Author response:

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

Reviewer #1 (Public Review):

Summary:

The current manuscript by Hajra et al deals with the role of the prominent Sirtuins SIRT1 and -3 during infection of macrophages with Salmonella Typhimurium (ST). Apparently, ST infection induces upregulation of host cell SRTs to aid its own metabolism during the intracellular lifestyle and to help reprogramming macrophage polarization. The manuscript has two parts, namely one part that deals with Salmonella infection in cells, where RAW 264.7 murine macrophage-like cells, sharing some features with primary macrophages, were employed. Infected RAW cells displayed a tendency to polarize towards wound-healing M2 and not inflammatory M1 macrophages, which was dependent on SRT. Consequently, the inflammatory response in RAW was more robust in the absence of SRT. Moreover, loss of SRTs leads to impaired bacterial proliferation in these cells, which was attributed to defects in metabolic adaption of the bacteria in the absence of SRT-activity and to the increased M1 inflammatory response.

Unfortunately, the line of argumentation remains incomplete because corresponding assays in mice showed the opposite result as compared to the experiments using RAW 264.7 cells. i.e. loss of SRTs leads to increased bacterial load in animals (versus impaired proliferation in RAW 264.7 cells). The authors cannot explain this discrepancy.

Strengths:

Extensive analysis of Salmonella infection in RAW macrophage-like cells and mice in the context of SRT1/3 function.

Weaknesses:

Lack of connection between the cell-based and organismic data, which are not supportive of each other.

We are highly grateful for your valuable and insightful comments. Thank you for appreciating the merit of our manuscript. We agree with the opposing phenotypes among the RAW264.7 cell line (Fig. 2A), primary peritoneal macrophages (ex vivo) (Fig.2B), and in vivo mouse model (Fig.8) findings. Both RAW264.7 macrophage and peritoneal macrophage infection show attenuated intracellular bacterial proliferation owing to the heightened proinflammatory burst. This is in sharp contrast to our in vivo mouse model of infection which shows increased organ burden and bacterial dissemination. The higher bacterial load in the organs including the spleen (Fig.8B) is attributed to increased pro-inflammatory cytokine burst and ROS production (Fig.8F-H, Fig.S9) triggering bacterial dissemination. The pro-inflammatory arsenals like IL-6, IL-1β and ROS that limit bacterial proliferation within the macrophages (F4/80+ macrophages within the spleen or in RAW264.7 macrophages or primary peritoneal macrophages) are facilitating bacterial dissemination in blood and to the other organs (Fig. 8I-L, Fig.S3F-G). This is in line with the following previous findings-

Klebsiella pneumoniae infection triggers an inflammatory response via secretion of IL-6 upon HIF-1α activation that induces bacterial dissemination (Holden VI, Breen P, Houle S, Dozois CM, Bachman MA. Klebsiella pneumoniae Siderophores Induce Inflammation, Bacterial Dissemination, and HIF-1α Stabilization during Pneumonia. mBio. 2016 Sep 13;7(5):e01397-16. doi: 10.1128/mBio.01397-16. PMID: 27624128; PMCID: PMC5021805.).

Correlation analysis of immune responses to Salmonella infection revealed that increased innate immune “cassette” opposes the adaptive immune arm leading to increased bacterial load in mice (Hotson AN, Gopinath S, Nicolau M, Khasanova A, Finck R, Monack D, et al. Coordinate actions of innate immune responses oppose those of the adaptive immune system during Salmonella infection of mice. Science signaling. 2016;9(410):ra4). 

In our revised manuscript, we have assessed additional splenic populations including CD45+, Ly6C+, and CD11c+ populations. Our results show that the CD45+ splenic population depicts increased bacterial loads like that of the total splenic population within the SIRT1/3 inhibited cohorts. However, CD45+ monocytes and Ly6C positive splenic population exhibit compromised burden within the SIRT1/3 inhibited cohorts. Moreover, within the CD11c+ population, CD45+ granulocytes or lymphocytes show comparable organ loads to that of the vehicle control or SIRT1 activator-treated mice group (Fig. M-S, Fig.S8). Overall, our data suggest heterogeneous bacterial burden in diverse splenic populations.

Reviewer #2 (Public Review):

Dipasree Hajra et al demonstrated that Salmonella was able to modulate the expression of Sirtuins (Sirt1 and Sirt3) and regulate the metabolic switch in both host and Salmonella, promoting its pathogenesis. The authors found Salmonella infection induced high levels of Sirt1 and Sirt3 in macrophages, which were skewed toward the M2 phenotype allowing Salmonella to hyper-proliferate. Mechanistically, Sirt1 and Sirt3 regulated the acetylation of HIF-1alpha and PDHA1, therefore mediating Salmonella-induced host metabolic shift in the infected macrophages. Interestingly, Sirt1 and Sirt3-driven host metabolic switch also had an effect on the metabolic profile of Salmonella. Counterintuitively, inhibition of Sirt1/3 led to increased pathogen burdens in an in vivo mouse model. Overall, this is a well-designed study. There are a few comments below that would further strengthen the current study.

Major comments:

In the in vivo study (lines 436-446) - the authors noticed increased pathogen burden in the EX-527 or the 3TYP-treated mice cohorts but decreased pathogen burden within the F4/80+ macrophage population. What are the other cell types that have increased pathogen burden in splenocytes from EX-527 or the 3TYP treated? Can this be further explored and explained?

While the authors indicated that IL-6 cytokine storm and elevated ROS production could result in bacterial dissemination in vivo, one could also argue that Sirt1/3 inhibitors might have an impact on gut function and/or gut microbiota (PMID: 22115311). Did Sirt1/3 inhibitors also lead to increased pathogen burdens in the gut? If so, the potential effect of these in vivo treatments on gut microbiota/colonization resistance should be discussed.

Minor comment:

Sirt1 has been shown to be degraded during Salmonella infection (PMID: 28192515), which is different from the current study. An explanation should be provided for this.

We thank you for your encouraging and gracious comments. We deeply appreciate your time and efforts in providing constructive feedback for the betterment of our work. As per your precious suggestions, we have assessed additional splenic populations including CD45+, Ly6C+, and CD11c+ populations apart from F4/80+ macrophage populations. Our analysis suggests that the CD45+ splenic population show increased bacterial loads similar to the total splenic population within the SIRT1/3 inhibited cohorts. However, CD45+ monocytes and Ly6C positive splenic population exhibit compromised burden within the SIRT1/3 inhibited cohorts. Moreover, CD11c+ population, CD45+ granulocytes or lymphocytes show comparable organ loads to that of the vehicle control or SIRT1 activator treated mice group (Fig. 8M-S). Overall, our data suggest heterogeneous bacterial burden in diverse splenic populations.

We immensely appreciate the reviewer for this insightful question about the effect of SIRT1/3 on the gut per se. To answer your question, we observed increased pathogen loads within the mesenteric lymph nodes of the gut in the SIRT1/3 inhibitor-treated mice groups (Fig.8B). In our revised manuscript, we evaluated gut inflammation via IL1-β estimation in the mice's ileal tissues and have observed heightened IL-1β production in the inhibitor-treated mice cohorts in comparison to the vehicle control (Fig. S3G). We have also examined gut epithelial pathology via Haematoxylin-Eosin (H&E) staining of the ileal sections to address the effect of in vivo treatment on gut microbiota and colonization resistance which is appended here. However, the gut microbiota crosstalk and their effect on colonization resistance is a part of another current study and it is being examined in detail there. Therefore, this appended H&E has not been incorporated in the revised manuscript.

Author response image 1.

In line with the reference PMID: 28192515, where Sirt1 has been shown to be degraded during Salmonella infection at later time points of infection, our study also has shown that both SIRT1 mRNA (Fig. 1A) and protein levels (Fig. S1A) show an elevated expression at 2h and 6h post-infection and show a downregulation at 16h in comparison to the 6h time point.  However, SIRT3 expression levels remain elevated even at later time points of infection. Therefore, we speculate that there is a shared role between SIRT1 and SIRT3 that facilitates the phenotypes reported in our study.

Reviewer #3 (Public Review):

Summary:

In this paper, Hajra et al have attempted to identify the role of Sirt1 and Sirt3 in regulating metabolic reprogramming and macrophage host defense. They have performed gene knockdown experiments in RAW macrophage cell lines to show that depletion of Sirt1 or Sirt3 enhances the ability of macrophages to eliminate Salmonella Typhimurium. However, in mice, inhibition of Sirt1 resulted in dissemination of the bacteria but the bacterial burden was still reduced in macrophages. They suggest that the effect they have observed is due to increased inflammation and ROS production by macrophages. They also try to establish a weak link with metabolism. They present data to show that the switch in metabolism from glycolysis to fatty acid oxidation is regulated by acetylation of Hif1a, and PDHA1.

Strengths:

The strength of the manuscript is that the role of Sirtuins in host-pathogen interactions has not been previously explored in-depth making the study interesting. It is also interesting to see that depletion of either Sirt1 or Sirt3 results in a similar outcome.

Weaknesses:

The major weakness of the paper is the low quality of data, making it harder to substantiate the claims. Also, there are too many pathways and mechanisms being investigated. It would have been better if the authors had focussed on either Sirt1 or Sirt3 and elucidated how it reprograms metabolism to eventually modulate host response against Salmonella Typhimurium. Experimental evidence is also lacking to prove the proposed mechanisms. For instance, they show correlative data that the knockdown of Sirt1-mediated shift in metabolism is due to HIF1a acetylation but this needs to be proven with further experiments.

We appreciate the reviewer’s critical analysis of our work. In the revised manuscript, we aimed to eliminate the low-quality data sets and have tried to substantiate them with better and conclusive ones, as directed in the recommendations for the author section. We agree with the reviewer that the inclusion of both Sirtuins 1 and 3 has resulted in too many pathways and mechanisms and focusing on one SIRT and its mechanism of metabolic reprogramming and immune modulation would have been a less complicated alternative approach. However, as rightly pointed out, our work demonstrated the shared and few overlapping roles of the two sirtuins, SIRT1 and SIRT3, together mediating the immune-metabolic switch upon Salmonella infection. As per the reviewer’s suggestion, we have performed additional experiments with HIF-1α inhibitor treatment in our revised manuscript to substantiate our correlative findings on SIRT1-mediated regulation of host glycolysis (Fig.7G).

Reviewer #1 (Recommendations For The Authors):

The authors state "SIRT1 and SIRT3 inhibition resulted in increased pathogen loads in organs and triggered enhanced bacterial dissemination, together leading to increased susceptibility of the mice to S. Typhimurium infection owing to increased ROS and IL-6 production." How can this be reconciled? To the reviewer, this is not a convincing explanation. The reviewer is not a mouse pathologist, so maybe did not understand the argument in full.

However, in order to clarify whether these phenomena can be brought into context and explained by for instance cell-autonomous (in (RAW) macrophages) versus non-autonomous (in mice) mechanisms, it would be required to bring in context the organismic phenotype with a cellular phenotype, using more physiologic primary macrophages.

(1) The authors show in Figure 8 that in general SRT inhibition leads to increased infection whereas SRT activation results in decreased infection. This is even true for e the spleen (e.g. Figure 8B), which should be full of macrophages upon infection.

(2) Only Figure 8L implies that endogenous primary, splenic macrophages show a higher infection rate upon pharmacologic SRT activation, which would potentially mirror the RAW results. This is however not supportive of their own explanation: Who would now produce more ROS and IL6 if these macrophages are more supportive of intracellular ST? Is there a difference in the roles or SRTs between different types of macrophages and/or neutrophils? And between macrophages and somatic cells concerning ST infection? The reviewer tends to believe that RAW cells display a defective killing response (such as ROS production) as they are highly transformed cells. Therefore, the authors should use cultured peritoneal macrophages or BMDMs in addition to RAW264.7 cells.

The literature cited by the authors also implies that the inflammatory response in mice is higher in the absence of SRTs. This is in line with a role for SRTs in (negatively) regulating M1 inflammatory polarization but probably not with increased bacterial burden in mice. If it was, then increased dissemination could be explained by increased tissue damage. However, the flow cytometry experiments from infected organs then do not confirm that, as the infection of individual cells is higher upon SRT inhibition. Thus there seems a broad gap between the role of SRTs in ST infection in RAW264.7 cells versus non-transformed cells.

I would not discard the RAW results, as I am convinced that they contain valuable data. However, it needs to be clarified what aspect of the host response RAW 264.7 cells represent. Primary macrophages might likely be more aggressive towards the bacteria. Finally, the question arises: what is the role of the metabolic switch in the in vivo setting?

The reviewer recommends repeating some key experiments by in-vitro-infecting BMDMs or isolated peritoneal macrophages (after some days of culturing) to bridge between the present RAW-derived data and the mouse data. How is the bacterial load with and without SRT inhibitor/activator in primary macrophages, when infected outside of the body? Can ex-vivo infection also affect polarization of e.g. peritoneal macrophages or the metabolic switch? If it is possible to find a conclusive explanation for their data, then this story might really add to our understanding of another aspect of how ST manipulates the host to survive.

In case the reviewer understands the mouse experiments correctly, all assays on peritoneal cells were performed after in-vivo-infection and/or treatment.

Together, RAW 264.7 murine macrophage-like cells might not be the right model to understand the phenotypes in full. As far as the reviewer knows, these cells are not capable of killing bacteria as effectively as activated primary macrophages or neutrophils.

A few of the key findings of RAW264.7 macrophages have been replicated in primary peritoneal macrophages (Fig. 2B, S3E-F, S6B, S7B-D). We wanted to clarify that the peritoneal macrophage experiments were performed ex vivo, wherein peritoneal macrophages were isolated from mice were then subjected to SIRT1/3 inhibitor treatments and Salmonella infection and not after in vivo treatment or infection. In ex vivo setting, we have examined the effect of SIRTs on the metabolic switch during Salmonella infection (Fig. S7B-D) which resembled our RAW264.7 macrophage data. Additionally, in in vivo setting, we have analyzed the transcript level expression of host metabolic genes and corresponding bacterial metabolic genes in infected mice liver and spleen tissue under SIRT1/3 inhibitor treatment (Fig.S7E-F, Fig.6C-D). Our primary peritoneal macrophage data exactly mirrors the RAW264.7 macrophage findings showing attenuated intracellular bacterial proliferation owing to the heightened proinflammatory burst upon SIRT1/3 knockdown or inhibition (Fig.2A-B). This is opposite to our in vivo mouse model of infection which shows increased organ burden and bacterial dissemination (Fig.8A-H). The pro-inflammatory arsenals that limit bacterial proliferation within the macrophages (F4/80+ macrophages within the spleen or in RAW264.7 macrophages or primary peritoneal macrophages) are facilitating bacterial dissemination in blood and to the other organs owing to tissue damage (Fig.8E-L). This is in line with the following previous findings-

Klebsiella pneumoniae infection triggers an inflammatory response via secretion of IL-6 upon HIF-1α activation that induces bacterial dissemination (Holden VI, Breen P, Houle S, Dozois CM, Bachman MA. Klebsiella pneumoniae Siderophores Induce Inflammation, Bacterial Dissemination, and HIF-1α Stabilization during Pneumonia. mBio. 2016 Sep 13;7(5):e01397-16. doi: 10.1128/mBio.01397-16. PMID: 27624128; PMCID: PMC5021805.).

Correlation analysis of immune responses to Salmonella infection revealed that increased innate immune “cassette” opposes the adaptive immune arm leading to increased bacterial load in mice (Hotson AN, Gopinath S, Nicolau M, Khasanova A, Finck R, Monack D, et al. Coordinate actions of innate immune responses oppose those of the adaptive immune system during Salmonella infection of mice. Science Signaling. 2016;9(410):ra4). 

As per the reviewer’s suggestions, we have analyzed other populations apart from F4/80+ macrophages and have observed that the CD45+ splenic population depicts increased bacterial loads like that of the total splenic population within the SIRT1/3 inhibited cohorts. However, CD45+ monocytes and Ly6C positive splenic population exhibit compromised burden within the SIRT1/3 inhibited cohorts. Moreover, the CD1c+ population, CD45+ granulocytes, or lymphocytes show comparable organ loads to that of the vehicle control or SIRT1 activator-treated mice group (Fig.8M-S, Fig.S8). Overall, our data suggest heterogeneous bacterial burden in diverse splenic populations.

Reviewer #3 (Recommendations For The Authors):

Abstract

The authors state that perturbing Sirt1 and Sirt3 results in a shift in Salmonella's metabolism. On the contrary, the data reflects the metabolism in the host cell and not the bacteria. This statement is wrong. They only show increased expression of some of the glycolytic genes in Salmonella, which is not sufficient to make the claim that the switch to fatty acid oxidation in macrophages is due to utilisation of glucose by the bacteria.

We value the reviewer’s response and have accordingly reframed our sentence in the abstract (Line 24-25).

Fig 1: Expression of Sirt1 - The data needs to be supported with a western blot for Sirt1 and Sirt3 but the Western blots shown in the supplementary figure are of very poor quality and do not support the authors' claim.

We have repeated the western blot and have supplemented the previous blot with an alternate blot in Fig. S1A as per your precious input.

Why haven't the authors shown any representative blots for Sirt1 and Sirt3 upon infection with Salmonella mutants? They need to italicize the genes when they describe mRNA expression.

Previously we had only performed transcript-level expression of Sirt1 and Sirt3 upon infection with Salmonella mutants and therefore representative blot image was absent. The gene names have been duly italicized while describing mRNA expression (Line 126-154). We regret the inconvenience caused. We have performed the western blotting to assess the protein expression profile upon infection with Salmonella mutants as per the reviewer’s suggestion and the representative blot image has been duly appended in the revised manuscript (Fig. S1B).

What is the rationale for examining Sirt1 and Sirt3 mRNA in M1 and M2 macrophages? Salmonella infection on its own will polarise the macrophages towards M1. How long were these macrophages infected? The time points are missing.

The rationale behind the examination of Sirt1 and Sirt3 mRNA in M1 and M2 polarized was to ascertain whether indeed M1 polarized macrophages exhibit decreased expression of Sirt1 or Sirt3 and polarization of macrophages toward M2 state show upregulation of Sirt1 and Sirt3 upon Salmonella infection. After confirming these above-mentioned findings through this preliminary experiment, we then hypothesized whether Salmonella infection on its own will polarise the macrophages toward an immunosuppressive M2 state at a later time course of infection as infection drives the induction of SIRT expression and whether this is mediated by Sirt1 and Sirt3 (Fig. 3). We are extremely apologetic for not mentioning the 16h time-point in the figure and the missing time point has been duly documented in the revised manuscript (Line 155).

Fig S2 knockdown of Sirt1 and Sirt3 are not convincing.

We are extremely sorry for the inconclusive knockdown blot. An alternative blot has been substantiated in the revised manuscript (Fig. S2,C-D).

Fig 2A and 2B the time point post infection has not been mentioned. Although it is stated that 2h and 16h post-infection samples were analysed. Only one time point has been shown.

We are sorry for the confusion. We wanted to clarify that Fig.2A and Fig. 2B show the fold proliferation where fold proliferation was calculated as CFU at 16hr divided by CFU at 2hr as mentioned in the materials and methods section under the heading of Intracellular proliferation or gentamicin protection assay.

Fold Proliferation= [CFU at 16h]/[CFU at 2h]

The cytokines data are intriguing in that the increase in IL-6 relative to control is seen only at 2h and 20h but not at 6h. Il-6 at 20h in untransfected cells is comparable to uninfected cells. Did the authors investigate cell death? Salmonella induces various forms of cell death which could account for the decreased cytokine production at later time points.

We have investigated the cell death upon Salmonella infection via MTT assay. At later time points of infection, we indeed observed around 16 percent decrease in cell survival compared to the initial time point of 2h. The results have been appended here and it supports our eminent reviewer’s reasoning for the decreased cytokine production at later time points.

Author response image 2.

Additional cytokines such as IL-1b would be helpful. Also, not sure how uninfected macrophages produce nearly 200pg of IL-10.

As per the author’s critical suggestion, we have assessed the IL-1b cytokine production at 16h post-infection in RAW264.7 macrophages and peritoneal macrophages and mice serum samples at 5th day post-infection (Fig.S3C, S3E-F). Our results indicate increased production of IL-b in the infected SIRT1/3 knockdown RAW264.7 macrophages, SIRT1/3 inhibitor-treated peritoneal macrophages and in mice serum samples under SIRT1/3 inhibitor treatment in comparison to the vehicle control. Additionally, we have quantified IL-1b in mice ileal tissues under SIRT1/3 inhibitor treatment (Fig.S3G) and have obtained heightened intestinal IL-1b production in the inhibitor-treated cohorts. We thank the reviewer for raising the concern for 200pg of IL-10 in the uninfected macrophages. We have repeated the experiment and have provided an alternative representative graph for the experiment wherein the IL-10 levels in the uninfected cohorts range between 20-40pg/ml (Fig. S3B).

It is surprising that the authors have found increased Sirt1 binding to NFkB, however there is no change in acetylated NFkB upon infection (Fig 4B). Acetylated p65 is equally high in uninfected Scrambled siRNA, UI shSirt1, STM Scr, and STM shSirt1. Furthermore, increased binding of Sirt1 with NFkb would mean decreased acetylation hence decreased inflammation. However, Salmonella induces profound inflammation.

We thank the reviewers for their insightful and critical questioning. We truly acknowledge that due to oversaturation there was no apparent change in the acetylated p65 among the different sample sets. Therefore, in the revised manuscript we have provided an image at lower exposure where the changes in the acetylation of the p65 subunit are apparent. Salmonella induces inflammation upon challenge similar to any other pathogens and induces acute inflammatory responses. This heightened acute inflammation at the initial phases of infection subsides at a later phase of infection. Here, we have performed the Sirt1 interaction with NFκB at 16hr post-infection where increased binding of Sirt1 with NFκB facilitates the resolution of the Salmonella-_induced acute inflammation. This is in line with previous reports that suggest SIRT1 suppresses acute inflammation through the promotion of p65 acetylation and inhibition of NFκB activity. (Yang H, Zhang W, Pan H, et al. SIRT1 activators suppress inflammatory responses through promotion of p65 deacetylation and inhibition of NF-κB activity. _PLoS One. 2012;7(9):e46364. doi:10.1371/journal.pone.0046364, Liu TF, Yoza BK, El Gazzar M, Vachharajani VT, McCall CE. NAD+-dependent SIRT1 deacetylase participates in epigenetic reprogramming during endotoxin tolerance. J Biol Chem. 2011;286(11):9856–64., Liu TF, Vachharajani V, Millet P, Bharadwaj MS, Molina AJ, McCall CE. Sequential actions of SIRT1-RELB-SIRT3 coordinate nuclear-mitochondrial communication during immunometabolic adaptation to acute inflammation and sepsis. J Biol Chem. 2015;290(1):396–408.)

Please explain how the acetylated p65 was analysed.

Total endogenous p65 subunit was immunoprecipitated using Anti-NFκB p65 antibody and the immunoprecipitated fraction was probed with Anti-Acetylated Lysine antibody to assess acetylated p65.

An increase in ROS production is seen in a relatively small percentage of cells- not more than 4% of cells. How does this contribute to such a significant difference in intracellular bacterial burden? Also, it is not clear how the authors calculated the fold change in proliferation. It is better to show the actual bacterial burden logarithmically.

We strongly agree with the reviewer’s concerns, and we have reanalyzed the flow cytometric data set. The revised data have been presented in Fig. S5 which shows a considerable increase in DCFDA positive population. For instance, the infected scrambled control shows around 2.44% of ROS-producing cells, however knockdown of SIRT1 and SIRT3 increases the ROS-producing cells to 27.34% and 28.64% respectively.

Fold proliferation was calculated as CFU at 16hr divided by CFU at 2hr as mentioned in the materials and methods section under the heading of Intracellular proliferation or gentamicin protection assay. Fold proliferation has been calculated as opposed to absolute CFU values to nullify the differential phagocytosis of bacteria to the macrophages among the samples.

Fold Proliferation= [CFU at 16h]/[CFU at 2h]

An increase in metabolic genes is not sufficient to show that the macrophages are metabolically reprogrammed.

We thank the reviewer for the valuable comment. We agree that an increase in metabolic gene profile is not sufficient to claim metabolic reprogramming. Therefore, in addition to the metabolic gene profile, we have estimated lactate production (end-product of glycolysis) as an indicator of glycolysis (Fig. 5 C-E) and have performed the fatty acid β oxidation activity (Fig. 5G-H) to support our claims.

Figure 5F the band intensities do not visually match the bands shown for PFK. For instance, shSIRT1 STM (1.00) and shSIRT3 STM (0.81).

We are extremely sorry for the erroneous band intensity for shSIRT3. Upon reanalysis of the band intensities, we have corrected the band intensity for shSIRT3 to 2.28 (Fig.5F).

It is surprising that HADHA is not expressed in uninfected samples.

We are extremely apologetic for the inappropriate representative blot. We feel that the discrepancy might have arisen due to the usage of old antibodies. We have provided an alternate blot for the HADHA gene where fresh antibody staining solution was used for probing which shows expression even in the uninfected samples (Fig.5F).

Figure 6A - What is the significance of PFA fixed samples (PI) compared to SI samples? This has not been discussed.

PFA-fixed samples are paraformaldehyde-treated bacterial samples that harbor the immune signals or Pattern Associated Molecular Patterns (PAMPs). The rationale for using PI in addition to SI samples was to show whether the phenomena is driven by live metabolically active pathogens or is mediated by PAMPs.

I understand that the hypothesis is that during the later phase of infection, there is an increase in fatty acid oxidation which correlates with a decrease in inflammation. However, at 6h there is no increase in genes regulating fatty acid oxidation. Why did the authors choose 6h when the previous experiments have been done at 16h?

We indeed agree with the reviewer’s understanding of our hypothesis that there is an increase in fatty acid oxidation along the progression of infection which correlates with a decrease in inflammation. The Salmonella intracellular replication has been reported to commence at 6h post-internalization when SPI-2 effector expression is fully established (Helaine S, Thompson JA, Watson KG, Liu M, Boyle C, Holden DW. Dynamics of intracellular bacterial replication at the single cell level. Proc Natl Acad Sci U S A. 2010;107(8):3746-3751. doi:10.1073/pnas.1000041107). Therefore, we have assessed the 6h timepoint post-infection in addition to the initial and later timepoints of 2h and 16h respectively. Additionally, the nanostring gene profiling data of both host and bacterial genes indicate the onset of both metabolic (Fig. 5A, 6A) and immune genes (Fig. 3A) modulation at 6h post-infection. We have validated these results via qPCR studies and have observed an upregulation in the transcript level of fatty acid oxidation genes as depicted in Fig. S7A in RAW264.7 macrophages.

Line 355 it is mentioned that Sirt1 and Sirt3 abrogate metabolic shift by reducing glycolytic flux. This is incorrect as experiments such as carbon chase assays have not been performed to investigate glycolytic flux.

As per the reviewer’s valuable suggestion, we have removed the word ‘flux’ from the above-mentioned statement(Line 351, Line 353).

Lines 392-393: "We immunoprecipitated PDHA1 and checked for its interaction with SIRT3 or SIRT1 under knockdown condition of SIRT3 or upon SIRT3 inhibitor treatment (Fig.7 G-H)"

What is the rationale for checking PDHA1 interaction with Sirt under Sirt knockdown conditions?

We are thankful to the reviewer for the critical comments. The rationale for checking PDHA1 interaction with Sirt was to ascertain that indeed Sirt interacted with PDHA1 under S. Typhimurium infection and abrogation of either protein expression (knockdown) or their enzymatic activity (inhibitor treatment) diminished the interaction.

Moreover, the blots are very confusing and do not represent the authors' claims.

(1) In the input blot I do not see Sirt3 depletion in shSirt3 knockdown sample.

The knockdown has been quantified in the input blot as per your suggestion. A knockdown of 40% has been obtained in the uninfected dataset whereas a knockdown of 47.1% has been obtained in the infected data set at 16h post-infection (Fig.7H).

(2) Why does Sirt1 interact with PDHA1 similar to Sirt3. Do both the proteins bind to PDHA1 at the same time/ competitively? If so do they both deacetylate?

In literature, Sirt3 has been shown to interact with PDHA1 and deacetylate PDHA1. However, the interaction of Sirt1 with PDHA1 has not been reported previously and therefore we are unable to comment on the exact dynamics of the interaction. Future studies need to be performed to explore these phenomena in depth. However, SIRT1 agonist SRT1720 has been shown to impact PDH phosphorylation and its activity (Han Y, Sun W, Ren D, Zhang J, He Z, Fedorova J, Sun X, Han F, Li J. SIRT1 agonism modulates cardiac NLRP3 inflammasome through pyruvate dehydrogenase during ischemia and reperfusion. Redox Biol. 2020 Jul;34:101538).

(3) Figure 7I in the IP: IgG samples Sirt3 seem to bind to IgG non-specifically, which questions the specificity of Sirt3 binding to PDHA1.

We appreciate the reviewer for pointing out this concern. The immunoprecipitation experiment has been repeated and the same has been appended in the revised manuscript and we observe no non-specific binding of Sirt3 antibody to IgG.

(4) In Figure 7I all the bands Ac PDHA1, PDHA1, and Sirt3 look similar with double bands, which has not been seen in other blots. How is this possible?

This cannot explain the increase in beta-oxidation observed.

We thank the reviewer for raising this concern. We have repeated the experiment and provided the alternative blot as per the reviewer’s suggestion.

The rationale for performing this experiment was to show that SIRT plays an important role in the activation of downstream TCA cycle pathways via PDHA1 deacetylation during Salmonella infection. The deacetylation of PDHA1 has been previously reported to cause transcriptional activation of the downstream TCA cycle and oxidative phosphorylation (Zhang Y, Wen P, Luo J, et al., Cell Death Dis.,2021). Additionally, PDHA1 hyperacetylation has been reported to cause lactate overproduction (An, S., Yao, Y., Hu, H. et al. PDHA1 hyperacetylation-mediated lactate overproduction promotes sepsis-induced acute kidney injury via Fis1 lactylation. Cell Death Dis 14, 457 (2023)). In our study, increased lactate production and PDHA1 hyperacetylation have been observed during SIRT3 inhibition conditions upon Salmonella infection.

Author response:

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

Reviewer #1:

(1) One issue that needs to be considered is the nomenclature of the enhancer. The authors have presented data to show this enhancer controls the expression of Ctnnb1 in the stomach, intestine, and colon tissues. However, the name proposed by the authors, ieCtnnb1 (intestinal enhancer of Ctnnb1), doesn't represent its functions. It might be more appropriate to call it a different name, such as gieCtnnb1 (gastrointestinal enhancer of Ctnnb1).

We thank the reviewer for the insightful suggestion and agree that wholemount reporter assays indicated ieCtnnb1 and ieCTNNB1 indeed display activity in the stomach. However, in current study, we focused on the cellular distribution and the function in intestinal epithelia. After careful consideration, we reasoned that the current designation, ieCtnnb1, would be more appropriately represent its expression pattern and functions based on provided evidence. We hope the reviewer could understand our reasoning.  

(2) The writing of this manuscript can be improved in a few places. 

a) The definitions or full names for the abbreviations of some terms, e.g., Ctnnb1, ieCtnnb1, in both abstract and main text, are needed when they first appear. Specifically, Line 108 should be moved to Lines 26 and 95. Lines 125126 are redundant. ieCtnnb1 in Line 130 needs to be defined.

We appreciate the suggestion. In the revision, we have included the definition of Ctnnb1 and the full name of ieCtnnb1 when they first appear in the abstract and the main text. Lines 125-126 were deleted in the revision.

b) Line 192-194, the description of the result needs to be rewritten to reflect

the higher expression of LacZ transcript in eGFP+ cells. 

We would like to emphasize that the key point of this part is that the enhancer activity of ieCtnnb1 is present in both Lgr5-eGFP+ and Lgr5-eGFP- cells. This was validated by single-cell sequencing, which revealed the presence of LacZ transcripts in the Paneth cells. Moreover, we could not confidently conclude that eGFP+ cells have higher expression levels of LacZ, as these measurements were obtained from separate, semi-quantitative RTqPCR experiments.

c)  More details are needed for how the data using human tumor samples were generated and how they were analyzed. 

We thank the suggestion. In the revision, we have provided additional details regarding the data and subsequent analyses of human CRC samples as follows: “We previously conducted paired analyses of chromatin immunoprecipitation sequencing (ChIP-seq) for H3K27ac and H3K4me3, alongside RNA-seq on 68 CRC samples and their adjacent normal (native) tissue (Li et al., 2021).  In the current study, we performed analyses for the enrichment of H3K27ac and H3K4me3 at ieCTNNB1 and CTNNB1 promoter regions, as well as the expression levels of CTNNB1, followed by combined analyses (Figure. 5A, Figure 5 - figure supplement 1).”

d) The genomic structures from multiple species are presented at the bottom of Figure 1a. However, the description and explanation are lacking in both the main text and the figure legend.

We apologize for not presenting clearly. We have added related description in the legend of Figure 1A as “The sequence conservation of the indicated species is shown at the bottom as vertical lines”. We also added an explanation in lines 162-163 of the main text: “Notably, unlike neCtnnb1, the primary sequence of ieCtnnb1 is not conserved among vertebrates (Figure 1A, bottom)”.

Reviewer #2:

(1) One of the main issues emerging during reading concerns the interpretation of the consequence of deleting the ieCtnnb1 enhancer. The authors write on line 235 that the deletion of ieCtnnb1 "undermined" Wnt signaling in the intestinal epithelium. This feels too strong, as the status of the pathway is only mildly affected, testified by the observation that mice with homozygous deletion on ieCtnnb1 are alive and well. The enhancer likely "only" drives higher Ctnnb1 expression, and it does not affect Wnt signaling by other mechanisms. The reduction of Wnt target gene expression upon its deletion is easily interpreted as the consequence of reduced β-catenin. Also the title, in my opinion, allows this ambiguity to stick in readers' minds. In other words, the authors present no evidence that the ieCtnnb1 enhancer controls Wnt signaling dosage via any mechanism other than its upregulation of Ctnnb1 expression in the intestinal epithelium. Reduced Ctnnb1, in turn, could explain the observed reduction of Wnt signaling output and the interesting downstream physiological consequences. Unless the authors think otherwise, I suggest they clarify this throughout the text, including necessary modifications to the title.

We greatly appreciate the reviewer’s important comments and suggestion. We agree that ieCtnnb1’s direct effect on the canonical Wnt signaling is to regulate the transcription of Ctnnb1 in the intestinal epithelia. Therefore, knockout of ieCtnnb1 leads to compromised expression of Ctnnb1 and, consequently, reduced Wnt signaling.  The term “undermined” is indeed too strong and has been revised to “compromised” in the revision (line 237). Similar revisions have been made throughout the manuscript. Particularly, the title was changed into “A Ctnnb1 enhancer transcriptionally regulates Wnt signaling dosage to balance homeostasis and tumorigenesis of intestinal epithelia”. However, as we state in the following point, decreased levels of β-catenin on ieCtnnb1 loss could lead to indirect effect, including the reduced expression of Bambi, which might cause a more significant decrease of nuclear β-catenin.

(2) It is unclear how the reduction of Ctnnb1 mRNA caused by deletion of ieCtnnb1 in mice could lead to a preferential decrease of nuclear more than membranous β-catenin (Fig. 1K and L). This might reflect a general cell autonomous reduction in Wnt signaling activation; yet, it is not clear how this could occur. Do the authors have any explanations for this?

It's a very important question. We observed that in inCtnnb1 knockout epithelia, the expression of Bambi (BMP and activin membrane-bound inhibitor) was significantly downregulated. Since BAMBI has been reported to stabilize β-catenin and facilitate its nuclear translocation, it is likely that the reduced level of BAMBI resulting from the loss of ieCtnnb1 further decreased nuclear βcatenin. In the revision, the expression change of Bambi has been added in Figure 1M. Moreover, the related content was extensively discussed with proper citations: “We noticed that after knocking out ieCtnnb1, the level of βcatenin in the nuclei of small intestinal crypt cells of Ctnnb1Δi.enh mice decreased more significantly compared to that in the cytoplasm (49.5% vs. 29.8%). Although the loss of ieCtnnb1 should not directly lead to reduced nuclear translocation of β-catenin, RNA-seq results showed that the loss of ieCtnnb1 causes a reduction in the expression of Bambi (BMP and activin membranebound inhibitor), a target gene in the canonical Wnt signaling pathway (Figure 1M). BAMBI promotes the binding of Frizzled to Dishevelled, thereby stabilizing β-catenin and facilitating its nuclear translocation (Lin et al., 2008; Liu et al., 2014; Mai et al., 2014; Zhang et al., 2015). Thus, it is likely that the decreased level of BAMBI resulting from the loss of ieCtnnb1 further reduced nuclear βcatenin”. 

(3) In Figure 1 K-L the authors show β-catenin protein level. Why not show its mRNA?

The mRNA levels of Ctnnb1 in small and large intestinal crypts were shown in Figure 1I and 1J, demonstrating reduced expression of Ctnnb1 upon ieCtnnb1 knockout. We hope the reviewer understands that it is unnecessary to measure the nuclear and cytosolic levels of Ctnnb1 transcripts, as the total mRNA level generally reflects the protein level. 

(4) Concerning the GSEA of Figure 1 that includes the Wnt pathway components: a) it would be interesting to see which components and to what extent is their expression affected; b) why should the expression of Wnt components that are not Wnt target genes be affected in the first place? It is odd to see this described uncritically and used to support the idea of downregulated Wnt signaling.

We appreciate the suggestion and apologize for any lack of clarity. The affected components of the Wnt signaling pathway and the extent of their changes are summarized in Figure 1 – figure supplement 3. Additionally, we have provided explanations for their downregulation. For instance, the reduced expression of Wnt3 and Wnt2b ligands in ieCtnnb1-KO crypts may be attributed to the decreased numbers of Paneth cells.  

(5) In lines 251-252 the authors refer to "certain technical issues" in the isolation of cell type from the intestinal epithelium. Why this part should be obscure in the characterization of a tissue for which there are several established protocols of isolation and analysis is not clear. I would rather describe what these issues have been and how they protocol of isolation and analysis is not clear. I would rather describe what these issues have been and how they might have affected the data presented.

We thank the reviewer for pointing this out. The single-cell preparation and sequencing of small intestinal cryptal epithelial cells were carried out largely according to reported protocols with slight modification. The enrichment of live crypt epithelial cells (EpCAM+DAPI-) by flow cytometry and cell filtering after single-cell sequencing were appropriate (Figure 2 – figure supplement 1A1C). We would like to emphasize a few points: 1) Unlike other protocols, we did not exclude immune cells, erythrocytes, or endothelial cells using negative sorting antibodies. 2) When defining cell populations, we focused exclusively on epithelial cell types and did not consider other cell types, such as immune cells. As a result, the so-called “undefined” cells include a mixture of nonepithelial cells. Indeed, markers for erythrocytes (AY036118/Erf1, PMID:12894589) and immune cells (Gm42418 and Lars2, PMID:30940803, PMID: 35659337) were the top three enriched genes in the “undefined” cluster (Figure 2 – figure supplement 1D). 3) Nonetheless, the overall findings remain robust, as key observations such as the loss of Paneth cells and reduced cell proliferation were validated through histological studies. This information has been incorporated into the revised manuscript with related references cited (lines 254-259). 

(6) It is interesting that human SNPs exist that seem to fall within the ieCTNNB1 enhancer and affect the gastrointestinal expression of CTNNB1. Could the author report or investigate whether this SNP is present in human populations that have been considered in large-scale studies for colorectal cancer susceptibility? It seems to me a rather obvious next step of extreme importance to be ignored.

(7) From Figure 5A a reader could conclude that colorectal tumor cells have a higher expression of CTNNB1 mRNA than in normal epithelium. This is the first time I have seen this observation which somewhat undermines our general understanding of Wnt-induced carcinogenesis exclusively initiated by APC mutations whereby it is β-catenin's protein level, not expression of its mRNA, of crucial importance. I find this to be potentially the most interesting observation of the current study, which could be linked to the activity of the enhancer discovered, and I suggest the authors elaborate more on this and perhaps consider it for future experimental follow-ups.

We appreciate the comments and suggestions.  We therefore added related content in the revision (lines 470-475): “Importantly, ieCTNNB1 displayed higher enhancer activity in most CRC samples collected in the study. Moreover, the SNP rs15981379 (C>T) within ieCTNNB1 is associated with the expression of CTNNB1 in the GI tract. Future population studies could investigate how the enhancer activity of ieCTNNB1 and this particular SNP are associated with CRC susceptibility and prognosis”.

(8) I am surprised that the authors, who seem to have dedicated lots of resources to this study, are satisfied by analyzing their ChIP experiments with qPCR rather than sequencing (Figure 6). ChIP-seq would produce a more reliable profile of the HNF4a and CREB1 binding sites on these loci and in other control regions, lending credibility to the whole experiment and binding site identification. Sequencing would also take care of the two following conceptual problems in primer design. 

First: while the strategy to divide enhancer and promoter in 6 regions to improve the resolution of their finding is commendable, I wonder how the difference in signal reflects primers' efficiency rather than HNF4/CREB1 exact positioning. The possibility of distinguishing between regions 2 and 3, for example, in a ChIP-qPCR experiment, also depends on the average DNA fragment length after sonication, a parameter that is not specified here. 

Second: what are the primers designed to detect the ieCtnnb1 enhancer amplifying in the yellow-columns samples of Figure 6G? In this sample, the enhancer is deleted, and no amplification should be possible, yet it seems that a value is obtained and set to 1 as a reference value.

This is indeed a crucial point, and we fully agree with the reviewer that “ChIP-seq would produce a more reliable profile of the HNF4a and CREB1 binding sites on these loci and in other control regions”. However, we believe that our current ChIP-qPCR experiments have adequately addressed the potential concerns raised by the reviewers. (1) We have ensured that the DNA fragment length after sonication falls within the range of 200 bp to 500 bp, with an average length of approximately 300 bp (Author response image 1A). We have stated the point in the revised methods section (line 633). (2) We have randomly inspected 14 out of 26 primer sets used in Figure 6 and its supplemental figure (Author response image 1B-E), confirming that all primer sets demonstrate equal amplification efficiency (ranging from 90% to 110%). This information has also been included in the revised methods section (line 650). (3) Figures 6G and 6H show reduced enrichment of HNF4𝛼 (6G) and p-S133-CREB1 (6H) at the Ctnnb1 promoter in ieCtnnb1 knockout ApcMin/+ tumor tissues. The ChIP-qPCR primers used were positioned at the Ctnnb1 promoter, not at ieCtnnb1, with IgG control enrichment serving as the reference values on the Y-axes. 

Author response image 1.

(A) Agarose gel electrophoresis of sonicated DNA. (B-E) Tests of amplification efficiency for primer sets used in ChIP-qPCR.

(9) The ChIP-qPCR showing preferential binding of pS133-CREB1 in small intestinal crypts and CHT15 cells (line 393) should be shown. 

The ChIP-qPCR results demonstrating preferential binding of p-S133-

CREB1 over CREB1 have been added in revised Figure 6C, 6D and Figure 6 – Supplement 1C.

(10) It is not entirely clear what the blue tracks represent at the bottom of Figures 6C-D and Figure 6 - Figure Supplement 1C-D. The ChIP-seq profiles of both CREB1 and HNF4a shown in Figures 6A and Figure 6 - Figure Supplement 1A do not seem to match. Taking HNF4a, for example from Figure 6 - Figure Supplement 1A it seems to bind on the Ctnnb1 promoter, while in Figure 6 - Figure Supplement 1D the peaks are within the first intron. I realize this might all be a problem with a different scale across figure panels, but I suggest producing a cleared figure.

We apologize for the confusion. We have revised Figure 6C-6D, Figure 6 - figure supplement 1C-D, and the corresponding legends to enhance clarity. (1) The top panels of Figures 6C and 6D respectively highlight shaded regions of ieCTNNB1 (pink) and the CTNNB1 promoter (grey) in Figure 6A, emphasizing the enrichment of p-S133-CREB1.  (2) The top panels of Figure 6 – figure supplement 1C and 1D respectively highlight shaded regions of ieCtnnb1 (pink) and the Ctnnb1 promoter (grey) in Figure 6A – figure supplement 1A, emphasizing the enrichment of HNF4α. (3) Because Figures 6C-6D and Figure 6 - figure supplement 1C-1D respectively correspond to human and mouse genomes, the positions of peaks and scales differ.  

(11) In the intro the authors refer to "TCF-4". I suggest they use the more recent unambiguous nomenclature for this family of transcription factors and call it TCF7L2.

TCF-4 has been changed into TCF7L2 in the revision (line 81)

(12) In lines 121-122, the authors write "Although numerous putative enhancers...only a fraction of them were functionally annotated". To what study/studies are the authors referring? Please provide references.

References were added in the revision (line 124)

(13) In some parts the authors use strong words that should in my opinion be attenuated. Examples are: (i) at line 224, "maintains" would be better substituted with "contribute", as in the absence of ieCtnnb1, Ctnnb1 is still abundantly expressed; (ii) at line 266 "compromised" when the proliferative capacity of CFCs and TACs seems to be only mildly reduced; (iii) at line 286 "disrupts", the genes are simply downregulated.

We thank these great suggestions. 1) On lines 224-225, the sentence was revised to: “These data suggest that ieCtnnb1 plays a specific role in regulating the transcription of Ctnnb1 in intestinal epithelia”. 2) On line 271, “compromised” were replaced with “mildly reduced”. 3) In ieCtnnb1 knockout epithelial cells of small intestine, genes related to secretory functions were decreased, while genes related to absorptive functions were increased. Therefore, the term 'disrupts' is more appropriate than 'downregulates'. 

Reviewer #3:

Line 81, c-Myc should be human MYC (italics) to agree with the other human gene names in this sentence. 

c-Myc has been changed into MYC in the revision (line 82)

Line 215, wildtype should be wild-type. 

“wildtype” has been changed into “wild-type” in the revision (line 215)

Line 224, Elimination of the enhancer did not abolish expression of Ctnnb1; therefore, it would be better to say that it "helps to maintain Ctnnb1 transcription" 

The sentence was changed into “These data suggest that ieCtnnb1 plays a specific role in regulating the transcription of Ctnnb1 in intestinal epithelia” in revision (lines 224-225)

Line 228, perhaps "to activate transcription" is meant. 

“active” has been changed into “activate” in the revision (line 228)

Line 235, consider "reduced" instead of "undermined". 

“undermined” has been replaced with “compromised” in the revision (line 237)

Line 262, "em" dashes should be a both ends of this insertion. 

Line 298, "dysfunctional" would be better.

Line 356, "samples were". 

Line 481, 12-hr (add hyphen). 

All above points have been optimized according to the reviewer’s suggestion.

Line 712, Is "poly-N" meant? 

“Poly-N” indicates undetected bases during sequencing. This explanation was added in the revision (lines 759-760).

Figure 1K, the GAPDH signal is not visible and that panel is unnecessary as there is an H3 control.   

Figure 1K and 1L respectively show levels of nuclear and cytoplasmic βcatenin. GAPDH and H3 were used as internal references for the cytoplasmic and nuclear fractions, respectively, confirming both robust fractionation and equal loading.

Author response:

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

Reviewer #3 (Public Review):

The iron manipulation experiments are in the whole animal and it is likely that this affects general feeding behaviour, which is known to affect NB exit from quiescence and proliferative capacity. The loss of ferritin in the gut and iron chelators enhancing the NB phenotype are used as evidence that glia provide iron to NB to support their number and proliferation. Since the loss of NB is a phenotype that could result from many possible underlying causes (including low nutrition), this specific conclusion is one of many possibilities.

We have investigated the feeding behavior of fly by Brilliant Blue (sigma, 861146)[1]. Our result showed that the amount of dye in the fly body were similar between control group and BPS group, suggesting that BPS almost did not affect the feeding behavior (Figure 3—figure supplement 1A).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

There was a gap between the Pros nuclear localization and downstream targets of ferritin, particularly NADH dehydrogenase and biosynthesis. Could overexpression of Ndi1 restore Pros localization in NBs?

Ferritin defect downregulates iron level, which leads to cell cycle arrest of NBs via ATP shortage. And cell cycle arrest of NBs probably results in NB differentiation[2, 3]. We have added the experiment in Figure 5—figure supplement 2. This result showed that overexpression of Ndi1 could significantly restore Pros localization in NBs.

The abstract requires revision to cover the major findings of the manuscript, particularly the second half.

We revised the abstract to add more major findings of the manuscript in the second half as follows:

“Abstract

Stem cell niche is critical for regulating the behavior of stem cells. Drosophila neural stem cells (Neuroblasts, NBs) are encased by glial niche cells closely, but it still remains unclear whether glial niche cells can regulate the self-renewal and differentiation of NBs. Here we show that ferritin produced by glia, cooperates with Zip13 to transport iron into NBs for the energy production, which is essential to the self-renewal and proliferation of NBs. The knockdown of glial ferritin encoding genes causes energy shortage in NBs via downregulating aconitase activity and NAD+ level, which leads to the low proliferation and premature differentiation of NBs mediated by Prospero entering nuclei. More importantly, ferritin is a potential target for tumor suppression. In addition, the level of glial ferritin production is affected by the status of NBs, establishing a bicellular iron homeostasis. In this study, we demonstrate that glial cells are indispensable to maintain the self-renewal of NBs, unveiling a novel role of the NB glial niche during brain development.”

In Figure 2B Mira appeared to be nuclear in NBs, which is inconsistent with its normal localization. Was it Dpn by mistake?

In Figure 2B, we confirmed that it is Mira. Moreover, we also provide a magnified picture in Figure 2B’, showing that the Mira mainly localizes to the cortex or in the cytoplasm as previously reported.

Figure 2C, Fer1HCH-GFP/mCherry localization was non-uniform in the NBs revealing 1-2 regions devoid of protein localization potentially corresponding to the nucleus and Mira crescent enrichment. It is important to co-label the nucleus in these cells and discuss the intracellular localization pattern of Ferritin.

We have revised the picture with nuclear marker DAPI in Figure 2C. The result showed that Fer1HCH-GFP/Fer2LCH-mCherry was not co-localized with DAPI, which indicated that Drosophila ferritin predominantly distributes in the cytosol[4, 5]. As for the concern mentioned by this reviewer, GFP/mCherry signal in NBs was from glial overexpressed ferritin, which probably resulted in non-uniform signal.

In Figure 3-figure supplement 3F, glial cells in Fer1HCH RNAi appeared to be smaller in size. This should be quantified. Given the significance of ferritin in cortex glial cells, examining the morphology of cortex glial cells is essential.

In Figure 3—figure supplement 3F, we did not label single glial cells so it was difficult to determine whether the size was changed. However, it seems that the chamber formed by the cellular processes of glial cells becomes smaller in Fer1HCH RNAi. The glial chamber will undergo remodeling during neurogenesis, which responses to NB signal to enclose the NB and its progeny[6]. Thus, the size of glial chamber is regulated by NB lineage size. In our study, ferritin defect leads to the low proliferation, inducing the smaller lineage of each NB, which likely makes the chamber smaller.

Since the authors showed that the reduced NB number was not due to apoptosis, a time-course experiment for glial ferritin KD is recommended to identify the earliest stage when the phenotype in NB number /proliferation manifests during larval brain development.

We observed brains at different larval stages upon glial ferritin KD. The result showed that NB proliferation decreased significantly, but NB number declined slightly at the second-instar larval stage (Figure 5—figure supplement 1E and F), suggesting that brain defect of glial ferritin KD manifests at the second-instar larval stage.

Transcriptome analysis on ferritin glial KD identified genes in mitochondrial functions, while the in vivo EM data suggested no defects in mitochondria morphology. A short discussion on the inconsistency is required.

For the observation of mitochondria morphology via the in vivo EM data, we focused on visible cristae in mitochondria, which was used to determine whether the ferroptosis happens[7]. It is possible that other details of mitochondria morphology were changed, but we did not focus on that. To describe this result more accurately, we replaced “However, our observation revealed no discernible defects in the mitochondria of NBs after glial ferritin knockdown” with the “However, our result showed that the mitochondrial double membrane and cristae were clearly visible whether in the control group or glial ferritin knockdown group, which suggested that ferroptosis was not the main cause of NB loss upon glial ferritin knockdown” in line 207-209.

The statement “we found no obvious defects of brain at the first-instar larval stage (0-4 hours after larval hatching) when knocking down glial ferritin (Figure 5-figure supplement 1C).” lacks quantification of NB number and proliferation, making it challenging to conclude.

We have provided the quantification of NB number and proliferation rate of the first-instar larval stage in Figure 5—figure supplement 1C and D. The data showed that there is no significant change in NB number and proliferation rate when knocking down ferritin, suggesting that no brain defect manifests at the first-instar larval stage.

A wild-type control is necessary for Figure 6A-C as a reference for normal brain sizes.

We have added Insc>mCherry RNAi as a reference in Figure 6A-D, which showed that the brain size of tumor model is larger than normal brain. Moreover, we removed brat RNAi data from Figure 6A-D to Figure 6—figure supplement 1A-D for the better layout.

In Figures 6B, D, “Tumor size” should be corrected to “Larval brain volume”.

Here, we measured the brain area to assess the severity of the tumor via ImageJ instead of 3D data of the brain volume. So we think it would be more appropriate to use the “Larval brain size” than “Larval brain volume” here. Thus, we have corrected “Tumor size” to “Larval brain size” in Figure 6B and D to Figure 6—figure supplement 1B and D.

Considering that asymmetric division defects in NBs may lead to premature differentiation, it is advisable to explore the potential involvement of ferritin in asymmetric division.

aPKC is a classic marker to determine the asymmetric division defect of NB. We performed the aPKC staining and found it displayed a crescent at the apical cortex based on the daughter cell position whether in control or glial ferritin knockdown (Figure 5—figure supplement 3A). This result indicated that there was no obvious asymmetric defect after glial ferritin knockdown.

In the statement "Secondly, we examined the apoptosis in glial cells via Caspase-3 or TUNEL staining, and found the apoptotic signal remained unchanged after glial ferritin knockdown (Figure 3-figure supplement 3A-D).", replace "the apoptosis in glial cells" with "the apoptosis in larval brain cells".

We have replaced "the apoptosis in glial cells" with "the apoptosis in larval brain cells" in line 216.

Include a discussion on the involvement of ferritin in mammalian brain development and address the limitations associated with considering ferritin as a potential target for tumor suppression.

We have added the discussion about ferritin in mammalian brain development in line 428-430 and limitation of ferritin for suppressing tumor in line 441-444.

Indicate Insc-GAL4 as BDSC#8751, even if obtained from another source. Additionally, provide information on the extensively used DeRed fly stock used in this study within the methods section.

We provided the stock information of Insc-GAL4 and DsRed in line 673-674.

Reviewer #2 (Recommendations For The Authors):

Major points:

The number of NBs differs a lot between experiments. For example, in Fig 1B and 1K controls present less than 100 NBs whereas in Figure 1 Supplementary 2B it can be seen that controls have more than 150. Then, depending on which control you compare the number of NBs in flies silencing Fer1HCH or Fer2LCH, the results might change. The authors should explain this.

Figure 1 Supplementary 2B (Figure 1 Supplementary 3B in the revised version) shows NB number in VNC region while Fig 1B and 1K show NB number in CB region. At first, we described the general phenotype showing the NB number in CB and VNC respectively (Fig 1 and Fig 1-Supplementary 1 and 3 in the revised version). And the NB number is consistent in each region. After then, we focused on NB number in CB for the convenience.

This reviewer encourages the authors to use better Gal4 lines to describe the expression patterns of ferritins and Zip13 in the developing brain. On the one hand, the authors do not state which lines they are using (including supplementary table). On the other hand, new Trojan GAL4 (or at least InSite GAL4) lines are a much better tool than classic enhancer trap lines. The authors should perform this experiment.

All stock source and number were documented in Table 2. Ferritin GAL4 and Zip13 GAL4 in this study are InSite GAL4. In addition, we also used another Fer2LCH enhancer trapped GAL4 to verify our result (DGRC104255) and provided the result in Figure 2—figure supplement 1. Our data showed that DsRed driven by Fer2LCH-GAL4 was co-localized with the glia nuclear protein Repo, instead of the NB nuclear protein Dpn, which was consistent with the result of Fer1HCH/Fer2LCH GAL4. In addition, we will try to obtain the Trojan GAL4 (Fer1HCH/Fer2LCH GAL4 and Zip13 GAL4) and validate this result in the future.

The authors exclude very rapidly the possibility of ferroptosis based only on some mitochondrial morphological features without analysing the other hallmarks of this iron-driven cell death. The authors should at least measure Lipid Peroxidation levels in their experimental scenario either by a kit to quantify by-products of lipid peroxidation such as Malonaldehide (MDA) or using an anti 4-HNE antibody.

We combined multiple experiments to exclude the possibility of ferroptosis. Firstly, ferroptosis can be terminated by iron chelator. And we fed fly with iron chelator upon glial ferritin knockdown, but NB number and proliferation were not restored, which suggested that ferroptosis probably was not the cause of NB loss induced by glial ferritin knockdown (Figure 3B and C). Secondly, Zip13 transports iron into the secretary pathway and further out of the cells in Drosophila gut[8]. Our data showed that knocking down iron transporter Zip13 in glia resulted in the decline of NB number and proliferation, which was consistent with the phenotype upon glial ferritin knockdown (Figure 3E-G). More importantly, the knockdown of Zip13 and ferritin simultaneously aggravated the phenotype in NB number and proliferation (Figure 3E-G). These results suggested that the phenotype was induced by iron deficiency in NB, which excluded the possibility of iron overload or ferroptosis to be the main cause of NB loss upon glial ferritin knockdown. Finally, we observed mitochondrial morphology on double membrane and the cristae that are critical hallmarks of ferroptosis, but found no significant damage (Figure 3-figure supplement 2E and F).

In addition, we have added the 4-HNE determination in Figure 3—figure supplement 2G and H. This result showed that 4-HNE level did not change significantly, suggesting that lipid peroxidation was stable, which supported to exclude the possibility that the ferroptosis led to the NB loss upon glial ferritin knockdown.

All of the above results together indicate that ferroptosis is not the cause of NB loss after ferritin knockdown.

A major flaw of the manuscript is related to the chapter Glial ferritin defects result in impaired Fe-S cluster activity and ATP production and the results displayed in Figure 4. The authors talk about the importance of FeS clusters for energy production in the mitochondria. Surprisingly, the authors do not analyse the genes involved in this process such as but they present the interaction with the cytosolic FeS machinery that has a role in some extramitochondrial proteins but no role in the synthesis of FeS clusters incorporated in the enzymes of the TCA cycle and the respiratory chain. The authors should repeat the experiments incorporating the genes NSF1 (CG12264), ISCU(CG9836), ISD11 (CG3717), and fh (CG8971) or remove (or at least rewrite) this entire section.

Thanks for this constructive advice and we have revised this in Figure 4B and C. We repeated the experiment with blocking mitochondrial Fe-S cluster biosynthesis by knocking down Nfs1 (CG12264), ISCU(CG9836), ISD11 (CG3717), and fh (CG8971), respectively. Nfs1 knockdown in NB led to a low proliferation, which was consistent with CIA knockdown. However, we did not observe the obvious brain defect in ISCU(CG9836), ISD11 (CG3717), and fh (CG8971) knockdown in NB. Our interpretation of these results is that Nfs1 probably is a necessary core component in Fe-S cluster assembly while others are dispensable[9].

The presence and aim of the mouse model Is unclear to this reviewer. On the one hand, It Is not used to corroborate the fly findings regarding iron needs from neuroblasts. On the other hand, and without further explanation, authors migrate from a fly tumor model based on modifying all neuroblasts to a mammalian model based exclusively on a glioma. The authors should clarify those issues.

Although iron transporter probably is different in Drosophila and mammal, iron function is conserved as an essential nutrient for cell growth and proliferation from Drosophila to mammal. The data of fly suggested that iron is critical for brain tumor growth and thus we verified this in mammalian model. Glioma is the most common form of central nervous system neoplasm that originates from neuroglial stem or progenitor cells[10]. Therefore, we validated the effect of iron chelator DFP on glioma in mice and found that DFP could suppress the glioma growth and further prolong the survival of tumor-bearing mice.

Minor points

Although referred to adult flies, the authors did not include either in the introduction or in the discussion existing literature about expression of ferritins in glia or alterations of iron metabolism in fly glia cells (PMID: 21440626 and 25841783, respectively) or usage of the iron chelator DFP in drosophila (PMID: 23542074). The author should check these manuscripts and consider the possibility of incorporating them into their manuscript.

Thanks for your remind. We have incorporated all recommended papers into our manuscript line 65-67 and 168.

The number of experiments in each figure is missing.

All experiments were repeated at least three times. And we revised this in Quantifications and Statistical Analysis of Materials and methods.

If graphs are expressed as mean +/- sem, it is difficult to understand the significance stated by the authors in Figure 2E.

We apologize for this mistake and have revised this in Quantifications and Statistical Analysis. All statistical results were presented as means ± SD.

When authors measure aconitase activity, are they measuring all (cytosolic and mitochondrial) or only one of them? This is important to better understand the experiments done by the authors to describe any mitochondrial contribution (see above in major points).

In this experiment, we were measuring the total aconitase activity. We also tried to determine mitochondrial aconitase but it failed, which was possibly ascribed to low biomass of tissue sample.

In this line, why do controls in aconitase and atp lack an error bar? Are the statistical tests applied the correct ones? It is not the same to have paired or unpaired observations.

It is the normalization. We repeated these experiments at least three times in different weeks respectively, because the whole process was time-consuming and energy-consuming including the collection of brains, protein determination and ATP or aconitase determination. And the efficiency of aconitase or ATP kit changed with time. We cannot control the experiment condition identically in different batches. Therefore, we performed normalization every time to present the more accurate result. The control group was normalized as 1 via dividing into itself and other groups were divided by the control. This normalized process was repeated three times. Therefore, there is no error bar in the control group. We think it is appropriate to apply ANOVA with a Bonferroni test in the three groups.

