposure experiments, we confirmed that body temperature had returned to baseline one hour before testing, and that mice displayed spontaneous feeding and grooming behaviors, which suggested adequate recovery. Moreover, the differences observed compared with sham-anesthetized controls support our interpretation that the results reflect CI-specific effects. Nonetheless, we acknowledge this potential confounding factor as an additional limitation.

Response to Reviewer 2:

We thank the reviewer for the constructive comments and clear summary of our findings. We fully agree that the impact of immobilization on skeletal muscle and BAT function under cold exposure represents a key future direction. In the present study, we performed acute cold exposure following short-term immobilization and assessed UCP1 expression and metabolic changes in BAT. However, we acknowledge that we did not fully examine coordinated functional adaptations between skeletal muscle and BAT under cold stress. In particular, how skeletal muscle–derived amino acid supply and IL-6–dependent mechanisms operate during cold exposure remains unresolved. We have therefore noted this explicitly as a limitation and highlighted it as a focus for future work. Going forward, we plan to investigate muscle–BAT metabolic crosstalk and IL-6 signaling in detail under cold conditions to clarify whether the observed responses are specific to CI or represent more general physiological adaptations.

(1) Herman MA, She P, Peroni OD, Lynch CJ, Kahn BB. Adipose tissue branched chain amino acid (BCAA) metabolism modulates circulating BCAA levels. J Biol Chem. 2010;285(15):11348-56. doi:10.1074/jbc.M109.075184.

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

Reviewer #1 (Public Review):

Summary:

Heat production mechanisms are flexible, depending on a wide variety of genetic, dietary, and environmental factors. The physiology associated with each mechanism is important to understand since loss of flexibility is associated with metabolic decline and disease. The phenomenon of compensatory heat production has been described in some detail in publications and reviews, notably by modifying BAT-dependent thermogenesis (for example by deleting UCP1 or impairing lipolysis, cited in this paper). These authors chose to eliminate exercise as an alternative means of maintaining body temperature. To do this, they cast either one or both mouse hindlimbs. This paper is set up as an evaluation of a loss of function of muscle on the functionality of BAT.

Strengths:

The study is supported by a variety of modern techniques and procedures.

Weaknesses:

The authors show that cast immobilization (CI) does not work as a (passive) loss of function, instead, this procedure produces a dramatic gain of function, putting the animal under considerable stress, inducing b-adrenergic effectors, increased oxygen consumption, and IL6 expression in a variety of tissues, together with commensurate cachectic effects on muscle and fat. The BAT is put under considerable stress, super-induced but relatively poor functioning. Thus within hours and days of CI, there is massive muscle loss (leading to high circulating BCAAs), and loss of lipid reserves in adipose and liver. The lipid cycle that maintains BAT thermogenesis is depleted and the mouse is unable to maintain body temperature.

I cannot agree with these statements in the Discussion:  

"We have here shown that cast immobilization suppressed skeletal muscle thermogenesis, resulting in failure to maintain core body temperature in a cold environment."

This result could also be attributed to high stress and decreased calorie reserves. Note also: CI suppresses 50% of locomotor activity, but the actual work done by the mouse carrying bilateral casts is not taken into account.

We appreciate the reviewer's suggestion. We thank you for raising this issue. As the reviewers suggest, we also consider that cold intolerance resulting from cast immobilization may be attributed to high stress levels, decreased calorie reserves, or reduced systemic locomotor activity. Indeed, reductions in the weight of visceral adipose tissue weight and increases in lipid utilization were observed in the early phase of cast immobilization (Fig.2G and 2F). This suggests that the depletion of calorie reserves induced by stress may affect cold intolerance in cast immobilized mice (Fig.1A-1B). On the other hand, the experiment shown in Fig.1C involved acute cold exposure of mice 2 h after cast immobilization. This result suggests that, even before the depletion of energy stores by immobilization of skeletal muscle, cast immobilization may cause cold intolerance in mice. In addition, as the reviewer suggests, cast immobilization may result in BAT thermogenesis and cachectic effects on muscle and fat. However, circulating corticosterone concentrations and hypothalamic CRH gene expression are not significantly altered after cast immobilization (Figure 2_figure supplement 2D-F). This raises questions about the contribution of stress to the changes in the systemic energy metabolism in this model. As such, we responded to the reviewers’ comments by revising this statement at the beginning of the ‘Discussion’ section and adding a discussion on pages 16, in addition to the existing discussion on pages 17–18.

Furthermore, to respond as best we could to the reviewer's comments, we performed additional experiments using the restraint stress model (Figure 7). We found that short-term restraint stress may recruit substrate supply from skeletal muscle for BAT thermogenesis via Il6 gene expression. Based on these data, we speculate that the interaction between BAT and skeletal muscle amino acid metabolism may operate under various physiological stress conditions, including infection and exercise, as well as skeletal muscle immobilization, stress, and cold exposure. This interaction may play a significant role in regulating body temperature and energy metabolism. We are currently investigating the effects of sympathetic activation on skeletal muscle amino acid metabolism and systemic thermoregulation via IL-6 secretion from skeletal muscle using a new model. These data will be reported in a subsequent report.

"Thermoregulatory system in endotherms cannot be explained by thermogenesis based on muscle contraction alone, with nonshivering thermogenesis being required as a component of the ability to tolerate cold temperatures in the long term."

This statement is correct, and it clearly showcases how difficult it is to interpret results using this CI strategy. The question to the author is- which components of muscle thermogenesis are actually inhibited by CI, and what is the relative heat contribution?

We appreciate raising this important issue. This study required the measurements of skeletal muscle temperature and electromyography in mice with cast immobilization, but we were unable to perform these measurements. We have therefore described the reviewers suggest on page 18 as limitations of this study.

In our additional experiments, we found that several genes that are usually activated in skeletal muscle during cold exposure are repressed in mice with cast immobilization (Figure 1_figure supplement 1_G-1K). Skeletal muscle is an important thermogenic organ. Although the role of the sarcolipin gene in non-shivering thermogenesis is well understood, the primary regulator of thermogenesis in metabolism and shivering remains unclear. In Future, we would like to use models in which key signals for energy metabolism are inhibited, such as muscle-specific PGC-1α-deficient mice and muscle-specific AMPK-deficient mice, to clarify important factors in skeletal muscle heat thermogenesis. We expect this approach to enable us to analyze the relative thermal contributions of each component of the heat production process in skeletal muscle, which has proven difficult in immobilized muscle models.

This conclusion is overinterpreted:

"In conclusion, we have shown that cast immobilization induced thermogenesis in BAT that was dependent on the utilization of free amino acids derived from skeletal muscle, and that muscle-derived IL-6 stimulated BCAA metabolism in skeletal muscle. Our findings may provide new insights into the significance of skeletal muscle as a large reservoir of amino acids in the regulation of body temperature".

In terms of the production of the article - the data shown in the heat maps has oddly obscure log10 dimensions. The changes are minimal, approx. 1.5x increase/decrease and therefore significance would be key to reporting these data. Fig.3C heatmap is not suitable. What are the 6 lanes to each condition? Overall, this has little/no information.

Rather than cherry-picking for a few genes, the results could be made more rigorous using RNA-seq profiling of BAT and muscle tissues.

We agree that this is an important point. Indeed, our model of skeletal muscle immobilization reveals only modest changes in metabolomics and gene expression analysis. We consider this to be a weakness of the study. However, the interactive thermogenic system that we discovered between skeletal muscle and BAT may also function under other conditions, such as acute stress and cold exposure. We should investigate this further in future models involving such dramatic metabolic changes. In fact, it has been shown that the levels of several metabolites are significantly altered in BAT after acute cold exposure.[1] Therefore, we have corrected the conclusion of this section, as stated on page 18, and added it. We also performed an enrichment analysis on the metabolomics data in BAT following cast immobilization and included the results in Figure 2_figure Supplement 1A. In addition, we excluded the heatmap from Fig. 3C of the pre-revision manuscript, as advised by the reviewer. Although we excluded the results in Figure 3C, we consider Figure 3_figure supplement_1 to be sufficient for the text.  

In addition, we agree with the reviewer's remarks on our gene expression analysis. In this study, we were unable to examine RNA-seq profiling of BAT and muscle tissue. Therefore, we have described this as a limitation of the study on page 20. However, we are interested in investigating the effect of IL-6 derived from skeletal muscle on RNA-seq profiling of skeletal muscle and BAT. We will conduct future RNA-seq analyses of BAT and skeletal muscle, using models of skeletal muscle immobilization, acute cold exposure and restraint stress.

Reviewer #2 (Public Review):

Summary:

In this study, the authors identified a previously unrecognized organ interaction where limb immobilization induces thermogenesis in BAT. They showed that limb immobilization by cast fixation enhances the expression of UCP1 as well as amino acid transporters in BAT, and amino acids are supplied from skeletal muscle to BAT during this process, likely contributing to increased thermogenesis in BAT. Furthermore, the experiments with IL-6 knockout mice and IL-6 administration to these mice suggest that this cytokine is likely involved in the supply of amino acids from skeletal muscle to BAT during limb immobilization.

Strengths:

The function of BAT plays a crucial role in the regulation of an individual's energy and body weight. Therefore, identifying new interventions that can control BAT function is not only scientifically significant but also holds substantial promise for medical applications. The authors have thoroughly and comprehensively examined the changes in skeletal muscle and BAT under these conditions, convincingly demonstrating the significance of this organ interaction.

Weaknesses:

Through considerable effort, the authors have demonstrated that limb-immobilized mice exhibit changes in thermogenesis and energy metabolism dynamics at their steady state. However, The impact of immobilization on the function of skeletal muscle and BAT during cold exposure has not been thoroughly analyzed.

Reviewer #3 (Public Review):

Summary:

In this manuscript, the authors show that impairment of hind limb muscle contraction by cast immobilization suppresses skeletal muscle thermogenesis and activates thermogenesis in brown fat. They also propose that free BCAAs derived from skeletal muscle are used for BAT thermogenesis, and identify IL-6 as a potential regulator.

Strengths:

The data support the conclusions for the most part.

Weaknesses: The data provided in this manuscript are largely descriptive. It is therefore difficult to assess the potential significance of the work. Moreover, many of the described effects are modest in magnitude, questioning the overall functional relevance of this pathway. There are no experiments that directly test whether BCAAs derived from adipose tissue are used for thermogenesis, which would require more robust tracing experiments. In addition, the rigor of the work should be improved. It is also recommended to put the current work in the context of the literature.

We appreciate the reviewer's valuable feedback. As the reviewer pointed out, many of the effects described in this study are modest in magnitude. This reflects a limitation of our study, which used skeletal muscle immobilization as a model. To clarify the overall functional relevance of this pathway, we therefore plan to use alternative models in which BAT thermogenesis and systemic cachectic effect are more strongly induced. We have added this point to the 'Conclusion' section on page 18.

In addition, previous findings reported that mitochondrial BCAA catabolism in brown adipocytes promotes systemic BCAA clearance, suggesting that BCAAs may be supplied to BAT from other organs during BAT thermogenesis.[5] However, as the reviewer rightly pointed out, the current study did not directly investigate whether BCAAs derived from adipose tissue contribute to thermogenic processes. In light of this, we have revised the manuscript to include a statement in the limitations section on page 20 that addresses this point. 

Metabolomic analysis of white adipose tissue (WAT) following skeletal muscle immobilization revealed alterations in amino acid concentrations in WAT in response to cast immobilization (Author response image 1A). Notably, levels of BCAAs in WAT remained largely unchanged at 24 hours after cast immobilization, but increased significantly by day 7 (Author response image 1B). At the 24-hour time point, when BAT thermogenesis is known to be activated, WAT weights was found to be reduced (Fig. 2H). Gene expression analysis of amino acid metabolism-related genes in WAT at this time point revealed a modest upregulation of several genes (Author response image 1C). Furthermore, a slight increase in the uptake of [³H] leucine into WAT was observed following immobilization (Fig. 3C). Collectively, these findings suggest that BCAAs within WAT may be primarily metabolized locally rather than being mobilized and supplied to BAT. In addition, given the relatively low levels of BCAAs per tissue mass and the limited capacity for BCAA uptake in WAT compared to other tissues, we consider it unlikely that WAT serves as a major reservoir of BCAAs.

Author response image 1.

(A) Amino acids in epididymal white adipose tissue (eWAT) of IL-6 KO (–/–) and WT (+/+) mice without (control) or with bilateral cast immobilization for the indicated times. Results are presented as heat maps of the log10 value of the fold change relative to control WT mice and are means of four mice in each group. (B) BCAA concentrations in eWAT of IL-6 KO and WT mice without (control) or with bilateral cast immobilization for 1 or 7 days. (n = 4 per group) (C) RT and real-time PCR analysis of the expression of SLC1A5, SLC7A1, SLC38A2, SLC43A1, BCAT2 and BCKDHA genes in eWAT of mice without (control) or with bilateral cast immobilization for 24 h. (n = 6 per group). All data other than in (A) are means ± SEM. *p < 0.05, **p < 0.01, ***p < 0.001 as determined by Dunnett's test (B) or by the unpaired t test (C).

Reviewer #1 (Recommendations for the authors): 

• Gypsum is an irrelevant label. Label consistently, with a procedure acronym, like CI or Imm.

We apologize for any confusion that our notation may have caused. We corrected all labels relating to the skeletal muscle immobilization model in mice to 'Imm'.

There are many grammatical errors and typos. Search for an example on Fudure1. The sense of some sentences is enough to obscure their meaning.

We appreciate the reviewer's points. We have checked the article for grammatical and typographical errors, correcting them where necessary.

• Figures 6E and F need to be re-annotated in the legend and on figures.

Following the peer reviewer's advice, we have re-annotated the Figure legends of this result.

Reviewer #2 (Recommendations for the authors): 

(1) It is difficult to understand how the data presented in Supplemental Table 1 were obtained. This appears to be data showing that the skeletal muscle weight of the hind limbs in mice accounts for 40 to 50% of the total skeletal muscle weight. How did the authors calculate the muscle weight? Specifically, how did they measure the weight of muscles that are neither in the hind limbs nor in the forelimbs ("Other")? Was this estimated from whole-body CT or MRI data?

In the legend, it mentions "the posterior cervical region," but what exactly was measured in the posterior cervical region? The methods for this data should be clearly described.

We appreciate the reviewers' comments. We apologize for any confusion caused by inadequate explanation of this data. This data was obtained by removing skeletal muscle from the posterior cervical region and measuring the weight of the wet tissue. We have taken care to remove most of the skeletal muscle, but some will remain. However, we do not believe that these errors are significant enough to alter the interpretation of the results. This has now been added to the 'Methods' section on page 21.

(2) Through considerable effort, the authors have demonstrated that limb-immobilized mice exhibit changes in thermogenesis and energy metabolism dynamics at their steady state. However, it remains unclear why limb-immobilized mice have reduced tolerance to cold exposure. Was there any change in the abundance of energy metabolism-related genes during cold exposure between the immobilized and control mice? For example, if the gene expression of UCP1 and UCP2, which are typically upregulated in brown adipose tissue (BAT) and skeletal muscle during cold exposure, was suppressed in the immobilized mice, it might explain their reduced cold tolerance. Thus, the changes in the response of skeletal muscle and BAT to cold exposure between immobilized and control mice should also be analyzed.

We thank the reviewer for the constructive comments. We consider the main weakness of this study to be the fact that we were unable to measure the temperature and electromyography (EMG) of the skeletal muscles of the cast-immobilized mice. Following the reviewers' advice, we analyzed the expression levels of several genes related to heat production or energy metabolism (Ucp1, Ucp2, Ucp3, Sln and Ppargc1a) in BAT and skeletal muscle of cast-immobilized mice after acute cold exposure (Figure1_figure supplement 1G-1K). The results showed that the expression of several genes that are usually increased in BAT and skeletal muscle during cold exposure was repressed in cast-immobilized mice. Notably, cast immobilization did not induce the UCP2 and PGC-1α genes at room temperature, and their upregulation during cold exposure was also suppressed in cast-immobilized mice. UCP2 is known to alter its expression in relation to energy metabolism, but it is unclear whether it regulates energy metabolism.[2] Additionally, UCP2 is understood to play a non-role in thermogenesis, and the function of the UCP2 in skeletal muscle remains unclear.[3] On the other hands, PGC-1α is widely recognized as a transcriptional coactivator that regulates various metabolic processes, including thermogenesis.[4] In our study, we found that the amounts of metabolites in the TCA cycle and the expression of the PGC-1α gene were decreased rapidly in immobilized skeletal muscle. This suggests that the metabolic rate is reduced in immobilized skeletal muscle (Figure 1_figure supplement 2A and 2F). In endothermic animals, energy expenditure in skeletal muscle plays a significant role in maintaining body temperature during both activity and rest. Hence, it is assumed that the reduced metabolic rate in skeletal muscle significantly impacts the maintenance of body temperature in cold conditions. Further investigation is required into the function of these genes in skeletal muscle thermogenesis, but we expect that the additional data suggest that the loss of muscle function due to immobilization affects the maintenance of body temperature under cold temperature. These results were discussed further on page 15.

Reviewer #3 (Recommendations for the authors): 

There are also more specific concerns related to the data supporting the claims.

(1) The relevance of increasing thermogenesis in BAT after cast immobilization is unclear, as adult humans have very little BAT. Thermogenesis gene and protein expression should be measured in white adipose tissue.

We would like to thank the reviewers for highlighting this important issue. We agree with the reviewer's comments. We did not observe significant changes in UCP1 expression in the subcutaneous adipose tissue of the inguinal region following skeletal muscle immobilization. We suspect that this is because skeletal muscle immobilization in mice did not exert a strong enough effect to induce browning of white adipose tissue. The ability of immobilizing skeletal muscle to activate thermogenesis in brown or beige adipocytes in adults remains unclear. We have therefore noted this limitation in our study in line 6.

Additionally, in this study, we aimed to clarify the role of skeletal muscle as an amino acid reservoir under metabolic stress conditions that increase BAT thermogenesis. To this end, we employed models of skeletal muscle immobilization, acute cold exposure, and restraint stress. We also intend to analyze the metabolic interactions between beige adipose tissue and skeletal muscle in more detail using models that induce browning, such as exercise or cold acclimation.

(2) In Figures 1E-G, there is no significant difference in UCP1 levels relative to the control, but body temperature is lowered from day 2 to day 7. How do the authors explain this?

This is an important point. We consider the decrease in body temperature of mice following cast immobilization at room temperature to be the result of a reduction in systemic locomotor activity.

(3) The small induction of PGC1a seen at 10 hours goes away after day 3. Why is this?

