Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

UGGTs are involved in the prevention of premature degradation for misfolded glycoproteins, by utilizing UGGT-KO cells and a number of different ERAD substrates. They proposed a concept by which the fate of glycoproteins can be determined by a tug-of-war between UGGTs and EDEMs.

Strengths:

The authors provided a wealth of data to indicate that UGGT1 competes with EDEMs, which promotes glycoprotein degradation.

Weaknesses:

Less clear, though, is the involvement of UGGT2 in the process. Also, to this reviewer, some data do not necessarily support the conclusion.

Major criticisms:

(1) One of the biggest problems I had on reading through this manuscript is that, while the authors appeared to generate UGGTs-KO cells from HCT116 and HeLa cells, it was not clearly indicated which cell line was used for each experiment. I assume that it was HCT116 cells in most cases, but I did not see that it was clearly mentioned. As the expression level of UGGT2 relative to UGGT1 is quite different between the two cell lines, it would be critical to know which cells were used for each experiment.

Thank you for this comment. We have clarified this point, especially in the figure legends.

(2) While most of the authors' conclusion is sound, some claims, to this reviewer, were not fully supported by the data. Especially I cannot help being puzzled by the authors' claim about the involvement of UGGT2 in the ERAD process. In most of the cases, KO of UGGT2 does not seem to affect the stability of ERAD substrates (ex. Fig. 1C, 2A, 3D). When the author suggests that UGGT2 is also involved in the ERAD, it is far from convincing (ex. Fig. 2D/E). Especially because now it has been suggested that the main role of UGGT2 may be distinct from UGGT1, playing a role in lipid quality control (Hung, et al., PNAS 2022), it is imperative to provide convincing evidence if the authors want to claim the involvement of UGGT2 in a protein quality control system. In fact, it was not clear at all whether even UGGT1 is also involved in the process in Fig. 2D/E, as the difference, if any, is so subtle. How the authors can be sure that this is significant enough? While the authors claim that the difference is statistically significant (n=3), this may end up with experimental artifacts. To say the least, I would urge the authors to try rescue experiments with UGGT1 or 2, to clarify that the defect in UGGT-DKO cells can be reversed. It may also be interesting to see that the subtle difference the authors observed is indeed N-glycan-dependent by testing a non-glycosylated version of the protein (just like NHK-QQQ mutants in Fig. 2C).

We appreciate this comment. According to this comment, we reevaluated the importance of UGGT2 for ER-protein quality control. As this reviewer mentioned, KO of UGGT2 does not affect the stability of ATF6a, NHK, rRI332-Flag or EMC1-△PQQ-Flag (Fig. 1E, 2A, and 3DE). Furthermore, we tested whether overexpression of UGGT2 reverses the phenotype of UGGT-DKO regarding the degradation rate of NHK, and we found that it did not affect the degradation rate of NHK, whereas overexpression of UGGT1 restored the degradation rate to that in WT cells.

Author response image 1.

Collectively, these facts suggest that the role of UGGT2 in ER protein quality control is rather limited in HCT116 cells. Therefore, we have decided not to mention UGGT2 in the title, and weakened the overall claim that UGGT2 contributes to ER protein quality control. Tissues with high expression of UGGT2 or cultured cells other than HCT116 would be appropriate for revealing the detailed function of UGGT2.

To this reviewer, it is still possible that the involvement of UGGT1 (or 2, if any) could be totally substrate-dependent, and the substrates used in Fig 2D or E happen not to be dependent to the action of UGGTs. To the reviewer, without the data of Fig. 2D and E the authors provide enough evidence to demonstrate the involvement of UGGT1 in preventing premature degradation of glycoprotein ERAD substrates. I am just afraid that the authors may have overinterpreted the data, as if the UGGTs are involved in stabilization of all glycoproteins destined for ERAD.

Based on the point this reviewer mentioned, we decided to delete previous Fig. 2D and 2E. There may be more or less efficacy of UGGT1 for preventing early degradation of substrates.

(3) I am a bit puzzled by the DNJ treatment experiments. First, I do not see the detailed conditions of the DNJ treatment (concentration? Time?). Then, I was a bit surprised to see that there were so little G3M9 glycans formed, and there was about the same amount of G2M9 also formed (Figure 1 Figure supplement 4B-D), despite the fact that glucose trimming of newly syntheized glycoproteins are expected to be completely impaired (unless the authors used DNJ concentration which does not completely impair the trimming of the first Glc). Even considering the involvement of Golgi endo-alpha-mannosidase, a similar amount of G3M9 and G2M9 may suggest that the experimental conditions used for this experiment (i.e. concentration of DNJ, duration of treatment, etc) is not properly optimized.

We think that our experimental condition of DNJ treatment is appropriate to evaluate the effect of DNJ. Referring to the other papers (Ali and Field, 2000; Karlsson et al., 1993; Lomako et al., 2010; Pearse et al., 2010; Tannous et al., 2015), 0.5 mM DNJ is appropriate. In our previously reported experiment, 16 h treatment with kifunensine mannosidase inhibitor was sufficient for N-glycan composition analysis prior to cell collection (Ninagawa et al., 2014), and we treated cells for a similar time in Figure 1-Figure Supplement 4 and 5 (and Figure 1-Figure Supplement 6). We could see the clear effect of DNJ to inhibit degradation of ATF6a with 2 hours of pretreatment (Fig. 1G). Furthermore, our results are very reasonable and consistent with previous findings that DNJ increased GM9 the most (Cheatham et al., 2023; Gross et al., 1983; Gross et al., 1986; Romero et al., 1985). In addition to DNJ, we used CST for further experiments in new figures (Fig. 1H and Figure 1-Figure supplement 6). DNJ and CST are inhibitors of glucosidase; DNJ is a stronger inhibitor of glucosidase II, while CST is a stronger inhibitor of glucosidase I (Asano, 2000; Saunier et al., 1982; Szumilo et al., 1987; Zeng et al., 1997). An increase in G3M9 and G2M9 was detected using CST (Figure1-Figure Supplement 6). Like DNJ, CST also inhibited ATF6a degradation in UGGT-DKO cells (Fig. 1H). These findings show that our experimental condition using glucosidase inhibitor is appropriate and strongly support our model (Fig. 5). Differences between the effects of DNJ and CST are now described in our manuscript pages 8 to 10.

Reviewer #2 (Public Review):

In this study, Ninagawa et al., shed light on UGGT's role in ER quality control of glycoproteins. By utilizing UGGT1/UGGT2 DKO cells, they demonstrate that several model misfolded glycoproteins undergo early degradation. One such substrate is ATF6alpha where its premature degradation hampers the cell's ability to mount an ER stress response.

While this study convincingly demonstrates early degradation of misfolded glycoproteins in the absence of UGGTs, my major concern is the need for additional experiments to support the "tug of war" model involving UGGTs and EDEMs in influencing the substrate's fate - whether misfolded glycoproteins are pulled into the folding or degradation route. Specifically, it would be valuable to investigate how overexpression of UGGTs and EDEMs in WT cells affects the choice between folding and degradation for misfolded glycoproteins. Considering previous studies indicating that monoglucosylation influences glycoprotein solubility and stability, an essential question is: what is the nature of glycoproteins in UGGTKO/EDEMKO and potentially UGGT/EDEM overexpression cells? Understanding whether these substrates become more soluble/stable when GM9 versus mannose-only translation modification accumulates would provide valuable insights.

In the new figure 2DE, we conducted overexpression experiments of structure formation factors UGGT1 and/or CNX, and degradation factors EDEMs. While overexpression of structure formation factors (Fig. 2DE) and KO of degradation factors (Ninagawa et al., 2015; Ninagawa et al., 2014) increased stability of substrates, KO of UGGT1 (Fig. 1E, 2A and 3DF) and overexpression of degradation factors (Fig. 2DE) (Hirao et al., 2006; Hosokawa et al., 2001; Mast et al., 2005; Olivari et al., 2005) accelerated degradation of substrates. A comparison of the properties of N-glycan with the normal type and the type without glucoses was already reported (Tannous et al., 2015). The rate of degradation of substrate was unchanged, but efficiency of secretion of substrates was affected.

The study delves into the physiological role of UGGT, but is limited in scope, focusing solely on the effect of ATF6alpha in UGGT KO cells' stress response. It is crucial for the authors to investigate the broader impact of UGGT KO, including the assessment of basal ER proteotoxicity levels, examination of the general efflux of glycoproteins from ER, and the exploration of the physiological consequences due to UGGT KO. This broader perspective would be valuable for the wider audience. Additionally, the marked increase in ATF4 activity in UGGTKO requires discussion, which the authors currently omit.

We evaluated the sensitivity of WT and UGGT1-KO cells to ER stress (Figure 4G). KO of UGGT1 increased the sensitivity to ER stress inducer Tg, indicating the importance of UGGT1 for resisting ER stress.

We add the following description in the manuscript about ATF4 activity in UGGT1-KO: “In addition to this, UGGT1 is necessary for proper functioning of ER resident proteins such as ATF6a (Fig. 4B-F). It is highly possible that ATF6a undergoes structural maintenance by UGGT1, which could be necessary to avoid degradation and maintain proper function, because ATF6a with more rigid in structure tended to remain in UGGT1-KO cells (Fig. 4C). Responses of ERSE and UPRE to ER stress, which require ATF6a, were decreased in UGGT1-KO cells (Fig. 4DE). In contrast, ATF4 reporter activity was increased in UGGT1-KO cells (Fig. 4F), while the basal level of ATF4 in UGGT1-KO cells was comparable with that in WT (Figure 1-Figure supplement 2B). The ATF4 pathway might partially compensate the function of the ERSE and UPRE pathways in UGGT1-KO cells in acute ER stress. This is now described on Page 17 in our manuscript.

The discussion section is brief and could benefit from being a separate section. It is advisable for the authors to explore and suggest other model systems or disease contexts to test UGGT's role in the future. This expansion would help the broader scientific community appreciate the potential applications and implications of this work beyond its current scope.

Thank you for making this point. The DISCUSSION part has now been separated in our manuscript. We added some points in the manuscript about other model organisms and diseases in the DISCUSSION as follows: “ Our work focusing on the function of mammalian UGGT1 greatly advances the understanding how ER homeostasis is maintained in higher animals. Considering that Saccharomyces cerevisiae does not have a functional orthologue of UGGT1 (Ninagawa et al., 2020a) and that KO of UGGT1 causes embryonic lethality in mice (Molinari et al., 2005), it would be interesting to know at what point the function of UGGT1 became evolutionarily necessary for life. Related to its importance in animals, it would also be of interest to know what kind of diseases UGGT1 is associated with. Recently, it has been reported that UGGT1 is involved in ER retention of Trop-2 mutant proteins, which are encoded by a causative gene of gelatinous drop-like corneal dystrophy (Tax et al., 2024). Not only this, but since the ER is known to be involved in over 60 diseases (Guerriero and Brodsky, 2012), we must investigate how UGGT1 and other ER molecules are involved in diseases.”

Reviewer #3 (Public Review):

This manuscript focuses on defining the importance of UGGT1/2 in the process of protein degradation within the ER. The authors prepared cells lacking UGGT1, UGGT2, or both UGGT1/UGGT2 (DKO) HCT116 cells and then monitored the degradation of specific ERAD substrates. Initially, they focused on the ER stress sensor ATF6 and showed that loss of UGGT1 increased the degradation of this protein. This degradation was stabilized by deletion of ERAD-specific factors (e.g., SEL1L, EDEM) or treatment with mannose inhibitors such as kifunesine, indicating that this is mediated through a process involving increased mannose trimming of the ATF6 N-glycan. This increased degradation of ATF6 impaired the function of this ER stress sensor, as expected, reducing the activation of downstream reporters of ER stress-induced ATF6 activation. The authors extended this analysis to monitor the degradation of other well-established ERAD substrates including A1AT-NHK and CD3d, demonstrating similar increases in the degradation of destabilized, misfolding protein substrates in cells deficient in UGGT. Importantly, they did experiments to suggest that re-overexpression of wild-type, but not catalytically deficient, UGGT rescues the increased degradation observed in UGGT1 knockout cells. Further, they demonstrated the dependence of this sensitivity to UGGT depletion on N-glycans using ERAD substrates that lack any glycans. Ultimately, these results suggest a model whereby depletion of UGGT (especially UGGT1 which is the most expressed in these cells) increases degradation of ERAD substrates through a mechanism involving impaired re-glucosylation and subsequent re-entry into the calnexin/calreticulin folding pathway.

I must say that I was under the impression that the main conclusions of this paper (i.e., UGGT1 functions to slow the degradation of ERAD substrates by allowing re-entry into the lectin folding pathway) were well-established in the literature. However, I was not able to find papers explicitly demonstrating this point. Because of this, I do think that this manuscript is valuable, as it supports a previously assumed assertion of the role of UGGT in ER quality control. However, there are a number of issues in the manuscript that should be addressed.

Notably, the focus on well-established, trafficking-deficient ERAD substrates, while a traditional approach to studying these types of processes, limits our understanding of global ER quality control of proteins that are trafficked to downstream secretory environments where proteins can be degraded through multiple mechanisms. For example, in Figure 1-Figure Supplement 2, UGGT1/2 knockout does not seem to increase the degradation of secretion-competent proteins such as A1AT or EPO, instead appearing to stabilize these proteins against degradation. They do show reductions in secretion, but it isn't clear exactly how UGGT loss is impacting ER Quality Control of these more relevant types of ER-targeted secretory proteins.

We appreciate your comment. It is certainly difficult to assess in detail how UGGT1 functions against secretion-competent proteins, but we think that the folding state of these proteins is improved, which avoids their degradation and increases their secretion. In Figure 1-Figure supplement 2E, there is a clear decrease in secretion of EPO in UGGT1-KO cells, suggesting that UGGT1 also inhibits degradation of such substrates. Note that, as shown in Fig. 3A-C, once a protein forms a solid structure, it is rarely degraded in the ER.

Lastly, I don't understand the link between UGGT, ATF6 degradation, and ATF6 activation. I understand that the idea is that increased ATF6 degradation afforded by UGGT depletion will impair activation of this ER stress sensor, but if that is the case, how does UGGT2 depletion, which only minimally impacts ATF6 degradation (Fig. 1), impact activation to levels similar to the UGGT1 knockout (Fig 4)? This suggests UGGT1/2 may serve different functions beyond just regulating the degradation of this ER stress sensor. Also, the authors should quantify the impaired ATF6 processing shown in Fig 4B-D across multiple replicates.

According to this valuable comment, we reevaluated our manuscript. As this reviewer mentioned, involvement of UGGT2 in the activation of ATF6a cannot be explained only by the folding state of ATF6a. Thus, the part about whether UGGT2 is effective in activating ATF6 is outside the scope of this paper. The main focus of this paper is the contribution of UGGT1 to the ER protein quality control mechanism.

Ultimately, I do think the data support a role for UGGT (especially UGGT1) in regulating the degradation of ERAD substrates, which provides experimental support for a role long-predicted in the field. However, there are a number of ways this manuscript could be strengthened to further support this role, some of which can be done with data they have in hand (e.g., the stats) or additional new experiments.

In this revision period, to further elucidate the function of UGGT, we did several additional experiments (new figures Fig. 1H, 2DE, 4G and, Figure 1-Figure Supplement 6). We hope that these will bring our papers up to the level you have requested.

Reviewer #1 (Recommendations For The Authors):

Minor points:

(1) Abbreviations: GlcNAc, N-acetylglucosamines -> why plural?

Corrected.

(2) Abstract: to this reviewer, it may not be so common to cite references in the abstract.

We submit this manuscript to eLife as “Research Advances”. In the instructions of eLife for “Research Advances”, there is the description: “A reference to the original eLife article should be included in the abstract, e.g. in the format “Previously we showed that XXXX (author, year). Here we show that YYYY.” We follow this.

(3) Introduction: "as the site of biosynthesis of approximately one-third of all proteins." Probably this statement needs a citation?

We added the reference there. You can also confirm this in “The Human Protein Atlas” website. https://www.proteinatlas.org/humanproteome/tissue/secretome

(4) Figure 1F - the authors claimed that maturation of HA was delayed also in UGGT2 cells, but it was not at all clear to me. Rescue experiments with UGGT2 would be desired.

We agree with this reviewer, but there was a statistically significant difference in the 80 min UGGT2-KO strain. Previously, it was reported that HA maturation rate was not affected by UGGT2 (Hung et al., 2022). We think that the difference is not large. A rescue experiment of UGGT2 on the degradation of NHK was conducted, and is shown in this response to referees.

(5) Figure 4A, here also the authors claim that UGGT2 is "slightly" involved in folding of ATF6alpha(P) but it is far from convincing to this reviewer.

Now we also think that involvement of UGGT2 in ER protein quality control should be examined in the future.

(6) Page 11, line 7 from the bottom: "peak of activation was shifted from 1 hour to 4 hours after the treatment of Tg in UGGT-KO cells". I found this statement a bit awkward; how can the authors be sure that "the peak" is 4 hours when the longest timing tested is 4 hours (i.e. peak may be even later)?

Corrected. We deleted the description.

(7) Page 11, line 4 "a more rigid structure that averts degradation" Can the authors speculate what this "rigid" structure actually means? The reviewer has to wonder what kind of change can occur to this protein with or without UGGT1. Binding proteins? The difference in susceptibility against trypsin appears very subtle anyway (Figure 4 Figure Supplement 1).

Let us add our thoughts here: Poorly structured ATF6a is immediately routed for degradation in UGGT1-KO cells. As a result, ATF6a with a stable or rigid structure have remained in the UGGT1-KO strain. ATF6a with a metastable state is tended to be degraded without assistance of UGGT1.

(8) Figure 1 Figure supplement 2; based on the information provided, I calculate the relative ratio of UGGT2/UGGT1 in HCT116 which is 4.5%, and in HeLa 26%. Am I missing something? Also significant figure, at best, should be 2, not 3 (i.e. 30%, not 29.8%).

Corrected. Thank you for this comment.

Reviewer #2 (Recommendations For The Authors):

(1) The effect in Fig. 2B with UGGT1-D1358A add-back is minimal. Testing the inactive and active add-back on other substrates, such as ATF6alpha, which undergoes a more rapid degradation, would provide a more comprehensive assessment.

To examine the effect of full length and inactive mutant of UGGT1 in UGGT1-KO and UGGT2-KO on the rate of degradation of endogenous ATF6a, we tried to select more than 300 colonies stably expressing full-length Myc-UGGT1/2, UGGT1/2-Flag, and UGGT1/2 (no tag), and their point mutant of them. However, no cell lines expressing nearly as much or more UGGT1/2 than endogenous ones were obtained. The expression level of UGGT1 seemed to be tightly regulated. A low-expressing stable cell line could not recover the phenotype of ATF6a degradation.

We also tried to measure the degradation rate of exogenously expressed ATF6a. But overexpressed ATF6a is partially transported to the Golgi and cleaved by proteases, which makes it difficult to evaluate only the effect of degradation.

(2) In reference to this statement on pg. 11:

"This can be explained by the rigid structure of ATF6(P) lacking structural flexibility to respond to ER stress because the remaining ATF6(P) in UGGT1-KO cells tends to have a more rigid structure that averts degradation, which is supported by its slightly weaker sensitivity to trypsin (Figure 4-figure supplement 1A). "

The rationale for testing ATF6(P) rigidity via trypsin digestion needs clarification. The authors should provide more background, especially if it relates to previous studies demonstrating UGGT's influence on substrate solubility. If trypsin digestion is indeed addressing this, it should be applied consistently to all tested misfolded glycoproteins, ensuring a comprehensive approach.

We now provide more background with three references about trypsin digestion. Trypsin digestion allows us to evaluate the structure of proteins originated from the same gene, but it can sometimes be difficult to comparatively evaluate the structure of proteins originated from different genes. For example, antitrypsin is resistant to trypsin by its nature, which does not necessarily mean that antitrypsin forms a more stable structure than other proteins. NHK, a truncated version of antitrypsin, is still resistant to trypsin compared with other substrates.

(3) Many of the figures described in the manuscript weren't referred to a specific panel. For example, pg. 12 "Fig. 1E and Fig.5," the exact panel for Fig. 5 wasn't referenced.

Thank you for this comment. Corrected.

(4) For experiments measuring the composition of glycoproteins in different KO lines, it is necessary to do the experiment more than once for conducting statistical analysis and comparisons. Moreover, the authors did not include raw composition data for these experiments. Statistical analysis should also be done for Fig. 4E-F.

Our N-glycan composition data (Figure 1-Figure supplement 5 and 6C) is consistent with previous our papers (George et al., 2021; George et al., 2020; Ninagawa et al., 2015; Ninagawa et al., 2014). We did it twice in the previous study and please refer to it regarding statistical analysis (George et al., 2020). We add the raw composition data of N-glycan (Figure 1-Figure supplement 4 and 6B). In Fig. 4D-F, now statistical analysis is included.

Ali, B.R., and M.C. Field. 2000. Glycopeptide export from mammalian microsomes is independent of calcium and is distinct from oligosaccharide export. Glycobiology. 10:383-391.

Asano, N. 2000. Glycosidase-Inhibiting Glycomimetic Alkaloids. Biological Activities and Therapeutic Perspectives. Journal of Synthetic Organic Chemistry, Japan. 58:666-675.

Cheatham, A.M., N.R. Sharma, and P. Satpute-Krishnan. 2023. Competition for calnexin binding regulates secretion and turnover of misfolded GPI-anchored proteins. J Cell Biol. 222.

George, G., S. Ninagawa, H. Yagi, J.I. Furukawa, N. Hashii, A. Ishii-Watabe, Y. Deng, K. Matsushita, T. Ishikawa, Y.P. Mamahit, Y. Maki, Y. Kajihara, K. Kato, T. Okada, and K. Mori. 2021. Purified EDEM3 or EDEM1 alone produces determinant oligosaccharide structures from M8B in mammalian glycoprotein ERAD. Elife. 10.

George, G., S. Ninagawa, H. Yagi, T. Saito, T. Ishikawa, T. Sakuma, T. Yamamoto, K. Imami, Y. Ishihama, K. Kato, T. Okada, and K. Mori. 2020. EDEM2 stably disulfide-bonded to TXNDC11 catalyzes the first mannose trimming step in mammalian glycoprotein ERAD. Elife. 9:e53455.

Gross, V., T. Andus, T.A. Tran-Thi, R.T. Schwarz, K. Decker, and P.C. Heinrich. 1983. 1-deoxynojirimycin impairs oligosaccharide processing of alpha 1-proteinase inhibitor and inhibits its secretion in primary cultures of rat hepatocytes. Journal of Biological Chemistry. 258:12203-12209.

Gross, V., T.A. Tran-Thi, R.T. Schwarz, A.D. Elbein, K. Decker, and P.C. Heinrich. 1986. Different effects of the glucosidase inhibitors 1-deoxynojirimycin, N-methyl-1-deoxynojirimycin and castanospermine on the glycosylation of rat alpha 1-proteinase inhibitor and alpha 1-acid glycoprotein. Biochem J. 236:853-860.

Hirao, K., Y. Natsuka, T. Tamura, I. Wada, D. Morito, S. Natsuka, P. Romero, B. Sleno, L.O. Tremblay, A. Herscovics, K. Nagata, and N. Hosokawa. 2006. EDEM3, a soluble EDEM homolog, enhances glycoprotein endoplasmic reticulum-associated degradation and mannose trimming. J Biol Chem. 281:9650-9658.

Hosokawa, N., I. Wada, K. Hasegawa, T. Yorihuzi, L.O. Tremblay, A. Herscovics, and K. Nagata. 2001. A novel ER alpha-mannosidase-like protein accelerates ER-associated degradation. EMBO reports. 2:415-422.

Hung, H.H., Y. Nagatsuka, T. Solda, V.K. Kodali, K. Iwabuchi, H. Kamiguchi, K. Kano, I. Matsuo, K. Ikeda, R.J. Kaufman, M. Molinari, P. Greimel, and Y. Hirabayashi. 2022. Selective involvement of UGGT variant: UGGT2 in protecting mouse embryonic fibroblasts from saturated lipid-induced ER stress. Proc Natl Acad Sci U S A. 119:e2214957119.

Karlsson, G.B., T.D. Butters, R.A. Dwek, and F.M. Platt. 1993. Effects of the imino sugar N-butyldeoxynojirimycin on the N-glycosylation of recombinant gp120. Journal of Biological Chemistry. 268:570-576.

Lomako, J., W.M. Lomako, C.A. Carothers Carraway, and K.L. Carraway. 2010. Regulation of the membrane mucin Muc4 in corneal epithelial cells by proteosomal degradation and TGF-beta. Journal of cellular physiology. 223:209-214.

Mast, S.W., K. Diekman, K. Karaveg, A. Davis, R.N. Sifers, and K.W. Moremen. 2005. Human EDEM2, a novel homolog of family 47 glycosidases, is involved in ER-associated degradation of glycoproteins. Glycobiology. 15:421-436.

Ninagawa, S., T. Okada, Y. Sumitomo, S. Horimoto, T. Sugimoto, T. Ishikawa, S. Takeda, T. Yamamoto, T. Suzuki, Y. Kamiya, K. Kato, and K. Mori. 2015. Forcible destruction of severely misfolded mammalian glycoproteins by the non-glycoprotein ERAD pathway. J Cell Biol. 211:775-784.

Ninagawa, S., T. Okada, Y. Sumitomo, Y. Kamiya, K. Kato, S. Horimoto, T. Ishikawa, S. Takeda, T. Sakuma, T. Yamamoto, and K. Mori. 2014. EDEM2 initiates mammalian glycoprotein ERAD by catalyzing the first mannose trimming step. J Cell Biol. 206:347-356.

Olivari, S., C. Galli, H. Alanen, L. Ruddock, and M. Molinari. 2005. A novel stress-induced EDEM variant regulating endoplasmic reticulum-associated glycoprotein degradation. J Biol Chem. 280:2424-2428.

Pearse, B.R., T. Tamura, J.C. Sunryd, G.A. Grabowski, R.J. Kaufman, and D.N. Hebert. 2010. The role of UDP-Glc:glycoprotein glucosyltransferase 1 in the maturation of an obligate substrate prosaposin. J Cell Biol. 189:829-841.

Romero, P.A., B. Saunier, and A. Herscovics. 1985. Comparison between 1-deoxynojirimycin and N-methyl-1-deoxynojirimycin as inhibitors of oligosaccharide processing in intestinal epithelial cells. Biochem J. 226:733-740.

Saunier, B., R.D. Kilker, J.S. Tkacz, A. Quaroni, and A. Herscovics. 1982. Inhibition of N-linked complex oligosaccharide formation by 1-deoxynojirimycin, an inhibitor of processing glucosidases. Journal of Biological Chemistry. 257:14155-14161.

Szumilo, T., G.P. Kaushal, and A.D. Elbein. 1987. Purification and properties of the glycoprotein processing N-acetylglucosaminyltransferase II from plants. Biochemistry. 26:5498-5505.

Tannous, A., N. Patel, T. Tamura, and D.N. Hebert. 2015. Reglucosylation by UDP-glucose:glycoprotein glucosyltransferase 1 delays glycoprotein secretion but not degradation. Molecular biology of the cell. 26:390-405.

Zeng, Y., Y.T. Pan, N. Asano, R.J. Nash, and A.D. Elbein. 1997. Homonojirimycin and N-methyl-homonojirimycin inhibit N-linked oligosaccharide processing. Glycobiology. 7:297-304.

Author response:

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

Reviewer #1 (Public Review): 

Summary:

The goal of this project is to test the hypothesis that individual differences in experience with multiple languages relate to differences in brain structure, specifically in the transverse temporal gyrus. The approach used here is to focus specifically on the phonological inventories of these languages, looking at the overall size of the phonological inventory as well as the acoustic and articulatory diversity of the cumulative phonological inventory in people who speak one or more languages. The authors find that the thickness of the transverse temporal gyrus (either the primary TTG, in those with one TTG, or in the second TTG, in people with multiple gyri) was related to language experience, and that accounting for the phonological diversity of those languages improved the model fit. Taken together, the evidence suggests that learning more phonemes (which is more likely if one speaks more than one language) leads to experience-related plasticity in brain regions implicated in early auditory processing.

Strengths:

This project is rigorous in its approach--not only using a large sample, but replicating the primary finding in a smaller, independent sample. Language diversity is difficult to quantify, and likely to be qualitatively and quantitatively distinct across different populations, and the authors use a custom measure of multilingualism (accounting for both number of languages as well as age of acquisition) and three measures of phonological diversity. The team has been careful in discussion of these findings, and while it is possible that pre-existing differences in brain structure could lead to an aptitude difference which could drive one to learn more than one language, the fine-grained relationships with phonological diversity seem less likely to emerge from aptitude rather than experience. 

Weaknesses:

It is a bit unclear how the measures of phonological diversity relate to one another--they are partially separable, but rest on the same underlying data (the phonemes in each language). It would be helpful for the reader to understand how these measures are distributed (perhaps in a new figure), and the degree to which they are correlated with one another. 

Thank you for the comment. Indeed our description missed this important detail that we now included in the manuscript. Unsurprisingly, the distances all correlated with one another, which we present in Table 2 in Section 2.3 of the revised manuscript. We have also added a figure with distributions of the three distance measures (see Figure S3).

Further, as the authors acknowledge, it is always possible that an unseen factor instead drives these findings--if typological lexical distance measures are available, it would be helpful to enter these into the model to confirm that phonological factors are the specific driver of TTG differences and not language diversity in a more general sense. That said, the relationship between phonological diversity and TTG structure is intuitive. 

Thank you for the suggestion. To further establish that our results reflected the relationship between TTG structure and phonological diversity specifically (as opposed to language diversity in a more general sense), we derived a fourth measure of language experience, where the AoA index of different languages was weighted by lexical distances between the languages. Here, we followed the methodology described in Kepinska, Caballero, et al. (2023): We used Levenshtein Distance Normalized Divided (LDND) (Wichmann et al., 2010) which was computed using the ASJP.R program by Wichmann (https://github.com/Sokiwi/InteractiveASJP01). Information on lexical distances was combined with language experience information per participant using Rao's quadratic entropy equation in the same way as for the phonological measures.

We then entered this language experience measure accounting for lexical distances between the languages into linear models predicting the thickness of the second left and right TTG (controlling for participants’ age, sex and mean hemispheric thickness) in the main sample, and compared these models with the corresponding models including the original three phonological distance measures (models 24 in Author response table 1), and the measure with no typological information (1).

Below, we list adjusted R2 values of all models, from which it is clear that the index of multilingual language experience accounting for lexical distances between languages (5) explained less variance than the index incorporating phoneme-level distances between languages (2), both in the left and the right hemisphere. This further strengthens our conclusion that our results reflected the relationship between TTG structure and phonological diversity specifically, as opposed to language diversity in a more general sense.

Author response table 1.

We have added a description of this analysis to the manuscript, Section 3.3, lines 357-370.

One curious aspect of this paper relates to the much higher prevalence of split or duplicate TTG in the sample. The authors do a good job speculating on how features of the TASH package might lead to this, but it is unclear where the ground truth lies--some discussion of validation of TASH against a gold standard would be useful. 

The validation of the TASH toolbox in comparison to gold standard manual measurement involved assessing how well the measurements of left and right Heschl's gyrus (HG) volumes obtained using the TASH method correlated with those obtained through manual labeling (see Dalboni da Rocha et al., 2020 for details). This validation process was conducted across three independent datasets. Additionally, for comparison, the manually labeled HG volumes were also compared with those obtained using FreeSurfer's Destrieux parcellation of the transverse temporal gyrus in the same datasets. The validation process, therefore, involved rigorous comparisons of HG volumes obtained through manual labeling, FreeSurfer, and TASH across different datasets, along with an assessment of inter-rater reliability for the manual labeling procedure. This comprehensive approach ensures that the results are robust and reliable. TASH_complete, the version used in the present work, is an extension of the extensively validated TASH, which apart from the first gyrus, also identifies additional transverse temporal gyri (i.e. Heschl’s gyrus duplications and multiplications) situated in the PT, when present. Since work on the correspondence between manually identified TTG multiplications is still ongoing, as outlined in the Methods section, we complemented the automatic segmentation by extensive visual assessment of the identified posterior gyri. This process involved removing from the analysis those gyri that lay along the portion of the superior temporal plane that curved vertically (i.e., within the parietal extension, Honeycutt et al., 2000), when present. Given that TASH_complete and TASH operate on the same principles and are both based on FreeSurfer’s surface reconstruction and cortical parcellation (which have been extensively validated against manual tracing and other imaging modalities, showing good accuracy), and since we have visually inspected all segmentations, we are confident as to the accuracy of the reported TTG variability. It has to be further noted that the prevalence of TTG multiplications beyond 2nd full posterior duplications was not systematically assessed in previous descriptive reports (Marie, 2015). However, we acknowledge that more work is needed to further ascertain anatomical accuracy of the segmentations, and we elaborate on this point in the Discussion of the revised manuscript (lines 621-623).

Reviewer #2 (Public Review):

This work investigates the possible association between language experience and morphology of the superior temporal cortex, a part of the brain responsible for the processing of auditory stimuli. Previous studies have found associations between language and music proficiency as well as language learning aptitude and cortical morphometric measures in regions in the primary and associated auditory cortex. These studies have most often, however, focused on finding neuroanatomical effects of difference between features in a few (often two) languages or from learning single phonetic/phonological features and have often been limited in terms of N. On this background, the authors use more sophisticated measures of language experience that take into account the age of onset and the differences in phonology between languages the subjects have been exposed to as well as a larger number of subjects (N = 146 + 69) to relate language experience to the shape and structure of the superior temporal cortex, measured from T1weighted MRI data. It shows solid evidence for there being a negative relationship between language experience and the right 2nd transverse temporal gyrus as well as some evidence for the relationship representing phoneme-level cross-linguistic information. 

Strengths 

The use of entropy measures to quantify language experience and include typological distance measures allows for a more general interpretation of the results and is an important step toward respecting and making use of linguistic diversity in neurolinguistic experiments. 

A relatively large group of subjects with a range of linguistic backgrounds. 

The full analysis of the structure of the superior temporal cortex including cortical volume, area, as well as the shape of the transverse gyrus/gyri. There is a growing literature on the meaning of the shape and number of the transverse gyri in relation to language proficiency and the authors explore all measures given the available data. 

The authors chose to use a replication data set to verify their data, which is applaudable. However, see the relevant point under "Weaknesses". 

Weaknesses 

The authors fail to explain how a thinner cortex could reflect the specialization of the auditory cortex in the processing of diverse speech input. The Dynamic Restructuring Model (Pliatsikas, 2020) which is referred to does not offer clear guidance to interpretation. A more detailed discussion of how a phonologically diverse environment could lead to a thinner cortex would be very helpful. 

Thank you for bringing our attention to this point. We have now extended the explanation we had previously included in the Discussion by including the following passage on p. 20 (lines 557-566) of the revised manuscript:

“Experience-induced pruning is essential for maintaining an efficient and adaptive neural network. It reinforces relevant neural circuits for faster more efficient information processing, while diminishing those that are less active, or less beneficial. The cortical specialization may need to arise because phonologically more diverse language experience requires that the mapping of acoustic signal to sound categories is denser, more detailed and more intricate. As a result, the brain may need to engage in more intensive processing to discriminate between and accurately perceive the sound categories of each language. This increased cognitive demand may, in turn, require the auditory and language processing regions of the brain to adapt and become more efficient. Over time, this heightened effort for successful speech perception and sound discrimination may lead to neural plasticity, resulting in cortical specialization. This means that cortical areas become more finely tuned and specialized for processing the unique phonological features of language(s) spoken by individuals.” 

We have also added a passage to the Introduction regarding the possible microscopic or physiological underpinnings of the brain structural differences that we observe macroscopically using structural MRI (lines 68-73): 

“Such environmental effect on cortical thickness might in turn be tied to microstructural changes to the underlying brain tissue, such as modifications in dendritic length and branching, synaptogenesis or synaptic pruning, growth of capillaries and glia, all previously tied to some kind of environmental enrichment and/or skill learning (see Lövdén et al., 2013; Zatorre et al., 2012 for overviews). Increased cortical thickness may reflect synaptogenesis and dendritic growth, while cortical thinning observed with MRI may be a result of increased myelination (Natu et al., 2019) or synaptic pruning.”

It is difficult to understand what measure of language experience is used when. Clearer and more explicit nomenclature would assist in the interpretation of the results. 

We have added more explicit list of indices used in the Introduction (lines 104-107 of the revised manuscript) and in Section 2.4 and used them consistently throughout the text:

(1) language experience index not accounting for typological features: ‘Language experience - no typology’

(2) measures combining language experience with typological distances at different levels: 

a. ‘Language experience – features’, 

b. ‘Language experience – phonemes’, 

c. ‘Language experience – phonological classes’.

There is a lack of description of the language backgrounds of the included subjects. How many came from each of the possible linguistic backgrounds? How did they differ in language exposure? This would be informative to evaluate the generalizability of the conclusions. 

Thank you for raising this point. Given the complexity of participants’ language experience, ranging between monolingual to speaking 7 different languages, we opted for a fully parametric approach in quantifying it. We used the Shannon’s entropy and Rao’s quadratic entropy equations to create continuous measures of language experience, without the constraints of a minimum sample size per language and the need to exclude participants with underrepresented languages. To add further details in our description of the language background, we summarize the language background of both samples in the newly added Table 1 presenting a breakdown of participants by number of languages they spoke, and Supplementary Table S1 listing all languages spoken by each participant.

Only the result from the multiple transverse temporal gyri (2nd TTG) is analyzed in the replicated dataset. Only the association in the right hemisphere 2nd TTG is replicated but this is not reflected in the discussion or the conclusions. The positive correlation in the right TTG is thus not attempted to be replicated. 

Thank you for bringing this point to our attention. Since only few participants presented single gyri in the left (n = 7) and the right hemisphere (n = 14), the replication analysis focused on the second TTG results only. We have now commented on this fact in Section 3.5 (lines 413-415), as well as in the Discussion (lines 594-596). 

The replication dataset differed in more ways than the more frequent combination of English and German experience, as mentioned in the discussion. Specifically, the fraction of monolinguals was higher in the replication dataset and the samples came from different scanners. It would be better if the primary and replication datasets were more equally matched. 

Indeed, the replication sample did not fully mimic the characteristics of the main sample and a better match between the two samples would have been preferable. As elaborated in the Introduction, however, the data was split into two groups according to the date of data acquisition, which also coincided with the field strength of the scanners used for data acquisition: the first, main sample’s data were acquired on a 1.5T, the replication sample’s on 3T. We opted for keeping this split and not introducing additional noise in the analysis by using data from different field strengths at the cost of not fully matching the two datasets. Observing the established effects (even partially) in this somewhat different replication sample, however, seems in our view to further strengthen our results. 

Even if the language experience and typological distance measures are a step in the right direction for correctly associating language exposure with cortical plasticity, it still is a measure that is insensitive to the intensity of the exposure. The consequences of this are not discussed. 

Indeed, we agree with the reviewer that there is still a lot of grounds to cover to fully understand the relationship between language experience and cortical plasticity. We have added a paragraph to the Discussion (lines 587-592 of the revised manuscript) to bring attention to this issue:

“Future research should also further increase the degree of detail in describing the multilingual language experience, as both AoA and proficiency (used here) are not sensitive to other aspects of multilingualism, such as intensity of the exposure to the different languages, or quantity and quality of language input. Since these aspects have been convincingly shown to be associated with neural changes (e.g., Romeo, 2019), incorporating further, more detailed measures describing individuals’ language experience could further enhance our understanding of cortical plasticity in general, and how the brain accommodates variable language experience in particular.” 

Reviewer #3 (Public Review): 

Summary: 

The study uses structural MRI to identify how the number, degree of experience, and phonemic diversity of language(s) that a speaker knows can influence the thickness of different sub-segments of the auditory cortex. In both a primary and replication sample of adult speakers, the authors find key differences in cortical thickness within specific subregions of the cortex due to either the age at which languages are acquired (degree of experience), or the diversity of the phoneme inventories carried by that/those language(s) (breadth of experience). 

Strengths: 

The results are first and foremost quite fascinating and I do think they make a compelling case for the different ways in which linguistic experience shapes the auditory cortex. 

The study uses a number of different measures to quantify linguistic experience, related to how many languages a person knows (taking into account the age at which each was learned) as well as the diversity of the phoneme inventories contained within those languages. The primary sample is moderately large for a study that focuses on brainbehaviour relationships; a somewhat smaller replication sample is also deployed in order to test the generality of the effects. 

Analytic approaches benefit from the careful use of brain segmentation techniques that nicely capture key landmarks and account for vagaries in the structure of STG that can vary across individuals (e.g., the number of transverse temporal gyri varies from 1-4 across individuals). 

Weaknesses: 

The specificity of these effects is interesting; some effects really do appear to be localized to the left hemisphere and specific subregions of the auditory cortex e.g., TTG. However because analyses only focus on auditory regions along the STG and MTG, one could be led to the conclusion that these are the only brain regions for which such effects will occur. The hypothesis is that these are specifically auditory effects, but that does make a clear prediction that nonauditory regions should not show the same sort of variability. I recognize that expanding the search space will inflate type-1 errors to a point where maybe it's impossible to know what effects are genuine. And the fine-grained nature of the effects suggests a coarse analysis of other cortical regions is likely to fail. So I don't know the right answer here. Only that I tend to wonder if some control region(s) might have been useful for understanding whether such effects truly are limited to the auditory cortex. Otherwise one might argue these are epiphenomenal or some hidden factor unrelated to auditory experience predicting that we'd also see them in the non-auditory cortex as well, either within or outside the brain's speech network(s). 

Thank you for raising this important issue. Our primary analyses indeed focused on the auditory regions, given their involvement in speech and language processing at different levels of processing hierarchy (from low – HG, to high – STG and STS). Here, we included a fairly broad range of ROIs (8 per hemisphere, 16 in total) and it has to be noted that it was only the bilateral planum temporale which showed an association with multilingualism. In the original submission we had indeed attempted at confirming the specificity of this result by performing a whole-brain vertex-wise analysis in freesurfer (see Table 3, Section 3.2, Figure S5), which again showed that the only cluster of vertices related to participants’ language experience at p < .0001 (uncorrected) was located in the superior aspect of the left STG, corresponding to the location of planum temporale and the second TTG. Lowering the threshold of statistical significance to p < .001 (uncorrected) results in further clusters of vertices whose thickness was positively associated with the degree of multilingual language experience localized in:

• Left hemisphere: central sulcus (S_cenral), long insular gyrus and central sulcus of the insula (G_Ins_lg_and_S_cent_ins), lingual gyrus (G_oc-temp_med-Lingual), planum temporale of the superior temporal gyrus (G_temp_sup-Plan_tempo), short insular gyri (G_insular_short), middle temporal gyrus (G_temporal_middle), and planum polare of the superior temporal gyrus (G_temp_sup-Plan_polar)

• Right hemisphere: angular gyrus (G_pariet_inf-Angular), superior temporal sulcus (S_temporal_sup), middle-posterior part of the cingulate gyrus and sulcus (G_and_S_cingul-Mid-Post), marginal branch of the cingulate sulcus (S_cingul-Marginalis), parieto-occipital sulcus (S_parieto_occipital), parahippocampal gyrus (G_oc-temp_med-Parahip), Inferior temporal gyrus (G_temporal_inf)

We present the result of this analysis in Author response image 1, where clusters are labelled according to the Destrieux anatomical atlas implemented in FreeSurfer:

Author response image 1.

As the reviewer points out, establishing relationships between our dependent and independent variables at a lower threshold of statistical significance might not reflect a true effect, and it is statistically more probable that multilingualism-related cortical thickness effects seem to be specific to the auditory regions. We do not exclude that an analysis of other pre-defined ROIs, performed at a similar level of detail as our present investigation, would uncover further significant associations between multilingual language experience and brain anatomy, but such an investigation is beyond the scope of the present work.

The reason(s) why we might find a link between cortical thickness and experience is not fully discussed. The introduction doesn't really mention why we'd expect cortical thickness to be correlated (positively or negatively) with speech experience. There is some discussion of it in the Discussion section as it relates to the Pliatsikas' Dynamic Restructuring Model, though I think that model only directly predicts thinning as a function of experience (here, negative correlations). It might have less to say about observed positive correlations e.g., HG in the right hemisphere. In any case, I do think that it's interesting to find some relationship between brain morphology and experience but clearer explanations for why these occur could help, and especially some mention of it in the intro so readers are clearer on why cortical thickness is a useful measure. 

We have expanded the section of the Introduction introducing cortical thickness pointing to different microstructural changes previously associated with environmental enrichment and skill learning (lines 68-73), and hope the link between cortical thickness and multilingual language experience is clearer now:

“Such environmental effect on cortical thickness might in turn be tied to microstructural changes to the underlying brain tissue, such as modifications in dendritic length and branching, synaptogenesis or synaptic pruning, growth of capillaries and glia, all previously tied to some kind of environmental enrichment and/or skill learning (see Lövdén et al., 2013; Zatorre et al., 2012 for overviews). Increased cortical thickness may reflect synaptogenesis and dendritic growth, while cortical thinning observed with MRI may be a result of increased myelination (Natu et al., 2019) or synaptic pruning.”

In addition, we have also expanded the Discussion section providing more reasoning for the links between cortical thickness and multilingual language experience (lines 557-566):

“Experience-induced pruning is essential for maintaining an efficient and adaptive neural network. It reinforces relevant neural circuits for faster more efficient information processing, while diminishing those that are less active, or less beneficial. The cortical specialization may need to arise because phonologically more diverse language experience requires that the mapping of acoustic signal to sound categories is denser, more detailed and more intricate. As a result, the brain may need to engage in more intensive processing to discriminate between and accurately perceive the sound categories of each language. This increased cognitive demand may, in turn, require the auditory and language processing regions of the brain to adapt and become more efficient. Over time, this heightened effort for successful speech perception and sound discrimination may lead to neural plasticity, resulting in cortical specialization. This means that cortical areas become more finely tuned and specialized for processing the unique phonological features of language(s) spoken by individuals.” 

One pitfall of quantifying phoneme overlap across languages is that what we might call a single 'phoneme', shared across languages, will, in reality, be realized differently across them. For instance, English and French may be argued to both use the vowel /u/ although it's realized differently in English vs. French (it's often fronted and diphthongized in many English speaker groups). Maybe the phonetic dictionaries used in this study capture this using a close phonetic transcription, but it's hard to tell; I suspect they don't, and in that case, the diversity measures would be an underestimate of the actual number of unique phonemes that a listener needs to maintain. 

The PHOIBLE database uses transcription that reflects phonological descriptive data as closely as possible, according to the available descriptive sources. Different realizations of sounds are (as much as possible) marked in the database. For example, the open front unrounded vowel /a/ is listed as e.g., [a] or [a̟ ], with the “+” sign denoting a fronted realization. This is done in PHOIBLE by the use of diacritics (see https://phoible.org/conventions) which further specify variations on the language-specific realizations of the phonemes listed in the database. Further details are available in Moran (2012) (https://digital.lib.washington.edu/researchworks/items/0d26e54d-950a-4d0b-b72c-3afb4b1aa9eb). In our calculation of phoneme-based distances a sign with and without a diacritic were treated as different phonemes, and therefore the different realizations were accounted for.

That said, we fully agree with the reviewer that in fact any diversity measure will be an underestimation of the actual variation, as between-speaker micro-variation can never be fully reflected in largescale typological databases as the one used in the present study. To the best of our knowledge, however, PHOIBLE offers the most comprehensive way of allowing for quantifying cross-linguistic variation to date, and we are looking forward for the field to offer further tools capturing the linguistic variability at an ever-finer level of detail. 

Discussion of potential genetic differences underlying the findings is interesting. One additional data point here is a study finding a relationship between the number of repeats of the READ1 (a factor of the DCDC2 gene) in populations of speakers, and the phoneme inventory of language(s) predominant in that population (DeMille, M. M., Tang, K., Mehta, C. M., Geissler, C., Malins, J. G., Powers, N. R., ... & Gruen, J. R. (2018). Worldwide distribution of the DCDC2 READ1 regulatory element and its relationship with phoneme variation across languages. Proceedings of the National Academy of Sciences, 115(19), 4951-4956.) Admittedly, that paper makes no claim about the cortical expression of that regulatory factor under study, and so more work needs to be done on whether this has any bearing at all on the auditory cortex. But it does represent one alternative account that does not have to do with plasticity/experience. 

We thank the reviewer for bringing this important line of research to our attention, which we now included in the Discussion (lines 494-498 of the revised manuscript).

The replication sample is useful and a great idea. It does however feature roughly half the number of participants meaning statistical power is weaker. Using information from the first sample, the authors might wish to do a post-hoc power analysis that shows the minimum sample size needed to replicate their effect; given small effects in some cases, we might not be surprised that the replication was only partial. I don't think this is a deal breaker as much as it's a way to better understand whether the failure to replicate is an issue of power versus fragile effects. 

Thank you for the suggestion. Indeed, the effect sizes established in the analyses using the main sample were small (e.g., f2 = 0.07). According to a power analysis performed with G*Power 3.1 (Faul et al., 2009), detecting an effect of this magnitude of the predictor of interest at alpha = .05 (two-tailed), in a linear multiple regression model with 4 predictors (i.e., 3 covariates of no-interest: sex, age, hemispheric thickness, and 1 predictor of interest), a sample of N = 114 is required to achieve 80% of power. Our partial lack of replicating the effect might therefore indeed be related to a lower power of the replication sample, rather than the effect itself being fragile.

Recommendations for the authors:

Reviewer #1 (Recommendations for the Authors): 

A few remaining details that I think you can handle: 

(1) Was there any correction for multiple comparisons, especially when multiple anatomical measures were investigated in separate models? (e.g. ln 130). 

Since three different anatomical measures were investigated in Analysis 1 and Analysis 2 (see Table 1), the alpha level of the two linear mixed models was lowered to α = .0166. Note that the p-values of the predictors of interest were p = .012 (mixed model with all auditory regions) and p = .005 (mixed model with all identified TTGs).

(2) In Table 2, since your sample skews heavily female, it would be more useful to present the counts of Male/Female totals for 1, 2, 3, 4, etc TTGs as proportions of the total for that sex rather than counts, so that the distribution across sex is more obvious. 

Thank you for bringing this issue to our attention. We have now included an additional row in Table 4, with proportions of males and females presenting different total number of identified gyri in the left and the right hemisphere.

(3) (ln 161) It wasn't clear to me how you dealt statistically with the fact that some participants had only one TTG - did you simply enter "0" as a value for cortical thickness for 2, 3, etc. for those participants? If so, it's possible that this result could reflect the number of split/duplicated gyri rather than the thickness of those gyri. 

Indeed, if non-existing gyri were coded with a value of “0” (it being the lowest possible thickness value), the results would reflect the configuration of TTGs (single vs multiple gyri) rather than a relationship between thickness and language experience.

The model was, however, fit to all available thickness values, and the gyri labels (1st, 2nd, 3rd) were modeled as a fixed factor with 3 levels. This procedure allowed us to localize the effect of language experience to a specific gyrus. The following formula was used with the lmer package in R:

thickness ~ age + sex + whole_brain_thickness + language_experience* gyrus*hemisphere + (1 | participant_id)

We observed a significant interaction between language experience and the 2nd gyrus (NB. no significant 3-way interaction between language experience, the 2nd gyrus and hemisphere pointed to the effect being bilateral). This result was then followed up with two linear models: one for the thickness values of the 2nd left and one for the 2nd right gyrus, each fit to the available data only (n = 130 for the left hemisphere; n = 96 for the right), see Table 5. This procedure ensured that only the available cortical thickness data were considered when establishing their relationship with our independent variable (language experience).

(4) I think more could be done in the results section to distinguish your three phonological measures--these details are evident in the Methods section, but if readers consume this paper front to back they may find it difficult to figure out what each measure really means. 

Thank you. We have added more explicit list of indices used in the Introduction (lines 104-107) and in Section 2.4. As per Reviewer #2 comments, the Methods section was also moved before the Results section, hopefully further enhancing the readability of the paper.

Typos: 

ln 270: "weighed"--could you have meant "weighted"? 

Corrected, thank you! 

ln 377: "Apart from phoneme-based typological distance measure explaining" --> "Apart from *the* phonemebased..." 

Corrected, thank you! 

Reviewer #2 (Recommendations for the Authors): 

The interpretation of the results would be much helped by the methods section being moved to precede it. Now, much of the results section is methods summaries that would not have been needed if the reader had been presented with the methods beforehand. This is especially true for the measures of language experience and typological distances used. 

Thank you. We have moved the Materials and Methods section before the Results section.

The equation in section "4.2 Language experience" should be H = - sum(p_i log2 (p_i)) and not H = - sum(p_i log2(i)). 

Corrected, thank you! 

It is unclear what "S" represents in the equation in the section "4.4 Combining typology and language experience (indexed by AoA)".  

The explanation has been added, thank you!

Author Response

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

Assessment note: “Whereas the results and interpretations are generally solid, the mechanistic aspect of the work and conclusions put forth rely heavily on in vitro studies performed in cultured L6 myocytes, which are highly glycolytic and generally not viewed as a good model for studying muscle metabolism and insulin action.”

While we acknowledge that in vitro models may not fully recapitulate the complexity of in vivo systems, we believe L6 myotubes are appropriate for studying the mechanisms underlying muscle metabolism and insulin action. L6 myotubes possess many important characteristics relevant to our research, including high insulin sensitivity and a similar mitochondrial respiration sensitivity compared to primary muscle fibres. Furthermore, several studies have demonstrated the utility of L6 myotubes as a model for studying insulin sensitivity and metabolism, including our own previous work (PMID: 19805130, 31693893, 19915010) and work of others (PMID:12086937, 29486284, 15193147).

Importantly, our observations from the L6 myotube model are supported by in vivo data from both mice and humans. Chow (Figure 3J, K) and high-fat fed mice (new data - Supplementary Figure 4 H-I) demonstrated a reduction in mitochondrial Ceramide and an increase in CoQ9. Muscle biopsies from humans showed a strong negative correlation between mitochondrial C18:0 ceramide levels and insulin sensitivity (PMID: 29415895). Further, complex I and IV abundance was strongly correlated with both muscle insulin sensitivity and mitochondrial ceramide (CerC18:0) (Figure 6E, F). This is consistent with our observations in L6 myotubes (Figure 6H, I). These findings support the relevance of our in vitro results to in vivo muscle metabolism.

Points from reviewer 1

1. Although the authors' results suggest that higher mitochondrial ceramide levels suppress cellular insulin sensitivity, they rely solely on a partial inhibition (i.e., 30%) of insulin-stimulated GLUT4-HA translocation in L6 myocytes. It would be critical to examine how much the increased mitochondrial ceramide would inhibit insulin-induced glucose uptake in myocytes using radiolabeled deoxy-glucose. Another important question to be addressed is whether glycogen synthesis is affected in myocytes under these experimental conditions. Results demonstrating reductions in insulin-stimulated glucose transport and glycogen synthesis in myocytes with dysfunctional mitochondria due to ceramide accumulation would further support the authors' claim.

Response: We have now conducted additional experiments focusing on glycogen synthesis as a readout of insulin sensitivity, as it offers an orthogonal method for assessing GLUT4 translocation and glucose uptake. L6-myotubes overexpressing the mitochondrial-targeted ASAH1 construct (as described in Fig. 3) were challenged with palmitate and insulin stimulated glycogen synthesis was measured using 14C radiolabeled glucose. As shown below, palmitate suppressed insulin-induced glycogen synthesis, which was effectively prevented by overexpression of ASAH1 (N = 5, * p<0.05) supporting our previous observation using GLUT4 translocation as a readout of insulin sensitivity (Fig. 3). These results provide additional evidence highlighting the role of dysfunctional mitochondria in muscle cell glucose metabolism.

These data have now been added to Supplementary Figure 4K and the results modified as follows:

“...For this reason, several in vitro models have been employed involving incubation of insulin sensitive cell types with lipids such as palmitate to mimic lipotoxicity in vivo. In this study we have used cell surface GLUT4-HA abundance as the main readout of insulin response...”

“Notably, mtASAH1 overexpression protected cells from palmitate-induced insulin resistance without affecting basal insulin sensitivity (Fig. 3E). Similar results were observed using insulin-induced glycogen synthesis as an orthologous technique for Glut4 translocation. These results provide additional evidence highlighting the role of dysfunctional mitochondria in muscle cell glucose metabolism (Sup. Fig. 5K). Importantly, mtASAH1 overexpression did not rescue insulin sensitivity in cells depleted…”

Author response image 1.

Additionally, the following text was added to the method section:

“L6 myotubes overexpressing ASAH were grown and differentiated in 12-well plates, as described in the Cell lines section, and stimulated for 16 h with palmitate-BSA or EtOH-BSA, as detailed in the Induction of insulin resistance section.

On day seven of differentiation, myotubes were serum starved in DMEM for 3.5 h. After incubation for 1 h at 37 °C with 2 µCi/ml D-[U-14C]-glucose in the presence or absence of 100 nM insulin, glycogen synthesis assay was performed, as previously described (Zarini S. et al., J Lipid Res, 63(10): 100270, 2022).”

1. In addition, it would be critical to assess whether the increased mitochondrial ceramide and consequent lowering of energy levels affect all exocytic pathways in L6 myoblasts or just the GLUT4 trafficking. Is the secretory pathway also disrupted under these conditions?

Response: This is an interesting point raised by the reviewer that is aimed at the next phase of this work, to identify how ceramide induced mitochondrial dysfunction drives insulin resistance. Looking at energy deficiency in more detail as well as general trafficking is part of ongoing work, but given the complexity of this question, it is beyond the scope of the current study.

Points from reviewer 2

1. The mechanistic aspect of the work and conclusions put forth rely heavily on studies performed in cultured myocytes, which are highly glycolytic and generally viewed as a poor model for studying muscle metabolism and insulin action. Nonetheless, the findings provide a strong rationale for moving this line of investigation into mouse gain/loss of function models.

Response: We acknowledge that in vitro models may not fully mimic in vivo complexity as described above in the response to the “Assessment note”. We have now added to the Discussion:

“In this study, we mainly utilised L6-myotubes, which share many important characteristics with primary muscle fibres. Both types of cells exhibit high sensitivity to insulin and respond similarly to maximal doses of insulin, with GLUT4 translocation stimulated between 2 to 4 times over basal levels in response to 100 nM insulin (as shown in Fig. 1-4 and (46,47)). Additionally, mitochondrial respiration in L6-myotubes has a similar sensitivity to mitochondrial poisons, as observed in primary muscle fibres (as shown in Fig. 5 (48)). Finally, inhibiting ceramide production increases CoQ levels in both L6-myotubes and adult muscle tissue (as shown in Fig. 2-3). Therefore, L6-myotubes possess the necessary metabolic features to investigate the role of mitochondria in insulin resistance, and this relationship is likely applicable to primary muscle fibres”.

1. One caveat of the approach taken is that exposure of cells to palmitate alone is not reflective of in vivo physiology. It would be interesting to know if similar effects on CoQ are observed when cells are exposed to a more physiological mixture of fatty acids that includes a high ratio of palmitate, but better mimics in vivo nutrition.

Response: We appreciate the reviewer's comment. Previously, we reported that mitochondrial CoQ depletion occurs in skeletal muscle after 14 and 42 days of HFHSD feeding, coinciding with the onset of insulin resistance (PMID: 29402381, see figure below).

Author response image 2.

These data demonstrated that our in vitro model recapitulates the loss of CoQ in insulin resistance observed in muscle tissue in response to a more physiological mixture of fatty acids. Further, it has been reported that different fatty acids can induce insulin resistance via different mechanisms (PMID:20609972), which would complicate interpretation of the data. Saturated fatty acids such as palmitate increase ceramides in cell-lines and humans, but unsaturated FAs generally do not (PMID: 10446195,14592453,34704121). As such we conclude that palmitate is a cleaner model for studying the effects of ceramide on skeletal muscle function.

We have added to discussion:

“…These findings align with our earlier observations demonstrating that mice exposed to HFHSD exhibit mitochondrial CoQ depletion in skeletal muscle (Fazakerley et al. 2018).”

1. While the utility of targeting SMPD5 to the mitochondria is appreciated, the results in Figure 5 suggest that this manoeuvre caused a rather severe form of mitochondrial dysfunction. This could be more representative of toxicity rather than pathophysiology. It would be helpful to know if these same effects are observed with other manipulations that lower CoQ to a similar degree. If not, the discrepancies should be discussed.

Response: As the reviewer suggests many of these lipids can cause cell death (toxicity) if the dose is too high. We have previously found that low levels (0.15 mM) of palmitate were sufficient to trigger insulin resistance without any signs of toxicity (Hoehn, K, PNAS, 19805130). Using a similar approach, we show that mitochondrial membrane potential is maintained in SMPD5 overexpressing cells (Sup. Fig. 2J - and Author response image 2). Given that toxicity is associated with a loss of mitochondrial membrane potential (eg., 50uM Saclac; RH panel), these data suggest SMPD5 overexpression is not causing overt toxicity.

Author response image 3.

Furthermore, we conducted an overrepresentation analysis of molecular processes within our proteomic data from SMPD5-overexpressing cells. As depicted below, no signs of cell toxicity were observed in our model at the protein level. This data is now available in supplementary table 1.

Author response table 1.

Our results are therefore consistent with a pathological condition induced by elevated levels of ceramides independently of cellular toxicity. The following text has been added to the discussion:“...downregulation of the respirasome induced by ceramides may lead to CoQ depletion.

Despite the significant impact of ceramide on mitochondrial respiration, we did not observe any indications of cell damage in any of the treatments, suggesting that our models are not explained by toxicity and increased cell death (Sup. Fig. 2H & J).”

1. The conclusions could be strengthened by more extensive studies in mice to assess the interplay between mitochondrial ceramides, CoQ depletion and ETC/mitochondrial dysfunction in the context of a standard diet versus HF diet-induced insulin resistance. Does P053 affect mitochondrial ceramide, ETC protein abundance, mitochondrial function, and muscle insulin sensitivity in the predicted directions?