In some cases, further rescue experiments would be appreciated. For example, expression of Ndi restores control NAD+ levels or number of NBs, it would be interesting to know if this is accompanied by restoring mitochondrial integrity and its ability to produce ATP.

We have determined ATP production after overexpressing Ndi1 and provided this result in Figure 4—figure supplement 1B. The data showed that expression of Ndi1 could restore ATP production upon glial Fer2LCH knockdown, which was consistent with our conclusion.

Lines 293-299 on page 7 are difficult to understand.

According to our above results, the decrease of NB number and proliferation upon glial ferritin knockdown (KD) was caused by energy deficiency. As shown in the schematic diagram (Author response image 1), “T” represented the total energy which was used for NB maintenance and proliferation. “N” indicated the energy for maintaining NB number. “P” indicated the energy for NB proliferation. “T” is equal to “N” plus “P”. When ferritin was knocked down in glia, “T”, “N” and “P” declined in “Ferritin KD” compared to “wildtype (WT)”. Knockdown of pros can prevent the differentiation of NB, but it cannot supply the energy for NB, which probably results in the rescue of NB number but not proliferation. Specifically, NB number increased significantly in “Ferritin KD Pros KD” compared to “Ferritin KD”, which resulted in consuming more energy for NB maintenance in “Ferritin KD Pros KD”. As shown in the schematic diagram, “T” was not changed between “Ferritin KD Pros KD” and “Ferritin KD”, whereas ”N” was increased in “Ferritin KD Pros KD” compared to “Ferritin KD”. Thus, “P” was decreased, which suggested that less energy was remained for proliferation, leading to the failure of rescue in NB proliferation. It seemed that the level of proliferation in “Ferritin KD Pros KD” was even lower than “Ferritin KD”.

Author response image 1.

The schematic diagram of relationship between energy and NB function in different groups. “T” represents total energy for NB maintenance and proliferation. “N” represents the energy for NB maintenance. “P” represents the energy for NB proliferation. T=N+P 

Line 601 should indicate that Tables 2 and 3 are part of the supplementary material.

We have revised this in line 678.

Figure 4-supplement 1. Only validation of 2 genes from a RNAseq seems too little.

We dissected hundreds of brains for sorting NBs because of low biomass of fly brain. This is a difficult and energy-consuming work. Most NBs were used for RNA-seq, so we can only use a small amount of sample left for validation which is not enough for more genes.

Figure 6E, the authors indicate that 10 mg/ml DFP injection could significantly prolong the survival time. Which increase in % is produced by DFP?

We have provided the bar graph in Author response image 2. The increase is about 16.67% by DFP injection.

Author response image 2.

The bar graph of survival time of mice treated with DFP. (The unpaired two-sided Student’s t test was employed to assess statistical significance. Statistical results were presented as means ± SD. n=7,6; *: p<0.05)

Reviewer #3 (Recommendations For The Authors):

As I read the initial results that built the story (glia make ferritin>release it> NBs take them up>use it for TCA and ETC) I kept thinking about what it meant for NBs to be 'lost'. This led me to consider alternate possibilities that the results might point to, other than the ones the authors were suggesting. It was only in Figure 5 that the authors ruled out some of those possibilities. I would suggest that they first illustrate how NBs are lost upon glial ferritin loss of function before they delve into the mechanism. This would also be a place to similarly address that glial numbers and general morphology are unchanged upon ferritin loss.

This recommendation provides a valuable guideline to build this story especially for researchers who are interested in neural stem cell studies. Actually, we tried this logic to present our study but found that there are several gaps in the middle of the manuscript, such as the relationship between glial ferritin and Pros localization in NB, so that the whole story cannot be fluently presented. Therefore, we decided to present this study in the current way.

More details of the screen would be useful to know. How many lines did they screen, what was the assay? This is not mentioned anywhere in the text.

We have added this in Screen of Materials and methods. We screened about 200 lines which are components of classical signaling pathways, highly expressed genes in glial cells or secretory protein encoding genes. UAS-RNAi lines were crossed with repo-Gal4, and then third-instar larvae of F1 were dissected. We got the brains from F1 larvae and performed immunostaining with Dpn and PH3. Finally, we observed the brain in Confocal Microscope.

Many graphs seem to be repeated in the main figures and the supplementary data. This is unnecessary, or at least should be mentioned.

We appreciate your kind reminder. However, we carefully went through all the figures and did not find the repeated graphs, though some of them look similar.

The authors mention that they tested which glial subtypes ferritin is needed in, but don't show the data. Could they please show the data? Same with the other iron transport/storage/regulation. Also, in both this and later sections, the authors could mention which Gal4 was used to label what cell types. The assumption is that the reader will know this information.

We have added the result of ferritin knockdown in glial subpopulations in Figure 1—figure supplement 2. However, considering that the quantity of iron-related genes, we did not take the picture, but we recorded this in Table 3.

For all their images showing colocalisation, magnified, single-colour images shown in grayscale will be useful. For example, without the magnification, it is not possible to see the NB expression of the protein trap line in Figure 2B. A magnified crop of a few NBs (not a single one like in 2C) would be more useful.

We have provided Figure 2A’, B’, D’ and Figure 3D’ as suggested.

There are a lot of very specific assays used to detect ROS, NAD, aconitase activity, among others. It would be nice to have a brief but clear description of how they work in the main text. I found myself having to refer to other sources to understand them. (I believe SoNAR should be attributed to Zhao et al 206 and not Bonnay et al 2020.)

We have added a brief description about ROS, aconitase activity, NAD in line 198-199, 229-231, and 269 as suggested.

I did not understand the normalisation done with respect to SoNAR. Is this standard practice? Is the assumption that 'overall protein levels will be higher in slowly proliferating NBs' reasonable? This is why they state the need to normalise.

The SoNAR normalization is not a standard practice. However, we think that our normalization of SoNar is reasonable. According to our results, the expression level of Dpn and Mira seemed higher in glial ferritin knockdown, so we speculated that some proteins accumulated in slowly proliferating NBs. Thus, we used Insc-GAL4 to drive DsRed for indicating the expression level of Insc and found that DsRed rose after glial ferritin knockdown, suggesting that Insc expression was increased indeed. Therefore, we have to normalize SoNar driven by Insc-GAL4 based on DsRed driven by Insc-Gal4, which eliminates the effect of increased Insc upon glial ferritin knockdown.

FAC is mentioned as a chelator? But the authors seem to use it oppositely. Is there an error?

FAC is a type of iron salt, which is used to supply iron. We have also indicated that in line 156 according to your advice. 

The lack of any cell death in the L3 brain surprised me. There should be plenty of hemilineages that die, as do many NBs, particularly in the abdominal segments. Is the stain working? Related to this, P35 is not the best method for rescuing cell death. H99 might be a better way to go.

We were also surprised to see this result and repeated this experiment for several times with both negative and positive controls. Moreover, we also used TUNEL to validate this result, which led to the same result. We will try to use H99 to rescue NB loss in the future, because it needs to be integrated and recombined with our current genetic tools.

It would be nice to see the aconitase activity signal as opposed to just the quantification.

This method can only determine the absorbance for indicating aconitase activity, so our result is just the quantification.

Glia are born after NBs are specified. In fact, they arise from NBs (and glioblasts). So, it's unlikely that the knockdown of ferritin in glia can at all affect initial NB specification.

We completely agree with this statement.

The section on tumor suppression seems out of place. The fly data on which the authors base this as an angle to chase is weak. Dividing cells will be impaired if they have inadequate energy production. As a therapeutic, this will affect every cell in the body. I'm not sure that cancer therapeutics is pursuing such broadly acting lines of therapies anymore.

Our data suggested that iron/ferritin is more critical for high proliferative cells. Tumor cells have a high expression of TfR (Transferrin Receptor)[11], which can bind to Transferrin and ferritin[12]. And ferritin specifically targets on the tumor cells[11]. Thus, we think iron/ferritin is extremely essential for tumor cells. If we can find the appropriate dose of iron/ferritin inhibitor, suppressing tumor growth but maintaining normal cell growth, iron/ferritin might be an effective target of tumor treatment.

The feedback from NB to glial ferritin is also weak data. The increased cell numbers (of unknown identity) could well be contributing to the increase in ferritin. I would omit the last two sections from the MS.

In brat RNAi and numb RNAi, increased cells are NB-like cells, which cannot undergo further differentiation and are not expected to produce ferritin. More importantly, we used Repo (glia marker) as the reference and quantified the ratio of ferritin level to Repo level, which can exclude the possibility that increased glial cells lead to the increase in ferritin.

References

(1) Tanimura T, Isono K, Takamura T, et al. Genetic Dimorphism in the Taste Sensitivity to Trehalose in Drosophila-Melanogaster. J Comp Physiol, 1982,147(4):433-7

(2) Myster DL, Duronio RJ. Cell cycle: To differentiate or not to differentiate? Current Biology, 2000,10(8):R302-R4

(3) Dalton S. Linking the Cell Cycle to Cell Fate Decisions. Trends in Cell Biology, 2015,25(10):592-600

(4) Nichol H, Law JH, Winzerling JJ. Iron metabolism in insects. Annu Rev Entomol, 2002,47:535-59

(5) Pham DQ, Winzerling JJ. Insect ferritins: Typical or atypical? Biochim Biophys Acta, 2010,1800(8):824-33

(6) Speder P, Brand AH. Systemic and local cues drive neural stem cell niche remodelling during neurogenesis in Drosophila. Elife, 2018,7

(7) Mumbauer S, Pascual J, Kolotuev I, et al. Ferritin heavy chain protects the developing wing from reactive oxygen species and ferroptosis. PLoS Genet, 2019,15(9):e1008396

(8) Xiao G, Wan Z, Fan Q, et al. The metal transporter ZIP13 supplies iron into the secretory pathway in Drosophila melanogaster. Elife, 2014,3:e03191

(9) Marelja Z, Leimkühler S, Missirlis F. Iron Sulfur and Molybdenum Cofactor Enzymes Regulate the  Life Cycle by Controlling Cell Metabolism. Front Physiol, 2018,9

(10) Morgan LL. The epidemiology of glioma in adults: a "state of the science" review. Neuro-Oncology, 2015,17(4):623-4

(11) Fan K, Cao C, Pan Y, et al. Magnetoferritin nanoparticles for targeting and visualizing tumour tissues. Nat Nanotechnol, 2012,7(7):459-64

(12) Li L, Fang CJ, Ryan JC, et al. Binding and uptake of H-ferritin are mediated by human transferrin receptor-1. Proc Natl Acad Sci U S A, 2010,107(8):3505-10

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The propagation of electrical signals within neuronal circuits is tightly regulated by the physical and molecular properties of neurons. Since neurons vary in size across species, the question arises whether propagation speed also varies to compensate for it. The present article compares numerous speed-related properties in human and rat neurons. They found that the larger size of human neurons seems to be compensated by a faster propagation within dendrites but not the axons of these neurons. The faster dendritic signal propagation was found to arise from wider dendritic diameters and greater conductance load in human neurons. In addition, the article provides a careful characterization of human dendrites and axons, as the field has only recently begun to characterize post-operative human cells. There are only a few studies reporting dendritic properties and these are not all consistent, hence there is the added value of reporting these findings, particularly given that the characterization is condensed in a compartmental model.

Strengths:

The study was performed with great care using standard techniques in slice electrophysiology (pharmacological manipulation with somatic patch-clamp) as well as some challenging ones (axonal and dendritic patch-clamp). Modeling was used to parse out the role of different features in regulating dendritic propagation speed. The finding that propagation speed varies across species is novel as previous studies did not find a large change in membrane time constant or axonal diameters (a significant parameter affecting speed). A number of possible, yet less likely factors were carefully tested (Ih, membrane capacitance). The main features outlined here are well-known to regulate speed in neuronal processes. The modeling was also carefully done to verify that the magnitude of the effects is consistent with the difference in biophysical properties. Hence, the findings appear very solid to me.

Weaknesses:

The role of diameter in regulating propagation speed is well-known in the axon literature.

We thank the reviewer for this comment. This is indeed true. The paper does not claim that this is new – we just refereed to Waxman’s book to acknowledge this established effect. Our main emphasize is on the impact of dendritic (rather than axonal) diameter – highlighting the faster EPSP speed near the input synapse and converging to steady-state value further away from the soma and using this to explore the impact of differences in dendritic diameter of rat vs. human on EPSP latency and velocity. We now made this point clearer in the revised text.

Reviewer #2 (Public Review):

Summary:

In this paper, Oláh and colleagues introduce new research data on the cellular and biophysical elements involved in transmission within the pyramidal circuits of the human neocortex. They gathered a comprehensive set of patch-clamp recordings from human and rat pyramidal neurons to compare how the temporal aspect of neuronal processing is maintained in the larger human neocortex. A broad range of experimental, theoretical, and computational methods are used, including two-photon guided dual whole-cell recordings, electron microscopy, and computational simulations of reconstructed neurons.

Recordings from synaptically connected pyramidal neurons revealed longer intercellular path lengths within the human neocortex. Further, by using dual whole-cell recordings from somadendrite and soma-axon locations, they found that short latencies from soma to soma can be partly attributed to an increased propagation speed for synaptic potentials, but not for the propagation of action potentials along the axon.

Next, in a series of extensive computational modeling studies focusing on the synaptic potentials, the authors observe that the short-latency within large human pyramidal neural circuits may have a passive origin. For a wide array of local synaptic input sites, the authors show that the conductance load of the dendrites, electrically coupled to a large diameter apical dendrite, affects the cable properties. The result is a relatively faster propagation of EPSPs in the human neuron.

The manuscript is well-written and the physiological experiments and biophysical arguments are very well explained. I appreciated the in-depth theoretical steps for the simulations. That passive cable properties of the dendrites are causing a higher velocity in human dendrites is interesting but there is a disconnect between the experimental findings and the model simulations. Based on the present data the contribution of active membrane properties cannot be dismissed and deserves further experiments.

See our response below

Strengths:

The authors present state-of-the-art 2P-guided dual whole-cell recordings in human neurons. In combination with detailed reconstructions, these approaches represent the next steps in unravelling the information processing in human circuits.

The computational modeling based on cable theory and experimentally constrained simulations provides an excellent integrated view of the passive membrane properties.

Weaknesses:

There are smaller and larger issues with the statistical analyses of the experimental data which muddles the interim conclusions.

That the cable properties alone are the main explanation for speeding the electrical signaling in human pyramidal neurons appears inconsistent with the experimental data.

This is an excellent point – we indeed performed analysis on only passive cases – highlighting (and now also ranking) the impact of the various morpho-electrical properties of the neurons on the differences in signal latency in human vs. rats. We did explored (not shown) the effect of active channels in the dendrites (including the h-current); as expected the results strongly depend on channel density and their spatial distribution over the dendritic tree. As we do not know these parameters for the modelled cells, we decided to remain focus on the impact of passive/morphological parameters. We also note that the experimental results (page 4-5 in manuscript) show minor contribution of h-current emphasizing that the passive properties have the main role in differentiating human and rats. differences between human and rat. 

Some of the electrophysiological experiments require further control experiments to make robust conclusions.

Reviewer #3 (Public Review):

Summary:

This study indicates that connections across human cortical pyramidal cells have identical latencies despite a larger mean dendritic and axonal length between somas in the human cortex. A precise demonstration combining detailed electrophysiology and modeling indicates that this property is due to faster propagation of signals in proximal human dendrites. This faster propagation is itself due to a slightly thicker dendrite, a larger capacitive load, and stronger hyperpolarizing currents. Hence, the biophysical properties of human pyramidal cells are adapted such that they do not compromise information transfer speed.

Strengths:

The manuscript is clear and very detailed. The authors have experimentally verified a large number of aspects that could affect propagation speed and have pinpointed the most important one. This paper provides an excellent comparison of biophysical properties between rat and human pyramidal cells. Thanks to this approach a comprehensive description of the mechanisms underlying the acceleration of propagation in human dendrite is provided.

Weaknesses:

Several aspects having an impact on propagation speed are highlighted (dendritic diameter, ionic channels, capacitive load) and there is no clear ranking of their impact on signal propagation speed. It seems that the capacitive load plays a major role, much more than dendritic diameter for which only a 10% increase is observed across species. Both aspects actually indicate that there is an increase in passive signal propagation speed with bigger cells at least close to the soma. This suggests that bigger cells are mechanically more rapid. An intuitive reason why capacitive load increases speed would also help the reader follow the demonstration.

We thank the referee for both these excellent points. In response to them:

(i) We now performed a new comprehensive statistical analysis and show the ranking of the effect of the different morphological/cable factors on EPSP propagation. This analysis appears in both Supp. Table 5& 6, Fig. S16 and also in the main text as follows:

To rank the impact of the various factors affecting EPSP propagation latency in human and rat neurons, we conducted a comprehensive statistical analysis using two complementary approaches: the generalized linear model (GLM) (Kiebel & Holmes, 2007) as well as SHAP (SHapley Additive exPlanations) (Lundberg & Lee, 2017) based on fitting Gradient Tree Boosting  (Friedman, 2002)model. We began by fitting a GLM without interaction terms among the factors affecting EPSP latency (Suppl. Table 5). This enables us to quantify the primary individual factors affecting EPSP propagation. Our analysis revealed the following ranking order: 1) physical distance of synapses from soma had the strongest effect; 2) species differences; 3) conductance load, as demonstrated by our “hybrid cells” manipulation; 4) radii of the apical dendrite, affecting the cables’ space constant, λ; and 5) the specific cable parameters, as revealed when using per-cell fitted parameters versus uniform cable parameters, was minimal. We next performed GLM analysis with interaction terms showing that, as expected, there are significant interactions between the factors affecting EPSP latency (Suppl. Table 6). To further validate the above ranking while incorporating the interactions between the various factors affecting EPSP latency, we performed a SHAP analysis. Notably, even with interactions included, the ranking of the factors affecting signal propagation are aligned with the results from the analysis based on the GLM without interaction terms (see Fig S.16).

(ii) As for the intuitive explanation required by the referee. We added the following paragraph In the Discussion:

The intuitive reason for this enhancement is that the large conductance load (the “leaky end” boundary conditions) more effectively “steals” the synaptic (axial) current (like water pouring faster into a large pool). The more mathematical intuition is that the large soma (sink) adds fast time constants to the system (see also related explanation in Fig. 4 in Eyal et al., 2014).

We thank the editors for considering and revising our manuscript for publication in eLife. We appreciate the positive appreciation of the work and the critical points raised by the reviewers. We have responded in detail to all the excellent comments from all reviewers. We believe that these revisions have significantly improved the quality of our study.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

There are two points that could improve the reading experience of this nice manuscript. These should be easily addressed with minor re-phrasing.

Credit to conduction velocity literature. Less widely known in the dendrite literature, in the axon literature, the relationship between propagation speed and process diameter is well established. I thought the two articles cited (Jack Noble Tsien and Agmon-Snir & Segev) were not as direct in the treatment of this relationship. The work of Stephen Waxman, for instance, made clear how axon diameter tightly controls propagation speed (see for instance the Scholarpedia entry by Swadlow and Waxman). In my opinion, this is a widely known piece of work, that is part of some introductory books to neuroscience. While the article does not claim they found this relationship, parts of the presentation are better understood if we ignore this well-known fact. I am referring to the abstract, intro, and the beginning of results where 'larger' is presented as synonymous with 'slower'. For instance 'to compensate for the increase neurons' size' (abstract) or 'the increase in size of dendrites and axons might come with a cost of longer signal propagation times' only makes sense if 'size' refers to spatial extent, not diameter.

We thank for this valid point; leaving out axon diameter references was not intentional. We have now added the suggested reference to our manuscript. In the size comparisons, we have only pointed out the obvious size differences between the body and the dendritic processes. We have reworded sentences with size comparisons.

In Abstract (lines 1-6):

Human-specific cognitive abilities depend on information processing in the cerebral cortex, where neurons are significantly larger, their processes are longer and sparser compared to rodents. We found that, in synaptically-connected layer 2/3 pyramidal cells (L2/3 PCs), soma-tosoma signal propagation delay is similar in humans and rodents. Thus, to compensate for the increase in neurons’s longer processes, membrane potential changes must propagate faster in human axons and/or dendrites.

In section “Effect of dendritic thickness” in Results we have modified it as follows:

The relationship between conduction velocity and axon diameter is well known for small myelinated and unmyelinated axons (Waxman and Bennett, 1972). Anatomical features of neuronal processes dendrites also have a major influence on signal propagation properties 5,19, thus …

Waxman, S. G. and Bennett, M. V. L. Relative conduction velocity of small myelinated and nonmyelinated fibres in the central nervous system. Nature New Biol., 238217-219, 1972.

Two or four dendritic factors? The study identifies two major dendritic factors influencing the propagation speed (diameter and load), however the end of the results highlights four factors. I did not understand how factor 2 was different than factor 1. Neither did I understand how factor 4 was different from the other factors. There seemed to be a little redundancy here that could be streamlined.

We thank the reviewer for pointing this out. We now have changes the respective text, added the ranking statistics (see above) to assess the effect of the different parameters on signal propagation in dendrites.

Microcircuits? The study found that the changes in speed arise from the dendrites rather than the axons, as such it seems it would be more precise to replace 'microcircuits' with 'dendrites'.

We are thankful for this suggestion. We change the title to Accelerated signal propagation speed in human neocortical dendrites.

Typos

P3 line 24 'find significant difference the propagation'.

P6 line 35 'how morphological differences' it would be useful to specify which morphological difference here.

Corrected.

Reviewer #2 (Recommendations For The Authors):

(1) The statistical analyses should be changed. T-testing populations and comparing visual differences of differences ("human minus rats") is a common but egregious error in the field of neurosciences (see doi:10.1038/nn.2886). The conclusion that HCN channels "... do not by themselves explained the differences between the two species" (lines 174-176) is not compelling. The design of the experiments presented in Figure 3 is paired recordings and the addition of a blocker (ZD7288 or TTX cocktail). These are classic 2 x 2 factorial designs (species x drug). The authors will need to perform a repeated-measured analysis of variance (RM-ANOVA) and provide information on the interaction significance. Please revise the figures and improve statistical reporting. Post-hoc comparisons of the velocity populations are required to support the idea of whether h-channels are explaining the observed differences.

Thank you for drawing our attention to this error. The statistical analysis of the pharmacological experiments was re-performed as suggested. After the 2-way ANOVA with repeated measures and Bonferroni post-hoc correction, we can indeed find significant differences only in the control group, namely that the propagation speed of bAPs in human dendrites was significantly higher. The implementation of the proposed statistical analysis demonstrates that the administration of ZD has no statistically significant effect on the propagation speed of human or rat dendrites. The treatment with TTX cocktail resulted in a significant difference in signal propagation in humans but not in rodents. However the trend is discernible and the P = 0.0588 value is close to the widely accepted 0.05 threshold. After the TTX cocktail treatment, the speed of signal propagation did not differ significantly between the two species. However, on average, the human dendrites remained faster. These alterations in P-values do not affect our primary conclusions. The MS text has been modified accordingly.

(2) Although ZD7288, in my opinion, influences the bAP (see point #1) the authors subsequently leave the h-current unblocked in the experiments in Figures 3D, E. Here, they use sodium, potassium, and calcium currents as well as synaptic conductances. I am puzzled why (in line 188) they claim the dendrites are "passive" although the data show h-currents are contributing to the shape of the bAP in human neurons. In line 196 they conclude voltage-gated conductances have a "minor" contribution and passive properties a main role. Please revise conclusions or provide better experimental support.

Thank you for this point. We meant to refer to the state in which no action potential can be generated, although the word 'passive' might be misleading in this context; we rephrase these sentences in the MS accordingly.

(3) A major concern is the injection of an AP in voltage-clamp mode. Although this is the right choice and I'm in support of the experiment, it is technically challenging to space clamp the soma and fully recapitulate the speed and amplitude of a 100 mV depolarization. The voltage drop in peak amplitude as well as the increased delay between the baseline AP (current clamp) and AP in blocker conditions (voltage clamp) could be fully explained by switching between current- and voltage-clamp modes. In additional control experiments, the authors should add a second voltage follower electrode (CC) at the soma showing whether the authors can preserve the original AP (from CC) in VC/blocker condition. It may well be they need to adjust the injection protocol.

Our experiments were designed to replicate the work of Stuart et al. (1994), in which they compared the attenuation of active and passive backpropagating signals. When they blocked Na+ channels with TTX they injected simulated action potentials in voltage-clamp mode. They concluded that TTX-sensitive Na+ channels cause somatic action potential entry into the dendritic compartment. They found a comparable attenuation of the backward propagating action potential in the dendrites in control conditions (~70 %). 

We performed control recordings based on the reviewer’s suggestion (Author response image 1).

Author response image 1.

Injection of the previously recorded AP (blue) in VC mode produced a completely similar somatic AP in CC mode (orange). The slight temporal delay between the two signal caused by the different position of the pipettes on the cell body.  The right panel shows the plot of the two peak-aligned APs as a function of each other, close to the blue ‘equality’ line. We concluded that the original AP is well preserved in VC/blocker condition.

(5) From the paragraph entitled "Modeling EPSP propagation in dendrites" and onwards the authors make countless conclusions based on theory and modelling results but without any statistical support. Multiple neurons are used thus it is rather straightforward to provide numerical support for the assertions. For example, but this is not an exhaustive list, how should we interpret that latency ranges are different (line 240, line 253) etc.? Or were the estimated Cm values of human and rat neurons (0.6 versus 1.1) significantly different? And if so, how does this align with the Cm estimates in the nucleated patch experiments?

We thank the referee for this comment and now added a set of statistical analyses. The results appear now throughout the whole theoretical paper in revised article. In particular with respect to Figs. 6&7 where we now show that, indeed, our various manipulations (e.g., hybrid vs. original cells) as well as the cable parameters (Cm, Rm) are indeed significantly different between human and rats whereas the membrane time constant is not significantly different between human and rat. As for Cm in human. Our limited sample size shows significant difference between human and rat. Yet, the range of values for Cm that we found in our modeling study does fall within the experimental range reported in the present study.

Minor

Line 44. The "simulated EPSP" example in Figure 2C is not a command waveform for an EPSC. Line 526 in the methods states that also ramp currents were used. Please revise to clarify the main text.

Thank you for bringing this discrepancy to our attention. In the experiments, we used ramp injections. We have made this clear in the main text as follows: ”... we tested orthodromic or forward propagating signal propagation velocity by injecting short-duration current ramps to simulate EPSP (sEPSP) signals in the dendrites and recorded the resultant subthreshold voltage response in the soma”

Line 522. The authors state the recordings were all carried out "in current clamp mode" but detailed VC method information is lacking. Did they use series resistance compensation?

We did not use series resistance compensation.

Line 479 From which region(s) where human "neocortical slices" sampled? Please add this information.

We have added regions of origin to the Methods section: frontal (n = 21), temporal (n = 20), parietal (n = 20), and occipital (n = 1).  

Please show higher temporal resolution example traces, for example in Figure 3. Differences are at the micrometer scale, but APs are shown at the millisecond scale. Hard to judge the quality of the data. Showing the command potentials (inset Figure 3D, E) is misleading (see major point #3).

In response to the reviewer's request, we have redrawn the example traces in Figure 3.

Please check the labeling of figures. There is information missing. For example, in Figure 5 A to C I am missing information and the units of the axes.

In the black plots on the right side of panels B and C, the y-axis shows the thickness measurements for the given dendrite stacked on top of each other and the x-axis shows the measurement values, the units for the x-axis are µm as mentioned in the figure legend.

Line 981 "scalebars" should read scale bars."

Line 986 "bootstraped" should read "bootstrapped".

Done.

Are the dendritic diameters increased for all basal and apical higher-order branches? It is unclear how the model simulations were built on diameters of primary and higher-order branches.

In our modelling study we took the actual diameter of the reconstructed PCs in both proximal and higher order branches. We did compare per-distance differences in diameter – but it is automatically incorporated into the computation of the basal load (“equivalent cables” in Figs 6&8).

The velocity calculation for axonal propagation (yielding a ~0.9 m/s conduction velocity, Figure 2B) is incorrect. Using the peak of the action potentials between soma and axon misses the fact that action potentials start earlier and spatially distally from the soma in the axon. Please revise the calculation to include the temporal delay and actual distance travelled by the forward propagating action potential.

Thank you for this question. We are aware that the AP is generated at the AIS and that it is located between the two recording electrodes and we have to take into account that the signal propagates from the AIS to the soma and this may shorten the delay in the system. To the best of our knowledge, there is no experimental evidence of the location of the AP generation site on the AIS in layer 2-3 pyramidal cells in the human neocortex, so we assumed that it is located 35 microns from the soma, and that the propagation speed from the AIS to the two directions is the same. Consequently, we have corrected our propagation velocity values as follows:

“For the axon bleb recordings we assumed that the axon initial segment (AIS) of the cells are 35 µm from the axon hillock, and the APs propagate to forward (to the bleb) and backward (to the soma) at the same speed. For the correction of the AIS we used the following formula: (2)

where vcorr is the corrected propagation speed for AIS position, l is the axonal distance between the soma and the axon bleb, t is the latency between the two measuring point, ais is the assumed position of the AIS alongside the axon (35 µm).”

What explains the strongly attenuated axonal action potential at the bleb? Is this representative?

The strongly attenuated axonal action potential at the bleb can be explained by a few key factors:

(1) Membrane Integrity: Bleb formation often indicates some level of membrane damage or alteration. This can disrupt the normal ionic gradients across the membrane, leading to a failure in generating or propagating action potentials effectively.

(2) Current Leakage: Bleb formation may create additional pathways for ion leakage, which can dissipate the electrical current that would normally propagate the action potential. This leakage reduces the overall amplitude of the action potential.

Line 275 "To our delight", please rephrase.

Corrected.

Reviewer #3 (Recommendations For The Authors):

- In Figure 1, the number of cells used to assess intersomatic distance is quite low. A larger number of neuron pairs should be analyzed to be more representative. Or at least an explanation of why such a low sampling can be conclusive.

We appreciate the reviewer’s concerns on sample sizes of the first set of experiments, where the anatomical pathways were measured through the synapses of coupled cells with electrophysiological recordings. We acknowledge that this is a limitation of our study. However, in this series of experiments, we simply wanted to experimentally confirm already known results which consisted of two parts: first, that in humans the dendrites and axons of neurons are longer, and second, that they have the same time delay in terms of synaptic latency. 

The reported similarity in synaptic latencies is consistent with the results of a recent study by Campagnola et al. (2022) showing that EPSP latencies of local connections between layer 2/3 pyramidal cells are in the same range in humans and mice (human median latency = 1.73 ms vs. mouse median latency = 1.49 ms). We came to the same conclusion in our previous work where we compared pyramidal basket cell synaptically coupled pairs in human and rat pairs (Molnár et al. 2016). 

On the other hand, we report interspecific differences in cable pathways from soma to soma, again consistent with the literature suggesting that the length of pyramidal neural processes is longer in humans than in rodents (see Supplementary Figure 1 and e.g. Berg et al. 2021).

From a practical point of view the collection of experimental data in this hard won experiment is particularly difficult. The electrophysiological recording of a connected pair with an appropriate pre- and postsynaptic series resistance, where human tissue samples are limited, is the first step here. To obtain information about the path of the signals between pre- and postsynaptic cells, an anatomical reconstruction is required. This requires a) a high-quality recovery of postsynaptic dendrites and presynaptic axons, b) successful tracing of all potential contact points between presynaptic axons and postsynaptic dendrites back to the pre- and postsynaptic soma. The difficulty of the latter point in particular arises from the fact that parts of the presynaptic axonal arbor are myelinated and the success of biocytin-based tracing depends on the length of the myelinated axon branches. The success/failure of complete axonal tracing only becomes apparent at the end of these efforts.

- The author should provide an intuitive explanation of why capacitive load accelerates propagation in the dendrite.

See answer above  

- The author should more clearly rank the contribution of each difference between rat and human neurons. The 10% increase in dendritic diameter which affects velocity only via a square root seems a very weak contribution. This should be clarified.

We now added a set of statistical methods to perform such a ranking in the theoretical part of this study, as described above (and in a new paragraph, attached above) in the revised article. 

References

Eyal, G., Mansvelder, H. D., de Kock, C. P. J., & Segev, I. (2014). Dendrites impact the encoding capabilities of the axon. Journal of Neuroscience, 34(24), 8063–8071. https://doi.org/10.1523/JNEUROSCI.5431-13.2014

Friedman, J. H. (2002). Stochastic gradient boosting. In Computational Statistics & Data Analysis (Vol. 38). www.elsevier.com/locate/csda

Kiebel, S. J., & Holmes, A. P. (2007). The General Linear Model. In K. Friston, J. Ashburner, S. Kiebel, T. Nichols, & P. William (Eds.), Statistical Parametric Mapping (pp. 101–125). Academic Press.

Lundberg, S. M., & Lee, S.-I. (2017). A unified approach to interpreting model predictions. Proceedings of the 31st International Conference on Neural Information Processing Systems, 4768–4777.

Author response:

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

Reviewer #1:

Comment#1: Ren et al developed a novel computational method to investigate cell evolutionary trajectory for scRNA-seq samples. This method, MGPfact, estimates pseudotime and potential branches in the evolutionary path by explicitly modeling the bifurcations in a Gaussian process. They benchmarked this method using synthetic as well as real-world samples and showed superior performance for some of the tasks in cell trajectory analysis. They further demonstrated the utilities of MGPfact using single-cell RNA-seq samples derived from microglia or T cells and showed that it can accurately identify the differentiation timepoint and uncover biologically relevant gene signatures. Overall I think this is a useful new tool that could deliver novel insights for the large body of scRNA-seq data generated in the public domain. The manuscript is written in a logical way and most parts of the method are well described.

Thank you for reviewing our manuscript and for your positive feedback on MGPfact. We are pleased that you find it useful for identifying differentiation timepoints and uncovering gene signatures. We will continue to refine MGPfact and explore its applications across diverse datasets. Your insights are invaluable, and we appreciate your support.

Comment#2: Some parts of the methods are not clear. It should be outlined in detail how pseudo time T is updated in Methods. It is currently unclear either in the description or Algorithm 1.

Thanks to the reviewers' comments. We've added a description of how pseudotime T is obtained between lines 138 and 147 in the article. In brief, the pseudotime of MGPfact is inferred through Gaussian process regression on the downsampled single-cell transcriptomic data. Specifically, T is treated as a continuous variable representing the progression of cells through the differentiation process. We describe the relationship between pseudotime and expression data using the formula:

Where f(T) is a Gaussian Process (GP) with covariance matrix S, and Ɛ represents the error term. The Gaussian process is defined as:

Where is the variance set to 1e-6.

During inference, we update the pseudotime by maximizing the posterior likelihood. Specifically, the posterior distribution of pseudotime T can be represented as:

Where is the likelihood function of the observed data Y*, and is the prior distribution of the Gaussian process. This posterior distribution integrates the observed data with model priors, enabling inference of pseudotime and trajectory simultaneously. Due to the high autocorrelation of  in the posterior distribution, we use Adaptive Metropolis within Gibbs (AMWG) sampling (Roberts and Rosenthal, 2009; Tierney, 1994). Other parameters are estimated using the more efficient SLICE sampling technique (Neal, 2003).

Comment#3: There should be a brief description in the main text of how synthetic data were generated, under what hypothesis, and specifically how bifurcation is embedded in the simulation.

Thank you for the reviewers' comments. We have added descriptions regarding the synthetic dataset in the methods section. The revised content is from line 487 to 493:

“The synthetic datasets were generated using four simulators: dyngen (Saelens et al., 2019), dyntoy (Saelens et al., 2019), PROSSTT (Papadopoulos et al., 2019), and Splatter (Zappia et al., 2017), each modeling different trajectory topologies such as linear, branching, and cyclic. Splatter simulates branching events by setting expression states and transition probabilities, dyntoy generates random expression gradients to reflect dynamic changes, and dyngen focuses on complex branching structures within gene regulatory networks.”

Comment#4: Please explain what the abbreviations mean at their first occurrence.

We appreciate the reviewers' feedback. We have thoroughly reviewed the entire manuscript and made sure that all abbreviations have had their full forms provided upon their first occurrence.

Comment#5: In the benchmark analysis (Figures 2/3), it would be helpful to include a few trajectory plots of the real-world data to visualize the results and to evaluate the accuracy.

We appreciate the reviewer's feedback. To more clearly demonstrate the performance of MGPfact, we selected three representative cases from the dataset for visual comparison. These cases represent different types of trajectory structures: linear, bifurcation, and multifurcation. The revised content is between line 220 and 226.

As shown in Supplementary Fig. 5, it is evident that MGPfact excels in capturing main developmental paths and identifying key bifurcation points. In the linear trajectory structure, MGPfact accurately predicted the linear structure without bifurcation events, showing high consistency with the ground truth (overall\=0.871). In the bifurcation trajectory structure, MGPfact accurately captured the main bifurcation event (overall\=0.636). In the multifurcation trajectory structure, although MGPfact predicted only one bifurcation point, its overall structure remains close to the ground truth, as evidenced by its high overall score (overall\=0.566). Overall, MGPfact demonstrates adaptability and accuracy in reconstructing various types of trajectory structures.

Comment#6: It is not clear how this method selects important genes/features at bifurcation. This should be elaborated on in the main text.

Thanks to the reviewers' comments. To enhance understanding, we've added detailed descriptions of gene selection in the main text and appendix, specifically from lines 150 to 161. In brief, MGPfact employs a Gaussian process mixture model to infer cell fate trajectories and identify independent branching events. We calculate load matrices using formulas 1 and 14 to assess each gene's contribution to the trajectories. Genes with an absolute weight greater than 0.05 are considered predominant in specific branching processes. Subsequently, SCENIC (Aibar et al., 2017; Bravo González-Blas et al., 2023) analysis was conducted to further infer the underlying regulons and annotate the biological processes of these genes.

Comment#7: It is not clear how survival analysis was performed in Figure 5. Specifically, were critical confounders, such as age, clinical stage, and tumor purity controlled?

To evaluate the predictive and prognostic impacts of the selected genes, we utilized the Cox multivariate regression model, where the effects of relevant covariates, including age, clinical stage, and tumor purity, were adjusted. We then conducted the Kaplan-Meier survival analysis again to ensure the reliability of the results. The revisions mainly include the following sections:

(1) We modified the description of adjusting for confounding factors in the survival analysis, from line 637 to 640:

“To adjust for possible confounding effects, the relevant clinical features including age, sex and tumor stage were used as covariates. The Cox regression model was implemented using R-4.2 package “survival”. And we generated Kaplan-Meier survival curves based on different classifiers to illustrate differences in survival time and report the statistical significance based on Log-rank test.”

(2) We updated the images in the main text regarding the survival analysis, including Fig. 5a-b, Fig. 6c, and Supplementary Fig. 8e.

Comment#8: I recommend that the authors perform some sort of 'robustness' analysis for the consensus tree built from the bifurcation Gaussian process. For example, subsample 80% of the cells to see if the bifurcations are similar between each bootstrap.

We appreciate the reviewers' feedback. We performed a robustness analysis of the consensus tree using 100 training datasets. This involved sampling the original data at different proportions, and then calculating the topological similarity between the consensus trajectory predictions of MGPfact and those without sampling, using the Hamming-Ipsen-Mikhailov (HIM ) metric. A higher score indicates greater robustness. The relevant figure is in Supplementary Fig. 4, and the description is in the main text from line 177 to 182.

The results indicate that the consensus trajectory predictions based on various sampling proportions of the original data maintain a high topological similarity with the unsampled results (HIM_mean=0.686). This demonstrates MGPfact’s robustness and generalizability under different data conditions, hence the capability of capturing bifurcative processes in the cells’ trajectory.

Reviewer #2:

Comment#1: The authors present MGPfact^XMBD, a novel model-based manifold-learning framework designed to address the challenges of interpreting complex cellular state spaces from single-cell RNA sequences. To overcome current limitations, MGPfact^XMBD factorizes complex development trajectories into independent bifurcation processes of gene sets, enabling trajectory inference based on relevant features. As a result, it is expected that the method provides a deeper understanding of the biological processes underlying cellular trajectories and their potential determinants. MGPfact^XMBD was tested across 239 datasets, and the method demonstrated similar to slightly superior performance in key quality-control metrics to state-of-the-art methods. When applied to case studies, MGPfact^XMBD successfully identified critical pathways and cell types in microglia development, validating experimentally identified regulons and markers. Additionally, it uncovered evolutionary trajectories of tumor-associated CD8+ T cells, revealing new subtypes with gene expression signatures that predict responses to immune checkpoint inhibitors in independent cohorts. Overall, MGPfact^XMBD represents a relevant tool in manifold learning for scRNA-seq data, enabling feature selection for specific biological processes and enhancing our understanding of the biological determinants of cell fate.

Thank you for your thoughtful review of our manuscript. We are thrilled to hear that you find MGPfact^XMBD beneficial for exploring cellular evolutionary paths in scRNA-seq data. Your insights are invaluable, and we look forward to incorporating them to further enrich our study. Thank you once again for your support and constructive feedback.

Comment#2: How the methods compare with existing Deep Learning based approaches such as TIGON is a question mark. If a comparison would be possible, it should be conducted; if not, it should be clarified why.

We appreciate the reviewer's comments. We have added a comparison with the sctour (Li, 2023) and TIGON methods (Sha, 2024).

It is important to note that the encapsulation and comparison of MGPfact are based on traditional differentiation trajectory construction. Saelens et al. established a systematic evaluation framework that categorizes differentiation trajectory structures into topological subtypes such as linear, bifurcation, multifurcation, graph, and tree, focusing on identifying branching structures in the cell differentiation process (Saelens et al., 2019). The sctour and TIGON methods mentioned by the reviewer are primarily used for estimating RNA velocity, focusing on continuous temporal evolution rather than explicit branching structures, and do not explicitly model branches. Therefore, we considered the predictions of these two methods as linear trajectories and compared them with MGPfact. While scTour explicitly estimates pseudotime, TIGON uses the concept of "growth," which is analogous to pseudotime, so we made the necessary adaptations.

Author response image 1 show that within this framework, compared to scTour (overall_mean=0.448) and TIGON (overall_mean=0.263), MGPfact still maintains a relatively high standard (overall_mean=0.534). This indicates that MGPfact has a significant advantage in accurately capturing branching structures in cell differentiation, especially in applications where explicit modeling of branches is required.

Author response image 1.

Comparison of MGPfact with scTour and TIGON in trajectory inference performance across 239 test datasets. a. Overall scores; b.F1_branches; c.HIM; d. cor_dist; e. wcor_features. All results are color-coded based on the trajectory types, with the black line representing the mean value. The “Overall” assessment is calculated as the geometric mean of all four metrics.

Comment#3: Missing Methods:

- The paper lacks a discussion of Deep Learning approaches for bifurcation analysis. e.g. scTour, Tigon.

- I am missing comments on methods such CellRank, and alternative approaches to delineate a trajectory.

We thank the reviewer for these comments.

(1) As mentioned in response to Comments#2, the scTour and TIGON methods are primarily used for estimating RNA velocity, focusing on continuous temporal evolution rather than explicit branching structures, and they do not explicitly model branches. We consider the predictions of these two methods as linear trajectories and compare them with MGPfact. The relevant description and discussion have been addressed in the response.

(2) We have added a description of RNA velocity estimation methods (scTour, TIGON, CellRank) in the introduction section. The revised content is from line 66 to 71:

“Moreover, recent studies based on RNA velocity has provided insights into cell state transitions. These methods measure RNA synthesis and degradation rates based on the abundance of spliced and unspliced mRNA, such as CellRank (Lange et al., 2022). Nevertheless, current RNA velocity analyses are still unable to resolve cell-fates with complex branching trajectory. Deep learning methods such as scTour (Li, 2023) and TIGON (Sha, 2024) circumvent some of these limitations, offering continuous state assumptions or requiring prior cell sampling information.”

Comment#4: Impact of MURP:

The rationale for using MURP is well-founded, especially for trajectory definition. However, its impact on the final results needs evaluation.

How does the algorithm compare with a random subselection of cells or the entire cell set?

Thank you for the comments. We fully agree that MURP is crucial in trajectory prediction. As a downsampling method, MURP is specifically designed to address noise issues in single-cell data by dividing the data into several subsets, thereby maximizing noise reduction while preserving the main structure of biological variation (Ren et al., 2022). In MGPfact, MURP typically reduces the data to fewer than 100 downsampled points, preserving the core biological structure while lowering computational complexity. To assess MURP's impact, we conducted experiments by randomly selecting 20, 40, 60, 80, and 100 cells for trajectory inference. These results were mapped back to the original data using the KNN graph structure for final predictions, which were then compared with the MURP downsampling results. Supplementary results can be found in Supplementary Fig. 3, with additional descriptions in the main text from line 170 to 176.

The results indicate that trajectory inference using randomly sampled cells has significantly lower prediction accuracy compared to that using MURP. This is particularly evident in branch assignment (F1_branches) and correlation cor_dist, where the average levels decrease by 20.5%-64.9%. In contrast, trajectory predictions using MURP for downsampling show an overall score improvement of 5.31%-185%, further highlighting MURP's role in enhancing trajectory inference within MGPfact.

Comment#5: What is the impact of the number of components selected?

Thank you for the comments. In essence, MGPfact consists of two main steps: 1) trajectory inference; 2) calculation of factorized scores and identification of high-weight genes. After step 1, MGPfact estimates parameters such as pseudotime T and bifurcation points B.  In step 2, we introduce a rotation matrix to obtain factor scores W_l  for each trajectory l by rotating Y*.

For all trajectories,

where e_l  is the error term for the -th trajectory. The number of features in Y* must match the dimensions of the rotation matrix R to ensure the factorized score matrix W contains factor scores for  trajectories, achieving effective feature representation and interpretation in the model.

Additionally, to further illustrate the impact of the number of principal components (PCs) on model performance in step 1, we conducted additional experiments. We used 3 PCs as the default and adjusted the number to evaluate changes from this baseline. As shown in Author response image 2, setting the number of PCs to 1 significantly decreases the overall performance score (overall_mean=0.363), as well as the wcor_features and wcor_dist metrics.  In contrast, increasing the number of PCs does not significantly affect the metrics. It ought to be mentioned that number of components used should be determined by the intrinsic biological characteristics of the cell fate-determination. Our experiment based on a limited number of datasets may not represent more complex scenarios in other cell types.

Author response image 2.

Robustness testing of the number of MURP PCA components on 100 training datasets. With the number of principal components (PCs) set to 3 by default; we tested the impact of different number of components (1-10) on the prediction results. In all box plots, the asterisk represents the mean value, while the whiskers extend to the farthest data points within 1.5 times the interquartile range. Significance is denoted as follows: not annotated indicates non-significant; * P < 0.05; ** P < 0.01; *** P < 0.001; two-sided paired Student’s T-tests.

Comment#6: Please comment on the selection of the kernel functions (rbf and polynomial) and explain why other options were discarded.

Thank you for the comments. We have added a description regarding the selection of radial basis functions and polynomial kernels in lines 126-130. As the reviewers mentioned, the choice of kernel functions is crucial in the MGPfact analysis pipeline for constructing the covariance matrix of the Gaussian process. We selected the radial basis function (RBF) kernel and the polynomial kernel to balance capturing data complexity and computational efficiency. The RBF kernel is chosen for its ability to effectively model smooth functions and capture local variations in the data, making it well-suited to the continuous and smooth characteristics of biological processes; its hyperparameters offer modeling flexibility. The polynomial kernel is used to capture more complex nonlinear relationships between input features, with its hyperparameters also allowing further customization of the model. In contrast, other complex kernels, such as Matérn or spectral kernels, were omitted due to their interpretability challenges and the risk of overfitting with limited data. However, as suggested by the reviewers, we will consider and test the impact of other kernel functions on the covariance matrix of the Gaussian process and their role in trajectory inference in our subsequent phases of algorithm design.

Comment#7: What is the impact of the Pseudotime method used initially? This section should be expanded with clear details on the techniques and parameters used in each analysis.

We are sorry for the confusion. We've added a description of how pseudotime T is obtained between line 138 and 147 in the main text. And the specific hyperparameters involved in the model and their prior settings are detailed in the supplementary information.

In brief, the pseudotime and related topological parameters of the bifurcative trajectories in MGPfact are inferred by Gaussian process regression from downsampled single-cell transcriptomic data (MURP). Specifically, T is treated as a continuous variable representing the progression of cells through the differentiation process. We describe the relationship between pseudotime and expression data as:

where f(T) is a Gaussian Process (GP) with covariance matrix S, and ε represents the error term. The Gaussian process is defined as:

where  is the variance set to 1e-6. During inference, we update the pseudotime by maximizing the posterior liklihood. Specifically, the posterior distribution of pseudotime is obtained by combining the observed data Y* with the prior distribution of the Gaussian process model.

We use the Markov Chain Monte Carlo method for parameter estimation, particularly employing the adaptive Metropolis-within-Gibbs (AMWG) sampling to handle the high autocorrelation of pseudotime.

Comment#8: Enhancing Readability: For clarity, provide intuitive descriptions of each evaluation function used in simulated and real data. The novel methodology performs well for some metrics but less so for others. A clear understanding of these measurements is essential.

To address the concern of readability, we have added descriptions of 5 evaluation metrics in the methodology section (Benchmarking MGPfact to state-of-the-art methods) in line 494 to 515. Additionally, we have included a summary and discussion of these metrics in the conclusion section in line 214-240 to help the readers better understand the significance and impact of these measurements.

(1) In brief, the Hamming-Ipsen-Mikhailov (HIM) distance measures the similarity between topological structures, combining the normalized Hamming distance and the Ipsen-Mikhailov distance, which focus on edge length differences and degree distribution similarity, respectively. The F1_branches is used to assess the accuracy of a model's branch assignment via Jaccard similarity between branch pairs. In trajectory inference, cor_dist quantifies the similarity of inter-cell distances between predicted and true trajectories, evaluating the accuracy of cell ordering. The wcor_features assesses the similarity of key features through weighted Pearson correlation, capturing biological variation. The Overall score is calculated as the geometric mean of these metrics, providing an assessment of overall performance.

(2) For MGPfact and the other seven methods included in the comparison, each has its own focus. MGPfact specializes in factorizing complex cell trajectories using Gaussian process mixture models, making it particularly capable of identifying bifurcation events. Therefore, it excels in the accuracy of branch partitioning and similarity of trajectory topology. Among other methods, scShaper (Smolander et al., 2022) and TSCAN(Ji and Ji, 2016) are more suited for generating linear trajectories and excel in linear datasets, accurately predicting pseudotime. The Monocle series, as typical representatives of tree methods, effectively capture complex topologies and are suitable for analyzing cell data with diversified differentiation paths.

Comment#9: Microglia Analysis:In Figures 3A-C, the genes mentioned in the text for each bifurcation do not always match those shown in the panels. Please confirm this.

Thank you for pointing this out. We have carefully reviewed the article and corrected the error where the genes shown in the figures did not correspond to the descriptions in the article. The specific corrections have been made between line 257 and 264:

“The first bifurcation determines the differentiated cell fates of PAM and HM, which involves a set of notable marker genes of both cell types, such as Apoe, Selplg (HM), and Gpnmb (PAM). The second bifurcation determines the proliferative status, which is crucial for the development and function of PAM and HM (Guzmán, n.d.; Li et al., 2019). The genes affected by the second bifurcation are associated with cell cycle and proliferation, such as Mki67, Tubb5, Top2a. The third bifurcation influences the development and maturity of microglia, of which the highly weighted genes, such as Tmem119, P2ry12, and Sepp1 are all previously annotated markers for establishment of the fates of microglia (Anderson et al., 2022; Li et al., 2019) (Supplementary Table 4).”

Comment#10: Regulons:

- The conclusions rely heavily on regulons. The Methods section describes using SCENIC, GENIE3, RCisTarget, and AUCell, but their relation to bifurcation analysis is unclear.

- Do you perform trajectory analysis on all MURP-derived cells or within each identified trajectory based on bifurcation? This point needs clarification to make the outcomes comprehensible. The legend of Figure 4 provides some ideas, but further clarity is required.

Thank you for the comments.

(1) To clarify, we used the tools like SCENIC to annotate the highly weighted genes (HWG) resulted from the bifurcation analysis for transcription factor regulation activity and possible impacts on biological processes. We have added descriptions to the analysis of our microglial data. The revised content is between line 265 and 266:

“Moreover, we retrieved highly active regulons from the HWG by MGPfact, of which the significance is quantified by the overall weights of the member genes.”

(2) We apologize for any confusion caused by our description. It is important to clarify that we performed an overall trajectory analysis on all MURP results, rather than analyzing within each identified trajectory. Specifically, we first used MURP to downsample all preprocessed cells, where each MURP subset represents a group of cells. We then conducted trajectory inference on all MURP subsets and identified bifurcation points. This process generated multiple independent differentiation trajectories, encompassing all MURP subsets. To clearly convey this point, we have added descriptions in the legend of Figure 4. The revised content is between line 276 and 283:

“Fig. 4. MGPfact reconstructed the developmental trajectory of microglia, recovering known determinants of microglia fate. a-c. The inferred independent bifurcation processes with respect to the unique cell types (color-coded) of microglia development, where phase 0 corresponds to the state before bifurcation; and phases 1 and 2 correspond to the states post-bifurcation. Each colored dot represents a metacell of unique cell type defined by MURP. The most highly weighted regulons in each trajectory were labeled by the corresponding transcription factors (left panels). The HWG of each bifurcation process include a set of highly weighted genes (HWG), of which the expression levels differ significantly among phases 1, 2, and 3 (right panels).”

Comment#11: CD8+ T Cells: The comparison is made against Monocle2, the method used in the publication, but it would be beneficial to compare it with more recent methods. Otherwise, the added value of MGPfact is unclear.

Per your request, we have expanded our comparative analysis to include not only Monocle2 but also more recent methods such as Monocle3 (Cao et al., 2019) and scFates Tree (Faure et al., 2023). We used adjusted R-squared values to evaluate each method's ability to explain trajectory variation. The results have been added to Table 2 and Supplementary Table 6. The revised content is between line 318 and 326:

We assessed the goodness-of-fit (adjusted R-square) of the consensus trajectory derived by MGPfact and three methods (Monocle 2, Monocle 3 and scFates Tree) for the CD8+ T cell subtypes described in the original studies (Guo et al., 2018; Zhang et al., 2018). The data showed that MGPfact significantly improved the explanatory power for most CD8+ T cell subtypes over Monocle 2, which was used in the original studies (P < 0.05, see Table 2 and Supplementary Table 6), except for the CD8-GZMK cells in the CRC dataset. Additionally, MGPfact demonstrated better explanatory power in specific cell types when compared to Monocle 3 and scFates Tree. For instance, in the NSCLC dataset, MGPfact exhibited higher explanatory power for CD8-LEF1 cells (Table 2, R-squared = 0.935), while Monocle 3 and scFates Tree perform better in other cell types.

Comment#12: Consensus Trajectory: A panel explaining how the consensus trajectory is generated would be helpful. Include both visual and textual explanations tailored to the journal's audience.

Thank you for the comments. Regarding how the consensus trajectory is constructed, we have illustrated and described this in Figure 1 and the supplementary methods. Taking the reviewers' suggestions into account, we have added more details about the generation process of the consensus trajectory in the methods section to enhance the completeness of the manuscript. The revised content is from line 599 to 606:

“Following MGPfact decomposition, we obtained multiple independent bifurcative trajectories, each corresponds to a binary tree within the temporal domain. These trajectories were then merged to construct a coherent diffusion tree, representing the consensus trajectory of cells’ fate. The merging process involves initially sorting all trajectories by their bifurcation time. The first (earliest) bifurcative trajectory is chosen as the initial framework, and subsequent trajectories are integrated to the initial framework iteratively by adding the corresponding branches at the bifurcation timepoints. As a result, the trajectories are ultimately merged into a comprehensive binary tree, serving as the consensus trajectory.”

Comment#13: Discussion:

- Check for typos, e.g., line 382 "pseudtime.".

- Avoid considering HVG as the entire feature space.

- The first three paragraphs are too similar to the Introduction. Consider shortening them to succinctly state the scenario and the implications of your contribution.

Thank you for pointing out the typos.

(1) We conducted a comprehensive review of the document to ensure there are no typographical errors.

(2) We restructured the first three paragraphs of the discussion section to clarify the limitations in the use of current manifold-learning methods and removed any absolute language regarding treating HVGs as the entire feature space. The revised content is from line 419 to 430:

“Single-cell RNA sequencing (scRNA-seq) provides a direct, quantitative snapshot of a population of cells in certain biological conditions, thereby revealing the actual cell states and functions. Although existing clustering and embedding algorithms can effectively reveal discrete biological states of cells, these methods become less efficient when depicting continuous evolving of cells over the temporal domain. The introduction of manifold learning offers a new dimension for discovery of relevant biological knowledge in cell fate determination, allowing for a better representation of continuous changes in cells, especially in time-dependent processes such as development, differentiation, and clonal evolution. However, current manifold learning methods face major limitations, such as the need for prior information on pseudotime and cell clustering, and lack of explainability, which restricts their applicability. Additionally, many existing trajectory inference methods do not support gene selection, making it difficult to annotate the results to known biological entities, thereby hindering the interpretation of results and subsequent functional studies.”

Comment#14: Minor Comments:

(1) Review the paragraph regarding the "current manifold-learning methods are faced with two major challenges." The message needs clarification.

(2) Increase the quality of the figures.

(3) Update the numbering of equations from #(.x) to (x).

We thank the reviewer for these detailed suggestions.

(1) We have thoroughly revised the discussion section, addressing overly absolute statements. The revised content is from line 426 to 428:

“However, current manifold learning methods face major limitations, such as the need for prior information on pseudotime and cell clustering, and lack of explainability, which restricts their applicability.”

(2) We conducted a comprehensive review of the figures in the article to more clearly present our results.

(3) We have meticulously reviewed the equations in the article to ensure there are no display issues with the indices.

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Author Response

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

We are grateful to the reviewers for their constructive comments. The following is our point-to-point responses.

Reviewer #1 (Recommendations For The Authors):

Point 1- Abstract: advanced morning peak « opposite » to pdf/pdfr mutants. To my knowledge, the alteration of PDF/PDFR suppresses the morning peak. I am not sure that an advance of the peak is « opposite » to its inhibition?

Mutants with disruptions in CNMa or CNMaR display advanced morning activity, indicating an enhanced state. Mutants with disruptions in Pdf or Pdfr exhibit no morning anticipation, suggesting a promoting role of these genes in morning anticipation. Therefore, our revised version is: “Specific elimination of each from clock neurons revealed that loss of the neuropeptide CNMa in two posterior dorsal clock neurons (DN1ps) or its receptor (CNMaR) caused advanced morning activity, indicating a suppressive role of CNMa-CNMaR on morning anticipation, opposite to the promoting role of PDF-PDFR on morning anticipation.” (Line 43-51)

Point 2- Fig 1K-L: the authors should show the sleep phenotype of the homozygous nAChRbeta2 mutant (if not lethal) for a direct comparison with the FRT/FLP genotype and thus evaluate the efficiency of the system.

We have incorporated sleep profiles of nAChRbeta2 mutant and W1118 into Fig 1K-L. nAChRbeta2 mutants (red) exhibited a sleep amount comparable to that of pan-neural nAChRbeta2 knockout flies (dark red), as shown below.

Author response image 1.

Point 3- Dh31-EGFP-FRT expression patterns look different in figS1 A (or fig1 H) and J. why that?

We re-examined the original data. Both (with R57C10-GAL4 for Fig. S1A, right, S1J, left) are Dh31EGFP.FRT samples displayed below which demonstrated consistent primary expression subsets. Any observed disparities in region "e" could potentially be attributed to variations during dissection.

Author response image 2.

Point 4- The knockdown experiments with the elav-switch (RU486) system (fig S2) do not seem to be as efficient as the HS-FLP system (fig 1H-J). The conclusions on the efficiency should be toned down.

We have revised accordingly: "Near Complete Disruption of Target Genes by GFPi and Flp-out Based cCCTomics" (Line 130): "Knocking out at the adult stage using either hsFLP driven Flp-out (Golic and Lindquist, 1989) (Fig. 1H-1J) or neural (elav-Switch) driven shRNAGFP (Nicholson et al., 2008; Osterwalder et al., 2001) (Fig. S2A-S2I), also resulted in the elimination of most, though not all, GFP signals." (Line 145-149)

Point 5- Fig 2H-J: the LD behavioral phenotype of pdfr pan-neuronal cripsr does not seem to correspond to what is described in the literature for the pdfr mutant (han), see hyun et al 2005 (no morning anticipation and advanced evening peak). I understand that the activity index is lower than controls but fig2H shows a large anticipatory activity that seems really unusual, and no advanced evening peak is observed. I think that the authors should show the CRISPR flies and pdfr mutants together, to better compare the phenotypes.

Thank you for pointing out that the phenotypes of pan-neuronal knockout of PDFR by unmodified Cas9 (Fig. 2H-2I of the previous version) whose morning anticipation still exist (Fig, 2H of the previous manuscript), although the significant decrease of morning anticipation index (Fig 2I of the previous manuscript) and advanced evening activity are not as pronounced as observed in han5304 (Fig. 3C in Hyun et al., 2005).

First, we have separated the activity plots of Fig. 2H of previous manuscript, as shown below. The activity from ZT18 to ZT24 shows a tendency of decreasing from ZT18 to ZT21 and a tendency of increasing from ZT21 to ZT24. The lowest activity before dawn during ZT18 to ZT24 shows at about ZT21, and the activity at ZT18 is comparable to the activity at ZT24. This is significantly different compared to the two control groups, whose activity tends to increase activity from ZT18 to ZT24 with an activity peak at ZT24.