This is an important point. Our investigation showed that the norepinephrine concentration in BAT and blood of cast-immobilized mice tends to increase, peaking at 24 hours of immobilization (Fig. 1H and Figure 2_figure supplement 2D), and then gradually returns to baseline. We speculate that this transient activation of the sympathetic nervous system may affect the expression of PGC1α in BAT. Additionally, although thermogenesis in BAT temporarily increases after skeletal muscle immobilization, studies from other research groups suggest that long-term skeletal muscle immobilization (two weeks) may increase non-shivering thermogenesis in skeletal muscle via high expression SLN.[6] Therefore, we hypothesize that other thermogenic mechanisms besides BAT might be involved during prolonged cast immobilization. We have added a discussion of these topics on page 16.

(4) The metabolic cage data are marked in multiple places as significant, but the effect size is extremely small. Please describe how significance was calculated (Figure 5 supplement 1B, E, F).

This is a valid point. This data was statistically analyzed using daily averages, with the results then being compiled. However, the figure was amended because it was not appropriate to use the original to demonstrate significant differences.

(5) How does IL-6 increase BCAA levels in muscle?

This is an important point. We are also investigating this issue with great interest. In future, we will use RNA-seq profiling to investigate the mechanism by which IL-6 regulates amino acid metabolism in skeletal muscle. This point was added as a

limitation of the study on page 19.

(6) What is the mechanism behind the elevated il6 levels after cast immobilization?

We appreciate the reviewer's points. Since IL-6 gene expression in skeletal muscle increases in response to acute cold exposure and acute stress, we hypothesize that IL-6 is regulated by β-adrenergic effectors. In our preliminary experiments, stimulation with norepinephrine or with clenbuterol, a β2-adrenergic receptor agonist, suggests an increase in IL-6 gene expression and the intracellular free BCAA concentration in cultured mouse muscle cells (Author response image 2A-2D). Going forward, our plans include conducting further studies using a mouse model in which the sympathetic nervous system is activated by administering LPS intracerebroventricularly, as well as using muscle-specific β2-adrenergic receptor knockout mice.  

Reference:

(1) Okamatsu-Ogura, Y., et al. UCP1-dependent and UCP1-independent metabolic changes induced by acute cold exposure in brown adipose tissue of mice. Metabolism. 2020 113:  154396 doi: 10.1016/j.metabol.2020.154396.

(2) Patrick Schrauwen and Matthijs Hesselink, UCP2 and UCP3 in muscle controlling body metabolism., J Exp Biol. 2002 Aug;205(Pt 15):2275-85. doi: 10.1242/jeb.205.15.2275.

(3) C Y Zhang, et al., Uncoupling protein-2 negatively regulates insulin secretion and is a major link between obesity, beta cell dysfunction, and type 2 diabetes., Cell. 2001 Jun 15;105(6):745-55. doi: 10.1016/s0092-8674(01)00378-6.

(4) Christophe Handschin and Bruce M Spiegelman, Peroxisome proliferator-activated receptor gamma coactivator 1 coactivators, energy homeostasis, and metabolism., Endocr Rev. 2006 Dec;27(7):728-35. doi: 10.1210/er.2006-0037.

(5) Yoneshiro, et al., BCAA catabolism in brown fat controls energy homeostasis through SLC25A44. Nature. 2019 572(7771): 614-619 doi: 10.1038/s41586-019-1503-x.

(6) Shigeto Tomiya, et al., Cast immobilization of hindlimb upregulates sarcolipin expression in atrophied skeletal muscles and increases thermogenesis in C57BL/6J mice., Am J Physiol Regul Integr Comp Physiol. 2019 Nov1;317(5):R649-R661.doi:10.1152/ajpregu.00118.2019.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

The authors had previously found that brief social isolation could increase the activity of these neurons, and that manipulation of these neurons could alter social behavior in a social rank-dependent fashion. This manuscript explored which of the outputs were responsible for this, identifying the central nucleus of the amygdala as the key output region. The authors identified some discrete behavior changes associated with these outputs, and found that during photostimulation of these outputs, neuronal activity appeared altered in 'social response' neurons.

Strengths:

Rigorous analysis of the anatomy. Careful examination of the heterogenous effects on cell activity due to stimulation, linking the physiology with the behavior via photostimulation during recording in vivo.

Weaknesses:

(1) There are some clear imbalances in the sample size across the different regions parsed. The CeA has a larger sample size, likely in part to the previous work suggesting differential effects depending on social rank/dominance. Given the potential variance, it may be hard to draw conclusions about the impact of stimulation across different social ranks for other groups.

While it may be difficult to draw conclusions about the impact of stimulation across different social ranks, we believe that the dominance-induced variance in our dataset reveals key insights into how social history may affect the function of these circuits. However, we do recognize that there are imbalances in sample size across the different circuits that we probed. To test whether we could detect a significant effect in our DRN^DAT-CeA:ChR2 group with a sample size matched to the DRN^DAT-BLP:ChR2 group (the lowest sample size of the three circuits probed), we subsampled and ran tests for statistical significance using the following MATLAB code:

Author response image 1.

We found that out of 1000 subsamples, we detected a statistically significant effect 40.5% of the time (Author response image 2A). This suggests that the optogenetic effect exists, though it is moderate and is variable across mice (as explained by the significant correlation between social rank and optogenetic effect).

To test whether these inconsistent effects may be an effect of variance induced by social rank, we wrote the following MATLAB code to maintain the distribution of social rank in our subsamples:

Author response image 2.

P-values from subsampling analysis show a moderately reproducible social preference effect in DRN^DAT-CeA:ChR2 mice, but not in DRN^DAT-BNST:ChR2 mice. (A-D) Histograms showing distribution of paired t-test p-values comparing OFF and ON social preference scores (as shown in Figure 4A-I) in subsampled groups (to match the sample size of the DRN^DAT-BLP:ChR2 group). (A) 14 DRN^DAT-CeA:ChR2 mice were randomly subsampled, a paired t-test was performed, and the resulting p-values were binned and plotted. (B) Same as (A), but ensuring that the proportion of subordinate, intermediate, and dominant mice in the subsampled groups were the same as the original distribution. (C) Same as (A), but with DRN^DAT-BNST:ChR2 mice. (D) Same as (B), but with DRN^DAT-BNST:ChR2 mice.

Author response image 3.

We found that out of 1000 subsamples, we detected a statistically significant effect 45.5% of the time when we maintained the original distribution of social rank in DRN^DAT-CeA:ChR2 mice (Author response image 2B). This suggests that reducing the sample size to N=14 reduces the statistical power and indeed can make an effect harder to reliably detect. The reviewer is correct in saying that sample imbalance may skew conclusions. However, given the rank-dependent optogenetic effect on social preference seen in DRN^DAT-CeA:ChR2 mice (N=29 mice, p=0.002, Figure 4H) that is notably absent in DRN^DAT-BLP:ChR2 mice (N=14 mice, p=0.806, Figure 4I), we hypothesize that we would not see a significant effect of photoactivating the DRN^DAT-BLP circuit on social preference, even with a larger sample size. While we acknowledge there may be evidence that there could be an effect in the DRN^DAT-BLP projection, this analysis reveals that this effect is not as robust as the effect we see in the DRN^DAT-CeA projection, which is the focus of this study. An in-depth exploration of the DRN^DAT projection to the BLP is certainly warranted in future studies.

Interestingly, the same analysis approach applied to DRN^DAT-BNST:ChR2 mice suggest a reliably negative result, with subsampling only resulting in a significant result 1.1% of the time (Author response image 2C) and 1.7% of the time if maintaining the original rank distribution (Author response image 2D).

(2) It is somewhat unclear why only the 'social object ratio' was used to assess the effects versus more direct measurements of social behavior.

We decided to use ‘social:object ratio’ as we felt that measurement more directly supported our claim of increased social preference through optogenetic manipulation; however, in our updated manuscript, we included direct measurements of social behavior in the revised manuscript (Figure 4—figure supplement 1) and have updated the legend to reflect this addition (lines 1679-1684; 1698-1708).

(3) Somewhat related, while it is statistically significant, it is unclear if the change seen in face investigation of biologically significant, on average, it looks like a few-seconds difference and that was not modulated by social rank.

While the effect size is relatively small (4.19 seconds, 2.32% of the session), we believe we should report any statistically significant findings we discover. However, due to the small effect size, we have de-emphasized our claims regarding this finding in the text (line 172).

(4) There are several papers studying these neurons that have explored behaviors examined here, as well as the physiological connectivity that are not cited that would provide important context for this work. In particular, multiple groups have found a dopamine-mediated IPSP in the BNST, in contrast to this work. There are technical differences that may drive these differences, but not addressing them is a major weakness.

In the revised text, we have cited the groups who have found different effects of dopamine-mediated effects in the ovBNST (specifically from Krawczyk et al., 2011, Maracle et al., 2018, and Yu et al., 2021) and reconciled these results with those from our study (lines 422-432).

(5) The inclusion of some markers for receptors for some of these outputs is interesting, and the authors suggest that this may be important, but this is somewhat disconnected from the rest of the work performed.

We agree that we cannot make any causal signaling mechanism claims with the current downstream receptor RNA expression data (and we are careful in avoiding making those claims in the text), but we include these data to offer a potential mechanism and hope that these descriptive data will be useful to the field for follow up studies.

Reviewer #2 (Public review):<br /> Summary:

The authors perform a series of studies to follow up on their previous work, which established a role for dorsal raphe dopamine neurons (DRN) in the regulation of social-isolation-induced rebound in mice. In the present study, Lee et. al, use a combination of modern circuit tools to investigate putatively distinct roles of DRN dopamine transporting containing (DAT) projections to the bed nucleus of the stria terminalis (BNST), central amygdala (CeA), and posterior basolateral amygdala (BLP). Notably, they reveal that optogenetic stimulation of distinct pathways confers specific behavioral states, with DRNDAT-BLP driving aversion, DRNDAT-BNST regulating non-social exploratory behavior, and DRNDAT-CeA promoting socialability. A combination of electrophysiological studies and in situ hybridization studies reveal heterogenous dopamine and neuropeptide expression and different firing properties, providing further evidence of pathway-specific neural properties. Lastly, the authors combine optogenetics and calcium imaging to resolve social encoding properties in the DRNDAT-CeA pathway, which correlates observed social behavior to socially engaged neural ensembles.

Collectively, these studies provide an interesting way of dissecting out separable features of a complex multifaceted social-emotional state that accompanies social isolation and the perception of 'loneliness.' The main conclusions of the paper provide an important and interesting set of findings that increase our understanding of these distinct DRN projections and their role in a range of social (e.g., prosocial, dominance), non-social, and emotional behaviors. However, as noted below, the examination of these circuits within a homeostatic framework is limited given that a number of the datasets did not include an isolated condition. The DRNDAT-CeA pathway was investigated with respect to social homeostatic states in the present study for some of the datasets.

Strengths: 

(1) The authors perform a comprehensive and elegant dissection of the anatomical, behavioral, molecular, and physiological properties of distinct DRN projections relevant to social, non-social, and emotional behavior, to address multifaceted and complex features of social state.<br /> (2) This work builds on prior findings of isolation-induced changes in DRN neurons and provides a working framework for broader circuit elements that can be addressed across the social homeostatic state.<br /> (3) This work characterizes a broader circuit implicated in social isolation and provides a number of downstream targets to explore, setting a nice foundation for future investigation.<br /> (4) The studies account for social rank and anxiety-like behavior in several of the datasets, which are an important consideration to the interpretation of social motivation states, especially in male mice with respect to dominance behavior.

Weaknesses:

(1) The conceptual framework of the study is based on the premise of social isolation and perceived 'loneliness' under the framework of social homeostasis, analogous to hunger. In this framework, social isolation should provoke an aversive state and compensatory social contact behavior. In the authors' prior work, they demonstrate synaptic changes in DRN neurons and social rebound following acute social isolation. Thus, the prediction would be that downstream projections also would show state-dependent changes as a function of social housing conditions (e.g., grouped vs. isolated). In the current paper, a social isolation condition was not included for the majority of the studies conducted (e.g., Figures 1-6 do not include an isolated condition, Figures 7-8 do include an isolated condition). Thus, while Figure 1-6 adds a very interesting and compelling set of data that is of high value to the social behavior field with respect to social and emotional processing and general circuit characterization, these studies do not directly investigate the impacts of dynamic social homeostatic state. The main claim of the paper, including the title (e.g., separable DRN projections mediate facets of loneliness-like state), abstract, intro, and discussion presents the claim of this work under the framework of dynamic social homeostatic states, which should be interpreted with caution, as the majority of the work in the paper did not include a social isolation comparison.

In previous studies, loneliness-like phenotypes have been characterized across species as having the key dimensions of an aversive state that increases prosociality[1–5].  These two features are amplified by photostimulation of DRN DA neurons, and as we show in this manuscript, are separable across different projections to each target, and our ability to distinctly mimic different aspects of the constellation of features we characterize as “loneliness.”

However we agree with the reviewer that we do not intend to imply that the mouse currently feels lonely.  Indeed, isolating the animals would occlude our ability to see photostimulation-induced mimicry of specific features of the loneliness-like phenotype, and this is precisely why we did not isolate animals for our ChR2 gain-of-function experiments.  To address the reviewers’ concern, we will change the title of our manuscript from making a claim of “mediating” (which we agree would rely more heavily on mediating actual (ethologically-induced) loneliness rather than “mimicry” (photostimulation-induced) behaviors associated with a loneliness-like phenotype. We have changed language regarding this claim throughout our manuscript (Lines 1, 83, 285, 369).

For the ChR2 experiments in particular, we intended the optogenetic manipulation to be a gain-of-function one to test the hypothesis that activation of these circuits is sufficient to recapitulate different facets of a loneliness-like state (i.e. prosociality, aversion, and increased exploratory behavior). As such, that is why we only included group-housed conditions for these experiments—to mimic the phenotype of social isolation without social isolation. To test the necessity of these circuits in mediating different facets of a loneliness-like state, we agree that silencing the studied projections in an isolated state is critical, which is what we show in Figure 8. We agree that the addition of an isolated condition to understand the circuit-specific impact of dynamic social homeostatic state is important (particularly through in vivo recordings of these specific circuits during relevant behaviors), and would be a great follow-up to this study.

(2) In Figure 1, the authors confirm co-laterals in the BNST and CeA via anatomical tracing studies. The goal of the optogenetic studies is to dissociate the functional/behavioral roles of distinct projections. However, one limitation of optogenetic projection targeting is the possibility of back-propagating action potentials (stimulation of terminals in one region may back-propagate to activate cell bodies, and then afferent projections to other regions), and/or stimulation of fibers of passage. Therefore, one limitation in the dataset for the optogenetic stimulation studies is the possibility of non-specific unintended activation of projections other than those intended (e.g., DRNDAT-CeA). This can be dealt with by administering lidocaine to prevent back-propagating action potentials.

While back-propagating action potentials are potentially confounding for the manipulation techniques presented in this paper, we do show circuit-specific optogenetic behavioral effects despite significant collateralization (specifically between DRN^DAT neurons projecting to the CeA and BNST; Figure 1H), suggesting circuit-specificity. Namely, we see that stimulation of DRN^DAT terminals in CeA promotes social preference (Figure 4E,K) whereas stimulation of DRN^DAT terminals in BNST promotes rearing (exploratory) behavior (Figure 3G). There is a non-negligible chance that we are stimulating DRN^DAT fibers of passage, which we have addressed in a caveat disclaimer included in the revised discussion (lines 345-347).

(3) It is unclear from the test, but in the subjects' section of the methods, it appears that only male animals were included in the study, with no mention of female subjects. It should be clear to the reader that this was conducted in males only if that is the case, with consideration or discussion, about female subjects and sex as a biological variable.

In the revised manuscript, we have included discussion about sex as a biological variable (lines 342-345).

(4) Averaged data are generally reported throughout the study in the form of bar graphs, across most figures. Individual data points would increase the transparency of the data.

In an effort to increase the transparency of the data, we have prepared source data for each data panel in the final version of the manuscript and will upload it to eLife.  

REFERENCES

(1) Cacioppo, J.T., Hughes, M.E., Waite, L.J., Hawkley, L.C., and Thisted, R.A. (2006). Loneliness as a specific risk factor for depressive symptoms: cross-sectional and longitudinal analyses. Psychol Aging 21, 140–151. https://doi.org/10.1037/0882-7974.21.1.140.

(2) Cacioppo, S., Capitanio, J.P., and Cacioppo, J.T. (2014). Toward a Neurology of Loneliness. Psychol Bull 140, 1464–1504. https://doi.org/10.1037/a0037618.

(3) Baumeister, R.F., and Leary, M.R. (1995). The need to belong: Desire for interpersonal attachments as a fundamental human motivation. Psychological Bulletin 117, 497–529. https://doi.org/10.1037/0033-2909.117.3.497.

(4) Niesink, R.J., and Van Ree, J.M. (1982). Short-term isolation increases social interactions of male rats: A parametric analysis. Physiology & Behavior 29, 819–825. https://doi.org/10.1016/0031-9384(82)90331-6.

(5) Panksepp, J., and Beatty, W.W. (1980). Social deprivation and play in rats. Behavioral & Neural Biology 30, 197–206. https://doi.org/10.1016/S0163-1047(80)91077-8.

Reviewer #3 (Public review):

Summary:

The authors investigated the role of dopaminergic neurons (dopamine transporter expressing, DAT) in the dorsal raphe nucleus (DRN) in regulating social and affective behavior through projections to the central nucleus of the amygdala (CeA), bed nucleus of the stria terminalis (BNST), and the posterior subdivision of the basolateral amygdala. The largest effect observed was in the DRN-DAT projections to the CeA. Augmenting previously published results from this group (Matthews et al., 2016), the comprehensive behavioral analysis relative to social dominance, gene expression analysis, electrophysiological profiling, and in vivo imaging provides novel insights into how DRN-DAT projections to the CeA influence the engagement of social behavior in the contexts of group-housed and socially isolated mice.

Strengths:

Correlational analysis with social dominance is a nice addition to the study. The overall computational analyses performed are well-designed and rigorous.

Weaknesses: 

(1) Analysis of dopamine receptor expression did not include Drd3, Drd4, or Drd5 which may provide more insights into how dopamine modulates downstream targets. This is particularly relevant to the BNST projection in which the densest innervation did not robustly co-localize with the expression of either Drd1 or Drd2. It is also possible that dopamine release from DRN-DAT neurons in any or all of these structures modulates neurotransmitter release from inputs to these regions that contain D2 receptors on their terminals.

Although we find that there is more Vipr2 and Npbwr1 expression compared to Drd1 and Drd2 expression in ovBNST, we still do find that a substantial proportion of cells in ovBNST express dopamine receptors (particularly D2 dopamine receptors, as shown in Figure 5C). In our revised manuscript, we have discussed potential functional mechanism through D3, D4, and D5 dopamine receptors, as well as pre-synaptic dopamine receptor expression (lines 459-461).