Response: We agree with the referee about the importance of performing in vivo studies to corroborate our in vitro data. We have now conducted extensive new studies in mice skeletal muscle using targeted metabolomic and lipidomic analyses to investigate the impact of ceramide depletion in CoQ levels in HF-fed mice. Mice were exposed to a HF-fed diet with or without the administration of P053 (selective inhibitor of CerS1) for 5 weeks. As illustrated in the figures below, the administration of P053 led to a reduction in ceramide levels (left panel), increase in CoQ levels (middle panel) and a negative correlation between these molecules (right panel), which is consistent with our in vitro findings.

Author response image 4.

Additional suggestions:

1. Figure 1: How does increased mitochondrial ceramide affect fatty acid oxidation (FAO) in L6-myocytes? As the accumulation of mitochondrial ceramide inhibits respirasome and mitochondrial activity in vitro, can reduce FAO in vivo, due to high mitochondrial ceramide, accounts for ectopic lipid deposition in skeletal muscle of obese subjects?

Response: We appreciate the reviewer for bringing up this intriguing point. We would like to emphasise that Complex II activity is vital for fatty acid oxidation. As shown in Fig. 5H, our results indicate that specifically Complex II mediated respiration was diminished in cells with SMPD5 overexpression, suggesting that ceramides hinder the mitochondria's capability to oxidise lipids. We agree that this mechanism may potentially play a role in the ectopic lipid accumulation seen in individuals with obesity.

We have added the following text to discussion:

“...the mitochondria to switch between different energy substrates depending on fuel availability, named “metabolic Inflexibility”...this mechanism may potentially play a role in the ectopic lipid accumulation seen in individuals with obesity, a condition linked with cardio-metabolic disease.”

1. Figure 2: Although the authors show that mtSMPD5 overexpression does not affect ceramide abundance in whole cell lysate, it would be critical to examine the abundance of this lipid in other cellular membranes and organelles, particularly plasma membrane. What is the effect of mtSMPD5 overexpression on plasma membrane lipids composition? Does that affect GLUT4-containing vesicles fusion into the plasma membrane, possibly due to depletion of v-SNARE or tSNARE?

Response: While we acknowledge the importance of this point we strongly feel that measuring lipids in purified membranes has its limitations because it is impossible to purify specific membranes without contamination from other kinds of membranes. For example, we have done proteomics on purified plasma membranes from different cell types and we always observe considerable mitochondrial contamination with these membranes (e.g. PMID 21928809). This was the main factor that led us to use the mitochondrial targeting approach.

Nevertheless we do acknowledge that there is a possibility that ceramides that are produced in the mitochondria in SMPD5 cells could leak out of mitochondria into other membranes and this could influence other aspects of GLUT4 trafficking and insulin action. However, we believe that the studies using mito targeted ASAH mitigate against this problem. Thus, we have now included a statement in the revised manuscript as follows: “It is also possible that ceramides generated within mitochondria in SMPD5 cells leak out from the mitochondria into other membranes (e.g. PM and Glut4 vesicles) affecting other aspects of Glut4 trafficking and insulin action. However, the observation that ASAH1 overexpression reversed IR without affecting whole cell ceramides argues against this possibility.”.

1. Figure 4: One critical piece of information missing is the effect (if any) of mitochondrial ceramide accumulation on the mRNAs encoding the ETC components affected by this lipid. Although the ETC protein's lower stability may account for the effect of increased ceramide, transcriptional inhibition can't be ruled out without checking the mRNA expression levels for these ETC components.

Response: To address this point, we have quantified the mRNA abundance of nine complex I subunits that exhibit downregulation in our proteomic dataset subsequent to mtSMPD5 overexpression (as depicted in Figure 4G).

Induction of mtSMPD5 expression with doxycycline (below - Left hand panel) had no effect on the mRNA levels of the Complex I subunits (below - right hand panel).. This is consistent with our initial hypothesis that the reduction in electron transport chain (ETC) components, caused by heightened ceramide levels, primarily arises from alterations in protein stability rather than gene expression. While we acknowledge the possibility that certain subunits might be regulated at the transcriptional level, the absence of mRNA downregulation across our data strongly suggests that, at the very least, a portion of the observed protein depletion is attributed to diminished protein stability. We have incorporated this dataset into Supplementary Figure 6J and added the following text to the results:

Author response image 5.

“Importantly, CI downregulation was not associated with reduction in gene expression as shown in Sup. Fig. 6J.”

Additionally, we have added the following text to discussion:

“In addition, the absence of mRNA downregulation in mtSMPD5 overexpressing cells strongly suggests that at least a portion of the observed protein depletion within CI is attributed to diminished protein stability.”

1. Figure 3: The authors state that neither palmitate nor mtASAH1 overexpression affected insulin-dependent Akt phosphorylation. However, the results in Figure 3F-G do not support this conclusion, as the overexpression of mtASAH1 does enhance the insulin-stimulated AKT (thr-308) phosphorylation. They need to clarify this issue.

Response: We have now analysed these data in a manner that preserves the control variance, consistent with the other figures in the manuscript and there is no significant change in Akt phosphorylation in ASAH over-expressing cells.

Author response image 6.

1. Figure S2: A functional assessment of mitochondrial function in HeLa cells would be helpful to validate the small effect of Saclac treatment on CI NDUFB8.

Response: Mitochondrial respiration was conducted in cells treated with Saclac (2 µM and 10 µM) for 24 hours. As shown below, in Hela cells, we did not detect any mitochondrial respiratory impairments at low doses, but only at high doses of Saclac. This suggests that the minor effect of Saclac on CI NDUFB8 is insufficient to alter mitochondrial function.

Author response image 7.

Reviewer #2 (Recommendations For The Authors):

Additional questions and comments for consideration:

1. The working model links ceramide-induced CoQ depletion to a reduction in ETC proteins and accompanying deficits in OxPhos capacity. The idea that mitochondrial dysfunction necessarily precedes and causes insulin resistance has been heavily debated for years because many animal and human studies have found no overt changes in ETC proteins and/or mitochondrial respiratory capacity during the early phases of insulin resistance. How do the investigators reconcile their work in the context of this controversy?

Response: We acknowledge this controversy in our revised manuscript more clearly now as follows on page 21: “We present evidence that mitochondrial dysfunction precedes insulin resistance. However, previous studies have failed to observe changes in mitochondrial morphology, respiration or ETC components during early stages of insulin resistance (72). However, in many cases such studies fail to document changes in insulin-dependent glucose metabolism in the same tissue as was used for assessment of mitochondrial function. This is crucial because we and others do not observe impaired insulin action in all muscles from high fat fed mice for example. In addition, surrogate measures such as insulin-stimulated Akt phosphorylation may not accurately reflect tissue specific insulin action as demonstrated in figure 1C. Thus, further work is required to clarify some of these inconsistencies''.

1. While the utility of targeting SMPD5 to the mitochondria is appreciated, the results in Figure 5 suggest that this manoeuvre caused a rather severe form of mitochondrial dysfunction. Is this representative of pathophysiology or toxicity?

Response: We believe we have addressed this in point 3 above (Principal comments, reviewer 1, point 3)

1. How did this affect other mitochondrial lipids (e.g. cardiolipin)?

Response: As shown in the supplementary figure 3, SMPD5 overexpression did not affect other lipids species such as cardiolipin (D-J). We have added to results:

“Importantly, mtSMPD5 overexpression did not affect ceramide abundance in the whole cell lysate nor other lipid species inside mitochondria such as cardiolipin, cholesterol and DAGs (Sup. Fig. 3 A, D-J)”

1. Are these severe effects rescued by CoQ supplementation?

Response: We have performed additional experiments to address this point. As shown below, mitochondrial ceramide accumulation induced by palmitate was not reversed by CoQ supplementation, as demonstrated in Figure 1F. We have added to results:

“Addition of CoQ9 had no effect on control cells but overcame insulin resistance in palmitate treated cells (Fig. 1A). Notably, the protective effect of CoQ9 appears to be downstream of ceramide accumulation, as it had no impact on palmitate-induced ceramide accumulation (Fig. 1E-F). Strikingly, both myriocin and CoQ9…”

Additionally, we assessed mitochondrial respiration by using SeaHorse in cells with SMPD5 overexpression treated with or without CoQ supplementation. Our results, depicted below, indicate that CoQ supplementation reversed the ceramide-induced decrease in basal and ATP linked mitochondrial respiration. We have modified Fig.5.

Author response image 8.

We have added to results:

“Respiration was assessed in intact mtSMPD5-L6 myotubes treated with CoQ9 by Seahorse extracellular flux analysis. mtSMPD5 overexpression decreased basal and ATP-linked mitochondrial respiration (Fig. 5 A, B &C), as well as maximal, proton-leak and non-mitochondrial respiration (Fig. 5 A, D, E & F) suggesting that mitochondrial ceramides induce a generalised attenuation in mitochondrial function. Interestingly, CoQ9 supplementation partially recovered basal and ATP-linked mitochondrial respiration, suggesting that part of the mitochondrial defects are induced by CoQ9 depletion. The attenuation in mitochondrial respiration is consistent with a depletion of the ETC subunits observed in our proteomic dataset (Fig. 4)...”

1. Are these same effects observed with other manipulations that lower CoQ to a similar degree?

Response: As mentioned in point 5 (additional suggestions from Reviewer 1), we conducted mitochondrial respiration measurements on HeLa cells treated with Saclac (2 µM and 10 µM) for 24 hours. Our findings showed no signs of mitochondrial respiratory impairments at low doses of Saclac in HeLa cells, despite observing CoQ depletion at this dose (Fig. Sup. 2C). We believe that this variation could be due to the varying sensitivity of mitochondrial respiration/ETC abundance to ceramide-induced CoQ depletion in different cell lines. Alternatively, it is possible that reduced mitochondrial respiration is a secondary event to other mitochondrial/cellular defects such as mitochondrial fragmentation or deficient nutrient transport inside mitochondria.

*Author response image 9.

1. The mitochondrial concentrations of CoQ required to maintain insulin sensitivity in L6 myocytes seem to vary from experiment to experiment. Is it the absolute concentration that matters and/or the change relative to a baseline condition?

Response: This is an excellent observation. The findings indicate that the absolute concentration of CoQ is the determining factor for insulin sensitivity, rather than the relative depletion of CoQ compared to basal conditions. We have added to discussion: “Finally, mtASAH1 overexpression increased CoQ levels. In both control and mtASAH1 cells, palmitate induced a depletion of CoQ, however the levels in palmitate treated mtASAH1 cells remained similar to control untreated cells (Fig. 3I). This suggests that the absolute concentration of CoQ is crucial for insulin sensitivity, rather than the relative depletion compared to basal conditions, thus supporting the causal role of mitochondrial ceramide accumulation in reducing CoQ levels in insulin resistance”

1. Considering that CoQ has been shown to have antioxidant properties, does the rescue observed after a 16 h treatment require the prolonged exposure, or alternatively, are similar effects observed during short-term exposures (~1-2 h), which might imply a different or additional mechanism.

Response: This is an excellent point that we have long considered. The problem is how to address the question in a way that will be definitive and we are concerned that the experiment suggested by the referee will not generate definitive data. A major issue is that CoQ has low solubility and needs to reach the right compartment. As such if short term treatment (as suggested) does not rescue, it would be difficult to make any definite conclusions as this might just be because insufficient CoQ is delivered to mitochondria. Conversely, if short term treatment does rescue this could be either because CoQ does get into mitochondria and regulate ETC or because of its general antioxidant function. So, even if we observe a rescue after 1 hour of incubation with CoQ, it will not clarify whether this is due to the antioxidant effect or simply because 1 hour is adequate to boost mitoCoQ levels. Thus, in our view this experiment might not get us any closer to the answer. Nevertheless, we do feel this is an important point and we have added the following statement to our revised manuscript to acknowledge this: “Because CoQ can accumulate in various intracellular compartments, it's important to consider that its impact on insulin resistance might be due to its overall antioxidant properties rather than being limited to a mitochondrial effect”

1. In Figure 1, CoQ depletion due to 4NB treatment resulted in increased ceramide levels. Could this be due to impaired palmitate oxidation leading to rerouting of intracellular palmitate to the ceramide pathway? This could be tested using stable isotope tracers.

Response: We have added the statement below to the manuscript to address this point. We feel that while an interesting experiment to perform it is somewhat outside of the major focus of this study.

“One possibility is that CoQ directly controls ceramide turnover (35). An alternate possibility is that CoQ inside mitochondria is necessary for fatty acid oxidation (12) and CoQ depletion triggers lipid overload in the cytoplasm promoting ceramide production (36). Future studies are required to determine how CoQ depletion promotes Cer accumulation. Regardless, these data indicate that ceramide and CoQ have a central role in regulating cellular insulin sensitivity.”

1. To a similar point, it would be helpful to know if the C2 ceramide analog is sufficient to cause elevated mito-ceramide and/or CoQ depletion. If not, the results might imply mitochondrial uptake of palmitate is required.

Response: We feel this point is analogous to Point 7 above in that this experiment is not definitive enough to make any clear conclusions as it may or may not work for many different reasons. For example, C2 ceramide may not work simply because it has the wrong chain length.

Moreover, it is clear that C2 ceramide has effects that clearly differ from those observed with palmitate most notably the inhibitory effect on Akt signalling. For these reasons we do not agree with the logic of this experiment.

We have mentioned in the results section:

“Based on these data we surmise that C2-ceramide does not faithfully recapitulate physiological insulin resistance, in contrast to that seen with incubation with palmitate”.

1. Likewise, does inhibition of CPT1 ameliorate or exacerbate palmitate-induced insulin resistance?

Response: This experiment has been performed by a number of different labs. For instance, muscle specific CPT1 overexpression is protective against high fat diet induced insulin resistance in mice (Bruce C, PMID19073774), CPT1 overexpression protects L6E9 muscle cells from fatty acid-induced insulin resistance (Sebastian D, PMID17062841) and increased beta-oxidation in muscle cells enhances insulin stimulated glucose metabolism and is protective against lipid induced insulin resistance (Perdomo G, PMID15105415). We have now cited all of these studies in our revised manuscript in the discussion: “In fact, increased fatty acid oxidation is protective against insulin resistance in several model organisms (37–39)”

1. Does the addition of palmitate to the cells treated with mtSMPD5 further reduce CoQ9 (Figure 2I and 2J)?

Response: This intriguing observation, as highlighted by the referee, has prompted us to conduct additional experiments to investigate the effects of palmitate and SMPD5 overexpression on Coenzyme Q (CoQ) levels in L6 myotubes. As demonstrated in the figures presented below, both palmitate and SMPD5 overexpression independently resulted in the depletion of CoQ9, with no observed additive effects suggesting that they shared a common pathway driving CoQ9 deficiency. One plausible hypothesis is that ceramides may trigger the depletion of a specific CoQ9 pool localised within the inner mitochondrial membrane, likely the pool associated with Complex I (CI) in the Electron Transport Chain (ETC). This hypothesis is supported by previous studies indicating that approximately ~25 - 35 % of CoQ binds to CI (PMID: 33722627) and our data demonstrating that ceramide induces a selective depletion of CI in L6 myotubes (Fig. 4).

We have added this result to Fig. 2I in the main section.

Author response image 10.

We have added to the result section:

“Mitochondrial CoQ levels were depleted in both palmitate-treated and mtSMPD5-overexpressing cells without any additive effects. This suggests that these strategies to increase ceramides share a common mechanism for inducing CoQ depletion in L6 myotubes (Fig. 2I).”

We have added to the discussion section:

“...These are known to form supercomplexes or respirasomes where ~25 - 35 % of CoQ is localised in mammals (58,16).…The observation that both palmitate and SMPD5 overexpression trigger CoQ depletion without additive effects support the notion that ceramides may trigger the depletion of a specific CoQ9 pool localised within the inner mitochondrial membrane.”

1. Some of the cell-based experiments appear to be underpowered and therefore confidence in the interpretations might benefit from additional repeats. For example, in Figure 3i, it appears that palmitate still causes a substantial reduction of CoQ in the cells treated with mtASAH1, even though mito-ceramide levels are restored to baseline. Please specify if these and other results are representative of multiple cell culture experiments or a single experiment.

Response: All data were derived from a minimum of 3-4 independent experiments from at least two separate cultures of L6 cells. Separate batches of drug treatments were prepared for each experiment. We have previously compared metabolic parameters between batches of cells differentiated at different times (i.e. at least weeks apart) in a previous study (Krycer PMID 31744882) and found variations of <20% for insulin-stimulated glucose oxidation. With an expected variance of 20% and a type I error rate of 0.05, this is sufficient to detect a 40% difference with a power of 0.8. As the reviewer has indicated this is likely underpowered in situations where variance is unexpectedly high or if a small difference needs to be detected.

In terms of Fig3, the reviewer raises an interesting point. As discussed in point 6, the fact that palmitate still appears to cause a depletion of CoQ in mtASAH1 cells likely indicates that the absolute concentration of CoQ is the determining factor for insulin sensitivity, rather than the relative depletion of CoQ compared to basal conditions. We have added to the discussion:

“Finally, mtASAH1 overexpression increased CoQ levels. In both control and mtASAH1 cells, palmitate induced a depletion of CoQ, but this effect was less pronounced in the mtASAH1 cell line (Fig. 3I). Our results suggest that the absolute concentration of CoQ is crucial for insulin sensitivity, rather than the relative depletion compared to basal conditions, thus supporting the causal role of mitochondrial ceramide accumulation in reducing CoQ levels in insulin resistance”

1. The color scheme of 2E is inconsistent with other panels in the figure.

Response: Corrected

1. It would be helpful if the axis labels for CoQ graphs were labeled as "Mito-CoQ" for clarity.

Response: Corrected

Author response:

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

Reviewer #1 (Public review):

Summary:

In this study, Ana Lapao et al. investigated the roles of Rab27 effector SYTL5 in cellular membrane trafficking pathways. The authors found that SYTL5 localizes to mitochondria in a Rab27A-dependent manner. They demonstrated that SYTL5-Rab27A positive vesicles containing mitochondrial material are formed under hypoxic conditions, thus they speculate that SYTL5 and Rab27A play roles in mitophagy. They also found that both SYTL5 and Rab27A are important for normal mitochondrial respiration. Cells lacking SYTL5 undergo a shift from mitochondrial oxygen consumption to glycolysis which is a common process known as the Warburg effect in cancer cells. Based on the cancer patient database, the author noticed that low SYTL5 expression is related to reduced survival for adrenocortical carcinoma patients, indicating SYTL5 could be a negative regulator of the Warburg effect and potentially tumorigenesis.

Strengths:

The authors take advantage of multiple techniques and novel methods to perform the experiments.

(1) Live-cell imaging revealed that stably inducible expression of SYTL5 co-localized with filamentous structures positive for mitochondria. This result was further confirmed by using correlative light and EM (CLEM) analysis and western blotting from purified mitochondrial fraction.

(2) In order to investigate whether SYTL5 and Rab27A are required for mitophagy in hypoxic conditions, two established mitophagy reporter U2OS cell lines were used to analyze the autophagic flux.

Weaknesses:

This study revealed a potential function of SYTL5 in mitophagy and mitochondrial metabolism. However, the mechanistic evidence that establishes the relationship between SYTL5/Rab27A and mitophagy is insufficient. The involvement of SYTL5 in ACC needs more investigation. Furthermore, images and results supporting the major conclusions need to be improved.

We thank the reviewer for their constructive comments. We agree that a complete understanding of the mechanism by which SYTL5 and Rab27A are recruited to the mitochondria and subsequently involved in mitophagy requires further investigation. Here, we have shown that SYTL5 recruitment to the mitochondria requires both its lipid-binding C2 domains and the Rab27A-binding SHD domain (Figure 1G-H). This implies a coincidence detection mechanism for mitochondrial localisation of SYTL5.  Additionally, we find that mitochondrial recruitment of SYTL5 is dependent on the GTPase activity and mitochondrial localisation of Rab27A (Figure 2D-E). We also identified proteins linked to the cellular response to oxidative stress, reactive oxygen species metabolic process, regulation of mitochondrion organisation and protein insertion into mitochondrial membrane to be enriched in the SYTL5 interactome (Figure 3A and C).

However, less details regarding the mitochondrial localisation of Rab27A are understood. To investigate this, we have now performed a mass spectrometry analysis to identify the interactome of Rab27A (see Author response table 1 below,). U2OS cells with stable expression of mScarlet-Rab27A or mScarlet only, were subjected to immunoprecipitation, followed by MS analysis.  Of the 32 significant Rab27A-interacting hits (compared to control), two of the hits are located in the inner mitochondrial membrane (IMM); ATP synthase F(1) complex subunit alpha (P25705), and mitochondrial very long-chain specific acyl-CoA dehydrogenase (VLCAD)(P49748). However, as these IMM proteins are not likely involved in mitochondrial recruitment of Rab27A, observed under basal conditions, we choose not to include these data in the manuscript. 

It is known that other RAB proteins are recruited to the mitochondria. During parkin-mediated mitophagy, RABGEF1 (a guanine nucleotide exchange factor) is recruited through its ubiquitin-binding domain and directs mitochondrial localisation of RAB5, which subsequently leads to recruitment of RAB7 by the MON1/CCZ1 complex[1]. As already mentioned in the discussion (p. 12), ubiquitination of the Rab27A GTPase activating protein alpha (TBC1D10A) is reduced in the brain of Parkin KO mouse compared to controls[35], suggesting a possible connection of Rab27A with regulatory mechanisms that are linked with mitochondrial damage and dysfunction. While this an interesting avenue to explore, in this paper we will not follow up further on the mechanism of mitochondrial recruitment of Rab27A. 

Author response table 1.

Rab27A interactome. Proteins co-immunoprecipitated with mScarlet-Rab27A vs mScarlet expressing control. The data show average of three replicates. 

To investigate the role of SYTL5 in the context of ACC, we acquired the NCI-H295R cell line isolated from the adrenal gland of an adrenal cancer patient. The cells were cultured as recommended from ATCC using DMEM/F-12 supplemented with NuSerum and ITS +premix. It is important to note that the H295R cells were adapted to grow as an adherent monolayer from the H295 cell line which grows in suspension. However, there can still be many viable H295R cells in the media. 

We attempted to conduct OCR and ECAR measurements using the Seahorse XF upon knockdown of SYTL5 and/or Rab27A in H295R cells. For these assays, it is essential that the cells be seeded in a monolayer at 70-90% confluency with no cell clusters[4]. Poor adhesion of the cells can cause inaccurate measurements by the analyser. Unfortunately, the results between the five replicates we carried out were highly inconsistent, the same knockdown produced trends in opposite directions in different replicates. This is likely due to problems with seeding the cells. Despite our best efforts to optimise seeding number, and pre-coating the plate with poly-D-lysine[5] we observed poor attachment of cells and inability to form a monolayer. 

To study the localisation of SYTL5 and Rab27A in an ACC model, we transduced the H295R cells with lentiviral particles to overexpress pLVX-SV40-mScarlet-I-Rab27A and pLVX-CMV-SYTL5-EGFP-3xFLAG. Again, this proved unsuccessful after numerous attempts at optimising transduction. 

These issues limited our investigation into the role of SYTL5 in ACC to the cortisol assay (Supplementary Figure 6). For this the H295R cells were an appropriate model as they are able to produce an array of adrenal cortex steroids[6] including cortisol[7]. In this assay, measurements are taken from cell culture supernatants, so the confluency of the cells does not prevent consistent results as the cortisol concentration was normalised to total protein per sample. With this assay we were able to rule out a role for SYTL5 and Rab27A in the secretion of cortisol.  

Another consideration when investigating the involvement of SYTL5 in ACC, is that in general ACC cells should have a low expression of SYTL5 as is seen from the patient expression data (Figure 6B).

The reviewer also writes “Furthermore, images and results supporting the major conclusions need to be improved.”. We have tried several times, without success, to generate U2OS cells with CRISPR/Cas9-mediated C-terminal tagging of endogenous SYTL5 with mNeonGreen, using an approach that has been successfully implemented in the lab for other genes. This is likely due to a lack of suitable sgRNAs targeting the C-terminal region of SYTL5, which have a low predicted efficiency score and a large number of predicted off-target sites in the human genome including several other gene exons and introns (see Author response image 2). 

We have also included new data (Supplementary Figure 4B) showing that some of the hypoxia-induced SYTL5-Rab27A-positive vesicles stain positive for the autophagy markers p62 and LC3B when inhibiting lysosomal degradation, further strengthening our data that SYTL5 and Rab27A function as positive regulators of mitophagy.  

Reviewer #2 (Public review): 

Summary:

The authors provide convincing evidence that Rab27 and STYL5 work together to regulate mitochondrial activity and homeostasis.

Strengths:

The development of models that allow the function to be dissected, and the rigorous approach and testing of mitochondrial activity.

Weaknesses:

There may be unknown redundancies in both pathways in which Rab27 and SYTL5 are working which could confound the interpretation of the results.

Suggestions for revision:

Given that Rab27A and SYTL5 are members of protein families it would be important to exclude any possible functional redundancies coming from Rab27B expression or one of the other SYTL family members. For Rab27 this would be straightforward to test in the assays shown in Figure 4 and Supplementary Figure 5. For SYTL5 it might be sufficient to include some discussion about this possibility.

We thank the reviewer for pointing out the potential redundancy issue for Rab27A and SYTL5. There are multiple studies demonstrating the redundancy between Rab27A and Rab27B. For example, in a study of the disease Griscelli syndrome, caused by Rab27A loss of function, expression of either Rab27A or Rab27B rescues the healthy phenotype indicating redundancy[8]. This redundancy however applies to certain function and cell types. In fact, in a study regarding hair growth, knockdown of Rab27B had the opposite effect to knockdown of Rab27A[9].

In this paper, we conducted all assays in U2OS cells, in which the expression of Rab27B is very low. Human Protein Atlas reports expression of 0.5nTPM for Rab27B, compared to 18.4nTPM for Rab27A. We also observed this low level of expression of Rab27B compared to Rab27A by qPCR in U2OS cells. Therefore, there would be very little endogenous Rab27B expression in cells depleted of Rab27A (with siRNA or KO). In line with this, Rab27B peptides were not detected in our SYTL5 interactome MS data (Table 1 in paper). Moreover, as Rab27A depletion inhibits mitochondrial recruitment of SYTL5 and mitophagy, it is not likely that Rab27B provides a functional redundancy. It is possible that Rab27B overexpression could rescue mitochondrial localisation of SYTL5 in Rab27A KO cells, but this was not tested as we do not have any evidence for a role of Rab27B in these cells. Taken together, we believe our data imply that Rab27B is very unlikely to provide any functional redundancy to Rab27A in our experiments. 

For the SYTL family, all five members are Rab27 effectors, binding to Rab27 through their SHD domain. Together with Rab27, all SYTL’s have been implicated in exocytosis in different cell types. For example, SYTL1 in exocytosis of azurophilic granules from neutrophils[10], SYTL2 in secretion of glucagon granules from pancreatic α cells[11], SYTL3 in secretion of lytic granules from cytotoxic T lymphocytes[12], SYTL4 in exocytosis of dense hormone containing granules from endocrine cells[13] and SYTL5 in secretion of the RANKL cytokine from osteoblasts[14]. This indicates a potential for redundancy through their binding to Rab27 and function in vesicle secretion/trafficking. However, one study found that different Rab27 effectors have distinct functions at different stages of exocytosis[15].

Very little known about redundancy or hierarchy between these proteins. Differences in function may be due to the variation in gene expression profile across tissues for the different SYTL’s (see Author response image 1 below). SYTL5 is enriched in the brain unlike the others, suggesting possible tissue specific functions. There are also differences in the binding affinities and calcium sensitivities of the C2iA and C2B domains between the SYTL proteins[16].

Author response image 1.

GTEx Multi Gene Query for SYTL1-5

All five SYTL’s are expressed in the U2OS cell line with nTPMs according to Human Protein Atlas of SYTL1: 7.5, SYTL2: 13.4, SYTL3:14.2, SYTL4: 8.7, SYTL5: 4.8. In line with this, in the Rab27A interactome, when comparing cells overexpressing mScarlet-Rab27A with control cells, we detected all five SYTL’s as specific Rab27A-interacting proteins (see Author response table 1 above). Whereas, in the SYTL5 interactome we did not detect any other SYTL protein (table 1 in paper), confirming that they do not form a complex with SYTL5. 

We have included the following text in the discussion (p. 12): “SYTL5 and Rab27A are both members of protein families, suggesting possible functional redundancies from Rab27B or one of the other SYTL isoforms. While Rab27B has a very low expression in U2OS cells, all five SYTL’s are expressed. However, when knocking out or knocking down SYTL5 and Rab27A we observe significant effects that we presume would be negated if their isoforms were providing functional redundancies. Moreover, we did not detect any other SYTL protein or Rab27B in the SYTL5 interactome, confirming that they do not form a complex with SYTL5.”

Suggestions for Discussion: 

Both Rab27A and STYL5 localize to other membranes, including the endolysosomal compartments. How do the authors envisage the mechanism or cellular modifications that allow these proteins, either individually or in complex to function also to regulate mitochondrial funcYon? It would be interesYng to have some views.

We agree that it would be interesting to better understand the mechanism involved in modulation of the localisation and function of SYTL5 and Rab27A at different cellular compartments, including the mitochondria. Here, we have shown that SYTL5 recruitment to the mitochondria involves coincidence detection, as both its lipid-binding C2 domains and the Rab27A-binding SHD domain are required (Figure 1G-H). Both these domains also seem required for localisation of SYTL5 to vesicles, and we can only speculate that binding to different lipids (Figure 1F) may regulate SYTL5 localisation. Additionally, we find that mitochondrial recruitment of SYTL5 is dependent on the GTPase activity and mitochondrial localisation of Rab27A (Figure 2D-E). However, this seems also the case for vesicular recruitment of SYTL5, although a few SYTL5-Rab27A (T23N) positive vesicles were seen (Figure 2E). 

To characterise the mechanisms involved in mitochondrial localisation of Rab27A, we have performed mass spectrometry analysis to identify the interactome of Rab27A (see Author response table 1 above). U2OS cells with stable expression of mScarlet-Rab27A or mScarlet only were subjected to immunoprecipitation, followed by MS analysis.  Of the 32 significant Rab27A-interacting hits (compared to control), two of the hits localise in the inner mitochondrial membrane (IMM); ATP synthase F(1) complex subunit alpha (P25705), and mitochondrial very long-chain specific acyl-CoA dehydrogenase (VLCAD)(P49748). However, as these IMM proteins are not likely involved in mitochondrial recruitment of Rab27A, observed under basal conditions, we chose not to include these data in the manuscript. 

It is known that other RAB proteins are recruited to the mitochondria by regulation of their GTPase activity. During parkin-mediated mitophagy, RABGEF1 (a guanine nucleotide exchange factor) is recruited through its ubiquitin-binding domain and directs mitochondrial localisation of RAB5, which subsequently leads to recruitment of RAB7 by the MON1/CCZ1 GEF complex[1]. As already mentioned in the discussion (p.12), ubiquitination of the Rab27A GTPase activating protein alpha (TBC1D10A) is reduced in the brain of Parkin KO mouse compared to controls[35], suggesting a possible connection of Rab27A with regulatory mechanisms that are linked with mitochondrial damage and dysfunction. While this an interesting avenue to explore, it is beyond the scope of this paper. 

Our data suggest that SYTL5 functions as a negative regulator of the Warburg effect, the switch from OXPHOS to glycolysis. While both SYTL5 and Rab27A seem required for mitophagy of selective mitochondrial components, and their depletion leading to reduced mitochondrial respiration and ATP production, only depletion of SYTL5 caused a switch to glycolysis. The mechanisms involved are unclear, but we found several proteins linked to the cellular response to oxidative stress, reactive oxygen species metabolic process, regulation of mitochondrion organisation and protein insertion into mitochondrial membrane to be enriched in the SYTL5 interactome (Figure 3A and C).

We have addressed this comment in the discussion on p.12 

Reviewer #3 (Public review):

Summary:

In the manuscript by Lapao et al., the authors uncover a role for the Rab27A effector protein SYTL5 in regulating mitochondrial function and turnover. The authors find that SYTL5 localizes to mitochondria in a Rab27A-dependent way and that loss of SYTL5 (or Rab27A) impairs lysosomal turnover of an inner mitochondrial membrane mitophagy reporter but not a matrix-based one. As the authors see no co-localization of GFP/mScarlet tagged versions of SYTL5 or Rab27A with LC3 or p62, they propose that lysosomal turnover is independent of the conventional autophagy machinery. Finally, the authors go on to show that loss of SYTL5 impacts mitochondrial respiration and ECAR and as such may influence the Warburg effect and tumorigenesis. Of relevance here, the authors go on to show that SYTL5 expression is reduced in adrenocortical carcinomas and this correlates with reduced survival rates.

Strengths:

There are clearly interesting and new findings here that will be relevant to those following mitochondrial function, the endocytic pathway, and cancer metabolism.

Weaknesses:

The data feel somewhat preliminary in that the conclusions rely on exogenously expressed proteins and reporters, which do not always align.

As the authors note there are no commercially available antibodies that recognize endogenous SYTL5, hence they have had to stably express GFP-tagged versions. However, it appears that the level of expression dictates co-localization from the examples the authors give (though it is hard to tell as there is a lack of any kind of quantitation for all the fluorescent figures). Therefore, the authors may wish to generate an antibody themselves or tag the endogenous protein using CRISPR.

We agree that the level of SYTL5 expression is likely to affect its localisation. As suggested by the reviewer, we have tried hard, without success, to generated U2OS cells with CRISPR knock-in of a mNeonGreen tag at the C-terminus of endogenous SYTL5, using an approach that has been successfully implemented in the lab for other genes. This is likely due to a lack of suitable sgRNAs targeting the C-terminal region of SYTL5, which have a low predicted efficiency score and a large number of predicted off-target sites in the human genome including several other gene exons and introns (see Author response image 2). 

Author response image 2.

Overview of sgRNAs targeting the C-terminal region of SYTL5 

Although the SYTL5 expression level might affect its cellular localization, we also found the mitochondrial localisation of SYTL5-EGFP to be strongly increased in cells co-expressing mScarletRab27A, supporting our findings of Rab27A-mediated mitochondrial recruitment of SYTL5. We have also included new data (Supplementary Figure 4B) showing that some of the hypoxia-induced SYTL5Rab27A-positive vesicles stain positive for the autophagy markers p62 and LC3B when inhibiting lysosomal degradation, further strengthening our data that SYTL5 and Rab27A function as positive regulators of mitophagy.  

In relation to quantitation, the authors found that SYTL5 localizes to multiple compartments or potentially a few compartments that are positive for multiple markers. Some quantitation here would be very useful as it might inform on function. 

We find that SYTL5-EGFP localizes to mitochondria, lysosomes and the plasma membrane in U2OS cells with stable expression of SYTL5-EGFP and in SYTL5/Rab27A double knock-out cells rescued with SYTL5EGFP and mScralet-Rab27A. We also see colocalization of SYTL5-EGFP with endogenous p62, LC3 and LAMP1 upon induction of mitophagy. However, as these cell lines comprise a heterogenous pool with high variability we do not believe that quantification of the overexpressing cell lines would provide beneficial information in this scenario. As described above, we have tried several times to generate SYTL5 knock-in cells without success.  

The authors find that upon hypoxia/hypoxia-like conditions that punctate structures of SYTL5 and Rab27A form that are positive for Mitotracker, and that a very specific mitophagy assay based on pSu9-Halo system is impaired by siRNA of SYTL5/Rab27A, but another, distinct mitophagy assay (Matrix EGFP-mCherry) shows no change. I think this work would strongly benefit from some measurements with endogenous mitochondrial proteins, both via immunofluorescence and western blot-based flux assays. 

In addition to the western blotting for different endogenous ETC proteins showing significantly increased levels of MTCO1 in cells depleted of SYTL5 and/or Rab27A (Figure 5E-F), we have now blotted for the endogenous mitochondrial proteins, COXIV and BNIP3L, in DFP and DMOG conditions upon knockdown of SYTL5 and/or Rab27A (Figure 5G and Supplementary Figure 5A). Although there was a trend towards increased levels, we did not see any significant changes in total COXIV or BNIP3L levels when SYTL5, Rab27A or both are knocked down compared to siControl. Blotting for endogenous mitochondrial proteins is however not the optimum readout for mitophagy. A change in mitochondrial protein level does not necessarily result from mitophagy, as other factors such as mitochondrial biogenesis and changes in translation can also have an effect. Mitophagy is a dynamic process, which is why we utilise assays such as the HaloTag and mCherry-EGFP double tag as these indicate flux in the pathway. Additionally, as mitochondrial proteins have different half-lives, with many long-lived mitochondrial proteins[17], differences in turnover rates of endogenous proteins make the results more difficult to interpret. 

A really interesting aspect is the apparent independence of this mitophagy pathway on the conventional autophagy machinery. However, this is only based on a lack of co-localization between p62or LC3 with LAMP1 and GFP/mScarlet tagged SYTL5/Rab27A. However, I would not expect them to greatly colocalize in lysosomes as both the p62 and LC3 will become rapidly degraded, while the eGFP and mScarlet tags are relatively resistant to lysosomal hydrolysis. -/+ a lysosome inhibitor might help here and ideally, the functional mitophagy assays should be repeated in autophagy KOs. 

We thank the reviewer for this suggestion. We have now repeated the colocalisation studies in cells treated with DFP with the addition of bafilomycin A1 (BafA1) to inhibit the lysosomal V-ATPase. Indeed, we find that a few of the SYTL5/Rab27A/MitoTracker positive structures also stain positive for p62 and LC3 (Supplementary Figure 4B). As expected, the occurrence of these structures was rare, as BafA1 was only added for the last 4 hrs of the 24 hr DFP treatment. However, we cannot exclude the possibility that there are two different populations of these vesicles.

The link to tumorigenesis and cancer survival is very interesYng but it is not clear if this is due to the mitochondrially-related aspects of SYTL5 and Rab27A. For example, increased ECAR is seen in the SYTL5 KO cells but not in the Rab27A KO cells (Fig.5D), implying that mitochondrial localization of SYTL5 is not required for the ECAR effect. More work to strengthen the link between the two sections in the paper would help with future direcYons and impact with respect to future cancer treatment avenues to explore. 

We agree that the role of SYTL5 in ACC requires future investigation. While we observe reduced OXPHOS levels in both SYTL5 and Rab27A KO cells (Figure 5B), glycolysis was only increased in SYTL5 KO cells (Figure 5D). We believe this indicates that Rab27A is being negatively regulated by SYTL5, as ECAR was unchanged in both the Rab27A KO and Rab27A/SYTL5 dKO cells. This suggests that Rab27A is required for the increase in ECAR when SYTL5 is depleted, therefore SYTL5 negatively regulates Rab27A. The mechanism involved is unclear, but we found several proteins linked to the cellular response to oxidative stress, reactive oxygen species metabolic process, regulation of mitochondrion organisation and protein insertion into mitochondrial membrane to be enriched in the SYTL5 interactome (Figure 3A and C).

To investigate the link to cancer further, we tested the effect of knockdown of SYTL5 and/or Rab27A on the levels of mitochondrial ROS. ROS levels were measured by flow cytometry using the MitoSOX Red dye, together with the MitoTracker Green dye to normalise ROS levels to the total mitochondria. Cells were treated with the antioxidant N-acetylcysteine (NAC)[18] as a negative control and menadione as a positive control, as menadione induces ROS production via redox cycling[19]. We must consider that there is also a lot of autofluorescence from cells that makes it impossible to get a level of ‘zero ROS’ in this experiment. We did not see a change in ROS with knockdown of SYTL5 and/or Rab27A compared to the NAC treated or siControl samples (see Author response image 3 below). The menadione samples confirm the success of the experiment as ROS accumulated in these cells. Thus, based on this, we do not believe that low SYTL5 expression would affect ROS levels in ACC tumours.

Author response image 3.

Mitochondrial ROS production normalised to total mitochondria

As discussed in our response to Reviewer #1, we tried hard to characterise the role of SYTL5 in the context of ACC using the NCI-H295R cell line isolated from the adrenal gland of an adrenal cancer patient. We attempted to conduct OCR and ECAR measurements using the Seahorse XF upon knockdown of SYTL5 and/or Rab27A in H295R cells without success, due to poor attachment of the cells and inability to form a monolayer. We also transduced the H295R cells with lentiviral particles to overexpress pLVX-SV40-mScarlet-I-Rab27A and pLVX-CMV-SYTL5-EGFP-3xFLAG to study the localisation of SYTL5 and Rab27A in an ACC model. Again, this proved unsuccessful after numerous attempts at optimising the transduction. These issues limited our investigation into the role of SYTL5 in ACC to the cortisol assay (Supplementary Figure 6). For this the H295R cells were an appropriate model as they are able to produce an array of adrenal cortex steroids[6] including cortisol[7] In this assay, measurements are taken from cell culture supernatants, so the confluency of the cells does not prevent consistent results as the cortisol concentration was normalised to total protein per sample. With this assay we were able to rule out a role for SYTL5 and Rab27A in the secretion of cortisol.  

Another consideration when investigating the involvement of SYTL5 in ACC, is that in general ACC cells should have a low expression of SYTL5 as is seen from the patient expression data (Figure 6B).

Further studies into the link between SYTL5/Rab27A and cancer are beyond the scope of this paper as we are limited to the tools and expertise available in the lab.

References

(1) Yamano, K. et al. Endosomal Rab cycles regulate Parkin-mediated mitophagy. eLife 7 (2018). https://doi.org:10.7554/eLife.31326

(2) Carré, M. et al. Tubulin is an inherent component of mitochondrial membranes that interacts with the voltage-dependent anion channel. The Journal of biological chemistry 277, 33664-33669 (2002). https://doi.org:10.1074/jbc.M203834200

(3) Hoogerheide, D. P. et al. Structural features and lipid binding domain of tubulin on biomimetic mitochondrial membranes. Proceedings of the National Academy of Sciences 114, E3622-E3631 (2017). https://doi.org:10.1073/pnas.1619806114

(4) Plitzko, B. & Loesgen, S. Measurement of Oxygen Consumption Rate (OCR) and Extracellular Acidification Rate (ECAR) in Culture Cells for Assessment of the Energy Metabolism. Bio Protoc 8, e2850 (2018). https://doi.org:10.21769/BioProtoc2850

(5) Yavin, E. & Yavin, Z. Attachment and culture of dissociated cells from rat embryo cerebral hemispheres on polylysine-coated surface. The Journal of cell biology 62, 540-546 (1974). https://doi.org:10.1083/jcb.62.2.540

(6) Wang, T. & Rainey, W. E. Human adrenocortical carcinoma cell lines. Mol Cell Endocrinol 351, 5865 (2012). https://doi.org:10.1016/j.mce.2011.08.041

(7) Rainey, W. E. et al. Regulation of human adrenal carcinoma cell (NCI-H295) production of C19 steroids. J Clin Endocrinol Metab 77, 731-737 (1993). https://doi.org:10.1210/jcem.77.3.8396576

(8) Barral, D. C. et al. Functional redundancy of Rab27 proteins and the pathogenesis of Griscelli syndrome. J. Clin. Invest. 110, 247-257 (2002). https://doi.org:10.1172/jci15058

(9) Ku, K. E., Choi, N. & Sung, J. H. Inhibition of Rab27a and Rab27b Has Opposite Effects on the Regulation of Hair Cycle and Hair Growth. Int. J. Mol. Sci. 21 (2020). https://doi.org:10.3390/ijms21165672

(10) Johnson, J. L., Monfregola, J., Napolitano, G., Kiosses, W. B. & Catz, S. D. Vesicular trafficking through cortical actin during exocytosis is regulated by the Rab27a effector JFC1/Slp1 and the RhoA-GTPase–activating protein Gem-interacting protein. Mol. Biol. Cell 23, 1902-1916 (2012). https://doi.org:10.1091/mbc.e11-12-1001

(11) Yu, M. et al. Exophilin4/Slp2-a targets glucagon granules to the plasma membrane through unique Ca2+-inhibitory phospholipid-binding activity of the C2A domain. Mol. Biol. Cell 18, 688696 (2007). https://doi.org:10.1091/mbc.e06-10-0914

(12) Kurowska, M. et al. Terminal transport of lyXc granules to the immune synapse is mediated by the kinesin-1/Slp3/Rab27a complex. Blood 119, 3879-3889 (2012). https://doi.org:10.1182/blood-2011-09-382556

(13) Zhao, S., Torii, S., Yokota-Hashimoto, H., Takeuchi, T. & Izumi, T. Involvement of Rab27b in the regulated secretion of pituitary hormones. Endocrinology 143, 1817-1824 (2002). https://doi.org:10.1210/endo.143.5.8823

(14) Kariya, Y. et al. Rab27a and Rab27b are involved in stimulation-dependent RANKL release from secretory lysosomes in osteoblastic cells. J Bone Miner Res 26, 689-703 (2011). https://doi.org:10.1002/jbmr.268

(15) Zhao, K. et al. Functional hierarchy among different Rab27 effectors involved in secretory granule exocytosis. Elife 12 (2023). https://doi.org:10.7554/eLife.82821

(16) Izumi, T. Physiological roles of Rab27 effectors in regulated exocytosis. Endocr J 54, 649-657 (2007). https://doi.org:10.1507/endocrj.kr-78

(17) Bomba-Warczak, E. & Savas, J. N. Long-lived mitochondrial proteins and why they exist. Trends in cell biology 32, 646-654 (2022). https://doi.org:10.1016/j.tcb.2022.02.001

(18) Curtin, J. F., Donovan, M. & Cotter, T. G. Regulation and measurement of oxidative stress in apoptosis. Journal of Immunological Methods 265, 49-72 (2002). https://doi.org:https://doi.org/10.1016/S0022-1759(02)00070-4

(19) Criddle, D. N. et al. Menadione-induced Reative Oxygen Species Generation via Redox Cycling Promotes Apoptosis of Murine Pancreatic Acinar Cells. Journal of Biological Chemistry 281, 40485-40492 (2006). https://doi.org:https://doi.org/10.1074/jbc.M607704200

Author response:

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

We would like to thank you and the two Reviewers for the thoughtful evaluation of the manuscript and the support for publication. We have addressed all points raised by the two Reviewers.

- We have extensively streamlined the manuscript. Repetitive passages regarding the respective kinase cascades have been removed.

- We improved the presentation of the main Figures (mainly labeling and font size):

- Figure 1: C, D, E, F o Figure 2: C, E, F, G, I, o Figure 3: D o Figure 4: F

- Figure 5: A, B, C, D, E

- We integrated new SI-data related to kinase functions, expression and the ‘cell-type comparisons’ of the KinCon reporter system (Figure Supplement 4, 5).

Below you will find a detailed point-by-point response.

Reviewer #1 (Recommendations For The Authors):

Regarding the issue of the use of the word "dynamics," as described in the public review, here are a few examples of ambiguous use in different sentences: o Line 27: dynamics of full-length protein kinases. Is this referring to the dynamics of conformational interconversion between inactive and active states?

- Line 138: dynamic functioning of kinases. It is not clear what this means. o Line 276: ... alters KinCon dynamics. Not clear if they are measuring time-dependent process or a single point. 

- Figure legend 4F: dynamics of CDK4/6 reporters. Again, not clear how the assay is measuring dynamics.

In my opinion, the authors use proper terminology that describes their assay in which the term dynamics is not used: Title: "... impact of protein and small molecule interactions on kinase conformations" and Line 89 "... reporter can be used to track conformational changes of kinases...".

We have replaced the “dynamics” sections. 

- Line 27: The understanding of the structural dynamics of…

- Line 91: This reporter can be used to track dynamic changes of kinases conformations…

- Line 139: Conventional methods often fall short in capturing the dynamics of kinases within their native cellular environments…

- Line 146: Such insights into the molecular structure dynamics of kinases in intact cells…

- Line 199: In order to enhance our understanding of kinase structure dynamics…

- Line 276: These findings underline that indeed the trimeric complex formation alters….

- Figure Legend 4F: Quantification of alterations of CDK4/6 KinCon reporter bioluminescence signals…

The authors state that KinCon has predictive capabilities (abstract and line 142). What do  the authors mean by this?

Previously we have benchmarked the suitability of the KinCon reporter for target engagement assays of wt and mutated kinase activities. With this we determined specificities of melanoma drugs for mutated BRAF variants (Mayrhofer 2020, PNAS). 

The authors indicate that KinCon is a highly sensitive assay. Can the authors elaborate on what high sensitivity means?  

With sensitivity we mean that we can detect conformation dynamics of the reporter at low expression levels of the hybrid protein expressed in the cell line of choice.

- Line 209: Immunoblotting of cell lysates following luminescence measurements showed expression levels of the reporters in the range and below the endogenous expressed kinases (Figure 1E).  …

- Line 219:   Using this readout, we showed that at expression levels of the BRAF KinCon reporter below the immunoblotting detection limit, one hour of drug exposure exclusively converted BRAF-V600E to the more closed conformation (Figure 1F, G, Figure Supplement 1B). 

- Line 221: These data underline that at expression levels far below the endogenous kinase, protein activity conformations can be tracked in intact cells. …

For example, can they discuss how other fluorescence-based approaches that are less sensitive would not be able to accomplish the same type of results or derive similar conclusions? Can they provide a resolution metric both in space and time? Given that the authors state that this is a technical report, this information is of relevance.

We highlight the key pros & cons of the KinCon reporter technology in following sections:

-Line 529: The KinCon technology, introduced here, seeks to address the previously mentioned challenges. It has the potential to become a valuable asset for tracking kinase functions in living cells which are hard to measure solely via phosphotransferase activities. Overall, it offers an innovative solution for understanding kinase activity conformations, which could pave the way for more novel intervention strategies for kinase entities with limited pharmaceutical targeting potential. So far, this relates to the tracking of kinase-scaffold and pseudo-kinase functions.

- Line 535: Key advantages of the KinCon reporter technology is the robustness of the system to track kinase conformations at varying expression levels. However, in contrast to fluorescence-based reporter read-outs subcellular analysis and cell sorting are still challenging due to comparable low levels of light emission

The authors nicely describe how KinCon works in Figure 1B and part of 1C. I do think that the bottom of panel 1C needs to be revised, as well as the text describing the potential scenarios of potency, efficacy, and synergism.

One issue with this part of Figure 1C is that it is not clear what the x-axis in the 3 plots refers to. Is this time? Is this concentration of a small molecule, inhibitor, or binding partner? This was confusing also in the context of the term dynamics used throughout the text. The terms potency, efficacy, and synergism should be subtitles, or the panels and the x-axis should be better defined, especially for a non-specialized reader.

Related to this part of Figure 1C is the text. The authors mention potency, effectiveness, and synergy (Line 195). Can the authors use more fundamental terminology related to these three scenarios, for example, changes in activation constant, and percent of protein activates? Also, why synergy is only related to effectiveness? Can synergy also be associated with potency?

Thank you for bringing this up, we have revised Figure 1C to better reflect the mentioned effects of potency. To avoid confusion, we removed the illustration for drug synergism. Accordingly, we have integrated the axis descriptions for the presented dose-response curves.   

Thus, we have further streamlined the text in the introduction – examples are shown below:

- Line 195: Light recordings and subsequent calculations of time-dependent dosage variations of bioluminescence signatures of parallel implemented KinCon configurations aid in establishing dose-response curves. These curves are used for discerning pharmacological characteristics such as drug potency, effectiveness of drug candidates, and potential drug synergies (Figure 1C)

- Figure 1C:  Shown is the workflow for the KinCon reporter construct engineering and analyses using KinCon technology. The kinase gene of interest is inserted into the multiple cloning site of a mammalian expression vector which is flanked by respective PCA fragments (-F[1], -F[2]) and separated with interjacent flexible linkers. Expression of the genetically encoded reporter in indicated multi-well formats allows to vary expression levels and define a coherent drug treatment plan. Moreover, it is possible to alter the kinase sequence (mutations) or to co-express or knock-down the respective endogenous kinase, interlinked kinases or proteinogenic regulators of the respective pathway. After systematic administration of pathway modulating drugs or drug candidates, analyses of KinCon structure dynamics may reveal alterations in potency, efficacy, and potential synergistic effects of the tested bioactive small molecules (schematic dose response curves are depicted)

Lastly, the use of these three cartoons gives the impression that the experimental results to come will follow a similar representation. Instead, the results are presented in bar plots for many different conditions. I think this will lead to confusion for a broad audience.

The bottom panel of Figure 1C is not the depiction of real experiments but rather an illustration of fitted dose-response curves. We would like to present previous demonstrations of doseresponse curves using BRAF KinCon data and ERK phosphorylation (Röck 2019, Sci. Advances) 

We further agree with the reviewer and have therefore added a new part in the methods section addressing the evaluation of data extensively. 

- Line 668: In Figure 1 E and F, a representative experiment of n=4 independent experiments is shown. In these cases, absolute bioluminescence values without any normalization are shown. Otherwise, data was indicated as RLU (relative light unit) fold change. This means the data was normalized on the indicated control condition (either with normalization of the western blot or without; as indicated.

For a non-expert reader, can the authors clarify the use of tracking basal conformations vs. transient over-expression of the various KinCon constructs? Moreover, the authors use the term transient over-expression for 10, 16, 24, and 48 h (Line 203). This, to a non-expert reader, does not seem transient.

We have revised the manuscript to clarify it:

- Line 207: We showed that transient over-expression of these KinCon reporters for a time frame of 10h, 16h, 24h or 48h in HEK293T cells delivers consistently increasing signals for all KinCon reporters (Figure 1E, Figure Supplement 1A). 

- Figure 1E) Representative KinCon experiments of time-dependent expressions of indicated KinCon reporter constructs in HEK293T cells are shown (mean ±SEM). Indicated KinCon reporters were transiently over-expressed in 24-well format in HEK293T cells for 10h, 16h, 24h and 48h each.

Regarding Figure 1E and similar graphical representations: Why is the signal (RLU) nonlinear with time? If the fluorescence of the KinCon construct is linearly related to its expression or concentration inside the cell, one would expect a linear increase. Have the authors plotted RLU/Expression band intensity to account for changes in protein concentration? For instance, some of the results within Figure 3 are normalized to concentration on reporter expression level.

Out intention was to show that varying expression levels can be used for the illustrated target engagement assays.Indeed, the represented elevations of RLU might be  due to factors such as: 

- Doubling times of cells

- Cell density

- Media composition (which changes over time)

- Reporter protein stabilities

- Abundance of interactors of kinases

For the results with LKB1, the authors claim that intermediate fold change in fluorescence (Figure 2E) is due to a partially closed intermediate state (Line 262). Can the authors discard the possibility by which there is a change in populations of active and inactive that on average give intermediate values?

Based on our experience with KinCon reporter conformation states of kinases we tested so far, we assume that the presented data reflects an intermediate state. We agree that it needs further validation. We have changed the text accordingly:

- Line 264: Upon interaction with LKB1 this conformation shifts to a partially closed intermediate state.

The authors claim in Line 274 that mutations located at the interface of the LKB1/STRADalpha complex affect interactions and hypothesize that allosteric communication between LKB1 and STRADalpha is essential for function. Given that these mutations are at the interaction interface, why would the authors postulate an allosteric mechanism that evokes an effect distant from the interaction/active site? Could it be that function requires surface contacts alone that are disrupted by the mutations?

We agree with the reviewer and changed our argumentation for this point:

- Line 276: These findings underline that indeed the trimeric complex formation alters the opening and closing of the tested full-length kinase structures using the applied KinCon reporter read out

I was unable to find text to explain the following: Figure 2I shows the mutation R74A as n.s., but in the text, only W308C is mentioned to not change fluorescence. Could the authors clarify why R74A is not discussed in the text?  Maybe this reviewer missed the text in which it was discussed.

We adapted the manuscript and include the R74A mutation as followed:

- Line 296: Among these mutations, only the W308C and R74A mutation prevented significant closing of the LKB1 conformation when co-expressed with STRAD𝛼 and MO25 (Figure 2I).

In Figure 2I where the individual measurements of the LKB1-R74A KinCon are highlighted in red to better emphasize the deviations. In the case of the R74A mutation the effect seen might be due to the high deviation between the experiments (Highlighted in red). These deviations are much higher when compared to either the wt or the W308 mutant, and can also be seen in the LKB1-R74A-KinCon only condition (white). Even though no significant closing of the LKB1 conformation could be observed in the case of R74A, we believe, since the trend of the conformation closing upon complex formation is still visible that the effect is still there. Further replicates would be necessary to validate this theory. 

Similarly, the authors state in line 326 that the study included an analysis of RIPK2. However, I was unable to find results, graphs, or additional text discussing RIPK2.

The RIPK2 conformation was analyzed in Figure 3C (page 12).

Some figures of RLU use absolute values, percentages, and fold change. Is there are reason why the authors use different Y-axis values? These should be explained and justified in Methods. Similarly, bars for wt in Figures 3D, G, or 4D, E, F show no errors. How are the authors normalizing the data and repeats so that there is no error, and are they treating the rest of the data (i.e., mutants and/or treated with small molecules) in the same way?

We have changed the Y-axis values. Now, throughout the manuscript we show that there is a RLU fold-change. Except are selected experiments when solely absolute RLU values are shown (such as Figure 1E, F). We have also decided to integrate a paragraph into the methods section (Line 655). Figure 3D was changed as well.

- Line 668: In Figure 1 E and F, a representative experiment of n=4 independent experiments is shown.  In these cases absolute bioluminescence values without any normalisation are shown.  Otherwise, data was indicated as RLU fold change. This means the data was normalized on the indicated control condition (either with normalization of the western blot or without; as indicated).

The data is generally normalized on wt or untreated conditions, when the cells were treated with small molecules for target engagement assays. 

Lastly, the section starting in Line 472 reads more like a discussion of results from different types of inhibitors used in this study that results on its own. The authors should consider a new subtitle such as results or make this section a discussion.

We agree with the reviewer and this part of the results was split into a new section of the result:

- Line 455: “Effect of different kinase inhibitor types on the KinCon reporter system”.

Reviewer #2 (Recommendations For The Authors):

I have a few suggestions, since the paper is a distillation of a vast amount of work and tells a useful story.

(1) The work is very solid, uses examples from the literature, and also extends into new experimental space. An obvious weakness is mentioned by the authors for the CKD data, in that measurements with Cyclin D (the activating subunit) are not characterized, although Cyclin D might be assumed to be present. 

We performed experiments with the CDK4/6 KinCon reporters and co-expressed CyclinD with a ratio of 1:3 (HEK293T cells, expression for 48h). However, in the context of inhibitor treatments we could not track conformation changes in these initial experiments. The cells were treated with the indicated CDK4/6i [1µM] for 3h. This seems to not impact the conformation of CDK4/6 wt or mutated KinCon reporters. There is a tendency that CyclinD co-expression promotes CDK4/6 conformation opening (data not shown).

Author response image 1.

Bioluminescence signal of CDK4/6 KinCon reporters with co-expressed CyclinD3 (HEK293T, expression for 48h) upon exposure to indicated CDK4/6i [1µM] or DMSO for 3h (mean ±SEM, n=3 ind. experiments). No significant changes using the current setting.

(2) The work with the trimeric LKB1 complex involves pseudokinase, STRADalpha, whose conformation is also examined as a function of LKB1 status; since STRAD is an activator of LKB1. A future goal should be the evaluation of the complex in the presence of STRAD inhibitory/activating small molecules.

Thank you for this great idea, we are currently compiling a FWF grant application to get support for such a R&D project.

Minor points

• Have any of the data been repeated in a different cell background? This came to mind because HeLa cells lack LKB1, which might be a useful place to test the LKB1 data in a different context.

This experiment was performed and we show it in Figure Supplement 5. Further, we followed the advice of the reviewer and performed suggested experiments. We integrated the colon cancer cell line SW480 into the experimental setup. Overall, three cell settings showed the same pattern of KinCon reporter analyses for LKB1-STRADα-MO25 complex formation utilizing the LKB1- and STRADα-KinCon reporters.  

• The study picks up the PKA Cushings Syndrome field, which makes sense, and data are presented for L206R. PMID 35830806 explains how different patient mutations drive different signaling outcomes through distinct complex formations, and it would be interesting to discuss how mutations in KinCon complexes, especially those with mutations, could affect sub-cellular localization. Could the authors explain if this was done for any of the proteins, whose low experimental expression is a clear advantage, but is presumably hard to maintain across experiments?

The feedback of the reviewer motivated us to perform subcellular fractionation experiments. They were performed with PKAc wt and L206R KinCon reporters as well as BRAF wt and V600E reporters. We were not able to see major differences between the wt and mutated reporter constructs in respect to their nucleus: cytoplasm localizations (Figure Supplement 4). For your information, in a R+D project with the mitochondrial kinase PINK1 we see localization of the reporter as expected almost exclusively at the mitochondria fraction. 

- Line 495: In this context of activating kinase mutations we showed that using PKAc (wt and L206R) and BRAF (wt and V600E) reporters as example we could not track alterations of cytoplasmic and nuclear localization (Figure Supplement 4). Furthermore, subcellular localization of PKAc KinCon reporters did not change when L206R mutant was introduced (Figure Supplement 4). As a control BRAF wt and V600E KinCon reporters were used and also no changes in localization was observed.

• I suggest changing PMs (Figure 2 and others) simply to mutation, I read this as plasma membrane constantly.

We agree and we have changed it to “patient mutation” in Figure 2C, Figure 3E, Figure 4B.

Author Response

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

Reviewer #1:

This manuscript describes a set of four passage-reading experiments which are paired with computational modeling to evaluate how task-optimization might modulate attention during reading. Broadly, participants show faster reading and modulated eye-movement patterns of short passages when given a preview of a question they will be asked. The attention weights of a Transformerbased neural network (BERT and variants) show a statistically reliable fit to these reading patterns above-and-beyond text- and semantic-similarity baseline metrics, as well as a recurrent-networkbased baseline. Reading strategies are modulated when questions are not previewed, and when participants are L1 versus L2 readers, and these patterns are also statistically tracked by the same transformer-based network.