The activity from ZT6 to ZT12 increased much faster in Pdfr knockout flies and get to an activity plateau at about ZT11 compared to two control groups with a slower activity increasing from ZT6 to ZT12 with no activity plateau but an activity peak at ZT12.

Author response image 3.

Second, we have incorporated the phenotype of Pdfr mutants we previously generated (Pdfr-attpKO Deng et al., 2019) with Pdfr pan-neuronal knockout by Cas9.HC. This mutant lacks all seven transmembrane regions of Pdfr (a). The phenotypes are very similar between Pdfr-attpKO flies and Pdfr pan-neuronal knockout flies. In this experimental repeat, we found that a much more obvious advanced evening activity peak is observed both in pan-neuronal knockout flies and Pdfr-attpKO flies.

To further analyze the phenotypes of Pdfr pan-neuronal knockout flies by Cas9.HC, we referred to the literature. The activity pattern at ZT18 to ZT24 (activity tends to decrease from ZT18 to ZT21 and tends to increase from ZT21 to ZT24, with the lowest activity before dawn occurring at about ZT21, and activity at ZT18 comparable to activity at ZT24) is also reported in Pdfr knockout flies such as Fig3C and 3H in Hyun et al., 2005, Fig 2B in Lear et al., 2009, Fig 3B in Zhang et al., 2010, Fig .5A in Guo et al., 2014, and Fig 5B in Goda et al., 2019. Additionally, the less pronounced advanced evening activity peak compared to han5304 (Fig. 3C in Hyun et al., 2005) is also reported in Fig. 2B in Lear et al., 2009, Fig. 3B in Zhang et al., 2010, and Fig. 5B in Goda et al., 2019. We consider that this difference is more likely to be caused by environmental conditions or recording strategies (DAM system vs. video tracing).

Therefore, we revised the text to: “Pan-neuronal knockout of Pdfr resulted in a tendency towards advanced evening activity and weaker morning anticipation compared to control flies (Fig. 2H-2I), which is similar to Pdfr-attpKO flies. These phenotypes were not as pronounced as those reported previously, when han5304 mutants exhibited a more obvious advanced evening peak and no morning anticipation (Hyun et al., 2005)”.

Author response image 4.

Point 6-The authors should provide more information about the DD behavior (power is low, but how about the period of rhythmic flies, which is shortened in pdf (renn et al) and pdfr (hyun et al) mutants).

We have incorporated period data into Fig. 2I. Indeed, conditional knock out of Pdfr by Cas9.HC driven by R57C10-GAL4 shortens the period length, as shown below (previous data), also in Fig. 2I of the revised version.

In the revised Fig. 2I, we tested 45 Pdfr-attpKO flies during DD condition (3 out of 48 flies died during video tracing in DD condition), and only one fly was rhythmic. In contrast, 9 out of 48 Pdfr pan-neuronal knockout flies were rhythmic.

Author response image 5.

Point 7- P15 and fig6. The authors indicate that type II CNMa neurons do not show advanced morning activity as type I do, but Figs 6 I and K seem to show some advance although less important than type I. I am not sure that this supports the claim that type I is the main subset for the control of morning activity. This should be toned down.

We have re-organized Fig. 6 and revised the summary of these results as: “However, Type II neurons-specific CNMa knockout (CNMa ∩ GMR91F02) showed weaker advanced morning activity without advanced morning peak (Fig. 6N), while Type I neurons-specific CNMa knockout did (Fig. 6J), indicating a possibility that these two type I CNMa neurons constitute the main functional subset regulating the morning anticipation activity of fruit fly”. (Line 400-405)

Point 8- Figs 6M and N: is power determined from DD data? if yes, how about the period and arrhythmicity? Please also provide the LD activity profiles for the mutants and rescued pdfr genotypes.

Yes, the power was determined from the DD data. In the new version of the manuscript, we have included the activity plots for the LD phase in supplementary Fig S13, as well as shown below (A, B), and the period and arrhythmicity data for the DD phase in Fig. 6S and Table S7. We have also refined the related description as follows: “Moreover, knocking out Pdfr by GMR51H05, GMR79A11 and CNMa GAL4, which cover type I CNMa neurons, decreased morning anticipation of flies (Fig. 6T, Fig. S13B). However, the decrease in morning anticipation observed in the Pdfr knockout by CNMa-GAL4 was not as pronounced as with the other two drivers. Because the presumptive main subset of functional CNMa is also PDFR-positive, there is a possibility that CNMa secretion is regulated by PDF/PDFR signal”. (Line 413-419)

Author response image 6.

Point 9- Fig 7: does CNMaR affect DD behavior? This should be tested.

We analyzed the CNMaR-/- activity in the dark-dark condition over a span of six days. Results revealed a higher power in CNMaR mutants compared to control flies (Power: 93.5±41.9 (CNMaR-/-, n=48) vs 47.3±31.6 (w1118, n=47); Period: 23.7±0.3 h (CNMaR-/-, n=46) vs 23.7±0.3 h (w1118, n=47); arrhythmic rate 2/48 (CNMaR-/-) vs 0/47 (w1118)). Considering that mutating CNMa had no obvious effect on DD behavior, even if CNMaR affects DD behavior, it cannot be attributed to CNMa signal, we did not further repeat and analyze DD behavior of CNMaR mutant. We believe this raises another question beyond the scope of our current discussion.

Reviewer #2 (Recommendations For The Authors):

Point 1-One major concern is the apparent discrepancies in clock network gene expression using the Flp-Out and split-LexA approaches compared to what is known about the expression of several transmitter and peptide-related genes. For example, it is well established that the 5th-sLNv expresses CHAT (along with a single LNd), yet there appears to be no choline acetyltransferase (ChAT) signal in the 5th-sLNv as assayed by the Split-LexA approach (Fig. 4). This approach also suggests that DH31 is expressed in the s-LNvs, which, as one of the most intensely studied clock neuron are known to express PDF and sNPF, but not DH31. The results also suggest that the sLNvs express ChAT, which they do not. Remarkably PDF is not included in the expression analysis, this peptide is well known to be expressed in only two subgroups of clock neurons, and would therefore be an excellent test case for the expression analysis in Fig. 4. PDF should therefore be added to analysis shown in Fig. 4. Another discrepancy is PdfR, which split LexA suggests is expressed in the Large LNvs but not the small LNvs, the opposite of what has been shown using both reporter expression and physiology. The authors do acknowledge that discrepancies exist between their data and previous work on expression within the clock network (lines 237 and 238). However, the extent of these discrepancies is not made clear and calls into question the accuracy of Flp-Out and Split LexA approaches.

The concerns mentioned above are:

(1) sLNvs express PDF and sNPF but not Dh31;

(2) ChAT presents in 5th-sLNv and one LNd but not in other sLNvs;

(3) PDFR presents in sLNvs but not l-LNvs.

(4) PDF is not included in the analysis.

To verify the accuracy of these intersection analyses, all related to PDF positive neurons (except 5th-sLNv and LNds), we stained PDF and examined the co-localization between PDF-positive LNvs and the respective drivers ChAT-KI-LexA, Pdfr-KI -LexA, Dh31-KI -LexA, and Pdf-KI -LexA.

First, Dh31-KI-LexA labeled four s-LNvs, as shown below (also in Fig. S9A). Therefore, the results of the intersection analysis of Dh31-KI-LexA with Clk856-GAL4 are correct. The difference in the results compared to previous literature is attributed to Dh31-KI-LexA labels different neurons than the previous driver or antibody.

Second, no s-LNv was labeled by ChAT-KI -LexA as shown below. We rechecked our intersection data and found that we analyzed 10 brains of ChAT-KI-LexA∩Clk856-GAL4 while only two brains showed sLNvs positively. To enhance the accuracy of intersection analysis results, we marked all positive signal records when positive subsets were found in less than 1/3 of the total analyzed brains (Table S4).

Third, one l-LNv and at least two s-LNvs were labeled by Pdfr-KI-LexA, as shown below (also in Fig. S9B). Fourth, Pdf-KI-LexA labels all PDF-positive neurons, but the intersection analysis by Pdf-KI-LexA and Clk856-GAL4 only showed scattered signals, as shown below (D, also in Fig. S9C). For these cases, we found some positive signals expected but not observed in our dissection. The possible reason could be the inefficiency of LexAop-FRT-myr::GFP driven by LexA. Therefore, our intersection results must miss some positive signals.

Author response image 7.

Finally, we revised the text to (Line 286-317):

To assess the accuracy of expression profiles using CCT drivers, we compared our dissection results with previous reports. Initially, we confirmed the expression of CCHa1 in two DN1s (Fujiwara et al., 2018), sNFP in four s-LNvs and two LNds(Johard et al., 2009), and Trissin in two LNds (Ma et al., 2021), aligning with previous findings. Additionally, we identified the expression of nAChRα1, nAChRα2, nAChRβ2, GABA-B-R2, CCHa1-R, and Dh31-R in all or subsets of LNvs, consistent with suggestions from studies using ligands or agonists in LNvs (Duhart et al., 2020; Fujiwara et al., 2018; Lelito and Shafer, 2012; Shafer et al., 2008) (Table S4).

Regarding previously reported Nplp1 in two DN1as (Shafer et al., 2006), we found approximately five DN1s positive for Nplp-KI-LexA, indicating a broader expression than previously reported. A similar pattern emerged in our analysis of Dh31-KI-LexA, where four DN1s, four s-LNvs, and two LNds were identified, contrasting with the two DN1s found in immunocytochemical analysis (Goda et al., 2016). Colocalization analysis of Dh31-KI-LexA and anti-PDF revealed labeling of all PDF-positive s-LNvs but not l-LNvs (Fig S9A), suggesting that the differences may arise from the broader labeling of 3' end knock-in LexA drivers or the amplitude effect of the binary expression system. The low protein levels might go undetected in immunocytochemical analysis. This aligns with transcriptome analysis findings showing Nplp1 positive in DN1as, a cluster of CNMa-positive DN1ps, and a cluster of DN3s (Ma et al., 2021), which is more consistent with our dissection.

Despite the well-known expression of PDF in LNvs and PDFR in s-LNvs (Renn et al., 1999; Shafer et al., 2008), we did not observe stable positive signals for both in Flp-out intersection experiments, although both Pdf-KI-LexA and Pdfr-KI-LexA label LNvs as expected (Fig S9B-S9C). We also noted fewer positive neurons in certain clock neuron subsets compared to previous reports, such as NPF in three LNds and some LNvs (Erion et al., 2016; He et al., 2013; Hermann et al., 2012; Johard et al., 2009; Lee et al., 2006) and ChAT in four LNds and the 5th s-LNv (Johard et al., 2009; Duhart et al., 2020) (Table S4). We attribute this limitation to the inefficiency of LexAop-FRT-myr::GFP driven by LexA, acknowledging that our intersection results may miss some positive signals.

Point 2-Related to this, the authors rather inaccurately suggest that the field's understanding of PdfR expression within the clock neuron network is "inconsistent" and "variable" (lines 368-377). This is not accurate. It is true that the first attempts to map PdfR expression with antisera and GAL4s were inaccurate. However, subsequent work by several groups has produced strong convergent evidence that with the exception of the l-LNvs after several days post-eclosion, PdfR is expressed in the Cryptochrome expressing a subset of the clock neuron network. This section of the study should be revised.

We thank the reviewer for pointing this out. As we have already addressed and revised the related part in the RESULTS section (Line 308-317), we have now removed this part from the DISCUSSION section of the revised version.

Point 3-One minor issue that would avoid unnecessary confusion by readers familiar with the circadian literature is the say that activity profiles are plotted in the study. The authors have centered their averaged activity profiles on the 12h of darkness. This is the opposite of the practice of the field, and it leads to some initial confusion in the examination of the morning and evening peak data. The authors may wish to avoid this by centering their activity plots on the 12h light phase, which would put the morning peak on the left and the evening peak on the right. This is the way the field is accustomed to examining locomotor activity profiles.

The centering of averaged activity profiles on the 12 h of darkness is done to highlight the phenotype of advanced morning activity. To prevent any confusion among readers, we have included a sentence in the figure legend explaining the difference in our activity profiles compared to previous literatures: "Activity profiles were centered of the 12 h darkness in all figures with evening activity on the left and morning activity on the right, which is different from general circadian literatures. (Fig. 2H legend)" (Line 957-959))

Point 4-The authors conclude that the loss of PDF and CNMa have opposite effects on the morning peak of locomotor activity (line 392). But they also acknowledge, briefly, that things are not that simple: loss of CNMa causes a phase advance, but loss of PDF causes a loss or reduction in the anticipatory peak. It is still significant to find a peptide transmitter with the clock neuron network that regulates morning activity, but the authors should revise their conclusion regarding the opposing actions of PDF and CNMa, which is not well supported by the data.

We have revised the relevant parts.

ABSTRACT: “Specific elimination of each from clock neurons revealed that loss of the neuropeptide CNMa in two posterior dorsal clock neurons (DN1ps) or its receptor (CNMaR) caused advanced morning activity, indicating a suppressive role of CNMa-CNMaR on morning anticipation, opposite to the promoting role of PDF-PDFR on morning anticipation.” (Line 43-48)

DISCUSSION: “Furthermore, given that the morning anticipation vanishing phenotype of Pdf or Pdfr mutant indicates a promoting role of PDF-PDFR signal, while the enhanced morning anticipation phenotype of CNMa mutant suggests an inhibiting role of CNMa signal, we consider the two signals to be antagonistic.” (Line 492-495)

Point 5-The authors should acknowledge, cite, and incorporate the substantive discussion of CNMa peptide and the DN1p neuronal class in Reinhard et al. 2022 (Front Physiol. 13: 886432).

We have revised the text accordingly and cited this paper: “Type I with two neurons whose branches projecting to the anterior region, as in CNMa∩GMR51H05, CNMa∩Pdfr, and CNMa∩GMR79A11 (Fig. 6E, 5G, 6H), and type II with four neurons branching on the posterior side with few projections to the anterior region, as in CNMa∩GMR91F02 (Fig. 6F). These two types of DN1ps’ subsets were also reported and profound discussed previously (Lamaze et al., 2018; Reinhard et al., 2022)”. (Line 393-397)

Reviewer #3 (Recommendations For The Authors):

Point 1-Throughout the manuscript figure legends (axis, genotypes, etc) are too small to be appreciated. Fig. 1. Panel A. The labels are very difficult to read.

We have attempted to enlarge the font as much as possible in the revised version.

Point 2-Fig. 1. H-J Why is efficiency not mentioned in all the examples?

In the revised manuscript, the results of Fig 1H-1J are discussed in the revised version (Line 145-147). The reason that we did not calculate the exact efficiency is that the GFP intensity is not stable enough which might change during dissection, mounting or intensity of laser in our experimental process. Therefore, in all results related to GFP signal (Fig. 1B-1J, Fig. S1, Fig. S2, Fig. 2B-2D), we relied on qualitative judgment rather than quantitative judgment, unless the GFP signal was easily quantifiable (such as in cases with limited cells or no GFP signal in the experimental group).

Point 3-Fig. 1. Panel L, left (light phase): the statistical comparisons are not clearly indicated (the same happens in Figs 3Q and 3R).

We have now re-arranged Fig. 1L and Fig. 3Q-3R to make the statistical comparisons clear in the new version.

Point 4-Line 792. Could induced be introduced?

Yes, we have now corrected this typo.

Point 5-Fig. S1. Check labels for consistency. GMR57C10 Gal4 driver is most likely R57C10.

We have now revised the labels (Fig. S1).

Point 6-Fig. S2. If the experiments were repeated and several brains were observed, the authors should include the efficiency and the number of flies as reported in Fig. S1.

We have now added the number of flies in Fig. S2 as reported in Fig. S1. As Response to Point 2 mentioned, due to the instability of the GFP signal, we are unable to provide a quantitative efficiency in this context.

Point 7-Fig S4. The fig legend describes panels I-J which are not shown in the current version of the manuscript.

We now have deleted them.

Point 8-Fig 2I. Surprising values for morning anticipation indexes even for controls (0.5 would indicate ¨no anticipation¨; in controls, the expected values would be >>0.5, as most of the activity is concentrated right before the transition. Could the authors explain this unexpected result?

We have revised the description of the calculation in the methods section (Line 612). After calculating the ratio of the last three hours of activity to the total six hours of activity, the results were further subtracted by 0.5. Therefore, the index should be ≤0.5. When the index is equal to 0, it indicates no morning anticipation.

Point 9-Fig 2K/L. The authors mention that not all genes are effectively knocked out with their strategy. Could this be accounted for the specific KD strategy, its duration, or the promotor strength? It is surprising no explanation is provided in the text (page 9 line 179).

In our pursuit of establishing a broadly effective method for gene editing, Fig. 2H-2L and Fig. 2D revealed that previous attempts have fallen short of achieving this objective. The observed inefficiency may be attributed to the intensity of the promoter, resulting in inadequate expression. Alternatively, the insufficient duration of the operation may also contribute to the lack of success. However, in the context of sleep and rhythm research applications, the age of the fruit fly tests is typically fixed, limiting the potential to enhance efficiency by extending the manipulation time. Moreover, increasing the expression level may pose challenges related to cytotoxicity, as reported in previous studies (Port et al., 2014). We refrain from offering specific explanations, as we lack a definitive plan and cannot provide additional robust evidence to support the above speculations. Consequently, in our ongoing efforts, we aim to enhance the efficiency of the tool system while operating within the current constraints.

Point 10-Page 9, line 179. Can the authors include a brief description of the reason for the different modifications? Only one was referenced.

We have revised related part in the manuscript (Line 223-231):

Cas9.M9: We fused a chromatin-modulating peptide (Ding et al., 2019), HMGN1 183 (High mobility group nucleosome binding domain 1), at the N-terminus of Cas9 and HMGB1 184 (High mobility group protein B1) at its C-terminus with GGSGP linker, termed Cas9.M9.

Cas9.M6: We also obtained a modified Cas9.M6 with HMGN1 at the N-terminus and an undefined peptide (UDP) at the C-terminus. (NOTE：UDP was gained by accident)

Cas9.M0: We replaced the STARD linker between Cas9 and NLS in Cas9.HC with GGSGP the linker (Zhao et al., 2016), termed Cas9.M0

Point 11-The authors tested the impact of KO nAChR2 across the different versions of conditional disruption (Fig 1K-L, Fig 2L, Fig 3R). It is surprising they observe a difference in daytime sleep upon knocking down with Cas9.HC (2L) but not with Cas9.M9 (3R) and the reverse is seen for night-time sleep. Could the authors provide an explanation? Efficiency is not the issue at stake, is it?

In Fig. 2K, the day sleep of flies (R57C10-GAL4/UAS-sgRNAnAChRbeta2; UAS-Cas9/+) was significantly decreased compared to flies (R57C10-GAL4/UAS-sgRNAnAChRbeta2; +/+), but not when compared to flies (R57C10-GAL4/+; UAS-Cas9/+). Our criterion for asserting a difference is that the experimental group must show a significant distinction from both control groups. Therefore, we concluded that there was no significant difference between the experimental group and the control groups in Fig. 2K.

Point 12-Fig. 4. Which of the two strategies described in A-B was employed to assemble the expression profile of CCT genes in clock neurons shown in C? This information should be part of the fig legend.

We have now revised the legend as follows: “(A-B) Schematic of intersection strategies used in Clk856 labelled clock neurons dissection, Flp-out strategy (A) and split-LexA strategy (B). The exact strategy used for each gene is annotated in Table S5.”

Point 13-Similarly, how many brains were analyzed to give rise to the table shown in C?

We have now revised the legend of Table S4 to address this concern. As indicated in: “The largest N# for each gene in Table S4 is the brain number analyzed for each gene”.

Point 14-Finally, the sentence ¨The figure is...¨ requires revision.

We have now revised it: “The exact cell number for each subset is annotated in Table S4”.

Point 15-Legend to Table S3. The authors have done an incredible job testing many gRNAs for each gene potentially relevant for communication. However, there is very little information to make the most out of it; for instance, the legend does not inform why many of the targeted genes do not appear to have been tested any further. It would be useful to the reader to discern whether despite being the 3 most efficient gRNAs, they were still not effective in targeting the gene of interest, or whether they showed off-targets, or it was simply a matter of testing the educated guesses. This information would be invaluable for the reader.

First, we designed and generated transgenic UAS-sgRNA fly lines for all these sgRNAs. We randomly selected 14 receptor genes, known for their difficulty in editing based on our experience, to assess the efficiency of our strategy, as depicted in Fig. 3M-3P, Fig. S5, and Fig. S6. We believe these results are representative and indicative of the efficiency of sgRNAs designed using our process and applied with the modified Cas9.

Secondly, we acknowledge your valid concern. While we selected sgRNAs with no predicted off-target effects through various prediction models (outlined in the Methods under C-cCCTomics sgRNA design), we did not conduct whole-genome sequencing. Consequently, we can only assert that the off-target possibility is relatively low. To address potential misleading effects arising from off-target concerns, it is essential to validate these results through mutants, RNAi, or alternative UAS-sgRNAs targeting the same gene.

Point 16-Table S4. Some of the data presented derives from observations made in 1-2 brains for a specific cluster; isn´t it too little to base a decision on whether a certain gene is (or not) expressed? It is surprising since the same CCT line was observed/analysed in more brains for other clusters. Can the authors explain the rationale?

The N# number represents the GFP positive number, and we have revised the legend of Table S4. The largest N# number denotes the total number of brains analyzed for a specific CCT line. It's possible that, due to variations in our dissection or mounting process, some clusters were only observed in 1-2 brains out of the total brains analyzed. To enhance the accuracy of intersection analysis results, we marked all positive signal records when positive subsets were found in less than 1/3 of the total analyzed brains (Table S4).

Point 17-The paragraph describing this data in the results section needs revising (lines 233-243).

We have now revised this. (Line 286-317)

Point 18-While it is customary for authors to attempt to improve the description of the activity patterns by introducing new parameters (i.e. MAPI and EAPI, lines 253-258) it would be interesting to understand the difference between the proposed method and the one already in use (which compares the same parameter, i.e., the slope (defined as ¨the slope of the best-fitting linear regression line over a period of 6 h prior to the transition¨, i.e., Lamaze et al. 2020 and many others). Is there a need to introduce yet another one?

This approach is necessary. The slope defined by Lamaze et al. utilizes data from only 2 time points, which may not accurately capture the pattern within a period before light on or off. Linear regression is not well-suited for a single fly due to the high variability in activity at each time point, making it challenging to fit the model at the individual level. The parameters we have introduced (MAPI and EAPI) in this paper are concise and can be applied at the individual level, effectively reflecting the morning or evening anticipation characteristics of each fly.

As an alternative, the activity plot of a certain fly line could be represented by an average of all flies' activity in one experiment. This would make linear regression easier to fit. However, several independent experiments are required for statistical robustness, necessitating the inclusion of hundreds of flies for each strain in a single analysis.

Point 19-In general, the legends of supplementary figures are a bit too brief. S7 and S8: it is not clear which of the two intersectional strategies were used (it would benefit whoever is interested in replicating the experiments). Legend to Fig S8 should read ¨similar to Fig S7¨.

We have now revised the legend and included “The exact strategy used for each gene is annotated in Table S5” in the legend.

Point 20-The legend in Table S6 should clearly state the genotypes examined. What does the marking in bold refer to?

We have now revised annotation of Table S6. Marking in bold refer to results out of one SD compared to control group.

Point 21-Line 314. The sentence needs revision.

We have revised these sentences.

Point 22-Line 391 (and also in the results section). The authors attempt to describe the CNMa phenotype as the opposite of pdf/pdfr mutant phenotypes. However, no morning anticipation/advanced morning anticipation are not necessarily opposite phenotypes.

We have revised related description.

ABSTRACT: “Specific elimination of each from clock neurons revealed that loss of the neuropeptide CNMa in two posterior dorsal clock neurons (DN1ps) or its receptor (CNMaR) caused advanced morning activity, indicating a suppressive role of CNMa-CNMaR on morning anticipation, opposite to the promoting role of PDF-PDFR on morning anticipation.” (Line 43-48)

DISCUSSION: “Furthermore, given that the morning anticipation vanishing phenotype of Pdf or Pdfr mutant indicates a promoting role of PDF-PDFR signal, while the enhanced morning anticipation phenotype of CNMa mutant suggests an inhibiting role of CNMa signal, we consider the two signals to be antagonistic.” (Line 492-495)

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Author Response

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

Reviewer #1 (Public Review):

This paper describes the development and initial validation of an approach-avoidance task and its relationship to anxiety. The task is a two-armed bandit where one choice is 'safer' - has no probability of punishment, delivered as an aversive sound, but also lower probability of reward - and the other choice involves a reward-punishment conflict. The authors fit a computational model of reinforcement learning to this task and found that self-reported state anxiety during the task was related to a greater likelihood of choosing the safe stimulus when the other (conflict) stimulus had a higher likelihood of punishment. Computationally, this was represented by a smaller value for the ratio of reward to punishment sensitivity in people with higher task-induced anxiety. They replicated this finding, but not another finding that this behavior was related to a measure of psychopathology (experiential avoidance), in a second sample. They also tested test-retest reliability in a sub-sample tested twice, one week apart and found that some aspects of task behavior had acceptable levels of reliability. The introduction makes a strong appeal to back-translation and computational validity, but many aspects of the rationale for this task need to be strengthened or better explained. The task design is clever and most methods are solid - it is encouraging to see attempts to validate tasks as they are developed. There are a few methodological questions and interpretation issues, but they do not affect the overall findings. The lack of replicated effects with psychopathology may mean that this task is better suited to assess state anxiety, or to serve as a foundation for additional task development.

We thank the reviewer for their kind comments and constructive feedback. We agree that the approach taken in this paper appears better suited to state anxiety, and further work is needed to assess/improve its clinical relevance.

Reviewer #1 (Recommendations For The Authors):

1) For the introduction, the authors communicate well the appeal of tasks with translational potential, and setting up this translation through computational validity is a strong approach. However, I had some concerns about how the task was motivated in the introduction:

a) The authors state that current approach-avoidance tasks used in humans do not resemble those used in the non-human literature, but do not provide details on what exactly is missing from these tasks that makes translation difficult.

Our intention for the section that the reviewer refers to was to briefly convey that historically, approach-avoidance conflict would have been measured either using questionnaires or joystick-based tasks which have no direct non-human counterpart. However, we note that the phrasing was perhaps unfair to recent tasks that were explicitly designed to be translatable across species. Therefore, we have amended the text to the following:

In humans, on the other hand, approach-avoidance conflict has historically been measured using questionnaires such as the Behavioural Inhibition/Activation Scale (Carver & White, 1994), or cognitive tasks that rely on motor biases, for example by using joysticks to approach/move towards positive stimuli and avoid/move away from negative stimuli, which have no direct non-human counterparts (Guitart-Masip et al., 2012; Kirlic et al., 2017; Mkrtchian et al., 2017; Phaf et al., 2014).

b) Although back-translation to 'match' human paradigms to non-animal paradigms is useful for research, this isn't the end goal of task development. What really matters is how well these tasks, whether in humans or not, capture psychopathology-relevant behavior. Many animal paradigms were developed and brought into extensive use because they showed sensitivity to pharmacological compounds (e.g., benzodiazepines). The introduction accepts the validity of these paradigms at face value, and doesn't address whether developing human tests of psychopathology based on sensitivity to existing medication classes is the best way to generate new insights about psychopathology.

We agree that whilst paradigms with translational and computational validity have merits of their own for neuroscientific theory, clinical validity (i.e. how well the paradigm reflects a phenomenon relevant to psychopathology) is key in the context of clinical applications. While our findings of associations between task performance and self-reported (state) anxiety suggest that our approach is a step in the right direction, the lack of associations with clinical measures was disappointing. Although future work is needed to more directly test the sensitivity of the current approach to psychopathology, this may mean that it, and its non-human counterparts, do not measure behaviours relevant to pathological anxiety. Since our primary focus in this paper was on translational and computational validity, we have opted to discuss the author’s suggestion in the ‘Discussion’ section, as follows:

Further, it is worth noting that many animal paradigms were developed and widely adopted due to their sensitivity to anxiolytic medication (Cryan & Holmes, 2005). Given the lack of associations with clinical measures in our results, it is possible that current translational models of anxiety may not fully capture behaviours that are directly relevant to pathological anxiety. To develop translational paradigms of clinical utility, future research should place a stronger emphasis on assessing their clinical validity in humans.

c) The authors may want to bring in the literature on the description-experience gap (e.g., PMID: 19836292) when discussing existing decision tasks and their computational dissimilarity to non-human operant conditioning tasks.

We thank the reviewer for this useful addition to the introduction. We have now added the following to the 'Introduction’ section:

Moreover, evidence from economic decision-making suggests that explicit offers of probabilistic outcomes can impact decision-making differently compared to when probabilistic contingencies need to be learned from experience (referred to as the ‘description-experience gap’; Hertwig & Erev, 2009); this finding raises potential concerns regarding the use of offer-based tasks in humans as approximations of non-human tasks that do not involve explicit offers.

d) How does one evaluate how computationally similar human vs. non-human tasks are? What are the criteria for making this judgement? Specific to the current tasks, many animal learning tasks are not learning tasks in the same sense that human learning tasks are, in terms of the number of trials used and if the animals are choosing from a learned set of contingencies versus learning the contingencies during the testing.

The computational similarity of human and non-human strategies in a given translational task can be tested empirically. This can be done by fitting models to the data and assessing whether similar models explain choices, even if parameter distributions might vary across species due to, for example, physiological differences. Indeed, non-human animals require much more training to perform even uni-dimensional reinforcement learning, but once they are trained, it should be possible to model their responses. In fact, it should even be possible to take training data into account in some cases. For example, the training phase of the Vogel/Geller-Seifter preclinical tests require an animal to learn to emit a certain action (e.g. lever press) simply to obtain some reward. In the next phase, an aversive outcome is introduced as an additional outcome, but one could model both the training and test phase together – the winning model in our studies would be a suitable candidate to model behaviour here. As we also discuss predictive validity in the ‘Discussion’ section, we opted to add the following text there too:

… computational validity would also need to be assessed directly in non-human animals by fitting models to their behavioural data. This should be possible even in the face of different procedures across species such as number of trials or outcomes used (shock or aversive sound). We are encouraged by our finding that the winning computational model in our study relies on a relatively simple classical reinforcement learning strategy. There exist many studies showing that non-human animals rely on similar strategies during reward and punishment learning (Mobbs et al., 2020; Schultz, 2013); albeit to our knowledge this has never been modelled in non-human animals where rewards and punishment can occur simultaneously.

2) What do the authors make of the non-linear relationship between probability of punishment and probability of choosing the conflict stimulus (Fig 2d), especially in the high task-induced anxiety participants? Did this effect show up in the replication sample as well?

Figures 2c-e were created by binning the continuous predictors of outcome probabilities into discrete bins of equal interval. Since punishment probability varied according to Gaussian random walks, it was also distributed with more of its mass in the central region (~ 0.4), and so values at the extreme bins were estimated on fewer data and with greater variance. The non-linear relationships are likely thus an artefact of our task design and plotting procedure. The pattern was also evident in the replication sample, see Author response image 1:

Author response image 1.

However, since these effects were estimated as linear effects in the logistic regression models, and to avoid overfitting/interpretations of noise arising from our task design, we now plot logistic curves fitted to the raw data instead.

3) How correlated were learning rate and sensitivity parameters? The EM algorithm used here can sometimes result in high correlations among these sets of parameters.

As the reviewer suspects the parameters were strongly correlated, especially across the punishment-specific parameters. The Pearson’s r estimates for the untransformed parameter values were as follows:

Reward parameters: discovery sample r = -0.39; replication sample r = -0.78

Punishment parameters: discovery sample r = -0.91; replication sample r = -0.85

We have included the correlation matrices of the estimated parameters as Supplementary Figure 2 in the ‘Computational modelling’ section of the Supplement.

We have now also re-fitted the winning model using variational Bayesian inference (VBI) via Stan, and found that the cross-parameter correlations were much lower than when the data were fitted using EM. We also ran a sensitivity analysis assessing whether using VBI changed the main findings of our studies. This showed that the correlation between task-induced anxiety and the reward-punishment sensitivity index was robust to fitting method, as was the mediating effect of reward-punishment sensitivity index on anxiety’s effect on choice. This indicates that overall our key findings are robust to different methods of parameter-fitting.

We now direct readers to these analyses from the new ‘Sensitivity analyses’ section in the manuscript, as follows:

As our procedure for estimating model parameters (the expectation-maximisation algorithm, see ‘Methods’) produced high inter-parameter correlations in our data (Supplementary Figure 2), we also re-estimated the parameters using Stan’s variational Bayesian inference algorithm (Stan Development Team, 2023) – this resulted in lower inter-parameter correlations, but our primary computational finding, that the effect of anxiety on choice is mediated by relative sensitivity to reward/punishment was consistent across algorithms (see Supplement section 9.8 for details).

We have included the relevant analyses comparing EM and VBI in the Supplement, as follows:

[9.8 Sensitivity analysis: estimating parameters via expectation maximisation and variational Bayesian inference algorithms]

Given that the expectation maximisation (EM) algorithm produced high inter-parameter correlations, we ran a sensitivity analysis by assessing the robustness of our computational findings to an alternative method of parameter estimation – (mean-field) variational Bayesian inference (VBI) via Stan (Stan Development Team, 2023). Since, unlike EM, the results of VBI are very sensitive to initial values, we fitted the data 10 times with different initial values.

Inter-parameter correlations

The VBI produced lower inter-parameter correlations than the EM algorithm (Supplementary Figure 8).

Sensitivity analysis

Since multicollinearity in the VBI-estimated parameters was lower than for EM, indicating less trade-off in the estimation, we re-tested our computational findings from the manuscript as part of a sensitivity analysis. We first assessed whether we observed the same correlations between task-induced anxiety and punishment learning, and reward-punishment sensitivity index (Supplementary Figure 9a). Punishment learning rate was not significantly associated with task-induced anxiety in any of the 10 VBI iterations in the discovery sample, although it was in 9/10 in the replication sample. On the other hand, the reward-punishment sensitivity index was significantly associated with task-induced anxiety in 9/10 VBI iterations in the discovery sample and all iterations in the replication sample. This suggests that the correlation of anxiety and sensitivity index is robust to these two fitting approaches.

We also re-estimated the mediation models, where in the EM-estimated parameters, we found that the reward-punishment sensitivity index mediated the relationship between task-induced anxiety and task choice proportions (Supplementary Figure 9b). Again, we found that the reward-punishment sensitivity index was a significant mediator in 9/10 VBI iterations in the discovery sample and all iterations in the replication sample. Punishment learning rate was also a significant mediator in 9/10 iterations in the replication sample, although it was not in the discovery sample for all iterations, and this was not observed for the EM-estimated parameters.

Overall, we found that our key results, that anxiety is associated with greater sensitivity to punishment over reward, and this mediates the relationship between anxiety and approach-avoidance behaviour, were robust across both fitting methods.

As an aside, we were unable to run the model fitting using Markov chain Monte Carlo sampling approaches due to the computational power and time required for a sample of this size (Pike & Robinson, 2022, JAMA Psychiatry).

4) What is the split-half reliability of the task parameters?

We thank the reviewer for this query. We have now included a brief section on the (good-to-excellent) split-half reliability of the task in the manuscript:

We assessed the split-half reliability of the task by correlating the overall proportion of conflict option choices and model parameters from the winning model across the first and second half of trials. For overall choice proportion, reliability was simply calculated via Pearson’s correlations. For the model parameters, we calculated model-derived estimates of Pearson’s r values from the parameter covariance matrix when first- and second-half parameters were estimated within a single model, following a previous approach recently shown to accurately estimate parameter reliability (Waltmann et al., 2022). We interpreted indices of reliability based on conventional values of < 0.40 as poor, 0.4 - 0.6 as fair, 0.6 - 0.75 as good, and > 0.75 as excellent reliability (Fleiss, 1986). Overall choice proportion showed good reliability (discovery sample r = 0.63; replication sample r = 0.63; Supplementary Figure 5). The model parameters showed good-to-excellent reliability (model-derived r values ranging from 0.61 to 0.85 [0.76 to 0.92 after Spearman-Brown correction]; Supplementary Figure 5).

5) The authors do a good job of avoiding causal language when setting up the cross-sectional mediation analysis, but depart from this in the discussion (line 335). Without longitudinal data, they cannot claim that "mediation analyses revealed a mechanism of how anxiety induces avoidance".

Thank you for spotting this, we have now amended the text to:

… mediation analyses suggested a potential mechanism of how anxiety may induce avoidance.

Reviewer #2 (Public Review):

Summary:

The authors develop a computational approach-avoidance-conflict (AAC) task, designed to overcome limitations of existing offer based AAC tasks. The task incorporated likelihoods of receiving rewards/ punishments that would be learned by the participants to ensure computational validity and estimated model parameters related to reward/punishment and task induced anxiety. Two independent samples of online participants were tested. In both samples participants who experienced greater task induced anxiety avoided choices associated with greater probability of punishment. Computational modelling revealed that this effect was explained by greater individual sensitivities to punishment relative to rewards.

Strengths:

Large internet-based samples, with discovery sample (n = 369), pre-registered replication sample (n = 629) and test-retest sub group (n = 57). Extensive compliance measures (e.g. audio checks) seek to improve adherence.

There is a great need for RL tasks that model threatening outcomes rather than simply loss of reward. The main model parameters show strong effects and the additional indices with task based anxiety are a useful extension. Associations were broadly replicated across samples. Fair to excellent reliability of model parameters is encouraging and badly needed for behavioral tasks of threat sensitivity.

We thank the reviewer for their comments and constructive feedback.

The task seems to have lower approach bias than some other AAC tasks in the literature. Although this was inferred by looking at Fig 2 (it doesn't seem to drop below 46%) and Fig 3d seems to show quite a strong approach bias when using a reward/punishment sensitivity index. It would be good to confirm some overall stats on % of trials approached/avoided overall.

The range of choice proportions is indeed an interesting statistic that we have now included in the manuscript:

Across individuals, there was considerable variability in overall choice proportions (discovery sample: mean = 0.52, SD = 0.14, min/max = [0.03, 0.96]; replication sample: mean = 0.52, SD = 0.14, min/max = [0.01, 0.99]).

Weaknesses:

The negative reliability of punishment learning rate is concerning as this is an important outcome.

We agree that this is a concerning finding. As reviewer 3 notes, this may have been due to participants having control over the volume used to play the aversive sounds in the task (see below for our response to this point). Future work with better controlled experimental settings will be needed to determine the reliability of this parameter more accurately.

This may also have been due to the asymmetric nature of the task, as only one option could produce the punishment. This means that there were fewer trials on which to estimate learning about the occurrence of a punishment. Future work using continuous outcomes, as the reviewer suggests below, whilst keeping the asymmetric relationship between the options, could help in this regard.

We have included the following comment on this issue in the manuscript:

Alternatively, as participants self-determined the loudness of the punishments, differences in volume settings across sessions may have impacted the reliability of this parameter (and indeed punishment sensitivity). Further, the asymmetric nature of the task may have impacted our ability to estimate the punishment learning rate, as there were fewer occurrences of the punishment compared to the reward.

The Kendall's tau values underlying task induced anxiety and safety reference/ various indices are very weak (all < 0.1), as are the mediation effects (all beta < 0.01). This should be highlighted as a limitation, although the interaction with P(punishment|conflict) does explain some of this.

We now include references to the effect sizes to emphasise this limitation. We also note, as the reviewer suggests, that this may be due to crudeness of overall choice proportion as a measure of approach/avoidance, as it is contaminated with variables such as P(punishment|conflict).

One potentially important limitation of our findings is the small effect size observed in the correlation between task-induced anxiety and avoidance (Kendall's tau values < 0.1, mediation betas < 0.01). This may be attributed to the simplicity of using overall choice proportion as a measure of approach/avoidance, as the effect of anxiety on choice was also influenced by punishment probability.

The inclusion of only one level of reward (and punishment) limits the ecological validity of the sensitivity indices.

We agree that using multi-level outcomes will be an important question for future work and now explicitly note this in the manuscript, as below:

Using multi-level or continuous outcomes would also improve the ecological validity of the present approach and interpretation of the sensitivity parameters.

Appraisal and impact:

Overall this is a very strong paper, describing a novel task that could help move the field of RL forward to take account of threat processing more fully. The large sample size with discovery, replication and test-retest gives confidence in the findings. The task has good ecological validity and associations with task-based anxiety and clinical self-report demonstrate clinical relevance. The authors could give further context but test-retest of the punishment learning parameter is the only real concern. Overall this task provides an exciting new probe of reward/threat that could be used in mechanistic disease models.

We thank the reviewer again for helping us to improve our analyses and manuscript.

Reviewer #2 (Recommendations For The Authors):

Additional context:

In the introduction "cognitive tasks that bear little semblance to those used in the non-human literature" seems a little unfair. One study that is already cited (Ironside et al, 2020) used a task that was adapted from non-human primates for use in humans. It has almost identical visual stimuli (different levels of simultaneous reward and aversive outcome/punishment) and response selection processes (joystick) between species and some overlapping brain regions were activated across species for conflict and aversiveness. The later point that non-human animals must be trained on the association between action and outcome is well taken from the point of view of computational validity but perhaps not sufficient to justify the previous statement.

Our intention for this section was to briefly convey that historically, approach-avoidance conflict would have been measured either using questionnaires or joystick-based tasks which have no direct non-human counterpart. However, we agree that this phrasing is unfair to recent studies such as those by Ironside and colleagues. Therefore, we have amended the text to the following:

In humans, on the other hand, approach-avoidance conflict has historically been measured using questionnaires such as the Behavioural Inhibition/Activation Scale (Carver & White, 1994), or cognitive tasks that rely on motor biases to approach/move towards positive stimuli and avoid/move away from negative stimuli which have no direct non-human counterparts (Guitart-Masip et al., 2012; Kirlic et al., 2017; Mkrtchian et al., 2017; Phaf et al., 2014).

It would be good to speculate on why task induced anxiety made participants slower to update their estimates of punishment probability.

Although a meta-analysis of reinforcement learning studies using reward and punishment outcomes suggests a positive association between punishment learning rate and anxiety symptoms (and depressed mood), we paradoxically found the opposite effect. However, previous work has suggested that distinct forms of anxiety associate differently with anxiety (Wise & Dolan, 2020, Nat. Commun.), where somatic anxiety was negatively correlated with punishment learning rate whereas cognitive anxiety showed the opposite effect. We have now added the following to the manuscript, and noted that future work is needed to understand the potentially complex relationship between anxiety and learning from punishments:

Notably, although a recent computational meta-analysis of reinforcement learning studies showed that symptoms of anxiety and depression are associated with elevated punishment learning rates (Pike & Robinson, 2022), we did not observe this pattern in our data. Indeed, we even found the contrary effect in relation to task-induced anxiety, specifically that anxiety was associated with lower rates of learning from punishment. However, other work has suggested that the direction of this effect can depend on the form of anxiety, where cognitive anxiety may be associated with elevated learning rates, but somatic anxiety may show the opposite pattern (Wise & Dolan, 2020) and this may explain the discrepancy in findings. Additionally, parameter values are highly dependent on task design (Eckstein et al., 2022), and study designs to date may be more optimised in detecting differences in learning rate (Pike & Robinson, 2022) – future work is needed to better understand the potentially complex association between anxiety and punishment learning rate. Lastly, as punishment learning rate was severely unreliable in the test-retest analyses, and the associations between punishment learning rate and state anxiety were not robust to an alternative method of parameter estimation (variational Bayesian inference), the negative correlation observed in our study should be treated with caution.

Were those with more task-based anxiety more inflexible in general?

The lack of associations across reward learning rate and task-induced anxiety suggest that this was not a general inflexibility effect. To test the reviewer’s hypothesis more directly, we conducted a sensitivity analysis by examining the model with a general learning rate – this did not support a general inflexibility effect. Please see the new section in the Supplement below:

[9.10 Sensitivity analysis: anxiety and inflexibility]

As anxious participants were slower to update their estimates of punishment probability, we determined whether this was due to greater general inflexibility by examining the model including two sensitivity parameters, but one general learning rate (i.e. not split by outcome). The correlation between this general learning rate and task-induced anxiety was not significant in either samples (discovery: tau = -0.02, p = 0.504; replication: tau = -0.01, p = 0.625), suggesting that the effect is specific to punishment.

Was the 16% versus 20% of the two samples with clinically relevant anxiety symptoms significantly different? What about other demographics in the two samples?

The difference in proportions were not significantly different (χ2 = 2.33, p = 0.127). The discovery sample included more females and was older on average compared to the replication sample – information which we now report in the manuscript:

The discovery sample consisted of a significantly greater proportion of female participants than the replication sample (59% vs 52%, χ2 = 4.64, p = 0.031). The average age was significantly different across samples (discovery sample mean = 37.7, SD = 10.3, replication sample mean = 34.3, SD = 10.4; t785.5 = 5.06, p < 0.001). The differences in self-reported psychiatric symptoms across samples did not reach significance (p > 0.086).

It would be interesting to know how many participants failed the audio attention checks.

We have now included information about what proportion of participants fail each of the task exclusion criteria in the manuscript:

Firstly, we excluded participants who missed a response to more than one auditory attention check (see above; 8% in both discovery and replication samples) – as these occurred infrequently and the stimuli used for the checks were played at relatively low volume, we allowed for incorrect responses so long as a response was made. Secondly, we excluded those who responded with the same response key on 20 or more consecutive trials (> 10% of all trials; 4/6% in discovery and replication samples, respectively). Lastly, we excluded those who did not respond on 20 or more trials (1/2% in discovery and replication samples, respectively). Overall, we excluded 51 out of 423 (12%) in the discovery sample, and 98 out of 725 (14%) in the replication sample.

There doesn't appear to be a model with only learning from punishment (i.e. no reward learning) included in the model comparison. It would be interesting to see how it compared.

We have fitted the suggested model and found that it is the least parsimonious of the models. Since participants were monetarily incentivised based on the rewards only, this was to be expected. We have now added this ‘punishment learning only’ model and its variant including a lapse term into the model comparison. The two lowest bars on the y-axis in Author response image 2 represent these models.

Author response image 2.

Were sex effects examined as these have been commonly found in AAC tasks. How about other covariates such as age?

We have now tested the effects of sex and age on behaviour and on parameter values. There were indeed some significant effects, albeit with some inconsistencies across the two samples, which for completeness we have included in the manuscript, as follows:

While sex was significantly associated with choice in the discovery sample (β = 0.16 ± 0.07, p = 0.028) with males being more likely to choose the conflict option, this pattern was not evident in the replication sample (β = 0.08 ± 0.06, p = 0.173), and age was not associated with choice in either sample (p > 0.2).

Comparing parameters across sexes via Welch’s t-tests revealed significant differences in reward sensitivity (t289 = -2.87, p = 0.004, d = 0.34; lower in females) and consequently reward-punishment sensitivity index (t336 = -2.03, p = 0.043, d = 0.22; lower in females i.e. more avoidance-driven). In the replication sample, we observed the same effect on reward-punishment sensitivity index (t626 = -2.79, p = 0.005, d = 0.22; lower in females). However, the sex difference in reward sensitivity did not replicate (p = 0.441), although we did observe a significant sex difference in punishment sensitivity in the replication sample (t626 = 2.26, p = 0.024, d = 0.18).

Minor: Still a few placeholders (Supplementary Table X/ Table X) in the methods

We thank the reviewer for spotting these errors. We have now corrected these references.

Reviewer #3 (Public Review):

This study investigated cognitive mechanisms underlying approach-avoidance behavior using a novel reinforcement learning task and computational modelling. Participants could select a risky "conflict" option (latent, fluctuating probabilities of monetary reward and/or unpleasant sound [punishment]) or a safe option (separate, generally lower probability of reward). Overall, participant choices were skewed towards more rewarded options, but were also repelled by increasing probability of punishment. Individual patterns of behavior were well-captured by a reinforcement learning model that included parameters for reward and punishment sensitivity, and learning rates for reward and punishment. This is a nice replication of existing findings suggesting reward and punishment have opposing effects on behavior through dissociated sensitivity to reward versus punishment.

Interestingly, avoidance of the conflict option was predicted by self-reported task-induced anxiety. This effect of anxiety was mediated by the difference in modelled sensitivity to reward versus punishment (relative sensitivity). Importantly, when a subset of participants were retested over 1 week later, most behavioral tendencies and model parameters were recapitulated, suggesting the task may capture stable traits relevant to approach-avoidance decision-making.

We thank the reviewer for their useful analysis of our study. Indeed, it was reassuring to see that performance indices were reliable across time.

However, interpretation of these findings are severely undermined by the fact that the aversiveness of the auditory punisher was largely determined by participants, with the far-reaching impacts of this not being accounted for in any of the analyses. The manipulation check to confirm participants did not mute their sound is highly commendable, but the thresholding of punisher volume to "loud but comfortable" at the outset of the task leaves substantial scope for variability in the punisher delivered to participants. Indeed, participants' ratings of the unpleasantness of the punishment was moderate and highly variable (M = 31.7 out of 50, SD = 12.8 [distribution unreported]). Despite having this rating, it is not incorporated into analyses. It is possible that the key finding of relationships between task-induced anxiety, reward-punishment sensitivity and avoidance are driven by differences in the punisher experienced; a louder punisher is more unpleasant, driving greater task-induced anxiety, model-derived punishment sensitivity, and avoidance (and vice versa). This issue can also explain the counterintuitive findings from re-tested participants; lower/negatively correlated task-induced anxiety and punishment-related cognitive parameters may have been due to participants adjusting their sound settings to make the task less aversive (retest punisher rating not reported). It can therefore be argued that the task may not actually capture meaningful cognitive/motivational traits and their effects on decision-making, but instead spurious differences in punisher intensity.

We thank the reviewer for raising this important potential limitation of our study. We agree that how participants self-adjusted their sound volume may important consequences for our interpretations of the data. Unfortunately, despite the scalability of online data collection, this highlights one of its major weaknesses in the lack of controllability over experimental parameters. The previous paper from which we obtained our aversive sounds (Seow & Hauser, 2021, Behav Res, doi.org/10.3758/s13428-021-01643-0) contains useful analyses with regards to this discussion. When comparing the unpleasantness of the sounds played at 50% vs 100% volume, the authors indeed found that the lower volumes lead to lower unpleasantness ratings. However, the magnitude of this effect did not appear to be substantial (Fig. 4 from the paper), and even at 50% volume, the scream sounds we used were rated in the top quartile for unpleasantness, on average. This implies that the sounds have sufficient inherent unpleasantness, even when played at half intensity. We find this reassuring, in the sense that any self-imposed volume effects may not be large. Of note, our instructions to participants to adjust the volume to a ‘loud but comfortable’ level was based on the same phrasing used in this study.

To the reviewers point on how this might affect the reliability of the task, we have included the following in the ‘Discussion’ section:

Alternatively, as participants self-determined the loudness of the punishments, differences in volume settings across sessions may have impacted the reliability of this parameter (and indeed other measures).

Please see below for analyses accounting for punishment unpleasantness ratings.

This undercuts the proposed significance of this task as a translational tool for understanding anxiety and avoidance. More information about ratings of punisher unpleasantness and its relationship to task behavior, anxiety and cognitive parameters would be valuable for interpreting findings. It would also be of interest whether the same results were observed if the aversiveness of the punisher was titrated prior to the task.

As suggested, we have now included sensitivity analyses using the unpleasantness ratings that show their effect is minimal on our primary inference. We report relevant results below in the ‘Recommendations For The Authors’ section. At the same time, we think it is important to acknowledge that unpleasantness is a combination of both the inherent unpleasantness of the sound and the volume it is presented at, where only the latter is controlled by the participant. Therefore, these analyses are not a perfect indicator of the effect of participant control. For convenience, we reproduce the key findings from this sensitivity analysis here:

Approach-avoidance hierarchical logistic regression model

We assessed whether approach and avoidance responses, and their relationships with state anxiety, were impacted by punishment unpleasantness, by including unpleasantness ratings as a covariate into the hierarchical logistic regression model. Whilst unpleasantness was a significant predictor of choice (positively predicting safe option choices), all significant predictors and interaction effects from the model without unpleasantness survived (Supplementary Figure 11). Critically, this suggests that punishment unpleasantness does not account for all of the variance in the relationship between anxiety and avoidance.

Mediation model

When unpleasantness ratings were included in the mediation models, the mediating effect of the reward-punishment sensitivity index did not survive (discovery sample: standardised β = 0.003 ± 0.003, p = 0.416; replication sample: standardised β = 0.004 ± 0.003, p = 0.100; Supplementary Figure 12). Pooling the samples resulted in an effect that narrowly missed the significance threshold (standardised β = 0.004 ± 0.002, p = 0.068).

More generally, whether or not to titrate the punishments (and indeed the rewards) is an interesting experimental decision, which we think should be guided by the research question. In our case, we were interested in individual differences in reward/punishment learning and sensitivity and their relation to anxiety, so variation in how aversive the sounds affected approach-avoidance decisions was an important aspect of our design. In studies where the aim is to understand more general processes of how humans act under approach-avoidance conflict, it may be better to tightly control the salience of reinforcers.

Ultimately, the best test of the causal role of anxiety on avoidance, and against the hypothesis that our results were driven by spurious volume control effects, would be to run within-subjects anxiety interventions, where these volume effects are naturally accounted for. This will be an important direction for future studies using similar measures. We have added a paragraph in the ‘Discussion’ section on this point:

Relatedly, participants had some control over the intensity at which the punishments were presented, which may have driven our findings relating to anxiety and putative mechanisms of anxiety-related avoidance. Sensitivity analyses showed that our finding that anxiety is positively associated with avoidance in the task was robust to individual differences in self-reported punishment unpleasantness, whilst the mediation effects were not. Future work imposing better control over the stimuli presented, and/or using within-subjects designs will be needed to validate the role of reward/punishment sensitivities in anxiety-related avoidance.

Although the procedure and findings reported here remain valuable to the field, claims of novelty including its translational potential are perhaps overstated. This study complements and sits within a much broader literature that investigates roles for aversion and cognitive traits in approach-avoidance decisions. This includes numerous studies that apply reinforcement learning models to behavior in two-choice tasks with latent probabilities of reward and punishment (e.g., see doi: 10.1001/jamapsychiatry.2022.0051), as well as other translationally-relevant paradigms (e.g., doi: 10.3389/fpsyg.2014.00203, 10.7554/eLife.69594, etc).

We agree with the reviewer that our approach builds on previous work in reinforcement learning, approach-avoidance conflict and translational measures of anxiety. Whilst there are by now many studies using two-choice learning tasks with latent reward and punishment probabilities, our main, and which we refer to as ‘novel’, aim was to bring these fields together in such a way so as to model anxiety-related behaviour.

We note that we do not make strong statements about whether these effects speak to traits per se, and as Reviewer 1 notes, the evidence from our study suggests that the present measure may be better suited to assessing state anxiety. While computational model parameters can and are certainly often interpreted as constituting stable individual traits, a more simple interpretation of our findings may be that state anxiety is associated with a momentary preference for punishment avoidance over reward pursuit. This can still be informative for the study of anxiety, especially given the notion of a continuous relationship between adaptive/state anxiety and maladaptive/persistent anxiety.

Having said that, we agree with the underlying premise of the reviewer’s point that how the measure relates to trait-level avoidance/inhibition measures will be an interesting question for future work. We appreciate the importance of using tasks such as ours and those highlighted by the reviewer as trait-level measures, especially in computational psychiatry. We have now included a discussion on the potential roles of cognitive/motivational traits, in line with the reviewer’s recommendation – briefly, we have included the suggested references by the reviewer, discussed the measure’s potential relevance to cognitive/motivational traits, and direct interested readers to the broader literature. Please see below for details.

Reviewer #3 (Recommendations For The Authors):

As stated in the public review, punisher unpleasantness and its relationship to key findings (including for retest) should be reported and discussed.

We signpost readers to our new analyses, incorporating unpleasantness ratings into the statistical models, from the main manuscript as follows:

Since participants self-determined the volume of the punishments in the task, and therefore (at least in part) their aversiveness, we conducted sensitivity analyses by accounting for self-reported unpleasantness ratings of the punishment (see the Supplement). Our finding that anxiety impacts approach-avoidance behaviour was robust to this sensitivity analysis (p < 0.001), however the mediating effect of the reward-sensitivity sensitivity index was not (p > 0.1; see Supplement section 9.9 for details).

We reproduce the relevant section from the Supplement below. Overall, we found that the effect of anxiety on choices (via its interaction with punishment probability) remained significant after accounting for unpleasantness, however the mediating effect of reward-punishment sensitivity was no longer significant when unpleasantness ratings were included in the model. As noted above, unpleasantness ratings are not a perfect measure of self-imposed sound volume, and indeed punishment sensitivity is essentially a computationally-derived measure of unpleasantness, which makes it difficult to interpret the mediation model which contains both of these measures. However, since we found that anxiety affected choice over and above and effects of self-imposed sound volume (using unpleasantness ratings as a proxy measure), we argue that the task still holds value as a model of anxiety-related avoidance.

[Supplement Section 9.9: Sensitivity analyses of punishment unpleasantness]

Distribution of unpleasantness

The punishments were rated as unpleasant by the participants, on average (discovery sample: mean rating = 31.1 [scored between 0 and 50], SD = 13.1; replication sample: mean rating = 32.1, SD = 12.7; Supplementary Figure 10).

Approach-avoidance hierarchical logistic regression model

We assessed whether approach and avoidance responses, and their relationships with state anxiety, were impacted by punishment unpleasantness, by including unpleasantness ratings as a covariate into the hierarchical logistic regression model. Whilst unpleasantness was a significant predictor of choice (positively predicting safe option choices), all significant predictors and interaction effects from the model without unpleasantness ratings survived (Supplementary Figure 11). Critically, this suggests that punishment unpleasantness does not account for all of the variance in the relationship between anxiety and avoidance.

Mediation model

When unpleasantness ratings were included in the mediation models, the mediating effect of the reward-punishment sensitivity index did not survive (discovery sample: standardised β = 0.003 ± 0.003, p = 0.416; replication sample: standardised β = 0.004 ± 0.003, p = 0.100; Supplementary Figure 12). Pooling the samples resulted in an effect that narrowly missed the significance threshold (standardised β = 0.004 ± 0.002, p = 0.068).

Test-retest reliability of unpleasantness

The test-retest reliability of unpleasantness ratings was excellent (ICC(3,1) = 0.75), although participants gave significantly lower ratings in the second session (t56 = 2.7, p = 0.008, d = 0.37; mean difference of 3.12, SD = 8.63).

Reliability of other measures with/out unpleasantness

To assess the effect of accounting for unpleasantness ratings on reliability estimates of task performance, we extracted variance components from linear mixed models, following a standard approach (Nakagawa et al., 2017) – note that this was not the method used to estimate reliability values in the main analyses, but we used this specific approach to compare the reliability values with and without the covariate of unpleasantness ratings. The results indicated that unpleasantness ratings did not have a material effect on reliability (Supplementary Figure 14).

We discuss the findings of these sensitivity analyses in the ‘Discussion’ section, as follows:

Relatedly, participants had some control over the intensity at which the punishments were presented, which may have driven our findings relating to anxiety and putative mechanisms of anxiety-related avoidance. Sensitivity analyses showed that our finding that anxiety is positively associated with avoidance in the task was robust to individual differences in self-reported punishment unpleasantness, whilst the mediation effects were not. Future work imposing better control over the stimuli presented, and/or using within-subjects designs will be needed to validate the role of reward/punishment sensitivities in anxiety-related avoidance.

Introduction and discussion should spend more time relating the task and current findings to existing procedures and findings examining individual differences in avoidance and cognitive/motivational correlates.

We thank the reviewer for the opportunity to expand on the literature. Whilst there are numerous behavioural paradigms in both the human and non-human literature that involve learning about rewards and punishments, our starting point for the introduction was the state-of-the-art in translational models of approach-avoidance conflict models of anxiety. Therefore, for the sake of brevity and logical flow of our introduction, we have opted to bring in the discussion on other procedures primarily in the ‘Discussion’ section of the manuscript.

We have now included the reviewer’s suggested citations from their ‘Public Review’ as follows:

Since we developed our task with the primary focus on translational validity, its design diverges from other reinforcement learning tasks that involve reward and punishment outcomes (Pike & Robinson, 2022). One important difference is that we used distinct reinforcers as our reward and punishment outcomes, compared to many studies which use monetary outcomes for both (e.g. earning and losing £1 constitute the reward and punishment, respectively; Aylward et al., 2019; Jean-Richard-Dit-Bressel et al., 2021; Pizzagalli et al., 2005; Sharp et al., 2022). Other tasks have been used that induce a conflict between value and motor biases, relying on prepotent biases to approach/move towards rewards and withdraw from punishments, which makes it difficult to approach punishments and withdraw from rewards (Guitart-Masip et al., 2012; Mkrtchian et al., 2017). However, since translational operant conflict tasks typically induce a conflict between different types of outcome (e.g. food and shocks/sugar and quinine pellets; Oberrauch et al., 2019; van den Bos et al., 2014), we felt it was important to implement this feature. One study used monetary rewards and shock-based punishments, but also included four options for participants to choose from on each trial, with rewards and punishments associated with all four options (Seymour et al., 2012). This effectively requires participants to maintain eight probability estimates (i.e. reward and punishment at each of the four options) to solve the task, which may be too difficult for non-human animals to learn efficiently.

We have also included a discussion on the measure’s potential relevance to cognitive/motivational traits as follows:

Finally, whilst there is a broad literature on the roles of behavioural inhibition and avoidance tendency traits on decision-making and behaviour (Carver & White, 1994; Corr, 2004; Gray, 1982), we did not replicate the correlation of experiential avoidance and avoidance responses or the reward-punishment sensitivity index. Since there were also no significant correlations across task performance indices and clinical symptom measures, our findings suggest that the measure may be more sensitive to behaviours relating to state anxiety, rather more stable traits. Nevertheless, how performance in the present task relates to other traits such as behavioural approach/inhibition tendencies (Carver & White, 1994), as has been found in previous studies on reward/punishment learning (Sharp et al., 2022; Wise & Dolan, 2020) and approach-avoidance conflict (Aupperle et al., 2011), will be an important question for future work.