(2) Although not the focus of this study, without pharmacological blockade of dopamine receptors, it is not possible to assess what the contribution of dopamine is to the behavioral outcomes. Given the co-release of glutamate and GABA from these neurons, it is possible that dopamine plays only a marginal role in the functional connectivity of DRN-DAT neurons.

While we agree with the reviewer’s comments, we are careful to avoid making claims about dopamine-mediated physiological and behavioral effects of DRN^DAT neurons (despite that these neurons are genetically identified through the expression of dopamine transporter [DAT]), mentioned in lines 222-228 in the text.

(3) Photostimulation parameters used during the behavioral studies (8 pulses of light delivered at 30 Hz for several minutes) could lead to confounding results limiting data interpretation. As shown in Figure 6J, 8 pulses of light delivered at 30 Hz result in a significant attenuation of the EPSC amplitude in the BLP and CeA projection. Thus, prolonged stimulation could lead to significant synaptic rundown resulting in an overall suppression of connectivity in the later stages of the behavioral analyses.

Despite attenuation of EPSC amplitude in BLP and CeA projections and potential synaptic rundown, we still observe significant behavioral effects through optogenetic manipulation of these circuits (increasing the likelihood of capturing a ‘true positive’ rather than a ‘false negative’ effect). In general, we attempt to reduce the duty cycle by sparingly delivering trains of optogenetic stimulation (eight 5-ms pulses every 5 seconds). Additionally, in the real time place preference task where stimulation of the DRN^DAT-BLP projection significantly reduces the time spent in the “ON” chamber, stimulation is only delivered when the mouse is in the “ON” compartment of the apparatus. However, we do feel that the reviewer’s concern that EPSC attenuation and potential synaptic rundown may potentially explain the robust place avoidance effects in DRN^DAT-BLP:ChR2 mice in the first half of the session (Figure 2G). Importantly, we show in our previous published work (Matthews et al., 2016, Cell; Figure 3) through fast-scan cyclic voltammetry (FSCV) that dopamine transients were consistently recorded in response to eight pulses of 30 Hz DRN^TH stimulation delivered every 5 seconds in the BNST, though less consistently in the CeA.

Author response:

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

eLife Assessment

This useful manuscript shows a set of interesting data including the first cryo-EM structures of human PIEZO1 as well as structures of disease-related mutants in complex with the regulatory subunit MDFIC, which generate different inactivation phenotypes. The molecular basis of PIEZO channel inactivation is of great interest due to its association with several pathologies. This manuscript provides some structural insights that may help to ultimately build a molecular picture of PIEZO channel inactivation. While the structures are of use and clear conformational differences can be seen in the presence of the auxiliary subunit MDFIC, the strength of the evidence supporting the conclusions of the paper, especially the proposed role for pore lipids in inactivation, is incomplete and there is a lack of data to support them.

We thank the editors and reviewers for taking the time and effort to review our manuscript.  The evidence supporting the key role of pore lipids in hPIEZO1 activation is as follows. i. Compared with wild-type hPIEZO1, the hydrophobic acyl chain tails of the pore lipids retracted from the hydrophobic pore region in slower inactivating mutant hPIEZO1-A1988V (Fig. 7a-b). ii. Previous electrophysiological functional studies revealed that substituting this hydrophobic pore formed by I2447, V2450, and F2454 with a hydrophilic pore prolongs the inactivation time for both PIEZO1 and PIEZO2 channels (PMID: 30628892). iii. In the structure of the HX channelopathy mutant R2456H, the interaction between the hydrophilic phosphate group head of pore lipids and R2456 is disrupted, remodeling the blade and pore module and resulting in a significantly slow-inactivating rate. iv. The interaction between pore lipids and lipidated-MDFIC stabilizes the pore lipids to reseal the pore upon activation of the hPIEZO1-MDFIC complex.

According to previously proposed models for the role of pore lipids in mechanosensitive ion channels, such as MscS (PMID: 33568813), MS K2P (PMID: 25500157) and OSCA channels (PMID: 37402734), the pore lipids seal the channel pores in closed state and could be removed in open state by mechanical force induced membrane deformation, which obeys the force-from-lipids principle. Therefore, in our putative model, the pore lipids seal the hydrophobic pore of hPIEZO1 in the closed state. Upon activation of hPIEZO1, the pore lipids retract from the hydrophobic pore and interact with multi-lipidated MDFIC, stabilizing in the inactivation state. The mild channelopathy mutants make the pore lipids retract from the hydrophobic pore and harder to close upon activation. For the severe channelopathy mutant, the interaction between the pore lipids and R2456 is disrupted, resulting in the missing of pore lipids and significantly slow-inactivating. We fully understand the concern of the role of pore lipids in our proposed model. Therefore, we have toned down our putative model.

Public Reviews:  

Reviewer #1 (Public review):  

Summary:  

This manuscript by Shan, Guo, Zhang, Chen et al., shows a raft of interesting data including the first cryo-EM structures of human PIEZO1. Clearly, the molecular basis of PIEZO channel inactivation is of great interest and as such this manuscript provides some valuable extra information that may help to ultimately build a molecular picture of PIEZO channel inactivation. However, the current manuscript though does not provide any compelling evidence for a detailed mechanism of PIEZO inactivation.

Strengths:

This manuscript documents the first cryo-EM structures of human PIEZO1 and the gain of function mutants associated with hereditary anaemia. It is also the first evidence showing that PIEZO1 gain of function mutants are also regulated by the auxiliary subunit MDFIC.

We thank reviewer #1 for the encouragement.

Weaknesses:

While the structures are interesting and clear differences can be seen in the presence of the auxiliary subunit MDFIC the major conclusions and central tenets of the paper, especially a role for pore lipids in inactivation, lack data to support them. The post-translational modification of PIEZOser# auxiliary subunit MDFIC is not modelled as a covalent interaction.

We fully understand the concern of the role of pore lipids in our proposed model. Therefore, we have toned down our putative model.

The lipids densities of the post-transcriptional modification of PIEZO1 auxiliary subunit MDFIC are shown below. As the lipids densities are not confident, we only use the single-chain lipids to represent them. And the lipidated MDFIC is proven by the MDFIC identification paper.

Author response image 1.

Reviewer #2 (Public review):

Summary:

Mechanically activated ion channels PIEZOs have been widely studied for their role in mechanosensory processes like touch sensation and red blood cell volume regulation. PIEZO in vivo roles are further exemplified by the presence of gain-of-function (GOF) or loss-of-function (LOF) mutations in humans that lead to disease pathologies. Hereditary xerocytosis (HX) is one such disease caused due to GOF mutation in Human PIEZO1, which are characterized by their slow inactivation kinetics, the ability of a channel to close in the presence of stimulus. But how these mutations alter PIEZO1 inactivation or even the underlying mechanisms of channel inactivation remains unknown. Recently, MDFIC (myoblast determination family inhibitor proteins) was shown to directly interact with mouse PIEZO1 as an auxiliary subunit to prolong inactivation and alter gating kinetics. Furthermore, while lipids are known to play a role in the inactivation and gating of other mechanosensitive channels, whether this mechanism is conserved in PIEZO1 is unknown. Thus, the structural basis for PIEZO1 inactivation mechanism, and whether lipids play a role in these mechanisms represent important outstanding questions in the field and have strong implications for human health and disease.

To get at these questions, Shan et al. use cryogenic electron microscopy (Cryo-EM) to investigate the molecular basis underlying differences in inactivation and gating kinetics of PIEZO1 and human disease-causing PIEZO1 mutations. Notably, the authors provide the first structure of human PIEZO1 (hPIEZO1), which will facilitate future studies in the field. They reveal that hPIEZO1 has a more flattened shape than mouse PIEZO1 (mPIEZO1) and has lipids that insert into the hydrophobic pore region. To understand how PIEZO1 GOF mutations might affect this structure and the underlying mechanistic changes, they solve structures of hPIEZO1 as well as two HXcausing mild GOF mutations (A1988V and E756del) and a severe GOF mutation (R2456H). Unable to glean too much information due to poor resolution of the mutant channels, the authors also attempt to resolve MCFIC-bound structures of the mutants. These structures show that MDFIC inserts into the pore region of hPIEZO1, similar to its interaction with mPIEZO1, and results in a more curved and contracted state than hPIEZO1 on its own. The authors use these structures to hypothesize that differences in curvature and pore lipid position underlie the differences in inactivation kinetics between wild-type hPIEZO1, hPIEZO1 GOF mutations, and hPIEZO1 in complex with MDFIC.

Strengths:

This is the first human PIEZO1 structure. Thus, these studies become the stepping stone for future investigations to better understand how disease-causing mutations affect channel gating kinetics.

We thank reviewer #2 for the positive comments.

Weaknesses:

Many of the hypotheses made in this manuscript are not substantiated with data and are extrapolated from mid-resolution structures.

We fully understand the concern of the role of pore lipids in our proposed model. Therefore, we have toned down our putative model.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors used structural biology approaches to determine the molecular mechanism underlying the inactivation of the PIEZO1 ion channel. To this end, the authors presented structures of human PIEZO1 and its slow-inactivating mutants. The authors also determined the structures of these PIEZO1 constructs in complexes with the auxiliary subunit MDFIC, which substantially slows down PIEZO1 inactivation. From these structures, the authors suggested an anti-correlation between the inactivation kinetics and the resting curvature of PIEZO1 in detergent. The authors also observed a unique feature of human PIEZO1 in which the lipid molecules plugged the channel pore. The authors proposed that these lipid molecules could stabilize human PIEZO1 in a prolonged inactivated state.

We thank reviewer #3 for the summary.

Strengths:

Notedly, this manuscript reported the first structures of a human PIEZO1 channel, its channelopathy mutants, and their complexes with MDFIC. The evidence that lipid molecules could occupy the channel pore of human PIEZO1 is solid. The authors' proposals to correlate PIEZO1 resting curvature and pore-resident lipid molecules with the inactivation kinetics are novel and interesting.

Thanks for the positive comments.

Weaknesses:

However, in my opinion, additional evidence is needed to support the authors' proposals.

(1) The authors determined the apo structure of human PIEZO1, which showed a more flattened architecture than that of the mouse PIEZO1. Functionally, the inactivation kinetics of human PIEZO1 is faster than its mouse counterpart. From this observation (and some subsequent observations such as the complex with MDFIC), the authors proposed the anti-correlation between curvature and inactivation kinetics. However, the comparison between human and mouse PIEZO1 structure might not be justified. For example, the human and mouse structures were determined in different detergent environments, and the choice of detergent could influence the resting curvature of the PIEZO structures.

We apologize for the misleading statement about the anti-correlation between curvature and inactivation kinetics of PIEZOs. We cannot conclude that the observation of curvature variation of mPIEZO1 and hPIEZO1 is related to their inactivation kinetics based on structural studies and electrophysiological assay. The difference in structural basis between mPIEZO1 and hPIEZO1 is what we want to state. To avoid this misleading, we have revised the manuscript. 

For the concern about detergent, we cannot fully exclude its influence on the curvature of PIEZOs. However, previously reported structures of mPiezo1 (PDB: 7WLT, 5Z10, 6B3R) were in the different detergent environments or in lipid bilayer, but the curvature of mPiezo1 is similar as shown below. Considering the high sequence similarity between mPiezo1 and hPiezo1, we hypothesize that the curvature of both hPiezo1 and mPiezo1 may be unaffected by the detergent.

Author response image 2.

Overall structural comparison of curved mPIEZO1 in the lipid bilayer (PDB: 7WLT), mPiezo1 in CHAPS (PDB: 6B3R) and mPiezo1 in Digitonin (PDB: 5Z10).

(2) Related to point 1), the 3.7 Å structure of the A1988V mutant presented by the authors showed a similar curvature as the WT but has a slower inactivating kinetics.

Based on the structural comparison between hPIEZO1 and its A1998V mutant, the retraction of pore lipids from the hydrophobic center pore in hPIEZO1-A1998V is mainly responsible for its slower inactivating kinetics.

(3) Related to point 1), the authors stated that human PIEZO1 might not share the same mechanism as mouse PIEZO1 due to its unique properties. For example, MDFIC only modifies the curvature of human PIEZO1, and lipid molecules were only observed in the pore of the human PIEZO1. Therefore, it may not be justified to draw any conclusions by comparing the structures of PIEZO1 from humans and mice.

Thanks for the constructive suggestion. To avoid this misleading, we have revised the manuscript.

(4) Related to point 1), it is well established that PIEZO1 opening is associated with a flattened structure. If the authors' proposal were true, in which a more flattened structure led to faster inactivation, we would have the following prediction: more opening is associated with faster inactivation. In this case, we would expect a pressure-dependent increase in the inactivation kinetics.

Could the authors provide such evidence, or provide other evidence along this direction?

We appreciate the reviewer’s comment. We are not claiming a relationship between the flattened structure and activation/inactivation. We only present the results of the structure of wild-type/mutant PIEZO1.

(5) In Figure S2, the authors showed representative experiments of the inactivation kinetics of PIEZO1 using whole-cell poking. However, poking experiments have high cell-to-cell variability.

The authors should also show statics of experiments obtained from multiple cells.

We have shown the statics of representative electrophysiology experiments obtained from multiple cells in Figure S2.

(6) In Figure 2 and Figure 5, when the authors show the pore diameter, it could be helpful to also show the side chain densities of the pore lining residues.

We appreciate the reviewer’s suggestion. The side chain of the pore lining restricted residues have been shown in Figure 2 and Figure 5 and the densities of pore domain have been shown in Figure S4 and S14. Interestingly, the pore lining restricted residues in mPIEZO1 and hPIEZO1 is highly conserved.

(7) The authors observed pore-plugging lipids in slow inactivating conditions such as channelopathy mutations or in complex with MDFIC. The authors propose that these lipid molecules stabilize a "deep resting state" of PIEZO1, making it harder to open and harder to inactivate once opened. This will lead to the prediction that the slow-inactivating conditions will lead to a higher activation threshold, such as the mid-point pressure in the activation curve. Is this true?

Yes, it is true. In Figure S2, the MDFIC-induced slow-inactivation conditions in hPIEZO1-MDFIC, hPIEZO1-A1988V-MDFIC, hPIEZO1-E756del-MDFIC and hPIEZO1-R2456H-MDFIC result in larger half-activation thresholds than hPIEZO1, hPIEZO1-A1988V, hPIEZO1-E756del and hPIEZO1-R2456H, respectively.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I document the major issues below:

(1) Mouse vs Human inactivation

Line 21- "than the slower inactivating curved mouse PIEZO1 (mPIEZO1)."

Where is the data in this paper or any other paper that human PIEZO1 inactivates faster than mouse PIEZO1? This is central to the way the authors present the paper. In fact, the tau quoted for the hPIEZO1 of ~10 ms is similar to that often measured for mPIEZO1. The reference in the discussion for mouse vs human inactivation times is a review of mechanotransduction. Either the authors need to directly compare the tau of mP1 vs hP1 or quote the relevant primary literature if it exists.

As measured in HEK-PIKO cells transfected with mPiezo1, the inactivation time of mPiezo1 is 13 ± 1 ms (PMID: 29261642) at -80 mV. 

The tau is also voltage-dependent. The tau is beyond 20 ms at -60 mV for mPIEZO1 (PMID:

20813920) and for hPIEZO1 is still around 10 ms.

(2) MDFIC-lipidation

Without seeing the PDB or EMDB I can't guarantee this but from Figure 6d it seems like the Sacylation in the distal C-terminus of MDFIC is not modelled as a covalent interaction, these lipids are covalently added to the Cys residues in S-acylation via zDHHC enzymes. This should be modelled correctly.

Thanks for this suggestion. As the lipid densities of the post-transcriptional modification of PIEZOs auxiliary subunit MDFIC are not confident, we only use the single-chain lipids to represent them.

And the lipidated MDFIC is proven by the MDFIC identification paper (PMID: 37590348).

(3) Pore lipids and inactivation

The lipids close to the pore are interesting and the density for a lipid is also seen in the mouse MDFIC-PIEZO1 complex from Zhou, Ma et al, 2023. However, there is no data provided by the authors that the lipid is functionally relevant to anything. There is not even a correlation with inactivation in Figure 7. P1+MDFIC inactivates slowest yet the lipids are present within the pore. Second, there is no evidence for what these structures are: closed, or inactivated? In fact, the Xiao lab is now interpreting the 7WLU structure as inactivated.

The evidence supporting the key role of pore lipids in hPIEZO1 activation is as follows. i. Compared with wild-type hPIEZO1, the hydrophobic acyl chain tails of the pore lipids retracted from the hydrophobic pore region in slower inactivating mutant hPIEZO1-A1988V (Fig. 7a-b). ii. Previous electrophysiological functional studies revealed that substituting this hydrophobic pore formed by I2447, V2450, and F2454 with a hydrophilic pore prolongs the inactivation time for both PIEZO1 and PIEZO2 channels (PMID: 30628892). iii. In the structure of the HX channelopathy mutant R2456H, the interaction between the hydrophilic phosphate group head of pore lipids and R2456 is disrupted, remodeling the blade and pore module and resulting in a significantly slow-inactivating rate. iv. The interaction between pore lipids and lipidated-MDFIC stabilizes the pore lipids to reseal the pore upon activation of the hPIEZO1-MDFIC complex. Overall, the pore lipid is involved in inactivation, and we have toned down the statement.

(4) Cytosolic plug

There is additional cytosolic density for the human PIEZO1 that the authors intimate could be from a different binding partner. IS it possible to refine this density? Is it from the PIEZO1-tag? At the very least a little more information about this density should be given if it is going to be mentioned like this.

Our purification result shows that the protein is tag-free. We are also curious about the extra cytosolic density, but we do not know what it is.

(5) Reduced sensitivity of PIEZO1 in the presence of MDFIC and its regulatory mechanism

This was reported in the first article however no data is presented by the authors to support MDFIC increasing the mechanical energy required to open PIEZO1. The sentence in the discussion; "MDFIC enables hPIEZO1 to respond to different forces by modifying the pore module through lipid interactions." is not supported by any functional data and seems to be an over-interpretation of the structures.

We appreciate this suggestion. The half-activation threshold of hPEIZO1 and hPEIZO1-MDFIC is measured to be 7 μm and 9 μm, respectively (Fig.S2). In addition, the mechanical currents amplitude of hPIEZO1-MDFIC is extremely small compared to that of WT reaching the nA level (Fig.S2). Therefore, the less mechanosensitive hPIEZO1-MDFIC may require more mechanical energy to open than PIEZO1 WT.

6) Both referencing of the PIEZO1 literature and prose could be improved.

Thanks for the suggestion. We have improved the referencing and prose.