I should note that I served as a reviewer on an earlier version of this manuscript at a different venue. I had an overall positive view of the paper at that point, and the same opinion holds here as well.

Strengths:

• Task-optimization is a key notion in current models of reading and the current effort provides a computationally rigorous account of how such task effects might be modeled

• Multiple experiments provide reasonable effort towards generalization across readers and different reading scenarios

• Use of RNN-based baseline, text-based features, and semantic features provides a useful baseline for comparing Transformer-based models like BERT

Thank you for the accurate summary and positive evaluation.

Weaknesses:

1) Generalization across neural network models seems, to me, somewhat limited: The transformerbased models differ from baseline models in numerous ways (model size, training data, scoring algorithm); it is thus not clear what properties of these models necessarily supports their fit to human reading patterns.

Thank you for the insightful comment. To dissociate the effect of model architecture and the effect of training data, we have now compared the attention weights across three transformer-based models that have the same architecture but different training data/task: randomized (with all model parameters being randomized), pretrained, and fine-tuned models. Remarkably, even without training on any data, the attention weights in randomly initialized models exhibited significant similarity to human attention patterns (Figure. 3A). The predictive power of randomly initialized transformer-based models outperformed that of the SAR model. Through subsequent pre-training and fine-tuning, the predictive capacity of the models was further elevated. Therefore, both model architecture and the training data/task contribute to human-like attention distribution in the transformer models. We have now reported this result:

“The attention weights of randomly initialized transformer-based models could predict the human word reading time and the predictive power, which was around 0.3, was significantly higher than the chance level and the SAR (Fig. 3A, Table S1). The attention weights of pre-trained transformerbased models could also predict the human word reading time, and the predictive power was around 0.5, significantly higher than the predictive power of heuristic models, the SAR, and randomly initialized transformer-based models (Fig. 3A, Table S1). The predictive power was further boosted for local but not global questions when the models were fine-tuned to perform the goal-directed reading task (Fig. 3A, Table S1).”

In addition, we reported how training influenced the sensitivity of attention weights to text features and question relevance. As shown in Figure 4AB, attention in the randomized models were sensitive to text features across all layers. After pretraining, the models exhibited increased sensitivity to text features in the shallow layers, and decreased sensitivity to text features in deep layers. Subsequent finetuning on the reading comprehension task further attenuates the encoding of text features in deep layers but strengthens the sensitivity to task-relevant information.

2) Inferential statistics are based on a series of linear regressions, but these differ markedly in model size (BERT models involve 144 attention-based regressor, while the RNN-based model uses just 1 attention-based regressor). How are improvements in model fit balanced against changes in model size?

Thank you for pointing out this issue. The performance of linear regressions was evaluated based on 5-fold cross-validation, and the performance we reported was the performance on the test set. To match the number of parameters, we have now predicted human attention using the average of all heads. The predictive power of the average head was still significantly higher than the predictive power of the SAR model. We have now reported this result in our revised manuscript:

“For the fine-tuned models, we also predict the human word reading time using an unweighted averaged of the 144 attention heads and the predictive power was 0.3, significantly higher than that achieved by the attention weights of SAR (P = 4 × 10-5, bootstrap).”

Also, it was not clear to me how participant-level variance was accounted for in the modeling effort (mixed-effects regression?) These questions may well be easily remedied by more complete reporting.

In the previous manuscript, the word reading time was averaged across participants, and we did not consider the variance between participants. We have now analyzed eye movements of each participant and used the linear mixed effects model to test how different factors affected human word reading time to account for participantslevel and item-level variances.

“Furthermore, a linear mixed effect model also revealed that more than 85% of the DNN attention heads contribute to the prediction of human reading time when considering text features and question relevance as covariates (Supplementary Results).”

“Supplementary Methods To characterize the influences of different factors on human word reading time, we employed linear mixed effects models [5] implemented in the lmerTest package [6] of R. For the baseline model, we treated the type of questions (local vs. global; local = baseline) and all text/task-related features as fixed factors, and considered the interaction between the type of questions and these text/taskrelated features. We included participants and items (i.e., questions) as random factors, each with associated random intercepts…”

Supplementary Results The baseline mixed model revealed significant fixed effects for question type and all text/task-related features, as well as significant interactions between question type and these text/task-related features (Table S7). Upon involving SAR attention, we observed a statistically significant fixed effect associated with SAR attention. When involving attention weights of randomly initialized BERT, the mixed model revealed that most attention heads exhibited significant fixed effects, suggesting their contributions to the prediction of human word reading time. A broader range of attention heads showed significant fixed effects for both pre-trained and fine-tuned BERT.

3) Experiment 1 was paired with a relatively comprehensive discussion of how attention weights mapped to reading times, but the same sort of analysis was not reported for Exps 2-4; this seems like a missed opportunity given the broader interest in testing how reading strategies might change across the different parameters of the four experiments.

Thank you for the valuable suggestion. We have now also characterized how different reading measures, e.g., gaze duration and counts or rereading, were affected by text and task-related features in Experiments 2-4.

For Experiment 2: “For local questions, consistent with Experiment 1, the effects of question relevance significantly increased from early to late processing stages that are separately indexed by gaze duration and counts of rereading (Fig. S9A, Table S3).”

For Experiment 3: “For local questions, the layout effect was more salient for gaze duration than for counts of rereading. In contrast, the effect of word-related features and task relevance was more salient for counts of rereading than gaze duration (Fig. S9B, Table S3).”

For Experiment 4: “Both the early and late processing stages of human reading were significantly affected by layout and word features, and the effects were larger for the late processing stage indexed by counts of rereading (Fig. S9C, Table S3).”

4) Comparison of predictive power of BERT weights to human annotations of text relevance is limited: The annotation task asked participants to chose the 5 "most relevant" words for a given question; if >5 words carried utility in answering a question, this would not be captured by the annotation. It seems to me that the improvement of BERT over human annotations discussed around page 10-11 could well be due to this arbitrary limitation of the annotations.

Thank you for the insightful comment. We only allowed a participant to label 5 words since we wanted the participant to only label the most important information. As the reviewer pointed out, five words may not be enough. However, this problem is alleviated by having >26 annotators per question. Although each participant can label up to 5 words, pooling the results across >26 annotators results in nonzero relevance rating for an average 21.1 words for local questions and 26.1 words for global question. More important, as was outlined in Experimental Materials, we asked additional participants to answer questions based on only 5 annotated keywords. The accuracy for question answering were 75.9% for global questions and 67.6% for local questions, which was close to the accuracy achieved when the complete passage was present (Fig. 1B), suggesting that even 5 keywords could support question answering.

5) Abstract ln 35: This concluding sentence didn't really capture the key contribution of the paper which, at least from my perspective, was something closer to "we offer a computational account of how task optimization modulates attention during reading"

p 4 ln 66: I think this sentence does a good job capturing the main contributions of this paper

Thanks for your suggestion. We have modified our conclusion in Abstract accordingly.

6) p 4 ln 81: "therefore is conceptually similar" maybe "may serve a conceptually similar role"

We have rewritten the sentence.

“Attention in DNN also functions as a mechanism to selectively extract useful information, and therefore attention may potentially serve a conceptually similar role in DNN.”

7) p. 7 ln 140: "disproportional to the reading time" I didn't understand this sentence

Sorry for the confusion and we have rewritten the sentence.

“In Experiment 1, participants were allowed to read each passage for 2 minutes. Nevertheless, to encourage the participants to develop an effective reading strategy, the monetary reward the participant received decreased as they spent more time reading the passage (see Materials and Methods for details).”

8) p 8 ln 151: This was another sentence that helped solidify the main research contributions for me; I wonder if this framing could be promoted earlier?

Thank you for the suggestion and we have moved the sentence to Introduction.

9) p. 33: I may be missing something here, but I didn't follow the reasoning behind quantifying model fit against eye-tracking measures using accuracy in a permutation test. Models are assessed in terms of the proportion of random shuffles that show a greater statistical correlation. Does that mean that an accuracy value like 0.3 (p. 10 ln 208) means that 0.7 random permutations of word order led to higher correlations between attention weights and RT? Given that RT is continuous, I wonder if a measure of model fit such as RMSE or even R^2 could be more interpretable.

We have now realized that the term “prediction accuracy” was not clearly defined and have caused confusion. Therefore, in the revised manuscript, we have replaced this term with “predictive power”. Additionally, we have now introduced a clear definition of “prediction power” at its first mention in Result:

“…the predictive power, i.e., the Pearson correlation coefficient between the predicted and real word reading time, was around 0.2”

The permutation test was used to test if the predictive power is above chance. Specifically, if the predictive power is higher than the 95 percentile of the chancelevel predictive power estimated using permutations, the significant level (i.e., the p value) is 0.05. We have explained this in Statistical tests.

10) p. 33: FDR-based multiple comparisons are noted several times, but wasn't clear to me what the comparison set is for any given test; more details would be helpful (e.g. X comparisons were conducted across passages/model-variants/whatever)

Sorry for missing this important information. We have now mentioned which comparisons are corrected,

“…Furthermore, the predictive power was higher for global than local questions (P = 4 × 10-5, bootstrap, FDR corrected for comparisons across 3 features, i.e., layout features, word features, and question relevance)…”

Reviewer #2:

In this study, researchers aim to understand the computational principles behind attention allocation in goal-directed reading tasks. They explore how deep neural networks (DNNs) optimized for reading tasks can predict reading time and attention distribution. The findings show that attention weights in transformer-based DNNs predict reading time for each word. Eye tracking reveals that readers focus on basic text features and question-relevant information during initial reading and rereading, respectively. Attention weights in shallow and deep DNN layers are separately influenced by text features and question relevance. Additionally, when readers read without a specific question in mind, DNNs optimized for word prediction tasks can predict their reading time. Based on these findings, the authors suggest that attention in real-world reading can be understood as a result of task optimization.

The research question pursued by the study is interesting and important. The manuscript was well written and enjoyable to read. However, I do have some concerns.

We thank the reviewer for the accurate summary and positive evaluation.

1) In the first paragraph of the manuscript, it appears that the purpose of the study was to test the optimization hypothesis in natural tasks. However, the cited papers mainly focus on covert visual attention, while the present study primarily focuses on overt attention (eye movements). It is crucial to clearly distinguish between these two types of attention and state that the study mainly focuses on overt attention at the beginning of the manuscript.

Thank you for pointing out this issue. We have explicitly mentioned that we focus on overt attention in the current study. Furthermore, we have also discussed that native readers may rely more on covert attention so that they do not need to spend more time overtly fixating at the task relevant words.

In Introduction:

“Reading is one of the most common and most sophisticated human behaviors [16, 17], and it is strongly regulated by attention: Since readers can only recognize a couple of words within one fixation, they have to overtly shift their fixation to read a line of text [3]. Thus, eye movements serve as an overt expression of attention allocation during reading [3, 18].”

In Discussion:

“Therefore, it is possible that when readers are more skilled and when the passage is relatively easy to read, their processing is so efficient so that they do not need extra time to encode task-relevant information and may rely on covert attention to prioritize the processing of task-relevant information.”

2) The manuscript correctly describes attention in DNN as a mechanism to selectively extract useful information. However, eye-movement measures such as gaze duration and total reading time are primarily influenced by the time needed to process words. Therefore, there is a doubt whether the argument stating that attention in DNN is conceptually similar to the human attention mechanism at the computational level is correct. It is strongly suggested that the authors thoroughly discuss whether these concepts describe the same or different things.

Thank you for bringing up this very important issue and we have added discussions about why human and DNN may generate similar attention distributions. For example, we found that both DNN and human attention distributions are modulated by task relevance and word properties, which include word length, word frequency, and word surprisal. The influence of task relevance is relatively straightforward since both human readers and DNN should rely more on task relevant words to answer questions. The influence of word properties is less apparent for models than for human readers and we have added discussions:

For DNN’s sensitivity to word surprisal:

“The transformer-based DNN models analyzed here are optimized in two steps, i.e., pre-training and fine-tuning. The results show that pre-training leads to text-based attention that can well explain general-purpose reading in Experiment 4, while the fine-tuning process leads to goal-directed attention in Experiments 1-3 (Fig. 4B & Fig. 5A). Pre-training is also achieved through task optimization, and the pre-training task used in all the three models analyzed here is to predict a word based on the context. The purpose of the word prediction task is to let models learn the general statistical regularity in a language based on large corpora, which is crucial for model performance on downstream tasks [21, 22, 33], and this process can naturally introduce the sensitivity to word surprisal, i.e., how unpredictable a word is given the context.”

For DNN’s sensitivity to word length:

“Additionally, the tokenization process in DNN can also contribute to the similarity between human and DNN attention distributions: DNN first separates words into tokens (e.g., “tokenization” is separated into “token” and “ization”). Tokens are units that are learned based on co-occurrence of letters, and is not strictly linked to any linguistically defined units. Since longer words tend to be separated into more tokens, i.e., fragments of frequently co-occurred letters, longer words receive more attention even if the model pay uniform attention to each of its input, i.e., a token.”

3) When reporting how reading time was predicted by attention weights, the authors used "prediction accuracy." While this measure is useful for comparing different models, it is less informative for readers to understand the quality of the prediction. It would be more helpful if the results of regression models were also reported.

Sorry for the confusion. The prediction accuracy was defined as the correlation coefficient between the predicted and actual eye-tracking measures. We have now realized that the term “prediction accuracy” might have caused confusion. Therefore, in the revised manuscript, we have replaced this term with “predictive power”. Additionally, we have now introduced a clear definition of “prediction power” at its first mention in Result:

“…the predictive power, i.e., the Pearson correlation coefficient between the predicted and real word reading time, was around 0.2”

4) The motivations of Experiments 2 and 3 could be better described. In their current form, it is challenging to understand how these experiments contribute to understanding the major research question of the study.

Thank you for pointing out this issue. In Experiments 1, different types of questions were presented in separate blocks, and all the participants were L2 reader. Therefore, we conducted Experiments 2 and 3 to examine how reading behaviors were modulated when different types of questions were presented in a mixed manner, or when participants were L1 readers. We have now clarified the motivations:

“In Experiment 1, different types of questions were presented in blocks which encouraged the participants to develop question-type-specific reading strategies. Next, we ran Experiment 2, in which questions from different types were mixed and presented in a randomized order, to test whether the participants developed question-type-specific strategies in Experiment 1.”

“Experiments 1 and 2 recruited L2 readers. To investigate how language proficiency influenced task modulation of attention and the optimality of attention distribution, we ran Experiment 3, which was the same as Experiment 2 except that the participants were native English readers.”

Reviewer #3:

This paper presents several eyetracking experiments measuring task-directed reading behavior where subjects read texts and answered questions.

It then models the measured reading times using attention patterns derived from deep-neural network models from the natural language processing literature.

Results are taken to support the theoretical claim that human reading reflects task-optimized attention allocation.

STRENGTHS:

1) The paper leverages modern machine learning to model a high-level behavioral task (reading comprehension). While the claim that human attention reflects optimal behavior is not new, the paper considers a substantially more high-level task in comparison to prior work. The paper leverages recent models from the NLP literature which are known to provide strong performance on such question-answering tasks, and is methodologically well grounded in the NLP literature.

2) The modeling uses text- and question-based features in addition to DNNs, specifically evaluates relevant effects, and compares vanilla pretrained and task-finetuned models. This makes the results more transparent and helps assess the contributions of task optimization. In particular, besides finetuned DNNs, the role of the task is further established by directly modeling the question relevance of each word. Specifically, the claim that human reading is predicted better by task-optimized attention distributions rests on (i) a role of question relevance in influencing reading in Expts 1-2 but not 4, and (ii) the fact that fine-tuned DNNs improve prediction of gaze in Expts 1-2 but not 4.

3) The paper conducts experiments on both L2 and L1 speakers.

We thank the reviewer for the accurate summary and positive evaluation.

WEAKNESSES:

1) The paper aims to show that human gaze is predicted the the DNN-derived task-optimal attention distribution, but the paper does not actually derive a task-optimal attention distribution. Rather, the DNNs are used to extract 144 different attention distributions, which are then put into a regression with coefficients fitted to predict human attention. As a consequence, the model has 144 free parameters without apparent a-priori constraint or theoretical interpretation. In this sense, there is a slight mismatch between what the modeling aims to establish and what it actually does.

Regarding Weakness (1): This weakness should be made explicit, at least by rephrasing line 90. The authors could also evaluate whether there is either a specific attention head, or one specific linear combination (e.g. a simple average of all heads) that predicts the human data well.

Thank you for pointing out this issue. One the one hand, we have now also predicted human attention using the average of all heads, i.e., the simple average suggested by the reviewer. The predictive power of the average head was still significantly higher than the predictive power of the SAR model. We have now reported this result in our revised manuscript.

“For the fine-tuned models, we also predict the human word reading time using an unweighted averaged of the 144 attention heads and the predictive power was 0.3, significantly higher than that achieved by the attention weights of SAR (P = 4 × 10-5, bootstrap).”

On the other hand, since different attention weights may contribute differently to the prediction of human reading time, we have now also reported the weights assigned to individual attention head during the original regression analysis (Fig. S4). It was observed that the weight was highly distributed across attention head and was not dominated by a single head.

Even more importantly, we have now rephrased the statement in line 90 of the previous manuscript:

“We employed DNNs to derive a set of attention weights that are optimized for the goal-directed reading task, and tested whether such optimal weights could explain human attention measured by eye tracking.”

Furthermore, in Discussion, we mentioned that:

“Furthermore, we demonstrate that both humans and transformer-based DNN models achieve taskoptimal attention distribution in multiple steps… Similarly, the DNN models do not yield a single attention distribution, and instead it generates multiple attention distributions, i.e., heads, for each layer. Here, we demonstrate that basic text features mainly modulate the attention weights in shallow layers, while the question relevance of a word modulates the attention weights in deep layers, reflecting hierarchical control of attention to optimize task performance. The attention weights in both the shallow and deep layers of DNN contribute to the explanation of human word reading time (Fig. S4).”

2) While Experiment 1 tests questions from different types in blocks, and the paper mentions that this might encourage the development of question-type-specific reading strategies -- indeed, this specifically motivates Experiment 2, and is confirmed indirectly in the comparison of the effects found in the two experiments ("all these results indicated that the readers developed question-typespecific strategies in Experiment 1") -- the paper seems to miss the opportunity to also test whether DNNs fine-tuned for each of the question-types predict specifically the reading times on the respective question types in Experiment 1. Testing not only whether DNN-derived features can differentially predict normal reading vs targeted reading, but also different targeted reading tasks, would be a strong test of the approach.

Regarding Weakness (2): results after finetuning for each question type could be reported.

Thank you for the valuable suggestion. We have now fine-tuned the models separately based on global and local questions. The detailed fine-tuning parameters employed in the fine-tuning process were presented in Author response table 1.

Author response table 1.

The hyperparameter for fine-tuning DNN models with specific question type.

The fine-tuning process yielded a slight reduction in loss (i.e., the negative logarithmic score of the correct option) on the validation set. Specifically, for BERT, the loss decreased from 1.08 to 0.96; for ALBERT, it decreased from 1.16 to 0.76; for RoBERTa, it went down from 0.68 to 0.54. Nevertheless, the fine-tuning process did not improve the prediction of reading time (Author response image 1). A likely reason is that the number of global and local questions for training is limited (local questions: 520; global questions: 280), and similar questions also exist in RACE dataset that is used for the original fine tuning (sample size: 87,866). Therefore, a small number of questions can significantly change the reading strategy of human readers but using these questions to effectively fine-tune a model seems to be a more challenging task.

Author response image 1.

Fine-tuning based on local and global questions does not significantly modulate the prediction of human reading time. Lighter-color symbols show the results for the 3 BERT-family models (i.e., BERT, ALBERT, and RoBERTa) and the darker-color symbols show the average over the 3 BERT-family models. trans_fine: model fine-tuned based on the RACE dataset; trans_local: models additionally fine-tuned using local questions; trans_global: models additionally fine-tuned using global questions.

3) The paper compares the DNN-derived features to word-related features such as frequency and surprisal and reports that the DNN features are predictive even when the others are regressed out (Figure S3). However, these features are operationalized in a way that puts them at an unfair disadvantage when compared to the DNNs: word frequency is estimated from the BNC corpus; surprisal is derived from the same corpus and derived using a trigram model. The BNC corpus contains 100 Million words, whereas BERT was trained on several Billions of words. Relatedly, trigram models are now far surpassed by DNN-based language models. Specifically, it is known that such models do not fit human eyetracking reading times as well as modern DNN-based models (e.g., Figure 2 Dundee in: Wilcox et al, On the Predictive Power of Neural Language Models for Human Real-Time Comprehension Behavior, CogSci 2020). This means that the predictive power of the word-related features is likely to be underestimated and that some residual predictive power is contained in the DNNs, which may implicitly compute quantities related to frequency and surprisal, but were trained on more data. In order to establish that the DNN models are predictive over and above word-related features, and to reliably quantify the predictive power gained by this, the authors could draw on (1) frequency estimated from the corpora used for BERT (BookCorpus + Wikipedia), (2) either train a strong DNN language model, or simply estimate surprisal from a strong off-the-shelf model such as GPT-2.

This concern does not fundamentally cast doubt on the conclusions, since the authors found a clear effect of the task relevance of individual words, which by definition is not contained in those baseline models. However, Figure S3 -- specifically Figure S3C -- is likely to inflate the contribution of the DNN model over and above the text-based features.

Thank you for pointing out these issues. Following the valuable suggestion of the reviewer, we have now 1) computed word frequencies based on BookCorpus and Wikipedia and 2) calculated word surprisal using GPT-2.

“The word features included word length, logarithmic word frequency estimated based on the BookCorpus [62] and English Wikipedia using SRILM [68], and word surprisal estimated from GPT-2 Medium [69].”

These recalculated word frequency and surprisal are correlated with the original measures (word frequency: 0.98; surprisal: 0.59), and the updated results are also closely aligned with those reported in the previous manuscript.

Others:

1) How does the statistical modeling take into account that measures are repeated both within the items (same texts read by different subjects) and within the subjects (some subject read multiple texts)? I only see the items-level repetition be addressed in line 715-721 in comparing between local and global questions, but not elsewhere. The standard approach in the literature on human reading times (e.g. the Wilcox et al paper mentioned above, or ref. 44) is to use mixed-effects regression with appropriate random effects for items and subjects. The same question applies to the calculation of chance accuracy (line 702-709), which is done by shuffling words within a passage. Relatedly, how exactly was cross-validation (line 681) calculated? On the level of subjects, individual words, trials, texts, ...?

Thank you for raising up this issue. In the previous manuscript, the word reading time was averaged across participants. The cross-validation was conducted on the level of texts (i.e., passages). Following the valuable suggestion, we have now separately analyzed each participant and applied the linear mixed effects models.

“Furthermore, a linear mixed effect model also revealed that more than 85% of the DNN attention heads contribute to the prediction of human reading time when considering text features and question relevance as covariates (Supplementary Results).”

“Supplementary Methods To characterize the influences of different factors on human word reading time, we employed linear mixed effects models [5] implemented in the lmerTest package [6] of R. For the baseline model, we treated the type of questions (local vs. global; local = baseline) and all text/task-related features as fixed factors, and considered the interaction between the type of questions and these text/taskrelated features. We included participants and items (i.e., questions) as random factors, each with associated random intercepts…”

Supplementary Results The baseline mixed model revealed significant fixed effects for question type and all text/task-related features, as well as significant interactions between question type and these text/task-related features (Table S7). Upon involving SAR attention, we observed a statistically significant fixed effect associated with SAR attention. When involving attention weights of randomly initialized BERT, the mixed model revealed that most attention heads exhibited significant fixed effects, suggesting their contributions to the prediction of human word reading time. A broader range of attention heads showed significant fixed effects for both pre-trained and fine-tuned BERT.

2) I could not find any statement about code availability (only about data availability). Will the source code and statistical analysis code also be made available?

We have added the code availability statement.

“The code is now available at https://github.com/jiajiezou/TOA.”

3) The theoretical claim, and some basic features of the research, are quite similar to other recent work (Hahn and Keller, Modeling task effects in human reading with neural network-based attention, Cognition, 2023; cited with very little discussion as ref 44), which also considered task-directed reading in a question-answering task and derived task-optimized attention distributions. There are various differences, and the paper under consideration has both weaknesses and strengths when compared to that existing work -- e.g., that paper derived a single attention distribution from task optimization, but the paper under consideration provides more detailed qualitative analysis of the task effects, uses questions requiring more high-level reasoning, and uses more state-of-the-art DNNs.

The paper would benefit from being more explicit about how the work under review provides a novel angle over Ref 44 (Hahn and Keller, Cognition, 2023).

Thanks for bringing up this issue. We have now incorporated a more comprehensive discussion that compare the current study with the recent work conducted by Hahn and Keller:

“When readers read a passage to answer a question that can be answered using a word-matching strategy [45], a recent study has demonstrated that the specific reading goal modulates the word reading time and the effect can be modeled using a RNN model [46]. Here, we focus on questions that cannot be answered using a word-matching strategy (Fig. 1B) and demonstrate that, for these challenging questions, attention is still modulated by the reading goal but the attention modulation cannot be explained by a word-matching model (Fig. S3). Instead, the attention effect is better captured by transformer models than an advanced RNN model, i.e., the SAR (Fig. 3A). Combining the current study and the study by Hahn et al. [46], it is possible that the word reading time during a general-purpose reading task can be explained by a word prediction task, the word reading time during a simple goal-directed reading task that can be solved by word matching can be modeled by a RNN model, while the word reading time during a more complex goal-directed reading task involving inference is better modeled using a transformer model. The current study also further demonstrates that elongated reading time on task-relevant words is caused by counts of rereading and further studies are required to establish whether earlier eye movement measures can be modulated by, e.g., a word matching task.”

4) In Materials&Methods, line 599-636, specifically when "pretraining" is mentioned (line 632), it should be mentioned what datasets these DNNs were pretrained on.

We have now mentioned this in the revised manuscript:

“The pre-training process aimed to learn general statistical regularities in a language based on large corpora, i.e., BooksCorpus [62] and English Wikipedia…”

Author response:

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

Reviewer #1 (Public review):

Summary:

Insulin is crucial for maintaining metabolic homeostasis, and its release is regulated by various pathways, including blood glucose levels and neuromodulatory systems. The authors investigated the role of neuromodulators in regulating the dynamics of the adult Drosophila IPC population. They showed that IPCs express various receptors for monoaminergic and peptidergic neuromodulators, as well as synaptic neurotransmitters with highly heterogeneous profiles across the IPC population. Activating specific modulatory inputs, e.g. dopaminergic, octopaminergic or peptidergic (Leucokinin) using an optogenetic approach coupled with in vivo electrophysiology unveiled heterogeneous responses of individual IPCs resulting in excitatory, inhibitory or no responses. Interestingly, calcium imaging of the entire IPC population with or without simultaneous electrophysiological recording of individual cells showed highly specific and stable responses of individual IPCs suggesting their intrinsic properties are determined by the expressed receptor repertoire. Using the adult fly connectome they further corroborate the synaptic input of excitatory and inhibitory neuronal subsets of IPCs. The authors conclude that the heterogeneous modulation of individual IPC activity is more likely to allow for flexible control of insulin release to adapt to changes in metabolic demand and environmental cues.

Strengths:

This study provides a comprehensive, multi-level analysis of IPC properties utilizing single-nucleus RNA sequencing, anatomical receptor expression mapping, connectomics, electrophysiological recordings, calcium-imaging and an optogeneticsbased 'intrinsic pharmacology' approach. It highlights the heterogeneous receptor profiles of IPCs, demonstrating complex and differential modulation within the IPC population. The authors convincingly showed that different neuromodulatory inputs exhibit varied effects on IPC activity and simultaneous occurrence of heterogeneous responses in IPCs with some populations exciting a subset of IPCs while inhibiting others, showcasing the intricate nature of IPC modulation and diverse roles of IPC subgroups. The temporal dynamic of IPC modulation showed that polysynaptic and neuromodulatory connections play a major role in IPC response. The authors demonstrated that certain neuromodulatory inputs, e.g. dopamine, can shift the overall IPC population activity towards either an excited or inhibited state. The study thus provides a fundamental entry point to understanding the complex influence of neuromodulatory inputs on the insulinergic system of Drosophila.

We thank the reviewer for endorsing our study as a fundamental entry point to understanding the complex neuromodulation of the insulin system.

Weakness:

GPCRs are typically expressed at low levels and while the transcriptomic and reporter expression analysis was comprehensive, both approaches have the caveat that they do not allow validating protein level expression. Thus, some receptors might have been missed while others might be false positives. The authors acknowledged the challenges in accurately accessing receptor expression in complex modulatory systems indicating there are limitations in full understanding of the receptor profiles of IPCs.

We agree with the reviewer and acknowledge that both the transcript and protein expression need to be examined in order to obtain higher confidence in receptor expression profiles. The T2A-GAL4 lines used in our anatomical analyses do in fact provide insights into which of the receptor transcripts are translated. We added the following statement to the discussion section to clarify this approach “The singlenucleus transcriptome analysis reveals which receptor transcripts are expressed whereas the T2A-GAL4 lines used in our anatomical analyses provide insights on which of the receptor transcripts are translated. This is based on the fact that T2A peptides induce ribosome skipping during translation. Therefore, GAL4 protein is only produced when the receptor protein is produced(42,88).”

While this study provides valuable insights into the heterogeneity of IPC responses and receptor expression, it will require future studies to elucidate how these modulatory inputs affect insulin release and transcriptional long-term changes. The authors further analyzed male and female snRNAseq data and claimed that the differences in receptor expression were minimal. The experimental analyses used mated females only and while the study is very complete in this respect, it would have been extremely interesting to compare male flies in terms of their response profiles.

We thank the reviewer for acknowledging that long-term effects on release and transcript levels go beyond the scope of this study and agree that these questions should be addressed in future investigations. Concerning the differences between females and males: we did not find significant differences in the snRNAseq data between the two sexes. Moreover, a parallel study from our lab found no differences between males and females in IPC baseline activity (Bisen et al. 2024, eLife https://doi.org/10.7554/eLife.98514.1). We therefore did not follow this path for the present study. We explained our reasoning in the results section of our paper, by adding: “Since there were little differences in receptor expression between males and females (Fig. S1C), we used the transcriptomes from both sexes for all subsequent analyses.” in the transcriptome section, and “Since baseline recordings from IPCs, in addition to our transcriptomic analysis, revealed no significant difference between male and female flies(26), we only used mated females for our physiological experiments.” in the transition to the physiology section of our manuscript.

Lastly as also pointed out by the authors, their approach of using optogenetically driven excitation of modulatory neuronal subsets limits the interpretation of the results due to the possibly confounding direct or indirect effect of fast synaptic transmission on IPC excitation/inhibition, and the broad expression of some neuromodulatory lines used in this analysis.

We agree that our results are limited to general effects of neuronal populations rather than individual neurons or specific inputs, and that it is generally hard to untangle effects of fast transmitters from those of modulatory inputs. However, we believe that we are careful in presenting and interpreting our results in this regard.

Overall, however, the conclusions of this study are well supported by the data provided by the authors. Moreover, their detailed and thorough analysis of IPC modulation will have a significant impact on the field of metabolic regulation to understand the complex regulatory mechanism of insulin release, which can now be studied further to provide insight about metabolic homeostasis and neural control of metabolic processes.

We thank the referee kindly for these comments!

Reviewer #2 (Public review):

Summary:

Held et al. investigated the distinct activities of Insulin-Producing Cells (IPCs) by electrophysiological recordings and calcium imaging. In the brain of the fruit fly Drosophila melanogaster, there are approximately 14 IPCs that are analogous to mammalian pancreatic beta cells and provide a good model system for monitoring their activities in vivo. The authors performed single-nucleus RNA sequencing analysis to examine what types of neuromodulatory inputs are received by IPCs. A variety of neuromodulatory receptors are expressed heterogeneously in IPCs, which would explain the distinct activities of IPCs in response to the activations of neuromodulatory neurons. The authors also conducted the connectome analysis and G-protein prediction analysis to strengthen their hypothesis that the heterogeneity of IPCs may underlie the flexible insulin release in response to various environmental conditions.

Strengths:

The authors succeeded patch-clamp recordings and calcium imaging of individual IPCs in living animals at a single-cell resolution, which allows them to show the heterogeneity of IPCs precisely. They measured IPC activities in response to 9 types of neurons in patch-clamp recordings and 5 types of neurons in calcium imaging, comparing the similarities and differences in activities between two methods. These results support the idea that the neuromodulatory system affects individual IPC activities differently in a receptor-dependent manner.

We thank the reviewer for emphasizing how our in vivo experiments allow for a precise characterization of the IPC responses to modulatory inputs.

Weaknesses:

One concern is how much extent the heterogeneity of IPC activities in a short time scale is relevant to the net output, a release of insulin-like peptides in response to metabolic demands in a relatively longer time scale. The authors can test their hypothesis by manipulating the heterogeneous expressions of receptor genes in IPCs and examining IPC activities on a longer time scale. Moreover, while the authors focus on IPC activities, they did not show the activation of the neuromodulatory inputs and the net output of insulin levels in the data. The readers might want to know which neurons are indeed activated to send signals to IPCs and how IPC activities result in the secretion of insulin peptides.

We agree with the reviewer that the two experiments described, manipulating receptor expression before long-term recordings and measuring insulin levels after activating modulatory inputs, would deliver exciting insights into the interplay of modulatory inputs, IPC population activity, and insulin release. However, currently available methods for monitoring insulin release do not allow us to perform these experiments with a temporal resolution that would match the sensitivity and time resolution of our physiological experiments and are therefore not suited for a direct comparison. We also acknowledge that it would be extremely exciting to characterize the modulatory populations providing input to IPCs in terms of their sensitivity to internal state changes and external inputs. However, this clearly goes beyond the scope of our study. Essentially, one would have to perform experiments on a similar scale and breadth as we have done for IPCs here for the other populations. We aim to perform some of these experiments in follow up projects to this work.

Reviewer #1 (Recommendations for the authors):

(1) The authors used a 5% expression cutoff initially, which seems arbitrary. Can you explain the rationale for using this cutoff? If I interpret the authors' logic correctly and given there are 14 IPCs per animal, at 5% there is a 70% chance that 1 cell expresses that receptor.

We used a 5% cutoff to reduce false positives in our transcriptomic analysis. This threshold translates to expression in 0.8 out of 16 IPCs found in an individual fly on average. Hence, this cutoff ensures that receptors are expressed in at least 1 cell. Based on 392 IPC transcriptomes used in our analysis, our 5% threshold means that any receptor expressed in less than 20 transcriptomes will be deemed to be absent. At the population level, this ensures that our expression analysis is based on cells from at least two flies. However, we expect the actual number of flies from which the IPC transcriptomes were derived from to be much higher. We added the following statement to the methods section to clarify this point: “To determine if a transcript is present in the IPC transcriptomes, we used a 5% cutoff to reduce false positives. This cutoff is equivalent to expression in 0.8 IPCs out of 16 on average in an individual fly, and hence less than one IPC in the entire population. Since we used 392 IPC transcriptomes in our analysis, this cutoff means that expression in less than 20 IPCs will be deemed false positive”

(2) Were male and female brains examined separately and tested for divergent expression of T2A-reporter signals? While there were not many strong differences in the snRNAseq dataset, based on some discrepancies with the reporters it might be worthwhile to assess sex-specific differences that might account for the observed expression/non-expression of some receptors.

We did not investigate sex-specific differences using anatomical mapping, since our scRNA analysis pointed against that being a major factor. We clarified our reasoning in the results section by adding “Since there were little differences in receptor expression between males and females (Fig. S1C), we used the transcriptomes from both sexes for all subsequent analyses.” in the transcriptome section, and “Since baseline recordings from IPCs, in addition to our transcriptomic analysis, revealed no significant difference between male and female flies(26), we only used mated females for our physiological experiments.” in the transition to the physiology section of our manuscript.

(3) The anatomical reporter and transcriptome data for neuromodulatory receptor expression do not fully complement each other, e.g. in Fig1D Lkr is expressed only in one cluster but anatomical expression is observed in most IPCs. Ultimately, visualizing receptor expression at the protein level and functional analysis with genetic perturbation of the respective receptors is needed to draw strong conclusions.

We agree with the reviewer that visualizing receptor expression at protein level could help clarify some of these differences since neuropeptide GPCR transcripts tend to be less abundant whereas we expect protein expression to be more stable. However, out of the 14 receptors examined in our study, antibodies are only available for two: DH31R and LKR. Since our DH31R-T2A-GAL4 line does not drive expression in IPCs, we did not pursue this further. We did perform preliminary experiments to validate LKR protein expression in IPCs. Unfortunately, we found that the LKR antibody labels cells in the pars intercerebralis in both the wild type and LKR mutants (see Author response image 1 below). Therefore, we do not think it suitable to monitor LKR protein expression. Thus, additional investigations must await future generations of neuropeptide receptor antibodies. One biological reason for the discrepancies could be that anatomical quantification is based on cumulative expression while transcriptomic analysis captures a brief snapshot. We included “One explanation for the discrepancies could be that transcriptomic analysis provides a single snapshot, whereas anatomical data is based on cumulative expression. Fluorescent markers persist long after transcription and translation has terminated. Therefore, a higher likelihood for receptor expression can be expected when it is quantified via anatomical techniques.” in our results part to give the readers more context.

Author response image 1.

(4) In Fig1E, As Dop2R reporter signal is not colocalizing with IPC whereas dop2R is expressed in all four clusters.

We tested if additional transcript variants with different C-termini are the cause for the discrepancy between transcriptome data and anatomical mapping. However, using a Trojan-GAL4 line for Octa2R that should account for other transcript variants did also not show any expression. At this point, with the tools we have, we cannot conclusively determine what the cause of this discrepancy is. Since we only see them with Dop2R and Octa2R, a mismatch caused by more general differences,

e.g. sex-specific differences, seems unlikely. A more plausible reason could be that for those lines, inadequate transgenes lead to failed expressions. We added “Hence, inadequate transgenes for Dop2R and Octα2R or the lack of protein translation are the likely cause for the discrepancy between transcriptome analysis and anatomical mapping.“ to our results part as a possible explanation for the discrepancy.

(5) Moving the AstANs expression images to the main figure (Fig 1E) would make sense as the authors focus on AstAN rather than MsRT or Dop2R in the later parts of their work.

We thank the reviewer for this suggestion and replaced the LKR image with an AstAR2 image, as suggested. We kept the other two receptors in the main figure as additional examples.

(6) Have the authors considered gap junction coupling of IPCs, which might explain the simultaneous responses in some cases?

We have indeed considered this exciting idea, as gap junctions between IPCs could potentially synchronize activity in connected IPC subpopulations. To test if gap junctions are a major factor in the IPC population, we performed experiments with patch-clamp recordings from a single IPC while performing calcium imaging of the IPC population (as demonstrated in Fig. 4J). In some of these experiments, we injected current into individual IPCs and tested for activity changes in the other IPCs. However, the preliminary data we acquired did not indicate that the current-induced train of action potentials was transmitted to others IPCs. Hence, it is unlikely that the IPCs are directly coupled by gap junctions. Given the challenging nature of these experiments, and the discouraging preliminary results, we have not followed up on the idea any further.

Reviewer #2 (Recommendations for the authors):

(1) Figure 3D was not described in the text.

We thank the reviewer for pointing out this mistake, we included the panel in Figure 3C and added the reference in the text describing the results from multiple animals shown in the panel.

(2) In Figure 4B, a scale of heat map is required. There is a blue spot with no ROI setting on the left side. On the right side of the photos, the ROI No.6 seemed to turn blue after activation. However, Figure 4D shows the ROI No.6 was inhibited.

We are now using a simplified heatmap in Figure 4B and added a scalebar. We also changed the example images to avoid any confusion. Previously, we used a random snapshot from before LED onset, now we used a snapshot from the actual time window to which we normalized the traces. Regarding the spot where no ROI is depicted but a response is visible: in this area, a trachea made it difficult to clearly delimit the cell body underneath, and we therefore excluded this ROI. Occlusions by trachea are one reason why we can typically not image the entire IPC population in a single animal.

(3) In Figure 4F, the regions of gray bars (baseline) contain blue and red colors to some extent, which makes me confused. Moreover, the description "within one cluster, the response seemed homogeneous, e.g., in fly #4 during the activation of DANs (Fig. 4F)." was not clear to me. How about fly #1, #2, and #3? It seems that the responses changed excitedly and inhibitory within a cluster. Although the authors tend to raise some consistent results with examples, it would not be so effective if I can see there are other counter-examples and exceptions in the results.

We apologize for the confusion we caused. The gray bars indicate the time window we used for baseline subtraction: The median activity of each IPC in this window was subtracted from the activity of that IPC. Hence, the median activity in this window is zero, but individual frames can have positive or negative values.

We thank the reviewer for pointing out the confusion about the homogeneous responses in one cluster. We clarified this part in the results, by adding “Recording from multiple IPCs at the same time uncovered that the activity of IPCs within a cluster was synchronized in some cases. For example, in fly #1 in the DAN activation experiment, the baseline activity pattern of the excited IPC cluster was already synchronized before the first activation (fly #1, cells 3-8). Furthermore, the excitation onset and duration during the activation of DANs was highly uniform in this cluster. However, in other flies, e.g. #2 and #3 in the DAN activation experiments, we did not observe this synchronicity. While all IPCs in the excited cluster displayed an excitatory response to the DAN activation in these flies, the onset and duration differed between individual IPCs. In addition, the IPCs also showed more variability in their baseline activity (Fig. 4F). These findings point towards a shared input that can lead to the synchronization of IPC activity in some clusters and time windows. One known such input is the behavioral state – flight strongly inhibits the activity of all IPCs with very short delays(22). The flies in our experiments were not flying, but this example illustrates the presence of strong, state-dependent inputs that can synchronize the IPC population activity.”

(4) In Figure 4J, no explanations of arrowheads, gray boxes, or asterisks are available in the legend.

We thank the reviewer for pointing out this omission. We added the missing information to the figure legend.

(5) "IPCs form distinct clusters." Is this cluster located closely each other or distant from one another?

We did not encounter a location-dependent relationship between the IPCs of one cluster in calcium imaging experiments, nor did the anatomical receptor mapping data or connectomics analysis give any indication for anatomical clusters. The location of individual IPC cell bodies is not stereotypical across flies. We clarified this point in the results by adding “IPCs form distinct functional clusters” and “However, we found no evidence in our anatomical data, calcium imaging experiments, or in the fly brain EM volume that these clusters are distinguishable based on IPC soma location in the pars intercerebralis.”

Author response:

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

Reviewer #1 (Public Review): 

Summary: 

The main conclusion of this manuscript is that the mediator kinases supporting the IFN response in Downs syndrome cell lines represent an important addition to understanding the pathology of this affliction. 

Strengths: 

Mediator kinase stimulates cytokine production. Both RNAseq and metabolomics clearly demonstrate a stimulatory role for CDK8/CDK19 in the IFN response. The nature of this role,  direct vs. indirect, is inferred by previous studies demonstrating that inflammatory transcription factors are Cdk8/19 substrates. The cytokine and metabolic changes are clear-cut and provide a potential avenue to mitigate these associated pathologies. 

Weaknesses: 

This study revealed a previously undescribed role for the CKM in splicing. The previous identification of splicing factors as substrates of CDK8/CDK19 is also intriguing. However, additional studies seem to be necessary in order to attach this new function to the CKM. As the authors point out, the changes in splicing patterns are relatively modest compared to other regulators. In addition, some indication that the proteins encoded by these genes exhibit reduced levels or activities would support their RNAseq findings. 

We have added new splicing data for the version of record. Specifically, we have added splicing data analysis for the "non-sibling" T21 cell line (±cortistatin A, t=4.5h) and for the sibling T21 line (±cortistatin A) at t=24h. The results are summarized in new Figure 5 – figure supplement 2. The data are in agreement with our prior data from the sibling T21 line ±CA at t=4.5h.  In particular, i) similar numbers of genes were impacted by splicing changes (alternative exon inclusion or alternative exon skipping) in CA-treated cells in the "non-sibling" T21 line compared with the sibling T21 line; ii) upon completion of a pathway analysis of these alternatively spliced genes, similar pathways were affected by CA in each case (non-sibling T21 vs. sibling T21), in particular those related to IFN signaling; iii) regarding the new t=24h timepoint for the sibling T21 line, similar numbers of genes were alternatively spliced (alternative exon inclusion or alternative exon skipping) in CA-treated cells compared with the 4.5h timepoint, and iv) the IPA results with the alternately spliced genes identified inflammatory signaling, mRNA processing, and lipid metabolism among other pathways, which broadly reflect the cytokine screen and metabolomics data in CA-treated cells (t=24h).

Additional evidence for CDK8/CDK19 regulation of splicing comes from our t=24h RNA-seq data in T21 cells ±CA.  GSEA results revealed down-regulation of many pathways related to RNA processing and splicing, suggesting that the splicing changes caused by Mediator kinase inhibition result from reduced expression of splicing regulators, at least at this longer timeframe. These results are summarized in new Figure 2 – figure supplement 2E. Collectively, the data shown in this article reveal a previously unidentified role for Mediator kinases as splicing regulators. We emphasize in the article, however, that the splicing effects of Mediator kinase inhibition appear modest, at least within the cell lines and timeframes of our experiments, especially when compared with CDK7 inhibition [Rimel et al. Genes Dev 2020 1452]. 

Seahorse analysis is normally calculated with specific units for oxygen consumption, ATP production, etc. It would be of interest to see the actual values of OCR between the D21 and T21 cell lines rather than standardizing the results. This will address the specific question about relative mitochondrial function between these cells. Reduced mitochondrial function has been associated with DS patients. Therefore, it would be important to know whether mitochondrial function is reduced in the T21 cells vs. the D21 control. Importantly for the authors' goal of investigating the use of CDK8/19 inhibitors in DS patients, does CA treatment reduce mitochondrial function to pathological levels? 

These are good points. We have addressed as follows.

(1) We have added a comparative analysis of Seahorse data for the sibling-matched T21 and D21 lines. As shown in new Figure 2 – figure supplement 4A-C, the T21 line shows higher basal levels of OCR and ECAR compared with D21. Although reviewer 1 states that "reduced mitochondrial function has been associated with DS patients" we are unaware of the study from which this conclusion was made. Our results are consistent with a Down syndrome mouse model study published last year [Sarver et al. eLife 2023 e86023]. We acknowledge that in this study, T21/D21 OCR levels varied in different tissues, but the majority of tissue types showed elevated OCR in T21, similar to our results in the human B-cells used here.

(2) Interestingly, CA treatment reduced OCR and ECAR in T21 cells (and D21), suggesting that Mediator kinase inhibition might normalize mitochondrial function (and ECAR) toward D21 levels. We show this comparison in new Figure 2 – figure supplement 4D-F. Indeed, CA treatment appears to normalize T21 mitochondrial function and ECAR toward D21 levels. Although this may suggest a therapeutic benefit, we emphasize that more experiments would be needed to make such claims with confidence. 

(3) We include a breakdown of mitochondrial parameters from Seahorse data in the bar plots shown in Figure 2–figure supplement 3. This includes ATP production, which shows reduced ATP levels in CA-treated T21 cells specifically.

(4) We have added Seahorse data for ECAR (extracellular acidification rate) in the siblingmatched D21 and T21 cells, ±CA. These results are shown in new Figure 2 – figure supplement 3D, and indicate that CA treatment reduces ECAR in both D21 and T21 cells. This result is consistent with a prior report that analyzed ECAR in CDK8 analog-sensitive HCT116 cells [Galbraith et al. Cell Rep 2017 1495].

Reviewer #2 (Public Review):

Summary: 

In this manuscript, Cozzolino et al. demonstrate that inhibition of the Mediator kinase CDK8 and its paralog CDK19 suppresses hyperactive interferon (IFN) signaling in Down syndrome (DS), which results from trisomy of chromosome 21 (T21). Numerous pathologies associated with DS are considered direct consequences of chronic IFN pathway activation, and thus hyperactive IFN signaling lies at the heart of pathophysiology. The collective interrogation of transcriptomics, metabolomics, and cytokine screens in sibling-matched cell lines (T21 vs D21) allows the authors to conclude that Mediator kinase inhibition could mitigate chronic, hyperactive IFN signaling in T21. To probe the functional outcomes of Mediator kinase inhibition, the authors performed cytokine screens, transcriptomic, and untargeted metabolomics. This collective approach revealed that Mediator kinases establish IFN-dependent cytokine responses at least in part through transcriptional regulation of cytokine genes and receptors. Mediator kinase inhibition suppresses cell responses during hyperactive IFN signaling through inhibition of pro- inflammatory transcription factor activity (anti-inflammatory effect) and alteration of core metabolic pathways, including upregulation of anti-inflammatory lipid mediators, which served as ligands for specific nuclear receptors and downstream phenotypic outcomes (e.g., oxygen consumption). These data provided a mechanistic link between Mediator kinase activity and nuclear receptor function. Finally, the authors also disclosed that Mediator kinase inhibition alters splicing outcomes. 

Overall, this study reveals a mechanism by which Mediator kinases regulate gene expression and establish that its inhibition antagonizes chronic IFN signaling through collective transcriptional,  metabolic, and cytokine responses. The data have implications for DS and other chronic inflammatory conditions, as Mediator kinase inhibition could potentially mitigate pathological immune system hyperactivation. 

Strengths: 

(1) One major strength of this study is the mechanistic evidence linking Mediator kinases to hyperactive IFN signaling through transcriptional changes impacting cell signaling and metabolism.  (2) Another major strength of this study is the use of sibling-matched cell lines (T21 vs D21) from various donors (not just one sibling pair), and further cross-referencing with data from large cohorts, suggesting that part of the data and conclusions are generalizable. 

(3) Another major strength of this study is the combined experimental approach including transcriptomics, untargeted metabolomics, and cytokine screens to define the mechanisms underlying suppression of hyperactive interferon signaling in DS upon Mediator kinase inhibition.  (4) Another major strength of this study is the significance of the work to DS and its potential impact on other chronic inflammatory conditions. 

Weakness: 

(1) Genetic evidence linking the mentioned nuclear receptors to activation of an anti-inflammatory program upon Mediator kinase inhibition could improve the definition of the mechanism and overall impact of the work. 

Existing data from other studies, some of which are cited in the article, have linked PPAR and LXR to lipid biosynthesis and anti-inflammatory signaling cascades. We assume that reviewer 2 is suggesting knockdown and/or degron depletion of specific nuclear receptors, to compare/contrast the effect of CA on IFN responses in T21 and D21 cells. Such experiments would help de-couple the NR-specific contributions from other CA-dependent effects. We consider these experiments important next steps for this project, but beyond the scope of this study. That said, we anticipate that data from such experiments might be challenging to interpret, given the complex and inter-connected cascade of transcriptional and metabolic changes that would result from PPAR or LXR depletion.  

(2) Page 5 states that "Mediator kinases broadly regulate cholesterol and fatty acid biosynthesis and this was further confirmed by the metabolomics data", but a clear mechanistic explanation was lacking. Likewise, the data suggest but do not prove, that altered lipid metabolites influence the function of nuclear receptors to regulate an anti-inflammatory program in response to Mediator kinase inhibition (p. 6), despite the fact the gene expression changes elicited by Mediator kinase inhibition tracked with downstream metabolic changes. 

We have clarified the text on page 5 to address this comment. Specifically, we note that CA treatment increases expression of FA metabolism and cholesterol metabolism genes in T21 cells under basal conditions, and the genes affected are shown in Figure 2–figure supplement 1E. Thus, the mechanistic explanation is that Mediator kinases cause elevated levels of FA and cholesterol metabolites via changes in expression of FA and cholesterol biosynthesis genes (at least in part). We further address the mechanism with the PRO-seq data and TFEA results in Figure 6; in particular, p53 activity is rapidly suppressed in CA-treated T21 cells (t=75min), and this alone is sufficient to activate SREBP [Moon et al. Cell 2019 564]. CA-dependent activation of SREBP target genes is a dominant feature in the T21 RNA-seq data (t=4.5h).

We agree with the second point raised by reviewer 2, that our data suggest but do not prove nuclear receptor function is altered by CA treatment. We do cite papers that have provided good evidence that the metabolites elevated in CA-treated cells are NR ligands and activate their target genes. Additional experiments to address this question might involve targeted depletion of select metabolites via inhibition of key biosynthetic enzymes. We consider these experiments beyond the scope of this already expansive article. That said, it will be challenging to conclusively demonstrate clear cause-effect relationships (e.g. to demonstrate whether select metabolites altered by CA treatment directly alter PPARA function), given i) the myriad transcriptional and metabolic changes caused by CA treatment, coupled with the fact that ii) the CA-dependent lipid metabolite changes are spread out across chemically distinct NR agonists (e.g. endocannabinoids, oleamide, or cholesterol metabolites such as desmosterol), and iii) NR activation can occur via multiple different metabolites. 

(3) The figures are outstanding but dense. 

Thank you. We have done our best to represent the results clearly and within the publication guidelines. There was an enormous amount of data to summarize for this article.

(4) Figure 6 (PRO-Seq). The authors refer to pro-inflammatory TFs (e.g. NF-kB/RelA). It is not clear whether the authors have specifically examined TF binding at enhancers or more broadly at every region occupied by the interrogated TFs? 

This is a good point. Our analysis (TFEA) only identified the TFs whose activity was changing in CA-treated cells. It did not distinguish where these TFs were bound (enhancers vs. promoters). We completed a modified TFEA by separating enhancer TFs vs. promoter TFs. The results showed a preference for CA-dependent suppression of enhancer-bound TFs. This result is consistent with the general observation that stimulus-response transcription is controlled by enhancer-bound TFs (e.g. Kim et al. Nature 2010 182; Azofeifa et al. Genome Res 2018 334; Jones et al. bioRxiv 2024 585303). However, our TFEA enhancer/promoter analysis is preliminary and more work would be needed to address this comment in a rigorous way. Therefore, we did not include this analysis in the revision.  

Reviewing Editor Comments: 

Main suggestions for improvement: 

(1) Provide additional information about the mechanistic basis for the changes in lipid levels observed on kinase inhibition. 

We have changed the text to better emphasize that the mechanistic basis involves i) gene expression changes resulting from Mediator kinase inhibition (e.g. Fig 2 – figure supplement 1D, E, Fig 2 – figure supplement 2B, Fig 2 – figure supplement 4B-D); ii) activation of SREBP and PPAR and LXR, based upon IPA results with RNA-seq data (e.g. Fig 2B, Fig 2 – figure supplement 1F, Fig 2 – figure supplement 2D, Fig 2 – figure supplement 4E; Fig 3E), and iii) rapid CAdependent suppression of p53 function (Fig 6A), which will activate SREBP (Moon et al. Cell 2019 564).

(2) Provide direct genetic evidence that the nuclear receptors are activated by the lipid changes to mediate an anti-inflammatory program in response to Mediator kinase inhibition. 

This is an excellent question but we consider it beyond the scope of this already expansive study. That said, we cite several papers in the article that demonstrate that the lipids we observe elevated in CA-treated cells i) directly bind PPAR or LXR and ii) activate their TF function. We also note that the anti-inflammatory impacts of Mediator kinase inhibition are broad, affecting distinct gene sets through transcriptional changes, metabolites, and cytokines. Any NR-specific contributions could be challenging to de-couple from CA-dependent effects using knockdown or depletion methods, given the compensatory responses that would result. 

(3) Improve/expand the evidence that Mediator kinase inhibition confers reduced mitochondrial function. 

We have added new Seahorse data for sibling-matched D21 and T21 cells (±CA) for the version of record. Our prior results showed reduced mitochondrial function and OCR in CA-treated T21 cells.  We have added data that compares D21 and T21 mitochondrial function. As shown in new Figure 2 – figure supplement 4A-C, the T21 line shows higher basal levels of OCR and ECAR compared with D21. These results are consistent with a Down syndrome mouse model study published last year [Sarver et al. eLife 2023 e86023]. When we compare CA-treated T21 with D21 cells, mitochondrial respiration and OCR are similar, suggesting that Mediator kinase inhibition might normalize mitochondrial function (and ECAR) toward D21 levels. We show this comparison in new Figure 2 – figure supplement 4D-F. Although this may suggest a therapeutic benefit, we emphasize that more experiments would be needed to make such claims with confidence. 

(4) Determine whether mitochondrial function is reduced in the T21 cells vs. the D21 controls and whether kinase inhibition with the inhibitor reduces mitochondrial function to pathological levels.

For the version of record, we have added a direct comparison of mitochondrial parameters and OCR in the sibling-matched D21/T21 lines. The data show that T21 cells have higher OCR compared with D21. These results are consistent with a Down syndrome mouse model study published last year [Sarver et al. eLife 2023 e86023]. Our results also indicate that CA treatment brings OCR and other "mitochondrial parameters" in T21 cells toward D21 levels, as noted above.

(5) Consider whether the CDK8/19 inhibitor has off-target effects that would lessen its therapeutic value. 

We chose cortistatin A (CA) for this project because it is the most potent and selective inhibitor available for targeting CDK8/CDK19.  Initial published reports suggested off-target effects (Cee et al. Angew Chem IEE 2009), but these experiments used binding assays against the kinase protein alone, and did not measure binding or inhibition with biologically relevant, active kinase complexes.  Kinome-wide screens involving native, active kinase complexes showed no evidence of off-target effects for cortistatin A, even at concentrations 5000-times the measured KD (Pelish et al. Nature 2015).  See Author response image 1.

Related to CA therapeutic value, that is an important issue but beyond the scope of this study. We consider CA a valuable chemical probe, to use as a means to define CDK8/CDK19-dependent functions in cell line models. As a chemical probe, we consider CA the "best-in-class" Mediator kinase inhibitor, based upon all available data (Clopper & Taatjes Curr Opin Chem Biol 2022 102186).

That said, we understand the concern about off-target effects, which can never be ruled out with a chemical inhibitor. We include quantitative western data (Fig 1 – figure supplement 1A) that compares CA with a structurally distinct CDK8/CDK19 inhibitor, CCT251545. The data show that, as expected, CA (100nM) and CCT251545 (250nM) similarly inhibit STAT1 S727 phosphorylation in IFN-stimulated cells. The samples were pre-treated with inhibitor for 30 minutes prior to IFNg and collected 45 minutes after IFNg treatment. 

We did not complete any experiments with knockouts or kinasedead alleles primarily because knockouts or kinase-dead alleles are not reliable comparisons for chemical inhibition because of the different time frames involved. For example, there will be genetic compensation in edited cell lines (Rossi/Stanier Nature 2015 230) and we and others have shown that there are major differences between kinase protein loss through knockdown or knockout methods vs. rapid inhibition with small molecules (e.g. Poss et al. Cell Rep 2016 436; Sooraj et al. Mol Cell 2022 123). 

Author response image 1.

Information about cortistatin A. A) KiNativ kinome screen from HEK293 lysates. CA blocked capture of only CDK8/CDK19 in this MSbased assay, among over 200 kinases detected. B) Equilibrium binding constants and kinetics for CA. C) CA structure; note the dimethylamine is protonated at physiological pH, and forms a pi-cation interaction with W105 (crystal structure, panel D). Only CDK8 and CDK19 have an aromatic residue (W) at this position, providing a structural basis for high selectivity.

(6) Improve the presentation of the splicing data and better discuss how the splicing alterations may be contributing to the disease phenotype. 

We have added new splicing data for the version of record. Specifically, we have added splicing data analysis for the "non-sibling" T21 cell line (±cortistatin A, t=4.5h) and for the sibling T21 line (±cortistatin A) at t=24h. The results are summarized in new Figure 5 – figure supplement 2. The data are in agreement with our prior results from the sibling T21 line ±CA at t=4.5h.  In particular, i) similar numbers of genes were impacted by splicing changes (alternative exon inclusion or alternative exon skipping) in CA-treated cells in the "non-sibling" T21 line compared with the sibling T21 line; ii) upon completion of a pathway analysis of these alternatively spliced genes, similar pathways, including IFN signaling pathways, were affected by CA in each case (non-sibling T21 vs. sibling T21); iii) regarding the new t=24h timepoint for the sibling T21 line, similar numbers of genes were alternatively spliced (alternative exon inclusion or alternative exon skipping) in CA-treated cells compared with the 4.5h timepoint, and iv) the IPA results with the alternately spliced genes identified inflammatory signaling, mRNA processing, nucleotide and lipid metabolism among other pathways, which broadly reflect the cytokine screen and metabolomics data in CA-treated cells (t=24h). 

Additional evidence for CDK8/CDK19 regulation of splicing comes from our t=24h RNA-seq data in T21 cells ±CA.  GSEA results from sibling T21 cells ±CA revealed down-regulation of many pathways related to RNA processing and splicing (RNA-seq data, t=24h), suggesting that the splicing changes caused by Mediator kinase inhibition result from reduced expression of splicing regulators, at least at longer timeframes. These results are summarized in new Figure 2 – figure supplement 2E.  

Related to how splicing alterations may be contributing to the CA-dependent effects and their potential therapeutic implications, this is an interesting question but open-ended. It will not be straightforward to link specific splicing changes to possible therapeutic outcomes, especially given that there are hundreds of genes affected and because the effects are modest (i.e. not all-ornothing).

Reviewer #1 (Recommendations For The Authors): 

The findings that CA treatment leads to upregulation of as many genes are downregulated is consistent with previous studies of a 50:50 role for the CKM. However, most previous studies utilized knockout alleles or knockdown approaches. As the authors demonstrated in a previous study, CA inhibits kinase activity without changing CDK8 levels. Does this indicate that the kinase activity of Cdk8/19 is required for transcriptional repression? Previous in vitro studies suggested that Cdk8/19-dependent repression was independent of their kinase activity. The authors should comment on this. 