We also now direct readers to a recent, comprehensive review on applying computational methods to approach-avoidance behaviours in the ‘Introduction’ section:

A fundamental premise of this approach is that the brain acts as an information-processing organ that performs computations responsible for observable behaviours, including approach and avoidance (for a recent review on the application of computational methods to approach-avoidance conflict, see Letkiewicz et al., 2023).

I am curious why participants were excluded if they made the same response on 20+ consecutive trials. How does this represent a cut-off between valid versus invalid behavioral profiles?

We apologise for the lack of clarity on this point in our original submission – this exclusion criterion was specifically if participants used the same response key (e.g. the left arrow button) on 20 or more consecutive trials, indicating inattention. Since the left-right positions of the stimuli were randomised across trials, this did not exclude participants who repeatedly chose the same option frequently. However, as we show in the Supplement, this, along with the other exclusion criteria, did not affect our main findings.

We have now clarified this as follows:

… we excluded those who responded with the same response key on 20 or more consecutive trials (> 10% of all trials; 4%/6% in discovery and replication samples, respectively) – note that as the options randomly switched sides on the screen across trials, this did not exclude participants who frequently and consecutively chose a certain option.

Author response:

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

Public Reviews:

Reviewer #2 (Public review):

Summary:

This work by Grogan and colleagues aimed to translate animal studies showing that acetylcholine plays a role in motivation by modulating the effects of dopamine on motivation. They tested this hypothesis with a placebo-controlled pharmacological study administering a muscarinic antagonist (trihexyphenidyl; THP) to a sample of 20 adult men performing an incentivized saccade task while undergoing electroencephalography (EEG). They found that reward increased vigor and reduced reaction times (RTs) and, importantly, these reward effects were attenuated by trihexyphenidyl. High incentives increased preparatory EEG activity (contingent negative variation), and though THP also increased preparatory activity, it also reduced this reward effect on RTs.

Strengths:

The researchers address a timely and potentially clinically relevant question with a within-subject pharmacological intervention and a strong task design. The results highlight the importance of the interplay between dopamine and other neurotransmitter systems in reward sensitivity and even though no Parkinson's patients were included in this study, the results could have consequences for patients with motivational deficits and apathy if validated in the future.

Weaknesses:

The main weakness of the study is the small sample size (N=20) that unfortunately is limited to men only. Generalizability and replicability of the conclusions remain to be assessed in future research with a larger and more diverse sample size and potentially a clinically relevant population. The EEG results do not shape a concrete mechanism of action of the drug on reward sensitivity.

We thank the reviewer for their time and their assessment of this manuscript, and we appreciate their helpful comments on the previous version.

We agree that the sample size being smaller than planned due to the pandemic restrictions is a weakness for this study, and hope that future studies into cholinergic effects on motivation in humans will use larger sample sizes. They should also ensure women are not excluded from sample populations, which will become even more important if the research progresses to clinical populations.

Reviewer #3 (Public review):

Summary:

Grogan et al examine a role for muscarinic receptor activation in action vigor in a saccadic system. This work is motivated by a strong literature linking dopamine to vigor, and some animal studies suggesting that ACH might modulate these effects, and is important because patient populations with symptoms related to reduced vigor are prescribed muscarinic antagonists. The authors use a motivated saccade task with distractors to measure the speed and vigor of actions in humans under placebo or muscarinic antagonism. They show that muscarinic antagonism blunts the motivational effects of reward on both saccade velocity and RT, and also modulates the distractibility of participants, in particular by increasing the repulsion of saccades away from distractors. They show that preparatory EEG signals reflect both motivation and drug condition, and make a case that these EEG signals mediate the effects of the drug on behavior.

Strengths:

This manuscript addresses an interesting and timely question and does so using an impressive within subject pharmacological design and a task well designed to measure constructs of interest. The authors show clear causal evidence that ACH affects different metrics of saccade generation related to effort expenditure and their modulation by incentive manipulations. The authors link these behavioral effects to motor preparatory signatures, indexed with EEG, that relate to behavioral measures of interest and in at least one case statistically mediate the behavioral effects of ACH antagonism.

Weaknesses:

A primary weakness of this paper is the sample size - since only 20 participants completed the study. The authors address the sample size in several places and I completely understand the reason for the reduced sample size (study halt due to covid). Nonetheless, it is worth stating explicitly that this sample size is relatively small for the effect sizes typically observed in such studies highlighting the need for future confirmatory studies.

We thank the reviewer for their time and their assessment of this manuscript, and we appreciate their helpful comments on the previous version.

We agree that the small sample size is a weakness of the study, and hope that future work into cholinergic modulation of motivation can involve larger samples to replicate and extend this work.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Thank you for addressing my comments and clarifying the analysis sections. Women can be included in such studies by performing a pregnancy test before each test session, but I understand how this could have added to the pandemic limitations. Best of luck with your future work!

Thank you for your time in reviewing this paper, and your helpful comments.

Reviewer #3 (Recommendations for the authors):

The authors have done a great job at addressing my concerns and I think that the manuscript is now very solid. That said, I have one minor concern.

Thank you for your time in reviewing this paper, and your helpful comments.

For descriptions of mass univariate analyses and cluster correction, I am still a bit confused on exactly what terms were in the regression. In one place, the authors state:

On each iteration we shuffled the voltages across trials within each condition and person, and regressed it against the behavioural variable, with the model 'variable ~1 + voltage + incentive*distractorPresent*THP + (1 | participant)'.

I take this to mean that the regression model includes a voltage regressor and a three-way interaction term, along with participant level intercept terms.

However, elsewhere, the authors state:

"We regressed each electrode and time-point against the three behavioural variables separately, while controlling for effects of incentive, distractor, THP, the interactions of those factors, and a random effect of participant."

I take this to mean that the regression model included regressors for incentive, distractorPresent, THP, along with their 2 and 3 way interactions. I think that this seems like the more reasonable model - but I just want to 1) verify that this is what the authors did and 2) encourage them to articulate this more clearly and consistently throughout.

We apologise for the lack of clarity about the whole-brain regression analyses.

We used Wilkinson notation for this formula, where ‘A*B’ denotes ‘A + B + A:B’, so all main effects and lower-order interactions terms were included in the regression, as your second interpretation says. The model written out in full would be:

'variable ~1 + voltage + incentive + distractorPresent + THP + incentive*distractorPresent + incentive*THP + distractorPresent*THP +  incentive*distractorPresent*THP + (1 | participant)'    

We will clarify this in the Version of Record.

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors used a motivated saccade task with distractors to measure response vigor and reaction time (RT) in healthy human males under placebo or muscarinic antagonism. They also simultaneously recorded neural activity using EEG with event-related potential (ERP) focused analyses. This study provides evidence that the muscarinic antagonist Trihexyphenidyl (THP) modulates the motivational effects of reward on both saccade velocity and RT, and also increases the distractibility of participants. The study also examined the correlational relationships between reaction time and vigor and manipulations (THP, incentives) with components of the EEG-derived ERPs. While an interesting correlation structure emerged from the analyses relating the ERP biomarkers to behavior, it is unclear how these potentially epiphenomenal biomarkers relate to relevant underlying neurophysiology.

Strengths:

This study is a logical translational extension from preclinical findings of cholinergic modulation of motivation and vigor and the CNV biomarker to a normative human population, utilizing a placebo-controlled, double-blind approach.

While framed in the context of Parkinson's disease where cholinergic medications can be used, the authors do a good job in the discussion describing the limitations in generalizing their findings obtained in a normative and non-age-matched cohort to an aged PD patient population.

The exploratory analyses suggest alternative brain targets and/or ERP components that relate to the behavior and manipulations tested. These will need to be further validated in an adequately powered study. Once validated, the most relevant biomarkers could be assessed in a more clinically relevant population.

Weaknesses:

The relatively weak correlations between the main experimental outcomes provide unclear insight into the neural mechanisms by which the manipulations lead to behavioral manifestations outside the context of the ERP. It would have been interesting to evaluate how other quantifications of the EEG signal through time-frequency analyses relate to the behavioral outcomes and manipulations.

The ERP correlations to relevant behavioral outcomes were not consistent across manipulations demonstrating they are not reliable biomarkers to behavior but do suggest that multiple underlying mechanisms can give rise to the same changes in the ERP-based biomarkers and lead to different behavioral outcomes.

We thank the reviewer for their review and their comments.

We agree that these ERPs may not be reliable biomarkers yet, given the many-to-one mapping we observed where incentives and THP antagonism both affected the CNV in different ways, and hope that future studies will help clarify the use and limitations of the CNV as a potential biomarker of invigoration.

Our original hypothesis was specifically about the CNV as an index of preparatory behaviour, but we plan to look at potential changes to frequency characteristics in future work. We have included this in the discussion of future investigations. (page 16, line 428):

“Future investigations of other aspects of the EEG signals may illuminate us. Such studies could also investigate other potential signals that may be more sensitive to invigoration and/or muscarinic antagonism, including frequency-band power and phase-coherence, or measures of variability in brain signals such as entropy, which may give greater insight into processes affected by these factors.”

Reviewer #2 (Public Review):

Summary:

This work by Grogan and colleagues aimed to translate animal studies showing that acetylcholine plays a role in motivation by modulating the effects of dopamine on motivation. They tested this hypothesis with a placebo-controlled pharmacological study administering a muscarinic antagonist (trihexyphenidyl; THP) to a sample of 20 adult men performing an incentivized saccade task while undergoing electroengephalography (EEG). They found that reward increased vigor and reduced reaction times (RTs) and, importantly, these reward effects were attenuated by trihexyphenidyl. High incentives increased preparatory EEG activity (contingent negative variation), and though THP also increased preparatory activity, it also reduced this reward effect on RTs.

Strengths:

The researchers address a timely and potentially clinically relevant question with a within-subject pharmacological intervention and a strong task design. The results highlight the importance of the interplay between dopamine and other neurotransmitter systems in reward sensitivity and even though no Parkinson's patients were included in this study, the results could have consequences for patients with motivational deficits and apathy if validated in the future.

Weaknesses:

The main weakness of the study is the small sample size (N=20) that unfortunately is limited to men only. The generalizability and replicability of the conclusions remain to be assessed in future research with a larger and more diverse sample size and potentially a clinically relevant population. The EEG results do not shape a concrete mechanism of action of the drug on reward sensitivity.

We thank the reviewer for their review, and their comments.

We agree that our study was underpowered, not reaching our target of 27 participants due to pandemic restrictions halting our recruitment, and hope that future studies into muscarinic antagonism in motivation will have larger sample sizes, and include male and female participants across a range of ages, to assess generalisability.

We only included men to prevent the chance of administering the drug to someone pregnant. Trihexyphenidyl is categorized by the FDA as a Pregnancy Category Class C drug, and the ‘Summary of Product Characteristics’ states: “There is inadequate information regarding the use of trihexyphenidyl in pregnancy. Animal studies are insufficient with regard to effects on pregnancy, embryonal/foetal development, parturition and postnatal development. The potential risk for humans is unknown. Trihexyphenidyl should not be used during pregnancy unless clearly necessary.”

While the drug can be prescribed where benefits may outweigh this risk, as there were no benefits to participants in this study, we only recruited men to keep the risk at zero.

We have updated the Methods/Drugs section to explain this (page 17, line 494):

“The risks of Trihexyphenidyl in pregnancy are unknown, but the Summary Product of Characteristics states that it “should not be used during pregnancy unless clearly necessary”. As this was a basic research study with no immediate clinical applications, there was no justification for any risk of administering the drug during pregnancy, so we only recruited male participants to keep this risk at zero.”

And we reference to this in the Methods/Participants section (page 18, line 501):

“We recruited 27 male participants (see Drugs section above),…”

We agree that future work is needed to replicate this in different samples, and that this work cannot tell us the mechanism by which the drug is dampening invigoration, but we think that showing these effects do occur and can be linked to anticipatory/preparatory activity rather than overall reward sensitivity is a useful finding.

Reviewer #3 (Public Review):

Summary:

Grogan et al examine a role for muscarinic receptor activation in action vigor in a saccadic system. This work is motivated by a strong literature linking dopamine to vigor, and some animal studies suggesting that ACH might modulate these effects, and is important because patient populations with symptoms related to reduced vigor are prescribed muscarinic antagonists. The authors use a motivated saccade task with distractors to measure the speed and vigor of actions in humans under placebo or muscarinic antagonism. They show that muscarinic antagonism blunts the motivational effects of reward on both saccade velocity and RT, and also modulates the distractibility of participants, in particular by increasing the repulsion of saccades away from distractors. They show that preparatory EEG signals reflect both motivation and drug condition, and make a case that these EEG signals mediate the effects of the drug on behavior.

Strengths:

This manuscript addresses an interesting and timely question and does so using an impressive within-subject pharmacological design and a task well-designed to measure constructs of interest. The authors show clear causal evidence that ACH affects different metrics of saccade generation related to effort expenditure and their modulation by incentive manipulations. The authors link these behavioral effects to motor preparatory signatures, indexed with EEG, that relate to behavioral measures of interest and in at least one case statistically mediate the behavioral effects of ACH antagonism.

Weaknesses:

In full disclosure, I have previously reviewed this manuscript in another journal and the authors have done a considerable amount of work to address my previous concerns. However, I have a few remaining concerns that affect my interpretation of the current manuscript.

Some of the EEG signals (figures 4A&C) have profiles that look like they could have ocular, rather than central nervous, origins. Given that this is an eye movement task, it would be useful if the authors could provide some evidence that these signals are truly related to brain activity and not driven by ocular muscles, either in response to explicit motor effects (ie. Blinks) or in preparation for an upcoming saccade.

We thank the reviewer for re-reviewing the manuscript and for raising this issue.

All the EEG analyses (both ERP and whole-brain) are analysing the preparation period between the ready-cue and target appearance when no eye-movements are required. We reject trials with blinks or saccades over 1 degree in size, as detected by the Eyelink software according the sensitive velocity and acceleration criteria specified in the manuscript (Methods/Eye-tracking, page 19, line 550). This means that there should be no overt eye movements in the data. However, microsaccades and ocular drift are still possible within this period, which indeed could drive some effects. To measure this, we counted the number of microsaccades (<1 degree in size) in the preparation period between incentive cue and the target onset, for each trial. Further, we measure the mean absolute speed of the eye during the preparation period (excluding the periods during microsaccades) for each trial.

We have run a control analysis to check whether including ocular drift speed or number of microsaccades as a covariate in the whole-brain regression analysis changes the association between EEG and the behavioural metrics at frontal or other electrodes. Below we show these ‘variable ~ EEG’ beta-coefficients when controlling for each eye-movement covariate, in the same format as Figure 4. We did not run the permutation testing on this due to time/computational costs (it takes >1 week per variable), so p-values were not calculated, only the beta-coefficients. The beta-coefficients are almost unchanged, both in time-course and topography, when controlling for either covariate.  The frontal associations to velocity and distractor pull remain, suggesting they are not due to these eye movements.

We have added this figure as a supplemental figure.

For additional clarity in this response, we also plot the differences between these covariate-controlled beta-coefficients, and the true beta-coefficients from figure 4 (please note the y-axis scales are -0.02:0.02, not -0.15:0.15 as in Figure 4 and Figure 4-figure supplement 2). This shows that the changes to the associations between EEG and velocity/distractor-pull were not frontally-distributed, demonstrating eye-movements were not driving these effects. Relatedly, the RT effect’s change was frontally-distributed, despite Figure 4 showing the true relationship was central in focus, again indicating that effect was also not related to these eye movements.

Author response image 1.

Difference in beta-coefficients when eye-movement covariates are included. This is the difference from the beta-coefficients shown in Figure 4, please note the smaller y-axis limits.

The same pattern was seen if we controlled for the change in eye-position from the baseline period (measured by the eye-tracker) at each specific time-point, i.e., controlling for the distance the eye had moved from baseline at the time the EEG voltage is measured. The topographies and time-course plots were almost identical to the above ones:

Author response image 2.

Controlling for change in eye-position at each time-point does not change the regression results. Left column shows the beta-coefficients between the variable and EEG voltage, and the right column shows the difference from the main results in Figure 4 (note the smaller y-axis limits for the right-hand column).

Therefore, we believe the brain-behaviour regressions are independent of eye-movements. We have included the first figure presented here as an additional supplemental figure, and added the following to the text (page 10, line 265):

“An additional control analysis found that these results were not driven by microsaccades or ocular drift during the preparation period, as including these as trial-wise covariates did not substantially change the beta-coefficients (Figure 4 – Figure Supplement 2).”

For other EEG signals, in particular, the ones reported in Figure 3, it would be nice to see what the spatial profiles actually look like - does the scalp topography match that expected for the signal of interest?

Yes, the CNV is a central negative potential peaking around Cz, while the P3a is slightly anterior to this (peaking between Cz and FCz). We have added the topographies to the main figure (see point below).

This is the topography of the mean CNV (1200:1500ms from the preparation cue onset), which is maximal over Cz, as expected.

The P3a’s topography (200:280ms after preparation cue) is maximal slightly anterior to Cz, between Cz and FCz.

A primary weakness of this paper is the sample size - since only 20 participants completed the study. The authors address the sample size in several places and I completely understand the reason for the reduced sample size (study halt due to COVID). That said, they only report the sample size in one place in the methods rather than through degrees of freedom in their statistical tests conducted throughout the results. In part because of this, I am not totally clear on whether the sample size for each analysis is the same - or whether participants were removed for specific analyses (ie. due to poor EEG recordings, for example).  

We apologise for the lack of clarity here. All 20 participants were included in all analyses, although the number of trials included differed between behavioural and EEG analyses. We only excluded trials with EEG artefacts from the EEG analyses, not from the purely behavioural analyses such as Figures 1&2, although trials with blinks/saccades were removed from behavioural analyses too. Removing the EEG artefactual trials from the behavioural analyses did not change the findings, despite the lower power. The degrees of freedom in the figure supplement tables are the total number of trials (less 8 fixed-effect terms) included in the single-trial / trial-wise regression analyses we used.

We have clarified this in the Methods/Analysis (page 20, line 602):

“Behavioural and EEG analysis included all 20 participants, although trials with EEG artefacts were included in the behavioural analyses (18585 trials in total) and not the EEG analyses (16627 trials in total), to increase power in the former. Removing these trials did not change the findings of the behavioural analyses.”

And we state the number of participants and trials in the start of the behavioural results (page 3, line 97):

“We used single-trial mixed-effects linear regression (20 participants, 18585 trials in total) to assess the effects of Incentive, Distractors, and THP, along with all the interactions of these (and a random-intercept per participant), on residual velocity and saccadic RT.”

and EEG results section (page 7, line 193):

“We used single-trial linear mixed-effects regression to see the effects of Incentive and THP on each ERP (20 participants, 16627 trials; Distractor was included too, along with all interactions, and a random intercept by participant).”

Beyond this point, but still related to the sample size, in some cases I worry that results are driven by a single subject. In particular, the interaction effect observed in Figure 1e seems like it would be highly sensitive to the single subject who shows a reverse incentive effect in the drug condition.

Repeating that analysis after removing the participant with the large increase in saccadic RT with incentives did not remove the incentive*THP interaction effect – although it did weaken slightly from (β = 0.0218, p = .0002) to  (β=0.0197, p=.0082). This is likely because that while that participant did have slower RTs for higher incentives on THP, they were also slower for higher incentives under placebo (and similarly for distractor present/absent), making them less of an outlier in terms of effects than in raw RT terms. Below is Author response image 3 the mean-figure without that participant, and Author response image 4 that participant shown separately.

Author response image 3.

Author response image 4.

There are not sufficient details on the cluster-based permutation testing to understand what the authors did or whether it is reasonable. What channels were included? What metric was computed per cluster? How was null distribution generated?

We apologise for not giving sufficient details of this, and have updated the Methods/Analysis section to include these details, along with a brief description in the Results section.

To clarify here, we adapted the DMGroppe Mass Univariate Testing toolbox to also run cluster-based permutation regressions to examine the relationship between the behavioural variables and the voltages at all EEG electrodes at each time point. On each iteration we shuffled the voltages across trials within each condition and person, and regressed it against the behavioural variable, with the model ‘variable ~1 + voltage + incentive*distractorPresent*THP + (1 | participant)’. The Voltage term measured the association between voltage and the behavioural variable, after controlling for effects of incentive*distractor*THP on behaviour – i.e. does adding the voltage at this time/channel explain additional variance in the variable not captured in our main behavioural analyses. By shuffling the voltages, we removed the relationship to the behavioural variable, to build the null distribution of t-statistics across electrodes and time-samples. We used the ‘cluster mass’ method (Bullmore et al., 1999; Groppe et al., 2011; Maris & Oostenveld, 2007) to build the null distribution of cluster mass (across times/channels per iteration), and calculated the p-value as the proportion of this distribution further from zero than the absolute true t-statistics (two-tailed test).

We have given greater detail for this in the Methods/Analysis section (page 20, line 614):

“We adapted this toolbox to also run cluster-based permutation regressions to examine the relationship between the behavioural variables and the voltages at all EEG electrodes at each time point. On each iteration we shuffled the voltages across trials within each condition and person, and regressed it against the behavioural variable, with the model ‘~1 + voltage + incentive*distractorPresent*THP + (1 | participant)’. The Voltage term measured the association between voltage and the behavioural variable, after controlling for effects of incentive*distractor*THP on behaviour. By shuffling the voltages, we removed the relationship to the behavioural variable, to build the null distribution of t-statistics across electrodes and time-samples. We used the ‘cluster mass’ method (Bullmore et al., 1999; Groppe et al., 2011; Maris & Oostenveld, 2007) to build the null distribution, and calculated the p-value as the proportion of this distribution further from zero than the true t-statistics (two-tailed test). Given the relatively small sample size here, these whole-brain analyses should not be taken as definitive.”

And we have added a brief explanation to the Results section also (page 9, line 246):

“We regressed each electrode and time-point against the three behavioural variables separately, while controlling for effects of incentive, distractor, THP, the interactions of those factors, and a random effect of participant. This analysis therefore asks whether trial-to-trial neural variability predicts behavioural variability. To assess significance, we used cluster-based permutation tests (DMGroppe Mass Univariate toolbox; Groppe, Urbach, & Kutas, 2011), shuffling the trials within each condition and person, and repeating it 2500 times, to build a null distribution of ‘cluster mass’ from the t-statistics (Bullmore et al., 1999; Maris & Oostenveld, 2007) which was used to calculate two-tailed p-values with a family-wise error rate (FWER) of .05 (see Methods/Analysis for details).”

The authors report that "muscarinic antagonism strengthened the P3a" - but I was unable to see this in the data plots. Perhaps it is because the variability related to individual differences obscures the conditional differences in the plots. In this case, event-related difference signals could be helpful to clarify the results.

We thank the reviewer for spotting this wording error, this should refer to the incentive effect weakening the P3a, as no other significant effects were found on the P3a, as stated correctly in the previous paragraph. We have corrected this in the manuscript (page 9, line 232):

“This suggests that while incentives strengthened the incentive-cue response and the CNV and weakened the P3a, muscarinic antagonism strengthened the CNV,”

The reviewer’s suggestion for difference plots is very valuable, and we have added these to Figure 3, as well as increasing the y-axis scale for figure 3c to show the incentives weakening the P3a more clearly, and adding the topographies suggested in an earlier comment. The difference waves for Incentive and THP effects show that both are decreasing voltage, albeit with slightly different onset times – Incentive starts earlier, thus weakening the positive P3a, while both strengthen the negative CNV. The Incentive effects within THP and Placebo separately illustrate the THP*Incentive interaction.

We have amended the Results text and figure (page 7, line 200):

“The subsequent CNV was strengthened (i.e. more negative; Figure 3d) by incentive (β = -.0928, p < .0001) and THP (β = -0.0502, p < .0001), with an interaction whereby THP decreased the incentive effect (β= 0.0172, p = .0213). Figure 3h shows the effects of Incentive and THP on the CNV separately, using difference waves, and Figure 3i shows the incentive effect grows more slowly in the THP condition than the Placebo condition.

For mediation analyses, it would be useful in the results section to have a much more detailed description of the regression results, rather than just reporting things in a binary did/did not mediate sort of way. Furthermore, the methods should also describe how mediation was tested statistically (ie. What is the null distribution that the difference in coefficients with/without moderator is tested against?).

We have added a more detailed explanation of how we investigated mediation and mediated moderation, and now report the mediation effects for all tests run and the permutation-test p-values.

We had been using the Baron & Kenny (1986) method, based on 4 tests outlined in the updated text below, which gives a single measure of change in absolute beta-coefficients when all the tests have been met, but without any indication of significance; any reduction found after meeting the other 3 tests indicates a partial mediation under this method. We now use permutation testing to generate a p-value for the likelihood of finding an equal or larger reduction in the absolute beta-coefficients if the CNV were not truly related to RT. This found that the CNV’s mediation of the Incentive effect on RT was highly significant, while the Mediated Moderation of CNV on THP*Incentive was weakly significant.

During this re-analysis, we noticed that we had different trial-numbers in the different regression models, as EEG-artefactual trials were not excluded from the behavioural-only model (‘RT ~ 1 + Incentive’). However, this causes issues with the permutation testing as we are shuffling the ERPs and need the same trials included in all the mixed-effects models. Therefore, we have redone these mediation analyses, including only the trials with valid ERP measures (i.e. no artefactual trials) in all models. This has changed the beta-coefficients we report, but not the findings or conclusions of the mediation analyses. We have updated the figure to have these new statistics.

We have updated the text to explain the methodology in the Results section (page 12, line 284):

“We have found that neural preparatory activity can predict residual velocity and RT, and is also affected by incentives and THP. Finally, we ask whether the neural activity can explain the effects of incentives and THP, through mediation analyses. We used the Baron & Kenny ( 1986) method to assess mediation (see Methods/Analysis for full details). This tests whether the significant Incentive effect on behaviour could be partially reduced (i.e., explained) by including the CNV as a mediator in a mixed-effects single-trial regression. We measured mediation as the reduction in (absolute) beta-coefficient for the incentive effect on behaviour when the CNV was included as a mediator (i.e., RT ~ 1 + Incentive + CNV + Incentive*CNV + (1 | participant)). This is a directional hypothesis of a reduced effect, and to assess significance we ran a permutation-test, shuffling the CNV within participants, and measuring the change in absolute beta-coefficient for the Incentive effect on behaviour. This generates a distribution of mediation effects where there is no relationship between CNV and RT on a trial (i.e., a null distribution). We ran 2500 permutations, and calculated the proportion with an equal or more negative change in absolute beta-coefficient, equivalent to a one-tailed test. We ran this mediation analysis separately for the two behavioural variables of RT and residual velocity, but not for distractor pull as it was not affected by incentive, so failed the assumptions of mediation analyses (Baron & Kenny, 1986; Muller et al., 2005). We took the mean CNV amplitude from 1200:1500ms as our Mediator.

Residual velocity passed all the assumption tests for Mediation analysis, but no significant mediation was found. That is, Incentive predicted velocity (β=0.1304, t(1,16476)=17.3280, p<.0001); Incentive predicted CNV (β=-0.9122, t(1,16476)=-12.1800, p<.0001); and CNV predicted velocity when included alongside Incentive (β=0.0015, t(1,16475)=1.9753, p=.0483). However, including CNV did not reduce the Incentive effect on velocity, and in fact strengthened it (β=0.1318, t(1,16475)=17.4380, p<.0001; change in absolute coefficient: Δβ=+0.0014). Since there was no mediation (reduction), we did not run permutation tests on this.

However, RT did show a significant mediation of the Incentive effect by CNV: Incentive predicted RT (β=-0.0868, t(1,16476)=-14.9330, p<.0001); Incentive predicted CNV (β=-0.9122, t(1,16476)=-12.1800, p<.0001); and CNV predicted RT when included alongside Incentive (β=0.0127, t(1,16475)=21.3160, p<.0001). The CNV mediated the effect of Incentive on RT, reducing the absolute beta-coefficient (β=-0.0752, t(1,16475)=-13.0570, p<.0001; change in absolute coefficient: Δβ= -0.0116). We assessed the significance of this change via permutation testing, shuffling the CNV across trials (within participants) and calculating the change in absolute beta-coefficient for the Incentive effect on RT when the permuted CNV was included as a mediator. We repeated this 2500 times to build a null distribution of Δβ, and calculated the proportion with equal or stronger reductions for a one-tailed p-value, which was highly significant (p<.0001). This suggests that the Incentive effect on RT is partially mediated by the CNV’s amplitude during the preparation period, and this is not the case for residual velocity.

We also investigated whether the CNV could explain the cholinergic reduction in motivation (THP*Incentive interaction) on RT – i.e., whether CNV mediation the THP moderation. We measured Mediated Moderation as suggested by Muller et al. (2005; see Methods/Analysis for full explanation): Incentive*THP was associated with RT (β=0.0222, t(1,16474)=3.8272, p=.0001); and Incentive*THP was associated with CNV (β=0.1619, t(1,16474)=2.1671, p=.0302); and CNV*THP was associated with RT (β=0.0014, t(1,16472)=2.4061, p=.0161). Mediated Moderation was measured by the change in absolute Incentive*THP effect when THP*CNV was included in the mixed-effects model (β=0.0214, t(1,16472)=3.7298, p=.0002; change in beta-coefficient: Δβ= -0.0008), and permutation-testing (permuting the CNV as above) found a significant effect (p=.0132). This indicates cholinergic blockade changes how incentives affect preparatory negativity, and how this negativity reflects RT, which can explain some of the reduced invigoration of RT. However, this was not observed for saccade velocity.

And we have updated the Methods/Analysis section with a more detailed explanation too (page 21, line 627):

“For the mediation analysis, we followed the 4-step process  (Baron & Kenny, 1986; Muller et al., 2005), which requires 4 tests be met for the outcome (behavioural variable, e.g. RT), mediator (ERP, e.g., CNV) and the treatment (Incentive):

(1) Outcome is significantly associated with the Treatment (RT ~ 1 + Incentive + (1 | participant))

(2) Mediator is significantly associated with the Treatment (ERP ~ 1 + Incentive + (1 | participant))

(3) Mediator is significantly associated with the Outcome (RT ~ 1 + Incentive + ERP + (1 | participant))

(4) And the inclusion of the Mediator reduces the association between the Treatment and Outcome (Incentive effect from model #3)

The mediation was measured by the reduction in the absolute standardised beta coefficient between incentive and behaviour when the ERP mediator was included (model #3 vs model #1 above). We used permutation-testing to quantify the likelihood of finding these mediations under the null hypothesis, achieved by shuffling the ERP across trials (within each participant) to remove any link between the ERP and behaviour. We repeated this 2500 times to build a null distribution of the change in absolute beta-coefficients for the RT ~ Incentive effect when this permuted mediator was included (model #3 vs model #1). We calculated a one-tailed p-value by finding the proportion of the null distribution that was equal or smaller than the true values (as Mediation is a one-tailed prediction).

Mediated moderation (Muller et al., 2005) was used to see whether the effect of THP (the Moderator) on behaviour is mediated by the ERP, with the following tests (after the previous Mediation tests were already satisfied):

(5) THP moderates the Incentive effect, via a significant Treatment*Moderator interaction on the Outcome (RT ~ 1 + Incentive + THP + Incentive*THP + (1 | participant))

(6) THP moderates the Incentive effect on the Mediator, via a Treatment*Moderator interaction on the Outcome (ERP ~ 1 + Incentive + THP + Incentive*THP + (1 | participant))

(7) THP’s moderation of the Incentive effect is mediated by the ERP, via a reduction in the association of Treatment*Moderator on the Outcome when the Treatment*Moderator interaction is included (RT ~ 1 + Incentive + THP + Incentive*THP + ERP + ERP*THP + (1 | participant)

Mediated moderation is measured as the reduction in absolute beta-coefficients for ‘RT ~ Incentive*THP’ between model #5 and #7, which captures how much of this interaction could be explained by including the Mediator*Moderator interaction (ERP*THP in model #7). We tested the significance of this with permutation testing as above, permuting the ERP across trials (within participants) 2500 times, and building a null distribution of the change in the absolute beta-coefficients for RT ~ Incentive*THP between models #7 and #5. We calculated a one-tailed p-value from the proportion of these that were equal or smaller than the true change.”

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

(1) The analysis section could benefit from greater detail. For example, how exactly did they assess that the effects of the drug on peak velocity and RT were driven by non-distracting trials? Ideally, for every outcome, the analysis approach used should be detailed and justified.

We apologise for the confusion from this. To clarify, we found a 2-way regression (incentive*THP) on both residual velocity and saccadic RT and this pattern was stronger in distractor-absent trials for residual velocity, and stronger in distractor-present trials for saccadic RT, as can be seen in Figure 1d&e. However, as there was no significant 3-way interaction (incentive*THP*distractor) for either metric, and the 2-way interaction effects were in the same direction in distractor present/absent trials for both metrics, we think these effects were relatively unaffected by distractor presence.

We have updated the Results section to make this clearer: (page 3, line 94):

We measured vigour as the residual peak velocity of saccades within each drug session (see Figure 1c & Methods/Eye-tracking), which is each trial’s deviation of velocity from the main sequence. This removes any overall effects of the drug on saccade velocity, while still allowing incentives and distractors to have different effects within each drug condition. We used single-trial mixed-effects linear regression (20 participants, 18585 trials in total) to assess the effects of Incentive, Distractors, and THP, along with all the interactions of these (and a random-intercept per participant), on residual velocity and saccadic RT. As predicted, residual peak velocity was increased by incentives (Figure 1d; β = 0.1266, p < .0001), while distractors slightly slowed residual velocity (β = -0.0158, p = .0294; see Figure 1 – Figure supplement 1 for full behavioural statistics). THP decreased the effect of incentives on velocity (incentive * THP: β = -0.0216, p = .0030), indicating that muscarinic blockade diminished motivation by incentives. Figure 1d shows that this effect was similar in distractor absent/present trials, although slightly stronger when the distractor was absent; the 3-way (distractor*incentive*THP) interaction was not significant (p > .05), suggesting that the distractor-present trials had the same effect but weaker (Figure 1d).

Saccadic RT (time to initiation of saccade) was slower when participants were given THP (β = 0.0244, p = < .0001), faster with incentives (Figure 1e; β = -0.0767, p < .0001), and slowed by distractors (β = 0.0358, p < .0001). Again, THP reduced the effects of incentives (incentive*THP: β = 0.0218, p = .0002). Figure 1e shows that this effect was similar in distractor absent/present trials, although slightly stronger when the distractor was present; as the 3-way (distractor*incentive*THP) interaction was not significant and the direction of effects was the same in the two, it suggests the effect was similar in both conditions. Additionally, the THP*Incentive interactions were correlated between saccadic RT and residual velocity at the participant level (Figure 1 – Figure supplement 2).

We have given more details of the analyses performed in the Methods section and the results, as requested by you and the other reviewers (page 20, line 602):

Behavioural and EEG analysis included all 20 participants, although trials with EEG artefacts were included in the behavioural analyses (18585 trials in total) and not the EEG analyses (16627 trials in total), to increase power in the former. Removing these trials did not change the findings of the behavioural analyses.

We used single-trial linear-mixed effects models to analyse our data, including participant as a random effect of intercept, with the formula ‘~1 + incentive*distractor*THP + (1 | participant)’. We z-scored all factors to give standardised beta coefficients.

For the difference-wave cluster-based permutation tests (Figure 3 – Figure supplement 4), we used the DMGroppe Mass Univariate toolbox (Groppe et al., 2011), with 2500 permutations, to control the family-wise error rate at 0.05. This was used for looking at difference waves to test the effects of incentive, THP, and the incentive*THP interaction (using difference of difference-waves), across all EEG electrodes.

We adapted this toolbox to also run cluster-based permutation regressions to examine the relationship between the behavioural variables and the voltages at all EEG electrodes at each time point. On each iteration we shuffled the voltages across trials within each condition and person, and regressed it against the behavioural variable, with the model ‘~1 + voltage + incentive*distractorPresent*THP + (1 | participant)’. The Voltage term measured the association between voltage and the behavioural variable, after controlling for effects of incentive*distractor*THP on behaviour. By shuffling the voltages, we removed the relationship to the behavioural variable, to build the null distribution of t-statistics across electrodes and time-samples. We used the ‘cluster mass’ method (Bullmore et al., 1999; Groppe et al., 2011; Maris & Oostenveld, 2007) to build the null distribution, and calculated the p-value as the proportion of this distribution further from zero than the true t-statistics (two-tailed test). Given the relatively small sample size here, these whole-brain analyses should not be taken as definitive.

For the mediation analysis, we followed the 4-step process  (Baron & Kenny, 1986; Muller et al., 2005), which requires 4 tests be met for the outcome (behavioural variable, e.g. RT), mediator (ERP, e.g., CNV) and the treatment (Incentive):

(1) Outcome is significantly associated with the Treatment (RT ~ 1 + Incentive + (1 | participant))

(2) Mediator is significantly associated with the Treatment (ERP ~ 1 + Incentive + (1 | participant))

(3) Mediator is significantly associated with the Outcome (RT ~ 1 + Incentive + ERP + (1 | participant))

(4) And the inclusion of the Mediator reduces the association between the Treatment and Outcome (Incentive effect from model #3)

The mediation was measured by the reduction in the absolute standardised beta coefficient between incentive and behaviour when the ERP mediator was included (model #3 vs model #1 above). We used permutation-testing to quantify the likelihood of finding these mediations under the null hypothesis, achieved by shuffling the ERP across trials (within each participant) to remove any link between the ERP and behaviour. We repeated this 2500 times to build a null distribution of the change in absolute beta-coefficients for the RT ~ Incentive effect when this permuted mediator was included (model #3 vs model #1). We calculated a one-tailed p-value by finding the proportion of the null distribution that was equal or more negative than the true value (as Mediation is a one-tailed prediction). For this mediation analysis, we only included trials with valid ERP measures, even for the models without the ERP included (e.g., model #1), to keep the trial-numbers and degrees of freedom the same.

Mediated moderation (Muller et al., 2005) was used to see whether the effect of THP (the Moderator) on behaviour is mediated by the ERP, with the following tests (after the previous Mediation tests were already satisfied):

(5) THP moderates the Incentive effect, via a significant Treatment*Moderator interaction on the Outcome (RT ~ 1 + Incentive + THP + Incentive*THP + (1 | participant))

(6) THP moderates the Incentive effect on the Mediator, via a Treatment*Moderator interaction on the Outcome (ERP ~ 1 + Incentive + THP + Incentive*THP + (1 | participant))

(7) THP’s moderation of the Incentive effect is mediated by the ERP, via a reduction in the association of Treatment*Moderator on the Outcome when the Treatment*Moderator interaction is included (RT ~ 1 + Incentive + THP + Incentive*THP + ERP + ERP*THP + (1 | participant)

Mediated moderation is measured as the reduction in absolute beta-coefficients for ‘RT ~ Incentive*THP’ between model #5 and #7, which captures how much of this interaction could be explained by including the Mediator*Moderator interaction (ERP*THP in model #7). We tested the significance of this with permutation testing as above, permuting the ERP across trials (within participants) 2500 times, and building a null distribution of the change in the absolute beta-coefficients for RT ~ Incentive*THP between models #7 and #5. We calculated a one-tailed p-value from the proportion of these that were equal or more negative than the true change.

(2) Please explain why only men were included in this study. We are all hoping that men-only research is a practice of the past.

We only included men to prevent any chance of administering the drug to someone pregnant. Trihexyphenidyl is categorized by the FDA as a Pregnancy Category Class C drug, and the ‘Summary of Product Characteristics’ states: “There is inadequate information regarding the use of trihexyphenidyl in pregnancy. Animal studies are insufficient with regard to effects on pregnancy, embryonal/foetal development, parturition and postnatal development. The potential risk for humans is unknown. Trihexyphenidyl should not be used during pregnancy unless clearly necessary.”

While the drug can be prescribed where benefits may outweigh this risk, as there were no benefits to participants in this study, we only recruited men to keep the risk at zero.

We have updated the Methods/Drugs section to explain this (page 17, line 494):

“The risks of Trihexyphenidyl in pregnancy are unknown, but the Summary Product of Characteristics states that it “should not be used during pregnancy unless clearly necessary”. As this was a basic research study with no immediate clinical applications, there was no justification for any risk of administering the drug during pregnancy, so we only recruited male participants to keep this risk at zero.”

And we have referenced this in the Methods/Participants section (page 18, line 501):

“Our sample size calculations suggested 27 participants would detect a 0.5 effect size with .05 sensitivity and .8 power. We recruited 27 male participants (see Drugs section above)”

(3) Please explain acronyms (eg EEG) when first used.

Thank you for pointing this out, we have explained EEG at first use in the abstract and the main text, along with FWER, M1r, and ERP which had also been missed at first use.

Reviewer #3 (Recommendations For The Authors):

The authors say: "Therefore, acetylcholine antagonism reduced the invigoration of saccades by incentives, and increased the pull of salient distractors. We next asked whether these effects were coupled with changes in preparatory neural activity." But I found this statement to be misleading since the primary effects of the drug seem to have been to decrease the frequency of distractor-repulsed saccades... so "decreased push" would probably be a better analogy than "increased pull".

Thank you for noticing this, we agree, and have changed this to (page 5, line 165):

“Therefore, acetylcholine antagonism reduced the invigoration of saccades by incentives, and decreased the repulsion of salient distractors. We next asked whether these effects were coupled with changes in preparatory neural activity.”

I don't see anything in EEG preprocessing about channel rejection and interpolation. Were these steps performed? There are very few results related to the full set of electrodes.

We did not reject or interpolate any channels, as visual inspection found no obvious outliers in terms of noisiness, and no channels had standard deviations (across time/trials) higher than our standard cutoff (of 80). The artefact rejection was applied across all EEG channels, so any trials with absolute voltages over 200uV in any channel were removed from the analysis. On average 104/120 trials were included (having passed this check, along with eye-movement artefact checks) per condition per person, and we have added the range of these, along with totals across conditions to the Analysis section and a statement about channel rejection/interpolation (page 20, line 588):

“Epochs were from -200:1500ms around the preparation cue onset, and were baselined to the 100ms before the preparation cue appeared. Visual inspection found no channels with outlying variance, so no channel rejection or interpolation was performed. We rejected trials from the EEG analyses where participants blinked or made saccades (according to EyeLink criteria above) during the epoch, or where EEG voltage in any channel was outside -200:200μV (muscle activity). On average 104/120 trials per condition per person were included (SD = 21, range = 21-120), and 831/960 trials in total per person (SD=160, range=313-954). A repeated-measures ANOVA found there were no significant differences in number of trials excluded for any condition (p > .2).”

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.

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).

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.

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.

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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.

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.

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.

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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:

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.

In addition to our responses to reviewer suggestions below, a minor bug in the calculation of CAIS was brought to our attention by a reader of our preprint. We have corrected this bug and rerun analyses, whose results became slightly stronger as noise was removed. While we were doing that, someone pointed out to us that our equations were almost the same as Kullback-Leibler divergence, which explains why our metric performed so well. We have made the numerically trivial (see before vs. after figure below) mathematical change to use Kullback-Leibler divergence instead, and now have a better story, with a solid basis in information theory, as to why CAIS works.

Author response image 1.

Unfortunately, we discovered a second bug that caused our PIC correction code to fail to perform the needed correction for phylogenetic confounding. The previously reported correlation between CAIS (or ENC) with body mass no longer survives PIC-correction. We have therefore removed this analysis from the manuscript. Our story now stands more on the theoretical basis of CAIS and ENC than on the post facto validation than it previously did. We now also present CAIS and ENC on a more equal footing. ENC results are slightly stronger, while CAIS has the complementary advantage of correcting for amino acid frequencies.

The work involved in these changes, as well as some of the responses to reviews below, justifies changing the second author into a co-first author, and adding an additional coauthor (Hanon McShea) who discovered the second bug.

Reviewer #1 (Public Review): 

In this manuscript, the authors propose a new codon adaptation metric, Codon Adaptation Index of Species (CAIS), which they present as an easily obtainable proxy for effective population size. To permit between-species comparisons, they control for both amino acid frequencies and genomic GC content, which distinguishes their approach from existing ones. Having confirmed that CAIS negatively correlates with vertebrate body mass, as would be expected if small-bodied species with larger effective populations experience more efficient selection on codon usage, they then examine the relationship between CAIS and intrinsic structural disorder in proteins. 

The idea of a robust species-level measure of codon adaptation is interesting. If CAIS is indeed a reliable proxy for the effectiveness of selection, it could be useful to analyze species without reliable life history- or mutation rate data (which will apply to many of the genomes becoming available in the near future). 

A key question is whether CAIS, in fact, measures adaptation at the codon level. Unfortunately, CAIS is only validated indirectly by confirming a negative correlation with body mass. As a result, the observations about structural disorder are difficult to evaluate. 

As discussed in the preamble above, we have replaced the body mass validation with a stronger theoretical basis in information theory.

A potential problem is that differences in GC between species are not independent of life history. Effective population size can drive compositional differences due to the effects of GC-biased gene conversion (gBGC). As noted by Galtier et al. (2018), genomic GC correlates negatively with body mass in mammals and birds. It would therefore be important to examine how gBGC might affect CAIS, and to what extent it could explain the relationship between CAIS and body mass. 

Suppose that gBGC drives an increase in GC that is most pronounced at 3rd codon positions in highrecombination regions in small-bodied species. In this case, could observed codon usage depart more strongly from expectations calculated from overall genomic GC in small vertebrates compared to large ones? The authors also report that correcting for local intergenic GC was unsuccessful, based on the lack of a significant negative relationship with body mass (Figure 3D). In principle, this could also be consistent with local GC providing a relatively more appropriate baseline in regions with high recombination rates. Considering these scenarios would clarify what exactly CAIS is capturing. 

Figure 3 (previously Supplementary Figures S5A and S5B) shows that CAIS is negligibly correlated with %GC (not robust to multiple comparisons correction), and ENC not at all. We believe this is evidence against the possibility brought up by the reviewer, i.e. that Ne might affect gBGC (and hence global %GC). This relationship, if present, could act as a confounding effect, but it is not present within our species dataset. 

Note that we expect our genomic-GC-based codon usage expectations to reflect unchecked gBGC in an average genomic region, independently of whether that species has high or low Ne. Our working model is that non-selective forces, include gBGC as well as conventional mutation biases, vary among species, and that they rather than selection determine each species’ genome-wide %GC. By correcting for genome-wide %GC, CAIS and ENC correct for both mutation bias and gBGC, in order to isolate the effects of selection.

This argument, based on an average genomic region, is vulnerable to gene-rich genomic regions having differentially higher recombination rates and hence GC-biased gene conversion. However, we do not see the expected positive correlation between |𝐥𝐨𝐜𝐚𝐥 𝐆𝐂 - global GC| and CAIS (see new Figure 5), again suggesting that gene conversion strength is not a confounding factor acting on CAIS.

Given claims about "exquisitely adapted species", the case for using CAIS as a measure of codon adaptation would also be stronger if a relationship with gene expression could be demonstrated. RSCU is expected to be higher in highly expressed genes. Is there any evidence that the equivalent GCcontrolled measure behaves similarly? 

Correlations with gene expression are outside the scope of the current work, which is focused on producing and exploiting a single value of codon adaptation per species. It is indeed possible that our general approach of using Kullback-Leibler divergence to correct for genomic %GC could be useful in future work investigating differences among genes.  

The manuscript is overall easy to follow, though some additional context may be helpful for the general reader. A more detailed discussion of how this work compares to the approach taken by Galtier et al. (2018), which accounted for GC content and gBGC when examining codon preferences, would be appropriate, for example. In addition, it would have been useful to mention past work that has attempted to explicitly quantify selection on codon usage. 

One key difference between our work and that of Galtier et al. 2018 is that our approach does not rely on identifying specific codon preferences as a function of species. Our approach might therefore be robust to scenarios where different genes have different codon preferences (see Gingold et al. 2014 https://doi.org/10.1016/j.cell.2014.08.011). At a high level, our results are in broad agreement with those of Galtier et al., 2018, who found that gBGC affected all animal species, regardless of Ne, and who like us, found that the degree of selection on codon usage depended on Ne.

Reviewer #2 (Public Review): 

## Summary 

The goal of the authors in this study is to develop a more reliable approach for quantifying codon usage such that it is more comparable across species. Specifically, the authors wish to estimate the degree of adaptive codon usage, which is potentially a general proxy for the strength of selection at the molecular level. To this end, the authors created the Codon Adaptation Index for Species (CAIS) that controls for differences in amino acid usage and GC% across species. Using their new metric, the authors find a previously unobserved negative correlation between the overall adaptiveness of codon usage and body size across 118 vertebrates. As body size is negatively correlated with effective population size and thus the general strength of natural selection, the negative correlation between CAIS and body size is expected. The authors argue this was previously unobserved due to failures of other popular metrics such as Codon Adaptation Index (CAI) and the Effective Number of Codons (ENC) to adequately control for differences in amino acid usage and GC content across species. Most surprisingly, the authors also find a positive relationship between CAIS and the overall "disorderedness" of a species protein domains. As some of these results are unexpected, which is acknowledged by the authors, I think it would be particularly beneficial to work with some simulated datasets. I think CAIS has the potential to be a valuable tool for those interested in comparing codon adaptation across species in certain situations. However, I have certain theoretical concerns about CAIS as a direct proxy for the efficiency of selection $sN_e$ when the mutation bias changes across species.  

## Strengths 

(1) I appreciate that the authors recognize the potential issues of comparing CAI when amino acid usage varies and correct for this in CAIS. I think this is sometimes an under-appreciated point in the codon usage literature, as CAI is a relative measure of codon usage bias (i.e. only considers synonyms). However, the strength of natural selection on codon usage can potentially vary across amino acids, such that comparing mean CAI between protein regions with different amino acid biases may result in spurious signals of statistical significance (see Cope et al. Biochemica et Biophysica Acta - Biomembranes 2018 for a clear example of this). 

We now cite Cope et al. as an example of how amino acid composition can act as a confounding factor.

(2) The authors present numerous analysis using both ENC and mean CAI as a comparison to CAIS, helping given a sense of how CAIS corrects for some of the issues with these other metrics. I also enjoyed that they examined the previously unobserved relationship between codon usage bias and body size, which has bugged me ever since I saw Kessler and Dean 2014. The result comparing protein disorder to CAIS was particularly interesting and unexpected. 

Unfortunately, our previous PIC correction code was buggy, and in fact the relationship with body size does not survive PIC correction (although it is strong prior to PIC correction). We have therefore removed it from the paper. However, the more novel result on protein disorder remains strong.

(3) The CAIS metric presented here is generally applicable to any species that has an annotated genome with protein-coding sequences. 

## Weaknesses 

(1) The main weakness of this work is that it lacks simulated data to confirm that it works as expected. This would be particularly useful for assessing the relationship between CAIS and the overall effect of protein structure disorder, which the authors acknowledge is an unexpected result. I think simulations could also allow the authors to assess how their metric performs in situations where mutation bias and natural selection act in the same direction vs. opposite directions. Additionally, although I appreciate their comparisons to ENC and mean CAI, the lack of comparison to other popular codon metrics for calculating the overall adaptiveness of a genome (e.g. dos Reis et al.'s $S$ statistic, which is a function of tRNA Adaptation Index (tAI) and ENC) may be more appropriate. Even if results are similar to $S$, CAIS has a noted advantage that it doesn't require identifying tRNA gene copy numbers or abundances, which I think are generally less readily available than genomic GC% and protein-coding sequences. 

The main limitation of dos Reis’s test in our view is that, like the better versions of CAI, it requires comparable orthologs across species. See also the discussion below re the benefits of proteome-wide approach. We now also note the advantage of not needing tRNA gene copy numbers and abundances. 

Simulated datasets would be great, but we think it a nice addition rather than must-have, in particular because we are skeptical about whether our understanding of all relevant processes is good enough such that simulations would add much to our more heuristic argument along the lines of Figure 2. E.g. the complications of Gingold et al. 2014 cited above are pertinent, but incorporating them would make simulations quite involved. Instead, we now have a stronger theoretical justification for CAIS grounded in information theory. We have significantly expanded discussion of Figure 2 to give a clearer idea of the conceptual underpinnings of CAIS and ENC.

The authors mention the selection-mutation-drift equilibrium model, which underlies the basic ideas of this work (e.g. higher $N_e$ results in stronger selection on codon usage), but a more in-depth framing of CAIS in terms of this model is not given. I think this could be valuable, particularly in addressing the question "are we really estimating what we think we're estimating?" 

Let's take a closer look at the formulation for RSCUS. From here on out, subscripts will only be used to denote the codon and it will be assumed that we are only considering the case of r = genome for some species s.

I think what the authors are attempting to do is "divide out" the effects of mutation bias (as given by $E_i$), such that only the effects of natural selection remain, i.e. deviations from the expected frequency based on mutation bias alone represent adaptive codon usage. Consider Gilchrist et al. MBE 2015, which says that the expected frequency of codon i at selection-mutation-drift equilibrium in gene g for an amino acid with Na synonymous codons is

where ∆M is the mutation bias, ∆η is the strength of selection scaled by the strength of drift, and φg is the gene expression level of gene g. In this case, ∆M and ∆η reflect the strength and direction of mutation bias and natural selection relative to a reference codon, for which ∆M,∆η = 0. Assuming the selection-mutation-drift equilibrium model is generally adequate to model of the true codon usage patterns in a genome (as I do and I think the authors do, too), the Ei,g could be considered the expected observed frequency codon i in gene g

E[Oi,g].

Let’s re-write the  in the form of Gilchrist et al., such that it is a function of mutation bias ∆M. For simplicity we will consider just the two codon case and assume the amino acid sequence is fixed. Assuming GC% is at equilibrium, the term gr and 1 − gr can be written as

where µx→y is the mutation rate from nucleotides x to y. As described in Gilchrist et al. MBE 2015 and Shah and Gilchrist PNAS 2011, the mutation bias .This can be expressed in terms of the equilibrium GC content by recognizing that

As we are assuming the amino acid sequence is fixed, the probability of observing a synonymous codon i at an amino acid becomes just a Bernoulli process. 

If we do this, then 

Recall that in the Gilchrist et al. framework, the reference codon has ∆MNNG,NNG \= 0 =⇒ e−∆MNNG,NNG \=1. Thus, we have recovered the Gilchrist et al. model from the formulation of $E_i$ under the assumption that natural selection has no impact on codon usage and codon NNG is the pre-defined reference codon. To see this, plug in 0 for ∆η in equation (1).. 

We can then calculate the expected RSCUS using equation (1) (using notation E[Oi]) and equation (6) for the two codon case. For simplicity assume, we are only considering a gene of average expression (defined as ). Assume in this case that NNG is the reference codon (∆MNNG,∆ηNNG \= 0).

This shows that the expected value of RSCUS for a two-codon amino acid is expected to increase as the strength of selection $\Delta\eta$ increases, which is desired. Note that $\Delta\eta$ in Gilchrist et al. is formulated in terms of selection *against* a codon relative to the reference, such that a negative value represents that a codon is favored relative to the reference. If $\Delta\eta = 0$ (i.e. selection does not favor either codon), then $E[RSCUS] = 1$. Also note that the expected RSCUS does not remain independent of the mutation bias. This means that even if $sN_e$ (i.e. the strength of natural selection) does not change between species, changes to the strength and direction of mutation bias across species could impact RSCUS. Assuming my math is right, I think one needs to be cautious when interpreting CAIS as representative of the differences in the efficiency of selection across species except under very particular circumstances. One such case could be when it is known that mutation bias varies little across the species of interest. Looking at the species used in this manuscript, most of them have a GC content ranging around 0.41, so I suspect their results are okay. 

Although I have not done so, I am sure this could be extended to the 4 and 6 codon amino acids. 

We thank Reviewer 2 for explicitly laying out the math that was implicit in our Figures 1 and 2. While we keep our more heuristic presentation, our revised manuscript now more clearly acknowledges that the per-site codon adaptation bias depicted in Figure 1 has limited sensitivity to s*Ne. The reason that we believe our approach worked despite this, is that we think the phenomenon is driven by what is shown in Figure 2. I.e., where Ne makes a difference is by determining the proteome-wide fraction of codons subject to significant codon adaptation, rather than by determining the strength of codon adaptation at any particular site or gene. We have made multiple changes to the texts to make this point clearer.

Another minor weakness of this work is that although the method is generally applicable to any species with an annotated genome and the code is publicly available, the code itself contains hard-coded values for GC% and amino acid frequencies across the 118 vertebrates. The lack of a more flexible tool may make it difficult for less computationally-experienced researchers to take advantage of this method. 

Genome-wide %GC values are hard-coded because they were taken from the previous study of James et al. (2023) https://doi.org/10.1093/molbev/msad073. As summarized in the manuscript, genome-wide %GC was a byproduct of a scan of all six reading frames across genic and intergenic sequences available from NCBI with access dates between May and July 2019. The more complicated code used to calculate the intergenic %GC, and the code used to calculate amino acid frequencies is located at https://github.com/MaselLab/CodonAdaptation-Index-of-Species. Luckily, someone else just wrote a simpler end to end pipeline for us, on the basis of our preprint. We now note this in the Acknowledgements, and link to it: https://github.com/gavinmdouglas/handy_pop_gen/blob/main/CAIS.py.

Author response:

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

We thank the reviewers for their careful and overall positive evaluation of our work and the constructive feedback! To address the main concerns, we have:

– Clarified a major misunderstanding of our instructions: Participants were only informed that they would receive different stimuli of medium intensity and were thus not aware that the stimulation temperature remained constant

– Implemented a new analysis to evaluate how participants rated their expectation and pain levels in the control condition

– Added a paragraph in the discussion in which we argue that our paradigm is comparable to previous studies

Below, we provide responses to each of the reviewers’ comments on our manuscript.

Reviewer #1 (Public Review):

Summary:  

In this important paper, the authors investigate the temporal dynamics of expectation of pain using a combined fMRI-EEG approach. More specifically, by modifying the expectations of higher or lower pain on a trial-to-trial basis, they report that expectations largely share the same set of activations before the administration of the painful stimulus, and that the coding of the valence of the stimulus is observed only after the nociceptive input has been presented. fMRIinformed EEG analysis suggested that the temporal sequence of information processing involved the Dorsolateral prefrontal cortex (DLPFC), the anterior insula, and the anterior cingulate cortex. The strength of evidence is convincing, and the methods are solid, but a few alternative interpretations about the findings related to the control group, as well as a more in-depth discussion on the correlations between the BOLD and EEG signals would strengthen the manuscript. 

Thank you for your positive evaluation! In the revised version of the manuscript, we elaborated on the control condition and the BOLD-EEG correlations in more detail.

Strengths:  

In line with open science principles, the article presents the data and the results in a complete and transparent fashion. 

From a theoretical standpoint, the authors make a step forward in our understanding of how expectations modulate pain by introducing a combination of spatial and temporal investigation. It is becoming increasingly clear that our appraisal of the world is dynamic, guided by previous experiences, and mapped on a combination of what we expect and what we get. New research methods, questions, and analyses are needed to capture these evolving processes.  

Thank you very much for these positive comments!

Weaknesses:  

The control condition is not so straightforward. Across the manuscript it is defined as "no expectation", and in the legend of Figure 1 it is mentioned that the third state would be "no prediction". However, it is difficult to conceive that participants would not have any expectations or predictions. Indeed, in the description of the task it is mentioned that participants were instructed that they would receive stimuli during "intermediate sensitive states". The results of the pain scores and expectations might support the idea that the control condition is situated in between the placebo and nocebo conditions. However, since this control condition was not part of the initial conditioning, and participants had no reference to previous stimuli, one might expect that some ratings might have simply "regressed to the mean" for a lack of previous experience. 

General considerations and reflections:  

Inducing expectations in the desired direction is not a straightforward task, and results might depend on the exact experimental conditions and the comparison group. In this sense, the authors' choice of having 3 groups of positive, negative, and "neutral" expectations is to be praised. On the other hand, also control groups form their expectations, and this can constitute a confounder in every experiment using expectation manipulation, if not appropriately investigated. 

Thank you for raising these important concerns! Firstly, as it seems that we did not explain the experimental procedure in a clear fashion, there appeared to be a general misunderstanding regarding our instructions. We want to emphasize that we did not tell participants that the stimulus intensity would always be the same, but that pain stimuli would be different temperatures of medium intensity. Furthermore, our instruction did not necessarily imply that our algorithm detected a state of medium sensitivity, but that the algorithm would not make any prediction, e.g., due to highly fluctuating states of pain sensitivity, or no clear-cut state of high or low pain sensitivity. We changed this in the Methods (ll. 556-560, 601-606, 612-614) and Results (ll. 181-192) sections of the manuscript to clarify these important features of our procedure.

Then, we absolutely agree that participants explicitly and implicitly form expectations regarding all conditions over time, including the control condition. We carefully considered your feedback and rephrased the control condition, no longer framing it as eliciting “no expectations” but as “neutral expectations” in the revised version of the manuscript. This follows the more common phrasing in the literature and acknowledges that participants indeed build up expectations in the control condition. However, we do still think that we can meaningfully compare the placebo and nocebo condition to the control condition to investigate the neuronal underpinnings of expectation effects. Independently of whether participants build up an expectation of “medium” intensities in the control condition, which caused them to perceive stimuli in line with this expectation, or if they simply perceived the stimuli as they were (of medium intensity) with limited effects of expectations, the crucial difference to the placebo and nocebo conditions is that there was no alteration of perception due to previous experiences or verbal information and no shift of perception from the actual stimulus intensity towards any direction in the control condition. This allowed us to compare the neural basis of a modulation of pain perception in either direction to a condition in which this modulation did not take place. 