Reviewer #2 (Recommendations for the authors):

(1) The authors speculate that the difference in curvature between human and mouse PIEZO1 results in its fast inactivation but do not provide experimental evidence to support this idea. This claim would have been bolstered by showing that the GOF human mutations have a more curved structure, but these proved too structurally unstable to be solved at high resolution. However, the authors state that the 3.7 angstrom map solved for hPIEZO1-A1988V does have an overall similar architecture as wild-type hPIEZO1; thus, contradicting their hypothesis.

We apologize for the misleading statement. In our revised manuscript, we do not claim a relationship between the flattened structure and activation/inactivation. We only present the results of the structure of wild-type/mutant PIEZO1.

The structure comparison between the A1988V mutant and WT shows a similar architecture but a different occupancy pattern of pore lipids. Therefore, we suggested that the A1988V mutant has slightly slower inactivation kinetics, mainly due to the exit of pore lipids from the pore.

(2) The authors show that interaction with MDFIC alters hPIEZO1 structure to be more curved and use this to support their idea that changing the curvature of the protein underlies the prolonged inactivation kinetics. It has been previously shown that MDFIC does not change the structure of mPIEZO1 but does alter its inactivation and gating kinetics. How does this discrepancy fit into the inactivation model proposed by the authors? Similarly, their claim that MDFIC slows hPIEZO1 inactivation and weakens mechanosensitivity just by affecting the pore module and changing blade curvature is made based on observation and no experimental data to test it.

We have revised the manuscript to avoid misleading the relationship between the curvature and the inaction kinetics of hPIEZO1. The evidence reported previously that substitution of the hydrophobic pore, formed by I2447, V2450, and F2454, with a hydrophilic pore prolongs the inactivation time for both PIEZO1 and PIEZO2 channels (PMID: 30628892). In addition, the severe HX channelopathy mutant R2456H, wherein the interaction between the hydrophilic phosphate group head and R2456 is disrupted, leads to remodeling of the blade and pore module. Indeed, our observation is limited and further experiments will be performed to support our model.

(3) How does their model fit in cell types that have PIEZO1 (or GOF mutant PIEZO1) but not MDFIC?

In cell types that have PIEZO1 or GOF mutant PIEZO1 but not MDFIC, PIEZO1 or GOF mutant PIEZO1 may have a faster inactivation rate than those that bind to MDFIC. It can be proved that overexpressed PIEZOs exhibit faster inactivation kinetics than those in some native cell types with MDFIC expression (PMID: 20813920, 30132757).

(4) Figure S2 is missing quantification of the electrophysiology data. The authors should show summary data in addition to their representative traces including the Imax for all conditions, tau for data shown in b, and sample size for all conditions, and related statistics. The text claims that MDFIC decreases mechanosensitivity (line 156) but there is no data to support this.

For the electrophysiological assay in Figure S2, we referred to previously reported mPIEZO1 mutants (PMID: 23487776, 28716860). We confirmed that the slower inactivation phenotypes of these mutations of hPIEZO1 are similar to those of mPIEZO1.

The half-activation threshold of hPEIZO1 and hPEIZO1-MDFIC is measured to be 7 μm and 9 μm, respectively. This tendency of increased half-activation threshold of hPIEZO1 upon binding with MDFIC is also shown in the electrophysiological result of hPIEZO1 channelopathy mutants.

(5) In line 144, the authors mention that they were able to validate the MDFIC density with multilipidated cysteines on the C-terminal amphipathic helix, but they do not show the density with fitted lipids. While individual densities for some of the lipids are shown in extended Figure 12, it would be helpful to include a figure where they show the map for MDFIC with fitted lipids in it.

Thanks for the valuable suggestion. As the lipid densities of the post-transcriptional modification of PIEZOs auxiliary subunit MDFIC are not confident, we only use the single-chain lipids to represent them. And the lipidated MDFIC is proven by the MDFIC identification paper.

(6) The authors show that R2456 interacts with a lipid at the pore module and hypothesize that this underlies the fast inactivation of hPIEZO1. While they did not obtain a high-resolution structure of this mutant, this hypothesis could be tested by substituting R for side chains with different charges and performing electrophysiology to determine the effects on inactivation.

Thanks for the constructive suggestion. We will perform the electrophysiology assay for R2456 mutants with different side chains.

7) Figure 4 shows overall structure of hPIEZO1 GOF mutations A1988V and E756del in complex with MDFIC. Other than showing an overall similar structure to wildtype hPIEZO1, the authors do not show how the human mutations A1988V alter the structure of the protein at the site of change. Understanding how these mutations affect the local architecture of the protein has important relevance for human physiology.

As the GOF channelopathy mutant hPIEZO1-A1988V is structurally unstable, the density at the site of A1988V is too weak to figure out the related interaction in the structure of the hPIEZO1-A1988V mutant. 

Minor comment:

In general, the manuscript will benefit from heavy copy editing. For example, the word cartoon is misspelled in many of the figure legends.

We apologize for the mistake. The manuscript has been checked and revised.

Reviewer #3 (Recommendations for the authors):

Some portions of this manuscript were not well written. For example, at the end of the 3rd paragraph in the introduction, the authors talked about HX mutations and their correlation with malaria infection and plasma iron. This is irrelevant information and will only distract the readers. It would be ideal if the authors could go through the entire manuscript and improve its clarity.

Thanks for the suggestion. We have revised the sentences about HX mutations as suggested and improved the entire manuscript.

Author response:

We were delighted by the reviewers' general comments. We thank the reviewers for their thoughtful reviews, constructive criticism, and analysis suggestions. We have carefully addressed each of their points during the revision of the manuscript.

Unfortunately, after the paper was submitted to eLife, the first author, who ran all the analyses, left academia. We now realized that we currently do not have sufficient resources to perform all additional analyses as requested by the reviewers.

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

Public Reviews:

Reviewer #1 (Public Review):

This study uses MEG to test for a neural signature of the trial history effect known as 'serial dependence.' This is a behavioral phenomenon whereby stimuli are judged to be more similar than they really are, in feature space, to stimuli that were relevant in the recent past (i.e., the preceding trials). This attractive bias is prevalent across stimulus classes and modalities, but a neural source has been elusive. This topic has generated great interest in recent years, and I believe this study makes a unique contribution to the field. The paper is overall clear and compelling, and makes effective use of data visualizations to illustrate the findings. Below, I list several points where I believe further detail would be important to interpreting the results. I also make suggestions for additional analyses that I believe would enrich understanding but are inessential to the main conclusions.

(1) In the introduction, I think the study motivation could be strengthened, to clarify the importance of identifying a neural signature here. It is clear that previous studies have focused mainly on behavior, and that the handful of neuroscience investigations have found only indirect signatures. But what would the type of signature being sought here tell us? How would it advance understanding of the underlying processes, the function of serial dependence, or the theoretical debates around the phenomenon?

Thank you for pointing this out. Our MEG study was designed to address two questions: 1) we asked whether we could observe a direct neural signature of serial dependence, and 2) if so, whether this signature occurs at the encoding or post-encoding stage of stimulus processing in working memory. This second question directly concerns the current theoretical debate on serial dependence.

Previous studies have found only indirect signatures of serial dependence such as reactivations of information from the previous trial or signatures of a repulsive bias, which were in contrast to the attractive bias in behavior. Thus, it remained unclear whether an attractive neural bias can be observed as a direct reflection of the behavioral bias. Moreover, previous studies observed the neuronal repulsion during early visual processes, leading to the proposal that neural signals become attracted only during later, post-encoding processes. However, these later processing stages were not directly accessible in previous studies. To address these two questions, we combined MEG recordings with an experimental paradigm with two items and a retro-cue. This design allowed to record neural signals during separable encoding and post-encoding task phases and so to pinpoint the task phase at which a direct neural signature of serial dependence occurred that mirrored the behavioral effect.

We have slightly modified the Introduction to strengthen the study motivation.

(1a) As one specific point of clarification, on p. 5, lines 91-92, a previous study (St. JohnSaaltink et al.) is described as part of the current study motivation, stating that "as the current and previous orientations were either identical or orthogonal to each other, it remained unclear whether this neural bias reflected an attraction or repulsion in relation to the past." I think this statement could be more explicit as to why/how these previous findings are ambiguous. The St. John-Saaltink study stands as one of very few that may be considered to show evidence of an early attractive effect in neural activity, so it would help to clarify what sort of advance the current study represents beyond that.

Thank you for this comment. In the study by St. John-Saaltink et al. (2016), two gratings oriented at 45° and 135° were always presented to either the left or right side of a central fixation point in a trial (90° orientation difference). As only the left/right position of the 45° and 135° gratings varied across trials, the target stimulus in the current trial was either the same or differed by exactly 90° from the previous trial. In consequence, this study could not distinguish whether the observed bias was attractive or repulsive, which concerned both the behavioral effect and the V1 signal. Furthermore, the bias in the V1 signal was partially explained by the orientation that was presented at the same position in the previous trial, which could reflect a reactivation of the previous orientation rather than an actual altered orientation.

We have changed the Introduction accordingly.

References:

St. John-Saaltink E, Kok P, Lau HC, de Lange FP (2016) Serial Dependence in Perceptual Decisions Is Reflected in Ac6vity Pa9erns in Primary Visual Cortex. Journal of Neuroscience 36: 6186–6192.

(1b) The study motivation might also consider the findings of Ranieri et al (2022, J. Neurosci) Fornaciai, Togoli, & Bueti (2023, J. Neurosci), and Lou& Collins (2023, J. Neurosci) who all test various neural signatures of serial dependence.

Thank you. As all listed findings showed neural signatures revealing a reactivation of the previous stimulus or a response during the current trial, we have added them to the paragraph in the Introduction referring to this class of evidence for the neural basis for serial dependence.

(2) Regarding the methods and results, it would help if the initial description of the reconstruction approach, in the main text, gave more context about what data is going into reconstruction (e.g., which sensors), a more conceptual overview of what the 'reconstruction' entails, and what the fidelity metric indexes. To me, all of that is important to interpreting the figures and results. For instance, when I first read, it was unclear to me what it meant to "reconstruct the direction of S1 during the S2 epoch" (p. 10, line 199)? As in, I couldn't tell how the data/model knows which item it is reconstructing, as opposed to just reporting whatever directional information is present in the signal.

(2a) Relatedly, what does "reconstruction strength" reflect in Figure 2a? Is this different than the fidelity metric? Does fidelity reflect the strength of the particular relevant direction, or does it just mean that there is a high level of any direction information in the signal? In the main text explain what reconstruction strength and what fidelity is?

Thank you for pointing this out. We applied the inverted encoding model method to MEG data from all active sensors (271) within defined time-windows of 100 ms length. MEG data was recorded in two sessions on different days. Specifically, we constructed an encoding model with 18 motion direction-selective channels. Each channel was designed to show peak sensitivity to a specific motion direction, with gradually decreasing sensitivity to less similar directions. In a training step, the encoding model was fiCed to the MEG data of one session to obtain a weight matrix that indicates how well the sensor activity can be explained by the modeled direction. In the testing step, the weight matrix was inverted and applied to the MEG data of the other session, resulting in a response profile of ‘reconstruction strengths’, i.e., how strongly each motion direction was present in a trial. When a specific motion direction was present in the MEG signal, the reconstruction strengths peaked at that specific direction and decreased with increasing direction difference. If no information was present, reconstruction strengths were comparable across all modeled directions, i.e., the response profile was flat. To integrate response profiles across trials, single trial profiles were aligned to a common center direction (i.e., 180°) and then averaged.

To quantify the accuracy of each IEM reconstruction, i.e., how well the response profile represents a specific motion direction relative to all other directions we computed the ‘reconstruction fidelity’. Fidelity was obtained by projecting the polar vector of the reconstruction at every direction angle (in steps of 1°) onto the common center (180°) and averaging across all direction angles (Rademaker et al 2019, Sprague, Ester & Serences, 2016). As such, ‘reconstruction fidelity’ is a summary metric with fidelity greater than zero indicating an accurate reconstruction.

How does the model know which direction to reconstruct? Our modelling procedure was informed about the stimulus in question during both the training and the testing step. Specifically, we informed our model during the training step about e.g., the current S2. Then, we fit the model to training data from the S2 epoch and applied it to testing data from the S2 epoch. Crucially, during the testing step the motion direction in question, i.e., current S2, becomes relevant again. For example, when S2 was 120°, the reconstructions were shifted by 60° in order to align with the common center, i.e., 180°. In addition, we also tested whether we could reconstruct the motion direction of S1 during the S2 epoch. Here, we used again the MEG data from the S2 epoch but now for S1 training. i.e., the model was informed about S1 direction. Accordingly, the recentering step during testing was done with regard to the S1 direction. Similarly, we also reconstructed the motion direction of the previous target (i.e., the previous S1 or S2), e.g., during the S2 epoch.

Together, the multi-variate pattern of MEG activity across all sensors during the S2 epoch could contain information about the currently presented direction of S2, the direction of the preceding S1 and the direction of the target stimulus from the previous trial (i.e., either previous S1 or previous S2) at the same time. An important exception from this regime was the cross-reconstruction analysis (Appendix 1—figure 2). Here we trained the encoding model on the currently relevant item (S1 during the S1 epoch, S2 during the S2 epoch and the cued item during the retro-cue epoch) of one MEG session and reconstructed the previous target on the other MEG session.

Finally, to examine shifts of the neural representation, single-trial reconstructions were assigned to two groups, those with a previous target that was oriented clockwise (CW) in relation to the currently relevant item and those with a previous target that was oriented counter-clockwise (CCW). The CCW reconstructions were flipped along the direction space, hence, a negative deviation of the maximum of the reconstruction from 180° indicated an attraction toward the previous target, whereas a positive deviation indicated a repulsion. Those reconstructions were then first averaged within each possible motion direction and then across them to account for different presentation numbers of the directions, resulting in one reconstruction per participant, epoch and time point. To examine systematic shifts, we then tested if the maximum of the reconstruction was systematically different from the common center (180°). For display purposes, we subtracted the reconstructed maximum from 180° to compute the direction shifts. A positive shift thus reflected attraction and a negative shift reflected repulsion.

We have updated the Results accordingly.

References:

Rademaker RL, Chunharas C, Serences JT (2019) Coexisting representations of sensory and mnemonic information in human visual cortex. Nature Neuroscience. 22: 1336-1344.

Sprague TC, Ester EF, Serences JT (2016) Restoring Latent Visual Working Memory Representations in Human Cortex. Neuron. 91: 694-707

(3) Then in the Methods, it would help to provide further detail still about the IEM training/testing procedure. For instance, it's not entirely clear to me whether all the analyses use the same model (i.e., all trained on stimulus encoding) or whether each epoch and timepoint is trained on the corresponding epoch and timepoint from the other session. This speaks to whether the reconstructions reflect a shared stimulus code across different conditions vs. that stimulus information about various previous and current trial items can be extracted if the model is tailored accordingly.

As reported above, our modeling procedure was informed about same stimulus during both the training and the testing step, except for the cross-reconstruction analysis.

Regarding the training and testing data, the model was always trained on data from one session and tested on data from the other session, so that each MEG session once served as the training data set and once as the test data set, hence, training and test data were independent. Importantly, training and testing was always performed in an epoch- and time point-specific way: For example, the model that was trained on the first 100-ms time bin from the S1 epoch of the first MEG session was tested on the first 100-ms time bin from the S1 epoch of the second MEG session.

Specifically, when you say "aim of the reconstruction" (p. 31, line 699), does that simply mean the reconstruction was centered in that direction (that the same data would go into reconstructing S1 or S2 in a given epoch, and what would differentiate between them is whether the reconstruction was centered to the S1 or S2 direction value)?

As reported above, during testing the reconstruction was centered at the currently relevant direction. The encoding model was trained with the direction labels of S1, S2 or the target item, corresponding to the currently relevant direction, i.e., S1 in S1 epochs, S2 in S2 epochs and target item (S1 or S2) in the retro-cue epoch. The only exception was the reconstruction of S1 during the S2 epoch. Here the encoding model was trained on the S1 direction, but with data from the S2 epoch and then applied to the S2 epoch data and recentered to the S1 direction. So here, S1 and S2 were indeed trained and tested separately for the same epoch.

(4) I think training and testing were done separately for each epoch and timepoint, but this could have important implications for interpreting the results. Namely if the models are trained and tested on different time points, and reference directions, then some will be inherently noisier than others (e.g., delay period more so than encoding), and potentially more (or differently) susceptible to bias. For instance, the S1 and S2 epochs show no attractive bias, but they may also be based on more high-fidelity training sets (i.e., encoding), and therefore less susceptible to the bias that is evident in the retrocue epoch.

Thanks for pointing this out. Training and testing were performed in an epoch- and time point-specific way. Thus, potential differences in the signal-to-noise ratio between different task phases could cause quality differences between the corresponding reconstructed MEG signals. However, we did not observe such differences. Instead, we found comparable time courses of the reconstruction fidelities and the averaged reconstruction strengths between epochs (Figure 2b and 2c, respectively). Fig. 2b, e.g., shows that reconstruction fidelity for motion direction stimuli built up slowly during the stimulus presentation, reaching its maximum only after stimulus offset. This observation may contrast to different stimulus materials with faster build-ups, like the orientation of a Gabor.

We agree with the reviewer that, regardless of the comparable but not perfectly equal reconstruction fidelities, there are good arguments to assume that the neural representation of the stimulus during its encoding is typically less noisy than during its post-encoding processing and that this difference could be one of the reasons why serial dependence emerged in our study only during the retro-cue epoch. However, the argument could also be reversed: a biased representation, which represents a small and hard-to-detect neural effect, might be easier to observe for less noisy data. So, the fact that we found a significant bias only during the potentially “noisier” retro-cue epoch makes the effect even more noteworthy.

We mentioned the limitation related to our stimulus material already at the end of the Discussion. We have now added a new paragraph to the Discussion to address the two opposing lines of reasoning.  

(4) I believe the work would benefit from a further effort to reconcile these results with previous findings (i.e., those that showed repulsion, like Sheehan & Serences), potentially through additional analyses. The discussion attributes the difference in findings to the "combination of a retro-cue paradigm with the high temporal resolution of MEG," but it's unclear how that explains why various others observed repulsion (thought to happen quite early) that is not seen at any stage here. In my view, the temporal (as well as spatial) resolution of MEG could be further exploited here to better capture the early vs. late stages of processing. For instance, by separately examining earlier vs. later time points (instead of averaging across all of them), or by identifying and analyzing data in the sensors that might capture early vs. late stages of processing. Indeed, the S1 and S2 reconstructions show subtle repulsion, which might be magnified at earlier time points but then shift (toward attraction) at later time points, thereby counteracting any effect. Likewise, the S1 reconstruction becomes biased during the S2 epoch, consistent with previous observations that the SD effects grow across a WM delay. Maybe both S1 and S2 would show an attractive bias emerging during the later (delay) portion of their corresponding epoch? As is, the data nicely show that an attractive bias can be detected in the retrocue period activity, but they could still yield further specificity about when and where that bias emerges.