This is a challenging question to address, because the answer will depend on the timing of the experiment and the experimental context.  The short answer is that the kinase activity of CDK8/19 will activate some genes and reduce expression of others, at least in part because CDK8/19 phosphorylate TFs, which drive global gene expression programs. TF phosphorylation by CDK8/19 appears to activate some genes and repress others (e.g. STAT1 S727A example from Steinparzer et al. Mol Cell 2019 485), at least based upon RNA-seq data, but this doesn't measure the immediate effects on the transcriptome. It is true that kinase activity isn't required to block pol II incorporation into the PIC (Knuesel et al. Genes Dev 2009 439). This is a kinase-independent function of the module; MKM-Mediator binding will block Mediator-pol II interaction and therefore block PIC assembly and pol II initiation (Knuesel 2009; Ebmeier & Taatjes PNAS 2010 11283). The kinase-independent functions of CDK8/19 were not a focus of the work described here. We only focus on Mediator kinase activity. We also do not focus on potential effects on RNAPII initiation or PIC assembly, although these are important peripheral topics. 

Descriptors are less useful as the reader must go back to reconstruct the experiment: "Although metabolites were measured 24h after CA treatment, these data suggest that altered lipid metabolites influence LXR and PPAR function". Does "altered" mean the lipid concentrations were up or down? Similarly, lipids that "influenced" LXR function - were they stimulatory or inhibitory?    

Good point. Where possible, we used more accurate language when describing CAdependent changes.

I found many sections in the text confusing. For example: Figure 3. Mediator kinase inhibition antagonizes IFNγ transcriptional responses in T21 and D21. It takes a while to unpack this figure title. Instead of the double negative, the authors could simply state that "Mediator kinase is required for IFN-dependent transcriptional activation". Describing the protein activity, versus the drug-induced phenotype, can often clarify complicated scenarios. 

Good idea. We have edited the text to eliminate some but not all of these double negatives. In some cases we prefer to describe the consequence of kinase inhibition.

Reviewer #2 (Recommendations For The Authors): 

(1) The splicing data analysis is compelling, but not well integrated into the overall story and it cuts the storytelling logic in the Abstract. The authors could consider better integrating the large amount of data generated and better explaining how it relates to the various aspects of the proposed model (transcriptional, metabolism) to help improve potential cause-and-effect outcomes.     -

We agree. The large amount of data, combined with the different experimental approaches, makes it a challenge to summarize the data in a concise way. We have done our best to organize the results in a logical and clear manner. To address this comment, we have gone through the text and re-organized where possible, and we have edited the abstract. We have added new splicing data and the splicing results are now better integrated (in our opinion) in part because of the pathway results from the t=24h ±CA RNA-seq data, which show major reductions in gene sets related to splicing and RNA processing.

(2) The manuscript could improve its readability by providing specific details throughout. Examples include i) explaining why and what 29 cytokines were chosen for the screen (p. 3, p. 4) ii) providing major data analysis conclusions to the cytokine screen part (p. 3)  iii) expanding the conclusions to the metabolic pathway analysis (p. 4) iv) being more precise when referring to T21-specific changes (up or down?) (p 4), and "significantly altered" by CA treatment in T21 cells (up or down?) (p. 5). 

Good points. We have edited the text to address these comments. Please note that the 29 cytokines refers to a different study (Malle et al. Nature 2023) and we had no role in selecting the cytokines. Our screen involved 105 cytokines that were arrayed as part of a commercially available panel.

(3) The figures are outstanding but dense (e.g., Figure 1b, can any simplification and/or highlighting be done to underscore important features?). Some panels are illegible (e.g. Figure 1- supplement Figure 2a and b). The authors could improve data presentation. For example, the Venn diagrams (e.g., Figure 2f) are hard to quickly digest. Can the authors find a better way to highlight important data (e.g., hard to distinguish the meaning of font bolding from italics)?   

Thank you for these suggestions. Regarding Figure 1B, we simplified the metabolic pathways to emphasize the biochemicals that specifically relate to this study. We decided against highlighting specific metabolites beyond this simplification, because in our opinion it causes as many problems as it solves. Where possible, we have enlarged the panels with hard-to-read text; thank you for the suggestion. For the Venn diagrams, they convey a large amount of information in a single panel: increased or decreased gene expression in T21 or D21, cytokine genes or cytokine receptors, and gene expression convergence or divergence compared with protein levels from cytokine screens.  There is a different way to display the results, but it would involve generating more data panels to parse out the results. This could be considered better, but we opted for something that is more information-rich that requires only a single data panel. Given the large amount of data already shown, we hope the reviewer can understand this choice.

Author Response

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

Public Reviews:

Reviewer #2 (Public Review):

Summary:

This paper tests the idea that schooling can provide an energetic advantage over solitary swimming. The present study measures oxygen consumption over a wide range of speeds, to determine the differences in aerobic and anaerobic cost of swimming, providing a potentially valuable addition to the literature related to the advantages of group living.

Response: Thank you for the positive comments.

Strengths:

The strength of this paper is related to providing direct measurements of the energetics (oxygen consumption) of fish while swimming in a group vs solitary. The energetic advantages of schooling has been claimed to be one of the major advantages of schooling and therefore a direct energetic assessment is a useful result.

Response: Thank you for the positive comments.

Weaknesses:

1) Regarding the fish to water volume ratio, the arguments raised by the authors are valid. However, the ratio used is still quite high (as high as >2000 in solitary fish), much higher than that recommended by Svendsen et al (2006). Hence this point needs to be discussed in the ms (summarising the points raised in the authors' response)

Response: Thank you for the comments. We have addressed this point in the previous comments. In short, our ratio is within the range of the published literature. We conducted the additional signal-to-noise analysis for quality assurance.

2) Wall effects: Fish in a school may have been swimming closer to the wall. The fact that the convex hull volume of the fish school did not change as speed increased is not a demonstration that fish were not closer to the wall, nor is it a demonstration that wall effect were not present. Therefore the issue of potential wall effects is a weakness of this paper.

Response: Thank you for the comments. We have addressed this point in the previous comments. We provided many other considerations in addition to the convex hull volume. In particular, our boundary layer is < 2.5mm, which was narrower than the width of the giant danio of ~10 mm.

3) The authors stated "Because we took high-speed videos simultaneously with the respirometry measurements, we can state unequivocally that individual fish within the school did not swim closer to the walls than solitary fish over the testing period". This is however not quantified.

Response: Thank you for the comments. We have addressed this point in the previous comments. We want to note that the statement in the response letter is to elaborate the discussion points, but not stated as data in the manuscript. The bottom line is very few studies used PIV to quantify the thickness of the boundary layer like what we did in our experiment.

4) Statistical analysis. The authors have dealt satisfactorily with most of the comments.

However :

(a) the following comment has not been dealt with directly in the ms "One can see from the graphs that schooling MO2 tends to have a smaller SD than solitary data. This may well be due to the fact that schooling data are based on 5 points (five schools) and each point is the result of the MO2 of five fish, thereby reducing the variability compared to solitary fish."

(b) Different sizes were used for solitary and schooling fishes. The authors justify using larger fish as solitary to provide a better ratio of respirometer volume to fish volume in the tests on individual fish. However, mass scaling for tail beat frequency was not provided. Although (1) this is because of lack of data for this species and (2) using scaling exponent of distant species would introduce errors of unknown magnitude, this is still a weakness of the paper that needs to be acknowledged here and in the ms.

Response: Thank you for the comments. We have addressed both points in the previous comments and provided comprehensive discussions. We also stated the caveats in the method section of the manuscript.

Reviewer #3 (Public Review):

Zhang and Lauder characterized both aerobic and anaerobic metabolic energy contributions in schools and solitary fishes in the Giant danio (Devario aequipinnatus) over a wide range of water velocities. By using a highly sophisticated respirometer system, the authors measure the aerobic metabolisms by oxygen uptake rate and the non-aerobic oxygen cost as excess post-exercise oxygen consumption (EPOC). With these data, the authors model the bioenergetic cost of schools and solitary fishes. The authors found that fish schools have a J-shaped metabolism-speed curve, with reduced total energy expenditure per tail beat compared to solitary fish. Fish in schools also recovered from exercise faster than solitary fish. Finally, the authors conclude that these energetic savings may underlie the prevalence of coordinated group locomotion in fish.

The conclusions of this paper are mostly well supported by data.

Response: Thank you for the positive comments.

Recommendations for the authors:

Reviewer #3 (Recommendations For The Authors):

I have read carefully the revised version of the manuscript and would like to thank the authors for addressing all my comments/suggestions.

I have no additional comments/suggestions. Now, I strongly believe that this manuscript deserves to be published in eLife.

Response: Thank you for the positive comments.

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

General responses

Many thanks to the reviewers and editors for their very helpful comments on our manuscript. Below we respond (in blue text) to each of the reviewer comments, both the public ones and the more detailed individual comments in the second part of each review. In some cases, we consider these together where the same point is made in both sets of comments. We have made several changes to the manuscript in response to reviewer suggestions, and we respond in detail to the comments of reviewer #2 who feels that we have overstated the significance of our manuscript and suggests several relevant literature references. We prepared a table summarizing these references and why they differ substantially from the approach taken in our paper here.

Overall, we would like to emphasize to both reviewers and readers of this response document that previous studies of fish schooling dynamics (or collective movement of vertebrates in general, see Commentary Zhang & Lauder 2023 J. Exp. Biol., doi:10.1242/jeb.245617) have not considered a wide speed range and thus the importance of measuring EPOC (excess post-exercise oxygen consumption) as a key component of energy use. Quantifying both aerobic and non-aerobic energy use allows us to calculate the total energy expenditure (TEE) which we show differs substantially and, importantly, non-linearly with speed between schools and measurements on solitary individuals. Comparison between school total energy use and individual total energy use are critical to understanding the dynamics of schooling behaviour in fishes.

The scope of this study is the energetics of fish schools. By quantifying the TEE over a wide range of swimming speeds, we also show that the energetic performance curve is concave upward, and not linear, and how schooling behaviour modifies this non-linear relationship.

In addition, one key implication of our results is that kinematic measurements of fish in schools (such as tail beat frequency) are not a reliable metric by which to estimate energy use. Since we recorded high-speed video simultaneously with energetic measurements, we are able to show that substantial energy savings occur by fish in schools with little to no change in tail beat frequency, and we discuss in the manuscript the various fluid dynamic mechanisms that allow this. Indeed, studies of bird flight show that when flying in a (presumed) energy-saving V-formation, wing beat frequency can actually increase compared to flying alone. We believe that this is a particularly important part of our findings: understanding energy use by fish schools must involve actual measurements of energy use and not indirect and sometimes unreliable kinematic measurements such as tail beat frequency or amplitude.

Reviewer #1 (Public Review):

Summary:

In the presented manuscript the authors aim at quantifying the costs of locomotion in schooling versus solitary fish across a considerable range of speeds. Specifically, they quantify the possible reduction in the cost of locomotion in fish due to schooling behavior. The main novelty appears to be the direct measurement of absolute swimming costs and total energy expenditure, including the anaerobic costs at higher swimming speeds.

In addition to metabolic parameters, the authors also recorded some basic kinematic parameters such as average distances or school elongation. They find both for solitary and schooling fish, similar optimal swimming speeds of around 1BL/s, and a significant reduction in costs of locomotion due to schooling at high speeds, in particular at ~5-8 BL/s.

Given the lack of experimental data and the direct measurements across a wide range of speeds comparing solitary and schooling fish, this appears indeed like a potentially important contribution of interest to a broader audience beyond the specific field of fish physiology, in particular for researchers working broadly on collective (fish) behavior.

Response: Thank you for seeing the potential implications of this study. We also believe that this paper has broader implications for collective behaviour in general, and outline some of our thinking on this topic in a recent Commentary article in the Journal of Experimental Biology: (Zhang & Lauder 2023 doi:10.1242/jeb.245617). Understanding the energetics of collective behaviours in the water, land, and air is a topic that has not received much attention despite the widespread view that moving as a collective saves energy.

Strengths:

The manuscript is for the most part well written, and the figures are of good quality. The experimental method and protocols are very thorough and of high quality. The results are quite compelling and interesting. What is particularly interesting, in light of previous literature on the topic, is that the authors conclude that based on their results, specific fixed relative positions or kinematic features (tail beat phase locking) do not seem to be required for energetic savings. They also provide a review of potential different mechanisms that could play a role in the energetic savings.

Response: Thank you for seeing the nuances we bring to the existing literature and comment on the quality of the experimental method and protocols. Despite a relatively large literature on fish schooling based on previous biomechanical research, our studies suggest that direct measurement of energetic cost clearly demonstrates the energy savings that result from the sum of different fluid dynamic mechanisms depending on where fish are, and also emphasizes that simple metrics like fish tail beat frequency do not adequately reflect energy savings during collective motion.

Weaknesses:

A weakness is the actual lack of critical discussion of the different mechanisms as well as the discussion on the conjecture that relative positions and kinematic features do not matter. I found the overall discussion on this rather unsatisfactory, lacking some critical reflections as well as different relevant statements or explanations being scattered across the discussion section. Here I would suggest a revision of the discussion section.

Response: The critical discussion of the different possible energy-saving mechanisms is indeed an important topic. We provided a discussion about the overall mechanism of ‘local interactions’ in the first paragraph of “Schooling Dynamics and energy conservation”. To clarify, our aim with Figure 1 is to introduce the current mechanisms proposed in the existing engineering/hydrodynamic literature that have studied a number of possible configurations both experimentally and computationally. Thank you for the suggestion of better organizing the discussion to critically highlight different mechanisms that would enable a dynamic schooling structure to still save energy and why the appendage movement frequency does not necessarily couple with the metabolic energy expenditure. Much of this literature uses computational fluid dynamic models or experiments on flapping foils as representative of fish. This exact issue is of great interest to us, and we are currently engaged in a number of other experiments that we hope will shed light on how fish moving in specific formations do or don’t save energy.

Our aim in presenting Figure 1 at the start of the paper was to show that there are several ways that fish could save energy when moving in a group as shown by engineering analyses, but before investigating these various mechanisms in detail we first have to show that fish moving in groups actually do save energy with direct metabolic measurements. Hence, our paper treats the various mechanisms as inspiration to determine experimentally if, in fact, fish in schools save energy, and if so how much over a wide speed range. Our focus is to experimentally determine the performance curve that shows energy use as speed increases, for schools compared to individuals. Therefore, we have elected not to go into detail about these different hydrodynamic mechanisms in this paper, but rather to present them as a summary of current engineering literature views and then proceed to document energy savings (as stated in the second last paragraph of Introduction). We have an Commentary paper in the Journal of Experimental Biology that addresses this issue generally, and we are reluctant to duplicate much of that discussion here (Zhang & Lauder 2023 doi:10.1242/jeb.245617). We are working hard on this general issue as we agree that it is very interesting. We have revised the Introduction (second last paragraph of Introduction) and Discussion (first paragraph of Discussion) to better indicate our approach, but we have not added any significant discussion of the different hydrodynamic energy saving proposals as we believe that it outside the scope of this first paper and more suitable as part of follow-up studies.

Also, there is a statement that Danio regularly move within the school and do not maintain inter-individual positions. However, there is no quantitative data shown supporting this statement, quantifying the time scales of neighbor switches. This should be addressed as core conclusions appear to rest on this statement and the authors have 3d tracks of the fish.

Response: Thank you for pointing out this very important future research direction. Based on our observations and the hypothesized mechanisms for fish within the school to save energy (Fig. 1), we have been conducting follow-up experiments to decipher the multiple dynamic mechanisms that enable the fish within the school to save energy. Tracking the 3D position of each individual fish body in 3D within the fish school has proven difficult. We currently have 3D data on the nose position obtained simultaneously with the energetic measurements, but we do not have full 3D fish body positional data. Working with our collaborators, we are developing a 3-D tracking algorithm that will allow us to quantify how long fish spend in specific formations, and we currently have a new capability to record high-speed video of fish schooling moving in a flow tank for many hours (see our recent perspective by Ko et al., 2023 doi.org/10.1098/rsif.2023.0357). The new algorithms and the results will be published as separate studies and we think that these ongoing experiments are outside the scope of the current study with its focus on energetics. Nevertheless, the main point of Fig. 1 is to provide possible mechanisms to inspire future studies to dissect the detailed hydrodynamic mechanisms for energy saving, and the points raised by this comment are indeed extremely interesting to us and our ongoing experiments in this area. We provide a statement to clarify this point in the 1st paragraph of “Schooling dynamics and energy conservation” section.

Further, there is a fundamental question on the comparison of schooling in a flow (like a stream or here flow channel) versus schooling in still water. While it is clear that from a pure physics point of view that the situation for individual fish is equivalent. As it is about maintaining a certain relative velocity to the fluid, I do think that it makes a huge qualitative difference from a biological point of view in the context of collective swimming. In a flow, individual fish have to align with the external flow to ensure that they remain stationary and do not fall back, which then leads to highly polarized schools. However, this high polarization is induced also for completely non-interacting fish. At high speeds, also the capability of individuals to control their relative position in the school is likely very restricted, simply by being forced to put most of their afford into maintaining a stationary position in the flow. This appears to me fundamentally different from schooling in still water, where the alignment (high polarization) has to come purely from social interactions. Here, relative positioning with respect to others is much more controlled by the movement decisions of individuals. Thus, I see clearly how this work is relevant for natural behavior in flows and that it provides some insights on the fundamental physiology, but I at least have some doubts about how far it extends actually to “voluntary” highly ordered schooling under still water conditions. Here, I would wish at least some more critical reflection and or explanation.

Response: We agree completely with this comment that animal group orientations in still fluid can have different causes from their locomotion in a moving fluid. We very much agree with the reviewer that social interactions in still water, which typically involve low-speed locomotion and other behaviours such as searching for food by the group, can be important and could dictate fish movement patterns. In undertaking this project, we wanted to challenge fish to move at speed, and reasoned that if energy savings are important in schooling behaviour due to hydrodynamic mechanisms, we should see this when fish are moving forward against drag forces induced by fluid impacting the school. Drag forces scale as velocity squared, so we should see energy savings by the school, if any, as speed increases.

We also quantified fish school swimming speeds in the field from the literature and presented a figure showing that in nature fish schools can and do move at considerable speeds. This figure is part of our overview on collective behaviour recently in J. Exp. Biol. (Zhang & Lauder 2023 doi:10.1242/jeb.245617). It is only by studying fish schools moving over a speed range that we can understand the performance curve relating energy use to swimming speed. Indeed, we wonder if fish moving in still water as a collective versus as solitary individuals would show energy savings at all. We now provided the justification for studying fish schooling in moving fluids in the second and third paragraph of the Introduction. When animals are challenged hydrodynamically (e.g. at higher speed), it introduces the need to save energy. Movement in still water lacks the need for fish to save energy. When fish do not need to save locomotor energy in still water, it is hard to justify why we would expect to observe energy saving and related physiological mechanisms in the first place. As the reviewer said, the ‘high polarization in still water has to come purely from social interactions’. Our study does not dispute this consideration, and indeed we agree with it! In our supplementary materials, we acknowledged the definitions for different scenarios of fish schooling can have different behavioural and ecological drivers. Using these definitions, we explicitly stated, in the introduction, that our study focuses on active and directional schooling behaviour to understand the possible hydrodynamic benefits of energy expenditure for collective movements of fish schools. By stating the scope of our study at the outset, we hope that this will keep the discussion focused on the energetics and kinematics of fish schools, without unnecessarily addressing other many possible reasons for fish schooling behaviours in the discussion such as anti-predator grouping, food searching, or reproduction as three examples.

As this being said, we acknowledge (in the 2nd paragraph of the introduction) that fish schooling behaviour can have other drivers when the flow is not challenging. Also, there are robotic-&-animal interaction studies and computational fluid dynamic simulation studies (that we cited) that show individuals in fish schools interact hydrodynamically. Hydrodynamic interactions are not the same as behaviour interactions, but it does not mean individuals within the fish schooling in moving flow are not interacting and coordinating.

Related to this, the reported increase in the elongation of the school at a higher speed could have also different explanations. The authors speculate briefly it could be related to the optimal structure of the school, but it could be simply inter-individual performance differences, with slower individuals simply falling back with respect to faster ones. Did the authors test for certain fish being predominantly at the front or back? Did they test for individual swimming performance before testing them in groups together? Again this should be at least critically reflected somewhere.

Response: Thank you for raising this point. If the more streamlined schooling structure above 2 BL/s is due to the weaker individuals not catching up with the rest of the school, we would expect the weaker individuals to quit swimming tests well before 8 BL/s. However, we did not observe this phenomenon. Although we did not specifically test for the two questions the reviewer raises here, our results suggest that inter-individual variation in the swimming performance of giant Danio is not at the range of 2 to 8 BL/s (a 400% difference). While inter-individual differences certainly exist, we believe that they are small relative to the speeds tested as we did not see any particular individuals consistently unable to keep up with the school or certain individuals maintaining a position near the back of the school. As this being said, we provide additional interpretations for the elongated schooling structure at the end of the 2nd paragraph of the “schooling dynamics and energy conservation” section.

Reviewer #1 (Recommendations For The Authors):

Line 58: The authors write "How the fluid dynamics (...) enable energetic savings (...)". However, the paper focuses rather on the question of whether energetic savings exist and does not enlighten us on the dominant mechanisms. Although it gives a brief overview of all possible mechanisms, it remains speculative on the actual fluid dynamical and biomechanical processes. Thus, I suggest changing "How" to "Whether".

Response: Great point! We changed “How” to “Whether”.

Lines 129-140: In the discussion of the U-shaped aerobic rate, there is no direct comparison of the minimum cost values between the schooling and solitary conditions. Only the minimum costs during schooling are named/discussed. In addition to the data in the figure, I suggest explicitly comparing them as well for full transparency.

Response: Thanks for raising this point. We did not belabor this point because there was no statistical significance. As requested, we added a statement to address this with statistics in the 1st paragraph of the Results section.

Line 149: The authors note that the schooling fish have a higher turning frequency than solitary fish. Here, a brief discussion of potential explanations would be good, e.g. need for coordination with neighbors -> cost of schooling.

Response: Thank you for the suggestion. In the original version of the manuscript, we discussed that the higher turning frequency could be related to higher postural costs for active stability adjustment at low speeds. As requested, we now added that high turn frequency can relate to the need for coordination with neighbours in the last paragraph of the “Aerobic metabolic rate–speed curve of fish schools” section. As indicated above, the suspected costs of coordination did not result in higher costs of schooling at the lower speed (< 2 BL s-1, where the turn frequency is higher).

Line 151: The authors discuss the higher maximum metabolic rate of schooling fish as a higher aerobic performance and lower use of aerobic capacity. This may be confusing for non-experts in animal physiology and energetics of locomotion. I recommend providing somewhere in a paper an additional explanation to clarify it to non-experts. While lines 234-240 and further below potentially address this, I found this not very focused or accessible to non-experts. Here, I suggest the authors consider revisions to make it more comprehensible to a wider, interdisciplinary audience.

Response: We agree with the reviewer that the difference between maximum oxygen uptake and maximum metabolic rate can be confusing. In fact, among animal physiologists, these two concepts are often muddled. One of the authors is working on an invited commentary from J. Exp. Biol. to clearly define these two concepts. We have made the language in the section “Schooling dynamics enhances aerobic performance and reduces non-aerobic energy use” more accessible to a general audience. In addition, the original version presented the relevant framework in the first and the second paragraphs of the Introduction when discussing aerobic and non-aerobic energy contribution. In brief, when vertebrates exhibit maximum oxygen uptake, they use aerobic and non-aerobic energy contributions that both contribute to their metabolic rate. Therefore, the maximum total metabolic rate is higher than the one estimated from only maximum oxygen uptake. We used the method presented in Fig. 3a to estimate the maximum metabolic rate for metabolic energy use (combining aerobic and non-aerobic energy use). In kinesiology, maximum oxygen uptake is used to evaluate the aerobic performance and energy use of human athletes is estimated by power meters or doubly labelled water.

Line 211: The authors write that Danio regularly move within the school and do not maintain inter-individual positions. Given that this is an important observation, and the relative position and its changes are crucial to understanding the possible mechanisms for energetic savings in schools, I would expect some more quantitative support for this statement, in particular as the authors have access to 3d tracking data. For example introducing some simple metrics like average time intervals between swaps of nearest neighbors, possibly also resolved in directions (front+back versus right+left), should provide at least some rough quantification of the involved timescales, whether it is seconds, tens of seconds, or minutes.

Response: As responded in the comment above, 3-D tracking of both body position and body deformation of multiple individuals in a school is not a trivial research challenge and we have ongoing research on this issue. We hope to have results on the 3D positions of fish in schools soon! For this manuscript, we believe that the data in Figure 4E which shows the turning frequency of fish in schools and solitary controls shows the general phenomenon of fish moving around (as fish turn to change positions within the school), but we agree that more could be done to address this point and we are indeed working on it now.

Lines 212-217: There is a very strong statement that energetic savings by collective motion do not require fixed positional arrangements or specific kinematic features. While possibly one of the most interesting findings of the paper, I found that in its current state, it was not sufficiently/satisfactorily discussed. For example for the different mechanisms summarized, there will be clearly differences in their relevance based on relative distance and position. For example mechanisms 3 and 4 likely have significant contributions only at short distances. Here, the question is how relevant can they be if the average distance is 1 BL? Also, 1BL side by side is very much different from 1BL front to back, given the elongated body shape. For mechanisms 1 and 2, it appears relative positioning is quite important. Here, having maybe at least some information from the literature (if available) on the range of wall or push effects or the required precision in relative positioning for having a significant benefit would be very much desired. Also, do the authors suggest that a) these different effects overlap giving any position in the school a benefit, or b) that there are specific positions giving benefits due to different mechanisms and that fish "on purpose" switch only between these energetic "sweet" spots, I guess this what is towards the end referred to as Lighthill conjecture? Given the small group size I find a) rather unlikely, while b) actually also leads to a coordination problem if every fish is looking for a sweet spot. Overall, a related question is whether the authors observed a systematic change in leading individuals, which likely have no, or very small, hydrodynamic benefits.

Response: Thank you for the excellent discussion on this point. As we responded above, we have softened the tone of the statement. In the original version, we were clear that the known mechanisms as summarized in Fig. 1 lead us to ‘expect’ that fish do not need to be in a fixed position to save energy.

In general, current engineering/hydrodynamic studies suggest that any fish positioned within one body length (both upstream and downstream and side by side) will benefit from one or more of the hydrodynamic mechanisms that we expect will reduce energy costs, relative to a solitary individual. Our own studies using robotic systems suggest that a leading fish will experience an added mass “push” from a follower when the follower is located within roughly ½ body length behind the leader. We cited a Computational Fluid Dynamic (CFD) study about the relative distance among individuals for energy saving to be in effect. Please keep in mind that CFD simulation is a simplified model of the actual locomotion of fish and involves many assumptions and currently only resolves the time scale of seconds (see commentary of Zhang & Lauder 2023 doi:10.1242/jeb.245617 in J. Exp. Biol. for the current challenges of CFD simulation). To really understand the dynamic positions of fish within the school, we will need 3-D tracking of fish schools with tools that are currently being developed. Ideally, we would also have simultaneous energetic measurements, but of course, this is enormously challenging and it is not clear at this time how to accomplish this.

We certainly agree that the relative positions of fish (vertically staggered or in-line swimming) do affect the specific hydrodynamic mechanisms being used. We cited the study that discussed this, but the relative positions of fish remain an active area of research. More studies will be out next few years to provide more insight into the effects of the relative positions of fish in energy saving. The Lighthill conjecture is observed in flapping foils and whether fish schools use the Lighthill conjecture for energy saving is an active area of research but still unclear. We also provided a citation about the implication of the Lighthill conjecture on fish schools. Hence, our original version stated ‘The exact energetic mechanisms….would benefit from more in-depth studies’. We agree with the reviewer that not all fish can benefit Lighthill conjecture (if fish schools use it) at any given time point, hence the fish might need to rotate in using the Lighthill conjecture. This is one more explanation for the dynamic positioning of fish in a school.

Overall, in response to the question raised, we do not believe that fish are actively searching for “sweet spots” within the school, although this is only speculation on our part. We believe instead that fish, located in a diversity of positions within the school, get the hydrodynamic advantage of being in the group at that configuration.

We believe that fish, once they group and maintain a grouping where individuals are all within around one body length distance from each other, will necessarily get hydrodynamic benefits. As a collective group, we believe that at any one time, several different hydrodynamic mechanisms are all acting simultaneously and result in reduced energetic costs (Fig. 1).

Figure 4E: The y-axis is given in the units of 10-sec^-1 which is confusing is it 10 1/s or 1/(10s)? Why not use simply the unit of 1/s which is unambiguous?

Response: Thank you for the suggestions. We counted the turning frequency over the course of 10 seconds. To reflect more accurately on what we did, we used the suggested unit of 1/(10s) to more correctly correspond to how we made the measurements and the duration of the measurement. We recognize that this is a bit non-standard but would like to keep these units if possible.

Figure 4F: The unit in the school length is given in [mm], which suggests that the maximal measured school length is 4mm, this can't be true.

Response: Thank you for pointing this out. The unit should be [cm], which we corrected.

Reviewer #2 (Public Review):

Summary:

This paper tests the idea that schooling can provide an energetic advantage over solitary swimming. The present study measures oxygen consumption over a wide range of speeds, to determine the differences in aerobic and anaerobic cost of swimming, providing a potentially valuable addition to the literature related to the advantages of group living.

Response: Thank you for acknowledging our contribution is a valuable addition to the literature on collective movement by animals.

Strengths:

The strength of this paper is related to providing direct measurements of the energetics (oxygen consumption) of fish while swimming in a group vs solitary. The energetic advantages of schooling have been claimed to be one of the major advantages of schooling and therefore a direct energetic assessment is a useful result.

Response: Thank you for acknowledging our results are useful and provide direct measurements of energetics to prove a major advantage of schooling relative to solitary motion over a range of speeds.

Weaknesses:

The manuscript suffers from a number of weaknesses which are summarised below:

1) The possibility that fish in a school show lower oxygen consumption may also be due to a calming effect. While the authors show that there is no difference at low speed, one cannot rule out that calming effects play a more important role at higher speed, i.e. in a more stressful situation.

Response: Thank you for raising this creative point on “calming”. When vertebrates are moving at high speeds, their stress hormones (adrenaline, catecholamines & cortisol) increase. This phenomenon has been widely studied, and therefore, we do not believe that animals are ‘calm’ when moving at high speed and that somehow a “calming effect” explains our non-linear concave-upward energetic curves. “Calming” would have to have a rather strange non-linear effect over speed to explain our data, and act in contrast to known physiological responses involved in intense exercise (whether in fish or humans). It is certainly not true for humans that running at high speeds in a group causes a “calming effect” that explains changes in metabolic energy expenditure. We have added an explanation in the third paragraph in the section “Schooling dynamics enhances aerobic performance and reduces non-aerobic energy use”. Moreover, when animal locomotion has a high frequency of appendage movement (for both solitary individual and group movement), they are also not ‘calm’ from a behavioural point of view. Therefore, we respectfully disagree with the reviewer that the ‘calming effect’ is a major contributor to the energy saving of group movement at high speed. It is difficult to believe that giant danio swimming at 8 BL/s which is near or at their maximal sustainable locomotor limits are somehow “calm”. In addition, we demonstrated by direct energetic measurement that solitary individuals do not have a higher metabolic rate at the lower speed and thus directly show that there is very likely no cost of “uncalm” stress that would elevate the metabolic rate of solitary individuals. Furthermore, the current version of this manuscript compared the condition factor of the fish in the school and solitary individuals and found no difference (see Experimental Animal Section in the Methods). This also suggests that the measurement on the solitary fish is likely not confounded by any stress effects.

Finally, and as discussed further below, since we have simultaneous high-speed videos of fish swimming as we measure oxygen consumption at all speeds, we are able to directly measure fish behaviour. Since we observed no alteration in tail beat kinematics between schools and individuals (a key result that we elaborate on below), it’s very hard to justify that a “calming” effect explains our results. Fish in schools swimming at speed (not in still water) appear to be just as “calm” as solitary individuals.

2) The ratio of fish volume to water volume in the respirometer is much higher than that recommended by the methodological paper by Svendsen et al. (J Fish Biol 2016) Response: The ratio of respirometer volume to fish volume is an important issue that we thought about in detail before conducting these experiments. While Svendsen et al., (J. Fish Biol. 2016) recommend a respirometer volume-to-fish volume ratio of 500, we are not aware of any experimental study comparing volumes with oxygen measuring accuracy that gives this number as optimal. In addition, the Svendsen et al. paper does not consider that their recommendation might result in fish swimming near the walls of the flume (as a result of having relatively larger fish volume to flume volume) and hence able to alter their energetic expenditure by being near the wall. In our case, we needed to be able to study both a school (with higher animal volumes) and an individual (relatively lower volume) in the same exact experimental apparatus. Thus, we had to develop a system to accurately record oxygen consumption under both conditions.

The ratio of our respirometer to individual volume for schools is 693, while the value for individual fish is 2200. Previous studies (Parker 1973, Abrahams & Colgan, 1985, Burgerhout et al., 2013) that used a swimming-tunnel respirometer (i.e., a sealed treadmill) to measure the energy cost of group locomotion used values that range between 1116 and 8894 which are large and could produce low-resolution measurements of oxygen consumption. Thus, we believe that we have an excellent ratio for our experiments on both schools and solitary individuals, while maintaining a large enough value that fish don’t experience wall effects (see more discussion on this below, as we experimentally quantified the flow pattern within our respirometer).

The goal of the recommendation by Svendsen et al. is to achieve a satisfactory R2 (coefficient of determination) value for oxygen consumption data. However, Chabot et al., 2020 (DOI: 10.1111/jfb.14650) pointed out that only relying on R2 values is not always successful at excluding non-linear slopes. Much worse, only pursuing high R2 values has a risk of removing linear slopes with low R2 only because of a low signal-to-noise ratio and resulting in an overestimation of the low metabolic rate. Although we acknowledge the excellent efforts and recommendations provided by Svendsen et al., 2016, we perhaps should not treat the ratio of respirometer to organism volume of 500 as the gold standard for swim-tunnel respirometry. Svendsen et al., 2020 did not indicate how they reached the recommendation of using the ratio of respirometer to organism volume of 500. Moreover, Svendsen et al., 2020 stated that using an extended measuring period can help to resolve the low signal-to-noise ratio. Hence, the key consideration is to obtain a reliable signal-to-noise ratio which we will discuss below.

To ensure we obtain reliable data quality, we installed a water mixing loop (Steffensen et al., 1984) and used the currently best available technology of oxygen probe (see method section of Integrated Biomechanics & Bioenergetic Assessment System) to improve the signal-to-noise ratio. The water mixing loop is not commonly used in swim-tunnel respirometer. Hence, if a previously published study used a respirometer-to-organism ratio up to 8894, our updated oxygen measuring system is completely adequate to produce reliable signal-to-noise ratios in our system with a respirometer-to-organism ratio of 2200 (individuals) and 693 (schools). In fact, our original version of the manuscript used a published method (Zhang et al., 2019, J. Exp. Biol. https://doi.org/10.1242/jeb.196568) to analyze the signal-to-noise ratio and provided the quantitative approach to determine the sampling window to reliably capture the signal (Fig. S5).

3) Because the same swimming tunnel was used for schools and solitary fish, schooling fish may end up swimming closer to the wall (because of less volume per fish) than solitary fish. Distances to the wall of schooling fish are not given, and they could provide an advantage to schooling fish.

Response: This is an issue that we considered carefully in designing these experiments. After considering the volume of the respirometer and the size of the fish (see the response above), we decided to use the same respirometer to avoid any other confounding factors when using different sizes of respirometers with potentially different internal flow patterns. In particular, different sizes of Brett-type swim-tunnel respirometers differ in the turning radius of water flow, which can produce different flow patterns in the swimming section. Please note that we quantified the flow pattern within the flow tank using particle image velocimetry (PIV) (so we have quantitative velocity profiles across the working section at all tested speeds), and modified the provided baffle system to improve the flow in the working section.

Because we took high-speed videos simultaneously with the respirometry measurements, we can state unequivocally that individual fish within the school did not swim closer to the walls than solitary fish over the testing period (see below for the quantitative measurements of the boundary layer). Indeed, many previous respirometry studies do not obtain simultaneous video data and hence are unable to document fish locations when energetics is measured.

In studying schooling energetics, we believe that it is important to control as many factors as possible when making comparisons between school energetics and solitary locomotion. We took great care as indicated in the Methods section to keep all experimental parameters the same (same light conditions, same flow tank, same O2 measuring locations with the internal flow loop, etc.) so that we could detect differences if present. Changing the flow tank respirometer apparatus between individual fish and the schools studied would have introduced an unacceptable alteration of experimental conditions and would be a clear violation of the best experimental practices.

We have made every effort to be clear and transparent about the choice of experimental apparatus and explained at great length the experimental parameters and setup used, including the considerations about the wall effect in the extended Methods section and supplemental material provided.

Our manuscript provides the measurement of the boundary layer (<2.5 mm at speeds > 2 BL s-1) in the methods section of the Integrated Biomechanics & Bioenergetic Assessment System. We also state that the boundary layer is much thinner than the body width of the giant danio (~10 mm) so that the fish cannot effectively hide near the wall. Due to our PIV calibration, we are able to quantify flow near the wall.

In the manuscript, we also provide details about the wall effects and fish schools as follows from the manuscript: ”…the convex hull volume of the fish school did not change as speed increased, suggesting that the fish school was not flattening against the wall of the swim tunnel, a typical feature when fish schools are benefiting from wall effects. In nature, fish in the centre of the school effectively swim against a ‘wall’ of surrounding fish where they can benefit from hydrodynamic interactions with neighbours.”’ The notion that the lateral motion of surrounding slender bodies can be represented by a streamlined wall was also proposed by Newman et al., 1970 J. Fluid Mech. These considerations provide ample justification for the comparison of locomotor energetics by schools and solitary individuals.

4) The statistical analysis has a number of problems. The values of MO2 of each school are the result of the oxygen consumption of each fish, and therefore the test is comparing 5 individuals (i.e. an individual is the statistical unit) vs 5 schools (a school made out of 8 fish is the statistical unit). Therefore the test is comparing two different statistical units. One can see from the graphs that schooling MO2 tends to have a smaller SD than solitary data. This may well be due to the fact that schooling data are based on 5 points (five schools) and each point is the result of the MO2 of five fish, thereby reducing the variability compared to solitary fish. Other issues are related to data (for example Tail beat frequency) not being independent in schooling fish.

Response: We cannot agree with the reviewer that fish schools and solitary individuals are different statistical units. Indeed, these are the two treatments in the statistical sense: a school versus the individual. This is why we invested extra effort to replicate all our experiments on multiple schools of different individuals and compare the data to multiple different solitary individuals. This is a standard statistical approach, whether one is comparing a tissue with multiple cells to an individual cell, or multiple locations to one specific location in an ecological study. Our analysis treats the collective movement of the fish school as a functional unit, just like the solitary individual is a functional unit. At the most fundamental level of oxygen uptake measurements, our analysis results from calculating the declining dissolved oxygen as a function of time (i.e. the slope of oxygen removal). Comparisons are made between the slope of oxygen removal by fish schools and the slope of oxygen removal by solitary individuals. This is the correct statistical comparison.

The larger SD in individuals can be due to multiple biological reasons other than the technical reasons suggested here. Fundamentally, the different SD between fish schools and individuals can be the result of differences between solitary and collective movement and the different fluid dynamic interactions within the school could certainly cause differences in the amount of variation seen. Our interpretation of the ‘numerically’ smaller SD in fish schools than that of solitary individuals suggests that interesting hydrodynamic phenomena within fish schools remain to be discovered.

Reviewer #2 (Recommendations For The Authors):

I have reviewed a previous version of this paper. This new draft is somewhat improved but still presents a number of issues which I have outlined below.

Response: Thanks for your efforts to improve our paper with reviews, but a number of your comments apply to the previous version of the paper, and we have made a number of revisions before submitting it to eLife. We explain below how this version of the manuscript addresses many of your comments from both the previous and current reviews. As readers can see from our responses below, this version of the manuscript version no longer uses only ‘two-way ANOVA’ as we have implemented an additional statistical model. (Please see the comments below for more detailed responses related to the statistical models).

1) One of the main problems, and one of the reasons (see below) why many previous papers have measured TBF and not the oxygen consumption of a whole school, is that schooling also provides a calming effect (Nadler et al 2018) which is not easily differentiated from the hydrodynamic advantages (Abraham and Colgan 1985). This effect can reduce the MO2 while swimming and the EPOC when recovering. The present study does not fully take this potential issue into account and therefore its results are confounded by such effects. The authors state (line 401) that " the aerobic locomotion cost of solitary individuals showed no statistical difference from (in fact, being numerically lower) that of fish schools at a very low testing speed. The flow speed is similar to some areas of the aerated home aquarium for each individual fish. This suggests that the stress of solitary fish likely does not meaningfully contribute to the higher locomotor costs". While this is useful, the possibility that at higher speeds (i.e. a more stressful situation) solitary fish may experience more stress than fish in a school, cannot be ruled out.

Response: Thank you for finding our results and data useful. We have addressed the comments on calming or stress effects in our response above. The key point is that either solitary or school fish are challenged (i.e. stressed) at a high speed where the sizable increases in stress hormones are well documented in the exercise physiology literature. We honestly just do not understand how a “calming” effect could possibly explain the upward concave energetic curves that we obtained, and how “calming” could explain the difference between schools and solitary individuals. Since we have simultaneous high-speed videos of fish swimming as we measure oxygen consumption at all speeds, we are able to directly observe fish behaviour. It is not exactly clear what a “calming effect” would look like kinematically or how one would measure this experimentally, but since we observed no alteration in tail beat kinematics between schools and individuals (a key result that we elaborate on below), it’s very hard to justify that a “calming” effect explains our results. Fish in schools appear to be just as “calm” as solitary individuals.

If the reviewer's “calming effect” is a general issue, then birds flying in a V-formation should also experience a “calming effect”, but at least one study shows that birds in a V-formation experience higher wing beat frequencies.

In addition, Nalder et al., 2018 (https://doi.org/10.1242/bio.031997) did not study any such “calming effect”. We assume the reviewer is referring to Nalder et al., 2016, which showed that shoaling reduced fish metabolic rates in a resting respirometer that has little-to-no water current that would motivate fish to swim (which is very different from the swim-tunnel respirometer we used). Moreover, the inter-loop system used by Nalder et al., 2016 has the risk of mixing the oxygen uptake of the fish shoal and solitary individuals. Hence, we believe that it is not appropriate to extend the results of Nalder et al., 2016 to infer and insist on a calming effect for fish schools that we studied which are actively and directionally swimming over a wide speed range up to and including high speeds. Especially since our data clearly show that ‘the aerobic locomotion cost of solitary individuals showed no statistical difference from (in fact, being numerically lower) that of fish schools at very low testing speeds’. More broadly, shoaling and schooling are very different in terms of polarization as well as the physiological and behavioural mechanisms used in locomotion. Shoaling behaviour by fish in still water is not the same as active directional schooling over a speed range. Our supplementary Table 1 provides a clear definition for a variety of grouping behaviours and makes the distinction between shoaling and schooling.

Our detailed discussion about other literature mentioned by this reviewer can be seen in the comments below.

2) The authors overstate the novelty of their work. Line 29: "Direct energetic measurements demonstrating the 30 energy-saving benefits of fluid-mediated group movements remain elusive" The idea that schooling may provide a reduction in the energetic costs of swimming dates back to the 70s, with pioneering experimental work showing a reduction in tail beat frequency in schooling fish vs solitary (by Zuyev, G. V. & Belyayev, V. V. (1970) and theoretical work by Weihs (1973). Work carried out in the past 20 years (Herskin and Steffensen 1998; Marras et al 2015; Bergerhout et al 2013; Hemelrijk et al 2014; Li et al 2021, Wiwchar et al 2017; Verma et al 2018; Ashraf et al 2019) based on a variety of approaches has supported the idea of a reduction in swimming costs in schooling vs solitary fish. In addition, group respirometry has actually been done in early and more recent studies testing the reduction in oxygen consumption as a result of schooling (Parker, 1973; Itazawa et al., 1978; Abrahams and Colgan 1985; Davis & Olla, 1992; Ross & Backman, 1992, Bergerhout et al 2013; Currier et al 2020). Specifically, Abrahams and Colgan (1985) and Bergerhout et al (2013) found that the oxygen consumption of fish swimming in a school was higher than when solitary, and Abrahams and Colgan (1985) made an attempt to deal with the confounding calming effect by pairing solitary fish up with a neighbor visible behind a barrier. These issues and how they were dealt with in the past (and in the present manuscript) are not addressed by the present manuscript. Currier et al (2020) found that the reduction of oxygen consumption was species-specific.

Response: We cannot agree with this reviewer that we have overstated the novelty of our work, and, in fact, we make very specific comments on the new contributions of our paper relative to the large previous literature on schooling. We are well aware of the literature cited above and many of these papers have little or nothing to do with quantifying the energetics of schooling. In addition, many of these papers rely on simple kinematic measurements which are unrelated to direct energetic measurements of energy use. To elaborate on this, we present the ‘Table R’ below which evaluates and compares each of the papers this reviewer cites above. The key message (as we wrote in the manuscript) is that none of the previous studies measured non-aerobic cost (and thus do not calculate the total energy expenditure (TEE), which we show to be substantial. In addition, many of these studies do not compare schools to individuals, do not quantify both energetics and kinematics, and do not study a wide speed range. Only 33% of previous studies used direct measurements of aerobic metabolic rate to compare the locomotion costs of fish schools and solitary individuals (an experimental control). We want to highlight that most of the citations in the reviewer’s comments are not about the kinematics or hydrodynamics of fish schooling energetics, although they provide peripheral information on fish schooling in general. We also provide an overview of the literature on this topic in our paper in the Journal of Experimental Biology (Zhang & Lauder 2023 doi:10.1242/jeb.245617) and do not wish to duplicate that discussion here. We summarized and cited the relevant papers about the energetics of fish schooling in Table 1.

Author response table 1.

Papers cited by Reviewer #2, and a summary of their contributions and approach.

References cited above:

Zuyev, G., & Belyayev, V. V. (1970). An experimental study of the swimming of fish in groups as exemplified by the horsemackerel [Trachurus mediterraneus ponticus Aleev]. J Ichthyol, 10, 545-549.

Weihs, D. (1973). Hydromechanics of fish schooling. Nature, 241(5387), 290-291.

Herskin, J., & Steffensen, J. F. (1998). Energy savings in sea bass swimming in a school: measurements of tail beat frequency and oxygen consumption at different swimming speeds. Journal of Fish Biology, 53(2), 366-376.

Marras, S., Killen, S. S., Lindström, J., McKenzie, D. J., Steffensen, J. F., & Domenici, P. (2015). Fish swimming in schools save energy regardless of their spatial position. Behavioral ecology and sociobiology, 69, 219-226.

Burgerhout, E., Tudorache, C., Brittijn, S. A., Palstra, A. P., Dirks, R. P., & van den Thillart, G. E. (2013). Schooling reduces energy consumption in swimming male European eels, Anguilla anguilla L. Journal of experimental marine biology and ecology, 448, 66-71.

Hemelrijk, C. K., Reid, D. A. P., Hildenbrandt, H., & Padding, J. T. (2015). The increased efficiency of fish swimming in a school. Fish and Fisheries, 16(3), 511-521.

Li, L., Nagy, M., Graving, J. M., Bak-Coleman, J., Xie, G., & Couzin, I. D. (2020). Vortex phase matching as a strategy for schooling in robots and in fish. Nature communications, 11(1), 5408.

Wiwchar, L. D., Gilbert, M. J., Kasurak, A. V., & Tierney, K. B. (2018). Schooling improves critical swimming performance in zebrafish (Danio rerio). Canadian Journal of Fisheries and Aquatic Sciences, 75(4), 653-661.

Verma, S., Novati, G., & Koumoutsakos, P. (2018). Efficient collective swimming by harnessing vortices through deep reinforcement learning. Proceedings of the National Academy of Sciences, 115(23), 5849-5854.

Ashraf, I., Bradshaw, H., Ha, T. T., Halloy, J., Godoy-Diana, R., & Thiria, B. (2017). Simple phalanx pattern leads to energy saving in cohesive fish schooling. Proceedings of the National Academy of Sciences, 114(36), 9599-9604.

Parker Jr, F. R. (1973). Reduced metabolic rates in fishes as a result of induced schooling. Transactions of the American Fisheries Society, 102(1), 125-131.

Itazawa, Y., & Takeda, T. (1978). Gas exchange in the carp gills in normoxic and hypoxic conditions. Respiration physiology, 35(3), 263-269.

Abrahams, M. V., & Colgan, P. W. (1985). Risk of predation, hydrodynamic efficiency and their influence on school structure. Environmental Biology of Fishes, 13, 195-202.

Davis, M. W., & Olla, B. L. (1992). The role of visual cues in the facilitation of growth in a schooling fish. Environmental biology of fishes, 34, 421-424.

Ross, R. M., Backman, T. W., & Limburg, K. E. (1992). Group-size-mediated metabolic rate reduction in American shad. Transactions of the American Fisheries Society, 121(3), 385-390.

Currier, M., Rouse, J., & Coughlin, D. J. (2021). Group swimming behaviour and energetics in bluegill Lepomis macrochirus and rainbow trout Oncorhynchus mykiss. Journal of Fish Biology, 98(4), 1105-1111.

Halsey, L. G., Wright, S., Racz, A., Metcalfe, J. D., & Killen, S. S. (2018). How does school size affect tail beat frequency in turbulent water?. Comparative Biochemistry and Physiology Part A: Molecular & Integrative Physiology, 218, 63-69.

Johansen, J. L., Vaknin, R., Steffensen, J. F., & Domenici, P. (2010). Kinematics and energetic benefits of schooling in the labriform fish, striped surfperch Embiotoca lateralis. Marine Ecology Progress Series, 420, 221-229.

3) In addition to the calming effect, measuring group oxygen consumption suffers from a number of problems as discussed in Herskin and Steffensen (1998) such as the fish volume to water volume ratio, which varies considerably when testing a school vs single individuals in the same tunnel and the problem of wall effect when using a small volume of water for accurate O2 measurements. Herskin and Steffensen (1998) circumvented these problems by measuring tailbeat frequencies of fish in a school and then calculating the MO2 of the corresponding tailbeat frequency in solitary fish in a swim tunnel. A similar approach was used by Johansen et al (2010), Marras et al (2015), Halsey et al (2018). However, It is not clear how these potential issues were dealt with here. Here, larger solitary D. aequipinnatus were used to increase the signal-to-noise ratio. However, using individuals of different sizes makes other variables not so directly comparable, including stress, energetics, and kinematics. (see comment 7 below).

Response: We acknowledge the great efforts made by previous studies to understand the energetics of fish schooling. These studies, as detailed in the table and elaborated in the response above (see comment 2) are very different from our current study. Our study achieved a direct comparison of energetics (including both aerobic and non-aerobic cost) and kinematics between solitary individuals and fish schools that has never been done before. Our detailed response to the supposed “calming effect” is given above.

As highlighted in the previous comments and opening statement, our current version has addressed the wall effect, tail beat frequency, and experimental and analytical efforts invested to directly compare the energetics between fish schools and solitary individuals. As readers can see in our comprehensive method section, achieving the direct comparison between solitary individuals and fish schools is not a trivial task. Now we want to elaborate on the role of kinematics as an indirect estimate of energetics. Our results here show that kinematic measurements of tail beat frequency are not reliable estimates of energetic cost, and the previous studies cited did not measure EPOC and those costs are substantial, especially as swimming speed increases. Fish in schools can save energy even when the tail beat frequency does not change (although school volume can change as we show). We elaborated (in great detail) on why kinematics does not always reflect on the energetics in the submitted version (see last paragraph of “Schooling dynamics and energy conservation” section). Somehow modeling what energy expenditure should be based only on tail kinematics is, in our view, a highly unreliable approach that has never been validated (e.g., fish use more than just tails for locomotion). Indeed, we believe that this is an inadequate substitute for direct energy measurements. We disagree that using slightly differently sized individuals is an issue since we recorded fish kinematics across all experiments and included the measurements of behaviour in our manuscript. Slightly altering the size of individual fish was done on purpose to provide a better ratio of respirometer volume to fish volume in the tests on individual fish, thus we regard this as a benefit of our approach and not a concern.

Finally, in another study of the collective behaviour of flying birds (Usherwood, J. R., Stavrou, M., Lowe, J. C., Roskilly, K. and Wilson, A. M. (2011). Flying in a flock comes at a cost in pigeons. Nature 474, 494-497), the authors observed that wing beat frequency can increase during flight with other birds. Hence, again, we cannot regard movement frequency of appendages as an adequate substitute for direct energetic measurements.

4) Svendsen et al (2016) provide guidelines for the ratio of fish volume to water volume in the respirometer. The ratio used here (2200) is much higher than that recommended. RFR values higher than 500 should be avoided in swim tunnel respirometry, according to Svendsen et al (2016).

Response: Thank you for raising this point. Please see the detailed responses above to the same comment above. We believe that our experimental setup and ratios are very much in line with those recommended, and represent a significant improvement on previous studies which use large ratios.

5) Lines 421-436: The same goes for wall effects. Presumably, using the same size swim tunnel, schooling fish were swimming much closer to the walls than solitary fish but this is not specifically quantified here in this paper. Lines 421-436 provide some information on the boundary layer (though wall effects are not just related by the boundary layer) and some qualitative assessment of school volume. However, no measurement of the distance between the fish and the wall is given.

Response: Please see the detailed responses above to the same comment. Specifically, we used the particle image velocimetry (PIV) system to measure the boundary layer (<2.5 mm at speeds > 2 BL s-1) and stated the parameters in the methods section of the Integrated Biomechanics & Bioenergetic Assessment System. We also state that the boundary layer is much thinner than the body width of the giant danio (~10 mm) so that the fish cannot effectively hide near the wall. Due to our PIV calibration, we are able to quantify flow near the wall.

Due to our video data obtained simultaneously with energetic measurements, we do not agree that fish were swimming closer to the wall in schools and also note that we took care to modify the typical respirometer to both ensure that flow across the cross-section did not provide any refuges and to quantify flow velocities in the chamber using particle image velocimetry. We do not believe that any previous experiments on schooling behaviour in fish have taken the same precautions.

6) The statistical tests used have a number of problems. Two-way ANOVA was based on school vs solitary and swimming speed. However, there are repeated measures at each speed and this needs to be dealt with. The degrees of freedom of one-way ANOVA and T-tests are not provided. These tests took into account five groups of fish vs. five solitary fish. The values of MO2 of each school are the result of the oxygen consumption of each fish, and therefore the test is comparing 5 individuals (i.e. an individual is the statistical unit) vs 5 schools (a school made out of 8 fish is the statistical unit). Therefore the test is comparing two different statistical units. One can see from the graphs that schooling MO2 tend to have a smaller SD than solitary data. This may well be due to the fact that schooling data are based on 5 points (five schools) and each point is the result of the MO2 of five fish, thereby reducing the variability compared to solitary fish. TBF, on the other hand, can be assigned to each fish even in a school, and therefore TBF of each fish could be compared by using a nested approach of schooling fish (nested within each school) vs solitary fish, but this is not the statistical procedure used in the present manuscript. The comparison between TBFs presumably is comparing 5 individuals vs all the fish in the schools (6x5=30 fish). However, the fish in the school are not independent measures.

Response: We cannot agree with this criticism, which may be based on this reviewer having seen a previous version of the manuscript. We did not use two-way ANOVA in this version. This version of the manuscript reported the statistical value based on a General Linear Model (see statistical section of the method). We are concerned that this reviewer did not in fact read either the Methods section or the Results section. In addition, it is hard to accept that, from examination of the data shown in Figure 3, there is not a clear and large difference between schooling and solitary locomotion, regardless of the statistical test used.

Meanwhile, the comments about the ‘repeated’ measures from one speed to the next are interesting, but we cannot agree. The ‘repeated’ measures are proper when one testing subject is assessed before and after treatment. Going from one speed to the next is not a treatment. Instead, the speed is a dependent and continuous variable. In our experimental design, the treatment is fish school, and the control is a solitary individual. Second, we never compared any of our dependent variables across different speeds within a school or within an individual. Instead, we compared schools and individuals at each speed. In this comparison, there are no ‘repeated’ measures. We agree with the reviewer that fish in the school are interacting (not independent). This is one more reason to support our approach of treating fish schools as a functional and statistical unit in our experiment design (more detailed responses are stated in the response to the comment above).

7) The size of solitary and schooling individuals appears to be quite different (solitary fish range 74-88 cm, schooling fish range 47-65 cm). While scaling laws can correct for this in the MO2, was this corrected for TBF and for speed in BL/s? Using BL/s for speed does not completely compensate for the differences in size.

Response: Our current version has provided justifications for not conducting scaling in the values of tail beat frequency. Our justification is “The mass scaling for tail beat frequency was not conducted because of the lack of data for D. aequipinnatus and its related species. Using the scaling exponent of distant species for mass scaling of tail beat frequency will introduce errors of unknown magnitude.”. Our current version also acknowledges the consideration about scaling as follows: “Fish of different size swimming at 1 BL s-1 will necessarily move at different Reynolds numbers, and hence the scaling of body size to swimming speed needs to be considered in future analyses of other species that differ in size”

Reviewer #3 (Public Review):

Summary:

Zhang and Lauder characterized both aerobic and anaerobic metabolic energy contributions in schools and solitary fishes in the Giant danio (Devario aequipinnatus) over a wide range of water velocities. By using a highly sophisticated respirometer system, the authors measure the aerobic metabolisms by oxygen uptake rate and the non-aerobic oxygen cost as excess post-exercise oxygen consumption (EPOC). With these data, the authors model the bioenergetic cost of schools and solitary fishes. The authors found that fish schools have a J-shaped metabolism-speed curve, with reduced total energy expenditure per tail beat compared to solitary fish. Fish in schools also recovered from exercise faster than solitary fish. Finally, the authors conclude that these energetic savings may underlie the prevalence of coordinated group locomotion in fish.

The conclusions of this paper are mostly well supported by data, but some aspects of methods and data acquisition need to be clarified and extended.

Response: Thank you for seeing the value of our study. We provided clarification of the data acquisition system with a new panel of pictures included in the supplemental material to show our experimental system. We understand that our methods have more details and justifications than the typical method sections. First, the details are to promote the reproducibility of the experiments. The justifications are the responses to reviewer 2, who reviewed our previous manuscript version and also posted the same critiques after we provided the justifications for the construction of the system and the data acquisition.

Strengths:

This work aims to understand whether animals moving through fluids (water in this case) exhibit highly coordinated group movement to reduce the cost of locomotion. By calculating the aerobic and anaerobic metabolic rates of school and solitary fishes, the authors provide direct energetic measurements that demonstrate the energy-saving benefits of coordinated group locomotion in fishes. The results of this paper show that fish schools save anaerobic energy and reduce the recovery time after peak swimming performance, suggesting that fishes can apport more energy to other fitness-related activities whether they move collectively through water.

Response: Thank you. We are excited to share our discoveries with the world.

Weaknesses:

Although the paper does have strengths in principle, the weakness of the paper is the method section. There is too much irrelevant information in the methods that sometimes is hard to follow for a researcher unfamiliar with the research topic. In addition, it was hard to imagine the experimental (respirometer) system used by the authors in the experiments; therefore, it would be beneficial for the article to include a diagram/scheme of that respiratory system.

Response: We agree with the reviewer and hence added the pictures of the experimental system in the supplementary materials (Fig. S4). We think pictures are more realistic to present the system than schematics. We also provide a picture of the system during the process of making the energetic measurements. It is to show the care went to ensure fish are not affected by any external stimulation other than the water velocity. The careful experimental protocol is very critical to reveal the concave upward shaped curve of bony fish schools that was never reported before. Many details in the methods have been included in response to Reviewer 2.

Reviewer #3 (Recommendations For The Authors):

Overall, this is a very interesting, well-written, and nice article. However, many times the method section looks like a discussion. Furthermore, the authors need to check the use of the word "which" throughout the text. I got the feeling that it is overused/misused sometimes.

Response: Thank you for the positive comments. The method is written in that way to address the concerns of Reviewer 2 who reviewed our previous versions. We corrected the overuse of ‘which’ throughout the manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors investigate the contributions of the long noncoding RNA snhg3 in liver metabolism and MAFLD. The authors conclude that liver-specific loss or overexpression of Snhg3 impacts hepatic lipid content and obesity through epigenetic mechanisms. More specifically, the authors invoke that the nuclear activity of Snhg3 aggravates hepatic steatosis by altering the balance of activating and repressive chromatin marks at the Pparg gene locus. This regulatory circuit is dependent on a transcriptional regulator SND1.

Strengths:

The authors developed a tissue-specific lncRNA knockout and KI models. This effort is certainly appreciated as few lncRNA knockouts have been generated in the context of metabolism. Furthermore, lncRNA effects can be compensated in a whole organism or show subtle effects in acute versus chronic perturbation, rendering the focus on in vivo function important and highly relevant. In addition, Snhg3 was identified through a screening strategy and as a general rule the authors the authors attempt to follow unbiased approaches to decipher the mechanisms of Snhg3.

Weaknesses:

Despite efforts at generating a liver-specific knockout, the phenotypic characterization is not focused on the key readouts. Notably missing are rigorous lipid flux studies and targeted gene expression/protein measurement that would underpin why the loss of Snhg3 protects from lipid accumulation. Along those lines, claims linking the Snhg3 to MAFLD would be better supported with careful interrogation of markers of fibrosis and advanced liver disease. In other areas, significance is limited since the presented data is either not clear or rigorous enough. Finally, there is an important conceptual limitation to the work since PPARG is not established to play a major role in the liver.