Author response image 1.

Variability within conditions over time. Relative variability index for expectation (left) and pain ratings (right) per condition and measurement block. 

Lastly, we want to highlight that our finding of the control condition being rated in between the placebo and nocebo condition is in line with many previous studies that included similar control conditions and advanced our understanding of pain-related expectations (Bingel et al., 2011; Colloca et al., 2010; Shih et al., 2019). We thank the reviewer for the very interesting idea to evaluate the development of ratings in the control condition in more detail and added a new analysis to the manuscript in which we compared how much intra-subject variance was within the ratings of each of the three conditions and how much this variance changed over time. For this aim, we computed the relative variability index (Mestdagh et al., 2018), a measure that quantifies intra-subject variation over multiple ratings, and compared between the three conditions and the three measurement blocks. We observed differences in variances between conditions for both expectation (F(2,96) = 8.14, p < .001) and pain ratings (F(2,96) = 3.41, p = .037). For both measures, post-hoc tests revealed that there was significantly more variance in the placebo compared to the control condition (both p_holm < .05), but no difference between control and nocebo. The substantial and comparable variation in pain and expectation ratings in all three conditions (or at least between control and nocebo) shows that participants did not always expect and perceive the same intensity within conditions. Variance in expectation ratings decreased from the first block compared to the other two blocks (_F(1.35,64.64) = 5.69, p = .012; both p_holm < .05), which was not the case for pain ratings. Most importantly, there was no interaction effect of block and condition for neither expectation (_F(2.65,127.06) = 0.40, p = .728) nor pain ratings (F(4,192) = 0.48, p = .748), which implies that expectations were similarly dynamically updated in all conditions over the course of the experiment. This speak against a “regression to the mean” in the control condition and shows that control ratings fluctuated from trial to trial. We included this analysis and a more in-depth discussion of the choice of conditions in the Result (ll. 219-232) and Discussion (ll. 452-486) sections of the revised manuscript.

In addition, although fMRI is still (probably) the best available tool we have to understand the spatial representation of cortical processing, limitations about not only the temporal but even the spatial resolution should be acknowledged. Given the anatomical and physiological complexity of the cortical connections, as we know from the animal world, it is still well possible that subcircuits are activated also for positive and negative expectations, but cannot be observed due to the limitation of our techniques. Indeed, on an empirical/evolutionary basis it would remain unclear why we should have a system that waits for the valence of a stimulus to show differential responses. 

We agree that the spatial resolution of fMRI is limited and that our signal is often not able to dissociate different subcircuits. Whether on this basis differential processes occurred cannot be observed in fMRI but is indeed possible. We now include this reasoning in our Discussion (ll. 373-377):

“Importantly, the spatial resolution of fMRI is limited when it comes to discriminating whether the same pattern of activity is due to identical activation or to activation in different sub-circuits within the same area. Nonetheless, the overlap of areas is an indicator for similar processes involved in a more general preparation process.”

Also, moving in a dimension of network and graph theory, one would not expect single areas to be responsible for distinct processes, but rather that they would integrate information in a shared way, potentially with different feedback and feedforward communications. As such, it becomes more difficult to assume the insula is a center for coding potential pain, perhaps more of a node in a system that signals potential dangers for the integrity of the body. 

We appreciate the feedback on our interpretation of our results and agree that the overall network activity most likely determines how a large part of expectations and pain are coded. We therefore adjusted the Discussion, embedding the results in an interpretation considering networks (ll. 427-430, 432-435,438-442 ). 

The authors analyze the EEG signal between 0.5 to 128 Hz, finding significant results in the correlation between single-trial BOLD and EEG activity in the higher gamma range (see Figure 6 panel C). It would be interesting to understand the rationale for including such high frequencies in the signal, and the interpretation of the significant correlation in the high gamma range. 

On a technical level, we adapted our EEG processing pipeline from Hipp et al. (2011) who similarly investigated signals up to 128 Hz. Of note, the spectral smoothing was adjusted to match 3/4 octave, meaning that the frequency resolution at 128 Hz is rather broad and does not only contain oscillations at 128 Hz sharp. Gamma oscillations in general have repeatedly been reported in relation to pain and feedforward signals reflecting noxious information (e.g. Ploner et al., 2017; Strube et al., 2021). Strube et al. (2021) reported the highest effects of pain stimulus intensity and prediction error processing at high gamma frequencies (100 and 98 Hz, respectively). These findings could also serve as basis to interpret our results in this frequency range: If anticipatory activation in the ACC is linked to high gamma oscillations, which appear to play an important role in feedforward signaling of pain intensity and prediction errors, this could indicate that later processing of intensity in this area is already pre-modulated before the stimulus actually occurs. Of note: although not significant, it looks as if the cluster extends further into pain processing on a descriptive level. We added additional explanation regarding the interpretation of the correlation in the Discussion (ll. 414425):

“The link between anticipatory activity in the ACC and EEG oscillatory activity was observed in the high gamma band, which is consistent with findings that demonstrate a connection between increased fMRI BOLD signals and a relative shift from lower to higher frequencies (Kilner et al., 2005). Gamma oscillations have been repeatedly reported in the context of pain and expectations and have been interpreted as reflecting feedforward signals of noxious information ( e.g. Ploner et al., 2017; Strube et al., 2021). In combination with our findings, this might imply that high frequency oscillations may not only signal higher actual or perceived pain intensity during pain processing (Nickel et al., 2022; Ploner et al., 2017; Strube et al., 2021; Tu et al., 2016), but might also be instrumental in the transfer of directed expectations from anticipation into pain processing.”

Reviewer #2 (Public Review):  

I think this is a very promising paper. The combination of EEG and fMRI is unique and original. However, I also have some suggestions that I think could help improve the manuscript. 

This manuscript reports the findings of an EEG-fMRI study (n = 50) on the effects of expectations on pain. The combination of EEG with fMRI is extremely original and well-suited to study the transition from expectation to perception. However, I think that the current treatment of the data, as well as the way that the manuscript is currently written, does not fully capitalize on the potential of this unique dataset. Several findings are presented but there is currently no clear message coming out of this manuscript. 

First, one positive point is that the experimental manipulation clearly worked. However, it should be noted that the instructions used are not typical of studies on placebo/nocebo. Participants were not told that the stimulations would be of higher/lower intensity. Rather, they were told that objective intensities were held constant, but that EEG recordings could be used to predict whether they would perceive the stimulus as more or less intense. I think that this is an interesting way to manipulate expectations, but there could have been more justification in the introduction for why the authors have chosen this unusual procedure. 

Most importantly, we again want to emphasize again that participants were not aware that the stimulation temperature was always the same but were informed that they would receive different stimuli of medium intensity. We now clarify this in the revised Results (ll. 190-192) and Methods (ll. 612-614) sections.

While we agree that our procedure was not typical, we do not think that the manipulation is not comparable to previous studies on pain-related expectations. To our knowledge, either expectations regarding a treatment that changes pain perception (treatment expectancy) or expectations regarding stimulus intensities (stimulus expectancy) are manipulated (see Atlas & Wager, 2014). In our study, participants received a cue that induced expectations in regard to a ”treatment”, although in this case the “treatment” came from changes in their own brain activity. This is comparable to studies using TENS-devices that are supposedly changing peripheral pain transmission (Skvortsova et al., 2020). Thus, although not typical, our paradigm could be classified as targeting treatment expectancies and allowed us to examine effects on a trial-by-trial level within subjects. We added a paragraph regarding the comparability of our paradigm with previous studies in the Discussion of the revised manuscript (ll. 452-464) .

Also, the introduction mentions that little is known about potential cerebral differences between expectations of high vs. low pain expectations. I think the fear conditioning literature could be cited here. Activations in ACC, SMA, Ins, parahippocampal gyrus, PAG, etc. are often associated with upcoming threat, whereas activations vmPFC/default mode network are associated with safety. 

We thank you for your suggestions to add literature on fear conditioning. We agree there is some overlap between fear conditioning and expectation effects in humans, but we also believe there are fundamental differences regarding their underlying processes and paradigms. E.g. the expectation effects are not driven by classical learning algorithms but act in a large amount as self-fulfilling prophecies (see e.g. Jepma et al., 2018). However, we now acknowledge the similarities e.g in the recruitment of the insula and the vmPFC of the modalities in our Introduction (ll. 132-136 ).

The fact that the authors didn't observe a clearer distinction between high and low expectations here could be related to their specific instructions that imply that the stimulus is the same and that it is the subjective perception that is expected to change. In any case, this is a relatively minor issue that is easy to address. 

We apologize again for the lack of clarity in our instructions: Participants were unaware that they would receive the exact same stimulus. The clear effects of the different conditions on expectation and pain ratings also challenge the notion that participants always expected the same level of stimulation and/or perception. Additionally, if participants were indeed expecting a consistent level of intensity in all conditions, one would also assume to see the same anticipatory activation in the control condition as in the placebo and nocebo conditions, which is not the case. Thus, we respectfully disagree that the common effects might be explained by our instructions but would argue that they indeed reflect common (anticipatory) processes of positive and negative expectations.

Towards the end of the introduction, the authors present the aims of the study in mainly exploratory terms: 

(1) What are the differences between anticipation and perception? 

(2) What regions display a difference between high and low expectations (high > low or low < high) vs. an effect of expectation regardless of the direction (high and low different than neutral)? 

I think these are good questions, but the authors should provide more justification, or framework, for these questions. More specifically, what will they be able to conclude based on their observations? 

For instance (note that this is just an example to illustrate my point. I encourage the authors to come up with their own framework/predictions) : 

(1) Possibility #1: A certain region encodes expectations in a directed fashion (high > low) and that same region also responds to perception in the same direction (high > low). This region would therefore modulate pain by assimilating perception towards expectations. 

(2) Possibility # 2: different regions are involved in expectation and perception. Perhaps this could mean that certain regions influence pain processing through descending facilitation for instance...  

Thank you for pointing out that our hypotheses were not crafted carefully enough. We tried to give better explanations for the possible interpretations of our hypotheses. Additionally, we interpreted our results on the background of a broader framework for placebo and nocebo effects (predictive coding) to derive possible functions of the described brain areas. We embedded this in our Introduction (ll. 74-86, 158-175 ) and Discussion (ll. 384-388 ), interpreting the anticipatory activity and the activity during pain processing in the context of expectation formation as described in Büchel et al. (2014).

Interpretation derived from our framework (ll. 384-388):

e.g.: “Following the framework of predictive coding, our results would suggest that the DPMS is the network responsible for integrating ascending signals with descending signals in the pain domain and that this process is similar for positive and negative valences during anticipation of pain but differentiates during pain processing.”

Regarding analyses, I think that examining the transition from expectations to perception is a strong angle of the manuscript given the EGG-fMRI nature of the study. However, I feel that more could have been done here. One problem is that the sequence of analyses starts by identifying an fMRI signal of interest and then attempts to find its EEG correlates. The problem is that the low temporal resolution of fMRI makes it difficult to differentiate expectation from perception, which doesn't make this analysis a good starting point in my opinion. Why not start by identifying an EEG signal that differentiates perception vs expectation, and then look for its fMRI correlates?  

We appreciate your feedback on the transition from expectations to perceptions and also think that additional questions could be answered with our data set. However, based on the literature we had specific hypotheses regarding specific brain areas, and we therefore decided to start from the fMRI data with the superior spatial resolution and EEG was used to focus on the temporal dynamics within the areas important for anticipatory processes. We share the view that many different approaches in analyzing our data are possible. On the other hand, identifying relevant areas based on EEG characteristics inherits even more uncertainty due to the spatial filtering of the EEG signal. For the research question of this study a more accurate evaluation of the involved areas and the related representation was more important. We therefore decided to only implement the procedure already present in the manuscript. 

Finally, I found the hypotheses on "valenced" vs. "absolute" effects a little bit more difficult to follow. This is because "neutral" is not really neutral: it falls in between low and high. If I follow correctly, participants know that the temperature is always the same. Therefore, if they are told that the machine cannot predict whether their perception is going to be low or high, then it must be because it is likely to be in between. Ratings of expectation and pain ratings confirm that. The neutral condition is not "devoid" of expectations as the authors suggest.

Therefore, it would make sense to look at regions with the following pattern low > neutral > high, or vice-versa, low < neutral < high. Low & high being different than neutral is more difficult to interpret. I don't think that you can say that it reflects "absolute" expectations because neutral is also the expectation of a medium temperature. Perhaps it reflects "certainty/uncertainty" or something like that, but it is not clear that it reflects "expectations". 

Thank you for your valuable feedback! We considered your concerns about the interpretation of our results and completely agree that the control condition cannot be interpreted as void of expectations (ll. 119-123). We therefore evaluated the control condition in more detail in a separate analysis (ll. 219-232) and integrated a new assessment of the conditions into the Discussion (ll. 465-486). We changed the phrasing of our control condition to “neutral expectations”, as we agree that the control condition is not void of expectations and this phrasing is more in line with other studies (e.g. Colloca et al., 2010; Freeman et al., 2015; Schmid et al., 2015). We would argue that the neutral expectations can still be meaningfully compared to positive and negative expectations because only the latter shift expectations and perception in one direction. Thus, we changed our wording throughout the manuscript to acknowledge that we indeed did not test for general effects of expectations vs. no expectations, but for effects of directed expectations. Please also see our reasoning regarding the control condition in response to Reviewer 1, in which we addressed the interpretation of the control condition. We therefore still believe that the contrasts that we calculated between conditions are valid. The proposed new contrast largely overlaps with our differential contrast low>high and vice versa already reported in the manuscript (for additional results also see Supplements).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Figure 6, panel C. The figure mentions Anterior Cingulate Cortex R, whereas the legend mentions left ACC. Please check. 

Thanks for catching this, we changed the figure legend accordingly.

Reviewer #2 (Recommendations For The Authors):  

- I don't think that activity during the rating of expectations is easily interpretable. I think I would recommend not reporting it. 

The majority of participants completed the expectation rating relatively quickly (M = 2.17 s, SD = 0.35 s), which resulted in the overlap between the DLPFC EEG cluster and the expectation rating encompassing only a limited portion of the cluster (~ 1 s). We agree that this activity still is more difficult to interpret, yet we have decided to report it for reasons of completeness.

- The effects on SIIPS are interesting. I think that it is fine to present them as a "validation" of what was observed with pain ratings, but it also seems to give a direction to the analyses that the authors don't end up following. For instance, why not try other "signatures" like the NPS or signatures of pain anticipation? Also, why not try to look at EEG correlates of SIIPS? I don't think that the authors "need" to do any of that, but I just wanted to let them know that SIIPS results may stir that kind of curiosity in the readers.  

While this would be indeed very interesting, these additional analyses are not directly related to our current research question. We fear that too many analyses could be confusing for the readers. Nonetheless, we are grateful for your suggestion and will implement additional brain signatures in future studies. 

- The shock was calibrated to be 60%. Why not have high (70%) and low (30%) conditions at equal distances from neutral, like 80% and 40% for instance? The current design makes it hard to distinguish high from control. Perhaps the "common" effects of high + low are driven by a deactivation for low (30%)?  

We appreciate your feedback! We adjusted the temperature during the test phase to counteract habituation typically happening with heat stimuli. We believe that this was a good measure as participants rated the control condition at roughly VAS 50 (M = 51.40) which was our target temperature and then would be equidistant to the VAS 70 and VAS 30 during conditioning when no habituation should have taken place yet. We further tested whether participants rated placebo and nocebo trials at equal distances from the control condition and found no existent bias for either of the conditions. To do this, we computed the individual placebo effect (control minus placebo) and nocebo effect (nocebo minus control) for each participant during the test phase and statistically compared whether they differed in terms of magnitude. There was no significant difference between placebo and nocebo effects for both expectation (placebo effect M = 14.25 vs. nocebo effect M = 17.22, t(49) = 1.92, p = .061) and pain ratings (placebo effect M = 6.52 vs. nocebo effect M = 5.40, t(49) = -1.11, p = .274). This suggests that our expectation manipulation resulted in comparable shifts in expectation and pain ratings away from the control condition for both the placebo and nocebo condition and thus hints against any bias of the conditioning temperatures. Please also note that the analysis of the common effects was masked for differences of the high and low, therefore the effects cannot be driven by one condition by itself.

- If I understand correctly, all fMRI contrasts were thresholded with FWE. This is fine, but very strict. The authors could have opted for FDR. Maybe I missed something here....  

While it is true that FDR is the more liberal approach, it is not valid for spatially correlated fMRI data and is no longer available in SPM for the correction of multiple comparisons. The newly implemented topological peak based FDR correction is comparably sensitive with the FWE correction (see. Chumbley et al. BELEG). We opted for the slightly more conservative approach in our preregistration (_p_FWE < .05), therefore a change of the correction is not possible.

Altogether, I think that this is a great study. The combination of EEG and fMRI is truly unique and affords many opportunities to examine the transition from expectations to perception. The experimental manipulation of expectations seems to have worked well, and there seem to be very promising results. However, I think that more could have been done. At least, I would recommend trying to give more of a theoretical framework to help interpret the results.  

We are very grateful for your positive feedback. We took your suggestion seriously and tried to implement a more general framework from the literature (see Büchel et al., 2014) to provide a better explanation for our results.

References

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Author response:

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

Reviewer 1:

(1) The notion of a “root” causal gene - which the authors define based on a graph theoretic notion of topologically sorting graphs - requires a graph that is directed and acyclic. It is the latter that constitutes an important weakness here - it simply is a large simplification of human biology to draw out a DAG including hundreds of genes and a phenotype Y and to claim that the true graph contains no cycles.

We agree that real causal graphs in biology often contain cycles. We now include additional experimental results with cyclic directed graphs in the Supplementary Materials. RCSP outperformed the other algorithms even in this setting, but we caution the reader that the theoretical interpretation of the RCS score may not coincide with a root causal effect when cycles exist:

“We also evaluated the algorithms on directed graphs with cycles. We generated a linear SEM over ρ + 1 = 1000 variables in . We sampled the coefficient matrix β from a Bernoulli (1/(p − 1)) distribution but did not restrict the non-zero coefficients to the upper triangular portion of the matrix. We then proceeded to permute the variable ordering and weight each entry as in the Methods for the DAG. We repeated this procedure 30 times and report the results in Supplementary Figure 3.

RCSP again outperformed all other algorithms even in the cyclic case. The results suggest that conditioning on the surrogate ancestors also estimates the RCS well even in the cyclic case. However, we caution that an error term E_i can affect the ancestors of when cycles exist. As a result, the RCS may not isolate the causal effect of the error term and thus not truly coincide with the notion of a root causal effect in cyclic causal graphs.”

(2) I also encourage the authors to consider more carefully when graph structure learned from Perturb-seq can be ported over to bulk RNA-seq. Presumably this structure is not exactly correct - to what extent is the RCSP algorithm sensitive to false edges in this graph? This leap - from cell line to primary human cells - is also not modeled in the simulation. Although challenging - it would be ideal for the RCSP to model or reflect the challenges in correctly identifying the regulatory structure.

We now include additional experimental results, where we gradually increased the incongruence between the DAG modeling the Perturb-seq and the DAG modeling the bulk RNA-seq using a mixture of graphs. The performance of RCSP degraded gradually, rather than abruptly, with increasing incongruence. We therefore conclude that RCSP is robust to differences between the causal graphs representing Perturb-seq and bulk RNA-seq:

“We next assessed the performance of RCSP when the DAG underlying the Perturb-seq data differs from the DAG underlying the bulk RNA-seq data. We considered a mixture of two random DAGs in bulk RNA-seq, where one of the DAGs coincided with the Perturb-seq DAG and second alternate DAG did not. We instantiated and simulated samples from each DAG as per the previous subsection. We generated 0%, 25%, 50%, 75%, and 100% of the bulk RNA-seq samples from the alternate DAG, and the rest from the Perturb-seq DAG. We ideally would like to see the performance of RCSP degrade gracefully, as opposed to abruptly, as the percent of samples derived from the alternate DAG increases.

We summarize results in Supplementary Figure 4. As expected, RCSP performed the best when we drew all samples from the same underlying DAG for Perturb-seq and bulk RNA-seq. However, the performance of RCSP also degraded slowly as the percent of samples increased from the alternate DAG. We conclude that RCSP can accommodate some differences between the underlying DAGs in Perturb-seq and bulk RNA-seq with only a mild degradation in performance.”

(3) It should also be noted that in most Perturb-seq experiments, the entire genome is not perturbed, and frequently important TFs (that presumably are very far “upstream” and thus candidate “root” causal genes) are not expressed highly enough to be detected with scRNA-seq. In that context - perhaps slightly modifying the language regarding RCSP’s capabilities might be helpful for the manuscript - perhaps it would be better to describe it as an algorithm for causal discovery among a set of genes that were perturbed and measured, rather than a truly complete search for causal factors. Perhaps more broadly it would also benefit the manuscript to devote slightly more text to describing the kinds of scenarios where RCSP (and similar ideas) would be most appropriately applied - perhaps a well-powered, phenotype annotated Perturb-seq dataset performed in a disease relevant primary cell.

We now clarify that Perturb-seq can only identify root causal genes among the perturbed set of genes in the Discussion:

“Modern genome-wide Perturb-seq datasets also adequately perturb and measure only a few thousand, rather than all, gene expression levels. RCSP can only identify root causal genes within this perturbed and measured subset.”

We now also describe the scenario where RCSP can identify root causal genes well in the Introduction:

“Experiments demonstrate marked improvements in performance, when investigators have access to a large bulk RNA-seq dataset and a genome-wide Perturb-seq dataset from a cell line of a disease-relevant tissue.”

Reviewer 2:

(1) The process from health-to-disease is not linear most of the time with many checks along the way that aim to prevent the disease phenotype. This leads to a non-deterministic nature of the path from health-to-disease. In other words, with the same root gene perturbations, and depending on other factors outside of gene expression, someone may develop a phenotype in a year, another in 10 years and someone else never. Claiming that this information is included in the error terms might not be sufficient to address this issue. The authors should discuss this limitation.

The proposed approach accommodates the above non-deterministic nature. The error terms of model factors that are outside of gene expression. We model the relation from gene expression to Y as probabilistic rather than deterministic because , where E_Y introduces stochasticity. Thus, two individuals with the same instantiations of the root causes may develop disease differently. We now clarify this in Methods:

“The error terms model root causes that are outside of gene expression, such as genetic variation or environmental factors. Moreover, the relation from gene expression to Y is stochastic because , where E_Y introduces the stochasticity. Two individuals may therefore have the exact same error term values over but different instantiations of Y.”

(2) The paper assumes that the network connectivity will remain the same after perturbation. This is not always true due to backup mechanisms in the cells. For example, suppose that a cell wants to create product P and it can do it through two alternative paths: Path #1: A → B → P, Path #2: A → C → P. Now suppose that path #1 is more efficient, so when B can be produced, path #2 is inactive. Once the perturbation blocks element B from being produced, the graph connectivity changes by activation of path #2. I did not see the authors taking this into consideration, which seems to be a major limitation in using Perturb-seq results to infer conductivities.

We agree that backup mechanisms can exist and therefore now include additional experimental results, where we gradually increased the incongruence between the DAG modeling the Perturb-seq and the DAG modeling the bulk RNA-seq using a mixture of graphs. The performance of RCSP degraded gradually, rather than abruptly, with increasing incongruence. We therefore conclude that RCSP is robust to differences between the causal graphs representing Perturb-seq and bulk RNA-seq:

“We next assessed the performance of RCSP when the DAG underlying the Perturb-seq data differs from the DAG underlying the bulk RNA-seq data. We considered a mixture of two random DAGs in bulk RNA-seq, where one of the DAGs coincided with the Perturb-seq DAG and second alternate DAG did not. We generated 0%, 25%, 50%, 75%, and 100% of the bulk RNA-seq samples from the alternate DAG, and the rest from the Perturb-seq DAG. We ideally would like to see the performance of RCSP degrade gracefully, as opposed to abruptly, as the percent of samples derived from the alternate DAG increases.

We summarize results in Supplementary Figure 4. As expected, RCSP performed the best when we drew all samples from the same underlying DAG for Perturb-seq and bulk RNA-seq. However, the performance of RCSP also degraded slowly as the percent of samples increased from the alternate DAG. We conclude that RCSP can accommodate some differences between the underlying DAGs in Perturb-seq and bulk RNA-seq with only a mild degradation in performance.”

(3) There is substantial system heterogeneity that may cause the same phenotype. This goes beyond the authors claim that although the initial gene causes of a disease may differ from person to person, at some point they will all converge to changes in the same set of “root genes.” This is not true for many diseases, which are defined based on symptoms and lab tests at the patient level. You may have two completely different molecular pathologies that lead to the development of the same symptoms and test results. Breast cancer with its subtypes is a prime example of that. In theory, this issue could be addressed if there is infinite sample size. However, this assumption is largely violated in all existing biological datasets.

The proposed method accommodates the above heterogeneity. We do not assume that the root causes affect the same set of root causal genes. Instead the root causes and root causal genes may vary from person to person. We write in the Introduction:

“The problem is further complicated by the existence of complex disease, where a patient may have multiple root causal genes that differ from other patients even within the same diagnostic category... We thus also seek to identify patient-specific root causal genes in order to classify patients into meaningful biological subgroups each hopefully dictated by only a small group of genes.”

The root causal genes may further affect different downstream genes at the patient-specific level. However root causal genes tend to have many downstream effects so that virtually every gene expression level becomes correlated with Y. We now clarify this by describing the omnigenic root causal model in the Introduction as follows:

“Finally, application of the algorithm to two complex diseases with disparate pathogeneses recovers an omnigenic root causal model, where a small set of root causal genes drive pathogenesis but impact many downstream genes within each patient. As a result, nearly all gene expression levels are correlated with the diagnosis at the population level.”

(4) Were the values of the synthetic variables Z-scored?

Yes, all variables were z-scored. We now clarify this in Methods:

“We also standardized all variables before running the regressions to prevent gaming of the marginal variances in causal discovery (Reisach et al., 2021; Ng et al., 2024).”

(5) The algorithm seems to require both RNA-seq and Perturb-seq data (Algorithm 1, page 14). Can it function with RNA-seq data only? What will be different in this case?

The algorithm cannot function with observational bulk RNA-seq data only. We included Perturb-seq because causal discovery with observational RNA-seq data alone tends to be inaccurate and unstable, as highlighted by the results of CausalCell. We further emphasize that we do not rely on d-separation faithfulness in Methods, which is typically required for causal discovery from observational data alone:

“We can also claim the backward direction under d-separation faithfulness. We however avoid making this additional assumption because real biological data may not arise from distributions obeying d-separation faithfulness in practice.”

(6) Synthetic data generation: how many different graphs (SEMs) did they start from? (30?) How many samples per graph? Did they test different sample sizes?

We now clarify that we generate 30 random SEMs, each associated with a DAG. We used 200 samples for the bulk RNA-seq to mimic a relatively large but common sample size. We also drew 200 samples for each perturbation or control in the Perturb-seq data. We did not consider multiple sample sizes due to the time required to complete each run. Instead, we focused on a typical scenario where investigators would apply RCSP. We now write the following in the Methods:

“We drew 200 samples for the bulk RNA-seq data to mimic a large but common dataset size. We introduced knockdown perturbations in Perturb-seq by subtracting an offset of two in the softplus function: . We finally drew 200 samples for the control and each perturbation condition to generate the Perturb-seq data. We repeated the above procedure 30 times.” We also include the following in Results:

“We obtained 200 cell samples from each perturbation, and another 200 controls without perturbations. We therefore generated a total of 2501 × 200 = 500,200 single cell samples for each Perturb-seq dataset. We simulated 200 bulk RNA-seq samples.”

(7) The presentation of comparative results (Supplementary Figures 4 and 7) is not clear. No details are given on how these results were generated. (what does it mean “The first column denotes the standard deviation of the outputs for each algorithm?”) Why all other methods have higher SD differences than RCSP? Is it a matter of scaling? Shouldn’t they have at least some values near zero since the authors “added the minimum value so that all histograms begin at zero?”

Each of these supplementary figures contains a 6 by 3 table of figures. By the first column, we mean column one (with rows 1 through 6) of each figure. The D-RCS and D-SD scores represent standard deviations of the RCS and SD scores from zero of each gene, respectively. We can similarly compute the standard deviation of the outputs of the algorithms. We now clarify this in the Supplementary Materials:

“The figure contains 6 rows and 3 columns. Similar to the D-RCS, we can compute the standard deviation of the output of each algorithm from zero for each gene. The first column in Supplementary Figure 7 denotes the histograms of these standard deviations across the genes.”

Many histograms do not appear to start at zero because the bars are too small to be visible. We now clarify this in the Supplementary Materials as well:

“Note that the bars at zero are not visible for many algorithms, since only a few genes attained standard deviations near the minimum.”

(8) Why RCSP results are more like a negative binomial distribution and every other is kind of normal?

All other methods have higher standard deviations than RCSP because they fail to compute an accurate measure of the root causal effect. Recall that, just like a machine has a few root causal problems, only a few root casual genes have large root causal effects under the omnigenic root causal model. The results of RCSP look more like a negative binomial distribution because most RCS scores are concentrated around zero and only a few RCS scores are large – consistent with the omnigenic root causal model. The other algorithms fail to properly control for the upstream genes and thus attain large standard deviations for nearly all genes. We now clarify these points in the Supplementary Materials as follows:

“If an algorithm accurately identifies root causal genes, then it should only identify a few genes with large conditional root causal effects under the omnigenic root causal model. The RCSP algorithm had a histogram with large probability mass centered around zero with a long tail to the right. The standard deviations of the outputs of the other algorithms attained large values for nearly all genes. Incorporating feature selection and causal discovery with CausalCell introduced more outliers in the histogram of ANM. We conclude that only RCSP detected an omnigenic root causal model.”

(9) What is the significance of genes changing expression “from left to right” in a UMAP plot? (e.g., Fig. 3h and 3g)

The first UMAP dimension captured the variability of the RCS scores for most root causal genes. As a result, we could focus our analysis on the black cluster in Figure 3 (g) with large RCS scores in the subsequent pathway enrichment analysis summarized in Figure 3 (j). If two dimensions were involved, then we would need to analyze at least two clusters (e.g., black and pink), but this was not the case. We now clarify this in Results:

“The RCS scores of most of the top genes exhibited a clear gradation increasing only from the left to the right hand side of the UMAP embedding; we plot an example in Figure 3 (h). We found three exceptions to this rule among the top 30 genes (example in Figure 3 (i) and see Supplementary Materials). RCSP thus detected genes with large RCS scores primarily in the black cluster of Figure 3 (g). Pathway enrichment analysis within this cluster alone yielded supra-significant results on the same pathway detected in the global analysis...”

(10) The authors somewhat overstate the novelty of their algorithm. Representation of GRNs as causal graphs dates back in 2000 with the work of Nir Friedman in yeast. Other methods were developed more recently that look on regulatory network changes at the single sample level which the authors do not seem to be aware (e.g., Ellington et al, NeurIPS 2023 workshop GenBio and Bushur et al, 2019, Bioinformatics are two such examples). The methods they mention are for single cell data and they are not designed to connect single sample-level changes to a person’s phenotype. The RCS method needs to be put in the right background context in order to bring up what is really novel about it.

We agree that many methods already exist for uncovering associational, predictive (Markov, neighborhood) and causal gene regulatory networks. We now cite the above papers. However, the novelty in our manuscript is not causal graph discovery, but rather estimation of root causal effects, detection of root causal genes, and the proposal of the omnigenic root causal model. We now clarify this in the

Introduction:

“Many algorithms focus on discovering associational or predictive relations, sometimes visually represented as gene regulatory networks (Costa et al., 2017; Ellington et al., 2023). Other methods even identify causal relations (Friedman et al., 2000; Wang et al., 2023; Wen et al., 2000; Buschur et al., 2000), but none pinpoint the first gene expression levels that ultimately generate the vast majority of pathogenesis. Simply learning a causal graph does not resolve the issue because causal graphs do not summarize the effects of unobserved root causes, such as unmeasured environmental changes or variants, that are needed to identify all root causal genes. We therefore define the Root Causal Strength (RCS) score...”

Reviewer 3:

(1) Several assumptions of the method are problematic. The most concerning is that the observational expression changes are all causally upstream of disease. There is work using Mendelian randomization (MR) showing that the opposite is more likely to be true: most differential expression in disease cohorts is a consequence rather than a cause of disease (Porcu et al., 2021). Indeed, the oxidative stress of AMD has known cellular responses including the upregulation of p53. The authors need to think carefully about how this impacts their framework. Can the theory say anything in this light? Simulations could also be designed to address robustness.

Strictly speaking, we believe that differential expression in disease most likely has a cyclic causal structure: gene expression causes a diagnosis or symptom severity, and a diagnosis or symptom severity lead to treatments and other behavioral changes that perturb gene expression. For example, revTMWR in Porcu et al. (2021) uses trans-variants that are less likely to directly cause gene expression and instead directly cause a phenotype. However, TWMR as proposed in Porcu et al. (2019) instead uses cis-eQTLs and finds many putative causal relations from gene expression to phenotype. Thus, both causal directions likely hold.

RCSP uses disease-relevant tissue believed to harbor gene expression levels that cause disease. However, RCSP theoretically cannot handle the scenario where Y is a non-sink vertex and is a parent of a gene expression level because modern Perturb-seq datasets usually do not perturb or measure Y. We therefore empirically investigated the degree of error by running experiments, where we set Y to a non-sink vertex, so that it can cause gene expression. We find that the performance of RCSP degrades considerably for gene expression levels that contain Y as a parent. Thus RCSP is sensitive to violations of the sink target assumption:

“We finally considered the scenario where Y is a non-sink (or non-terminal) vertex. If Y is a parent of a gene expression level, then we cannot properly condition on the parents because modern Perturbseq datasets usually do not intervene on Y or measure Y . We therefore empirically investigated the degradation in performance resulting from a non-sink target Y, in particular for gene expression levels where Y is a parent. We again simulated 200 samples from bulk RNA-seq and each condition of Perturbseq with a DAG over 1000 vertices, an expected neighborhood size of 2 and a non-sink target Y . We then removed the outgoing edges from Y and resampled the DAG with a sink target. We compare the results of RCSP for both DAGs in gene expression levels where Y is a parent. We plot the results in Supplementary Figure 5. As expected, we observe a degradation in performance when Y is not terminal, where the mean RMSE increased from 0.045 to 0.342. We conclude that RCSP is sensitive to violations of the sink target assumption.”

(2) A closely related issue is the DAG assumption of no cycles. This assumption is brought to bear because it is required for much classical causal machinery, but is unrealistic in biology where feedback is pervasive. How robust is RCSP to (mild) violations of this assumption? Simulations would be a straightforward way to address this.

We agree that real causal graphs in biology often contain cycles. We now include additional experimental results with cyclic directed graphs in the Supplementary Materials. RCSP outperformed the other algorithms even in this setting, but we caution the reader that the theoretical interpretation of the RCS score may not coincide with a root causal effect when cycles exist:

“We also evaluated the algorithms on directed graphs with cycles. We generated a linear SEM over p + 1 = 1000 variables in . We sampled the coefficient matrix β from a Bernoulli (1/(p − 1)) distribution but did not restrict the non-zero coefficients to the upper triangular portion of the matrix. We then proceeded to permute the variable ordering and weight each entry as in the Methods for the DAG. We repeated this procedure 30 times and report the results in Supplementary Figure 3.

RCSP again outperformed all other algorithms even in the cyclic case. The results suggest that conditioning on the surrogate ancestors also estimates the RCS well even in the cyclic case. However, we caution that an error term E_i can affect the ancestors of , when cycles exist. As a result, the RCS may not isolate the causal effect of the error term and thus not truly coincide with the notion of a root causal effect in cyclic causal graphs.”

(3) The authors spend considerable effort arguing that technical sampling noise in X can effectively be ignored (at least in bulk). While the mathematical arguments here are reasonable, they miss the bigger picture point that the measured gene expression X can only ever be a noisy/biased proxy for the expression changes that caused disease: 1) Those events happened before the disease manifested, possibly early in development for some conditions like neurodevelopmental disorders. 2) bulk RNA-seq gives only an average across cell-types, whereas specific cell-types are likely “causal.” 3) only a small sample, at a single time point, is typically available. Expression in other parts of the tissue and at different times will be variable.

We agree that many other sources of error exist. The causal model of RNA-expression in Methods corresponds to a single snapshot in time for each sample. We now clarify this in the Methods as follows:

“We represent a snapshot of a biological causal process using an SEM over obeying Equation (3).”

We thus only detect the root causal genes in a single snapshot in time for each sample in bulk RNA-seq. If we cannot detect the root causal effect in a gene due to the signal washing out over time as in (1), or if the root causal effect in different cell types cancel each other out to exactly zero in bulk as in (2), then we cannot detect those root causal genes even with an infinite sample size.

(4) While there are connections to the omnigenic model, the latter is somewhat misrepresented. The authors refer to the “core genes” of the omnigenic model as being at the end (longitudinal) of pathogenesis. The omnigenic model makes no statements about temporal ordering: in causal inference terminology the core genes are simply the direct causes of disease.

We now clarify that we use the word pathogenesis to mean the causal cascade from root causes to the diagnosis. In this case, the direct causes of the diagnosis correspond to the end of pathogenesis, while the root causes correspond to the beginning. For example, if , with Y a diagnosis, then X₁ is a root causal gene while X₂ is a core (direct causal) gene. We now clarify this in the Introduction:

“Root causes of disease correspond to the most upstream causes of a diagnosis with strong causal effects on the diagnosis. Pathogenesis refers to the causal cascade from root causes to the diagnosis. Genetic and non-genetic factors may act as root causes and affect gene expression as an intermediate step during pathogenesis. We introduce root causal gene expression levels – or root causal genes for short – that correspond to the initial changes to gene expression induced by genetic and non-genetic root causes that have large causal effects on a downstream diagnosis (Figure 1 (a)). Root causal genes differ from core genes that directly cause the diagnosis and thus lie at the end, rather than at the beginning, of pathogenesis (Boyle et al., 2017).”

(5) A key observation underlying the omnigenic model is that genetic heritability is spread throughout the genome (and somewhat concentrated near genes expressed in disease relevant cell types). This implies that (almost) all expressed genes, or their associated (e)SNPs, are “root causes”.

We now clarify that genetic heritability can be spread throughout the genome in the omnigenic root causal model as well in the Discussion:

“Further, each causal genetic variant tends to have only a small effect on disease risk in complex disease because the variant can directly cause Y or directly cause any causal gene including those with small root causal effects on Y ; thus, all error terms that cause Y can model genetic effects on Y. However, the root causal model further elaborates that genetic and non-genetic factors often combine to produce a few root causal genes with large root causal effects, where non-genetic factors typically account for the majority of the large effects in complex disease. Many variants may therefore cause many genes in diseases with only a few root causal genes.”

We finally add Figure 5 into the Discussion as a concrete example illustrating the omnigenic root causal model:

(6) The claim that root causal genes would be good therapeutic targets feels unfounded. If these are highly variable across individuals then the choice of treatment becomes challenging. By contrast the causal effects may converge on core genes before impacting disease, so that intervening on the core genes might be preferable. The jury is still out on these questions, so the claim should at least be made hypothetical.

We clarify that we do not claim that root causal genes are better treatment targets than core genes in terms of magnitudes of causal effects on the phenotype. For example, in the common cold with a virus as the root cause, giving a patient an antiviral will eliminate fever and congestion, but so will giving a decongestant and an antipyretic. We only claim that treating root causal genes can eliminate disease near its pathogenic onset, just like giving an antiviral can eliminate the viral load and stop pathogenesis. We write the following the Introduction:

“Treating root causal genes can modify disease pathogenesis in its entirety, whereas targeting other causes may only provide symptomatic relief... Identifying root causal genes is therefore critical for developing treatments that eliminate disease near its pathogenic onset.”

We also further clarify in the Discussion that root causal genes account for deleterious causal effects not captured by the diagnosis Y:

“We finally emphasize that the root causal model accounts for all deleterious effects of the root causal genes, whereas the core gene model only captures the deleterious effects captured by the diagnosis Y. For example, the disease of diabetes causes retinopathy, but retinopathy is not a part of the diagnostic criteria of diabetes. As a result, the gene expression levels that cause retinopathy but not the diagnosis of diabetes are not core genes, even though they are affected by the root causal genes.”

We do agree that root causal genes may differ substantially between patients, although it is unclear if the heterogeneity is too great to develop treatments.

(7) The closest thing to a gold standard I believe we have for “root causal genes” is integration of molecular QTLs and GWAS, specifically coloc/MR. Here the “E” of RCSP are explicitly represented as SNPs. I don’t know if there is good data for AMD but there certainly is for MS. The authors should assess the overlap with their results. Another orthogonal avenue would be to check whether the root causal genes change early in disease progression.

Colocalization and Mendelian randomization unfortunately cannot identify root causal effects because they all attempt, either heuristically (colocalization) or rigorously (MR), to identify variants that cause each gene expression level rather than variants that directly cause each gene expression level and thus make up the error terms. We therefore need new methods that can identify direct causal variants in order to assess overlap.

We checked whether root causal genes change early in disease progression using knowledge of pathogenesis. In particular, oxidative stress induces pathogenesis in AMD, and RCSP identified root causal genes involved in oxidative stress in AMD:

“The pathogenesis of AMD involves the loss of RPE cells. The RPE absorbs light in the back of the retina, but the combination of light and oxygen induces oxidative stress, and then a cascade of events such as immune cell activation, cellular senescence, drusen accumulation, neovascularization and ultimately fibrosis (Barouch et al., 2007). We therefore expect the root causal genes of AMD to include genes involved in oxidative stress during early pathogenesis. The gene MIPEP with the highest D-RCS score in Figure 3 (d) indeed promotes the maturation of oxidative phosphorylation-related proteins (Shi et al., 2011). The second gene SLC7A5 is a solute carrier that activates mTORC1 whose hyperactivation increases oxidative stress via lipid peroxidation (Nachef et al., 2021; Go et al., 2020). The gene HEATR1 is involved in ribosome biogenesis that is downregulated by oxidative stress (Turi et al., 2018). The top genes discovered by RCSP thus identify pathways known to be involved in oxidative stress.”

Similarly, T cell infiltration across the blood brain barrier initiates pathogenesis in MS, and RCSP identified root causal genes involved in this infiltration:

“Genes with the highest D-RCS scores included MNT, CERCAM and HERPUD2 (Figure 4 (d)). MNT is a MYC antagonist that modulates the proliferative and pro-survival signals of T cells after engagement of the T cell receptor (Gnanaprakasam et al., 2017). Similarly, CERCAM is an adhesion molecule expressed at high levels in microvessels of the brain that increases leukocyte transmigration across the blood brain barrier (Starzyk et al., 2000). HERPUD2 is involved in the endoplasmic-reticulum associated degradation of unfolded proteins (Kokame et al., 2000). Genes with the highest D-RCS scores thus serve key roles in known pathogenic pathways of MS.”

(8) The available Perturb-seq datasets have limitations beyond on the control of the authors. 1) The set of genes that are perturbed. The authors address this by simply sub-setting their analysis to the intersection of genes represented in the perturbation and observational data. However, this may mean that a true ancestor of X is not modeled/perturbed, limiting the formal claims that can be made. Additionally, some proportion of genes that are nominally perturbed show little to no actual perturbation effect (for example, due to poor guide RNA choice) which will also lead to missing ancestors.

We now clarify that Perturb-seq can only identify root causal genes among the adequately perturbed set of genes in the Discussion:

“Modern genome-wide Perturb-seq datasets also only adequately perturb and measure a few thousand, rather than all, gene expression levels. RCSP can only identify root causal genes within this perturbed and measured subset.”

(9) The authors provide no mechanism for statistical inference/significance for their results at either the individual or aggregated level. While I am a proponent of using effect sizes more than p-values, there is still value in understanding how much signal is present relative to a reasonable null.

We now explain that RCSP does not perform statistical inference in Methods because it is not clear how to define the appropriate cut-off for the RCS score under the null distribution:

“We focus on statistical estimation rather than statistical inference because Φ_i > 0 when E_i causes Y under mild conditions, so we reject the null hypothesis that Φ_i \= 0 for many genes if many gene expression levels cause Y. However, just like a machine typically breaks down due to only one or a few root causal problems, we hypothesize that only a few genes have large RCS scores Φ_i ≫ 0 even in complex disease.”

(10) I agree with the authors that age coming out of a “root cause” is potentially encouraging. However, it is also quite different in nature to expression, including being “measured” exactly. Will RCSP be biased towards variables that have lower measurement error?

We tested the above hypothesis by plotting sequencing depth against the D-RCS scores of each gene. We observed a small negative correlation between sequencing depth and D-RCS scores, indicating the D-RCS scores are slightly biased upwards with low sequencing depth. However, genes with the largest D-RCS scores exhibited a wide variety of sequencing depths in both MS and AMD, suggesting that sequencing depth has minimal effect on the largest D-RCS scores. We now explain these results for AMD in the Supplementary Materials:

“Theorem 1 states that RCS scores may exhibit bias with insufficient sequencing depth. The genes with large D-RCS scores may therefore simply have low sequencing depths. To test this hypothesis, we plotted sequencing depth against D-RCS scores. Consistent with Theorem 1, we observed a small negative correlation between D-RCS and sequencing depth (ρ \= −0.16, p=2.04E-13), and D-RCS scores exhibited greater variability at the lowest sequencing depths (Supplementary Figure 8). However, genes with the largest D-RCS scores had mean sequencing depths interspersed between 20 and 3000. We conclude that genes with the largest D-RCS scores had a variety of sequencing depths ranging from low to high.”

We also report the results for MS:

“We plot sequencing depth against the D-RCS scores of each gene similar to the AMD dataset. We again observed a small negative correlation (ρ \= −0.136, p_<_2.2E-16), indicating that genes with low sequencing depths had slightly higher D-RCS scores on average (Supplementary Figure 12). However, genes with the largest D-RCS scores again had a variety of sequencing depths. We conclude that sequencing depth has minimal correlation with the largest D-RCS scores.”

(11) Finally, it’s a stretch to call K562 cells “lymphoblasts.” They are more myeloid than lymphoid.

We now clarify that K562 cells are undifferentiated blast cells that can be induced to differentiate into lymphoblasts in Results:

“We next ran RCSP on 137 samples collected from CD4+ T cells of multiple sclerosis (MS; GSE137143) as well as Perturb-seq data of 1,989,578 undifferentiated blast cells that can be induced to differentiate into lymphoblasts, or the precursors of T cells and other lymphocytes.”

Author Response

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

eLife assessment

This valuable study advances our understanding of the brain nuclei involved in rapid-eye movement (REM) sleep regulation. Using a combination of imaging, electrophysiology, and optogenetic tools, the study provides convincing evidence that inhibitory neurons in the preoptic area of the hypothalamus influence REM sleep. This work will be of interest to neurobiologists working on sleep and/or brain circuitry.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper identifies GABA cells in the preoptic hypothalamus which are involved in REM sleep rebound (the increase in REM sleep) after selective REM sleep deprivation. By calcium photometry, these cells are most active during REM, and show more claim signals during REM deprivation, suggesting they respond to "REM pressure". Inhibiting these cells ontogenetically diminishes REM sleep. The optogenetic and photometry work is carried out to a high standard, the paper is well-written, and the findings are interesting.

We thank the reviewer for the detailed feedback and thoughtful comments on how to improve our manuscript. To address the reviewer’s concerns, we revised our discussion and added new data. Below, we address the concerns point by point.

Points that could be addressed or discussed:

(1) The circuit mechanism for REM rebound is not defined. How do the authors see REM rebound as working from the POAGAD2 cells? Although the POAGAD2 does project to the TMN, the actual REM rebound could be mediated by a projection of these cells elsewhere. This could be discussed.

We demonstrate thatPOA GAD2→TMN cells become more frequently activated as the pressure for REMs builds up, whereas inhibiting these neurons during high REMs pressure leads to a suppression of the REMs rebound. It is not known how POA GAD2→TMN cells encodeincreased REMs pressure and subsequently influence the REMs rebound. REMsdeprivation wasshown to changethe intrinsic excitabilityof hippocampal neurons and impact synaptic plasticity (McDermott et al., 2003; Mallick and Singh, 2011 ; Zhou et al., 2020) . We speculate that increasedREMs pressure leads to an increase in the excitabilityof POA->TMN neurons, reflected inthe increased number ofcalcium peaks. The increased excitability of POA GAD2→TMN neurons in turn likely leads to stronger inhibition of downstream REM-off neurons. Consequently, as soon as REMsdeprivation stops, there is an increased chance for enteringREMs. The time coursefor how long it takes till the POA excitability resettles toits baseline consequently sets a permissive time window for increasedamounts of REMs to recover its lostamount. For future studies, it would be interesting to map how quickly the excitability ofPOA neurons increases or decays as afunction of the lost or recovered amount of REMs andunravel the cellularmechanisms underlying the elevated activity of POAGAD2 →TMN neurons during highREMs pressure, e.g., whether changes in the expression of ion channels contribute to increasedexcitability of these neurons (Donlea et al., 2014) . As we mentioned in the Discussion, the POAalso projects to other REMs regulatorybrain regions such as the vlPAG and LH. Therefore, it remains to be tested whether POA GAD2 →TMN neurons also innervate these brain regions to potentially regulate REMs homeostasis. We explicitly state this now in the revised Discussion.

(2) The "POAGAD2 to TMN" name for these cells is somewhat confusing. The authors chose this name because they approach the POAGAD2 cells via retrograde AAV labelling (rAAV injected into the TMN). However, the name also seems to imply that neurons (perhaps histamine neurons) in the TMN are involved in the REM rebound, but there is no evidence in the paper that this is the case. Although it is nice to see from the photometry studies that the histamine cells are selectively more active (as expected) in NREM sleep (Fig. S2), I could not logically see how this was a relevant finding to REM rebound or the subject of the paper. There are many other types of cells in the TMN area, not just histamine cells, so are the authors suggesting that these non-histamine cells in the TMN could be involved?

We acknowledge that other types of neurons in the TMN may also be involved in the REMs rebound, and therefore inhibition of histamine neurons by POA GAD2 →TMN neurons may not be the sole source of the observed effect. To stress that other neurons within the TMN and/or brain regions may also contribute to the REMs rebound, we have revised the Results section.

We performed complementary optogenetic inhibition experiments of TMN HIS neurons to investigate if suppression of these neurons is sufficient to promote REMs. We foundthat SwiChR++ mediated inhibition of TMNHIS neurons increased theamount of REMs compared withrecordings without laser stimulation in the same mice and eYFPmice withlaser stimulation. Thus, while TMN HIS neurons may not bethe only downstream target of GABAergic POA neurons, these data suggest that they contribute to REMs regulation. We have incorporated these results in Fig. S4 .

We further investigated whether the activity of TMN HIS neurons changes between two REMs episodes. Assumingthat REMs pressure inhibits the activity ofREM-off histamine neurons,their firing rates should behighest right after REMs ends when REMs pressure is lowest, and progressivelydecay throughout the inter-REM interval, and reach their lowest activity right before the onset of REMs ( Park et al., 2021) , similarto the activity profile observed for vlPAG REM-off neurons (Weber et al., 2018).We indeed found that TMNHIS neurons displaya gradual decrease in their activity throughout theinter-REM interval and thus potentially reflect the build up of REM pressure ( Fig. S2F ).

(3) It is a puzzle why most of the neurons in the POA seem to have their highest activity in REM, as also found by Miracca et al 2022, yet presumably some of these cells are going to be involved in NREM sleep as well. Could the same POAGAD2-TMN cells identified by the authors also be involved in inducing NREM sleep-inhibiting histamine neurons (Chung et al). And some of these POA cells will also be involved in NREM sleep homeostasis (e.g. Ma et al Curr Biol)? Is NREM sleep rebound necessary before getting REM sleep rebound? Indeed, can these two things (NREM and REM sleep rebound) be separated?

Previous studies have demonstrated that POA GABAergic neurons, including those projecting to the TMN, are involved in NREMs homeostasis (Sherin et al., 1998; Gong et al., 2004; Ma et al., 2019) . Therefore, we predict that POA neurons that are involved in NREMs homeostasis are a subset of POA GAD2 → TMN neurons in our manuscript.

Using optrode recordings in the POA, we recently reported that 12.4% of neurons sampled have higher activity during NREMs compared with REMs; in contrast, 43.8% of neurons sampled have the highest activity during REMs compared with NREMs (Antila et al., 2022) indicating that the proportion of NREM max neurons is smaller compared with REM max neurons. These proportions of neurons are in agreement with previous results (Takahashi et al., 2009) . Considering fiber photometry monitors the average activity of a population of neurons as opposed to individual neurons, it is possible that we recorded neural activity across heterogeneous populations and therefore our findings may disguise the neural activity of the low proportion of NREMs neurons. We previously reported thespiking activity of POA GAD2 →TMN neurons at the singlecell level (Chung et al., 2017) . We have noted in themanuscript thatwhile the activity ofPOA GAD2→TMN neurons is highestduring REMs, theneural activity increases at NREMs → REMs transitions indicating these neurons also areactive during NREMs.

Using our REMs restriction protocol, we selectively restricted REMs leading to the subsequent rebound of REMs without affecting NREMs and consequently we did not find an increase in the amount of NREMs during the rebound or an increase in slow-wave activity, a key characteristic of sleep rebound that gradually dissipates during recovery sleep (Blake and Gerard, 1937; Williams et al., 1964; Rosa and Bonnet, 1985; Dijk et al., 1990; Neckelmann and Ursin, 1993; Ferrara et al., 1999) . However, during total sleep deprivation when subjects are deprived of both NREMs and REMs, isolating NREMs and REMs rebound may not be attainable.

(4) Is it possible to narrow down the POA area where the GAD2 cells are located more precisely?

POA can be subdivided into anatomically distinct regions such as medial preoptic area, median preoptic area, ventrolateral preoptic area, and lateral preoptic area (MPO, MPN, VLPO, and LPO respectively). To quantify where the virus expressing GAD2 cells and optic fibers are located within the POA, we overlaid the POA coronal reference images (with red boundaries denoting these anatomically distinct regions) over the virus heat maps and optic fiber tracts from datasets used in Figure 1A. We found that virus expression and optic fiber tracts were located in the ventrolateral POA, lateral POA, and the lateral part of medial POA, and included this description in the text.

Author response image 1.

Location of virus expression (A) and optic fiber placement (B) within subregions of POA.

(5) It would be ideal to further characterize these particular GAD2 cells by RT-PCR or RNA seq. Which other markers do they express?

Single-cell RNA-sequencing of POA neurons has revealed an enormous level of molecular diversity, consisting of nearly 70 subpopulations based on gene expression of which 43 can be clustered into inhibitory neurons (Moffitt et al., 2018) . One of the most studied subpopulation of POA sleep-active neurons contains the inhibitory neuropeptide galanin (Sherin et al., 1998; Gaus et al., 2002; Chung et al., 2017; Kroeger et al., 2018; Ma et al., 2019; Miracca et al., 2022) . Galanin neurons have been demonstrated to innervate the TMN (Sherin et al., 1998) yet, within the galanin neurons 7 distinct clusters exist based on unique gene expression (Moffitt et al., 2018) . In addition to galanin, we have previously performed single-cell RNA-seq on POA GAD2 → TMN neurons and identified additional neuropeptides such as cholecystokinin (CCK), corticotropin-releasing hormone (CRH), prodynorphin (PDYN), and tachykinin 1 (TAC1) as subpopulations of GABAergic POA sleep-active neurons (Chung et al., 2017; Smith et al., 2023) . Like galanin, these neuropeptides can also be divided into multiple subtypes as well (Chen et al., 2017; Moffitt et al., 2018) . Thus while these molecular markers for POA neurons are immensely diverse, we agree that characterizing the molecular identity of POA GAD2 → TMN neurons and investigating the functional relevance of these neuropeptides in the context of REMs homeostasis would enrich our understanding of a neural circuit involved in REMs homeostasis and can stand as a separate extension of this manuscript.

Reviewer #2 (Public Review):

Maurer et al investigated the contribution of GAD2+ neurons in the preoptic area (POA), projecting to the tuberomammillary nucleus (TMN), to REM sleep regulation. They applied an elegant design to monitor and manipulate the activity of this specific group of neurons: a GAD2-Cre mouse, injected with retrograde AAV constructs in the TMN, thereby presumably only targeting GAD2+ cells projecting to the TMN. Using this set-up in combination with technically challenging techniques including EEG with photometry and REM sleep deprivation, the authors found that this cell-type studied becomes active shortly (≈40sec) prior to entering REM sleep and remains active during REM sleep. Moreover, optogenetic inhibition of GAD2+ cells inhibits REM sleep by a third and also impairs the rebound in REM sleep in the following hour. Despite a few reservations or details that would benefit from further clarification (outlined below), the data makes a convincing case for the role of GAD2+ neurons in the POA projecting to the TMN in REM sleep regulation.

We thank the reviewer for the thorough assessment of our study and supportive comments. We have addressed your concerns in the revised manuscript, and our point by point response is provided below.

The authors found that optogenetic inhibition of GAD2+ cells suppressed REM sleep in the hour following the inhibition (e.g. Fig2 and Fig4). If the authors have the data available, it would be important to include the subsequent hours in the rebound time (e.g. from ZT8.5 to ZT24) to test whether REM sleep rebound remains impaired, or recovers, albeit with a delay.

We thank the reviewer for this comment and agree that it would be interesting to know how REMs changes for a longer period of time throughout the rebound phase. For Fig. 2, we did not record the subsequent hours. For Fig 4, we recorded the subsequent rebound between ZT7.5 and 10.5. When we compare the REMs amount during this 4 hr interval, the SwiChR mice have less REMs compared with eYFP mice with marginal significance (unpaired t-test, p=0.0641). We also plotted the cumulative REMs amount during restriction and rebound phases, and found that the cumulative amount of REMs was still lower in SwiChR mice than eYFP mice at ZT 10.5 (Author response image 2). Therefore, it will be interesting to record for a longer period of time to test when the SwiChR mice compensate for all the REMs that was lost during the restriction period.

Author response image 2.

Cumulative amount of REMs during REMs deprivation and rebound combined with optogenetic stimulation in eYFP and SwiChR groups. This data is shown as bar graphs in Figure 4.

REM sleep is under tight circadian control (e.g. Wurts et al., 2000 in rats; Dijk, Czeisler 1995 in humans). To contextualize the results, it would be important to mention that it is not clear if the role of the manipulated neurons in REM sleep regulation hold at other circadian times of the day.

Author response image 3.

Inhibiting POA GAD2→ TMN neurons at ZT5-8 reduces REMs. (A) Schematic of optogenetic inhibition experiments. (B) Percentage of time spent in REMs, NREMs and wakefulness with laser in SwiChR++ and eYFP mice. Unpaired t-tests, p = 0.0013, 0.0469 for REMs and wakeamount. (C) Duration of REMs, NREMs, and wake episodes. Unpaired t-tests, p = 0.0113 for NREMs duration. (D) Frequency of REMs, NREMs, and wake episodes. Unpaired t-tests, p = 0.0063, 0.0382 for REMs and NREMs frequency.

REMs propensity is largest towards the end of the light phase (Czeisler et al., 1980; Dijk and Czeisler, 1995; Wurts and Edgar, 2000). As a control, we therefore performed the optogenetic inhibition experiments of POA GAD2→TMN neurons during ZT5-8 (Author response image 3). Similar to our results in Figure 2, we found that SwiChR-mediated inhibition of POA GAD2 →TMN neurons attenuated REMs compared with eYFP laser sessions. These findings suggest our results are consistentat other circadian times of the day.

The effect size of the REM sleep deprivation using the vibrating motor method is unclear. In FigS4-D, the experimental mice reduce their REM sleep to 3% whereas the control mice spend 6% in REM sleep. In Fig4, mice are either subjected to REM sleep deprivation with the vibrating motor (controls), or REM sleep deprivations + optogenetics (experimental mice).

The control mice (vibrating motor) in Fig4 spend 6% of their time in REM sleep, which is double the amount of REM sleep compared to the mice receiving the same treatment in FigS4-D. Can the authors clarify the origin of this difference in the text?

The effect size for REM sleep deprivation is now added in the text.

It is important to note that these figures are analyzing two different intervals of the REMs restriction. In Fig. S4D, we analyzed the total amount of REMs over the entire 6 hr restriction interval (ZT1.5-7.5). In Fig. 4, we analyzed the amount of REMs only during the last 3 hr of restriction (ZT4.5-7.5) as optogenetic inhibition was performed only during the last 3 hrs when the REMs pressure is high. In Fig. S4D, we looked at the amount of REMs during ZT1.5-4.5 and 4.5-7.5 and found that the amount of REMs during ZT4.5-7.5 (4.46 ± 0.25 %; mean ± s.e.m.) is indeed higher than ZT 1.5-4.5 (1.66 ± 0.62 %), and is comparable to the amount of REMs during ZT4.5-7.5 in eYFP mice (5.95 ± 0.52 %) in Fig. 4. We now clearly state in the manuscript at which time points we analyzed the amount, duration and frequency of REMs.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) A few further citations suggested: Discussion "The TMN contains histamine producing neurons and antagonizing histamine neurons causes sleepiness..." It would be appropriate to cite Uygun DS et al 2016 J Neurosci (PMID: 27807161) here. Using the same HDC-Cre mice as used by Maurer et al., Uygun et al found that selectively increasing GABAergic inhibition onto histamine neurons produced NREM sleep.

We apologize for omitting this important paper. In the revised manuscript, we added this citation.

(2) Materials and Methods.

Although the JAX numbers are given for the mouse lines based on researchers generously donating to JAX for others to use, please cite the papers corresponding to the GAD2-ires-Cre and HDC-ires-Cre mouse lines deposited at JAX.

GAD2-ires-Cre was described in Taniguchi H et al., 2011, Neuron (PMID: 21943598).