We are grateful for this suggestion. Before going into detail, we would like to explain our motivation for choosing the present analysis approach that included averaging time points within an epoch of interest.

Our aim was to detect a neuronal signature of serial dependence which is manifested as an attractive shift of about 3.5° degrees within the 360° direction space. To be able to detect such a small effect in the neural data and given the limited resolution of the reconstruction method and the noisy MEG signals, we needed to maximize the signal-to-noise ratio. A common method to obtain this is by averaging data points. In our study we asked subjects to perform 1022 trials, down-sampled the MEG data from the recorded sampling rate of 1200 Hz to 10 Hz (one data point per 100 ms) that we used for the estimation of reconstruction fidelity and calculated the final neural shift estimates by averaging time points that showed a robust reconstruction fidelity, thus representing interpretable data points.

Our procedure to maximize the signal-to-noise ratio was successful as we were able to reliably reconstruct the presented and remembered motion direction in all epochs (Figure 1a and 1b in the manuscript). However, the reconstruction did not work equally well for all time points within each epoch. In particular, there were time points with a non-significant reconstruction fidelity. In consequence, for the much smaller neural shift effect we did not expect to observe reliable time-resolved results, i.e., when considering each time point separately. Instead, we used the reconstruction results to define the time window in order to calculate the neural shift, i.e., we averaged across all time points with a significant reconstruction fidelity.

Author response image 1 depicts the neural shift separately for each time point during the retro-cue epoch. Importantly, the gray parts of the time courses indicate time points where the reconstruction of the presented or cued stimulus was not significant. This means that the reconstructed maxima at those time points were very variable/unreliable and therefore the neural shifts were hardly interpretable.

Author response image 1.

Time courses of the reconstruction shift reveal a tendency for an attractive bias during the retrocue phase. Time courses of the neural shift separately for each time point during the S1 (left panel), S2 (middle panel) and retro-cue epochs (right panel). Gray lines indicate time points with non-significant reconstruction fidelities and therefore very variable and non-interpretable neural reconstruction shifts. The colored parts of the lines correspond to the time periods of significant reconstruction fidelities with interpretable reconstruction shifts. Error bars indicate the middle 95% of the resampling distribution. Time points with less than 5% (equaling p < .05) of the resampling distribution below 0° are indicated by a colored circle. N = 10.

First, the time courses in the Author response image 1 show that the neural bias varied considerably between subjects, as revealed by the resampling distributions, at given time points. In this resampling procedure, we drew 10 participants in 10.000 iterations with replacement and calculated the reconstruction shift based on the mean reconstruction of the resampled participants. The observed variability stresses the necessity to average the values across all time points that showed a significant reconstruction fidelity to increase the signal-to-noise ratio.

Second, despite this high variability/low signal-to-noise ratio, Author response image 1 (right panel) shows that our choice for this procedure was sensible as it revealed a clear tendency of an attractive shift at almost all time points between 300 through 1500 ms after retro-cue onset with only a few individual time-points showing a significant effect (uncorrected for multiple comparisons). It is worth to mention that this time course did not overlap with the time course of previous target cross-reconstruction (Appendix 1—figure 2, right panel), as there was no significant target cross-reconstruction during the retro-cue epoch with an almost flat profile around zero. Also, there was no overlap with previous target decoding in the retro-cue epoch (Figure 5 in the manuscript). Here, the previous target was reactivated significantly only at early time points of 200 and 300 ms post cue onset (i.e., at time points with a non-significant reconstruction fidelity and therefore no interpretable neural shift), while the nominally highest values of the attractive neural shift were visible at later time points that also showed a significant reconstruction fidelity (Figure 2b in the manuscript).

Third, Author response image 1 (left and middle panel) shows the time courses of the neural shift during the S1 and S2 epochs. While no neural shift could be observed for S1, during the S2 epoch the time-resolved analysis indicated an initial attractive shift followed by a (nonsignificant) tendency for a repulsive shift. After averaging neural shifts across time points with a significant reconstruction fidelity, there was no significant effect with an overall tendency for repulsion, as reported in the paper. The attractive part of the neural shift during the S2 epoch was nominally strongest at very early time points (at 100-300 ms after S2 onset) and overlapped perfectly with the reactivation of the previous target as shown by the cross-reconstruction analysis (Appendix 1—figure 2, middle panel). This overlap suggests that the neural attractive shift did not reflect an actual bias of the early S2 representation, but rather a consequence of the concurrent reactivation of the previous target in the same neural code as the current representation. Finally, this neural attractive shift during S2 presentation did not correlate with the behavioral error (single trial-wise correlation: no significant time points during S2 epoch) or the behavioral bias (subject-wise correlation). In contrast, for the retro-cue epoch, we observed a significant correlation between the neural attractive shift and behavior.

Together, the time-resolved results show a clear tendency for an attractive neural bias during the retro-cue phase, thus supporting our interpretation that the attractive shift during the retro-cue phase reflects a direct neuronal signature of serial dependence. However, these additional analyses also demonstrated a large variability between participants and across time points, warranting a cautious interpretation. We conclude that our initial approach of averaging across time points was an appropriate way of reducing the high level of noise in the data and revealed the reported significant and robust attractive neural shift in the retrocue phase.

(5) A few other potentially interesting (but inessential considerations): A benchmark property of serial dependence is its feature-specificity, in that the attractive bias occurs only between current and previous stimuli that are within a certain range of similarity to each other in feature space. I would be very curious to see if the neural reconstructions manifest this principle - for instance, if one were to plot the trialwise reconstruction deviation from 0, across the full space of current-previous trial distances, as in the behavioral data. Likewise, something that is not captured by the DoG fivng approach, but which this dataset may be in a position to inform, is the commonly observed (but little understood) repulsive effect that appears when current and previous stimuli are quite distinct from each other. As in, Figure 1b shows an attractive bias for direction differences around 30 degrees, but a repulsive one for differences around 170 degrees - is there a corresponding neural signature for this component of the behavior?

We appreciate the reviewer's idea to split the data. However, given that our results strongly relied on the inclusion of all data points, i.e., including all distances in motion direction between the current S1, S2 or target and the previous target and requiring data averaging, we are concerned that our study was vastly underpowered to be able to inform whether the attractive bias occurs only within a certain range of inter-stimulus similarity. To address this important question, future studies would require neural measurements with much higher signal-to-noise-ratio than the present MEG recordings with two sessions per participant and 1022 trials in total.

Reviewer #2 (Public Review):

Summary:

The study aims to probe the neural correlates of visual serial dependence - the phenomenon that estimates of a visual feature (here motion direction) are attracted towards the recent history of encoded and reported stimuli. The authors utilize an established retro-cue working memory task together with magnetoencephalography, which allows to probe neural representations of motion direction during encoding and retrieval (retro-cue) periods of each trial. The main finding is that neural representations of motion direction are not systematically biased during the encoding of motion stimuli, but are attracted towards the motion direction of the previous trial's target during the retrieval (retro-cue period), just prior to the behavioral response. By demonstrating a neural signature of attractive biases in working memory representations, which align with attractive behavioral biases, this study highlights the importance of post-encoding memory processes in visual serial dependence.

Strengths:

The main strength of the study is its elegant use of a retro-cue working memory task together with high temporal resolution MEG, enabling to probe neural representations related to stimulus encoding and working memory. The behavioral task elicits robust behavioral serial dependence and replicates previous behavioral findings by the same research group. The careful neural decoding analysis benefits from a large number of trials per participant, considering the slow-paced nature of the working memory paradigm. This is crucial in a paradigm with considerable trial-by-trial behavioral variability (serial dependence biases are typically small, relative to the overall variability in response errors). While the current study is broadly consistent with previous studies showing that attractive biases in neural responses are absent during stimulus encoding (previous studies reported repulsive biases), to my knowledge it is the first study showing attractive biases in current stimulus representations during working memory. The study also connects to previous literature showing reactivations of previous stimulus representations, although the link between reactivations and biases remains somewhat vague in the current manuscript. Together, the study reveals an interesting avenue for future studies investigating the neural basis of visual serial dependence.

Weaknesses:

(1) The main weakness of the current manuscript is that the authors could have done more analyses to address the concern that their neural decoding results are driven by signals related to eye movements. The authors show that participants' gaze position systematically depended on the current stimuli's motion directions, which together with previous studies on eye movement-related confounds in neural decoding justifies such a concern. The authors seek to rule out this confound by showing that the consistency of stimulus-dependent gaze position does not correlate with (a) the neural reconstruction fidelity and (b) the repulsive shift in reconstructed motion direction. However, both of these controls do not directly address the concern. If I understand correctly the metric quantifying the consistency of stimulus-dependent gaze position (Figure S3a) only considers gaze angle and not gaze amplitude. Furthermore, it does not consider gaze position as a function of continuous motion direction, but instead treats motion directions as categorical variables. Therefore, assuming an eye movement confound, it is unclear whether the gaze consistency metric should strongly correlate with neural reconstruction fidelity, or whether there are other features of eye movements (e.g., amplitude differences across participants, and tuning of gaze in the continuous space of motion directions) which would impact the relationship with neural decoding. Moreover, it is unclear whether the consistency metric, which does not consider history dependencies in eye movements, should correlate with attractive history biases in neural decoding. It would be more straightforward if the authors would attempt to (a) directly decode stimulus motion direction from x-y gaze coordinates and relate this decoding performance to neural reconstruction fidelity, and (b) investigate whether gaze coordinates themselves are history-dependent and are attracted to the average gaze position associated with the previous trials' target stimulus. If the authors could show that (b) is not the case, I would be much more convinced that their main finding is not driven by eye movement confounds.

The reviewer is correct that our eye-movement analysis approach considered gaze angle (direction) and not gaze amplitude. We considered gaze direction to be the more important feature to control for when investigating the neural basis of serial dependence that manifests, given the stimulus material used in our study, as a shift/deviation of angle/direction of a representation towards the previous target motion direction. To directly relate gaze direction and MEG data to each other we equaled the temporal resolution of the eye tracking data to match that of the MEG data. Specifically, our analysis procedure of gaze direction provided a measure indicating to which extent the variance of the gaze directions was reduced compared with random gaze direction patterns, in relation to the specific stimulus direction within each 100 ms time bin. Importantly, this procedure was able to reveal not only systematic gaze directions that were in accordance with the stimulus direction or the opposite direction, but also picked up all stimulus-related gaze directions, even if the relation differed across participants or time.

Our analysis approach was highly sensitive to detect stimulus-related gaze directions during all task phases (Appendix 1—figure 3). As expected, we found systematic gaze directions when S1 and S2 were presented on the screen, and they were reduced thereafter, indicating a clear relationship between stimulus presentation and eye movement. Systematic gaze directions were also present in the retro-cue phase where no motion direction was presented. Here they showed a clearly different temporal dynamic as compared to the S1 and S2 phases. They appeared at later time points and with a higher variability between participants, indicating that they coincided with retrieving the target motion direction from working memory.

To relate gaze directions with MEG results, we calculated Spearman rank correlations. We found that there was no systematic relationship at any time point between the stimulus related reconstruction fidelity and the amount of stimulus-related gaze direction. Even more, the correlation varied strongly from time point to time point revealing its random nature. In addition to the lack of significant correlations, we observed clearly distinct temporal profiles for gaze direction (Appendix 1—figure 3a and Appendix 1—figure 3b) and the reconstruction fidelities (Figure 2b in the manuscript, Appendix 1—figure 3c), in particular in the critical retro-cue phase.

We favored this analysis approach over one that directly decoded stimulus motion direction from x-y gaze coordinates, as we considered it hardly feasible to compute an inverted encoding model with only two eye-tracker channels as an input (in comparison to 271 MEG sensors), and to our knowledge, this has not been done before. Other decoding methods have previously been applied to x-y gaze coordinates. However, in contrast to the inverted encoding model, they did not provide a measure of the representation shift which would be crucial for our investigation of serial dependence.

We appreciate the suggestion to conduct additional analyses on eye tracking data (including different temporal and spatial resolution and different features) and their relation to MEG data. However, the first author, who ran all the analyses, has in the meantime left academia. Unfortunately, we currently do not have sufficient resources to perform additional analyses.

While the presented eye movement control analysis makes us confident that our MEG finding was not crucially driven by stimulus-related gaze directions, we agree with the reviewer that we cannot completely exclude that other eye movement-related features could have contributed to our MEG findings. However, we would like to stress that whatever that main source for the observed MEG effect was (shift of the neuronal stimulus representation, (other) features of gaze movement, or shift of the neuronal stimulus representation that leads to systematic gaze movement), our study still provided clear evidence that serial dependence emerged at a later post-encoding stage of object processing in working memory. This central finding of our study is hard to observe with behavioral measures alone and is not affected by the possible effects of eye movements.

We have slightly modified our conclusion in the Results and Appendix 1. Please see also our response to comment 1 from reviewer 3.

(2) I am not convinced by the across-participant correlation between attractive biases in neural representations and attractive behavioral biases in estimation reports. One would expect a correlation with the behavioral bias amplitude, which is not borne out. Instead, there is a correlation with behavioral bias width, but no explanation of how bias width should relate to the bias in neural representations. The authors could be more explicit in their arguments about how these metrics would be functionally related, and why there is no correlation with behavioral bias amplitude.

We are grateful for this suggestion. We correlated the individual neuronal shift with the two individual parameter fits of the behavior shift, i.e., amplitude (a) and tuning width (w). We found a significant correlation between the individual neural bias and the w parameter (r = .70, p = .0246) but not with the a parameter (r = -.35, p = .3258) during the retro-cue period (Appendix 1—figure 1). This indicates that a broader tuning width of the individual bias (as reflected by a smaller w parameter) was associated with a stronger individual neural attraction.

It is important to note that for the calculation of the neural shift, all trials entered the analysis to increase the signal-to-noise ratio, i.e., it included many trials where current and previous targets were separated by, e.g., 100° or more. These trials were unlikely to produce serial dependence. Subjects with a more broadly tuned serial dependence had more interitem differences that showed a behavioral attraction and therefore more trials affected by serial dependence that entered the calculation of the neural shift. In contrast, individual differences in the amplitude (a) parameter were most likely too small, and higher individual amplitude did not involve more trials as compared to smaller amplitude to affect the neural bias in a way to be observed in a significant correlation.

We have added this explanation to Appendix 1.  

(3) The sample size (n = 10) is definitely at the lower end of sample sizes in this field. The authors collected two sessions per participant, which partly alleviates the concern. However, given that serial dependencies can be very variable across participants, I believe that future studies should aim for larger sample sizes.

We want to express our appreciation for raising this issue. We apologize that we did not explicitly explain and justifythe choice for the sample size used in our paper, in particular, as we had in fact performed a formal a-priori power analysis.

At the time of the sample size calculation, there were no comparable EEG or MEG studies to inform our power calculation. Thus, we based our calculation merely on the behavioral effect reported in the literature and, in particular, observed in a behavioral study from our lab that included four different experiments with overall more than 100 participants with 1632 trials each (see Fischer et al., 2020), in which the behavioral serial dependence effect (target vs. nontarget) was very robust. Based on the contrast between target and non-target with an effect size of 1.359 in Experiment 1, a power analysis with 80% desired power led to a small, estimated sample size of 6 subjects.

However, we expected that the detection of the neural signature of this effect would require more participants. Therefore, we based our power calculation on a much smaller behavioral effect, i.e. the modulation of serial dependence by the context-feature congruency that we observed in our previous study (Fischer et al., 2020). In particular, we focused on Experiment 1 of the previous study that used color as the feature for retro-cueing, as we planned to use exactly the same paradigm for the MEG study. In contrast to the serial dependence effect, its modulation by color resulted in a more conservative power estimate: Based on an effect size of 0.856 in that experiment, a sample size of n = 10 should yield a power of 80% with two MEG sessions per subject.

At the time when we conducted our study, two other studies were published that investigated serial dependence on the neural level. Both studies included a smaller number of data points than our study: Sheehan & Serences (2022) recorded about 840 trials in each of 6 participants, resulting in fewer data points both on the participant and on the trial level. Hajonides et al. (2023) measured 20 participants with 400 trials each, again resulting in fewer datapoints than our study (10 participants with 1022 trials each). Taken together, our a-priori sample size estimation resulted in comparable if not higher power as compared to other similar studies, making us feel confident that the estimated sample was sufficient to yield reliable results.

We have now included this description and the results of this power analysis in the Materials and Methods section.

Despite this, we fully agree with the reviewer that our study would profit from higher power. With the knowledge of the results from this study, future projects should attempt to increase substantially the signal-to-noise-ratio by increasing the number of trials in particular, in order to observe, e.g., robust time-resolved effects (see our comments to review 1).

References:

Fischer C, Czoschke S, Peters B, Rahm B, Kaiser J, Bledowski C (2020) Context information supports serial dependence of multiple visual objects across memory episodes. Nature Communication 11: 1932.

Sheehan TC, Serences JT (2022) Attractive serial dependence overcomes repulsive neuronal adaptation PLOS Biology 20: e3001711.

Hajonides JE, Van Ede F, Stokes MG, Nobre AC, Myers NE (2023) Multiple and Dissociable Effects of Sensory History on Working-Memory Performance Journal of Neuroscience 43: 2730–2740.

(4) It would have been great to see an analysis in source space. As the authors mention in their introduction, different brain areas, such as PPC, mPFC, and dlPFC have been implicated in serial biases. This begs the question of which brain areas contribute to the serial dependencies observed in the current study. For instance, it would be interesting to see whether attractive shifts in current representations and pre-stimulus reactivations of previous stimuli are evident in the same or different brain areas.

We appreciate this suggestion. As mentioned above, we currently do not have sufficient resources to perform a MEG source analysis.

Reviewer #3 (Public Review):

Summary:

This study identifies the neural source of serial dependence in visual working memory, i.e., the phenomenon that recall from visual working memory is biased towards recently remembered but currently irrelevant stimuli. Whether this bias has a perceptual or postperceptual origin has been debated for years - the distinction is important because of its implications for the neural mechanism and ecological purpose of serial dependence. However, this is the first study to provide solid evidence based on human neuroimaging that identifies a post-perceptual memory maintenance stage as the source of the bias. The authors used multivariate pattern analysis of magnetoencephalography (MEG) data while observers remembered the direction of two moving dot stimuli. After one of the two stimuli was cued for recall, decoding of the cued motion direction re-emerged, but with a bias towards the motion direction cued on the previous trial. By contrast, decoding of the stimuli during the perceptual stage was not biased.