We thank the reviewer for the detailed comment. In this study, hepatocyte-specific Snhg3 deficiency decreased body and liver weight and alleviated hepatic steatosis in DIO mice, whereas overexpression induced the opposite effect (Figure 2 and 3). Furthermore, we investigated the hepatic differentially expressed genes (DEGs) between the DIO Snhg3-HKI and control WT mice using RNA-Seq and revealed that Snhg3 exerts a global effect on the expression of genes involved in fatty acid metabolism using GSEA (Figure 4B). We validated the expression of some DEGs involved in fatty acid metabolism by RT-qPCR. The results showed that the hepatic expression levels of some genes involved in fatty acid metabolism, including Cd36, Cidea/c and Scd1/2 were upregulated in Snhg3-HKO mice and were downregulated in Snhg3-HKI mice compared to the controls (Figure 4C), respectively. Please check them in the first paragraph in p8.

As a transcription regulator of Cd36 and Cidea/c, it is well known that PPARγ plays major adipogenic and lipogenic roles in adipose tissue. Although the expression of PPARγ in the liver is very low under healthy conditions, induced expression of PPARγ in both hepatocytes and non-parenchymal cells (Kupffer cells, immune cells, and HSCs) in the liver has a crucial role in the pathophysiology of MASLD (Lee et al., 2023b, Chen et al., 2023, Gross et al., 2017). The activation of PPARγ in the liver induces the adipogenic program to store fatty acids in lipid droplets as observed in adipocytes (Lee et al., 2018). Moreover, the inactivation of liver PPARγ abolished rosiglitazone-induced an increase in hepatic TG and improved hepatic steatosis in lipoatrophic AZIP mice (Gavrilova et al., 2003). Furthermore, there is a strong correlation between the onset of hepatic steatosis and hepatocyte-specific PPARγ expression. Clinical trials have also indicated that increased insulin resistance and hepatic PPARγ expressions were associated with NASH scores in some obese patients (Lee et al., 2023a, Mukherjee et al., 2022). Even though PPARγ’s primary function is in adipose tissue, patients with MASLD have much higher hepatic expression levels of PPARγ, reflecting the fact that PPARγ plays different roles in different tissues and cell types (Mukherjee et al., 2022). As these studies mentioned above, our result also hinted at the importance of PPARγ in the pathophysiology of MASLD. Snhg3 deficiency or overexpression respectively induced the decrease or increase in hepatic PPARγ. Moreover, administration of PPARγ antagonist T0070907 mitigated the hepatic Cd36 and Cidea/c increase and improved Snhg3-induced hepatic steatosis. However,  conflicting findings suggest that the expression of hepatic PPARγ is not increased as steatosis develops in humans and in clinical studies and that PPARγ agonists administration didn’t aggravate liver steatosis (Gross et al., 2017). Thus, understanding how the hepatic PPARγ expression is regulated may provide a new avenue to prevent and treat the MASLD (Lee et al., 2018). We also discussed it in revised manuscript, please refer the first paragraph in the section of Discussion in p13.

Hepatotoxicity accelerates the development of progressive inflammation, oxidative stress and fibrosis (Roehlen et al., 2020). Chronic liver injury including MASLD can progress to liver fibrosis with the formation of a fibrous scar. Injured hepatocytes can secrete fibrogenic factors or exosomes containing miRNAs that activate HSCs, the major source of the fibrous scar in liver fibrosis (Kisseleva and Brenner, 2021). Apart from promoting lipogenesis, PPARγ has also a crucial function in improving inflammation and fibrosis (Chen et al., 2023). In this study, no hepatic fibrosis phenotype was seen in Snhg3-HKO and Snhg3-HKI mice (figures supplement 1D and 2D). Moreover, deficiency and overexpression of Snhg3 respectively decreased and increased the expression of profibrotic genes, such as collagen type I alpha 1/2 (Col1a1 and Col1a2), but had no effects on the pro-inflammatory factors, including transforming growth factor β1 (Tgfβ1), tumor necrosis factor α (Tnfα), interleukin 6 and 1β (Il6 and Il1β) (figures supplement 3A and B). Inflammation is an absolute requirement for fibrosis because factors from injured hepatocytes alone are not sufficient to directly activate HSCs and lead to fibrosis (Kisseleva and Brenner, 2021). Additionally, previous studies indicated that exposure to HFD for more 24 weeks causes less severe fibrosis (Alshawsh et al., 2022). In future, the effect of Snhg3 on hepatic fibrosis in mice need to be elucidated by prolonged high-fat feeding or by adopting methionine- and choline deficient diet (MCD) feeding. Please check them in the second paragraph in the section of Discussion in p13.

References

ALSHAWSH, M. A., ALSALAHI, A., ALSHEHADE, S. A., SAGHIR, S. A. M., AHMEDA, A. F., AL ZARZOUR, R. H. & MAHMOUD, A. M. 2022. A Comparison of the Gene Expression Profiles of Non-Alcoholic Fatty Liver Disease between Animal Models of a High-Fat Diet and Methionine-Choline-Deficient Diet. Molecules, 27. DIO:10.3390/molecules27030858, PMID:35164140

CHEN, H., TAN, H., WAN, J., ZENG, Y., WANG, J., WANG, H. & LU, X. 2023. PPAR-gamma signaling in nonalcoholic fatty liver disease: Pathogenesis and therapeutic targets. Pharmacol Ther, 245, 108391. DIO:10.1016/j.pharmthera.2023.108391, PMID:36963510

GAVRILOVA, O., HALUZIK, M., MATSUSUE, K., CUTSON, J. J., JOHNSON, L., DIETZ, K. R., NICOL, C. J., VINSON, C., GONZALEZ, F. J. & REITMAN, M. L. 2003. Liver peroxisome proliferator-activated receptor gamma contributes to hepatic steatosis, triglyceride clearance, and regulation of body fat mass. J Biol Chem, 278, 34268-76. DIO:10.1074/jbc.M300043200, PMID:12805374

GROSS, B., PAWLAK, M., LEFEBVRE, P. & STAELS, B. 2017. PPARs in obesity-induced T2DM, dyslipidaemia and NAFLD. Nat Rev Endocrinol, 13, 36-49. DIO:10.1038/nrendo.2016.135, PMID:27636730

KISSELEVA, T. & BRENNER, D. 2021. Molecular and cellular mechanisms of liver fibrosis and its regression. Nat Rev Gastroenterol Hepatol, 18, 151-166. DIO:10.1038/s41575-020-00372-7, PMID:33128017

LEE, S. M., MURATALLA, J., KARIMI, S., DIAZ-RUIZ, A., FRUTOS, M. D., GUZMAN, G., RAMOS-MOLINA, B. & CORDOBA-CHACON, J. 2023a. Hepatocyte PPARgamma contributes to the progression of non-alcoholic steatohepatitis in male and female obese mice. Cell Mol Life Sci, 80, 39. DIO:10.1007/s00018-022-04629-z, PMID:36629912

LEE, S. M., MURATALLA, J., SIERRA-CRUZ, M. & CORDOBA-CHACON, J. 2023b. Role of hepatic peroxisome proliferator-activated receptor gamma in non-alcoholic fatty liver disease. J Endocrinol, 257. DIO:10.1530/JOE-22-0155, PMID:36688873

LEE, Y. K., PARK, J. E., LEE, M. & HARDWICK, J. P. 2018. Hepatic lipid homeostasis by peroxisome proliferator-activated receptor gamma 2. Liver Res, 2, 209-215. DIO:10.1016/j.livres.2018.12.001, PMID:31245168

MUKHERJEE, A. G., WANJARI, U. R., GOPALAKRISHNAN, A. V., KATTURAJAN, R., KANNAMPUZHA, S., MURALI, R., NAMACHIVAYAM, A., GANESAN, R., RENU, K., DEY, A., VELLINGIRI, B. & PRINCE, S. E. 2022. Exploring the Regulatory Role of ncRNA in NAFLD: A Particular Focus on PPARs. Cells, 11. DIO:10.3390/cells11243959, PMID:36552725

ROEHLEN, N., CROUCHET, E. & BAUMERT, T. F. 2020. Liver Fibrosis: Mechanistic Concepts and Therapeutic Perspectives. Cells, 9. DIO:10.3390/cells9040875, PMID:32260126

Reviewer #2 (Public Review):

Through RNA analysis, Xie et al found LncRNA Snhg3 was one of the most down-regulated Snhgs by a high-fat diet (HFD) in mouse liver. Consequently, the authors sought to examine the mechanism through which Snhg3 is involved in the progression of metabolic dysfunction-associated fatty liver diseases (MASLD) in HFD-induced obese (DIO) mice. Interestingly, liver-specific Snhg3 knockout was reduced, while Snhg3 over-expression potentiated fatty liver in mice on an HFD. Using the RNA pull-down approach, the authors identified SND1 as a potential Sngh3 interacting protein. SND1 is a component of the RNA-induced silencing complex (RISC). The authors found that Sngh3 increased SND1 ubiquitination to enhance SND1 protein stability, which then reduced the level of repressive chromatin H3K27me3 on PPARg promoter. The upregulation of PPARg, a lipogenic transcription factor, thus contributed to hepatic fat accumulation.

The authors propose a signaling cascade that explains how LncRNA sngh3 may promote hepatic steatosis. Multiple molecular approaches have been employed to identify molecular targets of the proposed mechanism, which is a strength of the study. There are, however, several potential issues to consider before jumping to a conclusion.

(1) First of all, it's important to ensure the robustness and rigor of each study. The manuscript was not carefully put together. The image qualities for several figures were poor, making it difficult for the readers to evaluate the results with confidence. The biological replicates and numbers of experimental repeats for cell-based assays were not described. When possible, the entire immunoblot imaging used for quantification should be presented (rather than showing n=1 representative). There were multiple mislabels in figure panels or figure legends (e.g., Figure 2I, Figure 2K, and Figure 3K). The b-actin immunoblot image was reused in Figure 4J, Figure 5G, and Figure 7B with different exposure times. These might be from the same cohort of mice. If the immunoblots were run at different times, the loading control should be included on the same blot as well.

We thank the reviewer for the detailed comment. We have provided the clear figures in revised manuscript, please check them.

The biological replicates and numbers of experimental repeats for cell-based assays had been updated and please check them in the manuscript.

The entire immunoblot imaging used for quantification had been provided in the primary data. Please check them.

The original Figure 2I, Figure 2K, Figure 3K have been revised and replaced with new Figure 2F, Figure 2H, Figure 3H, and their corresponding figure legends has also been corrected in revised manuscript.

The protein levels of CD36, PPARγ and β-ACTIN were examined at the same time and we had revised the manuscript, please check them in revised Figure 7B and 7C.

(2) The authors can do a better job in explaining the logic for how they came up with the potential function of each component of the signaling cascade. Snhg3 is down-regulated by HFD. However, the evidence presented indicates its involvement in promoting steatosis. In Figure 1C, one would expect PPARg expression to be up-regulated (when Sngh3 was down-regulated). If so, the physiological observation conflicts with the proposed mechanism. In addition, SND1 is known to regulate RNA/miRNA processing. How do the authors rule out this potential mechanism? How about the hosting snoRNA, Snord17? Does it involve the progression of NASLD?

We thank the reviewer for the detailed comment. Our results showed that the expression of Snhg3 was decreased in DIO mice which led us to speculate that the downregulation of Snhg3 in DIO mice might be a stress protective reaction to high nutritional state, but the specific details need to be clarified. This is probably similar to fibroblast growth factor 21 (FGF21) and growth differentiation factor 15 (GDF15), whose endogenous expression and circulating levels are elevated in obese humans and mice despite their beneficial effects on obesity and related metabolic complications (Keipert and Ost, 2021). Although FGF21 can be induced by oxidative stress and be activated in obese mice and in NASH patients, elevated FGF21 paradoxically protects against oxidative stress and reduces hepatic steatosis (Tillman and Rolph, 2020).  We had added the content the section of Discussion, please check it in the second paragraph in p12.

SND1 has multiple roles through associating with different types of RNA molecules, including mRNA, miRNA, circRNA, dsRNA and lncRNA. SND1 could bind negative-sense SARS-CoV-2 RNA and promoted viral RNA synthesis, and to promote viral RNA synthesis (Schmidt et al., 2023). SND1 is also involved in hypoxia by negatively regulating hypoxia‐related miRNAs (Saarikettu et al., 2023). Furthermore, a recent study revealed that lncRNA SNAI3-AS1 can competitively bind to SND1 and perturb the m6A-dependent recognition of Nrf2 mRNA 3'UTR by SND1, thereby reducing the mRNA stability of Nrf2 (Zheng et al., 2023). Huang et al. also reported that circMETTL9 can directly bind to and increase the expression of SND1 in astrocytes, leading to enhanced neuroinflammation (Huang et al., 2023). However, whether there is an independent-histone methylation role of SND1/lncRNA-Snhg3 involved in lipid metabolism in the liver needs to be further investigated. We also discussed the limitation in the manuscript and please refer the section of Discussion in the third paragraph in p17.

Snhg3 serves as host gene for producing intronic U17 snoRNAs, the H/ACA snoRNA. A previous study found that cholesterol trafficking phenotype was not due to reduced Snhg3 expression, but rather to haploinsufficiency of U17 snoRNA. Upregulation of hypoxia-upregulated mitochondrial movement regulator (HUMMR) in U17 snoRNA-deficient cells promoted the formation of ER-mitochondrial contacts, resulting in decreasing cholesterol esterification and facilitating cholesterol trafficking to mitochondria (Jinn et al., 2015). Additionally, disruption of U17 snoRNA caused resistance to lipid-induced cell death and general oxidative stress in cultured cells. Furthermore, knockdown of U17 snoRNA in vivo protected against hepatic steatosis and lipid-induced oxidative stress and inflammation (Sletten et al., 2021). We determined the expression of hepatic U17 snoRNA and its effect on SND1 and PPARγ. The results showed that the expression of U17 snoRNA decreased in the liver of DIO Snhg3-HKO mice and unchanged in the liver of DIO Snhg3-HKI mice, but overexpression of U17 snoRNA had no effect on the expression of SND1 and PPARγ (figure supplement 5A-C), indicating that Sngh3 induced hepatic steatosis was independent on U17 snoRNA. We also discussed it in revised manuscript, please refer the section of Discussion in p15.

References

HUANG, C., SUN, L., XIAO, C., YOU, W., SUN, L., WANG, S., ZHANG, Z. & LIU, S. 2023. Circular RNA METTL9 contributes to neuroinflammation following traumatic brain injury by complexing with astrocytic SND1. J Neuroinflammation, 20, 39. DIO:10.1186/s12974-023-02716-x, PMID:36803376

JINN, S., BRANDIS, K. A., REN, A., CHACKO, A., DUDLEY-RUCKER, N., GALE, S. E., SIDHU, R., FUJIWARA, H., JIANG, H., OLSEN, B. N., SCHAFFER, J. E. & ORY, D. S. 2015. snoRNA U17 regulates cellular cholesterol trafficking. Cell Metab, 21, 855-67. DIO:10.1016/j.cmet.2015.04.010, PMID:25980348

KEIPERT, S. & OST, M. 2021. Stress-induced FGF21 and GDF15 in obesity and obesity resistance. Trends Endocrinol Metab, 32, 904-915. DIO:10.1016/j.tem.2021.08.008, PMID:34526227

SAARIKETTU, J., LEHMUSVAARA, S., PESU, M., JUNTTILA, I., PARTANEN, J., SIPILA, P., POUTANEN, M., YANG, J., HAIKARAINEN, T. & SILVENNOINEN, O. 2023. The RNA-binding protein Snd1/Tudor-SN regulates hypoxia-responsive gene expression. FASEB Bioadv, 5, 183-198. DIO:10.1096/fba.2022-00115, PMID:37151849

SCHMIDT, N., GANSKIH, S., WEI, Y., GABEL, A., ZIELINSKI, S., KESHISHIAN, H., LAREAU, C. A., ZIMMERMANN, L., MAKROCZYOVA, J., PEARCE, C., KREY, K., HENNIG, T., STEGMAIER, S., MOYON, L., HORLACHER, M., WERNER, S., AYDIN, J., OLGUIN-NAVA, M., POTABATTULA, R., KIBE, A., DOLKEN, L., SMYTH, R. P., CALISKAN, N., MARSICO, A., KREMPL, C., BODEM, J., PICHLMAIR, A., CARR, S. A., CHLANDA, P., ERHARD, F. & MUNSCHAUER, M. 2023. SND1 binds SARS-CoV-2 negative-sense RNA and promotes viral RNA synthesis through NSP9. Cell, 186, 4834-4850 e23. DIO:10.1016/j.cell.2023.09.002, PMID:37794589

SLETTEN, A. C., DAVIDSON, J. W., YAGABASAN, B., MOORES, S., SCHWAIGER-HABER, M., FUJIWARA, H., GALE, S., JIANG, X., SIDHU, R., GELMAN, S. J., ZHAO, S., PATTI, G. J., ORY, D. S. & SCHAFFER, J. E. 2021. Loss of SNORA73 reprograms cellular metabolism and protects against steatohepatitis. Nat Commun, 12, 5214. DIO:10.1038/s41467-021-25457-y, PMID:34471131

TILLMAN, E. J. & ROLPH, T. 2020. FGF21: An Emerging Therapeutic Target for Non-Alcoholic Steatohepatitis and Related Metabolic Diseases. Front Endocrinol (Lausanne), 11, 601290. DIO:10.3389/fendo.2020.601290, PMID:33381084

ZHENG, J., ZHANG, Q., ZHAO, Z., QIU, Y., ZHOU, Y., WU, Z., JIANG, C., WANG, X. & JIANG, X. 2023. Epigenetically silenced lncRNA SNAI3-AS1 promotes ferroptosis in glioma via perturbing the m(6)A-dependent recognition of Nrf2 mRNA mediated by SND1. J Exp Clin Cancer Res, 42, 127. DIO:10.1186/s13046-023-02684-3, PMID:37202791

(3) The role of PPARg in fatty liver diseases might be a rodent-specific phenomenon. PPARg agonist treatment in humans may actually reduce ectopic fat deposition by increasing fat storage in adipose tissues. The relevance of the findings to human diseases should be discussed.

We thank the reviewer for the detailed comment. As a transcription regulator of Cd36 and Cidea/c, it is well known that PPARγ plays major adipogenic and lipogenic roles in adipose tissue. Although the expression of PPARγ in the liver is very low under healthy conditions, induced expression of PPARγ in both hepatocytes and non-parenchymal cells (Kupffer cells, immune cells, and hepatic stellate cells (HSCs)) in the liver has a crucial role in the pathophysiology of MASLD (Lee et al., 2023b, Chen et al., 2023, Gross et al., 2017). The activation of PPARγ in the liver induces the adipogenic program to store fatty acids in lipid droplets as observed in adipocytes (Lee et al., 2018). Moreover, the inactivation of liver PPARγ abolished rosiglitazone-induced an increase in hepatic TG and improved hepatic steatosis in lipoatrophic AZIP mice (Gavrilova et al., 2003). Apart from promoting lipogenesis, PPARγ has also a crucial function in improving inflammation and fibrosis (Chen et al., 2023). Furthermore, there is a strong correlation between the onset of hepatic steatosis and hepatocyte-specific PPARγ expression. Clinical trials have also indicated that increased insulin resistance and hepatic PPARγ expressions were associated with NASH scores in some obese patients (Lee et al., 2023a, Mukherjee et al., 2022). Even though PPARγ’s primary function is in adipose tissue, patients with MASLD have much higher hepatic expression levels of PPARγ, reflecting the fact that PPARγ plays different roles in different tissues and cell types (Mukherjee et al., 2022). As these studies mentioned above, our result also hinted at the importance of PPARγ in the pathophysiology of MASLD. Snhg3 deficiency or overexpression respectively induced the decrease or increase in hepatic PPARγ. Moreover, administration of PPARγ antagonist T0070907 mitigated the hepatic Cd36 and Cidea/c increase and improved Snhg3-induced hepatic steatosis. However,  conflicting findings suggest that the expression of hepatic PPARγ is not increased as steatosis develops in humans and in clinical studies and that PPARγ agonists administration didn’t aggravate liver steatosis (Gross et al., 2017). Thus, understanding how the hepatic PPARγ expression is regulated may provide a new avenue to prevent and treat the MASLD (Lee et al., 2018). We also discussed it in revised manuscript, please refer the first paragraph in the section of Discussion in p13.

References

CHEN, H., TAN, H., WAN, J., ZENG, Y., WANG, J., WANG, H. & LU, X. 2023. PPAR-gamma signaling in nonalcoholic fatty liver disease: Pathogenesis and therapeutic targets. Pharmacol Ther, 245, 108391. DIO:10.1016/j.pharmthera.2023.108391, PMID:36963510

GAVRILOVA, O., HALUZIK, M., MATSUSUE, K., CUTSON, J. J., JOHNSON, L., DIETZ, K. R., NICOL, C. J., VINSON, C., GONZALEZ, F. J. & REITMAN, M. L. 2003. Liver peroxisome proliferator-activated receptor gamma contributes to hepatic steatosis, triglyceride clearance, and regulation of body fat mass. J Biol Chem, 278, 34268-76. DIO:10.1074/jbc.M300043200, PMID:12805374

GROSS, B., PAWLAK, M., LEFEBVRE, P. & STAELS, B. 2017. PPARs in obesity-induced T2DM, dyslipidaemia and NAFLD. Nat Rev Endocrinol, 13, 36-49. DIO:10.1038/nrendo.2016.135, PMID:27636730

LEE, S. M., MURATALLA, J., KARIMI, S., DIAZ-RUIZ, A., FRUTOS, M. D., GUZMAN, G., RAMOS-MOLINA, B. & CORDOBA-CHACON, J. 2023a. Hepatocyte PPARgamma contributes to the progression of non-alcoholic steatohepatitis in male and female obese mice. Cell Mol Life Sci, 80, 39. DIO:10.1007/s00018-022-04629-z, PMID:36629912

LEE, S. M., MURATALLA, J., SIERRA-CRUZ, M. & CORDOBA-CHACON, J. 2023b. Role of hepatic peroxisome proliferator-activated receptor gamma in non-alcoholic fatty liver disease. J Endocrinol, 257. DIO:10.1530/JOE-22-0155, PMID:36688873

LEE, Y. K., PARK, J. E., LEE, M. & HARDWICK, J. P. 2018. Hepatic lipid homeostasis by peroxisome proliferator-activated receptor gamma 2. Liver Res, 2, 209-215. DIO:10.1016/j.livres.2018.12.001, PMID:31245168

MUKHERJEE, A. G., WANJARI, U. R., GOPALAKRISHNAN, A. V., KATTURAJAN, R., KANNAMPUZHA, S., MURALI, R., NAMACHIVAYAM, A., GANESAN, R., RENU, K., DEY, A., VELLINGIRI, B. & PRINCE, S. E. 2022. Exploring the Regulatory Role of ncRNA in NAFLD: A Particular Focus on PPARs. Cells, 11. DIO:10.3390/cells11243959, PMID:36552725

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

As a general strategy for the revision, I would advise the authors to focus on strengthening the analysis of the liver with the two most important figures being Figure 2 and Figure 3. The mechanism as it stands is problematic which reduces the impact of the animal studies despite substantial efforts from the authors. Consider removing or toning down some of the studies focused on mechanisms in the nucleus, including changing the title.

We thank the reviewer for the detailed comment. In this study, hepatocyte-specific Snhg3 deficiency decreased body and liver weight, alleviated hepatic steatosis and promoted hepatic fatty acid metabolism in DIO mice, whereas overexpression induced the opposite effect. The hepatic differentially expressed genes (DEGs) between the DIO Snhg3-HKI and control WT mice using RNA-Seq and revealed that Snhg3 exerts a global effect on the expression of genes involved in fatty acid metabolism using GSEA (Figure 4B). RT-qPCR analysis confirmed that the hepatic expression levels of some genes involved in fatty acid metabolism, including Cd36, Cidea/c and Scd1/2, were upregulated in Snhg3-HKO mice and were downregulated in Snhg3-HKI mice compared to the controls (Figure 4C). Moreover, deficiency and overexpression of Snhg3 respectively decreased and increased the expression of profibrotic genes, such as Col1a1 and Col1a2, but had no effects on the pro-inflammatory factors, including Tgfβ1, Tnfα, Il6 and Il1β (figure supplement 3A and B). The results indicated that Snhg3 involved in hepatic steatosis through regulating fatty acid metabolism. Furthermore, PPARγ was selected to study its role in Snhg3-induced hepatic steatosis by integrated analyzing the data from CUT&Tag-Seq, ATAC-Seq and RNA-Seq. Finally, inhibition of PPARγ with T0070907 alleviated Snhg3 induced Cd36 and Cidea/c increases and improved Snhg3-aggravated hepatic steatosis. In summary, we confirmed that SND1/H3K27me3/PPARγ is partially responsible for Sngh3-inuced hepatic steatosis. As the reviewer suggested, we replaced the title with “LncRNA-Snhg3 Aggravates Hepatic Steatosis via PPARγ Signaling”.

(1) How is steatosis changing in the liver? Is this due to a change in fatty acid uptake, lipogenesis/synthesis, beta-oxidation, trig secretion, etc..? The analysis in Figures 2 and 3 is mostly focused on metabolic chamber studies which seem distracting, particularly in the absence of a mechanism and given a liver-specific perturbation. The authors should use a combination of targeted gene expression, protein blots, and lipid flux measurements to provide better insights here. The histology in Figure 2H suggests a very dramatic effect but does match with lipid measurements in 2I.

We thank the reviewer for the detailed comment. The pathogenesis of MASLD has not been entirely elucidated. Multifarious factors such as genetic and epigenetic factors, nutritional factors, insulin resistance, lipotoxicity, microbiome, fibrogenesis and hormones secreted from the adipose tissue, are recognized to be involved in the development and progression of MASLD (Buzzetti et al., 2016, Lee et al., 2017, Rada et al., 2020, Sakurai et al., 2021, Friedman et al., 2018). In this study, we investigated the hepatic differentially expressed genes (DEGs) between the DIO Snhg3-HKI and control WT mice using RNA-Seq and revealed that Snhg3 exerts a global effect on the expression of genes involved in fatty acid metabolism using GSEA (Figure 4B). We validated the expression of some DEGs involved in fatty acid metabolism by RT-qPCR. The results showed that the hepatic expression levels of some genes involved in fatty acid metabolism, including Cd36, Cidea/c and Scd1/2 were upregulated in Snhg3-HKO mice and were downregulated in Snhg3-HKI mice compared to the controls (Figure 4C), respectively. Additionally, we re-analyzed the metabolic chamber data using CalR and the results showed that there were no obvious differences in heat production, total oxygen consumption, carbon dioxide production or RER between DIO Snhg3-HKO or DIO Snhg3-HKI and the corresponding control mice (figure supplement 1C and 2C). Unfortunately, we did not detect lipid flux due to limited experimental conditions. However, in summary, our results indicated that Snhg3 is involved in hepatic steatosis by regulating fatty acid metabolism. Please check them in the first paragraph in p8.

Additionally, we determined the hepatic TC levels in other batch of DIO Snhg3-HKO and control mice and found there was no difference in hepatic TC (as below) between DIO Snhg3-HKO and control mice fed HFD 18 weeks. Perhaps the apparent difference in TC requires a prolonged high-fat diet feeding time.

Author response image 1.

Hepatic TC contents of in DIO Snhg3-Flox and Snhg3-HKO mice.

References

BUZZETTI, E., PINZANI, M. & TSOCHATZIS, E. A. 2016. The multiple-hit pathogenesis of non-alcoholic fatty liver disease (NAFLD). Metabolism, 65, 1038-48. DIO:10.1016/j.metabol.2015.12.012, PMID:26823198

FRIEDMAN, S. L., NEUSCHWANDER-TETRI, B. A., RINELLA, M. & SANYAL, A. J. 2018. Mechanisms of NAFLD development and therapeutic strategies. Nat Med, 24, 908-922. DIO:10.1038/s41591-018-0104-9, PMID:29967350

LEE, J., KIM, Y., FRISO, S. & CHOI, S. W. 2017. Epigenetics in non-alcoholic fatty liver disease. Mol Aspects Med, 54, 78-88. DIO:10.1016/j.mam.2016.11.008, PMID:27889327

RADA, P., GONZALEZ-RODRIGUEZ, A., GARCIA-MONZON, C. & VALVERDE, A. M. 2020. Understanding lipotoxicity in NAFLD pathogenesis: is CD36 a key driver? Cell Death Dis, 11, 802. DIO:10.1038/s41419-020-03003-w, PMID:32978374

SAKURAI, Y., KUBOTA, N., YAMAUCHI, T. & KADOWAKI, T. 2021. Role of Insulin Resistance in MAFLD. Int J Mol Sci, 22. DIO:10.3390/ijms22084156, PMID:33923817

(2) Throughout the manuscript the authors make claims about liver disease models, but this is not well supported since markers of advanced liver disease are not examined. The authors should stain and show expression for fibrosis and inflammation.

We thank the reviewer for the detailed comment. Metabolic dysfunction-associated fatty liver disease (MASLD) is characterized by excess liver fat in the absence of significant alcohol consumption. It can progress from simple steatosis to metabolic dysfunction-associated steatohepatitis (MASH) and fibrosis and eventually to chronic progressive diseases such as cirrhosis, end-stage liver failure, and hepatocellular carcinoma (Loomba et al., 2021). As the reviewer suggested, we detected the effect of Snhg3 on liver fibrosis and inflammation. The results showed no hepatic fibrosis phenotype was seen in Snhg3-HKO and Snhg3-HKI mice (figures supplement 1D and 2D). Moreover, deficiency and overexpression of Snhg3 respectively decreased and increased the expression of profibrotic genes, such as collagen type I alpha 1/2 (Col1a1 and Col1a2), but had no effects on the pro-inflammatory factors including Tgf-β, Tnf-α, Il-6 and Il-1β (figure supplement 3A and 3B). Inflammation is an absolute requirement for fibrosis because factors from injured hepatocytes alone are not sufficient to directly activate HSCs and lead to fibrosis (Kisseleva and Brenner, 2021). Additionally, previous studies indicated that exposure to HFD for more 24 weeks causes less severe fibrosis (Alshawsh et al., 2022). In future, the effect of Snhg3 on hepatic fibrosis in mice need to be elucidated by prolonged high-fat feeding or by adopting methionine- and choline deficient diet (MCD) feeding. Please check them in the second paragraph in the section of Discussion in p13.

References

ALSHAWSH, M. A., ALSALAHI, A., ALSHEHADE, S. A., SAGHIR, S. A. M., AHMEDA, A. F., AL ZARZOUR, R. H. & MAHMOUD, A. M. 2022. A Comparison of the Gene Expression Profiles of Non-Alcoholic Fatty Liver Disease between Animal Models of a High-Fat Diet and Methionine-Choline-Deficient Diet. Molecules, 27. DIO:10.3390/molecules27030858, PMID:35164140

KISSELEVA, T. & BRENNER, D. 2021. Molecular and cellular mechanisms of liver fibrosis and its regression. Nat Rev Gastroenterol Hepatol, 18, 151-166. DIO:10.1038/s41575-020-00372-7, PMID:33128017

LOOMBA, R., FRIEDMAN, S. L. & SHULMAN, G. I. 2021. Mechanisms and disease consequences of nonalcoholic fatty liver disease. Cell, 184, 2537-2564. DIO:10.1016/j.cell.2021.04.015, PMID:33989548

(3) Publicly available datasets show that PPARG protein is not expressed in the liver (Science 2015 347(6220):1260419, PMID: 25613900). Are the authors sure this is not an effect on another PPAR isoform like alpha? ChIP and RNA-seq pathway readouts do not distinguish between different isoforms.

We thank the reviewer for the detailed comment. As a transcription regulator of Cd36 and Cidea/c, it is well known that PPARγ plays major adipogenic and lipogenic roles in adipose tissue. Although the expression of PPARγ in the liver is very low under healthy conditions, induced expression of PPARγ in both hepatocytes and non-parenchymal cells (Kupffer cells, immune cells, and hepatic stellate cells (HSCs)) in the liver has a crucial role in the pathophysiology of MASLD (Lee et al., 2023b, Chen et al., 2023, Gross et al., 2017). The activation of PPARγ in the liver induces the adipogenic program to store fatty acids in lipid droplets as observed in adipocytes (Lee et al., 2018). Moreover, the inactivation of liver PPARγ abolished rosiglitazone-induced an increase in hepatic TG and improved hepatic steatosis in lipoatrophic AZIP mice (Gavrilova et al., 2003). Apart from promoting lipogenesis, PPARγ has also a crucial function in improving inflammation and fibrosis (Chen et al., 2023). Furthermore, there is a strong correlation between the onset of hepatic steatosis and hepatocyte-specific PPARγ expression. Clinical trials have also indicated that increased insulin resistance and hepatic PPARγ expressions were associated with NASH scores in some obese patients (Lee et al., 2023a, Mukherjee et al., 2022). Even though PPARγ’s primary function is in adipose tissue, patients with MASLD have much higher hepatic expression levels of PPARγ, reflecting the fact that PPARγ plays different roles in different tissues and cell types (Mukherjee et al., 2022). As these studies mentioned above, our result also hinted at the importance of PPARγ in the pathophysiology of MASLD. Snhg3 deficiency or overexpression respectively induced the decrease or increase in hepatic PPARγ. Moreover, administration of PPARγ antagonist T0070907 mitigated the hepatic Cd36 and Cidea/c increase and improved Snhg3-induced hepatic steatosis. However,  conflicting findings suggest that the expression of hepatic PPARγ is not increased as steatosis develops in humans and in clinical studies and that PPARγ agonists administration didn’t aggravate liver steatosis (Gross et al., 2017). Thus, understanding how the hepatic PPARγ expression is regulated may provide a new avenue to prevent and treat the MASLD (Lee et al., 2018). We also discussed it in revised manuscript, please refer the first paragraph in the section of Discussion in p13 in revised manuscript.

PPARα, most highly expressed in the liver, transcriptionally regulates lipid catabolism by regulating the expression of genes mediating triglyceride hydrolysis, fatty acid transport, and β-oxidation. Activators of PPARα decrease plasma triglycerides by inhibiting its synthesis and accelerating its hydrolysis (Chen et al., 2023). Mice with deletion of the Pparα gene exhibited more hepatic steatosis under HFD induction. As the reviewer suggested, we investigated the effect of Snhg3 on Pparα expression.  The result showed that both deficiency of Snhg3 or overexpression of Snhg3 doesn’t affect the mRNA level of Pparα as showing below, indicating that Snhg3-induced lipid accumulation independent on PPARα. Additionally, the exon, upstream 2k, 5’-UTR and intron regions of Pparγ, not Pparα, were enriched with the H3K27me3 mark (fold_enrichment = 4.15697) in the liver of DIO Snhg3-HKO mice using the CUT&Tag assay (table supplement 8), which was further confirmed by ChIP (Figure 6F and G). Therefore, we choose PPARγ to study its role in Sngh3-induced hepatic steatosis by integrated analyzing the data from CUT&Tag-Seq, ATAC-Seq and RNA-Seq.

Author response image 2.

The mRNA levels of hepatic Pparα expression in DIO Snhg3-HKO mice and Snhg3-HKI mice compared to the controls.

References

CHEN, H., TAN, H., WAN, J., ZENG, Y., WANG, J., WANG, H. & LU, X. 2023. PPAR-gamma signaling in nonalcoholic fatty liver disease: Pathogenesis and therapeutic targets. Pharmacol Ther, 245, 108391. DIO:10.1016/j.pharmthera.2023.108391, PMID:36963510

GAVRILOVA, O., HALUZIK, M., MATSUSUE, K., CUTSON, J. J., JOHNSON, L., DIETZ, K. R., NICOL, C. J., VINSON, C., GONZALEZ, F. J. & REITMAN, M. L. 2003. Liver peroxisome proliferator-activated receptor gamma contributes to hepatic steatosis, triglyceride clearance, and regulation of body fat mass. J Biol Chem, 278, 34268-76. DIO:10.1074/jbc.M300043200, PMID:12805374

GROSS, B., PAWLAK, M., LEFEBVRE, P. & STAELS, B. 2017. PPARs in obesity-induced T2DM, dyslipidaemia and NAFLD. Nat Rev Endocrinol, 13, 36-49. DIO:10.1038/nrendo.2016.135, PMID:27636730

LEE, S. M., MURATALLA, J., KARIMI, S., DIAZ-RUIZ, A., FRUTOS, M. D., GUZMAN, G., RAMOS-MOLINA, B. & CORDOBA-CHACON, J. 2023a. Hepatocyte PPARgamma contributes to the progression of non-alcoholic steatohepatitis in male and female obese mice. Cell Mol Life Sci, 80, 39. DIO:10.1007/s00018-022-04629-z, PMID:36629912

LEE, S. M., MURATALLA, J., SIERRA-CRUZ, M. & CORDOBA-CHACON, J. 2023b. Role of hepatic peroxisome proliferator-activated receptor gamma in non-alcoholic fatty liver disease. J Endocrinol, 257. DIO:10.1530/JOE-22-0155, PMID:36688873

LEE, Y. K., PARK, J. E., LEE, M. & HARDWICK, J. P. 2018. Hepatic lipid homeostasis by peroxisome proliferator-activated receptor gamma 2. Liver Res, 2, 209-215. DIO:10.1016/j.livres.2018.12.001, PMID:31245168

MUKHERJEE, A. G., WANJARI, U. R., GOPALAKRISHNAN, A. V., KATTURAJAN, R., KANNAMPUZHA, S., MURALI, R., NAMACHIVAYAM, A., GANESAN, R., RENU, K., DEY, A., VELLINGIRI, B. & PRINCE, S. E. 2022. Exploring the Regulatory Role of ncRNA in NAFLD: A Particular Focus on PPARs. Cells, 11. DIO:10.3390/cells11243959, PMID:36552725

(4) Previous work suggests that SNHG3 regulates its neighboring gene MED18 which is an important regulator of global transcription. Could some of the observed effects be due to changes in MED18 or other neighboring genes?

We thank the reviewer for the detailed comment. Previous work suggested that human SNHG3 promotes progression of gastric cancer by regulating neighboring MED18 gene methylation (Xuan and Wang, 2019). Here, we studied the effect of mouse Snhg3 on Med18 and the result showed that Snhg3 had no effect on the mRNA levels of Med18 (as below). Additionally, we also tested the effect of mouse Snhg3 on its neighboring gene, regulator of chromosome condensation 1 (Rcc1). Although deficiency of Snhg3 inhibited the mRNA level of Rcc1, overexpression of Snhg3 doesn’t affect the mRNA level of Rcc1 as showing below. RCC1, the only known guanine nucleotide exchange factor in the nucleus for Ran, a nuclear Ras-like G protein, directly participates in cellular processes such as nuclear envelope formation, nucleocytoplasmic transport, and spindle formation (Ren et al., 2020). RCC1 also regulates chromatin condensation in the late S and early M phases of the cell cycle. Many studies have found that RCC1 plays an important role in tumors. Furthermore, whether Rcc1 mediates the alleviated effect on MASLD of Snhg3 needs to be further investigated.

Author response image 3.

The mRNA levels of hepatic Rcc1 and Med18 expression in DIO Snhg3-HKO mice and Snhg3-HKI mice compared to the controls.

References

REN, X., JIANG, K. & ZHANG, F. 2020. The Multifaceted Roles of RCC1 in Tumorigenesis. Front Mol Biosci, 7, 225. DIO:10.3389/fmolb.2020.00225, PMID:33102517

XUAN, Y. & WANG, Y. 2019. Long non-coding RNA SNHG3 promotes progression of gastric cancer by regulating neighboring MED18 gene methylation. Cell Death Dis, 10, 694. DIO:10.1038/s41419-019-1940-3, PMID:31534128

(5) The claim that Snhg3 regulates SND1 protein stability seems subtle. There is data inconsistency between different panels regarding this regulation including Figure 5I, Figure 6A, and Figure 7E. In addition, is ubiquitination happening in the nucleus where Snhg3 is expressed?

We thank the reviewer for the detailed comment. The effect of Snhg3-induced SND1 expression had been confirmed by western blotting, please check them in Figure 5I, Figure 6A, Figure 7E and corresponding primary data. Additionally, Snhg3-induced SND1 protein stability seemed subtle, indicating there may be other mechanism by which Snhg3 promotes SND1, such as riboregulation. We had added it in the section of Discussion, please check it in the second paragraph in p16.

Additionally, we did not detect the sites where SND1 is modified by ubiquitination. Our results showed that Snhg3 was more localized in the nucleus (Figure 1D) and Snhg3 also promoted the nuclear localization of SND1 (Figure 5O). We had revised the diagram of Snhg3 action in Figure 8G. Please check them in revised manuscript.

(6) The authors show that the loss of Snhg3 changes the global H3K27me3 level. Few enzymes modify H3K27me3 levels. Did the authors check for an interaction between EZH2, Jmjd3, UTX, and Snhg3/SND1?

We thank the reviewer for the detailed comment. It is crucial to ascertain whether SND1 itself functions as a new demethylase or if it influences other demethylases, such as Jmjd3, enhancer of zeste homolog 2 (EZH2), and ubiquitously transcribed tetratricopeptide repeat on chromosome X (UTX). The precise mechanism by which SND1 regulates H3K27me3 is still unclear and hence requires further investigation. We had added the limitations in the section of Discussion and please check it in the third paragraph in p17.

(7) Can the authors speculate if the findings related to Snhg3/SND1 extend to humans?

We thank the reviewer for the detailed comment. Since the sequence of Snhg3 is not conserved between mice and humans, the findings in this manuscript may not be applicable to humans, but the detail need to be further exploited.

(8) As a general rule the figures are too small or difficult to read with limited details in the figure legends which limits evaluation. For example, Figure 1B and almost all of 4 cannot read labels. Figure 2, cannot see the snapshots show of mice or livers. What figure is supporting the claim that snhg3KI are more 'hyper-accessible'? Can the authors clarify what Figure 4H is referring to?

We thank the reviewer for the detailed comment. We have provided high quality figures in our revised manuscript.

The ‘hyper-accessible’ state in the liver of Snhg3-HKI mice was inferred by the differentially accessible regions (DARs), that is, we discovered 4305 DARs were more accessible in Snhg3-HKI mice and only 2505 DARs were more accessible in control mice and please refer table supplement 3).

The result of Figure 4H about heatmap for Cd36 was from hepatic RNA-seq of DIO Snhg3-HKI and control WT mice. For avoiding ambiguity, we have removed it.

(9) Authors stated that upon Snhg3 knock out, more genes are upregulated(1028) than downregulated(365). This description does not match Figure 4A. It seems in Figure 4A there are equal numbers of up and downregulated genes.

We thank the reviewer for the detailed question. We apologized for this mistake and have corrected it.

(10) Provide a schematic of the knockout and KI strategy in the supplement.

We thank the reviewer for the detailed comment. We had included the knockout and KI strategy in figure supplement 1A and B, and 2A.

Reviewer #2 (Recommendations For The Authors):

(1) Metabolic cage data need to be reanalyzed with CalR (particularly when the body weights are significantly different).

We thank the reviewer for the detailed comment. We reanalyzed the metabolic cage data using CalR (Mina et al., 2018). The results showed that there were no obvious differences in heat production, total oxygen consumption, carbon dioxide production and the respiratory exchange ratio between DIO Snhg3-HKO and control mice. Similar to DIO Snhg3-HKO mice, there was also no differences in heat production, total oxygen consumption, carbon dioxide production, and RER between DIO Snhg3-HKI mice and WT mice. Please check them in figure supplement 1C and 2C, and Mouse Calorimetry in Materials and Methods.

Reference

MINA, A. I., LECLAIR, R. A., LECLAIR, K. B., COHEN, D. E., LANTIER, L. & BANKS, A. S. 2018. CalR: A Web-Based Analysis Tool for Indirect Calorimetry Experiments. Cell Metab, 28, 656-666 e1. DIO:10.1016/j.cmet.2018.06.019, PMID:30017358

(2) ITT in Figure 2F should also be presented as % of the initial glucose level, which would reveal that there is no difference between WT and KO.

We thank the reviewer for the detailed comment. We repeated ITT experiment and include the new data in revised manuscript, please check it in Figure 2C.

(3) The fasting glucose results are inconsistent between ITT and GTT. Is there any difference in fasting glucose?

We thank the reviewer for the questions. The difference between GTT and ITT was caused owing to different fasting time, that is, mice were fasted for 6 h in ITT and were fasted for 16 h in GTT. It seems that Snhg3 doesn’t affect short- and longer-time fasting glucose levels and please refer Figures 2C and 3C.

Author Response:

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

Reviewer #1 (Public Review):

[...] The experiments are well-designed and carefully conducted. The conclusions of this work are in general well supported by the data. There are a couple of points that need to be addressed or tested.

1) It is unclear how LC phasic stimulation used in this study gates cortical plasticity without altering cellular responses (at least at the calcium imaging level). As the authors mentioned that Polack et al 2013 showed a significant effect of NE blockers in membrane potential and firing rate in V1 layer2/3 neurons during locomotion, it would be useful to test the effect of LC silencing (coupled to mismatch training) on both cellular response and cortical plasticity or applying NE antagonists in V1 in addition to LC optical stimulation. The latter experiment will also address which neuromodulator mediates plasticity, given that LC could co-release other modulators such as dopamine (Takeuchi et al. 2016 and Kempadoo et al. 2016). LC silencing experiment would establish a causal effect more convincingly than the activation experiment.

Regarding the question of how phasic stimulation could alter plasticity without affecting the response sizes or activity in general, we believe there are possibilities supported by previous literature. It has been shown that catecholamines can gate plasticity by acting on eligibility traces at synapses (He et al., 2015; Hong et al., 2022). In addition, all catecholamine receptors are metabotropic and influence intracellular signaling cascades, e.g., via adenylyl cyclase and phospholipases. Catecholamines can gate LTP and LTD via these signaling pathways in vitro (Seol et al., 2007). Both of these influences on plasticity at the molecular level do not necessitate or predict an effect on calcium activity levels. We have now expanded on this in the discussion of the revised manuscript.

While a loss of function experiment could add additional corroborating evidence that LC output is required for the plasticity seen, we did not perform loss-of-function experiments for three reasons:

1. The effects of artificial activity changes around physiological set point are likely not linear for increases and decreases. The problem with a loss of function experiment here is that neuromodulators like noradrenaline affect general aspects of neuronal function. This is apparent in Polack et al., 2013: during the pharmacological blocking experiment, the membrane hyperpolarizes, membrane variance becomes very low, and the cells are effectively silenced (Figure 7 of (Polack et al., 2013)), demonstrating an immediate impact on neuronal function when noradrenaline receptor activation is presumably taken below physiological/waking levels. In light of this, if we reduce LC output/noradrenergic receptor activation and find that plasticity is prevented, this could be the result of a direct influence on the plasticity process, or, the result of a disruption of another aspect of neuronal function, like synaptic transmission or spiking. We would therefore challenge the reviewer’s statement that a loss-of-function experiment would establish a causal effect more convincingly than the gain- of-function experiment that we performed.

2. The loss-of-function experiment is technically more difficult both in implementation and interpretation. Control mice show no sign of plasticity in locomotion modulation index (LMI) on the 10-minute timescale (Figure 4J), thus we would not expect to see any effect when blocking plasticity in this experiment. We would need to use dark-rearing and coupled-training of mice in the VR across development to elicit the relevant plasticity ((Attinger et al., 2017); manuscript Figure 5). We would then need to silence LC activity across days of VR experience to prevent the expected physiological levels of plasticity. Applying NE antagonists in V1 over the entire period of development seems very difficult. This would leave optogenetically silencing axons locally, which in addition to the problems of doing this acutely (Mahn et al., 2016; Raimondo et al., 2012), has not been demonstrated to work chronically over the duration of weeks. Thus, a negative result in this experiment will be difficult to interpret, and likely uninformative: We will not be able to distinguish whether the experimental approach did not work, or whether local LC silencing does nothing to plasticity.

Note that pharmacologically blocking noradrenaline receptors during LC stimulation in the plasticity experiment is also particularly challenging: they would need to be blocked throughout the entire 15 minute duration of the experiment with no changes in concentration of antagonist between the ‘before’ and ‘after’ phases, since the block itself is likely to affect the response size, as seen in Polack et al., 2013, creating a confound for plasticity-related changes in response size. Thus, we make no claim about which particular neuromodulator released by the LC is causing the plasticity.

1. There are several loss-of-function experiments reported in the literature using different developmental plasticity paradigms alongside pharmacological or genetic knockout approaches. These experiments show that chronic suppression of noradrenergic receptor activity prevents ocular dominance plasticity and auditory plasticity (Kasamatsu and Pettigrew, 1976; Shepard et al., 2015). Almost absent from the literature, however, are convincing gain-of-function plasticity experiments.

Overall, we feel that loss-of-function experiments may be a possible direction for future work but, given the technical difficulty and – in our opinion – limited benefit that these experiments, would provide in light of the evidence already provided for the claims we make, we have chosen not to perform these experiments at this time. Note that we already discuss some of the problems with loss-of-function experiments in the discussion.

2) The cortical responses to NE often exhibit an inverted U-curve, with higher or lower doses of NE showing more inhibitory effects. It is unclear how responses induced by optical LC stimulation compare or interact with the physiological activation of the LC during the mismatch. Since the authors only used one frequency stimulation pattern, some discussion or additional tests with a frequency range would be helpful.

This is correct, we do not know how the artificial activation of LC axons relates to physiological activation, e.g. under mismatch. The stimulation strength is intrinsically consistent in our study in the sense that the stimulation level to test for changes in neuronal activity is similar to that used to probe for plasticity effects. We suspect that the artificial activation results in much stronger LC activity than seen during mismatch responses, given that no sign of the plasticity in LMI seen in high ChrimsonR occurs in low ChrimsonR or control mice (Figure 4J). Note, that our conclusions do not rely on the assumption that the stimulation is matched to physiological levels of activation during the visuomotor mismatches that we assayed. The hypothesis that we put forward is that increasing levels of activation of the LC (reflecting increasing rates or amplitude of prediction errors across the brain) will result in increased levels of plasticity. We know that LC axons can reach levels of activity far higher than that seen during visuomotor mismatches, for instance during air puff responses, which constitute a form of positive prediction error (unexpected tactile input) (Figures 2C and S1C). The visuomotor mismatches used in this study were only used to demonstrate that LC activity is consistent with prediction error signaling. We have now expanded on these points in the discussion as suggested.

Reviewer #1 (Recommendations For The Authors):

1) In Figure 3E, there is a rebound response of ChrimsonR at the offset of the mismatch. Is that common? If so, what does it mean? If not, maybe replace it with a more common example trace.

This trace in fact represents the population average, so this offset response (or ‘rebound’) reflects a significant component of the population response to visual flow onset (i.e., mismatch offset), only under conditions of LC stimulation. See our response to reviewer 2 concerning this element of the response.

2) It would be helpful to have some discussions on how a mismatch signal reaches and activates LC from cortical neurons.

We have now added a short segment on this to the discussion.

Reviewer #2 (Public Review):

[...] The study provides very compelling data on a timely and fascinating topic in neuroscience. The authors carefully designed experiments and corresponding controls to exclude any confounding factors in the interpretation of neuronal activity in LC axons and cortical neurons. The quality of the data and the rigor of the analysis are important strengths of the study. I believe this study will have an important contribution to the field of system neuroscience by shedding new light on the role of a key neuromodulator. The results provide strong support for the claims of the study. However, I also believe that some results could have been strengthened by providing additional analyses and experimental controls. These points are discussed below.

Calcium signals in LC axons tend to respond with pupil dilation, air puffs, and locomotion as the authors reported. A more quantitative analysis such as a GLM model could help understand the relative contribution (and temporal relationship) of these variables in explaining calcium signals. This could also help compare signals obtained in the sensory and motor cortical domains. Indeed, the comparison in Figure 2 seems a bit incomplete since only "posterior versus anterior" comparisons have been performed and not within-group comparisons. I believe it is hard to properly assess differences or similarities between calcium signal amplitude measured in different mice and cranial windows as they are subject to important variability (caused by different levels of viral expression for instance). The authors should at the very least provide a full statistical comparison between/within groups through a GLM model that would provide a more systematic quantification.

To provide a more detailed comparison of responses, we have expanded on the analysis in Figure 2 to include comparative heatmaps from anterior and posterior imaging sites, as well as statistical comparisons of the response curves as a function of time. This shows how similar the responses are in the two regions.

Beyond this, we are not sure how a regression analysis (GLM or otherwise) would help support the main point we aim to make here. The responses in anterior and posterior regions are similar, which supports a broadcast model of LC function in the cortex, rather than specialized routing of prediction error signals to cortical areas. Linear contributions of the signals are apparent from the stimulus triggered responses, and while non-linear interactions between the different variables are certainly an interesting question, they go beyond the point we aim to make and would also not be captured by a regression analysis. In addition, we have refined our language replacing descriptors of ‘the same’ or ‘indistinguishable’ between the two regions with ‘similar’, to highlight that while we find no evidence of a difference, our analysis does not cover all possible differences that might appear when looking at non-linear interactions.

Previous studies using stimulations of the locus coeruleus or local iontophoresis of norepinephrine in sensory cortices have shown robust responses modulations (see McBurney-Lin et al., 2019, https://doi.org/10.1016/j.neubiorev.2019.06.009 for a review). The weak modulations observed in this study seem at odds with these reports. Given that the density of ChrimsonR-expressing axons varies across mice and that there are no direct measurements of their activation (besides pupil dilation), it is difficult to appreciate how they impact the local network. How does the density of ChrimsonR-expressing axons compare to the actual density of LC axons in V1? The authors could further discuss this point.

In terms of estimating the percentage of cortical axons labelled based on our axon density measurements: we refer to cortical LC axonal immunostaining in the literature to make this comparison.

In motor cortex, an average axon density of 0.07 µm/µm2 has been reported (Yin et al., 2021), and 0.09 µm/µm2 in prefrontal cortex (Sakakibara et al., 2021). Density of LC axons varies by cortical area, with higher density in motor cortex and medial areas than sensory areas (Agster et al., 2013): V1 axon density is roughly 70% of that in cingulate cortex (adjacent to motor and prefrontal cortices) (Nomura et al., 2014). So, we approximate a maximum average axon density in V1 of approximately 0.056 µm/µm2.

Because these published measurements were made from images taken of tissue volumes with larger z-depth (~ 10 µm) than our reported measurements (~ 1 µm), they appear much larger than the ranges reported in our manuscript (0.002 to 0.007 µm/µm2). We repeated the measurements in our data using images of volumes with 10 µm z-depth, and find that the percentage axons labelled in our study in high ChrimsonR-expressing mice ranges between 0.012 to 0.039 µm/µm2. This corresponds to between 20% to 70% of the density we would expect based on previous work. Note that this is a potentially significant underestimate, and therefore should be used as a lower bound: analyses in the literature use images from immunostaining, where the signal to background ratio is very high. In contrast, we did not transcardially perfuse our mice leading to significant background (especially in the pia/L1, where axon density is high - (Agster et al., 2013; Nomura et al., 2014)), and the intensity of the tdTomato is not especially high. We therefore are likely missing some narrow, dim, and superficial fibers in our analysis.

We also can quantify how our variance in axonal labelling affects our results: For the dataset in Figure 3, there doesn’t appear to be any correlation between the level of expression and the effect of stimulating the axons on the mismatch or visual flow responses for each animal (Author response image 1), while there is a significant correlation between the level of expression and the pupil dilation, consistent with the dataset shown in Figure 4. Thus, even in the most highly expressing mice, there is no clear effect on average response size at the level of the population. We have added these correlations to the revised manuscript as a new Figure S3.

**Author response image 1. **

Correlations between axon density and average effect of laser stimulation on stimulus responses and pupil dilation (data from manuscript Figure 3). Grey points show control mice, blue points show low ChrimsonR-expressing mice, and purple points show high ChrimsonR- expressing mice.

To our knowledge, there has not yet been any similar experiment reported utilizing local LC axonal optogenetic stimulation while recording cortical responses, so when comparing our results to those in the literature, there are several important methodological differences to keep in mind. The vast majority of the work demonstrating an effect of LC output/noradrenaline on responses in the cortex has been done using unit recordings, and while results are mixed, these have most often demonstrated a suppressive effect on spontaneous and/or evoked activity in the cortex (McBurney-Lin et al., 2019). In contrast to these studies, we do not see a major effect of LC stimulation either on baseline or evoked calcium activity (Figure 3), and, if anything, we see a minor potentiation of transient visual flow onset responses (see also Author response image 2). There could be several reasons why our stimulation does not have the same effect as these older studies:

1. Recording location: Unit recordings are often very biased toward highly active neurons (Margrie et al., 2002) and deeper layers of the cortex, while we are imaging from layer 2/3 – a layer notorious for sparse activity. In one of the few papers to record from superficial layers, it was been demonstrated that deeper layers in V1 are affected differently by LC stimulation methods compared to more superficial ones (Sato et al., 1989), with suppression more common in superficial layers. Thus, some differences between our results and those in the majority of the literature could simply be due to recording depth and the sampling bias of unit recordings.

2. Stimulation method: Most previous studies have manipulated LC output/noradrenaline levels by either iontophoretically applying noradrenergic receptor agonists, or by electrically stimulating the LC. Arguably, even though our optogenetic stimulation is still artificial, it represents a more physiologically relevant activation compared to iontophoresis, since the LC releases a number of neuromodulators including dopamine, and these will be released in a more physiological manner in the spatial domain and in terms of neuromodulator concentration. Electrical stimulation of the LC as used by previous studies differs from our optogenetic method in that LC axons will be stimulated across much wider regions of the brain (affecting both the cortex and many of its inputs), and it is not clear whether the cause of cortical response changes is in cortex or subcortical. In addition, electrical LC stimulation is not cell type specific.

3. Temporal features of stimulation: Few previous studies had the same level of temporal control over manipulating LC output that we had using optogenetics. Given that electrical stimulation generates electrical artifacts, coincident stimulation during the stimulus was not used in previous studies. Instead, the LC is often repeatedly or tonically stimulated, sometimes for many seconds, prior to the stimulus being presented. Iontophoresis also does not have the same temporal specificity and will lead to tonically raised receptor activity over a time course determined by washout times.

4. State specificity: Most previous studies have been performed under anesthesia – which is known to impact noradrenaline levels and LC activity (Müller et al., 2011). Thus, the acute effects of LC stimulation are likely not comparable between anesthesia and in the awake animal.

Due to these differences, it is hard to infer why our results differ compared to other papers. The study with the most similar methodology to ours is (Vazey et al., 2018), which used optogenetic stimulation directly into the mouse LC while recording spiking in deep layers of the somatosensory cortex with extracellular electrodes. Like us, they found that phasic optogenetic stimulation alone did not alter baseline spiking activity (Figure 2F of Vazey et al., 2018), and they found that in layers 5 and 6, short latency transient responses to foot touch were potentiated and recruited by simultaneous LC stimulation. While this finding appears more overt than the small modulations we see, it is qualitatively not so dissimilar from our finding that transient responses appear to be slightly potentiated when visual flow begins (Author response image 2). Differences in the degree of the effect may be due to differences in the layers recorded, the proportion of the LC recruited, or the fact anesthesia was used in Vazey et al., 2018.

Note that we only used one set of stimulation parameters for optogenetic stimulation, and it is always possible that using different parameters would result in different effects. We have now added a discussion on the topic to the revised manuscript.

In the analysis performed in Figure 3, it seems that red light stimulations used to drive ChrimsonR also have an indirect impact on V1 neurons through the retina. Indeed, figure 3D shows a similar response profile for ChrimsonR and control with calcium signals increasing at laser onset (ON response) and offset (OFF response). With that in mind, it is hard to interpret the results shown in Figure 3E-F without seeing the average calcium time course for Control mice. Are the responses following visual flow caused by LC activation or additional visual inputs? The authors should provide additional information to clarify this result.

This is a good point. When we plot the average difference between the stimulus response alone and the optogenetic stimulation + stimulus response, we do indeed find that there is a transient increase in response at the visual flow onset (and the offset of mismatch, which is where visual flow resumes), and this is only seen in ChrimsonR-expressing mice (Author response image 2). We therefore believe that these enhanced transients at visual flow onset could be due to the effect of ChrimsonR stimulation, and indeed previous studies have shown that LC stimulation can reduce the onset latency and latency jitter of afferent-evoked activity (Devilbiss and Waterhouse, 2004; Lecas, 2004), an effect which could mediate the differences we see. We have added this analysis to the revised manuscript in Figure 3 and added discussion accordingly.

**Author response image 2. **

Difference in responses to visual stimuli caused by optogenetic stimulation, calculated by subtracting the average response when no laser was presented from the average response when the laser was presented concurrent with the visual stimulus. Pink traces show the response difference for ChrimsonR-expressing mice, and grey shows the same for control mice. Black blocks below indicate consecutive timepoints after stimulation showing a significant difference between ChrimsonR and control as determined by hierarchical bootstrapping (p<0.05).

Some aspects of the described plasticity process remained unanswered. It is not clear over which time scale the locomotion modulation index changes and how many optogenetic stimulations are necessary or sufficient to saturate this index. Some of these questions could be addressed with the dataset of Figure 3 by measuring this index over different epochs of the imaging session (from early to late) to estimate the dynamics of the ongoing plasticity process (in comparison to control mice). Also, is there any behavioural consequence of plasticity/update of functional representation in V1? If plasticity gated by repeated LC activations reproduced visuomotor responses observed in mice that were exposed to visual stimulation only in the virtual environment, then I would expect to see a change in the locomotion behaviour (such as a change in speed distribution) as a result of the repeated LC stimulation. This would provide more compelling evidence for changes in internal models for visuomotor coupling in relation to its behavioural relevance. An experiment that could confirm the existence of the LC-gated learning process would be to change the gain of the visuomotor coupling and see if mice adapt faster with LC optogenetic activation compared to control mice with no ChrimsonR expression. Authors should discuss how they imagine the behavioural manifestation of this artificially-induced learning process in V1.