The construction of the HDC-ires-CRE line is described in Zecharia AY et al J Neurosci et al 2012 (PMID: 22993424).

We have now added these important citations in the revised manuscript.

(3) Similarly, for the viruses, please provide the citations for the AAV constructs that were donated to Addgene.

We have now added these citations in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

The authors rely heavily on their conclusions by using an optogenetic tool that inhibits the activity of GAD2+ neurons, however, it is not shown that these neurons are indeed inhibited as expected. An alternative approach to tackle this could be the application of a different technique to achieve the same output (e.g. chemogenetics). However, both experiments (confirmation of inhibition, or using a different technique) would require a significant amount of work, and given the numerous studies out there showing that these optogenetic tools tend to work, may not be necessary. Hence the authors could also cite a similar study that used a likewise construct and where it was indeed shown that this technique works (i.e. similar retrograde optogenetic construct with Cre depedendent expression combined with electrophysiological recordings).

This laser stimulation protocol was designed based on previous reports of sustained inhibition using the same inhibitory opsin and our prior results that recapitulate similar findings as inhibitory chemogenetic techniques (Iyer et al., 2016; Kim et al., 2016; Wiegert et al., 2017; Stucynski et al., 2022). We have now added this description in the Result section.

Fig1A - Right: the virus expression graphs are great and give a helpful insight into the variability. The image on the left (GCAMP+ cells) is less clear, the GCAMP+ cells don't differentiate well from the background. Perhaps the whole brain image with inset in POA can show the GCAMP expression more convincingly.

We have added a histology picture showing the whole brain image with inset in the POA in the updated Fig. 1A .

Statistics: The table is very helpful. Based on the degrees of freedom, it seems that in some instances the stats are run on the recordings rather than on the individual mice (e.g. Fig1). It could be considered to use a mixed model where subjects as taken into account as a factor.

Author response image 4.

ΔF/Factivity of POA GAD2→TMN neurons during NREMs. The duration of NREMs episodes was normalized in time, ranging from 0 to 100%. Shading, ± s.e.m. Pairwise t-tests with Holm-Bonferroni correctionp = 5.34 e-4 between80 and100. Graybar, intervals where ΔF/F activity was significantly different from baseline (0 to 20%, the first time bin). n = 10 mice. In Fig. 1E , we ran stats based on the recordings. In this data set, we ran stats based on the individual mice, and found that the activity also gradually increased throughout NREMs episodes.

There is an effect of laser in Fig2 on REM sleep amount, as well as an interaction effect with virus injection (from the table). Therefore, it would be helpful for the reader to also show REM sleep data from the control group (laser stimulation but no active optogenetics construct) in Fig 2.

To properly control laser and virus effect, we performed the same laser stimulation experiments in eYFP control mice (expressing only eYFP without optogenetic construct, SwiChR++) and the data is provided in Fig 2C .

Fig3B: At the start of the rebound of REM sleep, there is a massive amount of wakefulness, also reflected in the change of spectral composition. Could you comment on the text about what is happening here?

We quantified the amount of wakefulness during the first hour of REMs rebound and found that indeed there is no significant difference in wakefulness between REM restriction and baseline control conditions ( Fig. S4H ). Therefore, while the representative image in Fig 3B shows increased wakefulness at the beginning of REMs rebound, we do not think the overall amount of wakefulness is increased.

Fig 4, supplementary data: it would be helpful for the reader to have mentioned in the text the effect size of the REM sleep restriction protocol (e.g. mean and standard deviation).

Thank you for this suggestion. We have now added the effect size for the REM sleep restriction experiments in the main text.

REM sleep restriction and photometry experiment: could be improved by adding within the main body of text that, in order to conduct the photometry experiment in the last hours of REM sleep deprivation, the manual REM sleep deprivation had to be applied, because the vibrating motor technique disturbed the photometry recordings.

Thank you for this suggestion. We have added the description in the main text.

Suggestion to build further on the already existing data (not for this paper): you have a powerful dataset to test whether REM sleep pressure builds up during wakefulness or NREM sleep, by correlating when your optogenetic treatment occurs (NREM or wakefulness), with the subsequent rebound in REM sleep (see also Endo et al., 1998; Benington and Heller, 1994; Franken 2001).

We thank the reviewer for this excellent suggestion. We plan to carry out this experiment in the future.

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Author Response

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

We thank the three reviewers and the reviewing editor for their positive evaluation of our manuscript. We particularly appreciate that they unanimously consider our work as “important contributions to the understanding of how the CAF-1 complex works”, “The large amounts of data provided in the paper support the authors' conclusion very well” and “The paper effectively addresses its primary objective and is strong”. We also thank them for a careful reading and useful comments to improve the manuscript. We have built on these comments to provide an improved version of the manuscript, and address them point by point below .

Reviewer #1 (Public Review):

Summary:

This paper makes important contributions to the structural analysis of the DNA replication-linked nucleosome assembly machine termed Chromatin Assembly Factor-1 (CAF-1). The authors focus on the interplay of domains that bind DNA, histones, and replication clamp protein PCNA.

Strengths:

The authors analyze soluble complexes containing full-length versions of all three fission yeast CAF-1 subunits, an important accomplishment given that many previous structural and biophysical studies have focused on truncated complexes. New data here supports previous experiments indicating that the KER domain is a long alpha helix that binds DNA. Via NMR, the authors discover structural changes at the histone binding site, defined here with high resolution. Most strikingly, the experiments here show that for the S. pombe CAF-1 complex, the WHD domain at the C-terminus of the large subunit lacks DNA binding activity observed in the human and budding yeast homologs, indicating a surprising divergence in the evolution of this complex. Together, these are important contributions to the understanding of how the CAF-1 complex works.

Weaknesses:

1. There are some aspects of the experimentation that are incompletely described: <br /> In the SEC data (Fig. S1C) it appears that Pcf1 in the absence of other proteins forms three major peaks. Two are labeled as "1a" (eluting at ~8 mL) and "1b" (~10-11 mL). It appears that Pcf1 alone or in complex with either or both of the other two subunits forms two different high molecular weight complexes (e.g. 4a/4b, 5a/5b, 6a/6b). There is also a third peak in the analysis of Pcf1 alone, which isn't named here, eluting at ~14 mL, overlapping the peaks labeled 2a, 4c, and 5c. The text describing these different macromolecular complexes seems incomplete (p. 3, lines 32-33): "When isolated, both Pcf2 and Pcf3 are monomeric while Pcf1 forms large soluble oligomers". Which of the three Pcf1-alone peaks are oligomers, and how do we know? What is the third peak? The gel analysis across these chromatograms should be shown.

We thank the reviewer for his/her careful reading of the manuscript. Indeed, we plotted two curves in Figure S1C in a color that does not match the legend, leading to confusion. Curve 1, Pcf1 alone, depicted in red, should appear in pink as indicated in the legend and in the SDS-PAGE analysis below. Curve 1 exhibits two peaks, labeled as 1a and 1b. With an elution volume of 8.5mL close to the dead volume of the column, peak 1a corresponds to soluble oligomers, while peak 1b (10.4mL) likely corresponds to monomeric Pcf1. Curve 5 (Pcf1 + Pcf2 mixture) was in pink instead of purple as indicated in the legend. This curve consists of three distinct peaks (5a, 5b, and 5c). The SDS-PAGE analysis revealed the presence of oligomers of Pcf1-Pcf2 (5a, 8.3mL), the Pcf1-Pcf2 complex (5b, 9.8mL), and Pcf2 alone (5c, 13.6 mL).

The color has now been corrected in the revised manuscript.

More importantly, was a particular SEC peak of the three-subunit CAF-1 complex (i.e. 4a or 4b) characterized in the further experimentation, or were the data obtained from the input material prior to the separation of the different peaks? If the latter, how might this have affected the results? Do the forms inter-convert spontaneously?

We conducted all structural analyses and DNA/PCNA interactions Figures (1-4, S1-S4) with freshly SECpurified samples corresponding to the 4b peak (9.7mL). Aliquots were flash-frozen with 50% glycerol for in vitro histone assembly assays (Figure 5).

1. Given the strong structural predication about the roles of residues L359 and F380 (Fig. 2f), these should be mutated to determine effects on histone binding.

We are pleased that our structural predictions are considered as strong. We agree that investigating the role of the L359 and F380 residues will be critical to further refine the binding interface between histone H3-H4 and CAF-1. An in vitro and in vivo analysis of such mutated forms, alongside the current Pcf1-ED mutant characterized in this article and additional potential mutated forms, has the potential to provide a better understanding of the dynamic of histone deposition by CAF-1. However, these additional approaches would require to reach another step in breaking this enigmatic dynamic.

1. Could it be that the apparent lack of histone deposition by the delta-WHD mutant complex occurs because this mutant complex is unstable when added to the Xenopus extract?

We cannot formally exclude this possibility, and this could potentially applies to all mutated forms tested. However, in the absence of available antibodies against the fission yeast CAF-1 complex, we cannot test this hypothesis for technical reasons. Nevertheless, we feel reassured by the fact that the in vitro assays of nucleosome assembly are overall consistent with the in vivo assays. Indeed, all mutated forms tested that abolished or weakened nucleosome assembly also exhibited synthetic lethality/growth defect in the absence of a functional HIRA pathway, including the delta WHD mutated form. This genetic synergy, that reflects a defective histone deposition by CAF-1, is not specific to the fission yeast S. pombe and was previously reported in S. cerevisiae (Kaufman et al. MCB 1998; Krawitz et al. MCB 2002). This further supports the evolutionary conservation based on genetic assay as a read out for defective histone deposition by CAF-1.

Reviewer #1 (Recommendations For The Authors):

• p. 4: "An experimental molecular weight of 179 kDa was calculated using Small Angle X-ray Scattering (SAXS), consistent with a 1:1:1 stoichiometry (Figure S1e). These data are in agreement with a globular complex with a significant flexibility (Figure S1f)." There needs to be more description of the precision of the molecular weight measurement, and what aspects of these data indicate the flexibility.

The molecular weight was estimated using the correlation volume (Vc) defined by (Rambo & Tainer, Nature 2013, 496, 477-481). The estimated error with this method is around 10%. We added this information together with supporting arguments for the existence of flexibility: “An experimental molecular weight of 179 kDa was calculated using Small Angle X-ray Scattering (SAXS). Assuming an accuracy of around 10% with this method (Rambo and Tainer 2013), this value is consistent with a 1:1:1 stoichiometry for the CAF-1 complex (calculated MW 167kDa) (Figure S1e). In addition, the position of the maximum for the dimensionless Kratky plot was slightly shifted to higher values in the y and x axis compared to the position of the expected maximum of the curve for a fully globular protein (Figure S1f).

This shows that the complex was globular with a significant flexibility.”

• p. 6, lines 21-22: "In contrast, a large part of signals (338-396) did not vanish anymore upon addition of a histone complex preformed with two other histone chaperones known to compete with CAF-1 for histone binding..." Given the contrast made later with the 338-351 region which is insensitive to Asf1/Mcm2, it would be clearer for the reader to describe the Asf1/Mcm2-competed regions as residues 325-338 plus 352-396. Note that the numerical scale of residues doesn't line up perfectly with the data points in Figure 2d, and this should be fixed as well.

We thank this reviewer for spotting this typographical error; we intended to write "In contrast, a large part of signals (348-396) did not vanish anymore… “. We modified paragraph as suggested by the reviewer because we agree it is clearer for the reader : “In contrast, only a shorter fragment (338-347) vanished upon addition of Asf1-H3-H4-Mcm2(69-138), a histone complex preformed with two other histone chaperones, Asf1 and Mcm2, known to compete with CAF-1 for histone binding (Sauer et al. 2017) and whose histone binding modes are well established (Figure 2e) (Huang et al. 2015, Richet et al. 2015). This finding underscores a direct competition between residues (325-338) and (349-396) within the ED domain and Asf1/Mcm2 for histone binding.”

The slight shift in the numerical scale Figure 2d was also corrected.

• p. 8. Lines 22-24: "EMSAs with a double-stranded 40bp DNA fragment confirmed the homogeneity of the bound complex. When increasing the SpCAF-1 concentration, additional mobility shifts suggest, a cooperative DNA binding (Figure 3a)." I agree that the migration of the population is further retarded upon the addition of more protein. However, doesn't this negate the first sentence? That is, if multiple CAF-1 complexes can bind each dsDNA molecule, can these complexes be described as homogeneous?

We fully agree with the reviewer's comment and have removed the notion of homogeneity from the first sentence. “EMSAs with a double-stranded 40bp DNA fragment showed the formation of a bound complex.”

• Figure S2b Legend: "1H-15N HSQC spectra of Pcf1_ED (425-496)." The residue numbers should read 325-396.

The typo has been corrected.

• Is the title for Figure 5 correct?: "Figure 5: Rescue using Y340 and W348 in the ED domain, the intact KER DNA binding domain and the C-terminal WHD of Pcf1 in SpCAF-1 mediated nucleosome assembly." I don't see that any point mutation rescue experiments are done here.

The title of figure 5 has been modified for “Efficient nucleosome assembly by SpCAF-1 in vitro requires interactions with H3-H4, DNA and PCNA, and the C-terminal WHD domain”.

• Figure S6C. I assume the top strain lacks the Pcf2-GFP but this should be stated explicitly.

The following sentence “The top strain corresponds to a strain expressing wild-type and untagged Pcf2 as a negative control of GFP fluorescence” is now added to the figure legend. The figure S6C has been modified accordingly to mention “Pcf2 (untagged)” and state more explicitly.

• Regarding point #3 in the public review, a simple initial test of this idea would be to determine if similar amounts of wt and mutant complexes can be immunoprecipitated at the endpoint of the assembly reactions.

In the absence of available antibodies against the fission yeast CAF-1 complex, we cannot test this hypothesis for technical reasons. However, the in vitro assays of nucleosome assembly are overall consistent with the in vivo assays. Indeed, all mutated forms tested that abolished or weakened nucleosome assembly also exhibited synthetic lethality/growth defect in the absence of a functional HIRA pathway, including the delta WHD mutated form. This genetic synergy, reflecting defective histone deposition by CAF-1, is not specific to the fission yeast S. pombe, as it was previously reported in S. cerevisiae (Kaufman et al. MCB 1998; Krawitz et al. MCB 2002), further supporting the evolution conservation in the genetic assay as a read out for defective histone deposition by CAF-1.

• Foundational findings that should be cited: The role of PCNA in CAF-1 activity was first recognized by pioneering studies in the Stillman laboratory (PMID: 10052459, 11089978). The earliest recombinant studies of CAF-1 showed that the large subunit is the binding platform for the other two, showed that the KER and ED domains were required for histone deposition activity, and roughly mapped the p60-binding site on the large subunit (PMID: 7600578). Another early study roughly mapped the binding site for the third subunit and showed that biological effects of impairing the PCNA binding synergized with defects in the HIR pathway (PMID: 11756556), a genetic synergy first demonstrated in budding yeast (PMID: 9671489).

We thank the reviewer for providing these important references that are now cited in the manuscript. PMID: 10052459 and 11089978 are cited page 2 line 18 and 19, PMID: 7600578 page 19 line 5 and PMID: 11756556 and 9671489 page 18 line 2.

Reviewer #2 (Public Review):

Summary:

The authors describe the structure-functional relationship of domains in S. pombe CAF-1, which promotes DNA replication-coupled deposition of histone H3-H4 dimer. The authors nicely showed that the ED domain with an intrinsically disordered structure binds to histone H3-H4, that the KER domain binds to DNA, and that, in addition to a PIP box, the KER domain also contributes to the PCNA binding. The ED and KER domains as well as the WHD domain are essential for nucleosome assembly in vitro. The ED, KER domains, and the PIP box are important for the maintenance of heterochromatin.

Strengths:

The combination of structural analysis using NMR and Alphafold2 modeling with biophysical and biochemical analysis provided strong evidence on the role of the different domain structures of the large subunit of SpCAF-1, spPCF-1 in the binding to histone H3-H4, DNA as well as PCNA. The conclusion was further supported by genetic analysis of the various pcf1 mutants. The large amounts of data provided in the paper support the authors' conclusion very well.

Reviewer #2 (Recommendations For The Authors):

The paper by Ochesenbein describes the structural and functional analysis of S. pombe CAF-1 complex critical for DNA replication-coupled histone H3/H4 deposition. By using structural, biophysical, and biochemical analyses combined with genetic methods, the authors nicely showed that a large subunit of SpCAF1, SpPCF-1, consists of 5 structured domains with four connecting IDR domains. The ED domain with IDR nature binds to histone H3-H4 dimer with the conformational change of the other domain(s). SpCAF-1 binds to dsDNA by using the KER domain, but not the WHD domain. The experiments have been done with great care and a large amount of the data are highly reliable. Moreover, the results are clearly presented and convincingly written. The conclusion in the paper is very solid and will be useful for researchers who work in the field of chromosome biology.

Major points:

1. DNA binding of the KER mutant shown in Figures S3h and S3i, which was measured by the EMSA, looks similar to that of wild-type control in Figure S3f, which is different from the data in Figures 3b and 3e measured by the MST. The authors need a more precise description of the EMSA result of the KER mutant shown in Figures 3 and S3. The quantification of the EMSA result would resolve the point (should be provided).

A proposed by this reviewer, we performed quantification of all EMSA presented in Figure 3 and Figure S3. We quantified the signal of the free DNA band to calculate a percentage of bound DNA in each condition. All EMSA experiments were conducted in duplicate, allowing us to calculate an average value and standard deviation for each interaction. Representative curves and fitted values are reported below in the figure provided for the reviewer (panel a data for Pcf1_KER domain with two fitting models, panel b for the entire CAF-1 complexes and mutants, panel c for the isolated Pcf1_KER domains), all fitted values in panel d. Importantly, as illustrated in panel a, the complete model for a single interaction (complete KD model, dashed line curve) does not adequately fit the data. In contrast, a function incorporating cooperativity (Hill model) better accounts for the measured data (solid line curve). Consistently, we also used the Hill model to fit the binding curves measured with the MST technique. As also specified now in the text, the Hill model allows to determine an EC50 value (concentration of protein resulting in the disappearance of half of the free DNA band intensity) and a Hill coefficient value (representing cooperativity during the interaction) for each curve.

We measure a value of 3.4 ± 0.4 μM for the EC50 of SpCAF-1 WT, which is higher than the value measured by MST (0.7 ± 0.1 μM). Higher values were also calculated for all mutants and isolated Pcf1_KER domains compared to MST. These discrepancies could raise from the fact that the DNA concentration used in the two techniques were very different (20nM for MST experiments and 1μM for EMSA). Unlike the complete KD model, which includes in the calculation the DNA concentration (considered here as the "receptor"), the Hill model is fitted independently of this value. This model assumes that the “receptor” concentration is low compared to the KD. Here we calculate EC50 values on the same order of magnitude as the DNA concentration (low micromolar), The quantification obtained by EMSA is thus challenging to interpret. In contrast, values fitted by the MST measurements are more reliable since this limitation of low “receptor” concentration is correct.

Therefore, although measurements of EC50 and Hill coefficient from EMSA are reproducible, they may be confusing for quantifying apparent affinity values through EC50. Nevertheless, this quantitative analysis of EMSA, requested by the reviewer, has highlighted an interesting characteristic of the KER mutant that is consistent across both methods: even though the EMSA pointed by the reviewer (Figures S3h and S3i compared to the wild-type control in Figure 3d and Figure S3f) show similar EC50 values, the binding cooperativity is different. Binding curves for the KER mutants is no longer cooperative (Hill coefficient ~1), and this is observed for all KER curves (isolated Pcf1_KER domain and the entire SpCAF-1 complex) with both methods, EMSA and MST. We thus decided to emphasize this characteristic of the KER mutant in the text (page 9 line 30-32). “Importantly, this mutant also shows a lower binding cooperativity for DNA binding, as estimated by the Hill coefficient value close to 1, compared to values around 3 for the WT and other mutants.”

Since EMSA quantifications did not show a loss of “affinity” (as measured by the EC50 value) for the KER* mutants, compared to the WT contrary to MST measurements and because the DNA concentration was close to the measured EC50, we consider that EC50 values calculated by EMSA do not represent a KD value. If we add this quantification, we should discuss this point in detail. Thus, for sake of clarity, we prefer to put in the manuscript EMSA measurements as illustrations and qualitative validations of the interaction but not to include the quantification.

Author response image 1.

Quantitative analysis of interaction with DNA by EMSA. a: quantification of the amount of bound DNA for the Pcf1_KER domain (blue points with error bars). The fit with a KD model is shown as a dashed line, and the fit with a Hill model with a solid line. b: Examples of quantifications and fits (Hill model) for reconstituted SpCAF-1 WT and mutants. c: Examples of quantifications and fits (Hill model) for Pcf1_KER domains WT and mutant. d: EC50 values and Hill coefficients obtained for all EMSA experiments presented in Figure 3 and S3.

1. As with the cooperative DNA binding of CAF-1, it is very important to show the stoichiometry of CAF-1 to the DNA or the site size. Given a long alpha-helix of the KER domain with biased charges, it is also interesting to show a model of how the dsDNA binds to the long helix with a cooperative binding property (this is not essential but would be helpful if the authors discuss it).

We agree that having a molecular model for the binding of the KER helix to DNA would be especially interesting, but at this point, considering the accuracy of the tools currently at our disposal for predicting DNA-protein interactions, such a model would remain highly speculative.

1. Figure 5 shows nucleosome assembly by SpCAF-1. SpCAF-1-PIP* mutant produced a product with faster mobility than the control at 2 h incubation. How much amounts of SpCAF-1 was added in the reaction seems to be critical. At least a few different concentrations of proteins should be tested.

The slightly faster migration of the SpCAF-1-PIPis not systematically reproduced and we observed in several experiments that the band corresponding to supercoiled DNA migrated slightly above or below the one for the complementation by the SpCAF-1-WT (see Author response image 2 below). Thus this indicates that after 2 hours incubation the supercoiling assay with the SpCAF-1-PIP mutant compared to those achieved with the SpCAF-1-WT. To further document whether the WT or the PIP mutant are similar or not, we monitored difference of their nucleosome assembly efficiency by testing their ability to produce supercoiled DNA over shorter time, after 45 minute incubation. Under these conditions, we reproducibly detected supercoiled forms at earlier times with SpCAF-1-WT when compared to the SpCAF-1-PIP* (see figure 5 and Author response image 2). These observations indicate that mutation in the PIP motif of Pcf1 affects the rate of supercoiling in a distinct manner when compared to the other mutations that dramatically impair SpCAF-1 capacity to promote supercoiling.

Author response image 2.

Minor points:

1. Page 8, line 26 or Table 1 legend: Please explain what "EC50" is.

The definition of EC50, together with a reference paper for the Hill model have been added in the text page 8 lines 23-26, “The curves were fitted with a Hill model (Tso et al. 2018) with a EC50 value of 0.7± 0.1µM (effective concentration at which a 50% signal is observed) and a cooperativity (Hill coefficient, h) of 2.7 ± 0.2, in line with a cooperative DNA binging of SpCAF-1.”, in the Table 1 figure legend and in the method section (page 26).

1. Page 13, lines 9, 11: "Xenopus" should be italicized.

This is corrected

1. Page 14, second half: In S. pombe, the pcf1 deletion mutant is not lethal. It is helpful to mention the phenotype of the deletion mutant a bit more when the authors described the genetic analysis of various pcf1 mutants.

This point has been added on page 15, line 1.

1. Figure 1d and Figure S2a: Captions and labels on the X and Y axes are overlapped or misplaced.

This is corrected

1. Figure 5: Please add a schematic figure of the assay to explain how one can check the nucleosome assembly by looking at the form I, supercoiled DNAs.

A new panel has been added to Figure 5. This scheme depicts the supercoiling assay where supercoiled DNA (form I) is used as an indication of efficient nucleosome assembly. The figure legend has also been modified accordingly.

Reviewer #3 (Public Review):

Summary:

The study conducted by Ouasti et al. is an elegant investigation of fission yeast CAF-1, employing a diverse array of technologies to dissect its functions and their interdependence. These functions play a critical role in specifying interactions vital for DNA replication, heterochromatin maintenance, and DNA damage repair, and their dynamics involve multiple interactions. The authors have extensively utilized various in vitro and in vivo tools to validate their model and emphasize the dynamic nature of this complex.

Strengths:

Their work is supported by robust experimental data from multiple techniques, including NMR and SAXS, which validate their molecular model. They conducted in vitro interactions using EMSA and isothermal microcalorimetry, in vitro histone deposition using Xenopus high-speed egg extract, and systematically generated and tested various genetic mutants for functionality in in vivo assays. They successfully delineated domain-specific functions using in vitro assays and could validate their roles to large extent using genetic mutants. One significant revelation from this study is the unfolded nature of the acidic domain, observed to fold when binding to histones. Additionally, the authors also elucidated the role of the long KER helix in mediating DNA binding and enhancing the association of CAF-1 with PCNA. The paper effectively addresses its primary objective and is strong.

Weaknesses:

A few relatively minor unresolved aspects persist, which, if clarified or experimentally addressed by the authors, could further bolster the study.

1. The precise function of the WHD domain remains elusive. Its deletion does not result in DNA damage accumulation or defects in heterochromatin maintenance. This raises questions about the biological significance of this domain and whether it is dispensable. While in vitro assays revealed defects in chromatin assembly using this mutant (Figure 5), confirming these phenotypes through in vivo assays would provide additional assurance that the lack of function is not simply due to the in vitro system lacking PTMs or other regulatory factors.

Our work demonstrates that the WHD domain is important CAF-1 function during DNA replication. Indeed, the deletion of this domain lead to a synthetic lethality when combined with mutation of the HIRA complex, as observed for a null pcf1 mutant, indicating a severe loss of function in the absence of the WHD domain. We propose that these genetic interactions, previously reported in S. cerevisiae (Kaufman et al. MCB 1998; Krawitz et al. MCB 2002) are indicative of a defective histone deposition by CAF-1. Moreover, our work establishes that this domain is dispensable to prevent DNA damage accumulation and to maintain silencing at centromeric heterochromatin, indicating that the WHD domain specifies CAF-1 functions. Moreover, our work further demonstrates that, in contrast to the S. cerevisiae and human WHD domain, the S. pombe counterpart exhibits no DNA binding activity. We thus agree that the WHD domain may contribute to nucleosome assembly in vivo via PTMs or interactions with regulatory factors that may potentially lack in in vitro systems. However, addressing these aspects deserves further investigations beyond the scope of this article.

1. The observation of increased Pcf2-gfp foci in pcf1-ED cells, particularly in mono-nucleated (G2phase) and bi-nucleated cells with septum marks (S-phase), might suggest the presence of replication stress. This could imply incomplete replication in specific regions, leading to the persistence of Caf1-ED-PCNA factories throughout the cell cycle. To further confirm this, detecting accumulated single-stranded DNA (ssDNA) regions outside of S-phase using RPA as an ssDNA marker could be informative.

We cannot formally exclude that cells expressing the Pcf1-ED mutated form exhibit incomplete replication in specific regions, an aspect that would require careful investigations. However, the microscopy analysis (Fig. 6c and S6c) of this mutant showed no alteration in the cell morphology, including the absence of elongated cells compared to wild type, a hallmark of checkpoint activation caused by ssDNA (Enoch et al. Gene & Dev 1992). Therefore, investigating the consequences of the interplay between the binding of CAF-1 to PCNA and histones on the dynamic of DNA replication, is of particular interest but out of the scope of the current manuscript.

1. Moreover, considering the authors' strong assertion of histone binding defects in ED through in vitro assays (Figure 2d and S2a), these claims could be further substantiated, especially considering that some degree of histone deposition might still persist in vivo in the ED mutant (Figure 7d, viable though growth defective double ED*+hip1D mutants). For example, the approach, akin to the one employed in Fig. 6a (FLAG-IPs of various Pcf1-FLAG-tagged mutants), could also enable a comparison of the association of different mutants with histones and PCNA, providing a more thorough validation of their findings.

We have provided in the current manuscript data establishing how Pcf1 mutated forms interacted with PCNA (Fig. 6a, 6b). Regarding the interactions with histone H3-H4, the approach based on immunoprecipitation using various Pcf1-FLAG tagged mutants has been unsuccessful in our hands. Indeed, we were unable to obtain robust and reproducible interactions between Pcf1 or its various mutated form with H3-H4. This is likely because Co-IP approaches do not probe for direct interactions. Indirect interactions between Pcf1 and H3-H4 are potentially bridged by additional factors, including the two other subunits of CAF-1, Pcf2 and Pcf3, or Asf1. Therefore, we are not in a position to address in vivo the direct interactions between Pcf1 and histone H3-H4.

1. It would be valuable for the authors to speculate on the necessity of having disordered regions in CAF1. Specifically, exploring the overall distribution of these domains within disordered/unfolded structures could provide insightful perspectives. Additionally, it's intriguing to note that the significant disparities observed among mutants (ED, PIP, and KER*) in in vitro assays seem to become more generic in vivo, except for the indispensability of the WHD-domain. Could these disordered regions potentially play a crucial role in the phase separation of replication factories? Considering these questions could offer valuable insights into the underlying mechanisms at play.

We agree that the potential mechanistic role of partial disorder in CAF-1 is particularly interesting. Disordered regions of human CAF-1 have been reported to form nuclear bodies with liquid-liquid phase separation properties to maintain HIV latency (Ma et al EMBO J. 2021). As suggested, this raises the question of how disordered domains of Pcf1 could promote phase separation for replication factories, if such phenomenon happens in vivo. Moreover, numerous factors of the replisome also harbor disordered regions (Bedina, A. et al, 2013. Intrinsically Disordered Proteins in Replication Process. InTech. doi: 10.5772/51673), adding complexity in disentangling experimentally such questions. We have added these elements at the end of the discussion in the revised manuscript (page 20, lines 23-29). “Such plasticity and cross-talks provided by structurally disordered domains might be key for the multivalent CAF-1 functions. Human CAF-1 has been reported to form nuclear bodies with liquid-liquid phase separation properties to maintain HIV latency (Ma et al. 2021). This raises the question of a potential role of the disordered domains of Pcf1, together with other replisome factor harbouring such disordered regions (Bedina 2013), in promoting phase separation of replication factories, if such phenomenon happens in vivo. Further studies will be needed to tackle these questions.”

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 main changes to the manuscript are: 

(1) We have added additional analysis of running onsets in closed and open loop conditions for audiomotor (Figure 2H) and visuomotor (Figure 3H) coupling.  

(2) We have also added analysis of running speed and pupil dilation upon mismatch presentation (Figures S2A and S2B, S4A and S4B, and S5A and S5B).

(3) We have expanded on the discussion of the nature of differences between audiomotor and visuomotor mismatches.

Reviewer #1:

The manuscript presents a short report investigating mismatch responses in the auditory cortex, following previous studies focused on the visual cortex. By correlating the mouse locomotion speed with acoustic feedback levels, the authors demonstrate excitatory responses in a subset of neurons to halts in expected acoustic feedback. They show a lack of responses to mismatch in the visual modality. A subset of neurons show enhanced mismatch responses when both auditory and visual modalities are coupled to the animal's locomotion. 

While the study is well-designed and addresses a timely question, several concerns exist regarding the quantification of animal behavior, potential alternative explanations for recorded signals, correlation between excitatory responses and animal velocity, discrepancies in reported values, and clarity regarding the identity of certain neurons. 

Strengths: 

(1) Well-designed study addressing a timely question in the field. 

(2) Successful transition from previous work focused on the visual cortex to the auditory cortex, demonstrating generic principles in mismatch responses. 

(3) The correlation between mouse locomotion speed and acoustic feedback levels provides evidence for a prediction signal in the auditory cortex. 

(4) Coupling of visual and auditory feedback shows putative multimodal integration in the auditory cortex. 

Weaknesses: 

(1) Lack of quantification of animal behavior upon mismatches, potentially leading to alternative interpretations of recorded signals. 

(2) Unclear correlation between excitatory responses and animal velocity during halts, particularly in closed-loop versus playback conditions. 

(3) Discrepancies in reported values in a few figure panels raise questions about data consistency and interpretation. 

(4) Ambiguity regarding the identity of the [AM+VM] MM neurons. 

The manuscript is a short report following up on a series of papers focusing on mismatch responses between sensory inputs and predicted signals. While previous studies focused on the visual modality, here the authors moved to the auditory modality. By pairing mouse locomotion speed to the sound level of the acoustic feedback, they show that a subpopulation of neurons displays excitatory responses to halts in the (expected) acoustic feedback. These responses were lower in the open-loop state, when the feedback was uncorrelated to the animal locomotion. 

Overall it is a well-designed study, with a timely and well-posed question. I have several concerns regarding the nature of the MM responses and their interpretations. 

- One lacks quantification of the animal behavior upon mismatches. Behavioral responses may trigger responses in the mouse auditory cortex, and this would be an alternative explanation to the recorded signals. 

What is the animal speed following closed-loop halts (we only have these data for the playback condition)? 

We have quantified the running speed of the mouse following audiomotor and visuomotor mismatches. We found no evidence of a change in running speed. We have added this to Figures S2A and S4A, respectively.

Is there any pupillometry to quantify possible changes in internal states upon halts (both closed-loop and playback)?

The term 'internal state' may be somewhat ambiguous in this context. We assume the reviewer is asking whether we have any evidence for possible neuromodulatory changes. We know that there are noradrenergic responses in visual cortex to visuomotor mismatches (Jordan and Keller, 2023), but no cholinergic responses (Yogesh and Keller, 2023). Pupillometry, however, is likely not always sensitive enough to pick up these responses. With very strong neuromodulatory responses (e.g. to air puffs, or other startling stimuli), pupil dilation is of course detected, but this effect is likely at best threshold linear. Looking at changes in pupil size following audiomotor and visuomotor mismatch responses, we found no evidence of a change. We have added this to Figures S2B and S4B, respectively. Note, we suspect this is also strongly experience-dependent. The first audio- or visuomotor mismatch the mouse encounters is likely a more salient stimulus (to the rest of the brain, not necessarily to auditory or visual cortex), than the following ones.  

These quantifications must be provided for the auditory mismatches but also for the VM or [AM+VM] mismatches.  

During the presentation of multimodal mismatches [AM + VM], mice did not exhibit significant changes in running speed or pupil diameter. These data have been now added to Figures S5A and S5B.

- AM MM neurons supposedly receive a (excitatory) locomotion-driven prediction signal. Therefore the magnitude of the excitation should depend on the actual animal velocity. Does the halt-evoked response in a closed loop correlate with the animal speed during the halt? Is the correlation less in the playback condition? 

This is indeed what one would expect. We fear, however, that we don’t have sufficient data to address this question properly. Moreover, there is an important experimental caveat that makes the interpretation of the results difficult. In addition to the sound we experimentally couple to the locomotion speed of the mouse, the mouse self-generates sound by running (the treadmill rotating, changes to the airflow of the air-supported treadmill, footsteps, etc.). These sources of sound all also correlate in intensity with running speed. Thus, it is not entirely clear how our increase in sound amplitude with increasing running speed relates to the increase in self-generated sounds on the treadmill. This is one of the key reasons we usually do this type of experiment in the visual system where experimental control of visual flow feedback (in a given retinotopic location) is straightforward. 

Having said that, if we look at the how mismatch responses change as a function of locomotion speed across the entire population of neurons, there appears to be no systematic change with running speed (and the effects are highly dependent on speed bins we choose). However, just looking at the most audiomotor mismatch responsive neurons, we find a trend for increased responses with increasing running speed (Author response image 1). We analyzed the top 5% of cells that showed the strongest response to mismatch (MM) and divided the MM trials into three groups based on running speed: slow (10-20 cm/s), middle (20-30 cm/s), and fast (>30 cm/s). Given the fact that we have on average 14 mismatch events in total per neuron, we don’t have sufficient data to analyze this. 

Author response image 1.

The average response of strongest AM MM responders to AM mismatches as a function of running speed (data are from 51 cells, 11 fields of view, 6 mice). 

Values in Figure 2H are way higher than what can be observed in Figures 2C, and D. Could you explain the mismatch in values? Same for 3H and 4F. 

In Figure 2H (now Figure S2F), we display responses from 4 755 individual neurons. Since most recorded neurons did not exhibit significant responses to mismatch presentations, their responses cluster around zero, significantly contributing to the final average shown in panel D. To clarify how individual neurons contribute to the overall population activity, we have added a histogram showing the distribution of neurons responding to audiomotor mismatch and sound playback halts. We hope this addition clarifies how individual neuron responses affect the final population activity. 

Furthermore, neurons exhibiting suppression upon closed-loop halts (Figure 2C) show changes in deltaF/F of the same order of magnitude as the AM MM neurons (with excitatory responses). I cannot picture where these neurons are found in the scatter plot of Figure 2H. 

This is caused by a ceiling effect. While we could adjust the scale of the heat map to capture neurons with very high responses (e.g. [-50 50], Author response image 2), doing so would obscure the response dynamics of most neurons. Note that the number of neurons on the y-axis far exceeds the resolution of this figure and thus there are also aliasing issues that mask the strong responses. 

Author response image 2.

Responses of all L2/3 ACx neurons to audiomotor mismatches. Same as Figure 2C with different color scale [-50 50] which does not capture most of the neural activity.  

- Are [AM+VM] MM neurons AM neurons? 

Many of [AM + VM] and [AM] neurons overlap but it is not exactly the same population. This is partially visible in Figure 4F. There is a subset of neurons (13.7%; red dots, Figure 4F) that selectively responded to the concurrent [AM+VM] mismatch, while a different subset of neurons (11.2%; yellow dots, Figure 4F) selectively responded to the mismatch responses in isolation. The [VM] response contributes only little to the sum of the two responses [AM] + [VM]. 

Please do not use orange in Figure 4F, it is perceptually too similar to red. 

We have now changed it to yellow. 

Reviewer #2 (Public Review): 

In this study, Solyga and Keller use multimodal closed-loop paradigms in conjunction with multiphoton imaging of cortical responses to assess whether and how sensorimotor prediction errors in one modality influence the computation of prediction errors in another modality. Their work addresses an important open question pertaining to the relevance of non-hierarchical (lateral cortico-cortical) interactions in predictive processing within the neocortex. 

Specifically, they monitor GCaMP6f responses of layer 2/3 neurons in the auditory cortex of head-fixed mice engaged in VR paradigms where running is coupled to auditory, visual, or audio-visual sensory feedback. The authors find strong auditory and motor responses in the auditory cortex, as well as weak responses to visual stimuli. Further, in agreement with previous work, they find that the auditory cortex responds to audiomotor mismatches in a manner similar to that observed in visual cortex for visuomotor mismatches. Most importantly, while visuomotor mismatches by themselves do not trigger significant responses in the auditory cortex, simultaneous coupling of audio-visual inputs to movement non-linearly enhances mismatch responses in the auditory cortex. 

Their results thus suggest that prediction errors within a given sensory modality are non-trivially influenced by prediction errors from another modality. These findings are novel, interesting, and important, especially in the context of understanding the role of lateral cortico-cortical interactions and in outlining predictive processing as a general theory of cortical function. 

In its current form, the manuscript lacks sufficient description of methodological details pertaining to the closed-loop training and the overall experimental design. In several scenarios, while the results per se are convincing and interesting, their exact interpretation is challenging given the uncertainty about the actual experimental protocols (more on this below). Second, the authors are laser-focused on sensorimotor errors (mismatch responses) and focus almost exclusively on what happens when stimuli deviate from the animal's expectations. 

While the authors consistently report strong running-onset responses (during open-loop) in the auditory cortex in both auditory and visual versions of the task, they do not discuss their interpretation in the different task settings (see below), nor do they analyze how these responses change during closed-loop i.e. when predictions align with sensory evidence. 

However, I believe all my concerns can be easily addressed by additional analyses and incorporation of methodological details in the text. 

Major concerns: 

(1) Insufficient analysis of audiomotor mismatches in the auditory cortex: 

Lack of analysis of the dependence of audiomotor mismatches on the running speed: it would be helpful if the authors could clarify whether the observed audiomotor mismatch responses are just binary or scale with the degree of mismatch (i.e. running speed). Along the same lines, how should one interpret the lack of dependence of the playback halt responses on the running speed? Shouldn't we expect that during playback, the responses of mismatch neurons scale with the running speed? 

Regarding the scaling of AM mismatch responses with running speed, please see our response to reviewer 1 above to the same question. 

Regarding the playback halt response and dependence on running speed, we would not expect there to be a dependence. The playback halt response (by design) measures the strength of the sensory response to a cessation of a stimulus (think OFF response). These typically are less strong in cortex than the corresponding ON responses but need to be controlled for (else a mismatch response might just be an OFF response – the prediction error is quantified as the difference between AM mismatch response and playback halt response). Given that sound onset responses only have a small dependence on running state, we would similarly expect sound offset (playback halt) responses to exhibit only minimal dependence on running state. 

Slow temporal dynamics of audiomotor mismatches: despite the transient nature of the mismatches (1s), auditory mismatch responses last for several seconds. They appear significantly slower than previous reports for analogous visuomotor mismatches in V1 (by the same group, using the same methods) and even in comparison to the multimodal mismatches within this study (Figure 4C). What might explain this sustained activity? Is it due to a sustained change in the animal's running in response to the auditory mismatch? 

This is correct, neither AM or AM+VM mismatch return to baseline in the 3 seconds following onset. VM mismatch response in visual cortex also do not return to baseline in that time window (see e.g.

Figure 1E in (Attinger et al., 2017), or Figure 1F in (Zmarz and Keller, 2016). What the origin or computation significance of this sustained calcium response is we do not know. In intracellular signals, we do not see this sustained response (Jordan and Keller, 2020). Also peculiar is indeed the fact that in the case of AM mismatch the sustained response is similar in strength to the initial response. But also here, why this would be the case, we do not know. It is conceivable that the initial and the sustained calcium response have different origins, if the sustained response amplitude is all or nothing, the fact that the AM mismatch response is the smallest of the three could explain why sustained and initial responses are closer than for [AM+VM] or VM (in visual cortex) mismatch responses. All sustained responses appear to be roughly 1% dF/F. There are no apparent changes in running speed or pupil dilation that would correlate with the sustained activity (new panel A in Figure S2). 

(2) Insufficient analysis and discussion of running onset responses during audiomotor sessions: The authors report strong running-onset responses during open-loop in identified mismatch neurons. They also highlight that these responses are in agreement with their model of subtractive prediction error, which relies on subtracting the bottom-up sensory evidence from top-down motor-related predictions. I agree, and, thus, assume that running-onset responses during the open loop in identified 'mismatch' neurons reflect the motor-related predictions of sensory input that the animal has learned to expect. If this is true, one would expect that such running-onset responses should dampen during closed-loop, when sensory evidence matches expectations and therefore cancels out this prediction. It would be nice if the authors test this explicitly by analyzing the running-related activity of the same neurons during closed-loop sessions. 

Thank you for the suggestion. We now show running onset responses in both closed and open loop conditions for audiomotor and visuomotor coupling (new Figures 2H and 3H). In closed loop, we observe only a transient running onset response. In the open loop condition, running onset responses are sustained. For the visuomotor coupling, running onset responses are sustained in both closed and open loop conditions. This would be consistent with a slightly delayed cancellation of sound and motor related inputs in the audiomotor closed loop condition but not otherwise. 

(3) Ambiguity in the interpretation of responses in visuomotor sessions. 

Unlike for auditory stimuli, the authors show that there are no obvious responses to visuomotor mismatches or playback halts in the auditory cortex. However, the interpretation of these results is somewhat complicated by the uncertainty related to the training history of these mice. Were these mice exclusively trained on the visuomotor version of the task or also on the auditory version? I could not find this info in the Methods. From the legend for Figure 4D, it appears that the same mice were trained on all versions of the task. Is this the case? If yes, what was the training sequence? Were the mice first trained on the auditory and then the visual version? 

The training history of the animals is important to outline the nature of the predictions and mismatch responses that one should expect to observe in the auditory cortex during visuomotor sessions.

Depending on whether the mice in Figure 3 were trained on visual only or both visual and auditory tasks, the open-loop running onset responses may have different interpretations. 

a) If the mice were trained only on the visual task, how should one interpret the strong running onset responses in the auditory cortex? Are these sensorimotor predictions (presumably of visual stimuli) that are conveyed to the auditory cortex? If so, what may be their role? 

b) If the mice were also trained on the auditory version, then a potential explanation of the running-onset responses is that they are audiomotor predictions lingering from the previously learned sensorimotor coupling. In this case, one should expect that in the visual version of the task, these audiomotor predictions (within the auditory cortex) would not get canceled out even during the closedloop periods. In other words, mismatch neurons should constantly be in an error state (more active) in the closed-loop visuomotor task. Is this the case? 

If so, how should one then interpret the lack of a 'visuomotor mismatch' aligned to the visual halts, over and above this background of continuous errors? 

As such, the manuscript would benefit from clearly stating in the main text the experimental conditions such as training history, and from discussing the relevant possible interpretations of the responses. 

Mice were not trained on either audiomotor or visuomotor coupling and were reared normally. Prior to the recording day, the mice were habituated to running on the air-supported treadmill without any coupling for up to 5 days. On the first recording day, the mice experienced all three types of sessions (audiomotor, visuomotor, or combined coupling) in a random order for the first time. We have clarified this in the methods. 

Regarding the question of how one should interpret the strong running onset responses in the auditory cortex, this is complicated by the fact that – unless mice are raised visually or auditorily deprived – they always have life-long experience with visuomotor or audiomotor coupling. The visuomotor coupling they experience in VR is geometrically matched to what they would experience by moving in the real world, for the audiomotor coupling the exact relationship is less clear, but there are a diverse set of sound sources that scale in loudness with increasing running speed. Hence running onset responses reflect either such learned associations (as the reviewer also speculates), or spurious input. Rearing mice without coupling between movement and visual feedback does not abolish movement related responses in visual cortex (Attinger et al., 2017), to the contrary, it enhances them considerably. We suspect this reflects visual cortex being recruited for other functions in the absence of visual input. But given the data we have we cannot distinguish the different possible sources of running related responses. It is very likely that any “training” related effect we could achieve in a few hours pales in comparison to the life-long experience the mouse has in the world. 

Regarding the lack of a 'visuomotor mismatch' aligned to the visual halts, we are not sure we understand. Our interpretation is that there are no (or only a very small - we speculate that any nonzero VM mismatch response is just inherited from visual cortex) VM mismatch responses in auditory cortex above chance. Our data are consistent with the interpretation that there is no opposition of bottom up visual and top down motor related input in auditory cortex, hence no VM mismatch responses (independent of how strong the top-down motor related input is). This is of course not surprising – this is more of a sanity check and becomes relevant in the context of interpreting AM+VM responses. 

(4) Ambiguity in the interpretation of responses in multimodal versus unimodal sessions. 

The authors show that multimodal (auditory + visual) mismatches trigger stronger responses than unimodal mismatches presented in isolation (auditory only or visual only). Further, they find that even though visual mismatches by themselves do not evoke a significant response, co-presentation of visual and auditory stimuli non-linearly augments the mismatch responses suggesting the presence of nonhierarchical interactions between various predictive processing streams. 

In my opinion, this is an important result, but its interpretation is nuanced given insufficient details about the experimental design. It appears that responses to unimodal mismatches are obtained from sessions in which only one stimulus is presented (unimodal closed-loop sessions). Is this actually the case? An alternative and perhaps cleaner experimental design would be to create unimodal mismatches within a multimodal closed-loop session while keeping the other stimulus still coupled to the movement. 

This is correct, unimodal mismatches were acquired in unimodal coupling. Testing unimodal mismatch responses in multimodally coupled VR is an interesting idea we had initially even pursued. However, halting visual flow in a condition of coupling of both visual flow and sound amplitude to running speed has an additional complication. Introducing an audiomotor mismatch in this coupling inherently also creates an audiovisual (AV) mismatch, and the same applies to visuomotor mismatches, which cause a concurrent visuoaudio (VA) mismatch (Figure R3). This assumes that there are cross modal predictions from visual cortex to auditory cortex as there are from auditory cortex to visual cortex (Garner and Keller, 2022). There are interesting differences between the different types of mismatches, but with the all the necessary passive controls this quickly exceeded the amount of data we could reasonably acquire for this paper. This remains an interesting question for future research. 

Author response image 3.

Rationale of unimodal mismatches introduced within multimodal paradigm. 

Given the current experiment design (if my assumption is correct), it is unclear if the multimodal potentiation of mismatch responses is a consequence of nonlinear interactions between prediction/error signals exchanged across visual and auditory modalities. Alternatively, could this result from providing visual stimuli (coupled or uncoupled to movement) on top of the auditory stimuli? If it is the latter, would the observed results still be evidence of non-hierarchical interactions between various predictive processing streams? 

Mice are not in complete darkness during the AM mismatch experiments (the VR is off, but there is low ambient light in the experimental rooms primarily from computer screens), so we can rule out the possibility that the difference comes from having “no” visual input during AM mismatch responses. Addressing the question of whether it is this particular stimulus that cause the increase would require an experiment in which we couple sound amplitude but keep visual flow open loop. We did not do this, but also think this is highly unlikely. However, as described above, we did do an experiment in which we coupled both sound amplitude and visual flow to running, and then either halted visual flow, or sound amplitude, or both. Comparing the [AM+VM] and [AM+AV] mismatch responses, we find that [AM+VM] responses are larger than [AM+AV] responses as one would expect from an interaction between [AM] and [VM] responses (Author response image 4). Finally, either way the conclusion that there are nonhierarchical interactions of prediction error computations holds either way – if any visual stimulus (either visuomotor mismatch, or visual flow responses) influences audiomotor mismatch responses, this is evidence of non-hierarchical interactions.   

Author response image 4.

Average population response of all L2/3 neurons to concurrent [AM + VM] or [AM+AV] mismatch. Gray shading indicates the duration of the stimulus.

Along the same lines, it would be interesting to analyze how the coupling of visual as well as auditory stimuli to movement influences responses in the auditory cortex in close-loop in comparison to auditoryonly sessions. Also, do running onset responses change in open-loop in multimodal vs. unimodal playback sessions? 

We agree, and why we started out doing the experiments described above. We stopped with this however, because it quickly became a combinatorial nightmare. We will leave addressing the question of how different types of coupling influences responses in auditory cortex to brave future neuroscientists. 

Regarding the question of running onset responses, in both the multimodal and auditory only paradigms, running onset responses are transient; bottom-up sensory evidence is quickly subtracted from top-down motor-related prediction (Author response image 5). While there appears to be a small difference in the dynamics of running onset responses between these two paradigms, it was not significant. Note, we also have much less data than we would like here for this type of analysis. 

Author response image 5.

Running onset responses recorded in unimodal and multimodal closed loop sessions (1903 neurons, 16 fields of view, 8 mice)

We also compared running onsets in open loop sessions and did not find any significant differences between unimodal and multimodal sessions (Author response image 6). We found only six sessions in which animals performed at least two running onsets in each session type, therefore, we do not have enough data to include it in the manuscript. 

Author response image 6.

Running onset responses recorded within unimodal and multimodal open loop sessions (659 cells, 6 field of view, 5 mice).

Minor concerns and comments:

(1) Rapid learning of audiomotor mismatches: It is interesting that auditory mismatches are present even on day 1 and do not appear to get stronger with learning (same on day 2). The authors comment that this could be because the coupling is learned rapidly (line 110). How does this compare to the rate at which visuomotor coupling is learned? Is this rapid learning also observable in the animal's behavior i.e. is there a change in running speed in response to the mismatch? 

In the visual system this is a bit more complicated. If you look at visuomotor mismatch responses in a normally reared mouse, responses are present from the first mismatch (as far as we can tell given the inherently small dataset with just one response pre mouse). However, this is of course confounded by the fact that a normally reared mouse has visuomotor coupling throughout life from eye-opening. Raising mice in complete darkness, we have shown that approximately 20 min of coupling are sufficient to establish visuomotor mismatch responses (Attinger et al., 2017). 

Regarding the behavioral changes that correlate with learning, we are not sure what the reviewer would expect. We cannot detect a change in mismatch responses and hence would also not expect to see a change in behavior.

(2) The authors should clarify whether the sound and running onset responses of the auditory mismatch neurons in Figure 2E were acquired during open-loop. This is most likely the case, but explicitly stating it would be helpful. 

Both responses were measured in isolation (i.e. VR off, just sound and just running onset), not in an open-loop session. We have clarified in the figure legend that these are the same data as in Figure 1H and N. 

(3) In lines 87-88, the authors state 'Visual responses also appeared overall similar but with a small increase in strength during running ...'. This statement would benefit from clarification. From Figure S1 it appears that when the animal is sitting there are no visual responses in the auditory cortex. But when the animal is moving, small positive responses are present. Are these actually 'visual' responses - perhaps a visual prediction sent from the visual cortex to the auditory cortex that is gated by movement? If so, are they modulated by features of visual stimuli eg. contrast, intensity? Or, do these responses simply reflect motor-related activity (running)? Would they be present to the same extent in the same neurons even in the dark? 

This was wrong indeed - we have rephrased the statement as suggested. Regarding the source of visual responses, we use the term “visual response” operationally here agnostic to what pathway might be driving it (i.e. it could be a prediction triggered by visual input). 

We did not test if recorded visual responses are modulated by contrast or intensity. However, testing whether they are would not help us distinguish whether the responses are ‘visual’ or ‘visual predictions’. Finally, regarding the question about whether they are motor-related responses, this might be a misunderstanding. These are responses to visual stimuli while the mouse is already running (i.e. there is no running onset), hence we cannot test whether these responses are present in the dark (this would be the equivalent of looking at random triggers in the dark while the mouse is running).  

(4) The authors comment in the text (lines 106-107) about cessation of sound amplitude during audiomotor mismatches as being analogous to halting of visual flow in visuomotor mismatches. However, sound amplitude versus visual flow are quite different in nature. In the visuomotor paradigm, the amount of visual stimulation (photons per unit time) does not necessarily change systematically with running speed. Whereas, in the audiomotor paradigm, the SNR of the stimulus itself changes with running speed which may impact the accuracy of predictions. On a broader note, under natural settings, while the visual flow is coupled to movement, sound amplitude may vary more idiosyncratically with movement. 

This is a question of coding space. The coding space of visual cortex of the mouse is probably visual flow (or change in image) not number of photons. This already starts in the retina. The demonstration of this is quite impressive. A completely static image on the retina will fade to zero response (even though the number of photons remains constant). This is also why most visual physiologists use dynamic stimuli – e.g. drifting gratings, not static gratings – to map visual responses in visual cortex. If responses were linear in number of photons, this would make less of a difference. The correspondence we make is between visual flow (which we assume is the main coding space of mouse V1 – this is not established fact, but probably implicitly the general consensus of the field) and sound amplitude. Responses in auditory cortex are probably more linear in sound amplitude than visual cortex responses are linear in number of photons, but whether that is the correct coding space is still unclear, and as far as we can tell there is no clear consensus in the field. We did consider coupling running speed to frequency, which may work as well, but given the possible equivalence (as argued above) and the fact that we could see similar responses with sound amplitude coupling we did not explore frequency coupling. 

If visual speed is the coding space of V1, SNR should behave equivalently in both cases. 

Perhaps such differences might explain why unlike in the case of visual cortex experiments, running speed does not affect the strength of playback responses in the auditory cortex. 

Possible, but the more straightforward framing of this point is that sensory responses are enhanced by running in visual cortex while they are not in auditory cortex. A playback halt response (by design) is just a sensory response. Why running does not generally increase sensory responses in auditory cortex (L2/3 neurons), but does so in visual cortex, would be the more general version of the same question.

We fear we have no intelligent answer to this question.  

Reviewer #3 (Public Review): 

This study explores sensory prediction errors in the sensory cortex. It focuses on the question of how these signals are shaped by non-hierarchical interactions, specifically multimodal signals arising from same-level cortical areas. The authors used 2-photon imaging of mouse auditory cortex in head-fixed mice that were presented with sounds and/or visual stimuli while moving on a ball. First, responses to pure tones, visual stimuli, and movement onset were characterized. Then, the authors made the running speed of the mouse predictive of sound intensity and/or visual flow. Mismatches were created through the interruption of sound and/or visual flow for 1 second while the animal moved, disrupting the expected sensory signal given the speed of movement. As a control, the same sensory stimuli triggered by the animal's movement were presented to the animal decoupled from its movement. The authors suggest that auditory responses to the unpredicted silence reflect mismatch responses. That these mismatch responses were enhanced when the visual flow was congruently interrupted, indicates the cross-modal influence of prediction error signals. 

This study's strengths are the relevance of the question and the design of the experiment. The authors are experts in the techniques used. The analysis explores neither the full power of the experimental design nor the population activity recorded with 2-photon, leaving open the question of to what extent what the authors call mismatch responses are not sensory responses to sound interruption. The auditory system is sensitive to transitions and indeed responses to the interruption of the sound are similar in quality, if not quantity, in the predictive and the control situation. 

This study's strengths are the relevance of the question and the design of the experiment. The authors are experts in the techniques used. The analysis explores neither the full power of the experimental design nor the population activity recorded with 2-photon, leaving open the question of to what extent what the authors call mismatch responses are not sensory responses to sound interruption. The auditory system is sensitive to transitions and indeed responses to the interruption of the sound are similar in quality, if not quantity, in the predictive and the control situation. The pattern they observe is different from the visuomotor mismatch responses the authors found in V1 (Keller et al., 2012), where the interruption of visual flow did not activate neuronal activity in the decoupled condition. 

Just to add brief context to this. The reviewer is correct here, the (Keller et al., 2012) paper reports finding no responses to playback halt. However, this was likely a consequence of indicator sensitivity (these experiments were done with what now seems like a pre-historic version of GCaMP). Experiments performed with more modern indicators do find playback halt responses in visual cortex (see e.g. (Zmarz and Keller, 2016)). 

The auditory system is sensitive to transitions, also those to silence. See the work of the Linden or the Barkat labs on-off responses, and also that of the Mesgarani lab (Khalighinejad et al., 2019) on responses to transitions 'to clean' (Figure 1c) in the human auditory cortex. Since the responses described in the current work are modulated by movement and the relationship between movement and sound is more consistent during the coupled sessions, this could explain the difference in response size between coupled and uncoupled sessions. There is also the question of learning. Prediction signals develop over a period of several days and are frequency-specific (Schneider et al., 2018). From a different angle, in Keller et al. 2012, mismatch responses decrease over time as one might expect from repetition. 

Also for brief context, this might be a misconception. We don’t find a decrease of mismatch responses in the (Keller et al., 2012) paper – we assume what the reviewer is referring to is the fact that mismatch responses decrease in open-loop conditions (they normally do not in closed-loop conditions). This is the behavior one would expect if the mouse learns that movement no longer predicts visual feedback. 

It would help to see the responses to varying sound intensity as a function of previous intensity, and to plot the interruption response as a function of both transition and movement in both conditions. 

Given the large populations of neurons recorded and the diversity of the responses, from clearly negative to clearly positive, it would be interesting to understand better whether the diversity reflects the diversity of sounds used or a diversity of cell types, or both. 

Comments and questions: 

Does movement generate a sound and does this change with the speed of movement? It would be useful to have this in the methods. 

There are three ways to interpret the question – below the answers to all three:

(1) Running speed is experimentally coupled to sound amplitude of a tone played through a loudspeaker. Tone amplitude is scaled with running speed of the mouse in a closed loop fashion. We assume this is not what the reviewer meant, as this is described in the methods (and the results section). 

(2) Movements of the mouse naturally generate sounds (footsteps, legs moving against fur, etc.). Most of these sounds trivially scale with the frequency of leg movements – we assume this also not what the reviewer meant. 

(3) Finally, there are experimental sounds related to the rotation speed of the air supported treadmill that increase with running speed of the mouse. We have added this to the methods as suggested. 

Figures 1a and 2a. The mouse is very hard to see. Focus on mouse, objective, and sensory stimuli? The figures are generally very clear though. 

We have enlarged the mouse as suggested. 

1A-K was the animal running while these responses were measured? 

We did not restrict this analysis to running or sitting and pooled responses over both conditions.  We have made this more explicit in the results section.  

Data in Figure 1: Since the modulation of sensory responses by movement is relevant for the mismatch responses, I would move this analysis from S1 to Figure 1 and analyze the responses more finely in terms of running speed relative to sound and gratings. I would include here a more thorough analysis of the responses to 8kHz at varying intensities, for example in the decoupled sessions. Does the response adapt? Does it follow the intensity? 

We agree that these are interesting questions, but they do not directly pertain to our conclusions here. The key point Figure S1 addresses is whether auditory responses are generally enhanced by running (as they are e.g. in visual cortex) – the answer, on average, is no. We have tried emphasizing this more, but it changes the flow of the paper away from our main message, hence we have left the panels in the supplements. 

Regarding the 8kHz modulation, there is a general increase of the suppression of activity with increasing sound amplitude (Author response image 7 and Author response image 8). But due to the continuously varying amplitude of the stimulus, we do not have sufficient data (or do not know how to with the data we have) to address questions of adaptation. We assume there is some form of adaptation. However, either way, we don’t see how this would change our conclusions. 

Author response image 7.

Neural activity as a function of sound level in an AM open loop session. 

Author response image 8.

The average sound evoked population response of all ACx layer 2/3 neurons to 60 dB or 75 dB 8 kHz pure tones. Stimulus duration was 1 s (gray shading).

2C-D why not talk of motor modulation? Paralleling what happens in response to auditory and visual stimuli? 

This is correct, a mismatch response (we use mismatch here to operationally describe the stimulus – not the interpretation) can be described either as a prediction error (this is the interpretation) or a stimulus specific motor modulation. Note, the key here is “stimulus specific”. It is stimulus specific as there is an approximately 3x change between mismatch and playback halt (the same sensory stimulus with and without locomotion), but basically no change for sound onsets (Figure S1). Having said that, one explanation (prediction error) has predictive power (and hence is testable – see e.g. (Vasilevskaya et al., 2023) for an extensive discussion on exactly this argument for mismatch responses in visual cortex), while the other does not (a “stimulus specific” motor modulation has no predictive value or computational theory behind it and is simply a description). Thus, we choose to interpret it as a prediction error. Note, this finding does not stand in isolation and many of the testable predictions of the predictive processing interpretation have turned out to be correct (see e.g. (Keller and Mrsic-Flogel, 2018) for a review). 