Strengths:

The strengths of the paper are its design, which uses a retrospective cue to clearly distinguish the perceptual/encoding stage from the post-perceptual/maintenance stage, and the rigour of the careful and well-powered analysis. The study benefits from high within participant power through the use of sensitive MEG recordings (compared to the more common EEG), and the decoding and neural bias analysis are done with care and sophistication, with appropriate controls to rule out confounds.

Weaknesses:

A minor weakness of the study is the remaining (but slight) possibility of an eye movement confound. A control analysis shows that participants make systematic eye movements that are aligned with the remembered motion direction during both the encoding and maintenance phases of the task. The authors go some way to show that this eye gaze bias seems unrelated to the decoding of MEG data, but in my opinion do not rule it out conclusively. They merely show that the strengths of the gaze bias and the strength of MEGbased decoding/neural bias are uncorrelated across the 10 participants. Therefore, this argument seems to rest on a null result from an underpowered analysis.

Our MEG as well eye-movement analysis showed that they were sensitive to pick up robustly stimulus-related effects, both for presented and remembered motion directions. When relating both signals to each other by correlating MEG reconstruction strength with gaze direction, we found a null effect, as pointed out by the reviewer. Importantly, there was also a null effect when the shift of the reconstruction (representing our main finding) was correlated with gaze direction. Furthermore, an examination of the individual time courses of gaze direction and individual MEG reconstruction strength revealed that the lack of a relationship between MEG and gaze data did not rest on a singular observation but was present across all time points. Even more, the temporal profile of the correlation varied strongly from time point to time point revealing its random nature and indicating that there was no hint of a pattern that just failed to reach significance. Taking these observations together, our MEG findings were unlikely to be explained by eye position.

Nevertheless, we agree with the reviewer that there is general problem of interpreting a null effect with a limited number of observations (and an analysis approach that focused on one out of many possible features of the gaze movement). Thus, we admit that there is a (slight) possibility that eye movements contributed to the observed MEG effects. This possibility, however, did not affect our novel finding that serial dependence occurred during the postencoding stage of object processing in working memory.

Please see also our response to point 1 from reviewer 2.

Impact:

This important study contributes to the debate on serial dependence with solid evidence that biased neural representations emerge only at a relatively late post-perceptual stage, in contrast to previous behavioural studies. This finding is of broad relevance to the study of working memory, perception, and decision-making by providing key experimental evidence favouring one class of computational models of how stimulus history affects the processing of the current environment.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor concerns:

The significance statement opens "Our perception is biased towards sensory input from the recent past." This is a semantic point, but it seems a somewhat odd statement, given there is so much debate about whether serial dependence is perceptual vs. decisional, and that the current work indeed claims that it emerges at a late, post-encoding stage.

Thank you for this point. We agree. “Visual cognition is biased towards sensory input from the recent past.” would be a more appropriate statement. According to the Journal's guidelines, however, the paragraph with the Significant Statement will be not included in the final manuscript.

It would be preferable for data and code to be available at review so that reviewers might verify some procedural points for clarity.

Code and preprocessed data used for the presented analyses are now available on OSF via http://osf.io/yjc93/. Due to storage limitations, only the preprocessed MEG data for the main IEM analyses focusing on the current direction are uploaded. For access to additional data, please contact the authors.

For instance, I could use some clarification on the trial sequence. The methods first say the direction was selected randomly, but then later say each direction occurred equally often, and there were restrictions on the relationships between current and previous trial items. So it seems it couldn't have truly been random direction selection - was the order selected randomly from a predetermined set of possibilities?

For the S1/S2 stimuli in a trial the dots moved fully coherent in a direction randomly drawn from a pool of directions between 5° and 355° spaced 10° from one another, therefore avoiding cardinal directions. Across trials, there was a predetermined set of possible differences in motion direction between the current and the previous target. This set included 18 motion direction differences, ranging from -170° to 180°, in steps of 10°. Trial sequences were balanced in a way that each of these differences occurred equally often during a MEG session.

I could also use some additional assurance the sample size (participants or data points) is sufficient for the analysis approach deployed here.

We performed a formal a-priori power analysis to justify our choice for the sample size. Please see our response to reviewer 2, point 3, where we explained the procedure of the apriori power analysis in detail. We have now included this description and the results of this power analysis in the Materials and Methods.

Did you consider a decoding approach, instead of reconstruction, to test what information predominates the signal, in an unbiased way?

Thank you for this argument. With our analysis approach based on the inverted encoding model, we believe to be unbiased, since we first reconstructed whether the MEG signal contained information about the presented and remembered motion direction. Only in the next step, we tested whether this reconstructed signal showed an offset and if so, whether this offset was biased towards or away from the previous target. A decoding approach aims to answer classification questions and is not suitable to reveal the actual shifts of the neural information. In our study, we could decode, e.g., the current direction or the previous target, but this would not answer the question of whether and at which stage of object processing the current representation was biased towards the past. Moreover, in a decoding approach to reveal which information predominates in the signal, we would have to classify different options (e.g. current information vs previous), thereby biasing the possible set of results more than in our chosen analysis.

I think the claim of a "direct" neural signature may come off as an overstatement when the spatial and temporal aspects of the attractive bias are still so coarsely specified here.

Thank you for pointing this out. We agree that the term “direct neural signature” can be seen as an overstatement when it is interpreted to indicate a narrowly defined activity of a brain region (ideally via “direct” invasive recordings) that reflects serial dependence. Our definition of the term “direct” referred to the observation of an attractive shift in a neural representation of the current target motion direction item towards the previous target. This was in contrast to previous “indirect” evidence for the neural basis of serial dependence based on either repulsive shifts of neural representations that were opposite to the attractive bias in behavior or on a reactivation of previous information in the current trial without presenting evidence for the actual neural shift. With this definition in mind, we consider the title of our study a valid description of our findings.

Reviewer #2 (Recommendations For The Authors):

I was wondering why the authors chose a bootstrap test for their neural bias analysis instead of a permutation test, similar to the one they used for their behavioral analysis. As far as I know, bootstrap tests do not provide guaranteed type-1 error rate control. The procedure for the permutation test would be quite straightforward here, randomly permuting the sign of each participant's neural shift and recording the group-average shift in a permutation distribution. This test seems more adequate and more consistent with the behavioral analysis.

Thank you for this comment. We adapted a resampling approach (bootstrapping) that was similar to that by Ester et al. (2020) who also investigated categorical biases and also applied a reconstruction method (Inverted Encoding Model) to assess significance of a bias of the reconstructed orientation against zero in a certain direction. The bootstrapping method relied on a) detecting an offset against zero and b) evaluating the robustness of the observed effect across participants. In contrast, a permutation approach, as suggested by the reviewer, assesses whether an empirical neural shift is more extreme than the permutation distribution. The permutation approach seems more suited to assess the magnitude of the shift which in our study was not a priority. Therefore, we reasoned that the bootstrapping for our inference statistics was better suited to assess the direction of the neural shift and its robustness across participants.

We have added this additional information to the Materials and Methods:

References:

Ester EF, Sprague TC, Serences JT (2020) Categorical biases in human occipitoparietal cortex. Journal of Neuroscience 40:917–931.

The manuscript could be improved by more clearly spelling how the training and testing data were labelled, particularly for the reactivation analyses. If I understood correctly, in the first reactivation analysis the authors train and test on current trial data, but label both training and testing data according to the previous trial's motion direction. In the second analysis, they label the training data according to the current motion direction, but label the testing data according to the previous motion direction. Is that correct?

Yes, this is correct. Please see also our response to reviewer 1, point 2 and 3, for a detailed description.

I was surprised to see that the shift in the reconstructed direction is about three times larger than the behavioral attraction bias. Would one not expect these to be comparable in magnitude? It would be helpful to address and discuss this in the discussion section.

Thank you for pointing this out. We agree with the reviewer that as both measures provided an identical metric (angle degree), one would expect that their magnitudes should be directly comparable. However, we speculate that these magnitudes inform only about the direction of the bias and their significant difference from zero, thus they operate on different scales and are not directly comparable. For example, Hallenbeck et al. (2022) showed that fMRI-based reconstructed orientation bias and behavioral bias correlated on both individual and group level, despite strong magnitude differences. This is in line with our observation and supports the speculation that the magnitudes of neural and behavioral biases operate on different scales and, thus, are not directly comparable.

We have updated to the Discussion accordingly.

References:

Hallenbeck GE, Sprague TC, Rahmati M, Sreenivasan KK, Curtis CE (2022) Working memory representations in visual cortex mediate distraction effects Nature Communications 12: 471.

Reviewer #3 (Recommendations For The Authors):

(1) It may be worth showing that the gaze bias towards the current/cued stimulus is not biased towards the previous target. One option might be to run the same analysis pipeline used for the MEG decoding but on the eye-tracking data. Another could be to remove all participants with significant gaze bias, but given the small sample size, this might not be feasible.

We appreciate this suggestion. However, as mentioned above, we currently do not have sufficient resources to conduct additional analyses on the eye tracking data.

(2) Minor typo: Figure 3c - bias should be 11.7º, not -11.7º.

Corrected. Thank you!

Note on data/code availability: The authors state that preprocessed data and analysis code will be made available on publication, but are not available yet.

Code and preprocessed data used for the present analyses are now available on OSF via http://osf.io/yjc93/. Due to storage limitations, only the preprocessed MEG data for the main IEM analyses focusing on the current direction are uploaded. For access to additional data, please contact the authors.

Author response:

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

eLife assessment

This study provides valuable information on the mechanism of PepT2 through enhanced-sampling molecular dynamics, backed by cell-based assays, highlighting the importance of protonation of selected residues for the function of a proton-coupled oligopeptide transporter (hsPepT2). The molecular dynamics approaches are convincing, but with limitations that could be addressed in the manuscript, including lack of incorporation of a protonation coordinate in the free energy landscape, possibility of protonation of the substrate, errors with the chosen constant pH MD method for membrane proteins, dismissal of hysteresis emerging from the MEMENTO method, and the likelihood of other residues being affected by peptide binding. Some changes to the presentation could be considered, including a better description of pKa calculations and the inclusion of error bars in all PMFs. Overall, the findings will appeal to structural biologists, biochemists, and biophysicists studying membrane transporters.

We would like to express our gratitude to the reviewers for providing their feedback on our manuscript, and also for recognising the variety of computational methods employed, the amount of sampling collected and the experimental validation undertaken. Following the individual reviewer comments, as addressed point-by-point below, we have prepared a revised manuscript, but before that we address some of the comments made above in the general assessment:

• “lack of incorporation of a protonation coordinate in the free energy landscape”.

We acknowledge that of course it would be highly desirable to treat protonation state changes explicitly and fully coupled to conformational changes. However, at this point in time, evaluating such a free energy landscape is not computationally feasible (especially considering that the non-reactive approach taken here already amounts to almost 1ms of total sampling time).  Previous reports in the literature tend to focus on either simpler systems or a reduced subset of a larger problem.  As we were trying to obtain information on the whole transport cycle, we decided to focus here on non-reactive methods.

• “possibility of protonation of the substrate”.

The reviewers are correct in pointing out this possibility, which we had not discussed explicitly in our manuscript.  Briefly, while we describe a mechanism in which protonation of only protein residues (with an unprotonated ligand) can account for driving all the necessary conformational changes of the transport cycle, there is some evidence for a further intermediate protonation site in our data (as we commented on in the first version of the manuscript as well), which may or may not be the substrate itself. A future explicit treatment of the proton movements through the transporter, when it will become computationally tractable to do so, will have to include the substrate as a possible protonation site; for the present moment, we have amended our discussion to alert the reader to the possibility that the substrate could be an intermediate to proton transport. This has repercussions for our study of the E56 pKa value, where – if protons reside with a significant population at the substrate C-terminus – our calculated shift in pKa upon substrate binding could be an overestimate, although we would qualitatively expect the direction of shift to be unaffected. However, we also anticipate that treating this potential coupling explicitly would make convergence of any CpHMD calculation impractical to achieve and thus it may be the case that for now only a semi-quantitative conclusion is all that can be obtained.

• “errors with the chosen constant pH MD method for membrane proteins”.

We acknowledge that – as reviewer #1 has reminded us – the AMBER implementation of hybrid-solvent CpHMD is not rigorous for membrane proteins, and as such added a cautionary note to our paper.  We also explain how the use of the ABFE thermodynamic cycle calculations helps to validate the CpHMD results in a completely orthogonal manner (we have promoted this validation, which was in the supplementary figures, into the main text in the revised version).   We therefore remain reasonably confident in the results presented with regards to the reported pKa shift of E56 upon substrate binding, and suggest that if the impact of neglecting the membrane in the implicit-solvent stage of CpHMD is significant, then there is likely an error cancellation when considering shifts induced by the incoming substrate.

• “dismissal of hysteresis emerging from the MEMENTO method”.

We have shown in our method design paper how the use of the MEMENTO method drastically reduces hysteresis compared to steered MD for path generation, and find this improvement again for PepT2 in this study. We address reviewer #3’s concern about our presentation on this point by revising our introduction of the MEMENTO method, as detailed in the response below.

• “the likelihood of other residues being affected by peptide binding”.

In this study, we have investigated in detail the involvement of several residues in proton-coupled di-peptide transport by PepT2. Short of the potential intermediate protonation site mentioned above, the set of residues we investigate form a minimal set of sorts within which the important driving forces of alternating access can be rationalised.  We have not investigated in substantial detail here the residues involved in holding the peptide in the binding site, as they are well studied in the literature and ligand promiscuity is not the problem of interest here. It remains entirely possible that further processes contribute to the mechanism of driving conformational changes by involving other residues not considered in this paper. We have now made our speculation that an ensemble of different processes may be contributing simultaneously more explicit in our revision, but do not believe any of our conclusions would be affected by this.

As for the additional suggested changes in presentation, we provide the requested details on the CpHMD analysis. Furthermore, we use the convergence data presented separately in figures S12 and S16 to include error bars on our 1D-reprojections of the 2D-PMFs in figures 3, 4 and 5. (Note that we have opted to not do so in figures S10 and S15 which collate all 1D PMF reprojections for the OCC ↔ OF and OCC ↔ IF transitions in single reference plots, respectively, to avoid overcrowding those necessarily busy figures). We have also changed the colours schemes of these plots in our revision to improve accessibility. We have additionally taken the opportunity to fix some typos and further clarified some other statements throughout the manuscript, besides the requests from the reviewers.

Reviewer #1 (Public Review):

The authors have performed all-atom MD simulations to study the working mechanism of hsPepT2. It is widely accepted that conformational transitions of proton-coupled oligopeptide transporters (POTs) are linked with gating hydrogen bonds and salt bridges involving protonatable residues, whose protonation triggers gate openings. Through unbiased MD simulations, the authors identified extra-cellular (H87 and D342) and intra-cellular (E53 and E622) triggers. The authors then validated these triggers using free energy calculations (FECs) and assessed the engagement of the substrate (Ala-Phe dipeptide). The linkage of substrate release with the protonation of the ExxER motif (E53 and E56) was confirmed using constant-pH molecular dynamics (CpHMD) simulations and cellbased transport assays. An alternating-access mechanism was proposed. The study was largely conducted properly, and the paper was well-organized. However, I have a couple of concerns for the authors to consider addressing.

We would like to note here that it may be slightly misleading to the reader to state that “The linkage of substrate release with the protonation of the ExxER motif (E53 and E56) was confirmed using constant-pH molecular dynamics (CpHMD) simulations and cell-based transport assays.” The cellbased transport assays confirmed the importance of the extracellular gating trigger residues H87, S321 and D342 (as mentioned in the preceding sentence), not of the substrate-protonation link as this line might be understood to suggest.

(1) As a proton-coupled membrane protein, the conformational dynamics of hsPepT2 are closely coupled to protonation events of gating residues. Instead of using semi-reactive methods like CpHMD or reactive methods such as reactive MD, where the coupling is accounted for, the authors opted for extensive non-reactive regular MD simulations to explore this coupling. Note that I am not criticizing the choice of methods, and I think those regular MD simulations were well-designed and conducted. But I do have two concerns.

a) Ideally, proton-coupled conformational transitions should be modelled using a free energy landscape with two or more reaction coordinates (or CVs), with one describing the protonation event and the other describing the conformational transitions. The minimum free energy path then illustrates the reaction progress, such as OCC/H87D342-  →  OCC/H87HD342H →  OF/H87HD342H as displayed in Figure 3.

We concur with the reviewer that the ideal way of describing the processes studied in our paper would be as a higher-dimensional free energy landscapes obtained from a simulation method that can explicitly model proton-transfer processes. Indeed, it would have been particularly interesting and potentially informative with regards to the movement of protons down into the transporter in the OF → OCC → IF sequence of transitions. As we note in our discussion on the H87→E56 proton transfer: 

“This could be investigated using reactive MD or QM/MM simulations (both approaches have been employed for other protonation steps of prokaryotic peptide transporters, see Parker et al. (2017) and Li et al. (2022)).  However, the putative path is very long (≈ 1.7 nm between H87 and E56) and may or may not involve a large number of intermediate protonatable residues, in addition to binding site water. While such an investigation is possible in principle, it is beyond the scope of the present study.” 

Where even sampling the proton transfer step itself in an essentially static protein conformation would be pushing the boundaries of what has been achieved in the field, we believe that considering the current state-of-the-art, a fully coupled investigation of large-scale conformational changes and proton-transfer reaction is not yet feasible in a realistic/practical time frame. We also note this limitation already when we say that:

“The question of whether proton binding happens in OCC or OF warrants further investigation, and indeed the co-existence of several mechanisms may be plausible here”. 

Nonetheless, we are actively exploring approaches to treat uptake and movement of protons explicitly for future work.

In our revision, we have expanded on our discussion of the reasoning behind employing a non-reactive approach and the limitations that imposes on what questions can be answered in this study.

Without including the protonation as a CV, the authors tried to model the free energy changes from multiple FECs using different charge states of H87 and D342. This is a practical workaround, and the conclusion drawn (the OCC→ OF transition is downhill with protonated H87 and D342) seems valid. However, I don't think the OF states with different charge states (OF/H87D342-, OF/H87HD342-, OF/H87D342H, and OF/H87HD342H) are equally stable, as plotted in Figure 3b. The concern extends to other cases like Figures 4b, S7, S10, S12, S15, and S16. While it may be appropriate to match all four OF states in the free energy plot for comparison purposes, the authors should clarify this to ensure readers are not misled.