Regarding the question of plasticity time course: Unfortunately, owing to the paradigm used in Figure 3, the time course of the plasticity will not be quantifiable from this experiment. This is because in the first 10 minutes, the mouse is in closed loop visuomotor VR experience, undergoing optogenetic stimulation (this is the time period in which we record mismatches). We then shift to the open loop session to quantify the effect of optogenetic stimulation on visual flow responses. Since the plasticity is presumably happening during the closed loop phase, and we have no read-out of the plasticity during this phase (we do not have uncoupled visual flow onsets to quantify LMI in closed loop), it is not possible to track the plasticity over time.

Regarding the behavioral relevance of the plasticity: The type of plasticity we describe here is consistent with predictive, visuomotor plasticity in the form of a learned suppression of responses to self-generated visual feedback during movement. Intuitive purposes of this type of plasticity would be 1) to enable better detection of external moving objects by suppressing the predictable (and therefore redundant) self-generated visual motion and 2) to better detect changes in the geometry of the world (near objects have a larger visuomotor gain that far objects). In our paradigm, we have no intuitive read-out of the mouse’s perception of these things, and it is not clear to us that they would be reflected in locomotion speed, which does not differ between groups (manuscript Figure S5). Instead, we would need to turn to other paradigms for a clear behavioral read-out of predictive forms of sensorimotor learning: for instance, sensorimotor learning paradigms in the VR (such as those used in (Heindorf et al., 2018; Leinweber et al., 2017)), or novel paradigms that reinforce the mouse for detecting changes in the gain of the VR, or moving objects in the VR, using LC stimulation during the learning phase to assess if this improves acquisition. This is certainly a direction for future work. In the case of a positive effect, however, the link between the precise form of plasticity we quantify in this manuscript and the effect on the behavior would remain indirect, so we see this as beyond the scope of the manuscript. We have added a discussion on this topic to the revised manuscript.

Finally, control mice used as a comparison to mice expressing ChrimsonR in Figure 3 were not injected with a control viral vector expressing a fluorescent protein alone. Although it is unlikely that the procedure of injection could cause the results observed, it would have been a better control for the interpretation of the results.

We agree that this indeed would have been a better control. However, we believe that this is fortunately not a major problem for the interpretation of our results for two reasons:

1. The control and ChrimsonR expressing mice do not show major differences in the effect of optogenetic LC stimulation at the level of the calcium responses for all results in Figure 3, with the exception of the locomotion modulation indices (Figure 3I). Therefore, in terms of response size, there is no major effect compared to control animals that could be caused by the injection procedure, apart from marginally increased transient responses to visual flow onset – and, as the reviewer notes, it is difficult to see how the injection procedure would cause this effect.

2. The effect on locomotion modulation index (Figure 3I) was replicated with another set of mice in Figure 4C, for which we did have a form of injected control (‘Low ChrimsonR’), which did not show the same plasticity in locomotion modulation index (Figure 4E). We therefore know that at least the injection itself is not resulting in the plasticity effect seen.

Reviewer #2 (Recommendations For The Authors):

In experiments where axonal imaging was performed on LC axons, the authors should indicate the number of mice used in addition to the number of Field of View (FoV). Indeed, samples (FoVs) are not guaranteed to be independent as LC axons can span large cortical areas and the same axon can end up in different FoVs. Please provide statistics across mice/cranial windows to confirm the robustness of the results.

All information requested regarding animal numbers in axonal imaging are provided in the statistical Table S1, as well as in the text and figures (e.g., Figure 2A). Samples will be independent in time (as different FoVs were imaged on different days), but it is indeed possible that axon segments from different FoVs within an animal come from the same axon.

Averaging across animals greatly reduces statistical power. We have therefore implemented hierarchical bootstrapping instead: bootstrapping first occurs at the level of animal and then at the level of FoV. All p-values that were reported as significant in manuscript remained significant with this test, with no major reduction in significance level, with the exception of Figure S2B, where statistical significance was lost (p = 0.04 with Rank sum, p = 0.07 with hierarchical Bootstrapping). We therefore conclude that sampling from the same animals across days is not responsible for the significance of results reported.

References

Agster, K.L., Mejias-Aponte, C.A., Clark, B.D., Waterhouse, B.D., 2013. Evidence for a regional specificityi n the density and distribution of noradrenergic varicosities in rat cortex. Journal of Comparative Neurology 521, 2195–2207. https://doi.org/10.1002/cne.23270

Attinger, A., Wang, B., Keller, G.B., 2017. Visuomotor Coupling Shapes the Functional Development of Mouse Visual Cortex. Cell 169, 1291-1302.e14. https://doi.org/10.1016/j.cell.2017.05.023

Devilbiss, D.M., Waterhouse, B.D., 2004. The Effects of Tonic Locus Ceruleus Output on Sensory-Evoked Responses of Ventral Posterior Medial Thalamic and Barrel Field Cortical Neurons in the Awake Rat. J. Neurosci. 24, 10773–10785. https://doi.org/10.1523/JNEUROSCI.1573-04.2004

He, K., Huertas, M., Hong, S.Z., Tie, X., Hell, J.W., Shouval, H., Kirkwood, A., 2015. Distinct Eligibility Traces for LTP and LTD in Cortical Synapses. Neuron 88, 528–538. https://doi.org/10.1016/j.neuron.2015.09.037

Heindorf, M., Arber, S., Keller, G.B., 2018. Mouse Motor Cortex Coordinates the Behavioral Response to Unpredicted Sensory Feedback. Neuron 0. https://doi.org/10.1016/j.neuron.2018.07.046

Hong, S.Z., Mesik, L., Grossman, C.D., Cohen, J.Y., Lee, B., Severin, D., Lee, H.-K., Hell, J.W., Kirkwood, A., 2022. Norepinephrine potentiates and serotonin depresses visual cortical responses by transforming eligibility traces. Nat Commun 13, 3202. https://doi.org/10.1038/s41467-022-30827-1

Kasamatsu, T., Pettigrew, J.D., 1976. Depletion of brain catecholamines: failure of ocular dominance shift after monocular occlusion in kittens. Science 194, 206–209. https://doi.org/10.1126/science.959850

Lecas, J.-C., 2004. Locus coeruleus activation shortens synaptic drive while decreasing spike latency and jitter in sensorimotor cortex. Implications for neuronal integration. European Journal of Neuroscience 19, 2519–2530. https://doi.org/10.1111/j.0953-816X.2004.03341.x

Leinweber, M., Ward, D.R., Sobczak, J.M., Attinger, A., Keller, G.B., 2017. A Sensorimotor Circuit in Mouse Cortex for Visual Flow Predictions. Neuron 95, 1420-1432.e5. https://doi.org/10.1016/j.neuron.2017.08.036

Mahn, M., Prigge, M., Ron, S., Levy, R., Yizhar, O., 2016. Biophysical constraints of optogenetic inhibition at presynaptic terminals. Nat Neurosci 19, 554–556. https://doi.org/10.1038/nn.4266

Margrie, T.W., Brecht, M., Sakmann, B., 2002. In vivo, low-resistance, whole-cell recordings from neurons in the anaesthetized and awake mammalian brain. Pflugers Arch. 444, 491–498. https://doi.org/10.1007/s00424-002-0831-z

McBurney-Lin, J., Lu, J., Zuo, Y., Yang, H., 2019. Locus coeruleus-norepinephrine modulation of sensory processing and perception: A focused review. Neurosci Biobehav Rev 105, 190–199. https://doi.org/10.1016/j.neubiorev.2019.06.009

Müller, C.P., Pum, M.E., Amato, D., Schüttler, J., Huston, J.P., De Souza Silva, M.A., 2011. The in vivo neurochemistry of the brain during general anesthesia. Journal of Neurochemistry 119, 419–446. https://doi.org/10.1111/j.1471-4159.2011.07445.x

Nomura, S., Bouhadana, M., Morel, C., Faure, P., Cauli, B., Lambolez, B., Hepp, R., 2014. Noradrenalin and dopamine receptors both control cAMP-PKA signaling throughout the cerebral cortex. Front Cell Neurosci 8. https://doi.org/10.3389/fncel.2014.00247

Polack, P.-O., Friedman, J., Golshani, P., 2013. Cellular mechanisms of brain-state-dependent gain modulation in visual cortex. Nat Neurosci 16, 1331–1339. https://doi.org/10.1038/nn.3464

Raimondo, J.V., Kay, L., Ellender, T.J., Akerman, C.J., 2012. Optogenetic silencing strategies differ in their effects on inhibitory synaptic transmission. Nat Neurosci 15, 1102–1104. https://doi.org/10.1038/nn.3143

Sakakibara, Y., Hirota, Y., Ibaraki, K., Takei, K., Chikamatsu, S., Tsubokawa, Y., Saito, T., Saido, T.C., Sekiya, M., Iijima, K.M., n.d. Widespread Reduced Density of Noradrenergic Locus Coeruleus Axons in the App Knock-In Mouse Model of Amyloid-β Amyloidosis. J Alzheimers Dis 82, 1513–1530. https://doi.org/10.3233/JAD-210385

Sato, H., Fox, K., Daw, N.W., 1989. Effect of electrical stimulation of locus coeruleus on the activity of neurons in the cat visual cortex. Journal of Neurophysiology. https://doi.org/10.1152/jn.1989.62.4.946

Seol, G.H., Ziburkus, J., Huang, S., Song, L., Kim, I.T., Takamiya, K., Huganir, R.L., Lee, H.-K., Kirkwood, A., 2007. Neuromodulators control the polarity of spike-timing-dependent synaptic plasticity. Neuron 55, 919–929. https://doi.org/10.1016/j.neuron.2007.08.013

Shepard, K.N., Liles, L.C., Weinshenker, D., Liu, R.C., 2015. Norepinephrine is necessary for experience-dependent plasticity in the developing mouse auditory cortex. J Neurosci 35, 2432–2437.https://doi.org/10.1523/JNEUROSCI.0532-14.2015

Vazey, E.M., Moorman, D.E., Aston-Jones, G., 2018. Phasic locus coeruleus activity regulates cortical encoding of salience information. Proceedings of the National Academy of Sciences 115, E9439– E9448. https://doi.org/10.1073/pnas.1803716115

Yin, X., Jones, N., Yang, J., Asraoui, N., Mathieu, M.-E., Cai, L., Chen, S.X., 2021. Delayed motor learning in a 16p11.2 deletion mouse model of autism is rescued by locus coeruleus activation. Nat Neurosci 24, 646–657. https://doi.org/10.1038/s41593-021-00815-7

Author Response

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

Reviewer #1 (Public Review):

Thank you very much for your advices and comments. We took your suggestion into consideration and decided to modify it as you suggested. We will add more data and analysis on this topic in the article to make the exposition fuller.

1) There are different cells in liver tissue, in which BATF protein is expressed most.

Based on the analysis of single-cell public data (GEO accession: GSE129516), BATF is expressed in every cell cluster in the liver, with the highest expression in T cells and the least in cholangiocytes (Author response image 1).

Author response image 1.

2) The statistical data should be provided to support the liver specific over-expression of BATF.

The results of WB in figure2 (C & E) have been quantified and relevant content has been corrected.

3) For in vivo study, food intake is key data to exclude the change of energy intake.

Feed intake related result plots have been added to figureS2A.

4) For Fig.6 Since PD1 are also highly expressed in heart and spleen, how to exclude the effect of PD1 antibody on these tissues?

According to the images of the heart (Author response image 2 left) and spleen (Author response image 2 right) during mouse dissection, the morphology and size of the two organs were similar in HFD-CN and HFD-PD1 group. Moreover, relevant literature indicated that PD-1 blockade had little impact on the number and function of transferred T cells within the spleen(Peng et al.)，and anti-PD-1 had no effect on mouse splenic cell proliferation (Shindo et al.).Du et al. showed in their study that single use of PD-1 antibody (10 mg/kg, once every three days, for 4 weeks) did not affect mouse heart (Du et al.). Both our results and related literature indicated that PD 1 antibody should not have adverse effects on the heart and spleen.

Author response image 2.

Reviewer #2 (Public Review):

Thank you very much for your advices and comments. We have seriously considered your suggestion and will focus on it in our future research.

Weakness

1) BATF protein is also abundantly expressed in control hepatocyte, but the knockdown of BATF had no effect on lipid accumulation. Besides, the expression of BATF was elevated by high fat diets. So it will be interesting to investigate its role in the liver by using its hepatic conditional knockout mice.

We appreciate the reviewers' suggestion to investigate other functions of BATF in the liver besides its protective role in a high-fat environment. However, we did not use BATF knockout mice in this study because our data indicated that BATF knockdown had no effect on lipid accumulation. We will pursue further research and validation in future studies.

2) The data for the direct regulation of BATF on PD1 and IL-27 is not enough, it is better to carry out CHIP experiment to further confirm it.

Thank you for your valuable comments. The article by Kevin Man et al. found that, upregulation of transcription factor BATF regulates PD1 expression and repairs impaired cellular metabolism (Man et al.). This confirms that BATF has a regulatory effect on PD1. And in our manuscript, the dual luciferase reporter assay of BATF and PD1 confirmed that BATF can regulate the expression of PD1(Fig 5G). This confirms that BATF has a regulatory effect on PD1. We do not have conclusive evidence for a direct interaction between BATF and IL-27 yet, but there are some relevant studies that support their connection. For instance, BATF and IRF1 were found to be transcription factors induced early by IL-27 treatment, and essential for Tr1 cell differentiation and function, both in vitro and in vivo (Karwacz et al.). Moreover, Zhang et al. identified BATF as one of the transcription factors regulating IL-27 expression by transcription factor prediction and RNA sequencing analysis (Zhang et al.). These results lay the foundation for elucidating the regulation of PD1 and IL-27 by BATF.

Reviewer #2 (Recommendations For The Authors):

1. In Figure 3D, which subunit of AMPK was tested, alpha, beta or gamma?

Thank you for your valuable comments. We detected the expression level of AMPKα1, We have modified the relevant names in the figure and manuscript.

Reference：

Du, Shisuo, et al. "Pd-1 Modulates Radiation-Induced Cardiac Toxicity through Cytotoxic T Lymphocytes." 13.4 (2018): 510-20. Print.

Karwacz, Katarzyna, et al. "Critical Role of Irf1 and Batf in Forming Chromatin Landscape During Type 1 Regulatory Cell Differentiation." 18.4 (2017): 412-21. Print.

Man, Kevin, et al. "Transcription Factor Irf4 Promotes Cd8+ T Cell Exhaustion and Limits the Development of Memory-Like T Cells During Chronic Infection." 47.6 (2017): 1129-41. e5. Print.

Peng, Weiyi, et al. "Pd-1 Blockade Enhances T-Cell Migration to Tumors by Elevating Ifn-Γ Inducible Chemokinespd-1 Blockade Improves the Effectiveness of Act for Cancer." 72.20 (2012): 5209-18. Print.

Shindo, Yuichiro, et al. "Interleukin 7 and Anti-Programmed Cell Death 1 Antibody Have Differing Effects to Reverse Sepsis-Induced Immunosuppression." 43.4 (2015): 334. Print.

Zhang, Huiyuan, et al. "An Il-27-Driven Transcriptional Network Identifies Regulators of Il-10 Expression across T Helper Cell Subsets." 33.8 (2020): 108433. Print.

Author Response

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

eLife assessment

The authors describe a method to decouple the mechanisms supporting pancreatic progenitor self-renewal and expansion from feed-forward mechanisms promoting their differentiation. The findings are important because they have implications beyond a single subfield. The strength of evidence is solid in that the methods, data and analyses broadly support the claims with only minor weaknesses.

We are grateful for the substantial effort that reviewers put into reading our manuscript and providing such a detailed feedback. We have strived to address, as much as possible, all comments and criticisms. Thanks to the feedback, we believe that we have now a significantly improved manuscript. Below, there is a point-bypoint response.

Reviewer #1 (Public Review)

In this manuscript, the authors are developing a new protocol that aims at expanding pancreatic progenitors derived from human pluripotent stem cells under GMP-compliant conditions. The strategy is based on hypothesis-driven experiments that come from knowledge derived from pancreatic developmental biology.

The topic is of major interest in the view of the importance of amplifying human pancreatic progenitors (both for fundamental purposes and for future clinical applications). There is indeed currently a major lack of information on efficient conditions to reach this objective, despite major recurrent efforts by the scientific community.

Using their approach that combines stimulation of specific mitogenic pathways and inhibition of retinoic acid and specific branches of the TGF-beta and Wnt pathways, the authors claim to be able, in a highly robust and reproducible manner) to amplify in 10 passages the number of pancreatic progenitors (PP) by 2,000 folds, which is really an impressive breakthrough.

The work is globally well-performed and quite convincing. I have however some technical comments mainly related to the quantification of pancreatic progenitor amplification and to their differentiation into beta-like cells following amplification.

We thank the reviewer for the positive assessment. Below we provide a point-by-point response to specific comments and criticisms.

Reviewer #1 (Recommendations For The Authors)

Figure 1:

Panel A: What is exactly counted in Fig. 1A? Is it the number of PP (as indicated in the title) or the total number of cells? If it is PPs, was it done following PDX1/NKX6.1/SOX9 staining and FACS quantification? This question applies to a number of Figures and the authors should be clear on this point.

We now define ‘PP cells’ as ‘PP-containing cells’ (PP cells) the first time we use the term in the RESULTS section.

Panel D: I do not understand the source of TGFb1, GDF11, FGF18, PDGFA. Which cell type(s) express such factors in culture? I was not convinced that the signals are produced by PP and act through an autocrine loop. I have the same type of questions for the receptors: PDGFR on the second page of the results; RARs and RXRs on the third page.

We refer to these factors/receptors as components of a tentative autocrine loop. We agree we do not prove it and we now comment on this in the discussion section.

Figure 2:

FACS plots are very difficult to analyze for two reasons: I do not understand the meaning of the y axes (PDX1/SOX9). Does that mean that 100% of the cells were PDX1+/SOX9+? The authors should show the separated FACS plots. More importantly, the x axes indicate that NKX6.1 FACS staining is very weak. This is by far different from what can be read in publications performing the same types of experiments (publications by Millman, Otonkoski...as examples). How was quantification performed when it is so difficult to properly define positive vs negative populations? It is necessary to present proper "negative controls" for FACS experiments and to clearly indicate how positive versus cells were defined

We now explain the gating strategy better in the results section, all controls are included in figure S2.

Figure 3:

What is the exact "phenotype" of the cells that incorporated EdU: It would be really instructive to add PDX1/NKX6.1/SOX9 staining on top of EdU. I am also surprised that 20% of the cells stain positive for Annexin V. This is a huge fraction. Does that mean that many cells (20%) are dying and if the case, how amplification can take place under such deleterious conditions?

This is an interesting mechanistic point but performing these experiments would delay the publication of the final manuscript for too long. These assays were done at p3 in order to catch CINI cells that do not expand in most cases. It is important to note that cell death also appears higher in CINI cells. It is likely that the combination of these effects results in reproducible expansion under C5. We comment on the possibilities in the discussion section.

Figure 4:

On FACS plots the intensity at the single cell level (see x-axis of the figure) of the NKX6.1 staining is found to increase in Fig. 4G by 50-100 folds when compared to Fig. 4E. Is it expected? This should be discussed in the text. Do the authors observe the same increase by immunocytochemistry?

The apparent difference is actually 10-fold (from 2x102 to 2x103). We think that the most likely reason for this apparent increase is that at p0 we typically used very few cells for the FC in order to keep as many as possible for the subsequent expansion. If we had used more, we would be able to also detect cells with higher expression. As we mention in the bioinformatics analysis, NKX6 expression does increase with passaging and therefore it is also possible that at least part of this increase is real. However, we don’t have suitable data (same number of cells analyzed at each passage) to address this in a reliable manner.

Figure 5

Previous data from the scientific literature indicate that in vitro, by default, PP gives rise to duct-like cells. This is a bit described in the result section and supplementary figures taking into account the expression of transcription factors. However the data are not clearly explained and described in quite a qualitative manner. They should appear in a quantitative fashion (and the main figures), adding additional duct cell markers such as Carbonic anhydrase, SPP1, CFTR, and others. I assume that the authors can easily use their transcriptomic data to produce a Figure to be described and discussed in detail.

We think it can be misleading to use such markers (other than TFs and the latter only as a collective) because specific markers of terminal differentiation are more often than not expressed during development in multipotent progenitors, the most conspicuous example been CPA1. To illustrate the point, we used the RNA Seq data of and plotted the expression values of a panel of duct genes in isolated human fetal progenitors (Ramond et al., 2017) together with their expression in p0 PP and ePP cells from all three different procedure (please see below). All raw RNA Seq data were processed together to enable direct comparison. According to the analysis of Ramond et al the A population corresponds to MPCs, C to early endocrine progenitors (EP), D to late endocrine progenitors and, by inference and gene expression pattern B to BPs. Expression levels of all these markers were very similar suggesting that these markers cannot be used to distinguish between duct cells and progenitor cells. Importantly, SC-islets derived from either dPP or ePP cells express extremely low and similar levels of KRT19, a marker of duct cells. This latter information is now included in the last part of the results (Figure S7).

Author response image 1.

Fig. 7:<br /> The figure is a bit disappointing for 2 reasons. In A and B, the quality of INS, GCG, and SST staining is really poor. In E, GSIS is really difficult to interpret. They should not be presented as stimulatory indexes. The authors should present independently: INS content; INS secretion at low glucose; INS secretion at high glucose; INS secretion with KCL. Finally, the authors should indicate that glucose poorly (around 2 fold) activates insulin/C-Pept secretion in their stem-cell-derived islets.

We disagree with the quality assessment of the immunofluorescence. Stimulation indexes are also used very widely but we now provide data for actual C-peptide secretion normalized for DNA content of the SC-islets. For technical reasons we do not have normalized C-peptide secretion for human islets. However, we provide a direct comparison to the stimulation index of human islets assayed under the same conditions (2.7 mM glucose / 16.7 mM glucose / 16.7 mM glucose + 30 mM KCl) without presenting SC-islets separately and tweaking the glucose basal (lowering) and stimulation (increasing) levels to inflate the stimulation index. This is unfortunately common. In any case, we do not claim an improvement in the differentiation conditions and our S5-S7 steps may not be optimal but this is not the subject of this work.

Reviewer #2 (Public Review)

Summary

The paper presents a novel approach to expand iPSC-derived pdx1+/nkx6.1+ pancreas progenitors, making them potentially suitable for GMP-compatible protocols. This advancement represents a significant breakthrough for diabetes cell replacement therapies, as one of the current bottlenecks is the inability to expand PP without compromising their differentiation potential. The study employs a robust dataset and state-of-the-art methodology, unveiling crucial signaling pathways (eg TGF, Notch...) responsible for sustaining pancreas progenitors while preserving their differentiation potential in vitro.

Strengths

This paper has strong data, guided omics technology, clear aims, applicability to current protocols, and beneficial implications for diabetes research. The discussion on challenges adds depth to the study and encourages future research to build upon these important findings.

We thank the reviewer for the positive assessment. Below we provide a point-by-point response to general comments and criticisms.

Weaknesses

The paper does have some weaknesses that could be addressed to improve its overall clarity and impact. The writing style could benefit from simplification, as certain sections are explained in a convoluted manner and difficult to follow, in some instances, redundancy is evident. Furthermore, the legends accompanying figures should be self-explanatory, ensuring that readers can easily understand the presented data without the need to be checking along the paper for information.

We have simplified the text in several places and removed redundancies, particularly in the discussion. We revisited the figure legends and made minor corrections to increase clarity. However, regarding the figure legends, we think that adding the interpretation of the results would be redundant to the main text.

The culture conditions employed in the study might benefit from more systematic organization and documentation, making them easier to follow.<br /> There is a comparative Table (Table S1) where all conditions are summarized. We refer to this Table every time that we introduce a new condition. We also have a Table (Table S4) which presents all different media and components used it the differentiation procedure.

Another important aspect is the functionality of the expanded cells after differentiation. While the study provides valuable insights into the expansion of pancreas progenitors in vitro and does the basic tests to measure their functionality after differentiation the paper could be strengthened by exploring the behavior and efficacy of these cells deeper, and in an in vivo setting.

This will be done in a future study where we will also introduce a number of modifications in S5-S7

Quantifications for immunofluorescence (IF) data should be displayed.

We have not conducted quantifications of IFs because FC is much more objective and accurate. We have not conducted FC for CDX2 and AFP because all other data strongly favor C6 anyway. It should be noted that CDX2 and AFP expression is generally not addressed at all presumably because it raises uncomfortable questions and, to our knowledge, we are the first to address this so exhaustively.

Some claims made in the paper may come across as somewhat speculative.

We have now indicated so where applicable.

Additionally, while the paper discusses the potential adaptability of the method to GMP-compatible protocols, there is limited elaboration on how this transition would occur practically or any discussion of the challenges it might entail.

We have now added a paragraph discussing this in the discussion section.

Reviewer #2 (Recommendations For The Authors)

Related to Figure 1:

• Unclear if CINI or SB431542 + CINI was used (first paragraph of results...)

The paragraph was unclear and it is now rewritten

• Was the differentiation to PP similar between the different attempts? A basic QC for each Stem Cell technology differentiation would be good to include.

We added (Figure 1B) a comparison of expression data of general genes (QC) in PP cells showing very comparable patterns of expression. Some of these PP cells went on to expand and most did not but there is no apparent correlation of this with the gene expression data.

• qPCR data - relative fold? over what condition? (indicate on axis label)

We added a label as well as an explanation on p0 values in the figure legend

• FGF18/ PDGFA - worth including background in pancreas development as in the other factors.

Background information has been added

• Bioinformatics is a bit biased with a few genes selected - what are the DEGs / top enriched pathways? Maybe worth showing a volcano plot of the DEGs for example.

We have done all these standard analyses but we think that they did not contribute anything else useful to the study with the exception of pointing to the finding that the TGFb pathway is negatively correlated with expansion, and this is included in the study. The ‘unbiased’ analysis that the reviewer suggests did not turn out something else useful to exploit for the expansion. This does not mean that our approach is biased – in our view it is hypothesis-driven. As we also write in the manuscript, if in a certain pathway a key gene fails to be expressed, the pathway will not show up in any GO or GSEA analyses. However, the pathway will still be regulated. The RA and FGF18 cases clearly illustrate this. We realize that these analyses have become a standard but we think that it is not the only way to approach genomics data and these approaches did not offer much in the context of this study.

• The E2F part is very speculative

The pathway came up as a result of ‘unbiased’ GSEA analyses. However, we do agree and rephrased.

• The authors claim ' the negative correlation of TGFb signalling with expansion retrospectively justifies the use of A83 '. However, p0 is not treated with A83 - how can they tell that there is a correlation between TGFb signalling and expansion?

The correlation came from the RNA Seq data analysis during expansion. We have rephrased slightly to convey the message more clearly.

• Typo with TGFbeta inhibitor name is mispelled (A3801)

Corrected

• Page 5 - last paragraph - Table S3? (isnt it refering to S2?)

Since Table S2 is the list of the regulated genes and S3 is the list of the regulated signaling pathway components both are relevant here, we now refer to both.

• In the text Figure 2G should read Figure 1G (page 7, end of 1st paragraph).

Corrected

• 'Autocrine loop' existence – speculative

Added the phrase ‘we speculated’. We refer to this only as a tentative interpretation. We also elaborate in the discussion now.

Related to Figure 2:

• I am not sure if I would refer to chemical "activation/inhibition" of pathways as 'gain/loss of function'. Maybe this term is more adequate for genetic modifications.

For genetic manipulations, these terms are (supposed to be) accompanied by the adjective ‘genetic’ but to avoid misinterpretations we changed the terms to activation and inhibition as suggested.

• It would be good to include a summary of the different conditions as a schematic in one of the figures, to make it very clear to the reader what the conditions are.

We tried this in an early version of the manuscript but, in our view, it was adding complexity, rather than simplifying things. The problem is that as such the Table cannot be integrated in any figure if eg in Figure 2 it would be too early, if in Figure 4 it would be too late and so on. All conditions show up in detail in Table S1.

• Nkx6.1 - is the image representative? It looks like Nkx6.1 decreases over the passages.

We do mention in the text that ‘… even though expansion (in C5) appeared to somewhat reduce the number of NKX6.1+ cells. (Figure 2E-G). As we mentioned, this was one of the reasons to continue with other conditions (C6-C8).

• Upregulation of AFP/ CDX2 is a bit concerning - the IF for C5 p5 shows a high proportion of CDX2+ cells (Fig S2I). perhaps it would be good to quantify the IF.

It was concerning – this is why we then tested conditions C6-8. Since it is C6 that we propose at the end, it would be, in our view, extraneous to quantify CDX2 in C5.

• How do C5/C1/C0 compare to CINI?

We now remind the reader in the results section that CINI was not reproducible - so any other comparison would be extraneous.

Related to Figure 3:

• There is a 'Lore Ipsum' label above B

Corrected

Related to Figure 4:

• It is good that AFP expression is reduced at p10, but there seems to be a high proportion of AFP at p5. IF/FACS should be quantified.

We think that this would not add significantly since there are several other criteria, particularly the increase of the PDX1+/SOX9+/NKX6.1+ that clearly show that the C6 condition is preferable. Further elaboration of C6 could use such additional criteria. We comment on CDX2 / AFP in the discussion.

• CDX2 should be quantified by IF / FACS.

We think that this would not add significantly since there are several other criteria, particularly the increase of the PDX1+/SOX9+/NKX6.1+ that clearly show that the C6 condition is preferable. Further elaboration of C6 could use such additional criteria. We comment on CDX2 / AFP in the discussion.

• Karyotype analysis is good but not very precise when analyzing genetic micro alterations... what does a low-pass sequencing of the expanding lines look like? Are there any micro-deletions in the expanding lines?

This is an unusual request. Microdeletions may occur at any point – during passaging of hPS cells, differentiation as well as well as expansion but such data are so far not shown in publications – and reasonably so in our opinion. Thus, we have not done this analysis but it certainly would be appropriate in a clinical setting as part of QC.

• Data supporting that the cells can be cryopreserved and recovered with >85% survival rate is not provided.

We now provide data for the C6-mediated expansion (Figure 4J). The freezing procedure was developed during the time we were testing C5 and we don’t have sufficient data to show reliably the survival of the cells during C5 expansion. Thus, we have now removed the reference in the C5 part of the manuscript.

Related to Figure 5:

-Figure 5C - perhaps worth commenting on the different pathways that are enriched when cells undergo expansion and show some of the genes that are up/down regulated.

This is indeed of interest but since it will not address any specific question in the context of this work (eg is the endocrine program repressed?) and since it would not be followed by additional experiments we think that it would burden the manuscript unnecessarily. The data are accessible for any type of analysis through the GEO database.

• Figure S5D shows in vitro clustering away from in vivo PP - it would be good to explain how in vitro generated PP differs from their in vivo counterparts instead of restricting the comparison to the in vitro protocol.

We have added a possible interpretation of this observation in the results section and discuss, how one could go properly about this comparison.

• Quantification of Fig5F should be included. Is GP2 expression detectable by IF at p5 too?

We have quantified GP2 expression by FC at p10 but not at earlier stages. We include now the FC data in Fig5F

• Validation of Fig5G by qPCR would be good. PDX1 did not seem reduced by IF in Figure 4.

The purpose of Fig5G is to compare the expression of the same genes across different expansion approaches. Therefore, in our view, qPCRs would not be appropriate since we do not have samples from the other approaches. We did not claim a reduction in PDX1 expression.

• How can the authors explain the NGN3 expression at PP?

In our view, differentiation is a dynamic process and not all cells are synchronized at the same cell type, this is true in vivo and in vitro. Sc-RNA Seq data indeed show a small population of cells at PP that are NEUROG3+ (our unpublished data). We have now included this in the discussion.

Related to Figure 6:

• How do the different lines differ? Any statistical comparison between lines?

There is a paragraph dealing with the comparison of PP and ePP cells (p5 and p10) from different lines at the level of gene expression and the data are in Figure S6A-G. Then there is a paragraph addressing this at the level of PDX1/SOX9/NKX6.1 expression by FC. We have now expanded and rewrote the latter to include statistical comparisons across PPs from different lines at p0, p5 an p10

Related to Figure 7:

• Mention the use of micropatterned

Micropatterned wells - not really correct. They use Aggrewells, micropatterned plates are something else.

We changed ‘micropatterned wells’ into ‘microwells’

• Figure 7D, those are qPCR data. The label is inconsistent, why did they call it fold induction instead of fold change? Also, not sure if plotting the fold change to hPSC is the best here.

We use fold change when comparing the expression of the same gene at different passages but fold induction when comparing to its expression in hPS cells. We made sure it is also explained in the figure legends.

• Absolute values should be shown for the GSIS to determine basal insulin secretion. Also, sequential stimulation to address if the cells are able to respond to multiple glucose stimulations.

We include now the secreted amounts of human C-peptide under the different conditions (Figure S7) normalized for cell numbers using their DNA content for the normalization. The many parameters we have used suggest that dPP and ePP SC-islets are very similar. If we were claiming a better S5-S7 procedure, such an assay would have been necessary but in this context, we think it is not absolutely necessary.

• In vivo data would have strengthened the story. It is not clear if, in vivo, the cells will behave as the nonexpanded iPSC-derived beta cells.

We agree and these studies are under way but we do not expect to complete them soon. We feel that it is important that this work appears sooner rather than later.

Reviewer #3 (Public Review)

Summary:

In this work, Jarc et al. describe a method to decouple the mechanisms supporting progenitor self-renewal and expansion from feed-forward mechanisms promoting their differentiation.

The authors aimed at expanding pancreatic progenitor (PP) cells, strictly characterized as PDX1+/SOX9+/NKX6.1+ cells, for several rounds. This required finding the best cell culture conditions that allow sustaining PP cell proliferation along cell passages, while avoiding their further differentiation. They achieve this by comparing the transcriptome of PP cells that can be expanded for several passages against the transcriptome of unexpanded (just differentiated) PP cells.

The optimized culture conditions enabled the selection of PDX1+/SOX9+/NKX6.1+ PP cells and their consistent, 2000-fold, expansion over ten passages and 40-45 days. Transcriptome analyses confirmed the stabilization of PP identity and the effective suppression of differentiation. These optimized culture conditions consisted of substituting the Vitamin A containing B27 supplement with a B27 formulation devoid of vitamin A (to avoid retinoic acid (RA) signaling from an autocrine feed-forward loop), substituting A38-01 with the ALK5 II inhibitor (ALK5i II) that targets primarily ALK5, supplementation of medium with FGF18 (in addition to FGF2) and the canonical Wnt inhibitor IWR-1, and cell culture on vitronectin-N (VTN-N) as a substrate instead of Matrigel.

Strengths:

The strength of this work relies on a clever approach to identify cell culture modifications that allow expansion of PP cells (once differentiated) while maintaining, if not reinforcing, PP cell identity. Along the work, it is emphasized that PP cell identity is associated with the co-expression of PDX1, SOX9, and NKX6.1. The optimized protocol is unique (among the other datasets used in the comparison shown here) in inducing a strong upregulation of GP2, a unique marker of human fetal pancreas progenitors. Importantly GP2+ enriched hPS cell-derived PP cells are more efficiently differentiating into pancreatic endocrine cells (Aghazadeh et al., 2022; Ameri et al., 2017).

The unlimited expansion of PP cells reported here would allow scaling-up the generation of beta cells, for the cell therapy of diabetes, by eliminating a source of variability derived from the number of differentiation procedures to be carried out when starting at the hPS cell stage each time. The approach presented here would allow the selection of the most optimally differentiated PP cell population for subsequent expansion and storage. Among other conditions optimized, the authors report a role for Vitamin A in activating retinoic acid signaling in an autocrine feed-forward loop, and the supplementation with FGF18 to reinforce FGF2 signaling.

This is a relevant topic in the field of research, and some of the cell culture conditions reported here for PP expansion might have important implications in cell therapy approaches. Thus, the approach and results presented in this study could be of interest to researchers working in the field of in vitro pancreatic beta cell differentiation from hPSCs. Table S1 and Table S4 are clearly detailed and extremely instrumental to this aim.

We thank the reviewer for the positive assessment. Below we provide a point-by-point response to general comments and criticisms.

Weaknesses

The authors strictly define PP cells as PDX1+/SOX9+/NKX6.1+ cells, and this phenotype was convincingly characterized by immunofluorescence, RT-qPCR, and FACS analysis along the work. However, broadly defined PDX1+/SOX9+/NKX6.1+ could include pancreatic multipotent progenitor cells (MPC, defined as PDX1+/SOX9+/NKX6.1+/PTF1A+ cells) or pancreatic bipotent progenitors (BP, defined as PDX1+/SOX9+/NKX6.1+/PTF1A-) cells. It has been indeed reported that Nkx6.1/Nkx6.2 and Ptf1a function as antagonistic lineage determinants in MPC (Schaffer, A.E. et al. PLoS Genet 9, e1003274, 2013), and that the Nkx6/Ptf1a switch only operates during a critical competence window when progenitors are still multipotent and can be uncoupled from cell differentiation. It would be important to define whether culturing PDX1+/SOX9+/NKX6.1+ PP (as defined in this work) in the best conditions allowing cell expansion is reinforcing either an MPC or BP phenotype. Data from Figure S2A (last paragraph of page 7) suggests that PTF1A expression is decreased in C5 culture conditions, thus more homogeneously keeping BP cells in this media composition. However, on page 15, 2nd paragraph it is stated that "the strong upregulation of NKX6.2 in our procedure suggested that our ePP cells may have retracted to an earlier PP stage". Evaluating the co-expression of the previously selected markers with PTF1A (or CPA2), or the more homogeneous expression of novel BP markers described, such as DCDC2A (Scavuzzo et al. Nat Commun 9, 3356, 2018), in the different culture conditions assayed would more shield light into this relevant aspect.

This is certainly an interesting point. The RNA Seq data suggest that ePP cells resemble BP cells rather than MPCs and that this occurs during expansion. We have now added a new paragraph in the results section to illustrate this and added graphs of CPA2, PTF1A and DCDC2A expression during expansion in Figure 5, S5 as well as data in Table S5. In summary, we favor the interpretation that expanded cells are close but not identical to the BP identity and refer to that in the discussion. We have also amended the statement on page 15 stating the strong upregulation of NKX6.2 in our procedure suggested that our ePP cells may have retracted to an earlier PP stage.

In line with the previous comment, it would be extremely insightful if the authors could characterize or at least discuss a potential role for YAP underlying the mechanistic effects observed after culturing PP in different media compositions. It is well known that the nuclear localization of the co-activator YAP broadly promotes cell proliferation, and it is a key regulator of organ growth during development. Importantly in this context, it has been reported that TEAD and YAP regulate the enhancer network of human embryonic pancreatic progenitors and disruption of this interaction arrests the growth of the embryonic pancreas (Cebola, I. et al. Nat Cell Biol 17, 615-26, 2015). More recently, it has also been shown that a cell-extrinsic and intrinsic mechanotransduction pathway mediated by YAP acts as gatekeeper in the fate decisions of BP in the developing pancreas, whereby nuclear YAP in BPs allows proliferation in an uncommitted fate, while YAP silencing induces EP commitment (Mamidi, A. et al. Nature 564, 114-118, 2018; Rosado-Olivieri et al. Nature Communications 10, 1464, 2019). This mechanism was further exploited recently to improve the in vitro pancreatic beta cell differentiation protocol (Hogrebe et al., Nature Protocols 16, 4109-4143, 2021; Hogrebe et al, Nature Biotechnology 38, 460-470, 2020). Thus, YAP in the context of the findings described in this work could be a key player underlying the proliferation vs differentiation decisions in PP.

We do refer to these publications now and refer to the YAP pathway in the introduction and results sections as well as in the discussion. We have not investigated more because the kinetics of the different components of the pathway are complex and do not give an indication of whether the pathway becomes more or less active – please see below.

Author response image 2.

Regarding the improvements made in the PP cell culture medium composition to allow expansion while avoiding differentiation, some of the claims should be better discussed and contextualized with current stateof-the-art differentiation protocols. As an example, the use of ALK5 II inhibitor (ALK5i II) has been reported to induce EP commitment from PP, while RA was used to induce PP commitment from the primitive gut tube cell stage in recently reported in vitro differentiation protocols (Hogrebe et al., Nature Protocols 16, 41094143, 2021; Rosado-Olivieri et al. Nature Communications 10, 1464, 2019). In this context, and to the authors' knowledge, is Vitamin A (triggering autocrine RA signaling) usually included in the basal media formulations used in other recently reported state-of-the-art protocols? If so, at which stages? Would it be advisable to remove it?

These points and our views are now included in the discussion

In this line also, the supplementation of cell culture media with the canonical Wnt inhibitor IWR-1 is used in this work to allow the expansion of PP while avoiding differentiation. A role for Wnt pathway inhibition during endocrine differentiation using IWR1 has been previously reported (Sharon et al. Cell Reports 27, 22812291.e5, 2019). In that work, Wnt inhibition in vitro causes an increase in the proportion of differentiated endocrine cells. It would be advisable to discuss these previous findings with the results presented in the current work. Could Wnt inhibition have different effects depending on the differential modulation of the other signaling pathways?

These points are now included in the discussion together with the points above

Reviewer #3 (Recommendations For The Authors)

Recommendations for improving the writing and presentation and minor comments on the text and figures:

• In the Introduction (page 3, line 1) it is stated: "Diabetes is a global epidemic affecting > 9% of the global population and its two main forms result from .....". The authors could rephrase/remove "global" repeated twice.

Corrected

• On page 4 of the introduction, in the context of "Unlimited expansion of PP cells in vitro will require disentangling differentiation signals from proliferation/maintenance signals. Several pathways have been implicated in these processes..." the authors are advised to consider mentioning the YAP mediated mechanisms as another key aspect underlying MPC phenotype (Cebola, I. et al. Nat Cell Biol 17, 615-26, 2015) and the BP to endocrine progenitor (EP) commitment (Mamidi, A. et al. Nature 564, 114-118, 2018; Rosado-Olivieri et al. Nature Communications 10, 1464, 2019). This should be better discussed in the context of the Weaknesses mentioned in the Public Review. It would be worth considering adding effectors and other molecules involved in YAP and Hippo pathway signaling to Table S3.

We have added the role of the Hippo/YAP pathway in the introduction and mentioned in the results the finding that components of the pathway are generally not regulated except two that are now added in Table S3

• In page 4, paragraph 3, near "and SB431542, another general (ALK4/5/7) TGFβ inhibitor", consider removing "another". SB431542 is the same inhibitor mentioned in the other protocols at the beginning of the paragraph.

The paragraph is rewritten because it was not clear – we used A83-01 and not SB431542. Other approaches had used SB431542.

• Page 5, Table S2 is cited after Table S3, please consider reordering.

In fact, both S2 and S3 are relevant there, therefore we quote both now.

• Page 8, 2nd paragraph, near "Expression of both AFP and CDX2 increased transiently upon expansion, at p5 (Figure S2H-J)." How do you explain results in FigS2C, D and FigS2E (AFP/CDX2)? RT-qPCR data does not suggest transient downregulation.

AFP and CDX2 were – wrongly – italicized in the quoted passage. Therefore, in one case we refer to the protein and in the other to the transcript levels. We corrected and added the qualifier ‘appeared’. The difference is most likely due to translational regulation but we did not elaborate since we do not know. In any case, we have used the, less favorable but more robust, gene expression levels as the main criterion.

• Page 9, end of 2nd paragraph, Figure 5A is cited but it looks like this should be Figure 4A.

Corrected

• Page 9, 3rd paragraph, when stating "C5 ePP cells of the same passage no..." please replace "no" with a number or a suitable abbreviation.

Corrected

• Page 9, 3rd paragraph. Expressing the values in the Y axis in a consistent manner for FigS2B-D and FigS4A would make a comparison easier.

We strive to keep sections autonomous so that the reader would not have to flip between figures and sections – this is why we think that figure S4A is preferable as it is; it is a direct comparison of C6 to C5 for the different markers and has the additional advantage that one needs not to include p0 levels.

• Page 9, 3rd paragraph. Green dots in FigS4A stand for p5 cells? if so, shouldn't these average 1 for all assayed genes?

No, because the baseline (average 1) is the C5 expression at the corresponding passage no. We changed the y-axis label, hopefully it is clearer now.

• Page 10 3rd paragraph, please include color labels in Fig. 5G.

The different colors here correspond to the different expansion procedures that are compared. The samples are labelled on the x axis.

• Page 10 3rd paragraph, Figure 6G is cited but it looks like this should be Figure 5G.

Corrected

• Page 11, 1st paragraph, at "TF genes such as FOXA2 and RBJ remained comparable", please double check if "RBJ" should be "RBPJ".

Corrected

• Page 11, end of 1st paragraph, when stating "Of note, expression of PTF1A was also undetectable in all ePP cells (Table S5)", is PTF1A expression level close to 1000 (which units?) in Table S5 considered undetectable?

This statement regarding ‘undetectable PTF1A expression’ refers to expanded PP cells (ePP), not PP cells at p0. For the latter, expression is indeed close to 1000 in normalized RNA-sequence counts as mentioned in the Table legend.

-Page 11, 4th paragraph, "In summary, the comparative transcriptome analyses suggested that our C6 expansion procedure is more efficient at strengthening the PP identity". In the context of comments made in the Public Review, more accuracy needs to be put when defining PP identity. Are these MPC or BP?

The RNA Seq data suggest that expansion promotes a MPC  BP transition. We have added a paragraph in the corresponding results section and comment in the discussion.

• Page 15, 2nd paragraph, the sentence "expression of PTF1A, recently shown to promote endocrine differentiation of hPS cells (Miguel-Escalada et al., 2022)" is confusing. Please double-check sentence syntax and reference. Does PTF1A expression "promote" or "create epigenetic competence" for endocrine differentiation?

Its role is in the MPCs and it prepares the epigenetic landscape to allow for duct and endocrine specification later, thus it ‘creates epigenetic competence’. The paper was cited out of context and we have now corrected it.

Additional recommendations by the Reviewing Editor:

An insufficient number of experimental repetitions have been used for the following data: (Figure 1A, n = 2; Figures 2B-D, p10, n = 2; Figures 6A and B, VTN-N, n = 1).

This is true but we do not draw quantitative conclusions from or do comparisons with these data.

Author response:

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

Public Reviews:

Reviewer #2 (Public Review):

I have read the authors' response to my comments as well as to the other reviewers. Summarizing briefly, I don't think they provide substantial answer to the questions/comments by me or reviewer 3, and generally do not quantify the results/effects data. I still remain unconvinced about the analyses and conclusions. Rather than rewriting another set of comments, I think it will be more useful for all (authors and readers) simply to be able to see the entire set of reviews and responses together with the paper.

The authors disagree with the views of referees. The authors have provided point-wise precise responses to each of the previous comments. The authors find that the referee has not been able to engage with the responses and accompanying analysis that were provided while communicating the previous response.

The following extensive analyses were performed by the authors while submitting our revision of round 2 of peer-review to address the comments of reviewer 2 and reviewer 3   that were raised by them on the previous versions:

(1) We calculated the distribution of multiple metrics for both the apo and holo simulations, including their secondary structure composition, and demonstrated the robustness of our findings.

(2) We analyzed smaller 60 µs chunks from two parts of the 1.5 ms trajectory and showed how, in combination with the Markov state modeling (MSM) approach, these chunks effectively capture equilibrium properties.

(3) We thoroughly investigated the choice of starting structures, examining parameters such as Rg, RMSD, secondary structure, and SASA, in response to Referee 3's concerns about the objectivity of our dimension reduction approach.

(4) We conducted multiple analyses using VAMP-scores and justified the use of a Variational Autoencoder (VAE) over tICA.

(5) We had extensively verified the choice of hyperparameters used in constructing the MSM.

(6) To aleviate referee concerns, we had retrained a VAE with four latent dimensions and used it to build an MSM, ensuring the robustness of our approach.

However, we find that Referee has not considered these additional analysis in response to his/her comments on the manuscript.

Since referee 2 also draws comments from Referee 3, it is worth noting that some of the comments from Referee 2 and Referee 3 in Round 1 were mutually contradictory. In particular, Referee 3's suggestion in Round 1 to use the same initial configuration for simulations of intrinsically disordered proteins (IDPs) in both apo and ligand-bound forms contradicts the fundamental principle that IDPs should not possess structural bias. This recommendation also directly conflicts with Referee 2's request for greater diversity in starting structures. Our manuscript provided robust evidence that our initial configurations are indeed diverse, with one configuration coincidentally matching that used in the ligand-bound simulations. Despite this, we addressed both sets of concerns in our Round 2 revisions. Unfortunately, it seems that these efforts were overlooked in the subsequent round of review.

Referee 2's suggestion in prevous round of review comments to mix both holo and apo simulation trajectories for MSM construction is conceptually wrong and indicates a lack of understanding of transition matrix building in this field. Nevertheless, we addressed these comments by performing additional analyses and demonstrating the robustness of our current MSM.

Reviewer #3 (Public Review):

Summary:

While the authors have provided additional information in the updated manuscript, none of the additional analyses address the fundamental flaws of the manuscript.

The additional analyses do not convincingly demonstrate that these two extremely different simulation datasets (1500 microsecond unbiased MD for a-synuclein + fasudil, 23 separate 1-4 microsecond simulations of apo a-synuclein) are directly comparable for the purposes of building MSMs.

The 23 unbiased 1-4 microsecond simulations of apo αS totals to ~ 60 us.

Author response image 1.

Left figure : Distribution of the radius of gyration (Rg) of the 23 apo simulation (as shown in the colourbar) and holo simulation (black). Right figure : Mean and standard deviation (as error bar) of the Rg of the 23 apo (colourbar) and holo simulations (black).

We have plotted the distribution of the Radius of gyration ((Rg) for the 23 apo simulation (colour bar) and the holo simulation (black) as shown in the left figure and also compared the mean and standard deviations of the Rg values (right figure). We find that our apo simulations span the entire space of Rg as is spanned by the holo simulation. We have also measured the mean and standard deviations (SD) (horizontal error bar) of the apo and holo simulations. The fact that the apo simulations have mean and SDs comparable to those of the holo ensemble suggests that the majority of the apo simulations are sampling similar conformational space as those observed in the ligand-bound holo form and hence can be used for building the MSM.

The additional analyses do not demonstrate that there are sufficient conformational transitions among kinetically metastable states observed in 23 separate 1-4 microsecond simulations of apo a-synuclein to build a valid MSM, or that the latent space of the VAE is kinetically meaningful.      

We have performed the Chapman-Kolmogorov test to compare observed and predicted transition probabilities over increasing lag times and found good agreement between these probabilities, thereby suggesting that transitions between states are well-sampled for both the apo (Author response image 2) and holo simulation (Figure S9).

Author response image 2.

The Chapman-Kolmogorov test performed for the three state Markov State Model of the αS ensemble.

As for the latent space of VAE, we have compared the VAMP2 score and compared with tICA. VAE has a higher VAMP2 score as compared to tICA thereby indicating its efficacy in capturing slower mode for both apo and holo simulation (Fig. S7 and S8).

If one is interested in modeling the kinetics and thermodynamics of transitions between a set of conformational states, and they run a small number of MD simulations that are too short to see conformational transitions between conformational states - any kinetics and thermodynamics modeled by an MSM will be inherently meaningless. This is likely to be the case with the apo asynuclein dataset analyzed in this investigation.

We disagree with the referee’s view. The referee does not seem to understand the point of building Markov state models via short-time scale trajectories. The distribution of Rg of all the 23 apo simulations spans the entire Rg space sampled by the holo simulation, thereby suggesting that multiple short simulations can sample structures of varying sizes as sampled from the 1.5 ms holo simulation (see Author response image 1).

Simulations of 1-4 microseconds are almost certainly far too short to see a meaningful sampling of conformational transitions of a highly entangled 140-residue IDP beyond a very local relaxation of the starting structures, and the authors provide no analyses to suggest otherwise.

Author response image 3.

Autocorrelation of the first principal component of the backbone dihedral for the apo (colourbar) and holo (black) simulation.

Author response image 4.

Autocorrelation of the second principal component of the backbone dihedral for the apo (colourbar) and holo (black) simulation.

In order to assess the 23 short simulations in capturing meaningful kinetics and thermodynamics, we have computed the backbone dihedrals which were then reduced to two principal components for both the 23 apo and holo simulations. We then calculated the autocorrelation time for each of the components and for each of the apo and holo simulations which are plotted in Author response image 3 and Author response image 4 respectively.

The autocorrelation for the holo and most of the apo simulation is similar, thereby suggesting that there is sufficient sampling of conformational transitions between conformational states in the apo simulations and are therefore able to represent the structural changes of the system similarly to the long simulation.

Without convincingly demonstrating reasonable statistics of conformational changes from the very small apo simulation dataset analyzed here, it seems highly likely the apparent validity of the apo MSM results from learning a VAE latent space that groups structurally and kinetically distinct conformations into similar states, creating the spurious appearance of transitions between states. As such, the kinetics and thermodynamics of the resulting MSM are likely to be relatively meaningless, and comparisons with an MSM for a-synuclein in the presence of fasudil are likely to be meaningless.

We have shown above that the short simulations are able to capture the structural changes in the long simulation. In addition we have compared the VAMP2 score of the apo and holo simulation with tICA and found out that VAE is superior in capturing long timescale dynamics, for both apo and holo simulation (Fig. S7 and S8).

In its present form, this study provides an example of how the use of black-box machine learning methods to analyze molecular simulations can lead to obtaining misleading results (such as the appearance of a valid MSM) - when more basic analyses are omitted.

The authors disagree with the referee’s viewpoint on our manuscript. We find that the majority of the contents of the referee’s comments are cursory and lack objectivity.

The referee’s loose reference on Machine learning as a black box lacks basic knowledge to comprehend artificial deep neutral network’s long-proven ability to objectively deduce optimal set of lower-dimensional representation of conformational subspace of complex biomacromolecule. The referee’s views on the manuscript ignore the extensive optimization of hyper-parameters that were carried out by the authors in developing the suitable framework of beta-variational autoencoder for deducing optimal latent space representation of complex and fuzzy conformational  landscape of an IDP such as alpha-synuclein. We had thoroughly investigated the choice of starting structures, examining parameters such as Rg, RMSD, secondary structure, and SASA, in response to Referee 3's concerns about the objectivity of our dimension reduction approach. However, we find that referee 3 has ignored the analysis provided to justify our choice.

Referee 3's advocacy for linear dimensional reduction techniques overlooks the necessity and generality of non-linear approaches, as enabled by artificial deep neural network frameworks, demonstrated in the present manuscript. Nevertheless, our manuscript includes evidence demonstrating the optimality of our current reduced dimensions through varied dimensional analyses. Our extensive analysis, based on the VAMP-2 score, supports the sufficiency of the present dimensions compared to other linear reduction methods.

The referee’s views that developing Markov state models (MSM) of apo form of the alphasynulclein using multiple number of 1-4 microsecond long simulation length is misleading, suggests referee’s lack of knowledge on the fundamental purpose and motivation for the usage of MSM, which is, to derive long-time scale equilibrium properties from significantly short-length adaptively sampled trajectories. The referee has overlooked the extensive analysis that the authors had provided while demonstrating that the Markov state models developed from short length simulation trajectories of alpha-synclein can statistically replicate the properties derived from very long trajectories.

---

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

The following extensive analyses were performed to address the reviewer comments:

(1) We have calculated the distribution of radius of gyration (Rg), end-to-end distance (Ree), solvent accessible surface area (SASA)  of the apo and holo simulations and also their secondary structure composition.

(2) We have performed a similar analysis for the smaller 60 µs chunk from two parts of the 1.5 ms trajectory.

(3) The choice of starting structures have been thoroughly investigated in terms of Rg, RMSD, secondary structure and SASA.

(4) We have justified the use of VAE over tICA.

(5) We have verified the choice of hyperparameters that were used to build the MSM.

(6) We have retrained a VAE with four latent dimensions and used it to build MSM. 

(7) As per recommendation of the referee 1, we have updated the title of the manuscript by introducing ‘expansion’ phrase.

The manuscript has been accordingly revised by updating it with additional analysis.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This is a well-conducted study about the mechanism of binding of a small molecule (fasudil) to a disordered protein (alpha-synuclein). Since this type of interaction has puzzled researchers for the last two decades, the results presented are welcome as they offer relevant insight into the physical principles underlying this interaction.

Strengths:

The results show convincingly that the mechanism of entropic expansion can explain the previously reported binding of fasudil to alpha-synuclein. In this context, the analysis of the changes in the entropy of the protein and of water is highly relevant. The combination use of machine learning for dimensional reduction and of Markov State Models could become a general procedure for the analysis of other systems where a compound binds a disordered protein.

Weaknesses:

It would be important to underscore the computational nature of the results, since the experimental evidence that fasudil binds alpha-synuclein is not entirely clear, at least to my knowledge.

The experimental evidence of binding of fasudil to α-synuclein and potentially preventing its aggregation is reported in the paper “Fasudil attenuates aggregation of α-synuclein in models of Parkinson’s disease. Tatenhorst et al. Acta Neuropathologica Communications (2016) 4:39 DOI 10.1186/s40478-016-0310-y ”. In this work, solution state 15N-1H HSQC NMR experiments were performed of α-synuclein in increasing amounts of fasudil which led to large chemical shift perturbation of Y133 and Y136 residues. Additionally single and double mutant  synT-Y133A and synT-Y136A (tyrosine is replaced with alanine), when treated with fasudil, had no significant effect as evident from immunochemistry, thereby indicating that α-synuclein aggregation can be inhibited by the interaction of C-terminal tyrosines with  fasudil. These two analyses point to binding specific binding sites of fasudil to α-synuclein.

In our work, we have built a MSM using the latent dimension of a deep learning method called VAE,  to address how fasudil interacts with α-synuclein. An analysis of the macrostates as obtained from MSM, gives insights into how fasudil interacts with α-synuclein, in terms of  transition probabilities among the states, thereby predicting which states are most favorable for binding.

Reviewer #2 (Public Review):

The manuscript by Menon et al describes a set of simulations of alpha-Synuclein (aSYN) and analyses of these and previous simulations in the presence of a small molecule.

While I agree with the authors that the questions addressed are interesting, I am not sure how much we learn from the present simulations and analyses. In parts, the manuscript reads more like an attempt to apply a whole range of tools rather than with a goal of answering any specific questions.

In this manuscript, we have employed a variational bayesian method, VAE, that uses variational inference to approximate the distribution of latent variable. Unlike conventional linear dimension reduction methods such as tICA (as provided in the SI), this method has been found to be better (higher VAMP2 score) in capturing slow modes and thereby facilitate the study of long-time dynamics. Markov State Model was built on this lower dimension space which indicated the presence of three and six states for the apo and holo simulations respectively. The exclusivity of the states was justified by determining the backbone contact map and further mapping these states using a denoising CNN-VAE. The increase in the number of states in the presence of the small molecule was justified by calculating the entropy of the macrostates. The entropic contribution from water remained similar across all states, while for the protein in the holo ensemble, entropy was significantly modulated (either increased or decreased) compared to the apo state. In contrast, the entropy of the apo states showed much less modulation. This proves that an increase in the number of states is primarily an entropic effect caused by the small molecule. Finally we have compared the mean first passage time (MFPT) of other states to the most populated state, which reveals a strong correlation between transition time and the system's entropy for both apo and holo ensemble. However, the transition times (to the most populated state) are much lower for the holo ensemble, thereby suggesting that fasudil may potentially trap the protein conformations in the intermediate states, thereby slowing down αS in exploring the large conformational space and eventually slow down aggregation.

There's a lot going on in this paper, and I am not sure it is useful for the authors, readers or me to spell out all of my comments in detail. But here are at least some points that I found confusing/etc

Major concerns

p. 5 and elsewhere:

I lack a serious discussion of convergence and the statistics of the differences between the two sets of simulations. On p. 5 it is described how the authors ran multiple simulations of the ligandfree system for a total of 62 µs; that is about 25 times less than for the ligand system. I acknowledge that running 1.5 ms is unfeasible, but at a bare minimum the authors should discuss and analyse the consequences for the relatively small amount of sampling. Here it is important to say that while 62 µs may sound like a lot it is probably not enough to sample the relevant properties of a 140-residue long disordered protein.

As to referee 2’s original comment on ‘a lot going on in the manuscript’, we believe that the complexity of the project demanded that this work needs to be dealt with an extensive analysis and objective machine learning approaches, instead of routine collective variable or traditional linear dimensional reduction techniques. This is what has been accomplished in this manuscript. For someone to get the gist of the work, the last paragraph of the introduction and first paragraph of conclusion provides a summary of the overall finding and investigation in the manuscript. First, a VAE-based machine learning approach demonstrates the modulation of free energy landscape of alpha-synuclein in presence of fasudil. Next, Markov State Model elucidates distinct binding competing states of alpha-synuclein in presence of the small-molecule drug. Then the MSMderived metastable states of alpha-synuclein monomer are structurally characterized in presence of fasudil. Next we mapped the macrostates in apo and bound-state ensembles using denoising convolutional variational autoencoder, to ensure that these are mutually distinct. Next we show that fasudil exhibits conformation-dependent interactions with individual metastable states. Finally the investigation quantatively brings out entropic signatures of small molecule binding.

We thank the reviewer for the question. For the apo simulations, we performed 1-4 μs long simulations with 23 different starting structures and the ensemble amounted to an ensemble of ~62 μs. In the Supplementary figures,  we show analyses of how the starting structures used for apo simulations compare with the structure used to run the holo simulations as well as comparison of the apo and holo ensembles in terms of structures features as Rg, Ree, solvent accessible surface area (SASA) and secondary structure properties. This is updated in the manuscript on page 3,31- 33 and figures S1-S6, S25-S30.