Note, we try to only use the interpretation of “prediction error” when motivating why we do the experiments, and in the discussion, but not directly in the description of the results (e.g. in Figure 2).  

How does the mismatch affect the behavior of the mouse? Does it stop running? This could also influence the size of the response. 

We quantified animal behavior during audiomotor mismatches and did not find any significant acceleration or slowing down upon mismatch events. Thus, neural responses recorded during AM mismatches are unlikely to be explained by changes in animal behavior. These data have been added in Figure S2A and Figure S4A.

Figure 3. What about neurons that were positively modulated by both grating and movement? How do these neurons respond to the mismatch? 

Neurons positively modulated by both grating and movement were slightly more responsive to MM than the rest of the population, though this difference was not significant (Author response image 9). This is also visible in Figure 3G – the high VM mismatch responsive neurons are randomly distributed in regard to correlation with running speed and visual flow speed. 

Author response image 9.

Responses to visuomotor mismatches of neurons positively modulated by grating and movement and remaining of the population.

Line 176. The authors say 'Thus, in the case of a [AM + VM] mismatch both the halted visual flow and the halted sound amplitude are predicted by running speed' but the mismatch (halted flow and amplitude) is not predicted by the speed, correct? Please rephrase. 

Thank you for pointing this out – this was indeed phrased incorrectly. We have corrected this. 

How was the sound and/or visual flow interruption triggered? Did the animal have to run at a minimum speed in order for it to happen?

Sound and visual flow interruptions were triggered randomly, independent of the animal's running speed. However, for the analysis, only MM presentations during which animals were running at a speed of at least 0.3 cm/s were included. The 0.3 cm/s was simply the (arbitrary) threshold we used to determine if the mouse was running. In a completely stationary mouse a mismatch event will not have any effect (sound amplitude/visual flow speed are already at 0). This is described in the methods section.

Author response:

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

eLife assessment

This is a useful study examining the determinants and mechanisms of LRMP inhibi:on of cAMP regula:on of HCN4 channel ga:ng. The evidence provided to support the main conclusions is unfortunately incomplete, with discrepancies in the work that reduce the strength of mechanis:c insights.

Thank you for the reviews of our manuscript. We have made a number of changes to clarify our hypotheses in the manuscript and addressed all of the poten:al discrepancies by revising some of our interpreta:on. In addi:on, we have provided addi:onal experimental evidence to support our conclusions. Please see below for a detailed response to each reviewer comment.

Public Reviews

Reviewer #1 (Public Review):

Summary:

The authors use truncations, fragments, and HCN2/4 chimeras to narrow down the interaction and regulatory domains for LRMP inhibition of cAMP-dependent shifts in the voltage dependence of activation of HCN4 channels. They identify the N-terminal domain of HCN4 as a binding domain for LRMP, and highlight two residues in the C-linker as critical for the regulatory effect. Notably, whereas HCN2 is normally insensitive to LRMP, putting the N-terminus and 5 additional C-linker and S5 residues from HCN4 into HCN2 confers LRMP regulation in HCN2.

Strengths:

The work is excellent, the paper well written, and the data convincingly support the conclusions which shed new light on the interaction and mechanism for LRMP regulation of HCN4, as well as identifying critical differences that explain why LRMP does not regulate other isoforms such as HCN2.

Thank you.

Reviewer #2 (Public Review):

Summary:

HCN-4 isoform is found primarily in the sino-atrial node where it contributes to the pacemaking activity. LRMP is an accessory subunit that prevents cAMP-dependent potentiation of HCN4 isoform but does not have any effect on HCN2 regulation. In this study, the authors combine electrophysiology, FRET with standard molecular genetics to determine the molecular mechanism of LRMP action on HCN4 activity. Their study shows that parts of N- and C-termini along with specific residues in C-linker and S5 of HCN4 are crucial for mediating LRMP action on these channels. Furthermore, they show that the initial 224 residues of LRMP are sufficient to account for most of the activity. In my view, the highlight of this study is Fig. 7 which recapitulates LRMP modulation on HCN2-HCN4 chimera. Overall, this study is an excellent example of using time-tested methods to probe the molecular mechanisms of regulation of channel function by an accessory subunit.

Weaknesses:

(1) Figure 5A- I am a bit confused with this figure and perhaps it needs better labeling. When it states Citrine, does it mean just free Citrine, and "LRMP 1-230" means LRMP fused to Citrine which is an "LF" construct? Why not simply call it "LF"? If there is no Citrine fused to "LRMP 1-230", this figure would not make sense to me.

We have clarified the labelling of this figure and specifically defined all abbreviations used for HCN4 and LRMP fragments in the results section on page 14.

(2) Related to the above point- Why is there very little FRET between NF and LRMP 1-230? The FRET distance range is 2-8 nm which is quite large. To observe baseline FRET for this construct more explanation is required. Even if one assumes that about 100 amino are completely disordered (not extended) polymers, I think you would still expect significant FRET.

FRET is extremely sensitive to distance (to the 6th power of distance). The difference in contour length (maximum length of a peptide if extended) between our ~260aa fragment and our ~130 aa fragments is on the order of 450Å (45nm), So, even if not extended it is not hard to imagine that the larger fragments show a weaker FRET signal. In fact, we do see a slightly larger FRET than we do in control (not significant) which is consistent with the idea that the larger fragments just do not result in a large FRET.

Moreover, this hybridization assay is sensitive to a number of other factors including the affinity between the two fragments, the expression of each fragment, and the orientation of the fluorophores. Any of these factors could also result in reduced FRET.

We have added a section on the limitations of the FRET 2-hybrid assay in the discussion section on page 20. Our goal with the FRET assay was to provide complimentary evidence that shows some of the regions that are important for direct association and we have edited to the text to make sure we are not over-interpreting our results.

(3) Unless I missed this, have all the Cerulean and Citrine constructs been tested for functional activity?

All citrine-tagged LRMP constructs (or close derivatives) were tested functionally by coexpression with HCN (See Table 1 and pages 10-11). Cerulean-tagged HCN4 fragments are of course intrinsically not-functional as they do not include the ion conducting pore.

Reviewer #3 (Public Review):

Summary:

Using patch clamp electrophysiology and Förster resonance energy transfer (FRET), Peters and co-workers showed that the disordered N-terminus of both LRMP and HCN4 are necessary for LRMP to interact with HCN4 and inhibit the cAMP-dependent potentiation of channel opening. Strikingly, they identified two HCN4-specific residues, P545 and T547 in the C-linker of HCN4, that are close in proximity to the cAMP transduction centre (elbow Clinker, S4/S5-linker, HCND) and account for the LRMP effect.

Strengths:

Based on these data, the authors propose a mechanism in which LRMP specifically binds to HCN4 via its isotype-specific N-terminal sequence and thus prevents the cAMP transduction mechanism by acting at the interface between the elbow Clinker, the S4S5-linker, the HCND.

Weaknesses:

Although the work is interesting, there are some discrepancies between data that need to be addressed.

(1) I suggest inserting in Table 1 and in the text, the Δ shift values (+cAMP; + LRMP; +cAMP/LRMP). This will help readers.

Thank you, Δ shift values have been added to Tables 1 and 2 as suggested.

(2) Figure 1 is not clear, the distribution of values is anomalously high. For instance, in 1B the distribution of values of V1/2 in the presence of cAMP goes from - 85 to -115. I agree that in the absence of cAMP, HCN4 in HEK293 cells shows some variability in V1/2 values, that nonetheless cannot be so wide (here the variability spans sometimes even 30 mV) and usually disappears with cAMP (here not).

With a large N, this is an expected distribution. In 5 previous reports from 4 different groups of HCN4 with cAMP in HEK 293 (Fenske et al., 2020; Liao et al., 2012; Peters et al., 2020; Saponaro et al., 2021; Schweizer et al., 2010), the average expected range of the data is 26.6 mV and 39.9 mV for 95% (mean ± 2SD) and 99% (mean ± 3SD) of the data, respectively. As the reviewer mentions the expected range from these papers is slightly larger in the absence of cAMP. The average SD of HCN4 (with/without cAMP) in papers are 9.9 mV (Schweizer et al., 2010), 4.4 mV (Saponaro et al., 2021), 7.6 mV (Fenske et al., 2020), 10.0 mV (Liao et al., 2012), and 5.9 mV (Peters et al., 2020). Our SD in this paper is roughly in the middle at 7.6 mV. This is likely because we used an inclusive approach to data so as not to bias our results (see the statistics section of the revised manuscript on page 9). We have removed 2 data points that meet the statistical classification as outliers, no measures of statistical significance were altered by this.

This problem is spread throughout the manuscript, and the measured mean effects are indeed always at the limit of statistical significance. Why so? Is this a problem with the analysis, or with the recordings?

The exact P-values are NOT typically at the limit of statistical significance, about 2/3rds would meet the stringent P < 0.0001 cut-off. We have clarified in the statistics section (page 10) that any comparison meeting our significance threshold (P < 0.05) or a stricter criterion is treated equally in the figure labelling. Exact P-values are provided in Tables 1-3.

There are several other problems with Figure 1 and in all figures of the manuscript: the Y scale is very narrow while the mean values are marked with large square boxes. Moreover, the exemplary activation curve of Figure 1A is not representative of the mean values reported in Figure 1B, and the values of 1B are different from those reported in Table 1.

Y-axis values for mean plots were picked such that all data points are included and are consistent across all figures. They have been expanded slightly (-75 to -145 mV for all HCN4 channels and -65 to -135 mV for all HCN2 channels). The size of the mean value marker has been reduced slightly. Exact midpoints for all data are also found in Tables 1-3.

The GV curves in Figure 1B (previously Fig. 1A) are averages with the ±SEM error bars smaller than the symbols in many cases owing to relatively high n’s for these datasets. These curves match the midpoints in panel 1C (previously 1B). Eg. the midpoint of the average curve for HCN4 control in panel A is -117.9 mV, the same as the -117.8 mV average for the individual fits in panel B.

We made an error in the text based on a previous manuscript version about the ordering of the tables that has now been fixed so these values should now be aligned.

On this ground, it is difficult to judge the conclusions and it would also greatly help if exemplary current traces would be also shown.

Exemplary current traces have been added to all figures in the revised manuscript.

(3) "....HCN4-P545A/T547F was insensitive to LRMP (Figs. 6B and 6C; Table 1), indicating that the unique HCN4 C-linker is necessary for regulation by LRMP. Thus, LRMP appears to regulate HCN4 by altering the interactions between the C-linker, S4-S5 linker, and Nterminus at the cAMP transduction centre."

Although this is an interesting theory, there are no data supporting it. Indeed, P545 and T547 at the tip of the C-linker elbow (fig 6A) are crucial for LRMP effect, but these two residues are not involved in the cAMP transduction centre (interface between HCND, S4S5 linker, and Clinker elbow), at least for the data accumulated till now in the literature. Indeed, the hypothesis that LRMP somehow inhibits the cAMP transduction mechanism of HCN4 given the fact that the two necessary residues P545 and T547 are close to the cAMP transduction centre, remains to be proven.

Moreover, I suggest analysing the putative role of P545 and T547 in light of the available HCN4 structures. In particular, T547 (elbow) points towards the underlying shoulder of the adjacent subunit and, therefore, is in a key position for the cAMP transduction mechanism. The presence of bulky hydrophobic residues (very different nature compared to T) in the equivalent position of HCN1 and HCN2 also favours this hypothesis. In this light, it will be also interesting to see whether a single T547F mutation is sufficient to prevent the LRMP effect.

We agree that testing this hypothesis would be very interesting. However, it is challenging. Any mutation we make that is involved in cAMP transduction makes measuring the LRMP effect on cAMP shifts difficult or impossible.

Our simple idea, now clarified in the discussion, is that if you look at the regions involved in cAMP transduction (HCND, C-linker, S4-S5), there are very few residues that differ between HCN4 and HCN2. When we mutate the 5 non-conserved residues in the S5 segment and the C-linker, along with the NT, we are able to render HCN2 sensitive to LRMP. Therefore, something about the small sequence differences in this region confer isoform specificity to LRMP. We speculate that this happens because of small structural differences that result from those 5 mutations. If you compare the solved structures of HCN1 and HCN4 (there is no HCN2 structure available), you can see small differences in the distances between key interacting residues in the transduction centre. Also, there is a kink at the bottom of the S4 helix in HCN4 but not HCN1. This points a putatively important residue for cAMP dependence in a different direction in HCN4. We hypothesize in the discussion that this may be how LRMP is isoform specific.

Moreover, previous work has shown that the HCN4 C-linker is uniquely sensitive to di-cyclic nucleotides and magnesium ions. We are hypothesizing that it is the subtle change in structure that makes this region more prone to regulation in HCN4.

Reviewing Editor (recommendations for the Authors):

(1) Exemplar recordings need to be shown and some explanation for the wide variability in the V-half of activation.

Exemplar currents are now shown for each channel. See the response to Reviewer 3’s public comment 2.

(2) The rationale for cut sites in LRMP for the investigation of which parts of the protein are important for blocking the effect of cAMP is not logically presented in light of the modular schematics of domains in the protein (N-term, CCD, post-CCD, etc).

There is limited structural data on LRMP and the HCN4 N-terminus. The cut sites in this paper were determined empirically. We made fragments that were small enough to work for our FRET hybridization approach and that expressed well in our HEK cell system. The residue numbering of the LRMP modules is based on updated structural predictions using Alphafold, which was released after our fragments were designed. This has been clarified in the methods section on pages 5-6 and the Figure 2 legend of the revised manuscript.

(3) Role of the HCN4 C-terminus. Truncation of the HCN4 C-terminus unstructured Cterminus distal to the CNBD (Fig. 4 A, B) partially reverses the impact of LRMP (i.e. there is now a significant increase in cAMP effect compared to full-length HCN4). The manuscript is written in a manner that minimizes the potential role of the C-terminus and it is, therefore, eliminated from consideration in subsequent experiments (e.g. FRET) and the discussion. The model is incomplete without considering the impact of the C-terminus.

We thank the reviewer for this comment as it was a result that we too readily dismissed. We have added discussion around this point and revised our model to suggest that not only can we not eliminate a role for the distal C-terminus, our data is consistent with it having a modest role. Our HCN4-2 chimera and HCN4-S719x data both suggest the possibility that the distal C-terminus might be having some effect on LRMP regulation. We have clarified this in the results (pages 12-13) and discussion (page 19).

(4) For FRET experiments, it is not clear why LF should show an interaction with N2 (residues 125-160) but not NF (residues 1-160). N2 is contained within NF, and given that Citrine and Cerulean are present on the C-terminus of LF and N2/NF, respectively, residues 1-124 in NF should not impact the detection of FRET because of greater separation between the fluorophores as suggested by the authors.

This is a fair point but FRET is somewhat more complicated. We do not know the structure of these fragments and it’s hard to speculate where the fluorophores are oriented in this type of assay. Moreover, this hybridization assay is sensitive to affinity and expression as well. There are a number of reasons why the larger 1-260 fragment might show reduced FRET compared to 125-260. As mentioned in our response to reviewer 2’s public comment 2, we have added a limitation section that outlines the various caveats of FRET that could explain this.

(5) For FRET experiments, the choice of using pieces of the channel that do not correlate with the truncations studied in functional electrophysiological experiments limits the holistic interpretation of the data. Also, no explanation or discussion is provided for why LRMP fragments that are capable of binding to the HCN4 N-terminus as determined by FRET (e.g. residues 1-108 and 110-230, respectively) do not have a functional impact on the channel.

As mentioned in the response to comment 2, the exact fragment design is a function of which fragments expressed well in HEK cells. Importantly, because FRET experiments do not provide atomic resolution for the caveats listed in the revised limitations section on page 20-21, small differences in the cut sites do not change the interpretation of these results. For example, the N-terminal 1-125 construct is analogous to experiments with the Δ1-130 HCN4 channel.

We suspect that residues in both fragments are required and that the interaction involves multiple parts. This is stated in the results “Thus, the first 227 residues of LRMP are sufficient to regulate HCN4, with residues in both halves of the LRMP N-terminus necessary for the regulation” (page 11). We have also added discussion on this on page 21.

(6) A striking result was that mutating two residues in the C-linker of HCN4 to amino acids found in HCN channels not affected by LRMP (P545A, T547F), completely eliminated the impact of LRMP on preventing cAMP regulation of channel activation. However, a chimeric channel, (HCN4-2) in which the C-linker, the CNBD, and the C-terminus of HCN4 were replaced by that of HCN2 was found to be partially responsive to LRMP. These two results appear inconsistent and not reconciled in the model proposed by the authors for how LRMP may be working.

As stated in our answer to your question #3, we have revised our interpretation of these data. If the more distal C-terminus plays some role in the orientation of the C-linker and the transduction centre as a whole, these data can still be viewed consistent with our model. We have added some discussion of this idea in our discussion section.

(7) Replacing the HCN2 N-terminus with that from HCN4, along with mutations in the S5 (MCS/VVG) and C-linker (AF/PT) recapitulated LRMP regulation on the HCN2 background. The functional importance of the S5 mutations is not clear as no other experiments are shown to indicate whether they are necessary for the observed effect.

We have added our experiments on a midpoint HCN2 clone that includes the S5 mutants and the C-linker mutants in the absence of the HCN4 N-terminus (ie HCN2 MCSAF/VVGPT) (Fig. 7). And we have discussed our rationale for the S5 mutations as we believe they may be responsible for the different orientations of the S4-S5 linker in HCN1 and HCN4 structures that are known to impact cAMP regulation.

Reviewer #1 (Recommendations For The Authors):

A) Comments:

(1) Figure 1: Please show some representative current traces.

Exemplar currents are now shown for each channel in the manuscript.

(2) Figure 1: There appears to be a huge number of recordings for HCN4 +/- cAMP as compared to those with LRMP 1-479Cit. How was the number of recordings needed for sufficient statistical power decided? This is particularly important because the observed slowing of deactivation by cAMP in Fig. 1C seems like it may be fairly subtle. Perhaps a swarm plot would make the shift more apparent? Also, LRMP 1-479Cit distributions in Fig. 1B-C look like they are more uniform than normal, so please double-check the appropriateness of the statistical test employed.

We have revised the methods section (page 7) to discuss this, briefly we performed regular control experiments throughout this project to ensure that a normal cAMP response was occurring. Our minimum target for sufficient power was 8-10 recordings. We have expanded the statistics section (page 9) to discuss tests of normality and the use of a log scale for deactivation time constants which is why the shifts in Fig. 1D (revised) are less apparent.

(3) It would be helpful if the authors could better introduce their logic for the M338V/C341V/S345G mutations in the HCN4-2 VVGPT mutant.

See response to the reviewing editor’s comment 7.

B) Minor Comments:

(1) pg. 9: "We found that LRMP 1-479Cit inhibited HCN4 to an even greater degree than the full-length LRMP, likely because expression of this tagged construct was improved compared to the untagged full-length LRMP, which was detected by co-transfection with GFP." Co-transfection with GFP seems like an extremely poor and a risky measure for LRMP expression.

We agree that the exact efficiency of co-transfection is contentious although some papers and manufacturer protocols indicate high co-transfection efficiency (Xie et al., 2011). In this paper we used both co-transfection and tagged proteins with similar results.

(2) pg 9: "LRMP 1-227 construct contains the N-terminus of LRMP with a cut-site near the Nterminus of the predicted coiled-coil sequence". In Figure 2 the graphic shows the coiledcoil domain starting at 191. What was the logic for splitting at 227 which appears to be the middle of the coiled-coil?

See response to the reviewing editor’s comment 2.

(3) Figure 5C: Please align the various schematics for HCN4 as was done for LRMP. It makes it much easier to decipher what is what.

Fig. 5 has been revised as suggested.

(4) pg 12: I assume that the HCN2 fragment chosen aligns with the HCN4 N2 fragment which shows binding, but this logic should be stated if that is the case. If not, then how was the HCN2 fragment chosen?

This is correct. This has been explicitly stated in the revised manuscript (page 14).

(5) Figure 7: Add legend indicating black/gray = HCN4 and blue = HCN2.

This has been stated in the revised figure legend.

(6) pg 17: Conservation of P545 and T547 across mammalian species is not shown or cited.

This sentence is not included in the revised manuscript, however, for the interest of the reviewer we have provided an alignment of this region across species here.

Author response image 1.

Reviewer #2 (Recommendations For The Authors):

(1) It is not clear whether in the absence of cAMP, LRMP also modestly shifts the voltagedependent activity of the channels. Please clarify.

We have clarified that LRMP does not shift the voltage-dependence in the absence of cAMP (page 10). In the absence of cAMP, LRMP does not significantly shift the voltagedependence of activation in any of the channels we have tested in this paper (or in our prior 2020 paper).

(2) Resolution of Fig. 8b is low.

We ultimately decided that the cartoon did not provide any important information for understanding our model and it was removed.

(3) Please add a supplementary figure showing the amino acid sequence of LRMP to show where the demarcations are made for each fragment as well as where the truncations were made as noted in Fig 3 and Fig 4.

A new supplementary figure showing the LRMP sequence has been added and cited in the methods section (page 5). Truncation sites have been added to the schematic in Fig. 2A.

(4) In the cartoon schematic illustration for Fig. 3 and Fig.4, the legend should include that the thick bold lines in the C-Terminal domain represent the CNBD, while the thick bold lines in the N-Terminal domain represent the HCN domain. This was mentioned in Liao 2012, as you referenced when you defined the construct S719X, but it would be nice for the reader to know that the thick bold lines you have drawn in your cartoon indicate that it also highlights the CNBD or the HCN domain.

This has been added to figure legends for the relevant figures in the revised manuscript.

(5) On page 12, missing a space between "residues" and "1" in the parenthesis "...LRMP L1 (residues1-108)...".

Fixed. Thank you.

(6) Which isoform of LRMP was used? What is the NCBI accession number? Is it the same one from Peters 2020 ("MC228229")?

This information has been added to the methods (page 5). It is the same as Peters 2020.

Reviewer #3 (Recommendations For The Authors):

(1) "Truncation of residues 1-62 led to a partial LRMP effect where cAMP caused a significant depolarizing shift in the presence of LRMP, but the activation in the presence of LRMP and cAMP was hyperpolarized compared to cAMP alone (Fig. 3B, C and 3E; Table 1). In the HCN4Δ1-130 construct, cAMP caused a significant depolarizing shift in the presence of LRMP; however, the midpoint of activation in the presence of LRMP and cAMP showed a non-significant trend towards hyperpolarization compared to cAMP alone (Fig. 3C and 3E; Table 1)".

This means that sequence 62-185 is necessary and sufficient for the LRMP effect. I suggest a competition assay with this peptide (synthetic, or co-expressed with HCN4 full-length and LRMP to see whether the peptide inhibits the LRMP effect).

We respectfully disagree with the reviewer’s interpretation. Our results, strongly suggest that other regions such as residues 25-65 (Fig. 3C) and C-terminal residues (Fig. 6) are also necessary. The use of a peptide could be an interesting future experiment, however, it would be very difficult to control relative expression of a co-expressed peptide. We think that our results in Fig. 7E-F where this fragment is added to HCN2 are a better controlled way of validating the importance of this region.

(2) "Truncation of the distal C-terminus (of HCN4) did not prevent LRMP regulation. In the presence of both LRMP and cAMP the activation of HCN4-S719X was still significantly hyperpolarized compared to the presence of cAMP alone (Figs. 4A and 4B; Table 1). And the cAMP-induced shift in HCN4-S719X in the presence of LRMP (~7mV) was less than half the shift in the absence of LRMP (~18 mV)."

On the basis of the partial effects reported for the truncations of the N-terminus of HCN4 162 and 1-130 (Fig 3B and C), I do not think it is possible to conclude that "truncation of the distal C-terminus (of HCN4) did not prevent LRMP regulation". Indeed, cAMP-induced shift in HCN4 Δ1-62 and Δ1-130 in the presence of LRMP were 10.9 and 10.5 mV, respectively, way more than the ~7mV measured for the HCN4-S719X mutant.

As you rightly stated at the end of the paragraph:" Together, these results show significant LRMP regulation of HCN4 even when the distal C-terminus is truncated, consistent with a minimal role for the C-terminus in the regulatory pathway". I would better discuss this minimal role of the C-terminus. It is true that deletion of the first 185 aa of HCN4 Nterminus abolishes the LRMP effect, but it is also true that removal of the very Cterm of HCN4 does affect LRMP. This unstructured C-terminal region of HCN4 contains isotype-specific sequences. Maybe they also play a role in recognizing LRMP. Thus, I would suggest further investigation via truncations, even internal deletions of HCN4-specific sequences.

Please see the response to the reviewing editor’s comment 3.

(3) Figure 5: The N-terminus of LRMP FRETs with the N-terminus of HCN4.

Why didn't you test the same truncations used in Fig. 3? Indeed, based on Fig 3, sequences 1-25 can be removed. I would have considered peptides 26-62 and 63-130 and 131-185 and a fourth (26-185). This set of peptides will help you connect binding with the functional effects of the truncations tested in Fig 3.

Please see the response to the reviewing editor’s comment 2 and 5.

Why didn't you test the C-terminus (from 719 till the end) of HCN4? This can help with understanding why truncation of HCN4 Cterminus does affect LRMP, tough partially (Fig. 4A).

Please see the response to the reviewing editor’s comment 3.

(4) "We found that a previously described HCN4-2 chimera containing the HCN4 N-terminus and transmembrane domains (residues 1-518) with the HCN2 C-terminus (442-863) (Liao et al., 2012) was partially regulated by LRMP (Fig. 7A and 7B)".

I do not understand this partial LRMP effect on the HCN4-2 chimera. In Fig. 6 you have shown that the "HCN4-P545A/T547F was insensitive to LRMP (Figs. 6B and 6C; Table 1), indicating that the unique HCN4 C-linker is necessary for regulation by LRMP". How can be this reconciled with the HCN4-2 chimera? HCN4-2, "containing" P545A/T547F mutations, should not perceive LRMP.

Please see the response to the reviewing editor’s comment 6.

(5) "we next made a targeted chimera of HCN2 that contains the distal HCN4 N-terminus (residues 1-212) and the HCN2 transmembrane and C-terminal domains with 5 point mutants in non-conserved residues of the S5 segment and C-linker elbow (M338V/C341V/S345G/A467P/F469T)......Importantly, the HCN4-2 VVGPT channel is insensitive to cAMP in the presence of LRMP (Fig. 7C and 7D), indicating that the HCN4 Nterminus and cAMP-transduction centre residues are sufficient to confer LRMP regulation to HCN2".

Why did you insert also the 3 mutations of S5? Are these mutations somehow involved in the cAMP transduction mechanism?

You have already shown that in HCN4 only P545 and T547 (Clinker) are necessary for LRMP effect. I suggest to try, at least, the chimera of HCN2 with only A467P/F469T. They should work without the 3 mutations in S5.

Please see the response to the reviewing editor’s comment 7.

Author response:

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

eLife assessment 

fMRI was used to address an important aspect of human cognition - the capacity for structured representations and symbolic processing - in a cross-species comparison with non-human primates (macaques); the experimental design probed implicit symbolic processing through reversal of learned stimulus pairs. The authors present solid evidence in humans that helps elucidate the role of brain networks in symbolic processing, however the evidence from macaques was incomplete (e.g., sample size constraints, potential and hard-to-quantify differences in attention allocation, motivation, and lived experience between species).

Thank you very much for your assessment. We would like to address the potential issues that you raise point-by-point below.

We agree that for macaque monkey physiology, sample size is always a constraint, due to both financial and ethical reasons. We addressed this concern by combining the results from two different labs, which allowed us to test 4 animals in total, which is twice as much as what is common practice in the field of primate physiology. (We discuss this now on lines 473-478.)

Interspecies differences in motivation, attention allocation, task strategies etc. could also be limiting factors. Note that we did address the potential lack of attention allocation directly in Experiment 2 using implicit reward association, which was successful as evidenced by the activation of attentional control areas in the prefrontal cortex. We cannot guarantee that the strategies that the two species deploy are identical, but we tentatively suggest that this might be a less important factor in the present study than in other interspecies comparisons that use explicit behavioral reports. In the current study, we directly measured surprise responses in the brain in the absence of any explicit instructions in either species, which allowed us to  measure the spontaneous reversal of learned associations, which is a very basic element of symbolic representation. Our reasoning is that such spontaneous responses should be less dependent on attention allocation and task strategies. (We discuss this now in more detail on lines 478-485.)

Finally, lived experience could be a major factor. Indeed, obvious differences include a lifetime of open-field experiences and education in our human adult subjects, which was not available to the monkey subjects, and includes a strong bias towards explicit learning of symbolic systems (e.g. words, letters, digits, etc). However, we have previously shown that 5-month-old human infants spontaneously generalize learning to the reversed pairs after a short learning in the lab using EEG (Kabdebon et al, PNAS, 2019). This indicates that also with very limited experience, humans spontaneously reverse learned associations. (We discuss this now in more detail on lines 478-485.) It could be very interesting to investigate whether spontaneous reversal could be present in infant macaque monkeys, as there might be a critical period for this effect. Although neurophysiology in awake infant monkeys is highly challenging, it would be very relevant for future work. (We discuss this in more detail on lines 493-498.)

Public Reviews: 

Reviewer #1 (Public Review): 

Kerkoerle and colleagues present a very interesting comparative fMRI study in humans and monkeys, assessing neural responses to surprise reactions at the reversal of a previously learned association. The implicit nature of this task, assessing how this information is represented without requiring explicit decision-making, is an elegant design. The paper reports that both humans and monkeys show neural responses across a range of areas when presented with incongruous stimulus pairs. Monkeys also show a surprise response when the stimuli are presented in a reversed direction. However, humans show no such surprise response based on this reversal, suggesting that they encode the relationship reversibly and bidirectionally, unlike the monkeys. This has been suggested as a hallmark of symbolic representation, that might be absent in nonhuman animals. 

I find this experiment and the results quite compelling, and the data do support the hypothesis that humans are somewhat unique in their tendency to form reversible, symbolic associations. I think that an important strength of the results is that the critical finding is the presence of an interaction between congruity and canonicity in macaques, which does not appear in humans. These results go a long way to allay concerns I have about the comparison of many human participants to a very small number of macaques. 

We thank the reviewer for the positive assessment. We also very much appreciate the point about the interaction effect in macaque monkeys – indeed, we do not report just a negative finding. 

I understand the impossibility of testing 30+ macaques in an fMRI experiment. However, I think it is important to note that differences necessarily arise in the analysis of such datasets. The authors report that they use '...identical training, stimuli, and whole-brain fMRI measures'. However, the monkeys (in experiment 1) actually required 10 times more training. 

We agree that this description was imprecise. We have changed it to “identical training stimuli” (line 151), indeed the movies used for training were strictly identical. Furthermore, please note that we do report the fMRI results after the same training duration. In experiment 1, after 3 days of training, the monkeys did not show any significant results, even in the canonical direction. However, in experiment 2, with increased attention and motivation, a significant effect was observed on the first day of scanning after training, as was found in human subjects (see Figure 4 and Table 3).

More importantly, while the fMRI measures are the same, group analysis over 30+ individuals is inherently different from comparing only 2 macaques (including smoothing and averaging away individual differences that might be more present in the monkeys, due to the much smaller sample size). 

Thank you for understanding that a limited sampling size is intrinsic to macaque monkey physiology. We also agree that data analysis in humans and monkeys is necessarily different. As suggested by the reviewer, we added an analysis to address this, see the corresponding reply to the ‘Recommendations for the authors’ section below.

Despite this, the results do appear to show that macaques show the predicted interaction effect (even despite the sample size), while humans do not. I think this is quite convincing, although had the results turned out differently (for example an effect in humans that was absent in macaques), I think this difference in sample size would be considerably more concerning. 

Thank you for noting this. Indeed, the interaction effect is crucial, and the task design was explicitly made to test this precise prediction, described in our manuscript as the “reversibility hypothesis”. The congruity effect in the learned direction served as a control for learning, while the corresponding congruity effect in the reversed direction tested for spontaneous reversal. The reversibility hypothesis stipulates that in humans there should not be a difference between the learned and the reversed direction, while there should be for monkeys. We already wrote about that in the result section of the original manuscript and now also describe this more explicitly in the introduction and beginning of the result section.

I would also note that while I agree with the authors' conclusions, it is notable to me that the congruity effect observed in humans (red vs blue lines in Fig. 2B) appears to be far more pronounced than any effect observed in the macaques (Fig. 3C-3). Again, this does not challenge the core finding of this paper but does suggest methodological or possibly motivational/attentional differences between the humans and the monkeys (or, for example, that the monkeys had learned the associations less strongly and clearly than the humans). 

As also explained in response to the eLife assessment above, we expanded the “limitations” section of the discussion, with a deeper description of the possible methodological differences between the two species (see lines 478-485).

With the same worry in mind, we did increase the attention and motivation of monkeys in experiment 2, and indeed obtained a greater activation to the canonical pairs and their violation, -notably in the prefrontal cortex – but crucially still without reversibility.

In the end, we believe that the striking interspecies difference in size and extent of the violation effect, even for purely canonical stimuli, is an important part of our findings and points to a more efficient species-specific learning system, that our experiment tentatively relates to a symbolic competence.

This is a strong paper with elegant methods and makes a worthwhile contribution to our understanding of the neural systems supporting symbolic representations in humans, as opposed to other animals. 

We again thank the reviewer for the positive review.

Reviewer #2 (Public Review): 

In their article titled "Brain mechanisms of reversible symbolic reference: a potential singularity of the human brain", van Kerkoerle et al address the timely question of whether non-human primates (rhesus macaques) possess the ability for reverse symbolic inference as observed in humans. Through an fMRI experiment in both humans and monkeys, they analyzed the bold signal in both species while observing audio-visual and visual-visual stimuli pairs that had been previously learned in a particular direction. Remarkably, the findings pertaining to humans revealed that a broad brain network exhibited increased activity in response to surprises occurring in both the learned and reverse directions. Conversely, in monkeys, the study uncovered that the brain activity within sensory areas only responded to the learned direction but failed to exhibit any discernible response to the reverse direction. These compelling results indicate that the capacity for reversible symbolic inference may be unique to humans. 

In general, the manuscript is skillfully crafted and highly accessible to readers. The experimental design exhibits originality, and the analyses are tailored to effectively address the central question at hand.

Although the first experiment raised a number of methodological inquiries, the subsequent second experiment thoroughly addresses these concerns and effectively replicates the initial findings, thereby significantly strengthening the overall study. Overall, this article is already of high quality and brings new insight into human cognition. 

We sincerely thank the reviewer for the positive comments. 

I identified three weaknesses in the manuscript: 

- One major issue in the study is the absence of significant results in monkeys. Indeed, authors draw conclusions regarding the lack of significant difference in activity related to surprise in the multidemand network (MDN) in the reverse congruent versus reverse incongruent conditions. Although the results are convincing (especially with the significant interaction between congruency and canonicity), the article could be improved by including additional analyses in a priori ROI for the MDN in monkeys (as well as in humans, for comparison). 

First, we disagree with the statement about “absence of significant results in monkeys”. We do report a significant interaction which, as noted by the referee, is a crucial positive finding.

Second, we performed the suggested analysis for experiment 2, using the bilateral ROIs of the putative monkey MDN from previous literature (Mitchell, et al. 2016), which are based on the human study by Fedorenko et al. (PNAS, 2013). 

Author response table 1.

Congruity effect for monkeys in Experiment 2 within the ROIs of the MDN (n=3). Significance was assessed with one-sided one-sample t-tests.

As can be seen, none of the regions within the monkey MDN showed an FDR-corrected significant difference or interaction. Although the absence of a canonical congruity effect makes it difficult to draw strong conclusions, it did approach significance at an uncorrected level in the lateral frontal posterior region, similar to  the large prefrontal effect we report in Figures 4 and 5. Furthermore, for the reversed congruity effect there was never even a trend at the uncorrected level, and the crucial interaction of canonicity and congruity again approached significance in the lateral prefrontal cortex.  

We also performed an ANOVA  in the human participants of the VV experiment on the average betas across the 7 different fronto-parietal ROIs as used by Mitchell et al to define their equivalent to the monkey brain (Fig 1a, right in Mitchell et al. 2016) with congruity, canonicity and hemisphere (except for the anterior cingulate which is a bilateral ROI) as within-subject factors. We confirmed the results presented in the manuscript (Figure 4C) with notably no significant interaction between congruity and canonicity in any of these ROIs (all F-values (except insula) <1). A significant main effect of congruity was observed in the posterior middle frontal gyrus (MFG) and inferior precentral sulcus at the FDR corrected level. Analyses restricted to the canonical trials found a congruity effect in these two regions plus the anterior insula and anterior cingulate/presupplementary motor area, whereas no ROIs were significant at a FDR corrected level for reverse trials. There was a trend in the middle MFG and inferior precentral region for reversed trials. Crucially, there was not even a trend for the interaction between congruity and canonicity at the uncorrected level. The difference in the effect size between the canonical and reversed direction can therefore be explained by the larger statistical power due to the larger number of congruent trials (70%, versus 10% for the other trial conditions), not by a significant effect by the canonical and the reversed direction. 

Author response table 2.

Congruity effect for humans in Experiment 2 within the ROIs of the MDN (n=23).

These results support our contention that the type of learning of the stimulus pairs was very different in the two species. We thank the reviewer for suggesting these relevant additional analyses.

- While the authors acknowledge in the discussion that the number of monkeys included in the study is considerably lower compared to humans, it would be informative to know the variability of the results among human participants. 

We agree that this is an interesting question, although it is also very open-ended. For instance, we could report each subjects’ individual whole-brain results, but this would take too much space (and the interested reader will be able to do so from the data that we make available as part of this publication). As a step in this direction, we provide below a figure showing the individual congruity effects, separately for each experiment and for each ROI of table 5, and for each of the 52 participants for whom an fMRI localizer was available:

Author response image 1.

Difference in mean betas between congruent and incongruent conditions in a-priori linguistic and mathematical ROIs (see definition and analyses in Table 5) in both experiments (experiment 1 = AV, left panel; experiment 2= VV, right panel). Dots correspond to participants (red: canonical trials, green reversed trials).The boxplot notch is located at the median and the lower and upper box hinges at the 25th and 75th centiles. Whiskers extend to 1.5 inter-quartile ranges on either side of the hinges. ROIs are ranked by the median of the Incongruent-Congruent difference across canonical and reversed order, within a given experiment. For purposes of comparison between the two experiments, we have underlined with colors the top-five common ROIs between the two experiments. N.s.: non-significant congruity effect (p>0.05)

Several regions show a rather consistent difference across subjects (see, for instance, the posterior STS in experiment 1, left panel). Overall, only 3 of the 52 participants did not show any beta superior to 2 in canonical or reversed in any ROIs. The consistency is quite striking, given the limited number of test trials (in total only 16 incongruent trials per direction per participant), and the fact that these ROIs were selected for their responses to spoken or written  sentences, as part of a subsidiary task quite different from the main task.

- Some details are missing in the methods.  

Thank you for these comments, we reply to them point-by-point below.

Reviewer #3 (Public Review): 

This study investigates the hypothesis that humans (but not non-human primates) spontaneously learn reversible temporal associations (i.e., learning a B-A association after only being exposed to A-B sequences), which the authors consider to be a foundational property of symbolic cognition. To do so, they expose humans and macaques to 2-item sequences (in a visual-auditory experiment, pairs of images and spoken nonwords, and in a visual-visual experiment, pairs of images and abstract geometric shapes) in a fixed temporal order, then measure the brain response during a test phase to congruent vs. incongruent pairs (relative to the trained associations) in canonical vs. reversed order (relative to the presentation order used in training). The advantage of neuroimaging for this question is that it removes the need for a behavioral test, which non-human primates can fail for reasons unrelated to the cognitive construct being investigated. In humans, the researchers find statistically indistinguishable incongruity effects in both directions (supporting a spontaneous reversible association), whereas in monkeys they only find incongruity effects in the canonical direction (supporting an association but a lack of spontaneous reversal). Although the precise pattern of activation varies by experiment type (visual-auditory vs. visual-visual) in both species, the authors point out that some of the regions involved are also those that are most anatomically different between humans and other primates. The authors interpret their finding to support the hypothesis that reversible associations, and by extension symbolic cognition, is uniquely human. 

This study is a valuable complement to prior behavioral work on this question. However, I have some concerns about methods and framing. 

We thank the reviewer for the careful summary of the manuscript, and the positive comments.

Methods - Design issues: 

The authors originally planned to use the same training/testing protocol for both species but the monkeys did not learn anything, so they dramatically increased the amount of training and evaluation. By my calculation from the methods section, humans were trained on 96 trials and tested on 176, whereas the monkeys got an additional 3,840 training trials and 1,408 testing trials. The authors are explicit that they continued training the monkeys until they got a congruity effect. On the one hand, it is commendable that they are honest about this in their write-up, given that this detail could easily be framed as deliberate after the fact. On the other hand, it is still a form of p-hacking, given that it's critical for their result that the monkeys learn the canonical association (otherwise, the critical comparison to the non-canonical association is meaningless). 

Thank you for this comment. 

Indeed, for experiment 1, the amount of training and testing was not equal for the humans and monkeys, as also mentioned by reviewer 2. We now describe in more detail how many training and imaging days we used for each experiment and each species, as well as the number of blocks per day and the number of trials per block (see lines 572-577). We also added the information on the amount of training receives to all of the legends of the Tables.

We are sorry for giving the impression that we trained until the monkeys learned this. This was not the case. Based on previous literature, we actually anticipated that the short training would not be sufficient, and therefore planned additional training in advance. Specifically, Meyer & Olson (2011) had observed pair learning in the inferior temporal cortex of macaque monkeys after 816 exposures per pair. This is similar to the additional training we gave, about 80 blocks with 12 trials per pair per block. This is  now explained in more detail (lines 577-580).

Furthermore, we strongly disagree with the pejorative term p-hacking. The aim of the experiment was not to show a congruency effect in the canonical direction in monkeys, but to track and compare their behavior in the same paradigm as that of humans for the reverse direction. It would have been unwise to stop after human-identical training and only show that humans learn better, which is a given. Instead, we looked at brain activations at both times, at the end of human-identical training and when the monkeys had learned the pairs in the canonical direction. 

Finally, in experiment 2, monkeys were tested after the same 3 days of training as humans. We wrote: “Using this design, we obtained significant canonical congruity effects in monkeys on the first imaging day after the initial training (24 trials per pair), indicating that the animals had learned the associations” (lines 252-253).

(2) Between-species comparisons are challenging. In addition to having differences in their DNA, human participants have spent many years living in a very different culture than that of NHPs, including years of formal education. As a result, attributing the observed differences to biology is challenging. One approach that has been adopted in some past studies is to examine either young children or adults from cultures that don't have formal educational structures. This is not the approach the authors take. This major confound needs to minimally be explicitly acknowledged up front. 

Thank you for raising this important point. We already had a section on “limitations” in the manuscript, which we now extended (line 478-485). Indeed, this study is following a previous study in 5-month-old infants using EEG, in which we already showed that after learning associations between labels and categories, infants spontaneously generalize learning to the reversed pairs after a short learning period in the lab (Kabdebon et al, PNAS, 2019). We also cited preliminary results of the same paradigm as used in the current study but using EEG in 4-month-old infants (Ekramnia and Dehaene-Lambertz, 2019), where we replicated the results obtained by Kabdebon et al. 2019 showing that preverbal infants spontaneously generalize learning to the reversed pairs. 

Functional MRI in awake infants remains a challenge at this age (but see our own work, DehaeneLambertz et al, Science, 2002), especially because the experimental design means only a few trials in the conditions of interest (10%) and thus a long experimental duration that exceed infants’ quietness and attentional capacities in the noisy MRI environment. (We discuss this on lines 493-496.)

(3) Humans have big advantages in processing and discriminating spoken stimuli and associating them with visual stimuli (after all, this is what words are in spoken human languages). Experiment 2 ameliorates these concerns to some degree, but still, it is difficult to attribute the failure of NHPs to show reversible associations in Experiment 1 to cognitive differences rather than the relative importance of sound string to meaning associations in the human vs. NHP experiences. 

As the reviewer wrote, we deliberately performed Experiment 2 with visual shapes to control for various factors that might have explained the monkeys' failure in Experiment 1. 

(4) More minor: The localizer task (math sentences vs. other sentences) makes sense for math but seems to make less sense for language: why would a language region respond more to sentences that don't describe math vs. ones that do? 

The referee is correct: our use of the word “reciprocally” was improper (although see Amalric et Dehaene, 2016 for significant differences in both directions when non-mathematical sentences concern specific knowledge). We changed the formulation to clarify this as follows: “In these ROIs, we recovered the subject-specific coordinates of each participant’s 10% best voxels in the following comparisons: sentences vs rest for the 6 language Rois ; reading vs listening for the VWFA ; and numerical vs non-numerical sentences for the 8 mathematical ROIs.” (lines 678-680).

Methods - Analysis issues: 

(5) The analyses appear to "double dip" by using the same data to define the clusters and to statistically test the average cluster activation (Kriegeskorte et al., 2009). The resulting effect sizes are therefore likely inflated, and the p-values are anticonservative. 

It is not clear to us which result the reviewer is referring to. In Tables 1-4, we report the values that we found significant in the whole brain analysis, we do not report additional statistical tests for this data. For Table 5, the subject-specific voxels were identified through a separate localizer experiment, which was designed to pinpoint the precise activation areas for each subject in the domains of oral and written language-processing and math. Subsequently, we compared the activation at these voxel locations across different conditions of the main experiment. Thus, the two datasets were distinct, and there was no double dipping. In both interpretations of the comment, we therefore disagree with the reviewer.

Framing: 

(6) The framing ("Brain mechanisms of reversible symbolic reference: A potential singularity of the human brain") is bigger than the finding (monkeys don't spontaneously reverse a temporal association but humans do). The title and discussion are full of buzzy terms ("brain mechanisms", "symbolic", and "singularity") that are only connected to the experiments by a debatable chain of assumptions. 

First, this study shows relatively little about brain "mechanisms" of reversible symbolic associations, which implies insights into how these associations are learned, recognized, and represented. But we're only given standard fMRI analyses that are quite inconsistent across similar experimental paradigms, with purely suggestive connections between these spatial patterns and prior work on comparative brain anatomy. 

We agree with the referee that the term “mechanism” is ambiguous and, for systems neuroscientists, may suggest more than we are able to do here with functional MRI. We changed the title to “Brain areas for reversible symbolic reference, a potential singularity of the human brain”. This title better describes our specific contribution: mapping out the areas involved in reversibility in humans, and showing that they do not seem to respond similarly in macaque monkeys.

Second, it's not clear what the relationship is between symbolic cognition and a propensity to spontaneously reverse a temporal association. Certainly, if there are inter-species differences in learning preferences this is important to know about, but why is this construed as a difference in the presence or absence of symbols? Because the associations aren't used in any downstream computation, there is not even any way for participants to know which is the sign and which is the signified: these are merely labels imposed by the researchers on a sequential task. 

As explained in the introduction, the reversibility test addressed a very minimal core property of symbolic reference. There cannot be a symbol if its attachment doesn’t operate in both directions. Thus, this property is necessary – but we agree that it is not sufficient. Indeed, more tests are needed to establish whether and how the learned symbols are used in further downstream compositional tasks (as discussed in our recent TICS papers, Dehaene et al. 2022). We added a sentence in the introduction to acknowledge this fact:

“Such reversibility is a core and necessary property of symbols, although we readily acknowledge that it is not sufficient, since genuine symbols present additional referential and compositional properties that will not be tested in the present work.” (lines 89-92).

Third, the word "singularity" is both problematically ambiguous and not well supported by the results. "Singularity" is a highly loaded word that the authors are simply using to mean "that which is uniquely human". Rather than picking a term with diverse technical meanings across fields and then trying to restrict the definition, it would be better to use a different term. Furthermore, even under the stated definition, this study performed a single pairwise comparison between humans and one other species (macaques), so it is a stretch to then conclude (or insinuate) that the "singularity" has been found (see also pt. 2 above). 

We have published an extensive review including a description of our use of the term “singularity” (Dehaene et al., TICS 2022). Here is a short except: “Humans are different even in domains such as drawing and geometry that do not involve communicative language. We refer to this observation using the term “human cognitive singularity”, the word singularity being used here in its standard meaning (the condition of being singular) as well as its mathematical sense (a point of sudden change). Hominization was certainly a singularity in biological evolution, so much so that it opened up a new geological age (the Anthropocene). Even if evolution works by small continuous change (and sometimes it doesn’t [4]), it led to a drastic cognitive change in humans.”

We find the referee’s use of the pejorative term ”insinuate” quite inappropriate. From the title on, we are quite nuanced and refer only to a “potential singularity”. Furthermore, as noted above, we explicitly mention in the discussion the limitations of our study, and in particular the fact that only a single non-human species was tested (see lines 486-493). We are working hard to get chimpanzee data, but this is remarkably difficult for us, and we hope that our paper will incite other groups to collect more evidence on this point.

(7) Related to pt. 6, there is circularity in the framing whereby the authors say they are setting out to find out what is uniquely human, hypothesizing that the uniquely human thing is symbols, and then selecting a defining trait of symbols (spontaneous reversible association) *because* it seems to be uniquely human (see e.g., "Several studies previously found behavioral evidence for a uniquely human ability to spontaneously reverse a learned association (Imai et al., 2021; Kojima, 1984; Lipkens et al., 1988; Medam et al., 2016; Sidman et al., 1982), and such reversibility was therefore proposed as a defining feature of symbol representation reference (Deacon, 1998; Kabdebon and DehaeneLambertz, 2019; Nieder, 2009).", line 335). They can't have it both ways. Either "symbol" is an independently motivated construct whose presence can be independently tested in humans and other species, or it is by fiat synonymous with the "singularity". This circularity can be broken by a more modest framing that focuses on the core research question (e.g., "What is uniquely human? One possibility is spontaneous reversal of temporal associations.") and then connects (speculatively) to the bigger conceptual landscape in the discussion ("Spontaneous reversal of temporal associations may be a core ability underlying the acquisition of mental symbols").

We fail to understand the putative circularity that the referee sees in our introduction. We urge him/her to re-read it, and hope that, with the changes that we introduced, it does boil down to his/her summary, i.e. “What is uniquely human? One possibility is spontaneous reversal of temporal associations."

Reviewer #1 (Recommendations For The Authors): 

In general, the manuscript was very clear, easy to read, and compelling. I would recommend the authors carefully check the text for consistency and minor typos. For example: 

The sample size for the monkeys kept changing throughout the paper. E.g., Experiment 1: n = 2 (line 149); n = 3 (line 205).  

Thank you for catching this error, we corrected it. The number of animals was indeed 2  for experiment 1, and 3 for experiment 2. (Animals JD and YS participated in experiment 1 and JD, JC and DN in experiment 2. So only JD participated in both experiments.)

Similarly, the number of stimulus pairs is reported inconsistently (4 on line 149, 5 pairs later in the paper). 

We’re sorry that this was unclear. We used 5 sets of 4 audio-visual pairs each. We now clarify this, on line 157 and on lines 514-516.

At least one case of p>0.0001, rather than p < 0.0001 (I assume). 

Thank you once again, we now corrected this.

Reviewer #2 (Recommendations For The Authors): 

One major issue in the study is the absence of significant results in monkeys. Indeed, the authors draw conclusions regarding the lack of significant difference in activity related to surprise in the multidemand network (MDN) in the reverse congruent versus reverse incongruent conditions. Although the results are convincing (especially with the significant interaction between congruency and canonicity), the article could be improved by including additional analyses in a priori ROI for the MDN in monkeys (as well as in humans, for comparison). In other words: what are the statistics for the MDN regarding congruity, canonicity, and interaction in both species? Since the authors have already performed this type of analysis for language and Math ROIs (table 5), it should be relatively easy for them to extend it to the MDN. Demonstrating that results in monkeys are far from significant could further convince the reader. 

Furthermore, while the authors acknowledge in the discussion that the number of monkeys included in the study is considerably lower compared to humans, it would be informative to know the variability of the results among human participants. Specifically, it would be valuable to describe the proportion of human participants in which the effects of congruency, canonicity, and their interaction are significant. Additionally, stating the variability of the F-values for each effect would provide reassurance to the reader regarding the distinctiveness of humans in comparison to monkeys. Low variability in the results would serve to mitigate concerns that the observed disparity is merely a consequence of testing a unique subset of monkeys, which may differ from the general population. Indeed, this would be a greater support to the notion that the dissimilarity stems from a genuine distinction between the two species. 

We responded to both of these points above.

In terms of methods, details are missing: 

- How many trials of each condition are there exactly? (10% of 44 trials is 4.4) : 

We wrote: “In both humans and monkeys, each block started with 4 trials in the learned direction (congruent canonical trials), one trial for each of the 4 pairs (2 O-L and 2 L-O pairs). The rest of the block consisted of 40 trials in which 70% of trials were identical to the training; 10% were incongruent pairs but the direction (O-L or L-O) was correct (incongruent canonical trials), thus testing whether the association was learned; 10% were congruent pairs but the direction within the pairs was reversed relative to the learned pairs (congruent reversed trials) and 10% were incongruent pairs in reverse (incongruent reversed trials).”(See lines 596-600.)

Thus, each block comprised 4 initial trials, 28 canonical congruent trials, 4 canonical incongruent, 4 reverse congruent and 4 reverse incongruent trials, i.e. 4+28+3x4=40 trials.

- How long is one trial? 

As written in the method section: “In each trial, the first stimulus (label or object) was presented during 700ms, followed by an inter-stimulus-interval of 100ms then the second stimulus during 700ms. The pairs were separated by a variable inter-trial-interval of 3-5 seconds” i.e. 700+100+700=1500, plus 3 to 4.75 seconds of blank between the trials (see lines 531-533).

- How are the stimulus presentations jittered? 

See : “The pairs were separated by a variable inter-trial-interval randomly chosen among eight different durations between 3 and 4.75 seconds (step=250 ms). The series of 8 intervals was randomized again each time it was completed.”(lines 533-535).

- What is the statistical power achieved for humans? And for monkeys? 

We know of no standard way to define power for fMRI experiments. Power will depend on so many parameters, including the fMRI signal-to-noise ratio, the attention of the subject, the areas being considered, the type of analysis (whole-brain versus ROIs), etc.

- Videos are mentioned in the methods, is it the image and sound? It is not clear. 

We’re sorry that it was unclear. Video’s were only used for the training of the human subjects. We now corrected this in the method section (lines 552-554).

Reviewer #3 (Recommendations For The Authors): 

The main recommendations are to adjust the framing (making it less bold and more connected to the empirical evidence) and to ensure independence in the statistical analyses of the fMRI data. 

See our replies to the reviewer’s comments on “Framing” above. In particular, we changed the title of the paper from “Brain mechanisms of reversible symbolic reference” to “Brain areas for reversible symbolic reference”.

References cited in this response

Dehaene, S., Al Roumi, F., Lakretz, Y., Planton, S., & Sablé-Meyer, M. (2022). Symbols and mental programs : A hypothesis about human singularity. Trends in Cognitive Sciences, 26(9), 751‑766. https://doi.org/10.1016/j.tics.2022.06.010.

Dehaene-Lambertz, Ghislaine, Stanislas Dehaene, et Lucie Hertz-Pannier. Functional Neuroimaging of Speech Perception in Infants. Science 298, no 5600 (2002): 2013-15. https://doi.org/10.1126/science.1077066.

Ekramnia M, Dehaene-Lambertz G. 2019. Investigating bidirectionality of associations in young infants as an approach to the symbolic system. Presented at the CogSci. p. 3449.

Fedorenko E, Duncan J, Kanwisher N (2013) Broad domain generality in focal regions of frontal and parietal cortex. Proc Natl Acad Sci U S A 110:16616-16621.

Kabdebon, Claire, et Ghislaine Dehaene-Lambertz. « Symbolic Labeling in 5-Month-Old Human Infants ». Proceedings of the National Academy of Sciences 116, no 12 (2019): 5805-10. https://doi.org/10.1073/pnas.1809144116.

Mitchell, D. J., Bell, A. H., Buckley, M. J., Mitchell, A. S., Sallet, J., & Duncan, J. (2016). A Putative Multiple-Demand System in the Macaque Brain. Journal of Neuroscience, 36(33), 8574‑8585. https://doi.org/10.1523/JNEUROSCI.0810-16.2016

Author Response

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

Reviewer #1 (Public Review):

The biogenesis of outer membrane proteins (OMPs) into the outer membranes of Gram-negative bacteria is still not fully understood, particularly substrate recognition and insertion by beta-assembly machinery (BAM). In the studies, the authors present their studies that in addition to recognition by the last strand of an OMP, sometimes referred to as the beta-signal, an additional signal upstream of the last strand is also important for OMP biogenesis.

Strengths:

1. Overall the manuscript is well organized and written, and addresses an important question in the field. The idea that BAM recognizes multiple signals on OMPs has been presented previously, however, it was not fully tested.

2. The authors here re-address this idea and propose that it is a more general mechanism used by BAM for OMP biogenesis.

3. The notion that additional signals assist in biogenesis is an important concept that indeed needs fully tested in OMP biogenesis.

4. A significant study was performed with extensive experiments reported in an attempt to address this important question in the field.

5. The identification of important crosslinks and regions of substrates and Bam proteins that interact during biogenesis is an important contribution that gives clues to the path substrates take en route to the membrane.

Weaknesses:

Major critiques (in no particular order):

1. The title indicates 'simultaneous recognition', however no experiments were presented that test the order of interactions during OMP biogenesis.

We have replaced the word “Simultaneous” with “Dual” so as not to reflect on the timing of the recognition events for the distinct C-terminal signal and -5 signal.

1. Aspects of the study focus on the peptides that appear to inhibit OmpC assembly, but should also include an analysis of the peptides that do not to determine this the motif(s) present still or not.

We thank the reviewer for this comment. Our study focuses on the peptides which exhibited an inhibitory effect in order to elucidate further interactions between the BAM complex and substrate proteins, especially in early stage of the assembly process. In the case of peptide 9, which contains all of our proposed elements but did not have an inhibitory effect, there is the presence of an arginine residue at the polar residue next to hydrophobic residue in position 0 (0 Φ). As seen in Fig S5, S6, and S7, there are no positively charged amino acids in the polar residue positions in the -5 or last strands. This might be the reason why peptide 9, as well as peptide 24, the β-signal derived from the mitochondrial OMP Tom40 and contains a lysine at the polar position, did not display an inhibitory effect. Incorporating the reviewer's suggestions might elucidate conditions that should not be added to the elements, but this is not the focus of this paper and was not discussed to avoid complicating the paper.

1. The β-signal is known to form a β-strand, therefore it is unclear why the authors did not choose to chop OmpC up according to its strands, rather than by a fixed peptide size. What was the rationale for how the peptide lengths were chosen since many of them partially overlap known strands, and only partially (2 residues) overlap each other? It may not be too surprising that most of the inhibitory peptides consist of full strands (#4, 10, 21, 23).

A simple scan of known β-strands would have been an alternative approach, however this comes with the bias of limiting the experiments to predicted substrate (strand) sequences, and it presupposes that the secondary structure element would be formed by this tightly truncated peptide.

Instead, we allowed for the possibility that OMPs meet the BAM complex in an unfolded or partially folded state, and that the secondary structure (β-strand) might only form via β-argumentation after the substrate is placed in the context of the lateral gate. We therefore used peptides that mapped right across the entirety of OmpC, with a two amino acid overlap.

To clarify this important point regarding the unbiased nature of our screen, we have revised the text:

(Lines 147-151) "We used peptides that mapped the entirety of OmpC, with a two amino acid overlap. This we considered preferable to peptides that were restricted by structural features, such as β-strands, in consideration that β-strand formation may or may not have occurred in early-stage interactions at the BAM complex."

1. It would be good to have an idea of the propensity of the chosen peptides to form β-stands and participate in β-augmentation. We know from previous studies with darobactin and other peptides that they can inhibit OMP assembly by competing with substrates.

We appreciate the reviewer's suggestion. However, we have not conducted biophysical characterizations of the peptides to calculate the propensity of each peptide to form β-stands and participate in β-augmentation. The sort of detailed biophysical analysis done for Darobactin (by the Maier and Hiller groups, The antibiotic darobactin mimics a β-strand to inhibit outer membrane insertase Nature 593:125-129) was a Nature publication based on this single peptide. A further biophysical analysis of all of the peptides presented here goes well beyond the scope of our study.

1. The recognition motifs that the authors present span up to 9 residues which would suggest a relatively large binding surface, however, the structures of these regions are not large enough to accommodate these large peptides.

The β-signal motif (ζxGxx[Ω/Φ]x[Ω/Φ]) is an 8-residue consensus, some of the inhibitory peptides include additional residues before and after the defined motif of 8 residues, and the lateral gate of BamA has been shown interact with a 7-residue span (eg. Doyle et al, 2022). Cross-linking presented in our study showed BamD residues R49 and G65 cross-linked to the positions 0 and 6 of the internal signal in OmpC (Fig. 6D).