The reviewer is correct in their assessment that the aligning of PMFs in these figures is arbitrary; no relative free energies of the PMFs to each other can be estimated without explicit free energy calculations at least of protonation events at the end state basins. The PMFs in our figures are merely superimposed for illustrating the differences in shape between the obtained profiles in each condition, as discussed in the text, and we now make this clear in the appropriate figure captions.

b) Regarding the substrate impact, it appears that the authors assumed fixed protonation states. I am afraid this is not necessarily the case. Variations in PepT2 stoichiometry suggest that substrates likely participate in proton transport, like the Phe-Ala (2:1) and Phe-Gln (1:1) dipeptides mentioned in the introduction. And it is not rigorous to assume that the N- and C-termini of a peptide do not protonate/deprotonate when transported. I think the authors should explicitly state that the current work and the proposed mechanism (Figure 8) are based on the assumption that the substrates do not uptake/release proton(s).

This is indeed an assumption inherent in the current work. While we do “speculate that the proton movement processes may happen as an ensemble of different mechanisms, and potentially occur contemporaneously with the conformational change” we do not in the previous version indicate explicitly that this may involve the substrate. We make clear the assumption and this possibility in the revised version of our paper. Indeed, as we discuss, there is some evidence in our PMFs of an additional protonation site not considered thus far, which may or may not be the substrate. We now make note of this point in the revised manuscript.

As for what information can be drawn from the given experimental stoichiometries, we note in our paper that “a 2:1 stoichiometry was reported for the neutral di-peptide D-Phe-L-Ala and 3:1 for anionic D-Phe-L-Glu. (Chen et al., 1999) Alternatively, Fei et al. (1999) have found 1:1 stoichiometries for either of D-Phe-L-Gln (neutral), D-Phe-L-Glu (anionic), and D-Phe-L-Lys (cationic).” 

We do not assume that it is our place to arbit among the apparent discrepancies in the experimental data here, although we believe that our assumed 2:1 stoichiometry is additionally “motivated also by our computational results that indicate distinct and additive roles played by two protons in the conformational cycle mechanism”.

(2) I have more serious concerns about the CpHMD employed in the study.

a) The CpHMD in AMBER is not rigorous for membrane simulations. The underlying generalized Born model fails to consider the membrane environment when updating charge states. In other words, the CpHMD places a membrane protein in a water environment to judge if changes in charge states are energetically favorable. While this might not be a big issue for peripheral residues of membrane proteins, it is likely unphysical for internal residues like the ExxER motif. As I recall, the developers have never used the method to study membrane proteins themselves. The only CpHMD variant suitable for membrane proteins is the membrane-enabled hybrid-solvent CpHMD in CHARMM. While I do not expect the authors to redo their CpHMD simulations, I do hope the authors recognize the limitations of their method.

We discuss the limitations of the AMBER CpHMD implementation in the revised version. However, despite that, we believe we have in fact provided sufficient grounds for our conclusion that substrate binding affects ExxER motif protonation in the following way.

In addition to CpHMD simulations, we establish the same effect via ABFE calculations, where the substrate affinity is different at the E56 deprotonated vs protonated protein. This was figure S20 before, though in the revised version we have moved this piece of validation into a new panel of figure 6 in the main text, since it becomes more important with the CpHMD membrane problem in mind. Since the ABFE calculations are conducted with an all-atom representation of the lipids and the thermodynamic cycle closes well, it would appear that if the chosen CpHMD method has a systematic error of significant magnitude for this particular membrane protein system, there may be the benefit of error cancellation. While the calculated absolute pKa values may not be reliable, the difference made by substrate binding appears to be so, as judged by the orthogonal ABFE technique.

Although the reviewer does “not expect the authors to redo their CpHMD simulations”, we consider that it may be helpful to the reader to share in this response some results from trials using the continuous, all-atom constant pH implementation that has recently become available in GROMACS (Aho et al 2022, https://pubs.acs.org/doi/10.1021/acs.jctc.2c00516) and can be used rigorously with membrane proteins, given its all-atom lipid representation.

Unfortunately, when trying to titrate E56 in this CpHMD implementation, we found few protonationstate transitions taking place, and the system often got stuck in protonation state–local conformation coupled minima (which need to interconvert through rearrangements of the salt bridge network involving slow side-chain dihedral rotations in E53, E56 and R57). Author response image 1 shows this for the apo OF state, Author response image 2 shows how noisy attempts at pKa estimation from this data turn out to be, necessitating the use of a hybrid-solvent method.

Author response image 1.

All-atom CpHMD simulations of apo-OF PepT2. Red indicates protonated E56, blue is deprotonated.

Author response image 2.

Difficulty in calculating the E56 pKa value from the noisy all-atom CpHMD data shown in Author response image 1.

b) It appears that the authors did not make the substrate (Ala-Phe dipeptide) protonatable in holosimulations. This oversight prevents a complete representation of ligand-induced protonation events, particularly given that the substrate ion pairs with hsPepT2 through its N- & C-termini. I believe it would be valuable for the authors to acknowledge this potential limitation. 

In this study, we implicitly assumed from the outset that the substrate does not get protonated, which – as by way of response to the comment above – we now acknowledge explicitly. This potential limitation for the available mechanisms for proton transfer also applies to our investigation of the ExxER protonation states. In particular, a semi-grand canonical ensemble that takes into account the possibility of substrate C-terminus protonation may also sample states in which the substrate is protonated and oriented away from R57, thus leaving the ExxER salt bridge network in an apo-like state. The consequence would be that while the direction of shift in E56 pKa value will be the same, our CpHMD may overestimate its magnitude. It would thus be interesting to make the C-terminus protonatable for obtaining better quantitative estimates of the E56 pKa shift (as is indeed true in general for any other protein protonatable residue, though the effects are usually assumed to be negligible). We do note, however, that convergence of the CpHMD simulations would be much harder if the slow degree of freedom of substrate reorientation (which in our experience takes 10s to 100s of nanoseconds in this binding pocket) needs to be implicitly equilibrated upon protonation state transitions. We discuss such considerations in the revised paper.

Reviewer #2 (Public Review):

This is an interesting manuscript that describes a series of molecular dynamics studies on the peptide transporter PepT2 (SLC15A2). They examine, in particular, the effect on the transport cycle of protonation of various charged amino acids within the protein. They then validate their conclusions by mutating two of the residues that they predict to be critical for transport in cell-based transport assays. The study suggests a series of protonation steps that are necessary for transport to occur in Petp2. Comparison with bacterial proteins from the same family shows that while the overall architecture of the proteins and likely mechanism are similar, the residues involved in the mechanism may differ. 

Strengths: 

This is an interesting and rigorous study that uses various state-of-the-art molecular dynamics techniques to dissect the transport cycle of PepT2 with nearly 1ms of sampling. It gives insight into the transport mechanism, investigating how the protonation of selected residues can alter the energetic barriers between various states of the transport cycle. The authors have, in general, been very careful in their interpretation of the data. 

Weaknesses: 

Interestingly, they suggest that there is an additional protonation event that may take place as the protein goes from occluded to inward-facing but they have not identified this residue.

We have indeed suggested that there may be an additional protonation site involved in the conformational cycle that we have not been able to capture, which – as we discuss in our paper – might be indicated by the shapes of the OCC ↔ IF PMFs given in Figure S15. One possibility is for this to be the substrate itself (see the response to reviewer #1 above) though within the scope of this study the precise pathway by which protons move down the transporter and the exact ordering of conformational change and proton transfer reactions remains a (partially) open question. We acknowledge this, denote it with question marks in the mechanistic overview we give in Figure 8 and also “speculate that the proton movement processes may happen as an ensemble of different mechanisms, and potentially occur contemporaneously with the conformational change”.

Some things are a little unclear. For instance, where does the state that they have defined as occluded sit on the diagram in Figure 1a? - is it truly the occluded state as shown on the diagram or does it tend to inward- or outward-facing?

Figure 1a is a simple schematic overview intended to show which structures of PepT2 homologues are available to use in simulations. This was not meant to be a quantitative classification of states. Nonetheless, we can note that the OCC state we derived has extra- and intracellular gate opening distances (as measured by the simple CVs defined in the methods and illustrated in Figure 2a) that indicate full gate closure at both sides. In particular, although it was derived from the IF state via biased sampling, the intracellular gate opening distance in the OCC state used for our conformational change enhanced sampling was comparable to that of the OF state (ie, full closure of the gate), see Figure S2b and the grey bars therein. Therefore, we would schematically classify the OCC state to lie at the center of the diagram in Figure 1a. Furthermore, it is largely stable over triplicates of 1 μslong unbiased MD, where in 2/3 replicates the gates remain stable, and the remaining replicate there is partial opening of the intracellular gate (as shown in Figure 2 b/c under the “apo standard” condition). We comment on this in the main text by saying that “The intracellular gate, by contrast, is more flexible than the extracellular gate even in the apo, standard protonation state”, and link it to the lower barrier for transition to IF than to OF. We did this by saying that “As for the OCC↔OF transitions, these results explain the behaviour we had previously observed in the unbiased MD of Figure 2c.” We acknowledge this was not sufficiently clear and have added details to the latter sentence to help clarify better the nature of the occluded state.

The pKa calculations and their interpretation are a bit unclear. Firstly, it is unclear whether they are using all the data in the calculations of the histograms, or just selected data and if so on what basis was this selection done. Secondly, they dismiss the pKa calculations of E53 in the outward-facing form as not being affected by peptide binding but say that E56 is when there seems to be a similar change in profile in the histograms.

In our manuscript, we have provided two distinct analyses of the raw CpHMD data. Firstly, we analysed the data by the replicates in which our simulations were conducted (Figure 6, shown as bar plots with mean from triplicates +/- standard deviation), where we found that only the effect on E56 protonation was distinct as lying beyond the combined error bars. This analysis uses the full amount of sampling conducted for each replicate. However, since we found that the range of pKa values estimated from 10ns/window chunks was larger than the error bars obtained from the replicate analysis (Figures S17 and S18), we sought to verify our conclusion by pooling all chunk estimates and plotting histograms (Figure S19). We recover from those the effect of substrate binding on the E56 protonation state on both the OF and OCC states. However, as the reviewer has pointed out (something we did not discuss in our original manuscript), there is a shift in the pKa of E53 of the OF state only. In fact, the trend is also apparent in the replicate-based analysis of Figure 6, though here the larger error bars overlap. In our revision, we added more details of these analyses for clarity (including more detailed figure captions regarding the data used in Figure 6) as well as a discussion of the partial effect on the E53 pKa value. 

We do not believe, however, that our key conclusions are negatively affected. If anything, a further effect on the E53 pKa which we had not previously commented on (since we saw the evidence as weaker, pertaining to only one conformational state) would strengthen the case for an involvement of the ExxER motif in ligand coupling.

Reviewer #3 (Public Review):

Summary: 

Lichtinger et al. have used an extensive set of molecular dynamics (MD) simulations to study the conformational dynamics and transport cycle of an important member of the proton-coupled oligopeptide transporters (POTs), namely SLC15A2 or PepT2. This protein is one of the most wellstudied mammalian POT transporters that provides a good model with enough insight and structural information to be studied computationally using advanced enhanced sampling methods employed in this work. The authors have used microsecond-level MD simulations, constant-PH MD, and alchemical binding free energy calculations along with cell-based transport assay measurements; however, the most important part of this work is the use of enhanced sampling techniques to study the conformational dynamics of PepT2 under different conditions. 

The study attempts to identify links between conformational dynamics and chemical events such as proton binding, ligand-protein interactions, and intramolecular interactions. The ultimate goal is of course to understand the proton-coupled peptide and drug transport by PepT2 and homologous transporters in the solute carrier family. 

Some of the key results include:

(1) Protonation of H87 and D342 initiate the occluded (Occ) to the outward-facing (OF) state transition. 

(2) In the OF state, through engaging R57, substrate entry increases the pKa value of E56 and thermodynamically facilitates the movement of protons further down. 

(3) E622 is not only essential for peptide recognition but also its protonation facilitates substrate release and contributes to the intracellular gate opening. In addition, cell-based transport assays show that mutation of residues such as H87 and D342 significantly decreases transport activity as expected from simulations. 

Strengths: 

(1) This is an extensive MD-based study of PepT2, which is beyond the typical MD studies both in terms of the sheer volume of simulations as well as the advanced methodology used. The authors have not limited themselves to one approach and have appropriately combined equilibrium MD with alchemical free energy calculations, constant-pH MD, and geometry-based free energy calculations. Each of these 4 methods provides a unique insight regarding the transport mechanism of PepT2.

(2) The authors have not limited themselves to computational work and have performed experiments as well. The cell-based transport assays clearly establish the importance of the residues that have been identified as significant contributors to the transport mechanism using simulations.

(3) The conclusions made based on the simulations are mostly convincing and provide useful information regarding the proton pathway and the role of important residues in proton binding, protein-ligand interaction, and conformational changes.

Weaknesses: 

(1) Some of the statements made in the manuscript are not convincing and do not abide by the standards that are mostly followed in the manuscript. For instance, on page 4, it is stated that "the K64-D317 interaction is formed in only ≈ 70% of MD frames and therefore is unlikely to contribute much to extracellular gate stability." I do not agree that 70% is negligible. Particularly, Figure S3 does not include the time series so it is not clear whether the 30% of the time where the salt bridge is broken is in the beginning or the end of simulations. For instance, it is likely that the salt bridge is not initially present and then it forms very strongly. Of course, this is just one possible scenario but the point is that Figure S3 does not rule out the possibility of a significant role for the K64-D317 salt bridge. 

The reviewer is right to point out that the statement and Figure S3 as they were do not adequately support our decision to exclude the K64-D317 salt-bridge in our further investigations. The violin plot shown in Figure S3, visualised as pooled data from unbiased 1 μs triplicates, did indeed not rule out a scenario where the salt bridge only formed late in our simulations (or only in some replicates), but then is stable. Therefore, in our revision, we include the appropriate time-series of the salt bridge distances, showing how K64-D317 is initially stable but then falls apart in replicate 1, and is transiently formed and disengaged across the trajectories in replicates 2 and 3. We have also remade the data for this plot as we discovered a bug in the relevant analysis script that meant the D170-K642 distance was not calculated accurately. The results are however almost identical, and our conclusions remain.

(2) Similarly, on page 4, it is stated that "whether by protonation or mutation - the extracellular gate only opens spontaneously when both the H87 interaction network and D342-R206 are perturbed (Figure S5)." I do not agree with this assessment. The authors need to be aware of the limitations of this approach. Consider "WT H87-prot" and "D342A H87-prot": when D342 residue is mutated, in one out of 3 simulations, we see the opening of the gate within 1 us. When D342 residue is not mutated we do not see the opening in any of the 3 simulations within 1 us. It is quite likely that if rather than 3 we have 10 simulations or rather than 1 us we have 10 us simulations, the 0/3 to 1/3 changes significantly. I do not find this argument and conclusion compelling at all.

If the conclusions were based on that alone, then we would agree.  However, this section of work covers merely the observations of the initial unbiased simulations which we go on to test/explore with enhanced sampling in the rest of the paper, and which then lead us to the eventual conclusions.

Figure S5 shows the results from triplicate 1 μs-long trajectories as violin-plot histograms of the extracellular gate opening distance, also indicating the first and final frames of the trajectories as connected by an arrow for orientation – a format we chose for intuitively comparing 48 trajectories in one plot. The reviewer reads the plot correctly when they analyse the “WT H87-prot” vs “D342A H87-prot” conditions. In the former case, no spontaneous opening in unbiased MD is taking place, whereas when D342 is mutated to alanine in addition to H87 protonation, we see spontaneous transition in 1 out of 3 replicates.  However, the reviewer does not seem to interpret the statement in question in our paper (“the extracellular gate only opens spontaneously when both the H87 interaction network and D342-R206 are perturbed”) in the way we intended it to be understood. We merely want to note here a correlation in the unbiased dataset we collected at this stage, and indeed the one spontaneous opening in the case comparison picked out by the reviewer is in the condition where both the H87 interaction network and D342-R206 are perturbed. In noting this we do not intend to make statistically significant statements from the limited dataset. Instead, we write that “these simulations show a large amount of stochasticity and drawing clean conclusions from the data is difficult”. We do however stand by our assessment that from this limited data we can “already appreciate a possible mechanism where protons move down the transporter pore” – a hypothesis we investigate more rigorously with enhanced sampling in the rest of the paper. We have revised the section in question to make clearer that the unbiased MD is only meant to give an initial hypothesis here to be investigated in more detail in the following sections. In doing so, we also incorporate, as we had not done before, the case (not picked out by the reviewer here but concerning the same figure) of S321A & H87 prot. In the third replicate, this shows partial gate opening towards the end of the unbiased trajectory (despite D342 not being affected), highlighting further the stochastic nature that makes even clear correlative conclusions difficult to draw.

(3) While the MEMENTO methodology is novel and interesting, the method is presented as flawless in the manuscript, which is not true at all. It is stated on Page 5 with regards to the path generated by MEMENTO that "These paths are then by definition non-hysteretic." I think this is too big of a claim to say the paths generated by MEMENTO are non-hysteretic by definition. This claim is not even mentioned in the original MEMENTO paper. What is mentioned is that linear interpolation generates a hysteresis-free path by definition. There are two important problems here: (a) MEMENTO uses the linear interpolation as an initial step but modifies the intermediates significantly later so they are no longer linearly interpolated structures and thus the path is no longer hysteresisfree; (b) a more serious problem is the attribution of by-definition hysteresis-free features to the linearly interpolated states. This is based on conflating the hysteresis-free and unique concepts. The hysteresis in MD-based enhanced sampling is related to the presence of barriers in orthogonal space. For instance, one may use a non-linear interpolation of any type and get a unique pathway, which could be substantially different from the one coming from the linear interpolation. None of these paths will be hysteresis-free necessarily once subjected to MD-based enhanced sampling techniques.

We certainly do not intend to claim that the MEMENTO method is flawless. The concern the reviewer raises around the statement "These paths are then by definition non-hysteretic" is perhaps best addressed by a clarification of the language used and considering how MEMENTO is applied in this work. 

Hysteresis in the most general sense denotes the dependence of a system on its history, or – more specifically – the lagging behind of the system state with regards to some physical driver (for example the external field in magnetism, whence the term originates). In the context of biased MD and enhanced sampling, hysteresis commonly denotes the phenomenon where a path created by a biased dynamics method along a certain collective variable lags behind in phase space in slow orthogonal degrees of freedom (see Figure 1 in Lichtinger and Biggin 2023, https://doi.org/10.1021/acs.jctc.3c00140). When used to generate free energy profiles, this can manifest as starting state bias, where the conformational state that was used to seed the biased dynamics appears lower in free energy than alternative states. Figure S6 shows this effect on the PepT2 system for both steered MD (heavy atom RMSD CV) + umbrella sampling (tip CV) and metadynamics (tip CV). There is, in essence, a coupled problem: without an appropriate CV (which we did not have to start with here), path generation that is required for enhanced sampling displays hysteresis, but the refinement of CVs is only feasible when paths connecting the true phase space basins of the two conformations are available. MEMENTO helps solve this issue by reconstructing protein conformations along morphing paths which perform much better than steered MD paths with respect to giving consistent free energy profiles (see Figure S7 and the validation cases in the MEMENTO paper), even if the same CV is used in umbrella sampling. 