Also, regarding the choice of starting structures, we chose multiple distinct conformations from a previous simulation of alpha synuclein monomer, reported in Robustelli et. al, PNAS, 115 (21), E4758-E4766. The Rg of the starting structures represent the entire distribution of Rg of the holo ensemble; from compact, intermediate to extended states. Importantly, the Rg distribution of the apo and holo ensembles are highly comparable and overlapping, indicating that the apo simulations, although of short timescale, have sampled the phase space locally around each starting conformation and thus covered the protein phase space as in the holo simulation. Similarly, other structural properties such as SASA, Ree  and secondary structure are comparable for the two ensembles. These analyses show that the local sampling across a variety of starting conformations has ensured sufficient sampling of the IDP phase space. This is  updated in the manuscript on page 33-34 and figure S1, S25-S30.

p. 7:

The authors make it sound like a bad thing than some methods are deterministic. Why is that the case? What kind of uncertainty in the data do they mean? One can certainly have deterministic methods and still deal with uncertainty. Again, this seems like a somewhat ad hoc argument for the choice of the method used.

We appreciate the reviewer’s comment. In this work, we have used a single VAE model to map the simulation of αS in its apo state and in the presence of fasudil, into two dimensions. If we had used an autoencoder, which is a deterministic model, we would have to train two independent models; one for the apo-state and one for fasudil. It would then be questionable to compare the two dimensions obtained from two different autoencoders as the model parameters are not shared. 

VAE gives us this flexibility by not mapping it to a single point, but to a distribution, thereby encouraging it to learn more generalizable representation. The uncertainty is not in the data; but mapping a conformation (of the fasudil simulation) to a distribution would provide a new point for a similar structure (from the apo simulation). 

p. 8:

The authors should make it clear (i) what the reconstruction loss and KL is calculated over and (ii) what the RMSD is calculated over.

(i) The reconstruction loss is calculated between the reconstructed and original pairwise distances, whereas the KL loss is calculated between the approximated posterior distribution and the prior distribution (for VAE it is a standard normal distribution)

(ii) The RMSE is the root mean square error between the original data and the reconstructed data. 

(i) is updated on page 34 and (ii) is updated in the revised manuscript on page 8.

p. 9/figure 1:

The authors select a beta value that may be the minimum, but then is just below a big jump in the cross-validation error. Why does the error jump so much and isn't it slightly dangerous to pick a value close to such a large jump.

In this work, RMSE has been chosen as a metric to select the best VAE model. To do so, the β parameter (weighting factor for the KL loss) was varied. The β value was chosen as this had the minimum value.

This is updated on page 8.

p. 10:

Why was a 2-dimensional representation used in the VAE? What evidence do the authors have that the representation is meaningful? The authors state "The free energy landscape represents a large number of spatially close local minima representative of energetically competitive conformations inherent in αS" but they do not say what they mean by "spatially close". In the original space? If so, where is the evidence.

We thank the reviewer for the question. Even though an increase in the number of latent dimensions may make the model more accurate, this can also result in overfitting. The model can simply memorize the pattern in the data instead of generalizing them. A higher dimensional latent space is also more difficult to interpret; therefore, we chose two dimensions. 

The reconstruction loss (which is the mean squared error between the input and the reconstructed data) is of the order of 10-4. Also, the MSM built on the latent space of VAE is able to identify states that are distinct for both apo and holo simulations, which ensures that the latent space representation is meaningful.

We have also trained a model with 4 neurons in the latent space and built an MSM. The implied timescales indicate the presence of six states which is consistent with the model with two latent dimensions.

This is updated in the manuscript on page 13 and figure S14-S15.

No, not spatially close in the original space, but in the reduced two dimensional latent space.

p. 10:

It is not clear from the text whether the VAEs are the same for both aSYN and aSYN-Fasudil. I assume they are. Given that the Fasudil dataset is 25x larger, presumably the VAE is mostly driven by that system. Is the VAE an equally good representation of both systems?

Yes, the same model is used for both aSYN and aSYN-Fasudil ensemble.

The states obtained from the MSM of the aSyn ensemble are distinct when their Cα contact maps are analyzed. So we think it is a good representation for this system.

p. 10/11:

Do the authors have any evidence that the latent space representation preserves relevant kinetic properties? This is a key point because the entire analysis is built on this. The choice of using z1 and z2 to build the MSM seems somewhat ad hoc. What does the auto-correlation functions of Z1 and Z2 look like? Are the related to dynamics of some key structural properties like Rg or transient helical structure.

Autocorrelation of z1 and z2 of the latent space of VAE and the radius of gyration for asyn-fasudil simulation.

Author response image 5.

We find that z1 of VAE has a much slower decay as compared to Rg. This indicates that it is much better in capturing long-time-scale dynamics as compared to Rg.

p. 11:

What's the argument for not building an MSM with states shared for aSYN +- Fasudil?

We have built two different markov state models for two aSYN simulation in its apo state and in the presence of ligand. Mixing the two latent spaces to build one MSM would give incorrect transition timescales among the states as these are independent simulations.

p. 12:

Fig. 3b/c show quite clearly that the implied timescales are not converged at the chosen lag time (incidentally, it would have been useful with showing the timescales in physical time). The CK test is stated to be validated with "reasonable accuracy", though it is unclear what that means.

We have mentioned the physical timescales in the main manuscript (Page no. 38), which is 36 and 32 ns for apo and holo simulations, respectively. We used “reasonable accuracy” in the context of the Chapman-Kolmogorov test. We note that for the ligand simulations, the estimated and predicted models are in excellent agreement as compared to some of the transitions in the apo state. This good agreement implies that the model has reached Markovianity and the timescales have converged. 

The CK test is updated in the manuscript on page 12.

p. 12:

In Fig. 3d, what are the authors bootstrapping over? What are the errors if the authors analyse sampling noise (e.g. bootstrap over simulation blocks)?

For bootstrapping, we randomly deleted a part of the simulation (simulation block) and rebuilt the MSM with this reduced dataset. We repeated this 10 times and reported the average value of the population and the transition timescales over the 10 iterations.  

p. 13:

I appreciate that the authors build an MSM using only a subset of the fasudil simulations. Here, it would be important that this analysis includes the entire workflow so that the VAE is also rebuilt from scratch. Is that the case?

The VAE model was trained over data points of the ligand simulation sampled at every 9 ns starting from time t=0, for the entire 1.5 ms. We did not train it for the subset of the fasudil simulation, but rather used the trained VAE model to get the latent space of the 60 μs of the fasudil simulation to build the MSM. Additionally, we have compared the distributions of Rg for this simulation block with the apo ensemble and found good agreement among them. 

Rg distribution is updated in the manuscript on page 13 and see figure S10-S11.

p. 18:

I don't understand the goal of building the CVAE and DCVAE. Am I correct that the authors are building a complex ML model using only 3/6 input images? What is the goal of this analysis. As it stands, it reads a bit like simply wanting to apply some ML method to the data. Incidentally, the table in Fig. 6C is somewhat intransparent.

We appreciate the reviewer’s valid question. The ensemble averaged contact map of the macrostates of aSyn in apo state and in the presence of ligand posed us a challenge in finding contacts that are exclusive to each state. Since VAEs are excellent in finding patterns, we employed a convolutional VAE (typically used for images). However, owing to the few number of contact maps, the model overfitted and to prevent this, we added noise to the data.  A visual inspection of the ensemble averaged contact map, especially for IDPs is difficult and this lower dimensional space will give us a preliminary idea of how each macrostate is different from every other. The table in Fig. 6C provides scores for the denoised contact maps (SSIM and PSNR scores). An SSIM score above 0.9 and PSNR score between 20-48 indicates that the reconstruction of the contact map is of good quality.

p. 22:

"Our results indicate that the interaction of fasudil with αS residues governs the structural features of the protein."

What results indicate this?

By building a Markov State Model and comparing them across the apo and holo ensembles, we showed the interaction of fasudil with aSyn leads to the population of more states (than apo). In these states, we observe that fasudil interacts with aSyn in different regions as shown by the protein-ligand contact map as shown in figure 7. Also, the contact maps and the extent of secondary structure of the six states are distinct across the states. The location and extent of the helix and sheet-like character in the ensemble of the six macrostates as shown in figure S16-S17.  Based on these observations, we state that the interaction of the small molecule favors the population of new aSyn states that are distinct in their structural features.

p. 23:

The authors should add some (realistic) errors to the entropy values quoted. Fig. 8 have some error bars, though they seem unrealistically small. Also, is the water value quoted from the same force field and conditions as for the simulations?

The error values are the standard deviations that are provided by the PDB2ENTROPY package. Yes, the water value is from the same force field and conditions for the simulations are the same as reported in the section “Entropy of water”  

p. 23:

Has PDB2ENTROPY been validated for use with disordered proteins?

Yes, it has been used in the following paper studying liquid-liquid phase separation of an IDP. 

This paper has also been cited in the manuscript (reference 66).

“Thermodynamic forces from protein and water govern condensate formation of an intrinsically disordered protein domain” by Saumyak Mukherjee & Lars V. Schäfer, Nature Communications volume  14, Article number: 5892 (2023) https://doi.org/10.1038/s41467-023-41586-y

p. 23/24:

It would be useful to compare (i) the free energies of the states (from their populations), (ii) the entropies (as calculated) and (iii) the enthalpies (as calculated e.g. as the average force field energy). Do they match up?

Our analysis stems from previous studies where enthalpy driven drug design has not led to significant advances in drug design, particularly for IDPs. In the presence of the drug/ligand, the protein may be able to explore a larger conformational space and hence an increase in the number of states accessible by the protein, which we found by building Markov State Model using the latent space of VAE. The entropy of the protein is calculated based on the torsional degrees of freedom relative to the random distribution (the protein with the most random configuration).

p. 31:

It is unclear which previous simulation the new aSYN simulations were launched from. What is the size of the box used?

The starting conformations for the new aSYN simulations were randomly chosen from a previously reported 73 μs simulation in Robustelli et. al. (PNAS, 115 (21), E4758-E4766). 

Box size for the 23 simulation has been added to the supplemental information in Table S1.

Reviewer #3 (Public Review):

Summary:

In this manuscript Menon, Adhikari, and Mondal analyze explicit solvent molecular dynamics (MD) computer simulations of the intrinsically disordered protein (IDP) alpha-synuclein in the presence and absence of a small molecule ligand, Fasudil, previously demonstrated to bind alpha-synuclein by NMR spectroscopy without inducing folding into more ordered structures. In order to provide insight into the binding mechanism of Fasudil the authors analyze an unbiased 1500us MD simulation of alpha-synuclein in the presence of Fasudil previously reported by Robustelli et.al. (Journal of the American Chemical Society, 144(6), pp.2501-2510). The authors compare this simulation to a very different set of apo simulations: 23 separate1-4us simulations of alphasynuclein seeded from different apo conformations taken from another previously reported by Robustelli et. al. (PNAS, 115 (21), E4758-E4766), for a total of ~62us.

To analyze the conformational space of alpha-synuclein - the authors employ a variational autoencoder (VAE) to reduce the dimensionality of Ca-Ca pairwise distances to 2 dimensions, and use the latent space projection of the VAE to build Markov state Models. The authors utilize kmeans clustering to cluster the sampled states of alpha-synuclein in each condition into 180 microstates on the VAE latent space. They then coarse grain these 180 microstates into a 3macrostate model for apo alpha-synuclein and a 6-macrostate model for alpha-synuclein in the presence of fasudil using the PCCA+ course graining method. Few details are provided to explain the hyperparameters used for PCCA+ coarse graining and the rationale for selecting the final number of macrostates.

The authors analyze the properties of each of the alpha-synuclein macrostates from their final MSMs - examining intramolecular contacts, secondary structure propensities, and in the case of alpha-synuclein:Fasudil holo simulations - the contact probabilities between Fasudil and alphasynuclein residues.

The authors utilize an additional variational autoencoder (a denoising convolutional VAE) to compare denoised contact maps of each macrostate, and project onto an additional latent space. The authors conclude that their apo and holo simulations are sampling distinct regions of the conformational space of alpha-synuclein projected on the denoising convolutional VAE latent space.

Finally, the authors calculate water entropy and protein conformational entropy for each microstate. To facilitate water entropy calculations - the author's take a single structure from each macrostate - and ran a 20ps simulation at a finer timestep (4 femtoseconds) using a previously published method (DoSPT), which computes thermodynamic properties of water from MD simulations using autocorrelation functions of water velocities. The authors report that water entropy calculated from these individual 20ps simulations is very similar.

For each macrostate the authors compute protein conformational entropy using a previously published Maximum Information Spanning tree approach based on torsion angle distributions - and observe that the estimated protein conformational entropy is substantially more negative for the macrostates of the holo ensemble.

The authors calculate mean first passage times from their Markov state models and report a strong correlation between the protein conformational entropy of each state and the mean first passage time from each state to the highest populated state.

As the authors observe the conformational entropy estimated from macrostates of the holo alphasynuclein:Fasudil is greater than those estimated from macrostates of the apo holo alphasynuclein macrostates - they suggest that the driving force of Fasudil binding is an increase in the conformational entropy of alpha-synuclein. No consideration/quantification of the enthalpy of alpha-synuclein Fasudil binding is presented.

Strengths:

The author's utilize MD simulations run with an appropriate force field for IDPs (a99SB-disp and a99SB-disp water (Robustelli et. al, PNAS, 115 (21), E4758-E4766) - which has previously been used to perform MD simulations of alpha-synuclein that have been validated with extensive NMR data.

The contact probability between Fasudil and each alpha-synuclein residue observed in the previously performed 1500us MD simulation of alpha-synuclein in the presence of Fasudil (Robustelli et. al., Journal of the American Chemical Society, 144(6), pp.2501-2510) was previously found to be in good agreement with experimental NMR chemical shift perturbations upon Fasudil binding - suggesting that this simulation is a reasonable choice for understanding IDP:small molecule interactions.

Weaknesses:

Major Weakness 1: Simulations of apo alpha-synuclein and holo simulations of alpha-synuclein and fasudil are not comparable.

The most robust way to determine how presence of Fasudil affects the conformational ensemble of alpha-synuclein conclusions is to run apo and holo simulations of the same length from the same starting structures using the same simulation parameters.

The 23 1-4 us independent simulations of apo alpha-synuclein and the long unbiased 1500us alpha-synuclein in the presence of fasudil are not directly comparable. The starting structures of simulations used to build a Markov state model to describe apo alpha-synuclein were taken from a previously reported 73us MD simulation of alpha-synuclein run with the a99SB-disp force field and water model) with 100mM NaCl, (Robustelli et. al, PNAS, 115 (21), E4758-E4766). As the holo simulation of alpha-synuclein and Fasudil was run in 50mM NaCl, snapshots from the original apo alpha-synuclein simulation were resolvated with 50mM NaCl - and new simulations were run.

No justification is offered for how starting structures were selected. We have no sense of the conformational variability of the starting structures selected and no sense of how these conformations compare to the alpha-synuclein conformations sampled in the holo simulation in terms of standard structural descriptors such as tertiary contacts, secondary structure, radius of gyration (Rg), solvent exposed surface area etc. (we only see a comparison of projections on an uninterpretable non-linear latent-space and average contact maps). Additionally, 1-4 us is a relatively short timescale for a simulation of a 140 residue IDP- and one is unlikely to see substantial evolution for many structural properties of interest (ie. secondary structure, radius of gyration, tertiary contacts) in simulations this short. Without any information about the conformational space sample in the 23 apo simulations (aside from a projection on an uninterpretable latent space)- we have no way to determine if we observe transitions between distinct states in these short simulations, and therefore if it is possible the construct a meaningful MSM from these simulations.

If the structures used for apo simulations are on average more compact or contain more tertiary contacts - then it is unsurprising that in short independent simulations they sample a smaller region of conformational space. Similarly, if the starting structures have similar dimensions - but we only observe extremely local sampling around starting structures in apo simulations in the short simulation times - it would also not be surprising that we sample a smaller amount of conformational space. By only presenting comparisons of conformational states on an uninformative VAE latent space - it is not possible for a reader to ask simple questions about how the conformational ensembles compare.

It is noted that the authors attempt to address questions about sampling by building an MSM of single contiguous 60us portion of the holo simulation of alpha-synuclein and Fasudil - noting that:

"the MSM built using lesser data (and same amount of data as in water) also indicated the presence of six states of alphaS in presence of fasudil, as was observed in the MSM of the full trajectory. Together, this exercise invalidates the sampling argument and suggests that the increase in the number of metastable macrostates of alphaS in fasudil solution relative to that in water is a direct outcome of the interaction of alphaS with the small molecule."

However, the authors present no data to support this assertion - and readers have no sense of how the conformational space sampled in this portion of the trajectory compares to the conformational space sampled in the independent apo simulations or the full holo simulation. As the analyzed 60us portion of the holo trajectory may have no overlap with conformational space sampled in the independent apo simulations - it is unclear if this control provides any information. There is no quantification of the conformational entropy of the 6 states obtained from this portion of the holo trajectory or the full conformational space sampled. No information is presented to determine if we observe similar states in the shorter portion of the holo trajectory. Furthermore - as the authors provide almost no justification for the criteria used to select of the final number of macrostates for any of the MSMs reported in this work- and the number of macrostates is effectively a free parameter in the PCCA+ method, arriving at an MSM with 6 macrostates does not convey any information about the conformational entropy of alpha-synuclein in the presence or absence of ligands. Indeed - the implied timescale plot for 60us holo MSM (Figure S2) - shows that at least 10 processes are resolved in the 120 microstate model - and there is no information to provided explaining/justifying how a final 6-macrostate model was determined. The authors also do not project the conformations sampled in this sub- trajectory onto the latent space of the final VAE.

One certainly expects that an MSM built with 1/20th of the simulation data should have substantial differences from an MSM built from the full trajectory - so failing additional information and hyperparameter justification - one wonders if the emergence of a 6-state model could be the direct result of hardcoded VAE and MSM construction hyperparameter choices.

Required Controls For Supporting the Conclusions of the Study: The authors should initiate apo and holo simulations from the same starting structures - using the same simulation software and parameters. This could be done by adding a Fasudil ligand to the apo structures - or by removing the Fasudil ligand from a subset of holo structures. This would enable them to make apples-toapples comparisons about the effect of Fasudil on alpha-synuclein conformational space.

Failing to add direct apples-to-apples comparisons, which would be required to truly support the studies conclusions, the authors should at least compare the conformational space sampled in the independent apo simulations and holo simulations using standard interpretable IDP order parameters (ie. Rg, end-to-end distance, secondary structure order parameters) and/or principal components from PCA or tICA obtained from the holo simulation. The authors should quantify the number of transitions observed between conformational states in their apo simulations. The authors could also perform more appropriate holo controls, without additional calculations, by taking batches of a similar number of short 1-4us segments of simulations used to compute the apo MSMs and examining how the parameters/macrostates of the holo MSMs vary with the input with random selections.

In case of IDPs, one should not bias the simulation by starting from identical structures, as IDP does not have a defined structure and the starting configuration has little significance. It is the microenvironment that matters most. As for the choice of simulation software and parameters, we have used the same force field that was used in the holo simulation at the same temperature and same salt concentration. We have performed multiple independent simulations that have varying structural signatures such as Rg, SASA and secondary structure content. In fact, the starting structure for apo simulations covered the entire span of the Rg distribution of holo simulation, including the starting structure of the holo simulation. The simulations are unbiased w.r.t the starting structure. Although the fasudil simulation was run for 1.5 ms, we should also understand that it is difficult to run a millisecond range of simulation in reasonable time from a single starting structure. It is exactly for this reason that we start with different structures so that we do not bias ourselves and sample every possible conformation. 

We have updated the manuscript on page 33-34 and figure S1, S25-S30.

Considering the computational expense for simulating 1.5 ms timescale of a 140-residue IDP, we generated an ensemble from multiple short runs amounting to ~60 µs. The premise of this investigation is a widely popular method, Markov State Models (MSMs) that can be used to estimate long timescale kinetics and stationary populations of metastable states built from ensembles of short simulations. We have also demonstrated that comparable to the apo data, when we build an MSM for asyn-fasudil (holo) using 60 µs simulation block, the implied timescales (ITS) plot shows identical number of metastable states as for the 1.5 ms data.  

An intrinsically disordered protein (IDP) is not represented by a fixed structure. Therefore, it would be most appropriate to run multiple simulations starting from different initial structures and simulate the local environment around those structures; thus generating an ensemble effectively sampling the phase space. Accordingly, for initiating the apo simulations, instead of biasing the initial structure (using the starting structure used for simulations with fasudil), we chose randomly 23 different conformations from the 73 µs long simulation of 𝛼-synuclein monomer reported in Robustelli et. al, PNAS, 115 (21), E4758-E4766.  Based on the reviewer’s comment on providing a justification for choice of the starting structures for apo simulations, we provide a compilation of figures below showing comparison of standard conformational properties of the chosen initial structures for apo simulations with the starting structure of the long holo simulation; we have also provided comparative analyses of the apo (~60 µs) and holo ensemble (1.5 ms) properties. 

Figure S1 compares the Rg of the apo and holo ensembles of ~60 μs and 1.5 ms, respectively. The distributions are majorly overlapping, indicating that the apo ensemble is comparable to the holo ensemble, in terms of the extent of compaction of the conformations. In Figure 1, we have also marked the Rg values corresponding to the starting structures used to seed the apo simulations. It is evident that the 23 starting conformations chosen represent the whole range of the Rg space that is sampled in the holo ensemble. Therefore, while the apo simulations are relatively short (1-4 μs), the local sampling of these multiple starting conformations of variable compaction (Rg) ensures that the phase space is efficiently sampled and the resulting ensemble is comparable to the holo ensemble. Furthermore, the implementation of MSM on such an ensemble can be efficiently used to identify metastable states and the long timescale transitions happening between them

Another property that is proportional to Rg is the end-to-end distance of the protein conformations. Figure S2 shows that the distribution of this property in the apo and holo ensembles are highly similar.

Figure S3 depicts another fundamental structural descriptor i.e. solvent accessible surface area (SASA) that indicates the extent of folding and the exposure of the residues. The apo ensemble only shows a minimal shift in the distribution towards higher SASA values. The distributions of the two ensembles largely overlap. 

In Figure S25, we have provided the root mean square deviation (RMSD) of the starting structures used in the apo simulations with the structure used to start the long simulation with fasudil. The RMSD values range from 1.6 to 3 nm, indicating that the starting structures used are highly variable. This is justifiable for IDPs since they are not identified by a single, fixed structure, but rather by an array of different conformations.  

Figures S26-S28 show the fraction of the secondary structure elements i.e. helix, beta and coil in the starting structures of apo and holo simulations. All the conformations are mostly disordered in nature with the greatest extent of coil content. The helix content ranges from 3-10 % while sheet content varies from 3-15 % in the initial simulation structures. 

Figures S4-s6 represent the residue-wise percentage of secondary structure elements (helix, beta and coil) in the apo and holo ensembles. It is evident that the extent of secondary structure is comparable in the two ensembles. 

The above analyses comparing distributions of several structural features clearly indicate that the apo simulations we performed from different starting structures have effectively sampled the phase space as the single long simulation of the holo system.

We have discussed the above in the manuscript: Computational Methods section, Page 33-34.

The above VAMP score analyses (Figures S7 and S8has been now presented in the manuscript: Results and Discussion (Page 8)

Building the MSM

While building the MSM, we iteratively varied the hyperparameters to build a reasonable model. In this process, we explored different values of the number of clusters, maximum number of iterations, tolerance, stride, metric, seed, chunk size and initialization methods. There is no possible way to perform an optimization on the choice of the above hyperparameters using gradient descent methods, as no convergence would be guaranteed. The parameters were tuned carefully so that we get the best possible implied timescales of the system. The quality of the MSM was further validated using the Chapman-Kolmogorov (CK) test on a state-by-state basis i.e by considering the transitions between each pair of the metastable states. In addition, we have built the contact maps to show that the states are mutually exclusive. This is also justified by the latent space of denoising convolutional variational autoencoders.

We have compared the conformational space in the independent apo and holo simulations for Rg, Ree, SASA and secondary structure. As for PCA/TICA, we have computed the VAMP-2 score for TICA and found out to be low as compared to VAE. In fact, neural networks have been shown previously as a better dimension reduction technique due to its non-linearity over linear methods such as PCA or TICA.

Author response image 6.

Distribution of (a)Rg, (b) Ree, (c) SASA and of the apo ensemble and a 60 μs slice of the holo simulation trajectory.  (d) ITS plot of the 60 μs chunk.

First, someone familiar with MSM should understand that the basic philosophy of MSM is not the requirement of long simulation trajectories, which would defeat the purpose of its usage. Rather as motivated by Noe and coworkers in seminal PNAS (vol. 106, page 9011, year 2009) paper, MSM plays an important role in inferring long-time scale equilibrium properties by using significantly short-length scale non-equilibrium trajectories. 

Considering the difference in the size of the ensembles in the apo and holo simulations, we verified how different is the MSM built using 60 μs slice of the data from the 1.5 ms holo simulation in terms of the number of metastable states identified by the model. For this, we considered 60 μs data beginning from 966 μs - 1026 μs. First, we compared the gross structural properties of these datasets. Author response image 6a-c compares the distributions of Rg, Ree and SASA. The distributions show that the apo and holo simulations are very similar with respect to these standard properties of protein conformations. 

We built the MSM for this 60 μs data of the holo ensemble from the reduced data obtained from the same VAE model. We would like to clarify that the hyperparameters of the model are not hardcoded but rather carefully fine-tuned to obtain a good model that performs good kinetic discretization of the underlying macrostates. The implied timescale plot of this new MSM shows distinct timescales corresponding to six macrostates. This led us to conclude that the six-state model is robust despite the differences in the ensemble size. The implied timescale is shown in Author response image 6d.

The above analyses in Author response image 6 are presented in Results and Discussion, Page 13. 

Major Weakness 2: There is little justification of how the hyperparameters MSMs were selected. It is unclear if the results of the study depend on arbitrary hyperparameter selections such as the final number of macrostates in each model.

It is unclear what criteria were used to determine the appropriate number of microstates and macrostates for each MSM. Most importantly - as all analyses of water entropy and conformational entropy are restricted to the final macrostates - the criteria used to select the final number of macrostates with the PCCA+ are extremely important to the results of the conclusions of the study. From examining the ITS plots in Figure 3 - it seems both MSMs show the same number of resolved processes (at least 11) - suggesting that a 10-state model could be apropraite for both systems. If one were to simply select a large number of macrostates for the 20x longer holo simulation - do these states converge to the same conformational entropy as the states seen in the short apo simulations? Is there some MSM quality metric used to determine what number of macrostates is more appropriate?

Required Controls For Supporting the Conclusions of the Study: The authors should specify the criteria used to determine the appropriate number of microstates and macrostates for their MSMs and present controls that demonstrate that the conformational entropies calculated for their final states are not simply a function of the ratio of the number macrostates chosen to represent very disparate amounts of conformational sampling.

VAMP-2 score was used to determine the number of microstates. We have calculated the VAMP2 score by varying the number of microstates, ranging from 10 to 220. We find that the VAMP-2 score has saturated at a higher number of microstates for both apo and holo simulations.

The number of macrostates were determined by the gap between the lines of the Implied timescales plot followed by a CK test (shown in figure S1). Since we plotted the first 10 slowest timescales, the implied timescales show 10 timescales and this is not an indicator of the number of macrostates. The macrostates are separated by distinct gaps in the timescales and do not merge as seen beyond 5 timescales in the plot. The timescales, when leveled off and distinct, indicate that the system has well defined metastable states and the MSM is accurate in identifying the macrostates. We find this to be three and six for the apo and holo simulations from the corresponding implied timescales.

The above is discussed in Computational Methods, Page 37-38.

Major Weakness 3: The use of variational autoencoders (VAEs) obscures insights into the underlying conformational ensembles of apo and holo alpha-synuclein rather than providing new ones

No rationale is offered for the selection of the VAE architecture or hyperparameters used to reduce the dimensionality of alpha-synuclein conformational space.

It is not clear the VAEs employed in this study are providing any new insight into the conformational ensembles and binding mechanisms of Fasudil to alpha-synuclein, or if the underlying latent space of the VAEs are more informative or kinetically meaningful than standard linear dimensionality reduction techniques like PCA and tICA. The initial VAE is used to reduce the dimensionality of alpha-synuclein conformational ensembles to 2 degrees of freedom - but it is unclear if this projection is structurally or kinetically meaningful. It is not clear why the authors choice to use a 2-dimeinsional projection instead of a higher number of dimensions to build their MSMs. Can they produce a more kinetically and structurally meaningful model using a higher dimensional VAE latent space?

Additionally - it is not clear what insights are provided by the Denoising Convolutional Variational Autoencoder. The authors appear to be noising-and-denoising the contact maps of each macrostate, and then projecting the denoised values onto a new latent space - and commenting that they are different. Does this provide additional insight that looking at the contact maps in Figures 4&5 does not? Is this more informative than examining the distribution of the Radii of gyration or the secondary structure propensities of each ensemble? It is not clear what insight this analysis adds to the manuscript.

Suggested controls to improve the study: The authors should project interpretable IDP structural descriptors (ie. secondary structure, radius of gyration, secondary structure content, # of intramolecular contacts, # of intermolecular contacts between alpha-synuclein and Fasudil ) onto this latent space to illustrate if any of these properties are meaningful separated by the VAE projection. The authors should compare these projections, and MSMs built from these projections, to projections and MSMs built from projections using standard linear dimensionality projection techniques like PCA and tICA.

We have already pointed out the IDP structural parameters for the first question.

In case of VAE, the latent space captures the underlying pattern of the higher dimensional data. A non-linear projection using VAE has shown to have a higher VAMP-2 score over linear dimension reduction methods such as tICA. The latent space of VAE was then used to build the MSM, in order to get the macrostates and also the transition timescales among them. We can project the data onto a higher dimension, but the goal is to reduce it to lower dimensions where it will be easier to interpret. Higher number dimensions would also risk overfitting; and the model, instead of learning the pattern, it may simply memorize the data. The training and validation loss curve from VAE has reached the order of 10^-4 thereby indicating good reconstruction of the original data.

As for dimension reduction using tICA, the VAMP-2 score confirms that our VAE model performs better than tICA. This manuscript uses deep neural networks to understand the structural and kinetic process of IDP and small molecule interaction. Dimension reduction using tICA would give different reaction coordinates and MSM built using the projected data of tICA will not be one-to one comparable with that obtained from VAE.

We had to perform noising, as we had only 9 contact maps. This led to overfitting of the CVAE model. To overcome this problem, we have introduced white noise to our data, so as to prevent the model from overfitting. The objective of the DCVAE model was to see how distinct these contact maps are based on their locations on a lower dimensional space. A visual inspection of the ensemble averaged contact map, especially for IDPs is much more difficult as compared to folded proteins. So, even before computing the Rg, Ree, SASA or secondary structure, this lower dimensional space will give us a preliminary idea of how each macrostate is different from every other.

As for the distribution of Rg, we have plotted it in Author response image 7. The residue-wise percentage secondary structure is plotted in figure S4-S6  for the holo and apo simulation respectively.

Author response image 7.

Distribution of radius of gyration for the three and six macrostates in the apo and holo simulation respectively.

As for training a model with a higher number of latent dimensions, we have retrained a VAE model with four dimensions in the latent space. The loss was of the order of 10-4. We built a MSM with the appropriate number of microstates and found the presence of six macrostates as evident from the ITS plot as shown in Figure S14 and S15.

This data is presented in Results and Discussion, Page 13

Major Weakness 4: The MSMs produced in this study have large discrepancies with MSMs previously produced on the same dataset by the same authors that are not discussed.

Previously - two of the authors of this manuscript (Menon and Mondal) authored a preprint titled "Small molecule modulates α-synuclein conformation and its oligomerization via Entropy Expansion" (https://www.biorxiv.org/content/10.1101/2022.10.20.513005v1.full) that analyzed the same 1500us holo simulation of alpha-synuclein binding Fasudil. In this study - they utilized the variational approach to Markov processes (VAMP) to build an MSM using a 1D order parameter as input (the radius of gyration), first discretizing the conformational space into 300 microstates before similarly building a 6 macrostate model. From examining the contact maps and secondary structure propensities of the holo MSMs from the current study and the previous study- some of the macrostates appear similar, however there appear to be orders of magnitude differences in the timescales of conformational transitions between the two models. The timescales of conformational transitions in the previous MSM are on the order of 10s of microseconds, while the timescales of transitions in this manuscript are 100s-1000s microseconds. In the previous manuscript, a 3 state MSM is built from an apo α-synuclein obtained from a continuous 73ms unbiased MD simulation of alpha-synuclein run at a different salt concentration (100mM) and an additional 33 ms of shorter simulations. The apo MSM from the previous study similarly reports very fast timescales of transitions between apo states (on the order ~1ms) - while the MSM reported in the current study (Figure 9) are on the order of 10s-100s of microseconds).

These discrepancies raise further concerns that the properties of the MSMs built on these systems are extremely sensitive to the chosen projection methods and MSM modeling choices and hyperparameters, and that neither model may be an accurate description of the true underlying dynamics

Suggestions to improve the study: The authors should discuss the discrepancies with the MSMs reported in their previous studies.

In the previous preprint, the radius of gyration was used as the collective variable to build the MSM. In this manuscript, we have used a much more general collective variable, reduced pairwise distance using VAE. Firstly, the collective variables used to build the model in the two works are different. Secondly, for the 73 μs apo simulation in the previous manuscript, the salt concentration used was 100 mM, but in this work, we have used a salt concentration of 50 mM, same as the salt concentration used in the holo simulations. Since the two simulation conditions are different with respect to salt concentration, the conformational space sampled in these conditions will be different and this will be reflected in the nature/features of the metastable states and the associated transition kinetics. Thirdly, the lag time at which the MSM was built was 3.6 ns in the previous manuscript, whereas, in this work we have used 32 ns. This is already off by a factor of 10. So the order of timescales have also changed. Thus, changes in the collective variable and change in the lag time at which the system reaches Markovianity is different. Hence, the timescales of transition among the macrostates are also different. Because of these differences, it would not be correct to compare the results that we would get from the two investigations.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

To highlight the role of the entropic expansion mechanism, I would suggest modifying the title to capture this result, for example: "An Integrated Machine Learning Approach Delineates an Entropic Expansion Mechanism for the Binding of a Small Molecule to α-Synuclein".

We have changed the title as suggested by the reviewer.

To my knowledge the binding of fasudil to alpha-synuclein has been shown in the simulations by Robustelli et al (JACS 2022), but the experimental evidence is less clear cut. If an experimental binding affinity and the effect on alpha-synuclein aggregation have been measured, they should be reported.

Reviewer #2 (Recommendations For The Authors):

We thank the reviewer for the careful evaluation of our manuscript and providing comments and questions that we have attempted to address and incorporate. 

Minor

Abstract:

In "which is able to statistically distinguish fuzzy ensemble", what does the word "statistically" mean in this context? Do the authors present evidence that the two ensembles are statistically different, and if so in what ways?

We have analyzed the apo and holo ensembles of aSyn using the framework of Markov State Models, which provides the stationary populations of the states that the model identifies. For this reason, we have used ‘which is able to statistically distinguish fuzzy ensemble’ as we compare and contrast the metastable states that we resolve using MSM. The MSM provides metastable states which are identified through statistical analysis of the transitions between states (transition probability matrix). We characterize their structural features to distinguish them which gives a meaningful interpretation of the fuzzy ensemble.

Abstract:

What does "entropic ordering" mean?

We thank the reviewer for pointing this out. Here, we mean that the presence of the small molecule only affects the protein backbone entropy while the entropy of water is not affected in the simulations with fasudil. We will rewrite this more clearly in the abstract. 

The changed sentence is as follows: 

“A thermodynamic analysis indicates that small-molecule modulates the structural repertoire of αS by tuning protein backbone entropy, however the entropy of the water remains unperturbed.”

Abstract:

What does "offering insights into entropic modulation" mean?

In this investigation, we first discretized the ensemble of a small-molecule binding/interacting with a disordered aSyn into the underlying metastable states, followed by characterisation of these identified states. As small molecule interactions can affect the overall entropy of the IDP, we estimated the said effect of fasudil binding on aSyn. We find that small molecule binding effect is manifested in the protein backbone entropy and the solvent entropy is not affected. Through this work, we highlight these insights into the modulatory effect that fasudil brings about in the entropy of the system (entropic modulation).

p. 3/4:

When the authors write "However, a routine comparison of monomeric αS ensemble... ensemble" it is unclear whether they are referring to previous work (they only cite a paper with simulations of "apo" aSYN, and if so which. Do they mean Ref 32? Also, the word "routine" sounds odd in this context.

We thank the author for pointing this out. We compared the ensemble properties (such as the distributions of the radius of gyration, end-to-end distance, solvent accessible surface area, secondary structure properties) of ɑ-synuclein monomer that we generated in neat water and the ensemble of ɑ-synuclein in the presence of the small molecule fasudil that is reported in Robustelli et.al. (Journal of the American Chemical Society, 144(6), pp.2501-2510).  We have now modified this sentence in the main manuscript as follows: (Page no 3)

“However, comparison of the global and local structural features of the αS ensemble in neat water and that in the presence of fasudil [32] (see Figure S1-S6) did not indicate a significant difference that is a customary signature of the dynamic IDP ensemble.”

p. 4:

Regarding "Integrative approaches are therefore gaining importance in IDP studies", these kinds of integrative approaches have been used for 20 years for studies of IDPs (with increasing sophistication and success), so I think "gaining" is somewhat of a stretch.

We thank the reviewer for this comment. We agree with the reviewer and have now changed this sentence  as follows:

“Integrative approaches have been exploited in studying IDPs as well as small-molecule binding to IDPs.”

p. 5:

What does "large scale" mean in "This study showed no large-scale differences between the bound and unbound states of αS"? Do the authors mean substantially/significantly different, or differences on a large (length) scale?

Here, we refer to the study of small molecule (fasudil) binding study to α-synclein reported in Robustelli et.al. (Journal of the American Chemical Society, 144(6), pp.2501-2510). In this study, the authors report no substantial (“large scale”) differences in the conformational ensembles of αsynuclein in the bound and unbound states of fasudil such as the backbone conformation distributions. 

p. 6:

The authors write "In a clear departure from the classical view of ligand binding to a folded globular protein, the visual change in αS ensemble due to the presence of small molecule is not so strikingly apparent." I don't understand this. Normally, there is very little difference between apo and holo protein structures for folded proteins, so I don't understand the "in a clear departure" part. This seems like a strawman. Of course, for folded proteins one can generally see the ligand bound, but here the authors are talking about the protein.

In case of folded proteins, the overall tertiary structure of the protein remains mostly the same upon binding of the ligand. Structural changes are localized in nature and primarily around the binding site. However, in case of ⍺Syn, binding of fasudil is transient and not as strong as seen for folded proteins. “Clear departure” refers to the fact that for ⍺Syn, binding of fasudil is more subtle and dispersed across the ensemble of conformations rather than localized changes as in case of folded proteins.

p. 6:

I don't think the term "data-agnostic" makes sense since these methods are based on data and also make some assumptions about how the data can/should be used.

We have replaced this term with “model-agnostic”.

p. 16:

How are contacts defined; please add to caption.

A contact is considered if the Cα atoms of two residues are within a distance of 8 Å of each other. We have updated the caption with this information in Figures 4 and 5.  

p. 20:

What do the authors mean by "non-specific interactions" in this context?

The interactions of fasudil are predominantly with the negatively charged residues in the C-terminal region of ⍺Syn via charge-charge and π-stacking interactions (Robustelli et.al. (Journal of the American Chemical Society, 144(6), pp.2501-2510)).

In addition, in some metastable states that we identify, we also observe transient interactions with residues in the hydrophobic NAC region and N-terminal region. We refer to these transient interactions as “non-specific” interactions.

p. 27:

Are the axes of Fig. 9c/d z1 and z2?

Yes. The axes are z1 and z2

Smaller than minor

Abstract:

Rephrase "In particular, the presence of fasudil in milieu"

We have rephrased the sentence as follows: 

“In particular, the presence of fasudil in the solvent…”

p. 4:

What does the word "potentially" do in "ensemble of conformations potentially sampled"?

Here, by potentially, we mean the various conformations that the protein can adopt, subject to the environmental conditions. 

p. 10:

"we trained a large array of inter-residue pairwise distances"

The distances were not trained; please reformulate

We have corrected this sentence as follows:  

“We trained a VAE model using a large array of inter-residue pairwise distances.”

p. 13:

N/C-terminal -> terminus (or in the C-terminal region)

We have made the changes in the manuscript at the required places. 

p. 20:

Precedent -> previous (?)

We have made the change in the manuscript. 

p. 30:

As far as I understand, Anton does not use GPUs and does not run Desmond.

We thank the reviewer for providing this information. We referred to the original paper of the ⍺syn-fasudil simulations (Robustelli et.al. (Journal of the American Chemical Society, 144(6), pp.2501-2510)). The authors have performed equilibration with GPU/Desmond and used Anton for production runs. We have modified this sentence as:

We have modified this sentence as: 

“A 1500 μs long all-atom MD simulation trajectory of αS monomer in aqueous fasudil solution was simulated by D. E. Shaw Research with the Anton supercomputer that is specially purposed for running long-time-scale simulations.” on page 31

References : 

(1) Schütte  C,  Fischer  A,  Huisinga  W,  Deuflhard  P  (1999)  A  direct  approach  to  conformational  dynamics  based  on  hybrid  monte  carlo. J  Comput  Phys 151:146–168

(2) Chodera JD, Swope WC, Pitera JW, Dill KA (2006) Long-time protein folding dynamics from short-time molecular dynamics simulations.Multiscale  Model  Simul5:1214–1226.

Author response:

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

Reviewer #1 (Public review):

Summary:

This work seeks to provide genetic evidence for a role for beta-adrenergic receptors that regulate heart rate and blood flow on cavernous malformation development using a zebrafish model, and to extend information regarding beta-adrenergic drug blockade in cavernous malformation development, with the idea that these drugs may be useful therapeutically.

Strengths:

The work shows that genetic loss of a specific beta-adrenergic receptor in zebrafish, adrb1, prevents embryonic venous malformations and CCM in adult zebrafish brains. Two drugs, propranolol and metoprolol, also blunt CCM in the adult fish brain. These findings are predicted to potentially impact the treatment of human CCM, and they increase understanding of the factors leading to CCM.

Response 1: We are grateful for the reviewer’s acknowledgment of this study’s potential translational significance.

Weaknesses:

There are minor weaknesses that detract slightly from enthusiasm, including poor annotation of the Figure panels and lack of a baseline control for the study of Klf2 expression (Figure 4).

Response 2: We agree. Annotation of the Figure panels were added, and a baseline control for the study of klf2a expression (Figure 4) was added. Details were described in the response to “recommendations for the authors”.

Reviewer #2 (Public review):

Summary:

Previously, the authors developed a zebrafish model for cerebral cavernous malformations (CCMs) via CRISPR/Cas9-based mosaic inactivation of the ccm2 gene. This model yields CCM-like lesions in the caudal venous plexus of 2 days post-fertilization embryos and classical CNS cavernomas in 8-week fish that depend, like the mouse model, on the upregulation of the KLF2 transcription factor. Remarkably, the morpholino-based knockdown of the gene encoding the Beta1 adrenergic receptor or B1AR (adrb1; a hemodynamic regulator) in fish and treatment with the anti-adrenergic S enantiomer of propranolol in both fish and mice reduce the frequency and size of CMM lesions.

In the present study, the authors aim to test the model that adrb1 is required for CCM lesion development using adrb1 mutant fish (rather than morpholino-mediated knockdown and pharmacological treatments with the anti-adrenergic S enantiomer of propranolol or a racemic mix of metoprolol (a selective B1AR antagonist).

Strengths:

The goal of the work is important, and the findings are potentially highly relevant to cardiovascular medicine.

Response 3: We are grateful for the reviewer’s acknowledgment of this study’s scientific importance and clinical relevance.

Weaknesses:

(1) The following figures do not report sample sizes, making it difficult to assess the validity of the findings: Figures 1B and D (the number of scored embryos is missing), Figures 2G and 3B (should report both the number of fish and lesions scored, with color-coding to label the lesions corresponding to individual fish in which they were found).

Response 4: We agree. Sample sizes of Figures 1B and D were added in the figures and figure legends. Sample sizes of Figures 2G and 3B were added in their figure legend respectively. The lesion volume in Figures 2G and 3B is the total lesion volume in each brain.

(2) Figure 4 has a few caveats. First, the use of adrb1 morphants (rather than morphants) is at odds with the authors' goal of using genetic validation to test the involvement of adrb1 in CCM2-induced lesion development.

Second, the authors should clarify if they have validated that the tnnt (tnnt2a) morpholino phenocopies tnnt2a mutants in the context in which they are using it (this reviewer found that the tnnt2a morpholino blocks the heartbeat just like the mutant, but induces additional phenotypes not observed in the mutants).

Response 5: We appreciate the reviewer’s comments; however, generating adrb1^-/- and tnnt2a^-/- klf2a reporter fish, while also ensuring the presence of only one EGFP transgene allele for intensity measurement, would require prohibitively time-consuming breeding efforts.

The use of morpholinos for tnnt2a and adrb1, as well as their effects on the heart, have been well-documented in previous studies (Sehnert AJ et al., Nat Genet. 2002;31:106-10; Steele SL et al., J Exp Biol. 2011;214:1445-57).

Third, the data in Figure 4E is from just two embryos per treatment, a tiny sample size. Furthermore, judging from the number of points in the graph, only a few endothelial PCV cells appear to have been sampled per embryo. Also, judging from the photos and white arrowheads and arrows (Figure 4A-D), only the cells at the ventral side of the vessel were scored (if so, the rationale behind this choice requires clarification).

Response 6: We have increased the sample size, as described in the Figure 4 legend. Regarding the scoring of endothelial nuclei, we focused on the ventral side of the vessel because nuclei on the dorsal side often reside at branching points of the venous plexus. This positional variance could influence klf2a expression levels; thus, we focused on the ventral surface to limit this potential confounding variable.

Fourth, it is unclear whether and how the Tg(kdrl:mcherry)is5 endothelial reporter was used to mask the signals from the klf2a reporter. The reviewer knows by experience that accuracy suffers if a cytosolic or cell membrane signal is used to mask a nuclear green signal.

Response 7: We agree that it is theoretically possible for Förster resonance energy transfer (FRET) to occur, as the emission spectrum of EGFP (495-550 nm in our filter setup) overlaps with the absorption spectrum of mCherry. However, several factors reduce the likelihood of FRET in our experimental setup:

(1)  Without a nuclear localization signal, the majority of mCherry is localized in the cytoplasm, although small amounts may passively diffuse into the nucleus.

(2)  EGFP, on the other hand, is predominantly localized in the nucleus due to the presence of a nuclear localization signal.

(3)  FRET requires two fluorophores to be within a proximity of 8-10 nanometers or less for efficient energy transfer. The nuclear envelope, with a typical thickness of 30-50 nanometers, separates nuclear EGFP from cytoplasmic mCherry and FRET efficiency is inversely proportional to the sixth power of the distance between donor and acceptor. Thus, the theoretical likelihood of significant energy transfer under these conditions is low.

To empirically examine potential FRET between nuclear EGFP and mcherry in our experiment setup, we scanned and scored the Tg(klf2a:H2b-EGFP; kdrl:mcherry) double transgenic embryos and Tg(klf2a:H2b-EGFP) embryos for EGFP intensity. The result is attached here:

Author response image 1.

42 endothelial nuclei from 7 embryos were scored as described in the Experimental Procedures of the manuscript. Two tailed t test were performed. P=0.4529

Finally, the text and legend related to Figure 4 could be more explicit. What do the authors mean by a mosaic pattern of endothelial nuclear EGFP intensity, and how is that observation reflected in graph 4E? When I look at the graph, I understand that klf2a is decreased in C-D compared to A-B. Are some controls missing? Suppose the point is to show mosaicism of Klf2a levels upon ccm2 CRISPR. Don't you need embryos without ccm2 CRISPR to show that Klf2a levels in those backgrounds have average levels that vary within a defined range and that in the presence of ccm2 mosaicism, some cells have values significantly outside that range? Also, in 4A-D, what are the white arrowheads and arrows? The legend does not mention them.

Response 8: We have revised our description of Figure 4 to better convey that mosaic expression of KLF2a is evidenced by the wide variability of klf2a reporter intensity in endothelial cells in ccm2 CRISPR embryos. A baseline control for the study of klf2a expression was added to Figure 4. The arrowheads and arrows in Figure 4A-D are explained in Figure 4 legends.

Given the practical relevance of the findings to cardiovascular medicine, increasing the strength of the evidence would greatly enhance the value of this work.

Recommendations for the authors:

Reviewing Editor:

Concerns about the labeling of figures and sample sizes should both be addressed, as detailed in the reviews, as this will be important to ensure the robustness of the claims.

Reviewer #1 (Recommendations for the authors):

Overall a strong research advance that provides rigorous genetic analysis and further drug testing in the zebrafish CCM model. There are some minor issues that, if addressed, would strengthen the work.

Minor issues:

(1) Figures in general are very poorly annotated and labeled. None of the images in Figures 1-3 show the reporter used to visualize vessels/CM, and the scale bars are not sized in the Figures or legends. Figure 1B is an experiment where the effects of a drug that increases heart rate are evaluated in mutants and controls, but the drug is not mentioned in the figure panel. Figure 1D shows the percentage of embryos with CVP dilation, but the graph and accompanying description does not define whether the percent is relative to the total embryos from the intercross or the percent of that category having the CVP dilation.

Response 9: Changes were made in Figures and Figure legends. The transgenic reporter line Tg(fli1:EGFP) was annotated in Figures 1-3. Scale bars were sized in the Figures and Figure legends. The chemical used for Figure 1B was annotated in the Figure. The percentage of CVP dilation in the graph was explained in the Figure legend.

(2) Figure 4 does not include baseline data in unmanipulated embryos scored at the same time to show the increase in Klf2 expression with mosaic ccm2 deletion. This is important as the result in E is interpreted as a lack of change in the increase.

Response 10: A baseline control for the study of klf2a expression in Figure 4 was added.

Reviewer #2 (Recommendations for the authors):

SUGGESTIONS FOR EXPERIMENTS, DATA, OR ANALYSES

(1) For maximum rigor, in the Figure 4 experiment, use adrb1 mutants and tnnt2a (silent heart) mutants (or verify that the adrb1 and tnnt2a morpholinos faithfully copy the phenotype of interest). See: Guidelines for morpholino use in zebrafish (PMID: 29049395; PMCID: PMC5648102).

Response 11: See Response 5.

(2) Increase sample sizes if appropriate.

Response 12: In the revised version of the manuscript, we have increased the sample size, as described in the Figure 4 legend.

(3) The imaging and fluorescence intensity analysis methods require more detail for reproducibility's sake. Please provide this information. See as a guideline: Guillermo MarquésThomas PengoMark A Sanders (2020) Science Forum: Imaging methods are vastly underreported in biomedical research eLife 9:e55133.

Response 13: We added detailed procedures for the “Airyscan imaging and fluorescence intensity analysis” in the “Experimental Procedures”.

(4) I suggest further clarifying how inhibition of B1AR prevents cavernoma formation. Given that lesion formation is suppressed in adrb1 mutants (which have slow blood flow) and 2,3-BDM treatment (which also slows blood flow) has a similar effect, the beneficial effects of propranolol and metoprolol might be due to the slowing of blood flow via B1AR targeting rather than reflecting that B1AR is a critical component of the genetic circuit for cavernoma formation. Indeed, in prior work by the same first author and collaborators (Elife 2021 May 20:10:e62155), the investigators observed reduced cavernoma formation in embryos devoid of cardiac contractility and thus lacking blood flow (tnnt2a morphants). Such a scenario does not take away the value of a pharmacological treatment. Still, it implies a different mechanism and allows potentially many other drugs with similar effects on blood flow to be effective.

Discussing how B1AR activity is regulated and outlining future experiments would be helpful. Suggestions for the latter include testing the effect of normalizing blood flow in adrb1 mutants with a drug or providing exogenous B1AR in the myocardium or the endothelium to test the model further.

Response 14: We are grateful for the reviewer’s suggestions and added the statement for future experiments.

MINOR CORRECTIONS TO TEXT AND FIGURES

(1) Figure 4E: Label the four genotypes explicitly, rather than A-D for the reader's ease.

(2) Legend of Figure 4: "(F) EGFP intensity...". It should be (E).

CITATIONS TO CORRECT

(1) The citation for the Tg(kdrl:mcherry)is5 transgene needs to be corrected (reference 29 is from the Stainier lab). However, the "is" designation is for the Essner lab (https://zfin.org/action/feature/view/ZDB-ALT-110127-25)

Response 15: Corrections were made as instructed.

Author Response

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

eLife assessment

This important study identifies the mitotic localization mechanism for Aurora B and INCENP (parts of the chromosomal passenger complex, CPC) in Trypanosoma brucei. The mechanism is different from that in the more commonly studied opisthokonts and there is solid support from RNAi and imaging experiments, targeted mutations, immunoprecipitations with crosslinking/mass spec, and AlphaFold interaction predictions. The results could be strengthened by biochemically testing proposed direct interactions and demonstrating that the targeting protein KIN-A is a motor. The findings will be of interest to parasitology researchers as well as cell biologists working on mitosis and cell division, and those interested in the evolution of the CPC.

We thank the editor and the reviewers for their thorough and positive assessment of our work and the constructive feedback to further improve our manuscript. Please find below our responses to the reviewers’ comments. Please note that the conserved glycine residue in the Switch II helix in KIN-A was mistakenly labelled as G209 in the original manuscript. We now corrected it to G210 in the revised manuscript.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The CPC plays multiple essential roles in mitosis such as kinetochore-microtubule attachment regulation, kinetochore assembly, spindle assembly checkpoint activation, anaphase spindle stabilization, cytokinesis, and nuclear envelope formation, as it dynamically changes its mitotic localization: it is enriched at inner centromeres from prophase to metaphase but it is relocalized at the spindle midzone in anaphase. The business end of the CPC is Aurora B and its allosteric activation module IN-box, which is located at the C-terminal part of INCENP. In most well-studied eukaryotic species, Aurora B activity is locally controlled by the localization module of the CPC, Survivin, Borealin, and the N-terminal portion of INCENP. Survivin and Borealin, which bind the N terminus of INCENP, recognize histone residues that are specifically phosphorylated in mitosis, while anaphase spindle midzone localization is supported by the direct microtubule-binding capacity of the SAH (single alpha helix) domain of INCENP and other microtubule-binding proteins that specifically interact with INCENP during anaphase, which are under the regulation of CDK activity. One of these examples includes the kinesin-like protein MKLP2 in vertebrates.

Trypanosoma is an evolutionarily interesting species to study mitosis since its kinetochore and centromere proteins do not show any similarity to other major branches of eukaryotes, while orthologs of Aurora B and INCENP have been identified. Combining molecular genetics, imaging, biochemistry, cross-linking IP-MS (IP-CLMS), and structural modeling, this manuscript reveals that two orphan kinesin-like proteins KIN-A and KIN-B act as localization modules of the CPC in Trypanosoma brucei. The IP-CLMS, AlphaFold2 structural predictions, and domain deletion analysis support the idea that (1) KIN-A and KIN-B form a heterodimer via their coiled-coil domain, (2) Two alpha helices of INCENP interact with the coiled-coil of the KIN-A-KIN-B heterodimer, (3) the conserved KIN-A C-terminal CD1 interacts with the heterodimeric KKT9-KKT11 complex, which is a submodule of the KKT7-KKT8 kinetochore complex unique to Trypanosoma, (4) KIN-A and KIN-B coiled-coil domains and the KKT7-KKT8 complex are required for CPC localization at the centromere, (5) CD1 and CD2 domains of KIN-A support its centromere localization. The authors further show that the ATPase activity of KIN-A is critical for spindle midzone enrichment of the CPC. The imaging data of the KIN-A rigor mutant suggest that dynamic KIN-A-microtubule interaction is required for metaphase alignment of the kinetochores and proliferation. Overall, the study reveals novel pathways of CPC localization regulation via KIN-A and KIN-B by multiple complementary approaches.

Strengths:

The major conclusion is collectively supported by multiple approaches, combining site-specific genome engineering, epistasis analysis of cellular localization, AlphaFold2 structure prediction of protein complexes, IP-CLMS, and biochemical reconstitution (the complex of KKT8, KKT9, KKT11, and KKT12).

We thank the reviewer for her/his positive assessment of our manuscript.

Weaknesses:

• The predictions of direct interactions (e.g. INCENP with KIN-A/KIN-B, or KIN-A with KKT9-KKT11) have not yet been confirmed experimentally, e.g. by domain mutagenesis and interaction studies.

Thank you for this point. It is true that we do not have evidence for direct interactions between KIN-A with KKT9-KKT11. However, the interaction between INCENP with KIN-A/KIN-B is strongly supported by our cross-linking IP-MS of native complexes. Furthermore, we show that deletion of the INCENPCPC1 N-terminus predicted to interact with KIN-A:KIN-B abolishes kinetochore localization.

• The criteria used to judge a failure of localization are not clearly explained (e.g., Figure 5F, G).

As suggested by the reviewer in recommendation #14, we have now included example images for each category (‘kinetochores’, ‘kinetochores + spindle’, ‘spindle’) along with a schematic illustration in Fig. 5F.

• It remains to be shown that KIN-A has motor activity.

We thank the reviewer for this important comment. Indeed, motor activity remains to demonstrated using an in vitro system, which is beyond the scope of this study. What we show here is that the motor domain of KIN-A effectively co-sediments with microtubules and that spindle localization of KIN-A is abolished upon deletion of the motor domain. Moreover, mutation of a conserved Glycine residue in the Switch II region (G210) to Alanine (‘rigor mutation’, (Rice et al., 1999)), renders KIN-A incapable of translocating to the central spindle, suggesting that its ATPase activity is required for this process. To clarify this point in the manuscript, we have replaced all instances, where we refer to ‘motor activity’ of KIN-A with ‘ATPase activity’ when referring to experiments performed using the KIN-A rigor mutant. In addition, we have included a Multiple Sequence Alignment (MSA) of KIN-A and KIN-B from different kinetoplastids with human Kinesin-1, human Mklp2 and yeast Klp9 in Figure 6A and S6A, showing the conservation of key motifs required for ATP coordination and tubulin interaction. In the corresponding paragraph in the main text, we describe these data as follows:

‘We therefore speculated that anaphase translocation of the kinetoplastid CPC to the central spindle may involve the kinesin motor domain of KIN-A. KIN-B is unlikely to be a functional kinesin based on the absence of several well-conserved residues and motifs within the motor domain, which are fully present in KIN-A (Li et al., 2008). These include the P-loop, switch I and switch II motifs, which form the nucleotide binding cleft, and many conserved residues within the α4-L12 elements, which interact with tubulin (Fig. S6A) (Endow et al., 2010). Consistent with this, the motor domain of KIN-B, contrary to KIN-A, failed to localize to the mitotic spindle when expressed ectopically (Fig. S2E) and did not co-sediment with microtubules in our in vitro assay (Fig. S6B).’

• The authors imply that KIN-A, but not KIN-B, interacts with microtubules based on microtubule pelleting assay (Fig. S6), but the substantial insoluble fractions of 6HIS-KINA and 6HIS-KIN-B make it difficult to conclusively interpret the data. It is possible that these two proteins are not stable unless they form a heterodimer.

This is indeed a possibility. We are currently aiming at purifying full-length recombinant KIN-A and KIN-B (along with the other CPC components), which will allow us to perform in vitro interaction studies and to investigate biochemical properties of this complex (including the role of the motor domains of KIN-A and KIN-B) within the framework of an in-depth follow-up study. To address the point above, we have added the following text in the legend corresponding to Fig. S6:

‘Microtubule co-sedimentation assay with 6HIS-KIN-A2-309 (left) and 6HIS-KIN-B2-316 (right). S and P correspond to supernatant and pellet fractions, respectively. Note that both constructs to some extent sedimented even in the absence of microtubules. Hence, lack of microtubule binding for KIN-B may be due to the unstable non-functional protein used in this study.’

• For broader context, some prior findings should be introduced, e.g. on the importance of the microtubule-binding capacity of the INCENP SAH domain and its regulation by mitotic phosphorylation (PMID 8408220, 26175154, 26166576, 28314740, 28314741, 21727193), since KIN-A and KIN-B may substitute for the function of the SAH domain.

We have modified the introduction to include the following text and references mentioned by the reviewer: ‘The localization module comprises Borealin, Survivin and the N-terminus of INCENP, which are connected to one another via a three-helical bundle (Jeyaprakash et al., 2007, 2011; Klein et al., 2006). The two modules are linked by the central region of INCENP, composed of an intrinsically disordered domain and a single alpha helical (SAH) domain. INCENP harbours microtubule-binding domains within the N-terminus and the central SAH domain, which play key roles for CPC localization and function (Samejima et al., 2015; Kang et al., 2001; Noujaim et al., 2014; Cormier et al., 2013; Wheatley et al., 2001; Nakajima et al., 2011; Fink et al., 2017; Wheelock et al., 2017; van der Horst et al., 2015; Mackay et al., 1993).’

Reviewer #2 (Public Review):

How the chromosomal passenger complex (CPC) and its subunit Aurora B kinase regulate kinetochore-microtubule attachment, and how the CPC relocates from kinetochores to the spindle midzone as a cell transitions from metaphase to anaphase are questions of great interest. In this study, Ballmer and Akiyoshi take a deep dive into the CPC in T. brucei, a kinetoplastid parasite with a kinetochore composition that varies greatly from other organisms.