We appreciate this point of clarification and have modified the text to acknowledge that in the final registering of the peptide with its binding protein, some parts of the peptide might sit beyond the bounds of the BamD receptor’s binding pocket and the BamA lateral gate:

(Lines 458-471) "The β-signal motif (ζxGxx[Ω/Φ]x[Ω/Φ]) is an eight-residue consensus, and internal signal motif is composed of a nine-residue consensus. Recent structures have shown the lateral gate of BamA interacts with a 7-residue span of substrate OMPs. Interestingly, inhibitory compounds, such as darobactin, mimic only three resides of the C-terminal side of β-signal motif. Cross-linking presented here in our study showed that BamD residues R49 and G65 cross-linked to the positions 0 and 6 of the internal signal in OmpC (Fig. 6D). Both signals are larger than the assembly machineries signal binding pocket, implying that the signal might sit beyond the bounds of the signal binding pocket in BamD and the lateral gate in BamA. These finding are consistent with similar observations in other signal sequence recognition events, such as the mitochondrial targeting presequence signal that is longer than the receptor groove formed by the Tom20, the subunit of the translocator of outer membrane (TOM) complex (Yamamoto et al., 2011). The presequence has been shown to bind to Tom20 in several different conformations within the receptor groove (Nyirenda et al., 2013)."

Moreover, the distance between amino acids of BamD which cross-linked to the internal signal, R49 and Y62, is approximately 25 Å (pdbID used 7TT3). The distance of the maximum amino acid length of the internal signal of OmpC, from F280 to Y288, is approximately 22 Å (pdbID used 2J1N). This would allow for the signal to fit within the confines of the TRP motif of BamD.

Author response image 1.

1. The authors highlight that the sequence motifs are common among the inhibiting peptides, but do not test if this is a necessary motif to mediate the interactions. It would have been good to see if a library of non-OMP related peptides that match this motif could also inhibit or not.

With respect, this additional work would not address any biological question relevant to the function of BamD. To randomize sequences and then classify those that do or don’t fit the motif would help in refining the parameters of the β-signal motif, but that was not our intent.

We have identified the peptides from within the total sequence of an OMP, shown which peptides inhibit in an assembly assay, and then observed that the inhibitory peptides conform to a previously published (β-signal) motif.

1. In the studies that disrupt the motifs by mutagenesis, an effect was observed and attributed to disruption of the interaction of the 'internal signal'. However, the literature is filled with point mutations in OMPs that disrupt biogenesis, particular those within the membrane region. F280, Y286, V359, and Y365 are all residues that are in the membrane region that point into the membrane. Therefore, more work is needed to confirm that these mutations are in parts of a recognition motif rather than on the residues that are disrupting stability/assembly into the membrane.

As the reviewer pointed out, the side chains of the amino acids constituting the signal elements we determined were all facing the lipid side, of which Y286 and Y365 were important for folding as well as to be recognized. However, F280A and V359A had no effect on folding, but only on assembly through the BAM complex. The fact that position 0 functions as a signal has been demonstrated by peptidomimetics (Fig. 1) and point mutant analysis (Fig. 2). We appreciate this clarification and have modified the text to acknowledge that the all of the signal element faces the lipid side, which contributes to their stability in the membrane finally, and before that the BAM complex actively recognizes them and determines their orientation:

(Lines 519-526) After OMP assembly, all elements of the internal signal are positioned such that they face into the lipid-phase of the membrane. This observation may be a coincidence, or may be utilized by the BAM complex to register and orientate the lipid facing amino acids in the assembling OMP away from the formative lumen of the OMP. Amino acids at position 6, such as Y286 in OmpC, are not only component of the internal signal for binding by the BAM complex, but also act in structural capacity to register the aromatic girdle for optimal stability of the OMP in the membrane.

1. The title of Figure 3 indicates that disrupting the internal signal motif disrupts OMP assembly, however, the point mutations did not seem to have any effect. Only when both 280 and 286 were mutated was an effect observed. And even then, the trimer appeared to form just fine, albeit at reduced levels, indicating assembly is just fine, rather the rate of biogenesis is being affected.

We appreciate this point and have revised the title of Figure 3 to be:

(Lines 1070-1071) "Modifications in the putative internal signal slow the rate of OMP assembly in vivo."

1. In Figure 4, the authors attempt to quantify their blots. However, this seems to be a difficult task given the lack of quality of the blots and the spread of the intended signals, particularly of the 'int' bands. However, the more disturbing trend is the obvious reduction in signal from the post-urea treatment, even for the WT samples. The authors are using urea washes to indicate removal of only stalled substrates. However a reduction of signal is also observed for the WT. The authors should quantify this blot as well, but it is clear visually that both WT and the mutant have obvious reductions in the observable signals. Further, this data seems to conflict with Fig 3D where no noticeable difference in OmpC assembly was observed between WT and Y286A, why is this the case?

We have addressed this point by adding a statistical analysis on Fig. 4A. As the reviewer points out, BN-PAGE band quantification is a difficult task given the broad spread of the bands on these gels. Statistical analysis showed that the increase in intermediates (int) was statistically significant for Y286A at all times until 80 min, when the intermediate form signals decrease.

(Lines 1093-1096) "Statistical significance was indicated by the following: N.S. (not significant), p<0.05; , p<0.005; *. Exact p values of intermediate formed by Wt vs Y286A at each timepoint were as follows; 20 minutes: p = 0.03077, 40 minutes: p = 0.02402, 60 minutes: p = 0.00181, 80 minutes: p = 0.0545."

Further regarding the Int. band, we correct the statement as follows.

(Lines 253-254) "Consistent with this, the assembly intermediate which was prominently observed at the OmpC(Y286A) can be extracted from the membranes with urea;"

OMP assembly in vivo has additional periplasmic chaperones and factors present in order to support the assembly process. Therefore, it is likely that some proteins were assembled properly in vivo compared to their in vitro counterparts. Such a decrease has been observed not only in E. coli but also in mitochondrial OMP import (Yamano et al., 2010).

1. The pull-down assays with BamA and BamD should include a no protein control at the least to confirm there is no non-specific binding to the resin. Also, no detergent was mentioned as part of the pull downs that contained BamA or OmpC, nor was it detailed if OmpC was urea solubilized.

We have performed pull down experiments with a no-protein (Ni-NTA only) control as noted (Author response image 1). The results showed that the amount of OmpC carrying through on beads only was significantly lower than the amount of OmpC bound in the presence of BamD or BamA. The added OmpC was not treated with urea, but was synthesized by in vitro translation; the in vitro translated OmpC is the standard substrate in the EMM assembly assay (Supp Fig. S1) where it is recognized by the BAM complex. Thus, we used it for pull-down as well and, to make this clearer, we have revised as follows:

Author response image 2.

Pull down assay of radio-labelled OmpC with indicated protein or Ni-NTA alone (Ni-NTA) . T; total, FT; Flow throw, W; wash, E; Elute.

(Lines 252-265) "Three subunits of the BAM complex have been previously shown to interact with the substrates: BamA, BamB, and BamD (Hagan et al., 2013; Harrison, 1996; Ieva et al., 2011). In vitro pull-down assay showed that while BamA and BamD can independently bind to the in vitro translated OmpC polypeptide (Fig .S9A), BamB did not (Fig. S9B)."

11.

• The neutron reflectometry experiments are not convincing primarily due to the lack controls to confirm a consistent uniform bilayer is being formed and even if so, uniform orientations of the BamA molecules across the surface.

• Further, no controls were performed with BamD alone, or with OmpC alone, and it is hard to understand how the method can discriminate between an actual BamA/BamD complex versus BamA and BamD individually being located at the membrane surface without forming an actual complex.

• Previous studies have reported difficulty in preparing a complex with BamA and BamD from purified components.

• Additionally, little signal differences were observed for the addition of OmpC. However, an elongated unfolded polypeptide that is nearly 400 residues long would be expected to produce a large distinct signal given that only the C-terminal portion is supposedly anchored to BAM, while the rest would be extended out above the surface.

• The depiction in Figure 5D is quite misleading when viewing the full structures on the same scales with one another.

We have addressed these five points individually as follows.

i. The uniform orientation of BamA on the surface is guaranteed by the fixation through a His-tag engineered into extracellular loop 6 of BamA and has been validated in previous studies as cited in the text. Moreover, to explain this, we reconstructed another theoretical model for BamA not oriented well in the system as below. However, we found that the solid lines (after fitting) didn’t align well with the experimental data. We therefore assumed that BamA has oriented well in the membrane bilayer.

Author response image 3.

Experimental (symbols) and fitted (curves) NR profiles of BamA not oriented well in the POPC bilayer in D2O (black), GMW (blue) and H2O (red) buffer.

ii. There would be no means by which to do a control with OmpC alone or BamD alone as neither protein binds to the lipid layer chip. OmpC is diluted from urea and then the unbound OmpC is washed from the chip before NR measurements. BamD does not have an acyl group to anchor it to the lipid layer, without BamA to anchor to, it too is washed from the chip before NR measurements. We have reconstructed another theoretical model for both of BamA + BamD embedding in the membrane bilayer, and the fits were shown below. Apparently, the fits didn’t align well with the experimental data, which discriminate the BamA/BamD individually being located at the membrane surface without forming an actual complex.

Author response image 4.

Experimental (symbols) and fitted (curves) NR profiles of BamA+D embedding together in the POPC bilayer in D2O (black), GMW (blue) and H2O (red) buffer.

iii. The previous studies that reported difficulty in preparing a complex with BamA and BamD from purified components were assays done in aqueous solution including detergent solubilized BamA, or with BamA POTRA domains only. Our assay is superior in that it reports the binding of BamD to a purified BamA that has been reconstituted in a lipid bilayer.

iv. The relatively small signal differences observed for the addition of OmpC are expected, since OmpC is an elongated, unfolded polypeptide of nearly 400 residues long which, in the context of this assay, can occupy a huge variation in the positions at which it will sit with only the C-terminal portion anchored to BAM, and the rest moving randomly about and extended from the surface.

v. We appreciate the point raised and have now added a note in the Figure legend that these are depictions of the results and not a scale drawing of the structures.

1. In the crosslinking studies, the authors show 17 crosslinking sites (43% of all tested) on BamD crosslinked with OmpC. Given that the authors are presenting specific interactions between the two proteins, this is worrisome as the crosslinks were found across the entire surface of BamD. How do the authors explain this? Are all these specific or non-specific?

The crosslinking experiment using purified BamD was an effective assay for comprehensive analysis of the interaction sites between BamD and the substrate. However, as the reviewer pointed out, cross-linking was observed even at the sites that, in the context of the BAM complex, interact with BamC as a protein-protein interaction and would not be available for substrate protein-protein interactions. To complement this, analysis and to address this issue, we also performed the experiment in Fig. 6C.

In Fig. 6C, the interaction of BamD with the substrate is examined in vivo, and the results demonstrate that if BPA is introduced into the site, we designated as the substrate recognition site, it is cross-linked to the substrate. On the other hand, position 114 was found to crosslink with the substrate in vitro crosslinking, but not in vivo. It should be noted that position 114 has also been confirmed to form cross-link products with BamC, we believe that BamD-substrate interactions in the native state have been investigated. To explain the above, we have added the following description to the Results section.

(Lines 319-321) "Structurally, these amino acids locate both the lumen side of funnel-like structure (e.g. 49 or 62) and outside of funnel-like structure such as BamC binding site (e.g. 114) (fig. S12C). (Lines 350-357) Positions 49, 53, 65, and 196 of BamD face the interior of the funnel-like structure of the periplasmic domain of the BAM complex, while position 114 is located outside of the funnel-like structure (Bakelar et al., 2016; Gu et al., 2016; Iadanza et al., 2016). We note that while position 114 was cross-linked with OmpC in vitro using purified BamD, that this was not seen with in vivo cross-linking. Instead, in the context of the BAM complex, position 114 of BamD binds to the BamC subunit and would not be available for substrate binding in vivo (Bakelar et al., 2016; Gu et al., 2016; Iadanza et al., 2016)."

1. The study in Figure 6 focuses on defined regions within the OmpC sequence, but a more broad range is necessary to demonstrate specificity to these regions vs binding to other regions of the sequence as well. If the authors wish to demonstrate a specific interaction to this motif, they need to show no binding to other regions.

The region of affinity for the BAM complex was determined by peptidomimetic analysis, and the signal region was further identified by mutational analysis of OmpC. Subsequently, the subunit that recognizes the signal region was identified as BamD. In other words, in the process leading up to Fig. 6, we were able to analyze in detail that other regions were not the target of the study. We have revised the text to make clear that we focus on the signal region including the internal signal, and have not also analyzed other parts of the signal region:

(Lines 329-332) "As our peptidomimetic screen identified conserved features in the internal signal, and cross-linking highlighted the N-terminal and C-terminal TPR motifs of BamD as regions of interaction with OmpC, we focused on amino acids specifically within the β-signals of OmpC and regions of BamD which interact with β-signal."

1. The levels of the crosslinks are barely detectable via western blot analysis. If the interactions between the two surfaces are required, why are the levels for most of the blots so low?

These are western blots of cross-linked products – the efficiency of cross-linking is far less than 100% of the interacting protein species present in a binding assay and this explains why the levels for the blots are ‘so low’. We have added a sentence to the revised manuscript to make this clear for readers who are not molecular biologists:

(Lines 345-348) "These western blots reveal cross-linked products representing the interacting protein species. Photo cross-linking of unnatural amino acid is not a 100% efficient process, so the level of cross-linked products is only a small proportion of the molecules interacting in the assays."

15.

• Figure 7 indicates that two regions of BamD promote OMP orientation and assembly, however, none of the experiments appears to measure OMP orientation?

• Also, one common observation from panel F was that not only was the trimer reduced, but also the monomer. But even then, still a percentage of the trimer is formed, not a complete loss.

(i) We appreciate this point and have revised the title of Figure 7 to be:

(Lines 1137-1138) "Key residues in two structurally distinct regions of BamD promote β-strand formation and OMP assembly."

(ii) In our description of Fig. 7F (Lines 356-360) we do not distinguish between the amount of monomer and trimer forms, since both are reflective of the overall assembly rate i.e. assembly efficiency. Rather, we state that:

"The EMM assembly assay showed that the internal signal binding site was as important as the β-signal binding site to the overall assembly rates observed for OmpC (Fig. 7F), OmpF (fig. S15D), and LamB (fig. S15E). These results suggest that recognition of both the C-terminal β-signal and the internal signal by BamD is important for efficient protein assembly."

16.

• The experiment in Fig 7B would be more conclusive if it was repeated with both the Y62A and R197A mutants and a double mutant. These controls would also help resolve any effect from crowding that may also promote the crosslinks.

• Further, the mutation of R197 is an odd choice given that this residue has been studied previously and was found to mediate a salt bridge with BamA. How was this resolved by the authors in choosing this site since it was not one of the original crosslinking sites?

As stated in the text, the purpose of the experiment in Figure 7B is to measure the impact of pre-forming a β-strand in the substrate (OmpC) before providing it to the receptor (BamD). We thank the reviewer for the comment on the R197 position of BamD. The C-terminal domain of BamD has been suggested to mediate the BamA-BamD interface, specifically BamD R197 amino acid creates a salt-bridge with BamA E373 (Ricci et al., 2012). It had been postulated that the formation of this salt-bridge is not strictly structural, with R197 highlighted as a key amino acid in BamD activity and this salt-bridge acts as a “check-point” in BAM complex activity (Ricci et al., 2012, Storek et al., 2023). Our results agree with this, showing that the C-terminus of BamD acts in substrate recognition and alignment of the β-signal (Fig. 6, Fig S12). We show that amino acids in the vicinity of R197 (N196, G200, D204) cross-linked well to substrate and mutations to the β-signal prevent this interaction (Fig S12B, D). For mutational analysis of BamD, we looked then at the conservation of the C-terminus of BamD and determined R197 was the most highly conserved amino acid (Fig 6C). In order to account for this, we have adjusted the manuscript:

(Lines 376-377) "R197 has previously been isolated as a suppressor mutation of a BamA temperature sensitive strain (Ricci et al., 2012)."

(Lines 495-496) "This adds an additional role of the C-terminus of BamD beyond a complex stability role (Ricci et al., 2012; Storek et al., 2023)."

1. As demonstrated by the authors in Fig 8, the mutations in BamD lead to reduction in OMP levels for more than just OmpC and issues with the membrane are clearly observable with Y62A, although not with R197A in the presence of VCN. The authors should also test with rifampicin which is smaller and would monitor even more subtle issues with the membrane. Oddly, no growth was observed for the Vec control in the lower concentration of VCN, but was near WT levels for 3 times VCN, how is this explained?

While it would be interesting to correlate the extent of differences to the molecular size of different antibiotics such as rifampicin, such correlations are not the intended aim of our study. Vancomycin (VCN) is a standard measure of outer membrane integrity in our field, hence its use in our tests for membrane integrity.

We apologize to the reviewer as Figure 8 D-G may have been misleading. Figure 8D,E are using bamD shut-down cells expressing plasmid-borne BamD mutants. Whereas Figure 8F, G are the same strain as used in Figure 3. We have adjusted the figure as well as the figure legend: (Lines 1165-1169) D, E E coli bamD depletion cells expressing mutations at residues, Y62A and R197A, in the β-signal recognition regions of BamD were grown with of VCN. F, G, E coli cells expressing mutations to OmpC internal signal, as shown in Fig 3, grown in the presence of VCN. Mutations to two key residues of the internal signal were sensitive to the presence of VCN.

1. While Fig 8I indeed shows diminished levels for FY as stated, little difference was observed for the trimer for the other mutants compared to WT, although differences were observed for the dimer. Interestingly, the VY mutant has nearly WT levels of dimer. What do the authors postulate is going on here with the dimer to trimer transition? How do the levels of monomer compare, which is not shown?

The BN-PAGE gel system cannot resolve protein species that migrate below ~50kDa and the monomer species of the OMPs is below this size. We can’t comment on effects on the monomer because it is not visualized. The non-cropped gel image is shown here. Recently, Hussain et al., has shown that in vitro proteo-liposome system OmpC assembly progresses from a “short-lived dimeric” form before the final process of trimerization (Hussain et al., 2021). However, their findings suggest that LPS plays the final role in stimulation of dimer-to-trimer, a step well past the recognition step of the β-signals. Mutations to the internal signal of OmpC results in the formation of an intermediate, the substrate stalled on the BAM complex. This stalling, presumably, causes a hinderance to the BAM complex resulting in reduced timer and loss of dimer OmpF signal in the EMM of cells expressing OmpC double mutant strain, FY. cannot resolve protein species that migrate below ~50kDa and the monomer species of the OMPs is below this size. We can’t comment on effects on the monomer because it is not visualized. The non-cropped gel image is shown here. We have noted this in the revised text:

Author response image 5.

Non-cropped gel of Fig. 8I. the asterisk indicates a band observed in the sample loading wells at the top of the gel.

(Lines 417-418) "The dimeric form of endogenous OmpF was prominently observed in both the OmpC(WT) as well as the OmpC(VY) double mutant cells."

1. In the discussion, the authors indicate they have '...defined an internal signal for OMP assembly', however, their study is limited and only investigates a specific region of OmpC. More is needed to definitively say this for even OmpC, and even more so to indicate this is a general feature for all OMPs.

We acknowledge the reviewer's comment on this point and have expanded the statement to make sure that the conclusion is justified with the specific evidence that is shown in the paper and the supplementary data. We now state:

(Lines 444-447) "This internal signal corresponds to the -5 strand in OmpC and is recognized by BamD. Sequence analysis shows that similar sequence signatures are present in other OMPs (Figs. S5, S6 and S7). These sequences were investigated in two further OMPs: OmpF and LamB (Fig. 2C and D)."

Note, we did not state that this is a general feature for all OMPs. That would not be a reasonable proposition.

20.

• In the proposed model in Fig 9, it is hard to conceive how 5 strands will form along BamD given the limited surface area and tight space beneath BAM.

• More concerning is that the two proposal interaction sites on BamD, Y62 and R197, are on opposite sides of the BamD structure, not along the same interface, which makes this model even more unlikely.

• As evidence against this model, in Figure 9E, the two indicates sites of BamD are not even in close proximity of the modeled substrate strands.

We can address the reviewer’s three concerns here:

i. The first point is that the region (formed by BamD engaged with POTRA domains 1-2 and 5 of BamA) is not sufficient to accommodate five β-strands. Structural analysis reveals that the interaction between the N-terminal side of BamD and POTRA1-2 is substantially changed the conformation by substrate binding, and that this surface is greatly extended. This surface does have enough space to accommodate five beta-strands, as now documented in Fig. 9D, 9E using the latest structures (7TT5 and 7TT2) as illustrations of this. The text now reads:

(Lines 506-515) "Spatially, this indicates the BamD can serve to organize two distinct parts of the nascent OMP substrate at the periplasmic face of the BAM complex, either prior to or in concert with, engagement to the lateral gate of BamA. Assessing this structurally showed the N-terminal region of BamD (interacting with the POTRA1-2 region of BamA) and the C-terminal region of BamD (interacting with POTRA5 proximal to the lateral gate of BamA) (Bakelar et al., 2016; Gu et al., 2016; Tomasek et al., 2020) has the N-terminal region of BamD changing conformation depending on the folding states of the last four β-strands of the substrate OMP, EspP (Doyle et al., 2022). The overall effect of this being a change in the dimensions of this cavity change, a change which is dependent on the folded state of the substrate engaged in it (Fig 9 B-E)."

ii. The second point raised regards the orientation of the substrate recognition residues of BamD. Both Y62A and R197 were located on the lumen side of the funnel in the EspP-BAM transport intermediate structure (PDBID;7TTC); Y62A is relatively located on the edge of BamD, but given that POTRA1-2 undergoes a conformational change and opens this region, as described above, both are located in locations where they could bind to substrates. This was explained in the following text in the results section of revised manuscript.

(Lines 377-379) "Each residue was located on the lumen side of the funnel-like structure in the EspP-BAM assembly intermediate structure (PDBID; 7TTC) (Doyle et al., 2022)."

**Reviewer #2 (Public Review):"

Previously, using bioinformatics study, authors have identified potential sequence motifs that are common to a large subset of beta-barrel outer membrane proteins in gram negative bacteria. Interestingly, in that study, some of those motifs are located in the internal strands of barrels (not near the termini), in addition to the well-known "beta-signal" motif in the C-terminal region.

Here, the authors carried out rigorous biochemical, biophysical, and genetic studies to prove that the newly identified internal motifs are critical to the assembly of outer membrane proteins and the interaction with the BAM complex. The author's approaches are rigorous and comprehensive, whose results reasonably well support the conclusions. While overall enthusiastic, I have some scientific concerns with the rationale of the neutron refractory study, and the distinction between "the intrinsic impairment of the barrel" vs "the impairment of interaction with BAM" that the internal signal may play a role in. I hope that the authors will be able to address this.

Strengths:

1. It is impressive that the authors took multi-faceted approaches using the assays on reconstituted, cell-based, and population-level (growth) systems.

2. Assessing the role of the internal motifs in the assembly of model OMPs in the absence and presence of BAM machinery was a nice approach for a precise definition of the role.

Weaknesses:

1. The result section employing the neutron refractory (NR) needs to be clarified and strengthened in the main text (from line 226). In the current form, the NR result seems not so convincing.

What is the rationale of the approach using NR?

We have now modified the text to make clear that:

(Lines 276-280) "The rationale to these experiments is that NR provides: (i) information on the distance of specified subunits of a protein complex away from the atomically flat gold surface to which the complex is attached, and (ii) allows the addition of samples between measurements, so that multi-step changes can be made to, for example, detect changes in domain conformation in response to the addition of a substrate."

What is the molecular event (readout) that the method detects?

We have now modified the text to make clear that:

(Lines 270-274) "While the biochemical assay demonstrated that the OmpC(Y286A) mutant forms a stalled intermediate with the BAM complex, in a state in which membrane insertion was not completed, biochemical assays such as this cannot elucidate where on BamA-BamD this OmpC(Y286A) substrate is stalled."

What are "R"-y axis and "Q"-x axis and their physical meanings (Fig. 5b)?

The neutron reflectivity, R, refers to the ratio of the incoming and exiting neutron beams and it is measured as a function of Momentum transfer Q, which is defined as Q=4π sinθ/λ, where θ is the angle of incident and λ is the neutron wavelength. R(Q)is approximately given byR(Q)=16π2/ Q2 |ρ(Q)|2, where R(Q) is the one-dimensional Fourier transform of ρ(z), the scattering length density (SLD) distribution normal to the surface. SLD is the sum of the coherent neutron scattering lengths of all atoms in the sample layer divided by the volume of the layer. Therefore, the intensity of the reflected beams is highly dependent on the thickness, densities and interface roughness of the samples. This was explained in the following text in the method section of revised manuscript.

(Lines 669-678) "Neutron reflectivity, denoted as R, is the ratio of the incoming to the exiting neutron beams. It’s calculated based on the Momentum transfer Q, which is defined by the formula Q=4π sinθ/λ, where θ represents the angle of incidence and λ stands for the neutron wavelength. The approximate value of R(Q) can be expressed as R(Q)=16π2/ Q2 |ρ(Q)|2, where R(Q) is the one-dimensional Fourier transform of ρ(z), which is the scattering length density (SLD) distribution perpendicular to the surface. SLD is calculated by dividing the sum of the coherent neutron scattering lengths of all atoms in a sample layer by the volume of that layer. Consequently, factors such as thickness, volume fraction, and interface roughness of the samples significantly influence the intensity of the reflected beams."

How are the "layers" defined from the plot (Fig. 5b)?

The “layers” in the plot (Fig. 5b) represent different regions of the sample being studied. In this study, we used a seven-layer model to fit the experimental data (chromium - gold - NTA - HIS8 - β-barrel - P3-5 - P1-2. This was explained in the following text in the figure legend of revised manuscript. (Lines 1115-1116) The experimental data was fitted using a seven-layer model: chromium - gold - NTA - His8 - β-barrel - P3-5 - P1-2.

What are the meanings of "thickness" and "roughness" (Fig. 5c)?

We used neutron reflectometry to determine the relative positions of BAM subunits in a membrane environment. The binding of certain subunits induced conformational changes in other parts of the complex. When a substrate membrane protein is added, the periplasmic POTRA domain of BamA extends further away from the membrane surface. This could result in an increase in thickness as observed in neutron reflectometry measurements.

As for roughness, it is related to the interface properties of the sample. In neutron reflectometry, the intensity of the reflected beams is highly dependent on the thickness, densities, and interface roughness of the samples. An increase in roughness could suggest changes in these properties, possibly due to protein-membrane interactions or structural changes within the membrane.

(Lines 1116-1120) "Table summarizes of the thickness, roughness and volume fraction data of each layer from the NR analysis. The thickness refers to the depth of layered structures being studied as measured in Å. The roughness refers to the irregularities in the surface of the layered structures being studied as measured in Å."

What does "SLD" stand for?

We apologize for not explaining abbreviation when the SLD first came out. We explained it in revised manuscript. (Line 298)

1. In the result section, "The internal signal is necessary for insertion step of assembly into OM" This section presents an important result that the internal beta-signal is critical to the intrinsic propensity of barrel formation, distinct from the recognition by BAM complex. However, this point is not elaborated in this section. For example, what is the role of these critical residues in the barrel structure formation? That is, are they involved in any special tertiary contacts in the structure or in membrane anchoring of the nascent polypeptide chains?

We appreciate the reviewer's comment on this point. Both position 0 and position 6 appear to be important amino acids for recognition by the BAM complex, since mutations introduced at these positions in peptide 18 prevent competitive inhibition activity.

In terms of the tertiary structure of OmpC, position 6 is an amino acid that contributes to the aromatic girdle, and since Y286A and Y365A affected OMP folding as measured in folding experiments, it is perhaps their position in the aromatic girdle that contributes to the efficiency of β-barrel folding in addition to its function as a recognition signal. We have added a sentence in the revised manuscript:

(Lines 233-236) "Position 6 is an amino acid that contributes to the aromatic girdle. Since Y286A and Y365A affected OMP folding as measured in folding experiments, their positioning into the aromatic girdle may contributes to the efficiency of β-barrel folding, in addition to contributing to the internal signal."

The mutations made at position 0 had no effect on folding, so this residue may function solely in the signal. Given the register of each β-strand in the final barrel, the position 0 residues have side-chains that face out into the lipid environment. From examination of the OmpC crystal structure, the residue at position 0 makes no special tertiary contacts with other, neighbouring residues.  

Reviewer #1 (Recommendations For The Authors):

Minor critiques (in no particular order):

1. Peptide 18 was identified based on its strong inhibition for EspP assembly but another peptide, peptide 23, also shows inhibition and has no particular consensus.

We would correct this point. Peptide 23 has a strong consensus to the canonical β-signal. We had explained the sequence consensus of β-signal in the Results section of the text. In the third paragraph, we have added a sentence indicating the relationship between peptide 18 and peptide 23.

(Lines 152-168) "Six peptides (4, 10, 17, 18, 21, and 23) were found to inhibit EspP assembly (Fig. 1A). Of these, peptide 23 corresponds to the canonical β-signal of OMPs: it is the final β-strand of OmpC and it contains the consensus motif of the β-signal (ζxGxx[Ω/Φ]x[Ω/Φ]). The inhibition seen with peptide 23 indicated that our peptidomimetics screening system using EspP can detect signals recognized by the BAM complex. In addition to inhibiting EspP assembly, five of the most potent peptides (4, 17, 18, 21, and 23) inhibited additional model OMPs; the porins OmpC and OmpF, the peptidoglycan-binding OmpA, and the maltoporin LamB (fig. S3). Comparing the sequences of these inhibitory peptides suggested the presence of a sub-motif from within the β-signal, namely [Ω/Φ]x[Ω/Φ] (Fig. 1B). The sequence codes refer to conserved residues such that: ζ, is any polar residue; G is a glycine residue; Ω is any aromatic residue; Φ is any hydrophobic residue and x is any residue (Hagan et al., 2015; Kutik et al., 2008). The non-inhibitory peptide 9 contained some elements of the β-signal but did not show inhibition of EspP assembly (Fig. 1A).

Peptide 18 also showed a strong sequence similarity to the consensus motif of the β-signal (Fig. 1B) and, like peptide 23, had a strong inhibitory action on EspP assembly (Fig. 1A). Variant peptides based on the peptide 18 sequence were constructed and tested in the EMM assembly assay (Fig. 1C)."

1. It is unclear why the authors immediately focused on BamD rather than BamB, given that both were mentioned to mediate interaction with substrate. Was BamB also tested?

We thank the reviewer for this comment. Following the reviewer's suggestion, we have now performed a pull-down experiment on BamB and added it to Fig. S9. We also modified the text of the results as follows.

(Lines 262-265) "Three subunits of the BAM complex have been previously shown to interact with the substrates: BamA, BamB, and BamD (Hagan et al., 2013; Harrison, 1996; Ieva et al., 2011). In vitro pull-down assay showed that while BamA and BamD can independently bind to the in vitro translated OmpC polypeptide (Fig .S9A), BamB did not (Fig. S9B)."

1. For the in vitro folding assays of the OmpC substrates, labeled and unlabeled, no mention of adding SurA or any other chaperone which is known to be important for mediating OMP biogenesis in vitro.

We appreciate the reviewer’s concerns on this point, however chaperones such as SurA are non-essential factors in the OMP assembly reaction mediated by the BAM complex: the surA gene is not essential and the assembly of OMPs can be measured in the absence of exogenously added SurA. It remains possible that addition of SurA to some of these assays could be useful in detailing aspects of chaperone function in the context of the BAM complex, but that was not the intent of this study.

1. For the supplementary document, it would be much easier for the reader to have the legends groups with the figures.

Following the reviewer's suggestion, we have placed the legends of Supplemental Figures together with each Figure.

1. Some of the figures and their captions are not grouped properly and are separated which makes it hard to interpret the figures efficiently.

We thank the reviewer for this comment, we have revised the manuscript and figures to properly group the figures and captions together on a single page.

1. The authors begin their 'Discussion' with a question (line 454), however, they don't appear to answer or even attempt to address it; suggest removing rhetorical questions.

As per the reviewers’ suggestion, we removed this question.

1. Line 464, 'unbiased' should be removed. This would imply that if not stated, experiments are 'negatively' biased.

We removed this word and revised the sentence as follows:

(Lines 431-433) "In our experimental approach to assess for inhibitory peptides, specific segments of the major porin substrate OmpC were shown to interact with the BAM complex as peptidomimetic inhibitors."

1. Lines 466-467; '...go well beyond expected outcomes.' What does this statement mean?

Our peptidomimetics led to unexpected results in elucidating the additional essential signal elements. The manuscript was revised as follows:

(Lines 433-435) "Results for this experimental approach went beyond expected outcomes by identifying the essential elements of the signal Φxxxxxx[Ω/Φ]x[Ω/Φ] in β-strands other than the C-terminal strand."

1. Line 478; '...rich information that must be oversimplified...'?

We appreciate the reviewer’s pointed out. For more clarity, the manuscript was revised as follows:

(Lines 450-453) "The abundance of information which arises from modeling approaches and from the multitude of candidate OMPs, is generally oversimplified when written as a primary structure description typical of the β-signal for bacterial OMPs (i.e. ζxGxx[Ω/Φ]x[Ω/Φ]) (Kutik et al., 2008)."

1. There are typos in the supplementary figures.

We have revised and corrected the Supplemental Figure legends.  

Reviewer #2 (Recommendations For The Authors):

1. In Supplementary Information, I recommend adding the figure legends directly to the corresponding figures. Currently, it is very inconvenient to go back and forth between legends and figures.

Following the reviewer's suggestion, we have placed the legends of Supplemental Figures together with each Figure.

1. Line 94 (p.3): "later"

Lateral?

Yes. We have corrected this.

1. Line 113 (p.3): The result section, "Peptidomimetics derived from E. coli OmpC inhibit OMP assembly" Rationale of the peptide inhibition assay is not clear. How can the peptide sequence that effectively inhibit the assembly interpreted as the b-assembly signal? By competitive binding to BAM or by something else? What is the authors' hypothesis in doing this assay?

In revision, we have added following sentence to explain the aim and design of the peptidomimetics:

(Lines 140-145) "The addition of peptides with BAM complex affinity, such as the OMP β-signal, are capable of exerting an inhibitory effect by competing for binding of substrate OMPs to the BAM complex (Hagan et al., 2015). Thus, the addition of peptides derived from the entirety of OMPs to the EMM assembly assay, which can evaluate assembly efficiency with high accuracy, expects to identify novel regions that have affinity for the BAM complex."

1. Line 113- (p.3) and Fig. S1: The result section, "Peptidomimetics derived from E. coli OmpC inhibit OMP assembly"

Some explanation seems to be needed why b-barrel domain of EspP appears even without ProK?

We appreciate the reviewer’s pointed out. We added following sentence to explain:

(Lines 128-137) "EspP, a model OMP substrate, belongs to autotransporter family of proteins. Autotransporters have two domains; (1) a β-barrel domain, assembled into the outer membrane via the BAM complex, and (2) a passenger domain, which traverses the outer membrane via the lumen of the β-barrel domain itself and is subsequently cleaved by the correctly assembled β-barrel domain (Celik et al., 2012). When EspP is correctly assembled into outer membrane, a visible decrease in the molecular mass of the protein is observed due to the self-proteolysis. Once the barrel domain is assembled into the membrane it becomes protease-resistant, with residual unassembled and passenger domains degraded (Leyton et al., 2014; Roman-Hernandez et al., 2014)."

1. Line 186 (p.6): "Y285"

Y285A?

We have corrected the error, it was Y285A.

1. Lines 245- (p. 7)/ Lines 330- (p. 10)

It needs to be clarified that the results described in these paragraphs were obtained from the assays with EMM.

We appreciate the reviewer’s concerns on these points. For the first half, the following text was added at the beginning of the applicable paragraph to indicate that all of Fig. 4 is the result of the EMM assembly assay.

(Line 241) "We further analyzed the role of internal β-signal by the EMM assembly assay. At the second half, we used purified BamD but not EMM. We described clearly with following sentence."

(Lines 316-318) "We purified 40 different BPA variants of BamD, and then irradiated UV after incubating with 35S-labelled OmpC."

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Lines 40-42: The sentence "The coupling of structural connectome (SC) and functional connectome (FC) varies greatly across different cortical regions reflecting anatomical and functional hierarchies as well as individual differences in cognitive function, and is regulated by genes" is a misstatement. Regional variations of structure-function coupling do not really reflect differences in cognitive function among individuals, but inter-subject variations do.

Thank you for your comment. We have made revisions to the sentence to correct its misstatement. Please see lines 40-43: “The coupling of structural connectome (SC) and functional connectome (FC) varies greatly across different cortical regions reflecting anatomical and functional hierarchies[1, 6-9] and is regulated by genes[6, 8], as well as its individual differences relates to cognitive function[8, 9].”

(2) In Figure 1, the graph showing the relation between intensity and cortical depth needs explanation.

Thank you for your comment. We have added necessary explanation, please see lines 133-134: “The MPC was used to map similarity networks of intracortical microstructure (voxel intensity sampled in different cortical depth) for each cortical node.”

(3) Line 167: Change "increased" to "increase".

We have corrected it, please see lines 173-174: “…networks significantly increased with age and exhibited greater increase.”

(4) Line 195: Remove "were".

We have corrected it, please see line 204: “…default mode networks significantly contributed to the prediction…”

(5) Lines 233-240, Reproducibility analyses: Comparisons of parcellation templates were not made with respect to gene weights. Is there any particular reason?

Thank you for your comment. We have quantified the gene weights based on HCPMMP using the same procedures. We identified a correlation (r \= 0.25, p<0.001) between the gene weights in HCPMMP and BNA. Given that this is a relatively weak correlation, we need to clarify the following points.

Based on HCPMMP, we produced an averaged gene expression profile for 10,027 genes covering 176 left cortical regions[1]. The excluding 4 cortical regions that had an insufficient number of assigned samples may lead to different templates having a relatively weak correlation of gene associations. Moreover, the effect of different template resolutions on the results of human connectome-transcriptome association is still unclear.

In brain connectome analysis, the choice of parcellation templates can indeed influence the subsequent findings to some extent. A methodological study[2] provided referenced correlations about 0.4~0.6 for white matter connectivity and 0.2~0.4 for white matter nodal property between two templates (refer to Figure 4 and 5 in [2]). Therefore, the age-related coupling changes as a downstream analysis was calculated using multimodal connectome and correlated with gene expression profiles, which may be influenced by the choice of templates. 

We have further supplemented gene weights results obtained from HCPMMP to explicitly clarify the dependency of parcellation templates.

Please see lines 251-252: “The gene weights of HCPMMP was consistent with that of BNA (r = 0.25, p < 0.001).”

Author response image 1.

The consistency of gene weights between HCPMMP and BNA.

Please see lines 601-604: “Finally, we produced an averaged gene expression profile for 10,027 genes covering 176 left cortical regions based on HCPMMP and obtained the gene weights by PLS analysis. We performed Pearson's correlation analyses to assess the consistency of gene weights between HCPMMP and BNA.”

Reviewer #2 (Recommendations For The Authors):

Your paper is interesting to read and I found your efforts to evaluate the robustness of the results of different parcellation strategies and tractography methods very valuable. The work is globally easy to navigate and well written with informative good-quality figures, although I think some additional clarifications will be useful to improve readability. My suggestions and questions are detailed below (I aimed to group them by topic which did not always succeed so apologies if the comments are difficult to navigate, but I hope they will be useful for reflection and to incorporate in your work).

* L34: 'developmental disorder'

** As far as I understand, the subjects in HCP-D are mostly healthy (L87). Thus, while your study provides interesting insights into typical brain development, I wonder if references to 'disorder' might be premature. In the future, it would be interesting to extend your approach to the atypical populations. In any case, it would be extremely helpful and appreciated if you included a figure visualising the distribution of behavioural scores within your population and in relationship to age at scan for your subjects (and to include a more detailed description of the assessment in the methods section) given that large part of your paper focuses on their prediction using coupling inputs (especially given a large drop of predictive performance after age correction). Such figures would allow the reader to better understand the cognitive variability within your data, but also potential age relationships, and generally give a better overview of your cohort.

We agree with your comment that references to 'disorder' is premature. We have made revisions in abstract and conclusion. 

Please see lines 33-34: “This study offers insight into the maturational principles of SC-FC coupling in typical development.”

Please see lines 395-396: “Further investigations are needed to fully explore the clinical implications of SC-FC coupling for a range of developmental disorders.”

In addition, we have included a more detailed description of the cognitive scores in the methods section and provided a figure to visualize the distributions of cognitive scores and in relationship to age for subjects. Please see lines 407-413: “Cognitive scores. We included 11 cognitive scores which were assessed with the National Institutes of Health (NIH) Toolbox Cognition Battery (https://www.healthmeasures.net/exploremeasurement-systems/nih-toolbox), including episodic memory, executive function/cognitive flexibility, executive function/inhibition, language/reading decoding, processing speed, language/vocabulary comprehension, working memory, fluid intelligence composite score, crystal intelligence composite score, early child intelligence composite score and total intelligence composite score. Distributions of these cognitive scores and their relationship with age are illustrated in Figure S12.”

Author response image 2.

Cognitive scores and age distributions of scans.

* SC-FC coupling

** L162: 'Regarding functional subnetworks, SC-FC coupling increased disproportionately with age (Figure 3C)'.

*** As far as I understand, in Figure 3C, the points are the correlation with age for a given ROI within the subnetwork. Is this correct? If yes, I am not sure how this shows a disproportionate increase in coupling. It seems that there is great variability of SC-FC correlation with age across regions within subnetworks, more so than the differences between networks. This would suggest that the coupling with age is regionally dependent rather than network-dependent? Maybe you could clarify?

The points are the correlation with age for a given ROI within the subnetwork in Figure 3C. We have revised the description, please see lines 168-174: “Age correlation coefficients distributed within functional subnetworks were shown in Figure 3C. Regarding mean SC-FC coupling within functional subnetworks, the somatomotor (𝛽𝑎𝑔𝑒\=2.39E-03, F=4.73, p\=3.10E-06, r\=0.25, p\=1.67E07, Figure 3E), dorsal attention (𝛽𝑎𝑔𝑒\=1.40E-03, F=4.63, p\=4.86E-06, r\=0.24, p\=2.91E-07, Figure 3F), frontoparietal (𝛽𝑎𝑔𝑒 =2.11E-03, F=6.46, p\=2.80E-10, r\=0.33, p\=1.64E-12, Figure 3I) and default mode (𝛽𝑎𝑔𝑒 =9.71E-04, F=2.90, p\=3.94E-03, r\=0.15, p\=1.19E-03, Figure 3J) networks significantly increased with age and exhibited greater increase.” In addition, we agree with your comment that the coupling with age is more likely region-dependent than network-dependent. We have added the description, please see lines 329-332: “We also found the SC-FC coupling with age across regions within subnetworks has more variability than the differences between networks, suggesting that the coupling with age is more likely region-dependent than network-dependent.” This is why our subsequent analysis focused on regional coupling.  

*** Additionally, we see from Figure 3C that regions within networks have very different changes with age. Given this variability (especially in the subnetworks where you show both positive and negative correlations with age for specific ROIs (i.e. all of them)), does it make sense then to show mean coupling over regions within the subnetworks which erases the differences in coupling with age relationships across regions (Figures 3D-J)?

Considering the interest and interpretation for SC-FC coupling, showing the mean coupling at subnetwork scales with age correlation is needed, although this eliminates variability at regional scale. These results at different scales confirmed that coupling changes with age at this age group are mainly increased.

*** Also, I think it would be interesting to show correlation coefficients across all regions, not only the significant ones (3B). Is there a spatially related tendency of increases/decreases (rather than a 'network' relationship)? Would it be interesting to show a similar figure to Figure S7 instead of only the significant regions?

As your comment, we have supplemented the graph which shows correlation coefficients across all regions into Figure 3B. Similarly, we supplemented to the other figures (Figure S3-S6).

Author response image 3.

Aged-related changes in SC-FC coupling. (A) Increases in whole-brain coupling with age. (B) Correlation of age with SC-FC coupling across all regions and significant regions (p<0.05, FDR corrected). (C) Comparisons of age-related changes in SC-FC coupling among functional networks. The boxes show the median and interquartile range (IQR; 25–75%), and the whiskers depict 1.5× IQR from the first or third quartile. (D-J) Correlation of age with SC-FC coupling across the VIS, SM, DA, VA, LIM, FP and DM. VIS, visual network; SM, somatomotor network; DA, dorsal attention network; VA, ventral attention network; LIM, limbic network; FP, frontoparietal network; DM, default mode network.

*** For the quantification of MPC.

**** L421: you reconstructed 14 cortical surfaces from the wm to pial surface. If we take the max thickness of the cortex to be 4.5mm (Fischl & Dale, 2000), the sampling is above the resolution of your anatomical images (0.8mm). Could you expand on what the interest is in sampling such a higher number of surfaces given that the resolution is not enough to provide additional information?

The surface reconstruction was based on state-of-the-art equivolumetric surface construction techniques[3] which provides a simplified recapitulation of cellular changes across the putative laminar structure of the cortex. By referencing a 100-μm resolution Merkerstained 3D histological reconstruction of an entire post mortem human brain (BigBrain: https://bigbrain.loris.ca/main.php), a methodological study[4] systematically evaluated MPC stability with four to 30 intracortical surfaces when the resolution of anatomical image was 0.7 mm, and selected 14 surfaces as the most stable solution. Importantly, it has been proved the in vivo approach can serve as a lower resolution yet biologically meaningful extension of the histological work[4]. 

**** L424: did you aggregate intensities over regions using mean/median or other statistics?

It might be useful to specify.

Thank you for your careful comment. We have revised the description in lines 446-447: “We averaged the intensity profiles of vertices over 210 cortical regions according to the BNA”.

**** L426: personal curiosity, why did you decide to remove the negative correlation of the intensity profiles from the MPC? Although this is a common practice in functional analyses (where the interpretation of negatives is debated), within the context of cortical correlations, the negative values might be interesting and informative on the level of microstructural relationships across regions (if you want to remove negative signs it might be worth taking their absolute values instead).

We agree with your comment that the interpretation of negative correlation is debated in MPC. Considering that MPC is a nascent approach to network modeling, we adopted a more conservative strategy that removing negative correlation by referring to the study [4] that proposed the approach. As your comment, the negative correlation might be informative. We will also continue to explore the intrinsic information on the negative correlation reflecting microstructural relationships.

**** L465: could you please expand on the notion of self-connections, it is not completely evident what this refers to.

We have revised the description in lines 493-494: “𝑁𝑐 is the number of connection (𝑁𝑐 = 245 for BNA)”.

**** Paragraph starting on L467: did you evaluate the multicollinearities between communication models? It is possibly rather high (especially for the same models with similar parameters (listed on L440-444)). Such dependence between variables might affect the estimates of feature importance (given the predictive models only care to minimize error, highly correlated features can be selected as a strong predictor while the impact of other features with similarly strong relationships with the target is minimized thus impacting the identification of reliable 'predictors').

We agree with your comment. The covariance structure (multicollinearities) among the communication models have a high probability to lead to unreliable predictor weights. In our study, we applied Haufe's inversion transform[5] which resolves this issue by computing the covariance between the predicted FC and each communication models in the training set. More details for Haufe's inversion transform please see [5]. We further clarified in the manuscript, please see in lines 497-499: “And covariance structure among the predictors may lead to unreliable predictor weights. Thus, we applied Haufe's inversion transform[38] to address these issues and identify reliable communication mechanisms.”

**** L474: I am not completely familiar with spin tests but to my understanding, this is a spatial permutation test. I am not sure how this applies to the evaluation of the robustness of feature weight estimates per region (if this was performed per region), it would be useful to provide a bit more detail to make it clearer.

As your comment, we have supplemented the detail, please see lines 503-507: “Next, we generated 1,000 FC permutations through a spin test[86] for each nodal prediction in each subject and obtained random distributions of model weights. These weights were averaged over the group and were investigated the enrichment of the highest weights per region to assess whether the number of highest weights across communication models was significantly larger than that in a random discovery.”

**** L477: 'significant communication models were used to represent WMC...', but in L103 you mention you select 3 models: communicability, mean first passage, and flow graphs. Do you want to say that only 3 models were 'significant' and these were exactly the same across all regions (and data splits/ parcellation strategies/ tractography methods)? In the methods, you describe a lot of analysis and testing but it is not completely clear how you come to the selection of the final 3, it would be beneficial to clarify. Also, the final 3 were selected on the whole dataset first and then the pipeline of SC-FC coupling/age assessment/behaviour predictions was run for every (WD, S1, S2) for both parcellations schemes and tractography methods or did you end up with different sets each time? It would be good to make the pipeline and design choices, including the validation bit clearer (a figure detailing all the steps which extend Figure 1 would be very useful to understand the design/choices and how they relate to different runs of the validation).

Thank you for your comment. In all reproducibility analyses, we used the same 3 models which was selected on the main pipeline (probabilistic tractography and BNA parcellation). According to your comment, we produced a figure that included the pipeline of model selection as the extend of Figure 1. And the description please see lines 106-108: “We used these three models to represent the extracortical connectivity properties in subsequent discovery and reproducibility analyses (Figure S1).” 

Author response image 4.

Pipeline of model selection and reproducibility analyses.

**** Might the imbalance of features between structural connectivity and MPC affect the revealed SC-FC relationships (3 vs 1)? Why did you decide on this ratio rather than for example best WM structural descriptor + MPC?

We understand your concern. The WMC communication models represent diverse geometric, topological, or dynamic factors. In order to describe the properties of WMC as best as possible, we selected three communication models after controlling covariance structure that can significantly predict FC from the 27 models. Compared to MPC, this does present a potential feature imbalance problem. However, this still supports the conclusion that coupling models that incorporate microarchitectural properties yield more accurate predictions of FC from SC[6, 7]. The relevant experiments are shown in Figure S2 below. If only the best WM structural descriptor is used, this may lose some communication properties of WMC.

**** L515: were intracranial volume and in-scanner head motion related to behavioural measures? These variables likely impact the inputs, do you expect them to influence the outcome assessments? Or is there a mistake on L518 and you actually corrected the input features rather than the behaviour measures?

The in-scanner head motion and intracranial volume are related to some age-adjusted behavioural measures, as shown in the following table. The process of regression of covariates from cognitive measures was based on these two cognitive prediction studies [8, 9]. Please see lines 549-554: “Prior to applying the nested fivefold cross-validation framework to each behaviour measure, we regressed out covariates including sex, intracranial volume, and in-scanner head motion from the behaviour measure[59, 69]. Specifically, we estimated the regression coefficients of the covariates using the training set and applied them to the testing set. This regression procedure was repeated for each fold.”

Author response table 1.

** Additionally, in the paper, you propose that the incorporation of cortical microstructural (myelin-related) descriptors with white-matter connectivity to explain FC provides for 'a more comprehensive perspective for characterizing the development of SC-FC coupling' (L60). This combination of cortical and white-matter structure is indeed interesting, however the benefits of incorporating different descriptors could be studied further. For example, comparing results of using only the white matter connectivity (assessed through selected communication models) ~ FC vs (white matter + MPC) ~ FC vs MPC ~ FC. Which descriptors better explain FC? Are the 'coupling trends' similar (or the same)? If yes, what is the additional benefit of using the more complex combination? This would also add strength to your statement at L317: 'These discrepancies likely arise from differences in coupling methods, highlighting the complementarity of our methods with existing findings'. Yes, discrepancies might be explained by the use of different SC inputs. However, it is difficult to see how discrepancies highlight complementarity - does MCP (and combination with wm) provide additional information to using wm structural alone?~

According to your comment, we have added the analyses based on different models using only the myelin-related predictor or WM connectivity to predict FC, and further compared the results among different models. please see lines 519-521: “In addition, we have constructed the models using only MPC or SCs to predict FC, respectively. Spearman’s correlation was used to assess the consistency between spatial patterns based on different models.” 

Please see lines 128-130: “In addition, the coupling pattern based on other models (using only MPC or only SCs to predict FC) and the comparison between the models were shown in Figure S2A-C.” Please see lines 178-179: “The age-related patterns of SC-FC coupling based other coupling models were shown in Figure S2D-F.”

Although we found that there were spatial consistencies in the coupling patterns between different models, the incorporation of MPC with SC connectivity can improve the prediction of FC than the models based on only MPC or SC. For age-related changes in coupling, the differences between the models was further amplified. We agree with you that the complementarity cannot be explicitly quantified and we have revised the description, please see line 329: “These discrepancies likely arise from differences in coupling methods.”

Author response image 5.

Comparison results between different models. Spatial pattern of mean SC-FC coupling based on MPC ~ FC (A), SCs ~ FC (B), and MPC + SCs ~ FC (C). Correlation of age with SC-FC coupling across cortex based on MPC ~ FC (D), SCs ~ FC (E), and MPC + SCs ~ FC (F).

** For the interpretation of results: L31 'SC-FC coupling is positively associated with genes in oligodendrocyte-related pathways and negatively associated with astrocyte-related gene'; L124: positive myelin content with SC-FC coupling...and similarly on L81, L219, L299, L342, and L490:

***You use a T1/T2 ratio which is (in large part) a measure of myelin to estimate the coupling between SC and FC. Evaluation with SC-FC coupling with myeline described in Figure 2E is possibly biased by the choice of this feature. Similarly, it is possible that reported positive associations with oligodendrocyte-related pathways and SC-FC coupling in your work could in part result from a bias introduced by the 'myelin descriptor' (conversely, picking up the oligodendrocyte-related genes is a nice corroboration for the T1/T2 ration being a myelin descriptor, so that's nice). However, it is possible that if you used a different descriptor of the cortical microstructure, you might find different expression patterns associated with the SCFC coupling (for example using neurite density index might pick up neuronal-related genes?). As mentioned in my previous suggestions, I think it would be of interest to first use only the white matter structural connectivity feature to assess coupling to FC and assess the gene expression in the cortical regions to see if the same genes are related, and subsequently incorporate MPC to dissociate potential bias of using a myelin measure from genetic findings.

Thank you for your insightful comments. In this paper, however, the core method of measuring coupling is to predict functional connections using multimodal structural connections, which may yield more information than a single modal. We agree with your comment that separating SCs and MPC to look at the genes involved in both separately could lead to interesting discoveries. We will continue to explore this in the future.

** Generally, I find it difficult to understand the interpretation of SC-FC coupling measures and would be interested to hear your thinking about this. As you mention on L290-294, how well SC predicts FC depends on which input features are used for the coupling assessment (more complex communication models, incorporating additional microstructural information etc 'yield more accurate predictions of FC' L291) - thus, calculated coupling can be interpreted as a measure of how well a particular set of input features explain FC (different sets will explain FC more or less well) ~ coupling is related to a measure of 'missing' information on the SC-FC relationship which is not contained within the particular set of structural descriptors - with this approach, the goal might be to determine the set that best, i.e. completely, explains FC to understand the link between structure and function. When you use the coupling measures for comparisons with age, cognition prediction etc, the 'status' of the SC-FC changes, it is no longer the amount of FC explained by the given SC descriptor set, but it's considered a descriptor in itself (rather than an effect of feature selection / SC-FC information overlap) - how do you interpret/argue for this shift of use?

Thank you for your comment. In this paper, we obtain reasonable SC-FC coupling by determining the optimal set of structural features to explain the function. The coupling essentially measures the direct correspondence between structure and function. To study the relationship between coupling and age and cognition is actually to study the age correlation and cognitive correlation of this direct correspondence between structure and function. 

** In a similar vein to the above comment, I am interested to hear what you think: on L305 you mention that 'perfect SC-FC coupling may be unlikely'. Would this reasoning suggest that functional activity takes place through other means than (and is therefore somehow independent of) biological (structural) substrates? For now, I think one can only say that we have imperfect descriptors of the structure so there is always information missing to explain function, this however does not mean the SC and FC are not perfectly coupled (only that we look at insufficient structural descriptors - limitations of what imaging can assess, what we measure etc). This is in line with L305 where you mention that 'Moreover, our results suggested that regional preferential contributions across different SCs lead to variations in the underlying communication process'. This suggests that locally different areas might use different communication models which are not reflected in the measures of SC-FC coupling that was employed, not that the 'coupling' is lower or higher (or coupling is not perfect). This is also a change in approach to L293: 'This configuration effectively releases the association cortex from strong structural constraints' - the 'release' might only be in light of the particular structural descriptors you use - is it conceivable that a different communication model would be more appropriate (and show high coupling) in these areas.

Thank you for your insightful comments. We have changed the description, please see lines 315317: “SC-FC coupling is dynamic and changes throughout the lifespan[7], particularly during adolescence[6,9], suggesting that perfect SC-FC coupling may require sufficient structural descriptors.” 

*Cognitive predictions:

** From a practical stand-point, do you think SC-FC coupling is a better (more accurate) indicator of cognitive outcomes (for example for future prediction studies) than each modality alone (which is practically easier to obtain and process)? It would be useful to check the behavioural outcome predictions for each modality separately (as suggested above for coupling estimates). In case SC-FC coupling does not outperform each modality separately, what is the benefit of using their coupling? Similarly, it would be useful to compare to using only cortical myelin for the prediction (which you showed to increase in importance for the coupling). In the case of myelin->coupling-> intelligence, if you are able to predict outcomes with the same performance from myelin without the need for coupling measures, what is the benefit of coupling?

From a predictive performance point of view, we do not believe that SC-FC coupling is a better indicator than a single mode (voxel, network or other indicator). Our starting point is to assess whether SC-FC coupling is related to the individual differences of cognitive performances rather than to prove its predictive power over other measures. As you suggest, it's a very interesting perspective on the predictive power of cognition by separating the various modalities and comparing them. We will continue to explore this issue in the future study.

** The statement on L187 'suggesting that increased SC-FC coupling during development is associated with higher intelligence' might not be completely appropriate before age corrections (especially given the large drop in performance that suggests confounding effects of age).

According to your comment, we have removed the statement.

** L188: it might be useful to report the range of R across the outer cross-validation folds as from Figure 4A it is not completely clear that the predictive performance is above the random (0) threshold. (For the sake of clarity, on L180 it might be useful for the reader if you directly report that other outcomes were not above the random threshold).

According to your comment, we have added the range of R and revised the description, please see lines 195-198: “Furthermore, even after controlling for age, SC-FC coupling remained a significant predictor of general intelligence better than at chance (Pearson’s r\=0.11±0.04, p\=0.01, FDR corrected, Figure 4A). For fluid intelligence and crystal intelligence, the predictive performances of SC-FC coupling were not better than at chance (Figure 4A).”

In a similar vein, in the text, you report Pearson's R for the predictive results but Figure 4A shows predictive accuracy - accuracy is a different (categorical) metric. It would be good to homogenise to clarify predictive results.

We have made the corresponding changes in Figure 4.

Author response image 6.

Encoding individual differences in intelligence using regional SC-FC coupling. (A) Predictive accuracy of fluid, crystallized, and general intelligence composite scores. (B) Regional distribution of predictive weight. (C) Predictive contribution of functional networks. The boxes show the median and interquartile range (IQR; 25–75%), and the whiskers depict the 1.5× IQR from the first or third quartile.

*Methods and QC:

-Parcellations

** It would be useful to mention briefly how the BNA was applied to the data and if any quality checks were performed for the resulting parcellations, especially for the youngest subjects which might be most dissimilar to the population used to derive the atlas (healthy adults HCP subjects) ~ question of parcellation quality.

We have added the description, please see lines 434-436: “The BNA[31] was projected on native space according to the official scripts (http://www.brainnetome.org/resource/) and the native BNA was checked by visual inspection.” 

** Additionally, the appropriateness of structurally defined regions for the functional analysis is also a topic of important debate. It might be useful to mention the above as limitations (which apply to most studies with similar focus).

We have added your comment to the methodological issues, please see lines 378-379: “Third, the appropriateness of structurally defined regions for the functional analysis is also a topic of important debate.”

- Tractography

** L432: it might be useful to name the method you used (probtrackx).

We have added this name to the description, please see lines 455-456: “probabilistic tractography (probtrackx)[78, 79] was implemented in the FDT toolbox …”

** L434: 'dividing the total fibres number in source region' - dividing by what?

We have revised the description, please see line 458: “dividing by the total fibres number in source region.”

** L436: 'connections in subcortical areas were removed' - why did you trace connections to subcortical areas in the first place if you then removed them (to match with cortical MPC areas I suspect)? Or do you mean there were spurious streamlines through subcortical regions that you filtered?

On the one hand we need to match the MPC, and on the other hand, as we stated in methodological issues, the challenge of accurately resolving the connections of small structures within subcortical regions using whole-brain diffusion imaging and tractography techniques[10, 11]. 

** Following on the above, did you use any exclusion masks during the tracing? In general, more information about quality checks for the tractography would be useful. For example, L437: did you do any quality evaluations based on the removed spurious streamlines? For example, were there any trends between spurious streamlines and the age of the subject? Distance between regions/size of the regions?

We did not use any exclusion masks. We performed visual inspection for the tractography quality and did not assess the relationship between spurious streamlines and age or distance between regions/size of the regions.

** L439: 'weighted probabilistic network' - this was weighted by the filtered connectivity densities or something else?

The probabilistic network is weighted by the filtered connectivity densities.

** I appreciate the short description of the communication models in Text S1, it is very useful.

Thank you for your comment.

** In addition to limitations mentioned in L368 - during reconstruction, have you noticed problems resolving short inter-hemispheric connections?

We have not considered this issue, we have added it to the limitation, please see lines 383-384: “In addition, the reconstruction of short connections between hemispheres is a notable challenge.”

- Functional analysis:

** There is a difference in acquisition times between participants below and above 8 years (21 vs 26 min), does the different length of acquisition affect the quality of the processed data?

We have made relatively strict quality control to ensure the quality of the processed data.  

** L446 'regressed out nuisance variables' - it would be informative to describe in more detail what you used to perform this.

We have provided more detail about the regression of nuisance variables, please see lines 476-477: “The nuisance variables were removed from time series based on general linear model.”

** L450-452: it would be useful to add the number of excluded participants to get an intuition for the overall quality of the functional data. Have you checked if the quality is associated with the age of the participant (which might be related to motion etc). Adding a distribution of remaining frames across participants (vs age) would be useful to see in the supplementary methods to better understand the data you are using.