There are still differences between replicates in those PMFs, indicating slow conformational flexibility propagated from end-state sampling through MEMENTO. We use this to refine the CVs further with dimensionality reduction (see the Method section and Figure S8), before moving to 2D-umbrella sampling (figure 3). Here, we think, the reviewer’s point seems to bear. The MEMENTO paths are ‘non-hysteretic by definition’ with respect to given end states in the sense that they connect (by definition) the correct conformations at both end-states (unlike steered MD), which in enhanced sampling manifests as the absence of the strong starting-state bias we had previously observed (Figure S7 vs S6). They are not, however, hysteresis-free with regards to how representative of the end-state conformational flexibility the structures given to MEMENTO really were, which is where the iterative CV design and combination of several MEMENTO paths in 2D-PMFs comes in. 

We also cannot make a direct claim about whether in the transition region the MEMENTO paths might be separated from the true (lower free energy) transition paths by slow orthogonal degrees of freedom, which may conceivably result in overestimated barrier heights separating two free energy basins. We cannot guarantee that this is not the case, but neither in our MEMENTO validation examples nor in this work have we encountered any indications of a problem here.

We hope that the reviewer will be satisfied by our revision, where we replace the wording in question by a statement that the MEMENTO paths do not suffer from hysteresis that is otherwise incurred as a consequence of not reaching the correct target state in the biased run (in some orthogonal degrees of freedom).

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors): 

Figure S1: it would be useful to label the panels.

We have now done this.

At the bottom of page 4, it is written that "the extracellular gate only opens spontaneously when both the H87 interaction network and D342-R206 are perturbed (Figure S5)." But it is hard to interpret that from the figure.  

See also our response to reviewer #3. We have revised the wording of this statement, and also highlight in Figure S5 the crucial runs we are referring to, in order to make them easier to discern.

At the bottom of page 5, and top of page 6, there is a lot of "other" information shown, which is inserted for the record - this is a bit glossed over and hard to follow.

The “other” information refers to further conditions we had calculated PMFs for and that gave some insight, but which were secondary for drawing our key conclusions. We thank the reviewer for their feedback that this section needs clarification. We have revised this paragraph to make it easier to follow and highlight better the conclusions we draw form the data.

In Figure 7 it looks as though the asterisks have shifted.

We are indebted to the reviewer for spotting this error, the asterisks are indeed shifted one bar to the right of their intended position. The revised version fixes this issue.

Reviewer #3 (Recommendations For The Authors):

Minor points: In Figure 1a, The 7PMY label and arrow are slightly misplaced.

Figure 1a is a schematic diagram to show the available structures of PepT2 homologues (see also the response to reviewer #2 above). The 7PMY label placement is intentional to indicate a partially occluded inwards-facing state. As we write in the figure caption: “Intermediate positions between states indicate partial gate opening”.

Author Response

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

A revised version of the manuscript models "slope-based" excitability changes in addition to "threshold-based" changes. This serves to address the above concern that as constructed here changes in excitability threshold are not distinguishable from changes in input. However, it remains unclear what the model would do should only a subset of neurons receive a given, fixed input. In that case, are excitability changes sufficient to induce drift? This remains an important question that is not addressed by the paper in its current form.

Thank you for this important point. In the simulation of two memories (Fig. S6), we stimulated half of the neural population for each of the two memories. We therefore also showed that drift happens when only a subset of neuron was simulated.

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

Reviewer #1 (Public Review):

Current experimental work reveals that brain areas implicated in episodic and spatial memory have a dynamic code, in which activity r imulated networks for epresenting familiar events/locations changes over time. This paper shows that such reconfiguration is consistent with underlying changes in the excitability of cells in the population, which ties these observations to a physiological mechanism.

Delamare et al. use a recurrent network model to consider the hypothesis that slow fluctuations in intrinsic excitability, together with spontaneous reactivations of ensembles, may cause the structure of the ensemble to change, consistent with the phenomenon of representational drift. The paper focuses on three main findings from their model: (1) fluctuations in intrinsic excitability lead to drift, (2) this drift has a temporal structure, and (3) a readout neuron can track the drift and continue to decode the memory. This paper is relevant and timely, and the work addresses questions of both a potential mechanism (fluctuations in intrinsic excitability) and purpose (time-stamping memories) of drift.

The model used in this study consists of a pool of 50 all-to-all recurrently connected excitatory neurons with weights changing according to a Hebbian rule. All neurons receive the same input during stimulation, as well as global inhibition. The population has heterogeneous excitability, and each neuron's excitability is constant over time apart from a transient increase on a single day. The neurons are divided into ensembles of 10 neurons each, and on each day, a different ensemble receives a transient increase in the excitability of each of its neurons, with each neuron experiencing the same amplitude of increase. Each day for four days, repetitions of a binary stimulus pulse are applied to every neuron.

The modeling choices focus in on the parameter of interest-the excitability-and other details are generally kept as straightforward as possible. That said, I wonder if certain aspects may be overly simple. The extent of the work already performed, however, does serve the intended purpose, and so I think it would be sufficient for the authors to comment on these choices rather than to take more space in this paper to actually implement these choices. What might happen were more complex modeling choices made? What is the justification for the choices that are made in the present work?

The two specific modeling choices I question are (1) the excitability dynamics and (2) the input stimulus. The ensemble-wide synchronous and constant-amplitude excitability increase, followed by a return to baseline, seems to be a very simplified picture of the dynamics of intrinsic excitability. At the very least, justification for this simplified picture would benefit the reader, and I would be interested in the authors' speculation about how a more complex and biologically realistic dynamics model might impact the drift in their network model. Similarly, the input stimulus being binary means that, on the singleneuron level, the only type of drift that can occur is a sort of drop-in/drop-out drift; this choice excludes the possibility of a neuron maintaining significant tuning to a stimulus but changing its preferred value. How would the use of a continuous input variable influence the results.

(1) In our model, neurons tend to compete for allocation to the memory ensemble: neurons with higher excitability tend to be preferentially allocated and neurons with lower excitability do not respond to the stimulus. Because relative, but not absolute excitability biases this competition, we suggest that the exact distribution of excitability would not impact the results qualitatively. On the other hand, the results might vary if excitability was considered dependent on the activity of the neurons as previously reported experimentally (Cai 2016, Rachid 2016, Pignatelli 2019). An increase in excitability following neural activity might induce higher correlation among ensembles on consecutive days, decreasing the drift.

(2) We thank the reviewer for this very good point. Indeed, two recent studies (Geva 2023 , Khatib 2023) have highlighted distinct mechanisms for a drift of the mean firing rate and the tuning curve. We extended the last part of the discussion to include this point: “Finally, we intended to model drift in the firing rates, as opposed to a drift in the turning curve of the neurons. Recent studies suggest that drifts in the mean firing rate and tuning curve arise from two different mechanisms [33, 34]. Experience drives a drift in neurons turning curve while the passage of time drives a drift in neurons firing rate. In this sense, our study is consistent with these findings by providing a possible mechanism for a drift in the mean firing rates of the neurons driven a dynamical excitability. Our work suggests that drift can depend on any experience having an impact on excitability dynamics such as exercise as previously shown experimentally [9, 35] but also neurogenesis [9, 31, 36], sleep [37] or increase in dopamine level [38]”

Result (1): Fluctuations in intrinsic excitability induce drift

The two choices highlighted above appear to lead to representations that never recruit the neurons in the population with the lowest baseline excitability (Figure 1b: it appears that only 10 neurons ever show high firing rates) and produce networks with very strong bidirectional coupling between this subset of neurons and weak coupling elsewhere (Figure 1d). This low recruitment rate need may not necessarily be problematic, but it stands out as a point that should at least be commented on. The fact that only 10 neurons (20% of the population) are ever recruited in a representation also raises the question of what would happen if the model were scaled up to include more neurons.

This is a very good point. To test how the model depends on the network size, we plotted the drift index against the size of the ensemble. With this current implementation, we did not observe a significant correlation between the drift rate and size of the initial ensemble (Figure S2).

Author response image 1.

The rate of the drift does not depend on the size of the engram. Drift rate against the size of the original engram. Each dot shows one simulation (Methods). n = 100 simulations.

Result (2): The observed drift has a temporal structure

The authors then demonstrate that the drift has a temporal structure (i.e., that activity is informative about the day on which it occurs), with methods inspired by Rubin et al. (2015). Rubin et al. (2015) compare single-trial activity patterns on a given session with full-session activity patterns from each session. In contrast, Delamare et al. here compare full-session patterns with baseline excitability (E = 0) patterns. This point of difference should be motivated. What does a comparison to this baseline excitability activity pattern tell us? The ordinal decoder, which decodes the session order, gives very interesting results: that an intermediate amplitude E of excitability increase maximizes this decoder's performance. This point is also discussed well by the authors. As a potential point of further exploration, the use of baseline excitability patterns in the day decoder had me wondering how the ordinal decoder would perform with these baseline patterns.

This is a good point. Here, we aimed at dissociating the role of excitability from the one of the recurrent currents. We introduced a time decoder that compares the pattern with baseline excitability (E = 0), in order to test whether the temporal information was encoded in the ensemble i.e. in the recurrent weights. By contrast, because the neural activity is by construction biased towards excitability, a time decoder performed on the full session would work in a trivial way.

Result (3): A readout neuron can track drift

The authors conclude their work by connecting a readout neuron to the population with plastic weights evolving via a Hebbian rule. They show that this neuron can track the drifting ensemble by adjusting its weights. These results are shown very neatly and effectively and corroborate existing work that they cite very clearly.

Overall, this paper is well-organized, offers a straightforward model of dynamic intrinsic excitability, and provides relevant results with appropriate interpretations. The methods could benefit from more justification of certain modeling choices, and/or an exploration (either speculative or via implementation) of what would happen with more complex choices. This modeling work paves the way for further explorations of how intrinsic excitability fluctuations influence drifting representations.

Reviewer #2 (Public Review):

In this computational study, Delamare et al identify slow neuronal excitability as one mechanism underlying representational drift in recurrent neuronal networks and that the drift is informative about the temporal structure of the memory and when it has been formed. The manuscript is very well written and addresses a timely as well as important topic in current neuroscience namely the mechanisms that may underlie representational drift.

The study is based on an all-to-all recurrent neuronal network with synapses following Hebbian plasticity rules. On the first day, a cue-related representation is formed in that network and on the next 3 days it is recalled spontaneously or due to a memory-related cue. One major observation is that representational drift emerges day-by-day based on intrinsic excitability with the most excitable cells showing highest probability to replace previously active members of the assembly. By using a daydecoder, the authors state that they can infer the order at which the reactivation of cell assemblies happened but only if the excitability state was not too high. By applying a read-out neuron, the authors observed that this cell can track the drifting ensemble which is based on changes of the synaptic weights across time. The only few questions which emerged and could be addressed either theoretically or in the discussion are as follows:

1. Would the similar results be obtained if not all-to-all recurrent connections would have been molded but more realistic connectivity profiles such as estimated for CA1 and CA3?

This is a very interesting point. We performed further simulations to show that the results are not dependent on the exact structure of the network. In particular, we show that all-to-all connectivity is not required to observe a drift of the ensemble. We found similar results when the recurrent weights matrix was made sparse (Fig. S4a-c, Methods). Similarly to all-to-all connectivity, we found that the ensemble is informative about its temporal history (Fig. S4d) and that an output neuron can decode the ensemble continuously (Fig. S4e).

Author response image 2.

Sparse recurrent connectivity shows similar drifting behavior as all-to-all connectivity. The same simulation protocol as Fig. 1 was used while the recurrent weights matrix was made 50% sparse (Methods). a) Firing rates of the neurons across time. The red traces correspond to neurons belonging to the first assembly, namely that have a firing rate higher than the active threshold after the first stimulation. The black bars show the stimulation and the dashed line shows the active threshold. b) Recurrent weights matrices after each of the four stimuli show the drifting assembly. c) Correlation of the patterns of activity between the first day and every other days. d) Student's test t-value of the ordinal time decoder, for the real (blue) and shuffled (orange) data and for different amplitudes of excitability E. e) Center of mass of the distribution of the output weights (Methods) across days. c-e) Data are shown as mean ± s.e.m. for n = 10 simulations.

1. How does the number of excited cells that could potentially contribute to an engram influence the representational drift and the decoding quality?

This is indeed a very good question. We did not observe a significant correlation between the drift rate and size of the initial ensemble (Fig. S2).

Author response image 3.

The rate of the drift does not depend on the size of the engram. Drift rate against the size of the original engram. Each dot shows one simulation (Methods). n = 100 simulations.

1. How does the rate of the drift influence the quality of readout from the readout-out neuron?

We thank the reviewer for this interesting question. We introduced a measure of the “read-out quality” and plotted this value against the rate of the drift. We found a small correlation between the two quantities. Indeed, the read-out quality decreases with the rate of the drift.

Author response image 4.

The quality of the read-out decreases with the rate of the drift. Read-out quality computed on the firing rate of the output neuron against the rate of the drift (Methods). Each dot shows one simulation. n = 100 simulations.

Reviewer #3 (Public Review):

The authors explore an important question concerning the underlying mechanism of representational drift, which despite intense recent interest remains obscure. The paper explores the intriguing hypothesis that drift may reflect changes in the intrinsic excitability of neurons. The authors set out to provide theoretical insight into this potential mechanism.

They construct a rate model with all-to-all recurrent connectivity, in which recurrent synapses are governed by a standard Hebbian plasticity rule. This network receives a global input, constant across all neurons, which can be varied with time. Each neuron also is driven by an "intrinsic excitability" bias term, which does vary across cells. The authors study how activity in the network evolves as this intrinsic excitability term is changed.

They find that after initial stimulation of the network, those neurons where the excitability term is set high become more strongly connected and are in turn more responsive to the input. Each day the subset of neurons with high intrinsic excitability is changed, and the network's recurrent synaptic connectivity and responsiveness gradually shift, such that the new high intrinsic excitability subset becomes both more strongly activated by the global input and also more strongly recurrently connected. These changes result in drift, reflected by a gradual decrease across time in the correlation of the neuronal population vector response to the stimulus.

The authors are able to build a classifier that decodes the "day" (i.e. which subset of neurons had high intrinsic excitability) with perfect accuracy. This is despite the fact that the excitability bias during decoding is set to 0 for all neurons, and so the decoder is really detecting those neurons with strong recurrent connectivity, and in turn strong responses to the input. The authors show that it is also possible to decode the order in which different subsets of neurons were given high intrinsic excitability on previous "days". This second result depends on the extent by which intrinsic excitability was increased: if the increase in intrinsic excitability was either too high or too low, it was not possible to read out any information about past ordering of excitability changes.

Finally, using another Hebbian learning rule, the authors show that an output neuron, whose activity is a weighted sum of the activity of all neurons in the network, is able to read out the activity of the network. What this means specifically, is that although the set of neurons most active in the network changes, the output neuron always maintains a higher firing rate than a neuron with randomly shuffled synaptic weights, because the output neuron continuously updates its weights to sample from the highly active population at any given moment. Thus, the output neuron can readout a stable memory despite drift.

Strengths:

The authors are clear in their description of the network they construct and in their results. They convincingly show that when they change their "intrinsic excitability term", upon stimulation, the Hebbian synapses in their network gradually evolve, and the combined synaptic connectivity and altered excitability result in drifting patterns of activity in response to an unchanging input (Fig. 1, Fig. 2a). Furthermore, their classification analyses (Fig. 2) show that information is preserved in the network, and their readout neuron successfully tracks the active cells (Fig. 3). Finally, the observation that only a specific range of excitability bias values permits decoding of the temporal structure of the history of intrinsic excitability (Fig. 2f and Figure S1) is interesting, and as the authors point out, not trivial.

Weaknesses:

1. The way the network is constructed, there is no formal difference between what the authors call "input", Δ(t), and what they call "intrinsic excitability" Ɛ_i(t) (see Equation 3). These are two separate terms that are summed (Eq. 3) to define the rate dynamics of the network. The authors could have switched the names of these terms: Δ(t) could have been considered a global "intrinsic excitability term" that varied with time and Ɛ_i(t) could have been the external input received by each neuron i in the network. In that case, the paper would have considered the consequence of "slow fluctuations of external input" rather than "slow fluctuations of intrinsic excitability", but the results would have been the same. The difference is therefore semantic. The consequence is that this paper is not necessarily about "intrinsic excitability", rather it considers how a Hebbian network responds to changes in excitatory drive, regardless of whether those drives are labeled "input" or "intrinsic excitability".

This is a very good point. We performed further simulations to model “slope-based”, instead of “threshold-based”, changes in excitability (Fig. S5a, Methods). In this new definition of excitability, we changed the slope of the activation function, which is initially sampled from a random distribution. By introducing a varying excitability, we found very similar results than when excitability was varied as the threshold of the activation function (Fig. S5b-d). We also found similarly that the ensemble is informative about its temporal history (Fig. S5e) and that an output neuron can decode the ensemble continuously (Fig. S5f).

Author response image 5.

Change of excitability as a variable slope of the input-output function shows similar drifting behavior as considering a change in the threshold. The same simulation protocol as Fig. 1 was used while the excitability changes were modeled as a change in the activation function slope (Methods). a) Schema showing two different ways of defining excitability, as a threshold (top) or slope (bottom) of the activation function. Each line shows one neuron and darker lines correspond to neurons with increased excitability. b) Firing rates of the neurons across time. The red traces correspond to neurons belonging to the first assembly, namely that have a firing rate higher than the active threshold after the first stimulation. The black bars show the stimulation and the dashed line shows the active threshold. c) Recurrent weights matrices after each of the four stimuli show the drifting assembly. d) Correlation of the patterns of activity between the first day and every other days. e) Student's test t-value of the ordinal time decoder, for the real (blue) and shuffled (orange) data and for different amplitudes of excitability E. f) Center of mass of the distribution of the output weights (Methods) across days. d-f) Data are shown as mean ± s.e.m. for n = 10 simulations.

1. Given how the learning rule that defines input to the readout neuron is constructed, it is trivial that this unit responds to the most active neurons in the network, more so than a neuron assigned random weights. What would happen if the network included more than one "memory"? Would it be possible to construct a readout neuron that could classify two distinct patterns? Along these lines, what if there were multiple, distinct stimuli used to drive this network, rather than the global input the authors employ here? Does the system, as constructed, have the capacity to provide two distinct patterns of activity in response to two distinct inputs?