Using a combination of approaches, most importantly in silico protein predictions using alphafold multimer and light microscopy in dividing T. brucei, the authors convincingly present and analyse the composition of the T. brucei CPC. This includes the identification of KIN-A and KIN-B, proteins of the kinesin family, as targeting subunits of the CPC. This is a clear advancement over earlier work, for example by Li and colleagues in 2008. The involvement of KIN-A and KIN-B is of particular interest, as it provides a clue for the (re)localization of the CPC during the cell cycle. The evolutionary perspective makes the paper potentially interesting for a wide audience of cell biologists, a point that the authors bring across properly in the title, the abstract, and their discussion.

The evolutionary twist of the paper would be strengthened 'experimentally' by predictions of the structure of the CPC beyond T. brucei. Depending on how far the authors can extend their in-silico analysis, it would be of interest to discuss a) available/predicted CPC structures in well-studied organisms and b) structural predictions in other euglenozoa. What are the general structural properties of the CPC (e.g. flexible linkers, overall dimensions, structural differences when subunits are missing etc.)? How common is the involvement of kinesin-like proteins? In line with this, it would be good to display the figure currently shown as S1D (or similar) as a main panel.

We thank the reviewer for her/his encouraging assessment of our manuscript and the appreciation on the extent of the evolutionary relevance of our work. As suggested, we have moved the phylogenetic tree previously shown in Fig. S1D to the main Fig. 1F. Our AF2 analysis of CPC proteins and (sub)complexes from other kinetoplastids failed to predict reliable interactions among CPC proteins except for that between Aurora B and the IN box. It therefore remains unclear whether CPC structures are conserved among kinetoplastids. Because components of CPC remain unknown in other euglenozoa (other than Aurora B and INCENP), we cannot perform structural predictions of CPC in diplonemids or euglenids.

It remains unclear how common the involvement of kinesin-like proteins with the CPC is in other eukaryotes, partly because we could not identify an obvious homolog of KIN-A/KIN-B outside of kinetoplastids. Addressing this question would require experimental approaches in various eukaryotes (e.g. immunoprecipitation and mass spectrometry of Aurora B) as we carried out in this manuscript using Trypanosoma brucei.

Reviewer #3 (Public Review):

Summary:

The protein kinase, Aurora B, is a critical regulator of mitosis and cytokinesis in eukaryotes, exhibiting a dynamic localisation. As part of the Chromosomal Passenger Complex (CPC), along with the Aurora B activator, INCENP, and the CPC localisation module comprised of Borealin and Survivin, Aurora B travels from the kinetochores at metaphase to the spindle midzone at anaphase, which ensures its substrates are phosphorylated in a time- and space-dependent manner. In the kinetoplastid parasite, T. brucei, the Aurora B orthologue (AUK1), along with an INCENP orthologue known as CPC1, and a kinetoplastid-specific protein CPC2, also displays a dynamic localisation, moving from the kinetochores at metaphase to the spindle midzone at anaphase, to the anterior end of the newly synthesised flagellum attachment zone (FAZ) at cytokinesis. However, the trypanosome CPC lacks orthologues of Borealin and Survivin, and T. brucei kinetochores also have a unique composition, being comprised of dozens of kinetoplastid-specific proteins (KKTs). Of particular importance for this study are KKT7 and the KKT8 complex (comprising KKT8, KKT9, KKT11, and KKT12). Here, Ballmer and Akiyoshi seek to understand how the CPC assembles and is targeted to its different locations during the cell cycle in T. brucei.

Strengths & Weaknesses:

Using immunoprecipitation and mass-spectrometry approaches, Ballmer and Akiyoshi show that AUK1, CPC1, and CPC2 associate with two orphan kinesins, KIN-A and KIN-B, and with the use of endogenously expressed fluorescent fusion proteins, demonstrate for the first time that KIN-A and KIN-B display a dynamic localisation pattern similar to other components of the CPC. Most of these data provide convincing evidence for KIN-A and KIN-B being bona fide CPC proteins, although the evidence that KIN-A and KIN-B translocate to the anterior end of the new FAZ at cytokinesis is weak - the KIN-A/B signals are very faint and difficult to see, and cell outlines/brightfield images are not presented to allow the reader to determine the cellular location of these faint signals (Fig S1B).

We thank the reviewer for their thorough assessment of our manuscript and the insightful feedback to further improve our study. To address the point above, we have acquired new microscopy data for Fig. S1B and S1C, which now includes phase contrast images, and have chosen representative cells in late anaphase and telophase. We hope that the signal of Aurora BAUK1, KIN-A and KIN-B at the anterior end of the new FAZ can be now distinguished more clearly.

They then demonstrate, by using RNAi to deplete individual components, that the CPC proteins have hierarchical interdependencies for their localisation to the kinetochores at metaphase. These experiments appear to have been well performed, although only images of cell nuclei were shown (Fig 2A), meaning that the reader cannot properly assess whether CPC components have localised elsewhere in the cell, or if their abundance changes in response to depletion of another CPC protein.

We chose to show close-ups of the nucleus to highlight the different localization patterns of CPC proteins under the different RNAi conditions. In none of these conditions did we observe mis-localization of CPC subunits to the cytoplasm. To clarify this point, we added the following sentence in the legend for Figure 2A:

‘A) Representative fluorescence micrographs showing the localization of YFP-tagged Aurora BAUK1, INCENPCPC1, KIN-A and KIN-B in 2K1N cells upon RNAi-mediated knockdown of indicated CPC subunits. Note that nuclear close-ups are shown here. CPC proteins were not detected in the cytoplasm. RNAi was induced with 1 μg/mL doxycycline for 24 h (KIN-B RNAi) or 16 h (all others). Cell lines: BAP3092, BAP2552, BAP2557, BAP3093, BAP2906, BAP2900, BAP2904, BAP3094, BAP2899, BAP2893, BAP2897, BAP3095, BAP3096, BAP2560, BAP2564, BAP3097. Scale bars, 2 μm.’

Ballmer and Akiyoshi then go on to determine the kinetochore localisation domains of KIN-A and KIN-B. Using ectopically expressed GFP-tagged truncations, they show that coiled-coil domains within KIN-A and KIN-B, as well as a disordered C-terminal tail present only in KIN-A, but not the N-terminal motor domains of KIN-A or KIN-B, are required for kinetochore localisation. These data are strengthened by immunoprecipitating CPC complexes and crosslinking them prior to mass spectrometry analysis (IP-CLMS), a state-of-the-art approach, to determine the contacts between the CPC components. Structural predictions of the CPC structure are also made using AlphaFold2, suggesting that coiled coils form between KIN-A and KIN-B, and that KIN-A/B interact with the N termini of CPC1 and CPC2. Experimental results show that CPC1 and CPC2 are unable to localise to kinetochores if they lack their N-terminal domains consistent with these predictions. Altogether these data provide convincing evidence of the protein domains required for CPC kinetochore localisation and CPC protein interactions. However, the authors also conclude that KIN-B plays a minor role in localising the CPC to kinetochores compared to KIN-A. This conclusion is not particularly compelling as it stems from the observation that ectopically expressed GFP-NLS-KIN-A (full length or coiled-coil domain + tail) is also present at kinetochores during anaphase unlike endogenously expressed YFP-KIN-A. Not only is this localisation probably an artifact of the ectopic expression, but the KIN-B coiled-coil domain localises to kinetochores from S to metaphase and Fig S2G appears to show a portion of the expressed KIN-B coiled-coil domain colocalising with KKT2 at anaphase. It is unclear why KIN-B has been discounted here.

As the reviewer points out, a small fraction of GFP-NLS-KIN-B317-624 is indeed detectable at kinetochores in anaphase, although most of the protein shows diffuse nuclear staining. There are various explanations for this phenomenon: It is conceivable that the KIN-B motor domain may contribute to microtubule binding and translocation of the CPC from kinetochores onto the spindle in anaphase. In our experiments, ectopically expressed KIN-B317-624 likely outcompetes a fraction of endogenous KIN-B for binding to KIN-A, which could interfere with this translocation process, leaving a population of CPC ‘stranded’ at kinetochores in anaphase. Another possibility, hinted at by the reviewer, is that the C-terminus of KIN-B interacts with receptors at the kinetochore/centromere. Although we do not discount this possibility, we nevertheless decided to focus on KIN-A in this study, because the anaphase kinetochore retention phenotype for both full-length GFP-NLS-KIN-A and -KIN-A309-862 is much stronger than for KIN-B317-624. Two additional reasons were that (i) KIN-A is highly conserved within kinetoplastids, whereas KIN-B orthologs are missing in some kinetoplastids, and (ii) no convincing interactions between KIN-B and kinetochore proteins were predicted by AF2.

To address the reviewer’s point, we decided to include KIN-B in the title of this manuscript, which now reads: ‘Dynamic localization of the chromosomal passenger complex is controlled by the orphan kinesins KIN-A and KIN-B in the kinetoplastid parasite Trypanosoma brucei’.

Moreover, we modified the corresponding paragraph in the results section as follows:

‘Intriguingly, unlike endogenously YFP-tagged KIN-A, ectopically expressed GFP fusions of both full-length KIN-A and KIN-A310-862 clearly localized at kinetochores even in anaphase (Figs. 2, F and H). Weak anaphase kinetochore signal was also detectable for KIN-B317-624 (Fig. S2F). GFP fusions of the central coiled-coil domain or the C-terminal disordered tail of KIN-A did not localize to kinetochores (data not shown). These results show that kinetochore localization of the CPC is mediated by KIN-A and KIN-B and requires both the central coiled-coil domain as well as the C-terminal disordered tail of KIN-A.’

Next, using a mixture of RNAi depletion and LacI-LacO recruitment experiments, the authors show that kinetochore proteins KKT7 and KKT9 are required for AUK1 to localise to kinetochores (other KKT8 complex components were not tested here) and that all components of the KKT8 complex are required for KIN-A kinetochore localisation. Further, both KKT7 and KKT8 were able to recruit AUK1 to an ectopic locus in the S phase, and KKT7 recruited KKT8 complex proteins, which the authors suggest indicates it is upstream of KKT8. However, while these experiments have been performed well, the reciprocal experiment to show that KKT8 complex proteins cannot recruit KKT7, which could have confirmed this hierarchy, does not appear to have been performed. Further, since the LacI fusion proteins used in these experiments were ectopically expressed, they were retained (artificially) at kinetochores into anaphase; KKT8 and KIN-A were both able to recruit AUK1 to LacO foci in anaphase, while KKT7 was not. The authors conclude that this suggests the KKT8 complex is the main kinetochore receptor of the CPC - while very plausible, this conclusion is based on a likely artifact of ectopic expression, and for that reason, should be interpreted with a degree of caution.

We previously showed that RNAi-mediated depletion of KKT7 disrupts kinetochore localization of KKT8 complex members, whereas kinetochore localization of KKT7 is unaffected by disruption of the KKT8 complex (Ishii and Akiyoshi, 2020). Moreover, in contrast to the KKT8 complex, KKT7 remains at kinetochores in anaphase (Akiyoshi and Gull, 2014). These data show that KKT7 is upstream of the KKT8 complex. In this context, the LacI-LacO tethering approach can be very useful to probe whether two proteins (or domains of proteins) could interact in vivo either directly or indirectly. However, a recruitment hierarchy cannot be inferred from such experiments because the data just shows whether X can recruit Y to an ectopic locus (but not whether X is upstream of Y or vice versa). Regarding the retention of Aurora BAUK1 at kinetochores in anaphase upon ectopic expression of GFP-KKT8-LacI, we agree with the reviewer that these data need to be carefully interpreted. Nevertheless, the notion that the KKT7-KKT8 complex recruits the CPC to kinetochores is also strongly supported by IP-MS, RNAi experiments, and AF2 predictions. For clarification and to address the reviewer’s point, we re-formulated the corresponding paragraph in the main text:

‘We previously showed that KKT7 lies upstream of the KKT8 complex (Ishii and Akiyoshi, 2020). Indeed, GFP-KKT72-261-LacI recruited tdTomato-KKT8, -KKT9 and -KKT12 (Fig. S4E). Expression of both GFP-KKT72-261-LacI and GFP-KKT8-LacI resulted in robust recruitment of tdTomato-Aurora BAUK1 to LacO foci in S phase (Figs. 4, E and F). Intriguingly, we also noticed that, unlike endogenous KKT8 (which is not present in anaphase), ectopically expressed GFP-KKT8-LacI remained at kinetochores during anaphase (Fig. 4F). This resulted in a fraction of tdTomato-Aurora BAUK1 being trapped at kinetochores during anaphase instead of migrating to the central spindle (Fig. 4F). We observed a comparable situation upon ectopic expression of GFP-KIN-A, which is retained on anaphase kinetochores together with tdTomato-KKT8 (Fig. S4F). In contrast, Aurora BAUK1 was not recruited to LacO foci marked by GFP- KKT72-261-LacI in anaphase (Fig. 4E).’

Further IP-CLMS experiments, in combination with recombinant protein pull-down assays and structural predictions, suggested that within the KKT8 complex, there are two subcomplexes of KKT8:KKT12 and KKT9:KKT11, and that KKT7 interacts with KKT9:KKT11 to recruit the remainder of the KKT8 complex. The authors also assess the interdependencies between KKT8 complex components for localisation and expression, showing that all four subunits are required for the assembly of a stable KKT8 complex and present AlphaFold2 structural modelling data to support the two subcomplex models. In general, these data are of high quality and convincing with a few exceptions. The recombinant pulldown assay (Fig. 4H) is not particularly convincing as the 3rd eluate gel appears to show a band at the size of KKT11 (despite the labelling indicating no KKT11 was present in the input) but no pulldown of KKT9, which was present in the input according to the figure legend (although this may be mislabeled since not consistent with the text). The text also states that 6HIS-KKT8 was insoluble in the absence of KKT12, but this is not possible to assess from the data presented.

We thank the reviewer for pointing out an error in the text: ‘Removal of both KKT9 and KKT11 did not impact formation of the KKT8:KKT12 subcomplex’ should read ‘Removal of either KKT9 or KKT11 did not impact formation of the KKT8:KKT12 subcomplex’. Regarding the very faint band perceived to be KKT11 in the 3rd eluate: This band runs slightly lower than KKT11 and likely represents a bacterial contaminant (which we have seen also in other preps in the past). We have made a note of this in the corresponding legend (new Fig. 4I). Moreover, we provide the estimated molecular weights for each subunit, as suggested by the reviewer in recommendation #14 (see below):

‘(I) Indicated combinations of 6HIS-tagged KKT8 (~46 kDa), KKT9 (~39 kDa), KKT11 (~29 kDa) and KKT12 (~23 kDa) were co-expressed in E. coli, followed by metal affinity chromatography and SDS-PAGE. The asterisk indicates a common contaminant.’

The corresponding paragraph in the results section now reads:

To validate these findings, we co-expressed combinations of 6HIS-KKT8, KKT9, KKT11 and KKT12 in E. coli and performed metal affinity chromatography (Fig. 4I). 6HIS-KKT8 efficiently pulled down KKT9, KKT11 and KKT12, as shown previously (Ishii and Akiyoshi, 2020). In the absence of KKT9, 6HIS-KKT8 still pulled down KKT11 and KKT12. Removal of either KKT9 or KKT11 did not impact formation of the KKT8:KKT12 subcomplex. In contrast, 6HIS-KKT8 could not be recovered without KKT12, indicating that KKT12 is required for formation of the full KKT8 complex. These results support the idea that the KKT8 complex consists of KKT8:KKT12 and KKT9:KKT11 subcomplexes.’

It is also surprising that data showing the effects of KKT8, KKT9, and KKT12 depletion on KKT11 localisation and abundance are not presented alongside the reciprocal experiments in Fig S4G-J.

YFP-KKT11 is delocalized upon depletion of KKT8 and KKT9 (see below). Unfortunately, we were unsuccessful in our attempts at deriving the corresponding KKT12 RNAi cell line, rendering this set of data incomplete. Because these data are not of critical importance for this study, we decided not to invest more time in attempting further transfections.

Author response image 1.

The authors also convincingly show that AlphaFold2 predictions of interactions between KKT9:KKT11 and a conserved domain (CD1) in the C-terminal tail of KIN-A are likely correct, with CD1 and a second conserved domain, CD2, identified through sequence analysis, acting synergistically to promote KIN-A kinetochore localisation at metaphase, but not being required for KIN-A to move to the central spindle at anaphase. They then hypothesise that the kinesin motor domain of KIN-A (but not KIN-B which is predicted to be inactive based on non-conservation of residues key for activity) determines its central spindle localisation at anaphase through binding to microtubules. In support of this hypothesis, the authors show that KIN-A, but not KIN-B can bind microtubules in vitro and in vivo. However, ectopically expressed GFP-NLS fusions of full-length KIN-A or KIN-A motor domain did not localise to the central spindle at anaphase. The authors suggest this is due to the GPF fusion disrupting the ATPase activity of the motor domain, but they provide no evidence that this is the case. Instead, they replace endogenous KIN-A with a predicted ATPase-defective mutant (G209A), showing that while this still localises to kinetochores, the kinetochores were frequently misaligned at metaphase, and that it no longer concentrates at the central spindle (with concomitant mis-localisation of AUK1), causing cells to accumulate at anaphase. From these data, the authors conclude that KIN-A ATPase activity is required for chromosome congression to the metaphase plate and its central spindle localisation at anaphase. While potentially very interesting, these data are incomplete in the absence of any experimental data to show that KIN-A possesses ATPase activity or that this activity is abrogated by the G209A mutation, and the conclusions of this section are rather speculative.

Thank you for this important comment, which relates to a similar point raised by Reviewer 1 (see above). Indeed, ATPase and motor activity of KIN-A remain to demonstrated biochemically using recombinant proteins, which is beyond the scope of this study. We generated MSAs of KIN-A and KIN-B from different kinetoplastids with human Kinesin-1, human Mklp2 and yeast Klp9, which are now presented in Figure 6A and S6A. These clearly show that key motifs required for ATP or tubulin binding in other kinesins are highly conserved in KIN-A (but not KIN-B). This includes the conserved glycine residue in the Switch II helix (G234 in human Kinesin-1, G210 in T. brucei KIN-A), which forms a hydrogen bond with the γ-phosphate of ATP, and upon mutation has been shown to impair ATPase activity and trap the motor head in a strong microtubule (‘rigor’) state (Rice et al., 1999; Sablin et al., 1996). The prominent rigor phenotype of KIN-AG210A is consistent with KIN-A having ATPase activity. In addition to the data in Fig. 6A and S6A, we made following changes to the main text:

‘We therefore speculated that anaphase translocation of the kinetoplastid CPC to the central spindle may involve the kinesin motor domain of KIN-A. KIN-B is unlikely to be a functional kinesin based on the absence of several well-conserved residues and motifs within the motor domain, which are fully present in KIN-A (Li et al., 2008). These include the P-loop, switch I and switch II motifs, which form the nucleotide binding cleft, and many conserved residues within the α4-L12 elements, which interact with tubulin (Fig. S6A) (Endow et al., 2010). Consistent with this, the motor domain of KIN-B, contrary to KIN-A, failed to localize to the mitotic spindle when expressed ectopically (Fig. S2E) and did not co-sediment with microtubules in our in vitro assay (Fig. S6B).

Ectopically expressed GFP-KIN-A and -KIN-A2-309 partially localized to the mitotic spindle but failed to concentrate at the midzone during anaphase (Figs. 2, F and G), suggesting that N-terminal tagging of the KIN-A motor domain may interfere with its function. To address whether the ATPase activity of KIN-A is required for central spindle localization of the CPC, we replaced one allele of KIN-A with a C-terminally YFP-tagged G210A ATP hydrolysis-defective rigor mutant (Fig. 6A) (Rice et al., 1999) and used an RNAi construct directed against the 3’UTR of KIN-A to deplete the untagged allele. The rigor mutation did not affect recruitment of KIN-A to kinetochores (Figs. S6, C and D). However, KIN-AG210A-YFP marked kinetochores were misaligned in ~50% of cells arrested in metaphase, suggesting that ATPase activity of KIN-A promotes chromosome congression to the metaphase plate (Figs. S6, E-H).’

Impact:

Overall, this work uses a wide range of cutting-edge molecular and structural predictive tools to provide a significant amount of new and detailed molecular data that shed light on the composition of the unusual trypanosome CPC and how it is assembled and targeted to different cellular locations during cell division. Given the fundamental nature of this research, it will be of interest to many parasitology researchers as well as cell biologists more generally, especially those working on aspects of mitosis and cell division, and those interested in the evolution of the CPC.

We thank the reviewer for his/her feedback and thoughtful and thorough assessment of our study.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Why did the authors omit KIN-B from the title?

We decided to add KIN-B in the title. Please see our response to Reviewer #3 (public review).

(2) Abstract, line 28, "Furthermore, the kinesin motor activity of KIN-A promotes chromosome alignment in prometaphase and CPC translocation to the central spindle upon anaphase onset." This must be revised - see public review.

We changed this section of the abstract as follows:

‘Furthermore, the ATPase activity of KIN-A promotes chromosome alignment in prometaphase and CPC translocation to the central spindle upon anaphase onset. Thus, KIN-A constitutes a unique ‘two-in-one’ CPC localization module in complex with KIN-B, which directs the CPC to kinetochores (from S phase until metaphase) via its C-terminal tail, and to the central spindle (in anaphase) via its N-terminal kinesin motor domain.’

(3) Line 87-90. The findings by Li et al., 2008 (KIN-A and KIN-B interacting with Aurora B and epistasis analysis) should be introduced more comprehensively in the Introduction section.

We added the following sentence in the introduction:

‘In addition, two orphan kinesins, KIN-A and KIN-B, have been proposed to transiently associate with Aurora BAUK1 during mitosis (Li et al., 2008; Li, 2012).’

(4) Figure 1B. The way the Trypanosoma cell cycle is defined should be briefly explained in the main text, rather than just referring to the figure.

The ‘KN’ annotation of the trypanosome cell cycle is explained in the Figure 1 legend. We now also added a brief description in the main text:

‘We next assessed the localization dynamics of fluorescently tagged KIN-A and KIN-B over the course of the cell cycle (Figs. 1, B-E). T. brucei possesses two DNA-containing organelles, the nucleus (‘N’) and the kinetoplast (‘K’). The kinetoplast is an organelle found uniquely in kinetoplastids, which contains the mitochondrial DNA and replicates and segregates prior to nuclear division. The ‘KN’ configuration serves as a good cell cycle marker (Woodward and Gull, 1990; Siegel et al., 2008).’

(5) Line 118. Throughout the paper, it is not clear why GFP-NLS fusion was used instead of GFP fusion. Please justify the fusion of NLS.

NLS refers to a short ‘nuclear localization signal’ (TGRGHKRSREQ) (Marchetti et al., 2000), which ensures that the ectopically expressed construct is imported into the nucleus. When we previously expressed truncations of KKT2 and KKT3 kinetochore proteins, many fragments did not go into the nucleus presumably due to the lack of an NLS, which prevented us from determining which domains are responsible for their kinetochore localization. We have since then consistently used this short NLS sequence in our inducible GFP fusions in the past without any complications. We added a sentence in the Materials & Methods section under Trypanosome culture: ‘All constructs for ectopic expression of GFP fusion proteins include a short nuclear localization signal (NLS) (Marchetti et al., 2000).’ To avoid unnecessary confusion, we removed ‘NLS’ from the main text and figures.

(6) Line 121, "Unexpectedly". It is not clear why this was unexpected.

To clarify this point, we modified this paragraph in the results section:

‘To our surprise, KIN-A-YFP and GFP-KIN-B exhibited a CPC-like localization pattern identical to that of Aurora BAUK1: Both kinesins localized to kinetochores from S phase to metaphase, and then translocated to the central spindle in anaphase (Figs. 1, C-E). Moreover, like Aurora BAUK1, a population of KIN-A and KIN-B localized at the new FAZ tip from late anaphase onwards (Figs. S1, B and C). This was unexpected, because KIN-A and KIN-B were previously reported to localize to the spindle but not to kinetochores or the new FAZ tip (Li et al., 2008). These data suggest that KIN-A and KIN-B are bona fide CPC proteins in trypanosomes, associating with AuroraAUK1, INCENPCPC1 and CPC2 throughout the cell cycle.’

(7) Line 127-129. Defining homologs and orthologs is tricky - there are many homologs and paralogs of kinesin-like proteins. The method to define the presence or absence of KIN-A/KIN-B homologs should be described in the Materials and Methods section.

Due to the difficulty in defining true orthologs for kinesin-like proteins, we took a conservative approach: reciprocal best BLAST hits. We first searched KIN-A homologs using BLAST in the TriTryp database or using hmmsearch using manually prepared hmm profiles. When the top hit in a given organism found T. brucei KIN-A in a reciprocal BLAST search in T. brucei proteome, we considered the hit as a true ortholog. We modified the Materials and Methods section as below.

‘Searches for homologous proteins were done using BLAST in the TriTryp database (Aslett et al., 2010) or using hmmsearch using manually prepared hmm profiles (HMMER version 3.0; Eddy, 1998). The top hit was considered as a true ortholog only if the reciprocal BLAST search returned the query protein in T. brucei.’

(8) Line 156. For non-experts of Trypanosoma cell biology, it is not clear how the nucleolar localization is defined.

The nucleolus in T. brucei is discernible as a DAPI-dim region in the nucleus.

(9) Fig.2G and Fig.S2F. These data imply that the coiled-coil and C-terminal tail domains of KIN-A/KIN-B are important for anaphase spindle midzone enrichment. However, it is odd that this was not mentioned. This reviewer recommends that the authors quantify the midzone localization data of these constructs and discuss the role of the coiled-coil domains.

One possibility is that KIN-A and KIN-B need to form a complex (via their coiled-coil domains) to localize to the spindle midzone. Another likely possibility, which is discussed in the manuscript, is that N-terminal tagging of KIN-A impairs motor activity. This is supported by the fact that the central spindle localization is also disrupted in full-length GFP-KIN-A. We decided not to provide a quantification for these data due to low sample sizes for some of the constructs (e.g. expression not observed in all cells).

(10) Line 288-289, "pLDDT scores improved significantly for KIN-A CD1 in complex with KKT9:KKT11 (>80) compared to KIN-A CD1 alone (~20) (Figs. S3, A and B)." I can see that pLDDT score is about 20 at KIN-A CD1 from Figs S3A, but the basis of pLDDT > 80 upon inclusion go KKT9:KKT11 is missing.

We added the pLDDT and PAE plots for the AF2 prediction of KIN-A700-800 in complex with KKT9:KKT11 in Fig. S5B.

(11) Fig. 5A. Since there is no supporting biochemical data for KIN-A-KKT9-KKT11 interaction, it is important to assess the stability of AlphaFold-based structural predictions of the KIN-A-KKT9-KKT11 interaction. Are there significant differences among the top 5 prediction results, and do these interactions remain stable after the "simulated annealing" process used in the AlphaFold predictions? Are predicted CD1-interacting regions/amino residues in KKT9 and KKT11 evolutionarily conserved?

See above. The interaction was predicted in all 5 predictions as shown in Fig. S5B. Conservation of the CD1-interacting regions in KKT9 and KKT11 are shown below:

Author response image 2.

KKT9 (residues ~53 – 80 predicted to interact with KIN-A in T. brucei)

Author response image 3.

KKT11 (residues 61-85 predicted to interact with KIN-A in T. brucei)

(12) Line 300, Fig. S5D and E, "failed to localize at kinetochores". From this resolution of the microscopy images, it is not clear if these proteins fail to localize at kinetochores as the KKT and KIN-A310-716 signals overlap. Perhaps, "failed to enrich at kinetochores" is a more appropriate statement.

We changed this sentence according to the reviewer’s suggestion.

(13) Line 309 and Fig 5D and F, "predominantly localized to the mitotic spindle". From this image shown in Fig 5D, it is not clear if KIN-A∆CD1-YFP and Aurora B are predominantly localized to the spindle or if they are still localized to centromeres that are misaligned on the spindle. Without microtubule staining, it is also not clear how microtubules are distributed in these cells. Please clarify how the presence or absence of kinetochore/spindle localization was defined.

As shown in Fig. S5E and S5F, deletion of CD1 clearly impairs kinetochore localization of KIN-A (kinetochores marked by tdTomato-KKT2). Moreover, misalignment of kinetochores, as observed upon expression of the KIN-AG210A rigor mutant, would result in an increase in 2K1N cells and proliferation defects, which is not the case for the KIN-A∆CD1 mutant (Fig. 5H, Fig. S5I). KIN-A∆CD1-YFP appears to localize diffusely along the entire length of the mitotic spindle, whereas we still observe kinetochore-like foci in the rigor mutant. Unfortunately, we do not have suitable antibodies that would allow us to distinguish spindle microtubules from the vast subpellicular microtubule array present in T. brucei and hence need to rely on tagging spindle-associated proteins such as MAP103.

(14) Fig. 5F, G, S5F. Along the same lines, it would be helpful to show example images for each category - "kinetochores", "kinetochores + spindle", and "spindle".

As suggested by the reviewer, we have now included example images for each category (‘kinetochores’, ‘kinetochores + spindle’, ‘spindle’) along with a schematic illustration in Fig. 5F.

(15) Line 332 and Fig. S6A. The experiment may be repeated in the presence of ATP or nonhydrolyzable ATP analogs.

We thank the reviewer for the suggestion. We envisage such experiments for an in-depth follow-up study.

(16) Line 342, "motor activity of KIN-A". Until KIN-A is shown to have motor activity, the result based on the rigor mutant does not show that the motor activity of KIN-A promotes chromosome congression. The result suggests that the ATPase activity of KIN-A is important.

We changed that sentence as suggested by the reviewer.

(17) Line 419 -. The authors base their discussion on the speculation that KIN-A is a plus-end directed motor. Please justify this speculation.

Indeed, the notion that KIN-A is a plus-end directed motor remains a hypothesis, which is based on sequence alignments with other plus-end directed motors and the observation that the KIN-A motor domain is involved in translocation of the CPC to the central spindle in anaphase. We have modified the corresponding section in the discussion as follows:

‘It remains to be investigated whether KIN-A truly functions as a plus-end directed motor. The role of the KIN-B in this context is equally unclear. Since KIN-B does not possess a functional kinesin motor domain, we deem it unlikely that the KIN-A:KIN-B heterodimer moves hand-over-hand along microtubules as do conventional (kinesin-1 family) kinesins. Rather, the KIN-A motor domain may function as a single-headed unit and drive processive plus-end directed motion using a mechanism similar to the kinesin-3 family kinesin KIF1A (Okada and Hirokawa, 1999).’

(18) Line 422-423, "plus-end directed motion using a mechanism similar to kinesin-3 family kinesins (such as KIF1A)." Please cite a reference supporting this statement.

See above. We cited a paper by (Okada and Hirokawa, 1999).

Reviewer #2 (Recommendations For The Authors):

Please provide a quantification of data shown in Figure 2F-H and described in lines 151-166.

We decided not to provide a quantification for these data due to low sample sizes for some of the constructs (e.g. expression not observed in all cells).

It appears as if the paper more or less follows a chronological order of the experiments that were performed before AF multimer enabled the insightful and compelling structural analysis. That is a matter of style, but in some cases, the writing could be updated, shortened, or re-arranged into a more logical order. Concrete examples:

(i) Line 144: "we did not include CPC2 for further analysis in this study" Although CPC2 features at a prominent and interesting position in the predicted structures of the kinetoplastid CPC, shown in later main figures.

We attempted RNAi-mediated depletion of CPC2 using two different shRNA constructs. However, we cannot exclude the possibility that the knockdown of CPC2 was less efficient compared with the other CPC subunits. For this reason, we decided to remove all the data on CPC2 from Fig. S2.

(ii) The work with the KIN-A motor domain only and KIN-A ∆motor domain (Fig 2) begs the question about a more subtle mutation to interfere with the motor domain. Which is ultimately presented in Fig 6. I think that the final paragraph and Figure 6 follow naturally after Figure 2.

We appreciate the suggestion. However, we would like to keep Figure 6 there.

(iii) The high-confidence structural predictions in Fig 3 and Fig 4 are insightful. The XL-MS descriptions that precede them are not so helpful (Fig 3A and 4G and in the text). To emphasize their status as experimental support for the predicted structures, which is very important, it would be good to discuss the XL-MS after presenting the models.

As suggested, we have re-arranged the text and/or figures such that the AF2 predictions are discussed first and the CLMS data are brought in afterwards.

Figure 1A prominently features an arbitrary color code and a lot of protein IDs without a legend. That is not a very convincing start. Figure S1 is more informative, containing annotated protein names and results of the KIN-A and KIN-B IPs. Please improve Figure 1A, for example by presenting a modified version of Figure S1. In all these types of figures, please list both protein names and gene IDs.

We agree with the reviewer that the IP-MS data in Fig. S1 is more informative and hence decided to swap the heatmaps in Fig. 1A and Fig. S1A. We further annotated the heatmap corresponding to the Aurora BAUK1 IP-MS (now presented in Fig. S1) as suggested by the reviewer.

The visualization of the structural predictions is not consistent among figures:

(i) The structure in Fig 4I is important and could be displayed larger. The pLDDT scores, and especially those of the non-displayed models, do not add much information and should not be a main panel. If the authors want to display the pLDDT scores, I recommend a panel (main or supplement) of the structure colored for local prediction confidences, as in Fig 5A.

(ii) In Figure 5A itself, it is hard to follow the chains in general, and KIN-A in particular, since the structure is pLDDT-coloured. Please present an additional panel colored by chain (consistent with Fig 4I, as mentioned above).

(iii) The summarizing diagram, currently displayed as Fig 4J, should be placed after Fig 5A and take the discovered KIN-A - KKT9-11 connection into account. Ideally, it also covers the suspected importance of the motor domain and serves as a summarising diagram.

We thank the reviewer for the constructive comments. For each structure prediction, we now present two images side by side; one coloured by chain and one colored by pLDDT. We recently re-ran AF2 for the full CPC and also for the KKT7N-KKT8 complex, and got improved predictions. Hence some of the models in Fig. 3/S3 and Fig. 4/S4 have been updated accordingly. For the CLMS plots, we also decided to colour the cross-links according to whether the 30 angstrom distance constraints were fulfilled or not in the AF2 prediction. We also increased the size of the structures shown in Fig. 4. Furthermore, we decided to remove the summarizing diagram from Fig. 4 and instead made a new main Fig. 7, which shows a more detailed schematic, which also takes into account the proposed function of the KIN-A motor domain, as suggested by the reviewer, and other points addressed in the Discussion.

The methods section for the structural predictions lacks essential information. Predictions can only be reproduced if the version of AF2 multimer v2.x is specified and key parameters are mentioned.

As suggested, we have added the details in the Materials and Methods section as follows.

‘Structural predictions of KIN-A/KIN-B, KIN-A310-862/KIN-B317-624, CPC1/CPC2/KIN-A300-599/KIN-B 317-624, and KIN-A700-800/KKT9/KKT11 were performed using ColabFold version 1.3.0 (AlphaFold-Multimer version 2), while those of AUK1/CPC1/CPC2/KIN-A1-599/KIN-B, KKT71-261/KKT9/KKT11/KKT8/KKT12, KKT9/KKT11/KKT8/KKT12, and KKT71-261/KKT9/KKT11 were performed using ColabFold version 1.5.3 (AlphaFold-Multimer version 2.3.1) using default settings, accessed via https://colab.research.google.com/github/sokrypton/ColabFold/blob/v1.3.0/AlphaFold2.ipynb and https://colab.research.google.com/github/sokrypton/ColabFold/blob/v1.5.3/AlphaFold2.ipynb.’

Line 121, please explain the "Unexpectedly" by including a reference to the work from Li and colleagues. A statement with some details would be useful, as the difference between both studies appears to be crucial for the novelty of this paper. Alternatively, refer to this being covered in the discussion.

To clarify this point, we modified this paragraph in the results section:

‘To our surprise, KIN-A-YFP and GFP-KIN-B exhibited a CPC-like localization pattern identical to that of Aurora BAUK1: Both kinesins localized to kinetochores from S phase to metaphase, and then translocated to the central spindle in anaphase (Figs. 1, C-E). Moreover, like Aurora BAUK1, a population of KIN-A and KIN-B localized at the new FAZ tip from late anaphase onwards (Figs. S1, B and C). This was unexpected, because KIN-A and KIN-B were previously reported to localize to the spindle but not to kinetochores or the new FAZ tip (Li et al., 2008). These data suggest that KIN-A and KIN-B are bona fide CPC proteins in trypanosomes, associating with AuroraAUK1, INCENPCPC1 and CPC2 throughout the cell cycle.’

Line 285 refers to "conserved" regions in the C-terminal part of KIN-A, referring to Figure 5. Please expand the MSA in Figure 5B to get an idea about the conservation/variation outside CD1 and CD2.

We now present the full MSA for KIN-A proteins in kinetoplastids in Fig. S5A.

Please specify what is meant by Line 367-369 for someone who is not familiar with the work by Komaki et al. 2022. Either clarify in the text or clarify in the text with data to support it.

We updated the corresponding section in the discussion as follows:

‘Komaki et al. recently identified two functionally redundant CPC proteins in Arabidopsis, Borealin Related Interactor 1 and 2 (BORI1 and 2), which engage in a triple helix bundle with INCENP and Borealin using a conserved helical domain but employ an FHA domain instead of a BIR domain to read H3T3ph (Komaki et al., 2022).’

Data presented in Figure S6A, the microtubule co-sedimentation assay, is not convincing since a substantial amount of KIN-A/B is pelleted in the absence of microtubules. Did the authors spin the proteins in BRB80 before the assay to continue with soluble material and reduce sedimentation in the absence of microtubules? If the authors want to keep the wording in lines 331-332, the MT-binding properties of KIN-A and KIN-B need to be investigated in more detail, for example with a titration and a quantification thereof. Otherwise, they should change the text and replace "confirms" with "is consistent with". In any case, the legend needs to be expanded to include more information.

To address the point above, we have added the following text in the legend corresponding to Fig. S6:

‘Microtubule co-sedimentation assay with 6HIS-KIN-A2-309 (left) and 6HIS-KIN-B2-316 (right). S and P correspond to supernatant and pellet fractions, respectively. Note that both constructs to some extent sedimented even in the absence of microtubules. Hence, lack of microtubule binding for KIN-B may be due to the unstable non-functional protein used in this study.’

We have also updated the main text in the results section:

‘We therefore speculated that anaphase translocation of the kinetoplastid CPC to the central spindle may involve the kinesin motor domain of KIN-A. KIN-B is unlikely to be a functional kinesin based on the absence of several well-conserved residues and motifs within the motor domain, which are fully present in KIN-A (Li et al., 2008). These include the P-loop, switch I and switch II motifs, which form the nucleotide binding cleft, and many conserved residues within the α4-L12 elements, which interact with tubulin (Fig. S6A) (Endow et al., 2010). Consistent with this, the motor domain of KIN-B, contrary to KIN-A, failed to localize to the mitotic spindle when expressed ectopically (Fig. S2E) and did not co-sediment with microtubules in our in vitro assay (Fig. S6B).’

Details:

The readability of the pAE plots could be improved by arranging sequences according to their position in the structure. For example in Fig4I, KKT8 could precede KKT12. If it is easy to update this, the authors might want to do so.

We re-ran the AF2 predictions for the KKT7N – KKT8 complex in Fig. 4/S4 and changed the order according to the reviewer’s suggestion (KKT9:KKT11:KKT8:KKT12).

The same paper is referred to as Je Van Hooff et al. 2017 and as Van Hooff et al. 2017

Thank you for pointing this out. We have corrected the citation.

Reviewer #3 (Recommendations For The Authors):

(1) Please state at the end of the introduction/start of the results section that this work was performed in procyclic trypanosomes. Given that the cell cycles of procyclic and bloodstream forms differ, this is important.

We added this information at the end of the introduction:

‘Here, by combining biochemical, structural and cell biological approaches in procyclic form T. brucei, we show that the trypanosome CPC is a pentameric complex comprising Aurora BAUK1, INCENPCPC1, CPC2 and the two orphan kinesins KIN-A and KIN-B.’

(2) Please define NLS at first use (line 118), and for clarity, explain the rationale for using GFP with an NLS.

NLS refers to a short ‘nuclear localization signal’ (TGRGHKRSREQ) (Marchetti et al., 2000), which ensures that the ectopically expressed construct is imported into the nucleus. When we previously expressed truncations of KKT2 and KKT3 kinetochore proteins, many fragments did not go into the nucleus presumably due to the lack of an NLS, which prevented us from determining which domains are responsible for their kinetochore localization. We have since then consistently used this short NLS sequence in our inducible GFP fusions in the past without any complications. We added a sentence in the Materials & Methods section under Trypanosome culture: ‘All constructs for ectopic expression of GFP fusion proteins include a short nuclear localization signal (NLS) (Marchetti et al., 2000).’ To avoid unnecessary confusion, we removed ‘NLS’ from the main text and figures.

(3) Lines 148-150 - it would strengthen this claim if KIN-A/B protein levels were assessed by Western blot.

We now present a Western blot in Fig. S2C, showing that bulk KIN-B levels are clearly reduced upon KIN-A RNAi. The same is true also to some extent for KIN-A levels upon KIN-B RNAi, although this is less obvious, possibly due to the lower efficiency of KIN-B compared to KIN-A RNAi as judged by fluorescence microscopy (quantified in Fig. 2D and 2E).

(4) Line 253 - the text mentions the removal of both KKT9 and KKT11, which is not consistent with the figure (Fig 4H) - do you mean the removal of either KKT9 or KKT11?

Yes, we thank the reviewer for pointing out this mistake in the text, which has now been corrected.

(5) Line 337 - please include a reference for the G209A ATPase-defective rigor mutant - has this been shown to result in KIN-A being inactive previously?

Please see above our answer in public review.

(6) It is not always obvious when fluorescent fusion proteins are being expressed endogenously or ectopically, or when they are being expressed in an RNAi background or not without tracing the cell lines in Table S1 - please ensure this is clearly stated throughout the manuscript.

We now made sure that this is clearly stated in the main text as well as in the figure legends.

(7) Line 410 - 'KIN-A C-terminal tail is stuffed full of conserved CDK1CRK3 sites' - what does 'stuffed full' really mean (this is rather imprecise) and what are the consensus sites - are these CDK1 consensus sites that are assumed to be conserved for CRK3? I'm not aware of consensus sites for CRK3 having been determined, but if they have, this should be referenced.

We have modified the corresponding section in the discussion as follows:

‘In support of this, the KIN-A C-terminal tail harbours many putative CRK3 sites (10 sites matching the minimal S/T-P consensus motif for CDKs) and is also heavily phosphorylated by Aurora BAUK1 in vitro (Ballmer et al. 2024). Finally, we speculate that the interaction of KIN-A motor domain with microtubules, coupled to the force generating ATP hydrolysis and possibly plus-end directed motion, eventually outcompetes the weakened interactions of the CPC with the kinetochore and facilitates the extraction of the CPC from chromosomes onto spindle microtubules during anaphase. Indeed, deletion of the KIN-A motor domain or impairment of its motor function through N-terminal GFP tagging causes the CPC to be trapped at kinetochores in anaphase. Central spindle localization is additionally dependent on the ATPase activity of the KIN-A motor domain as illustrated by the KIN-A rigor mutant.’

(8) Lines 412-416: this proposal is written rather definitively - given no motor activity has been demonstrated for KIN-A, please make clear that this is still just a theory.

See above.

(9) Fig 1: KKT2 is not highlighted in Fig 1A - given this has been used for colocalization in Fig 1C-E, was it recovered, and if not, why not? Fig 1B-E: the S phase/1K1N terminology is somewhat misleading. Not all S phase cells will have elongated kinetoplasts - usually an asterisk is used to signify replicated DNA, not kinetoplast shape. If it is to be used here for elongation, then for consistency, N should be used for G2/mitotic cells.

Fig. 1A (now Fig. S1A) only shows the tip 30 hits. KKT2 was indeed recovered with Aurora BAUK1 (see Table S2) and is often used as a kinetochore marker in trypanosomes by our lab and others since the signal of fluorescently tagged KKT2 is relatively bright and KKT2 localizes to centromeres throughout the cell cycle.

(10) A general comment for all image figures is that these do not have accompanying brightfield images and it is therefore difficult to know where the cell body is, or sometimes which nuclei and kinetoplasts belong to which cell where DNA from more than one cell is within the image. It would be beneficial if brightfield images could be added, or alternatively, the cell outlines were traced onto DAPI or merged images. Also, brightfield images would allow the stage of cytokinesis (pre-furrowing/furrowing/abscission) in anaphase cells to be determined.

Since this study primarily addresses the recruitment mechanism of the CPC to kinetochores and to the central spindle from S phase to metaphase and in anaphase, respectively, and CPC proteins are not observed outside of the nucleus during these cell cycle stages, we did not present brightfield images in the figures. However, this point is particularly valid for discerning the localization of KIN-A and KIN-B to the new FAZ tip from late anaphase onwards. Hence, we acquired new microscopy data for Fig. S1B and S1C, which now includes phase contrast images, and have chosen representative cells in late anaphase and telophase. We hope that the signal of Aurora BAUK1, KIN-A and KIN-B at the anterior end of the new FAZ can be now distinguished more clearly.

(11) Fig 2A: legend should state that the micrographs show the localisation of the proteins within the nucleus as whole cells are not shown. 2C: can INCENP not be split into 2 lines - the 'IN' looks like 1N at first glance, which is confusing.

We have applied the suggested change in Fig. 2.

(12) Fig 3 (and other AF2 figures): Could the lines for satisfied & not satisfied in the key be thicker so they more closely resemble the lines in the figure and are less likely to be confused with the disordered regions of the CPC components?

We have now made those lines thicker.

(13) Why were different E value thresholds used in Fig 3 and Fig 4?

The CLMS data in Fig. 3 and Fig. 4 now both use the same E value threshold of E-3 (previously E-4 was used in Fig. 4). To determine a sensible significance threshold, we included some yeast protein sequences (‘false positives’) in the database used in pLink2 for identification of crosslinked peptides. Note that we recently also re-ran AF2 for the full CPC and for the KKT7N-KKT8 complex and got improved predictions. Hence some of the models in Fig. 3/S3 and Fig. 4/S4 have been updated accordingly. For the CLMS plots, we also decided to colour the cross-links according to whether the 30 angstrom distance constraints were fulfilled or not in the AF2 prediction.

(14) Fig 4H legend - please give the expected sizes of these recombinant proteins & check the 3rd elution panel (see public review comments).

See above response in public review.

(15) Fig 4I - please explain what the colours of the PAE plot and the values in the key signify, as well as how the Scored Residue values are arrived at. Please also define the pIDDT in the legend.

We have cited DeepMind’s 2021 methods paper, in which the outputs of AlphaFold are explained in detail. We also added a short description of the pLDDT and PAE scores and the corresponding colour coding in the legends of Fig. 3 and Fig. 4, respectively.

From figure 3 legend:

‘(B) Cartoon representation showing two orientations of the trypanosome CPC, coloured by protein on the left (Aurora BAUK1: crimson, INCENPCPC1: green, CPC2: cyan, KIN-A: magenta, and KIN-B: yellow) or according to their pLDDT values on the right, assembled from AlphaFold2 predictions shown in Figure S3. The pLDDT score is a per-residue estimate of the confidence in the AlphaFold prediction on a scale from 0 – 100. pLDDT > 70 (blue, cyan) indicates a reasonable accuracy of the model, while pLDDT < 50 (red) indicates a low accuracy and often reflects disordered regions of the protein (Jumper et al., 2021). BS3 crosslinks in (B) were mapped onto the model using PyXlinkViewer (blue = distance constraints satisfied, red = distance constraints violated, Cα-Cα Euclidean distance threshold = 30 Å) (Schiffrin et al., 2020).’

From Figure 4 legend:

‘(G) AlphaFold2 model of the KKT7 – KKT8 complex, coloured by protein (KKT71-261: green, KKT8: blue, KKT12: pink, KKT9: cyan and KKT11: orange) (left) and by pLDDT (center). BS3 crosslinks in (H) were mapped onto the model using PyXlinkViewer (Schiffrin et al., 2020) (blue = distance constraints satisfied, red = distance constraints violated, Cα-Cα Euclidean distance threshold = 30 Å). Right: Predicted Aligned Error (PAE) plot of model shown on the left (rank_2). The colour indicates AlphaFold’s expected position error (blue = low, red = high) at the residue on the x axis if the predicted and true structures were aligned on the residue on the y axis (Jumper et al., 2021).’

(16) Fig 6 legend - Line 730 should say (F) not (C).

Thank you for pointing out this typo.

(17) Fig S1A - a key is missing for the colours. Fig S1B/C - cell outlines or a brightfield image are really needed here - see earlier comment. Fig S1D - there doesn't seem to be a method for how this tree was generated.

See above response in public review regarding Fig. S1A and S1B/C. The tree in Fig. S1D is based on (Butenko et al., 2020).

(18) Fig S2: A: how was protein knockdown validated (especially for CPC2 where there was little obvious phenotype)? Fig S2B: the y-axis should read proportion of cells, not percentage. Fig S2E - NLS should be labelled.

Thank you for pointing out the mistake in the labelling.

(19) Fig S3: PAE plots should be labelled with protein names, not A-E. Similarly, the pIDDT plots should be labelled as in Fig 4I.

We have corrected the labelling in Fig. S3.

(20) Fig S5A-D - cell cycle stage labels are missing from images.

Thank you for pointing out the missing cell cycle stage labels.

Addition by editor:

In line 126 the statement that KIN-A and KIN-B "associate with Aurora-AUK1, INCENP-CPC1 and CPC2 throughout the cell cycle" seems too strong. There is no direct evidence for this. Please re-phrase as "likely associate" or "suggest... that ... may...".

We have modified that sentence according to the editor’s suggestion.

References:

Akiyoshi, B., and K. Gull. 2014. Discovery of Unconventional Kinetochores in Kinetoplastids. Cell. 156. doi:10.1016/j.cell.2014.01.049.

Butenko, A., F.R. Opperdoes, O. Flegontova, A. Horák, V. Hampl, P. Keeling, R.M.R. Gawryluk, D. Tikhonenkov, P. Flegontov, and J. Lukeš. 2020. Evolution of metabolic capabilities and molecular features of diplonemids, kinetoplastids, and euglenids. BMC Biology 2020 18:1. 18:1–28. doi:10.1186/S12915-020-0754-1.

Cormier, A., D.G. Drubin, and G. Barnes. 2013. Phosphorylation regulates kinase and microtubule binding activities of the budding yeast chromosomal passenger complex in vitro. J Biol Chem. 288:23203–23211. doi:10.1074/JBC.M113.491480. Endow, S.A., F.J. Kull, and H. Liu. 2010. Kinesins at a glance. J Cell Sci. 123:3420. doi:10.1242/JCS.064113.

Fink, S., K. Turnbull, A. Desai, and C.S. Campbell. 2017. An engineered minimal chromosomal passenger complex reveals a role for INCENP/Sli15 spindle association in chromosome biorientation. J Cell Biol. 216:911–923. doi:10.1083/JCB.201609123.

van der Horst, A., M.J.M. Vromans, K. Bouwman, M.S. van der Waal, M.A. Hadders, and S.M.A. Lens. 2015. Inter-domain Cooperation in INCENP Promotes Aurora B Relocation from Centromeres to Microtubules. Cell Rep. 12:380–387. doi:10.1016/J.CELREP.2015.06.038.

Ishii, M., and B. Akiyoshi. 2020. Characterization of unconventional kinetochore kinases KKT10/19 in Trypanosoma brucei. J Cell Sci. doi:10.1242/jcs.240978.

Jeyaprakash, A.A., C. Basquin, U. Jayachandran, and E. Conti. 2011. Structural Basis for the Recognition of Phosphorylated Histone H3 by the Survivin Subunit of the Chromosomal Passenger Complex. Structure. 19:1625–1634. doi:10.1016/J.STR.2011.09.002.

Jeyaprakash, A.A., U.R. Klein, D. Lindner, J. Ebert, E.A. Nigg, and E. Conti. 2007. Structure of a Survivin–Borealin–INCENP Core Complex Reveals How Chromosomal Passengers Travel Together. Cell. 131. doi:10.1016/j.cell.2007.07.045.

Jumper, J., R. Evans, A. Pritzel, T. Green, M. Figurnov, O. Ronneberger, K. Tunyasuvunakool, R. Bates, A. Žídek, A. Potapenko, A. Bridgland, C. Meyer, S.A.A. Kohl, A.J. Ballard, A. Cowie, B. Romera-Paredes, S. Nikolov, R. Jain, J. Adler, T. Back, S. Petersen, D. Reiman, E. Clancy, M. Zielinski, M. Steinegger, M. Pacholska, T. Berghammer, S. Bodenstein, D. Silver, O. Vinyals, A.W. Senior, K. Kavukcuoglu, P. Kohli, and D. Hassabis. 2021. Highly accurate protein structure prediction with AlphaFold. Nature 2021 596:7873. 596:583–589. doi:10.1038/s41586-021-03819-2.

Kang, J.S., I.M. Cheeseman, G. Kallstrom, S. Velmurugan, G. Barnes, and C.S.M. Chan. 2001. Functional cooperation of Dam1, Ipl1, and the inner centromere protein (INCENP)-related protein Sli15 during chromosome segregation. J Cell Biol. 155:763–774. doi:10.1083/JCB.200105029.

Klein, U.R., E.A. Nigg, and U. Gruneberg. 2006. Centromere targeting of the chromosomal passenger complex requires a ternary subcomplex of Borealin, Survivin, and the N-terminal domain of INCENP. Mol Biol Cell. 17:2547–2558. doi:10.1091/MBC.E05-12-1133.

Komaki, S., E.C. Tromer, G. De Jaeger, N. De Winne, M. Heese, and A. Schnittger. 2022. Molecular convergence by differential domain acquisition is a hallmark of chromosomal passenger complex evolution. Proc Natl Acad Sci U S A. 119. doi:10.1073/PNAS.2200108119/-/DCSUPPLEMENTAL.

Li, Z. 2012. Regulation of the Cell Division Cycle in Trypanosoma brucei. Eukaryot Cell. 11:1180. doi:10.1128/EC.00145-12.

Li, Z., J.H. Lee, F. Chu, A.L. Burlingame, A. Günzl, and C.C. Wang. 2008. Identification of a Novel Chromosomal Passenger Complex and Its Unique Localization during Cytokinesis in Trypanosoma brucei. PLoS One. 3. doi:10.1371/journal.pone.0002354.

Mackay, A.M., D.M. Eckley, C. Chue, and W.C. Earnshaw. 1993. Molecular analysis of the INCENPs (inner centromere proteins): separate domains are required for association with microtubules during interphase and with the central spindle during anaphase. J Cell Biol. 123:373–385. doi:10.1083/JCB.123.2.373.

Marchetti, M.A., C. Tschudi, H. Kwon, S.L. Wolin, and E. Ullu. 2000. Import of proteins into the trypanosome nucleus and their distribution at karyokinesis. J Cell Sci. 113 ( Pt 5):899–906. doi:10.1242/JCS.113.5.899.

Nakajima, Y., A. Cormier, R.G. Tyers, A. Pigula, Y. Peng, D.G. Drubin, and G. Barnes. 2011. Ipl1/Aurora-dependent phosphorylation of Sli15/INCENP regulates CPC-spindle interaction to ensure proper microtubule dynamics. J Cell Biol. 194:137–153. doi:10.1083/JCB.201009137.

Noujaim, M., S. Bechstedt, M. Wieczorek, and G.J. Brouhard. 2014. Microtubules accelerate the kinase activity of Aurora-B by a reduction in dimensionality. PLoS One. 9. doi:10.1371/JOURNAL.PONE.0086786.

Okada, Y., and N. Hirokawa. 1999. A processive single-headed motor: Kinesin superfamily protein KIF1A. Science (1979). 283:1152–1157. doi:10.1126/SCIENCE.283.5405.1152.

Rice, S., A.W. Lin, D. Safer, C.L. Hart, N. Naber, B.O. Carragher, S.M. Cain, E. Pechatnikova, E.M. Wilson-Kubalek, M. Whittaker, E. Pate, R. Cooke, E.W. Taylor, R.A. Milligan, and R.D. Vale. 1999. A structural change in the kinesin motor protein that drives motility. Nature 1999 402:6763. 402:778–784. doi:10.1038/45483.

Sablin, E.P., F.J. Kull, R. Cooke, R.D. Vale, and R.J. Fletterick. 1996. Crystal structure of the motor domain of the kinesin-related motor ncd. Nature 1996 380:6574. 380:555–559. doi:10.1038/380555a0.

Samejima, K., M. Platani, M. Wolny, H. Ogawa, G. Vargiu, P.J. Knight, M. Peckham, and W.C. Earnshaw. 2015. The Inner Centromere Protein (INCENP) Coil Is a Single α-Helix (SAH) Domain That Binds Directly to Microtubules and Is Important for Chromosome Passenger Complex (CPC) Localization and Function in Mitosis. J Biol Chem. 290:21460–21472. doi:10.1074/JBC.M115.645317.

Schiffrin, B., S.E. Radford, D.J. Brockwell, and A.N. Calabrese. 2020. PyXlinkViewer: A flexible tool for visualization of protein chemical crosslinking data within the PyMOL molecular graphics system. Protein Sci. 29:1851–1857. doi:10.1002/PRO.3902.

Author Response

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

Reviewer #1 (Public Review):

Summary:

This study investigated behavioural performance on a competing speech task and neural attentional filtering over the course of two years in a group of middle-aged to older adults. Neural attentional filtering was quantified using EEG by comparing neural envelope tracking to an attended vs. an unattended sentence. This dataset was used to examine the stability of the link between behavior and neural filtering over time. They found that neural filtering and behavior were correlated during each measurement, but EEG measures at the first time point did not predict behavioural performance two years later. Further, while behavioural measures showed relatively high test-retest reliability, the neural filtering reliability was weak with an r-value of 0.21. The authors conclude that neural tracking-based metrics have limited ability to predict longitudinal changes in listening behavior.

Strengths:

This study is novel in its tracking of behavioural performance and neural envelope tracking over time, and it includes an impressively large dataset of 105 participants. The manuscript is clearly written.

Weaknesses:

The weaknesses are minor, primarily concerning how the reviewers interpret their data. Specifically, the envelope tracking measure is often quite low, close to the noise floor, and this may affect testretest reliability. Furthermore, the trajectories may be affected by accelerated age-related declines that are more apparent in neural tracking than in behaviour.

We thank the reviewer for their supportive assessment of our work. We describe in detail how we have addressed the two main concerns raised here—neural filtering’s low test-retest reliability and differences in age-related behavioural vs. neural change—in our response to the more detailed recommendations below.

To briefly summarise here:

(1) In Figure 5, we now illustrate more transparently how the employed structural equation framework helps to overcome the issue of low test-retest reliability of neural filtering as originally reported.

(2) We include two additional control analyses, one of which relates neural tracking of attended speech (featuring a moderately high T1–T2 correlation of r = .64 even outside of latent modelling) to behavioural change. Importantly, this analysis provides critical empirical support for the apparent independence of neural and behavioural trajectories.

(3) We more clearly describe how the latent-variable modelling strategy accounts for differences in age-related change along the neural and behavioural domain. Moreover, the results of the of 18 additional control analysis also suggest that the absence of a change-change relationship is not primarily due to differential effects of age on brain and behaviour.

Reviewer #1 (Recommendations For The Authors):

1) Figure 3:

Does the 70-year range reach a tipping point?

Is that why neural filtering drops dramatically in this age group, whereas the other groups do not change or increase slightly?

This can also be seen with behavioral accuracy to a lesser extent. Perhaps test-retest reliability is affected by accelerated age-related declines in older listeners, as was found for envelope tracking measures in Decruy et al. 2019.

We agree with the reviewer that at first glance the data seem to suggest a critical tipping point in the age range above 70 years. It is important to emphasize, however, that the four age bins were not based on equal number of data points. In fact, the >70 age group included the fewest participants, leading to a less reliable estimate of change. Together with the known observation of increasing interindividual differences with increasing age, the results do not allow for any strong conclusions regarding a potential tipping point. For the same reasons, we used the four age bins for illustrative purposes, only, and did not include them in any statistical modelling.

We did however include chronological age as a continuous predictor in latent change score modelling. Here, we modelled its influence on participants’ T1 neural and behavioural status, as well as its effect on their respective change, thereby accounting for any differential (linear) effects of age on neural vs. behavioural functioning and its change.

On p.14 of the revised manuscript, we now state more clearly that the latent change score model did in fact account for the potential influence of age on the change-related relationships:

"In line with our hypotheses, we modelled the longitudinal impact of T1 neural functioning on the change in speed, and tested for a change-change correlation. Since the analyses conducted up to this point have either directly shown or have suggested that longitudinal change per domain may be affected by age, we included individuals’ age as a time-invariant covariate in the final model. We modelled the influence of age on neural and behavioural functioning at T1 but also on individual change per domain. By accounting for linear effects of age on longitudinal change, we also minimize its potential impact on the estimation of change-change relationship of interest. Note that we refrained from fitting separate models per age group due to both limited and different number of data points per age group."

2) Would good test-retest reliability be expected when the actual values of envelope tracking for attended vs. unattended speech are so low? The investigators address this by including measurement errors in the models, but I am not certain this kind adequately deals with envelope tracking values that are close to the noise floor.

We thank the reviewer for this comment. We addressed the concerns regarding the low re-test reliability of our neural-attentional metric (and its potential impact on observing a systematic changechange relationship) in two separate ways.

The major outcome of these tests is that low re-test reliability of neural tracking is (i) not generally true, and (ii) is not the cause of the main finding, i.e., a low or absent correlations of behavioural vs. neural changes over time.

In more detail, to show how latent change score modelling improves test-retest reliability by explicitly modelling measurement error, we first extracted and correlated T1 and T2 latent factors scores from the respective univariate models of neural filtering and response speed.

Indeed, at the latent level, the correlation of T1–T2 neural filtering was moderately high at r = .65 (compared to r = .21 at the manifest level). The correlation of T1–T2 response speed was estimated as r = .75 (compared to r = .71).

Figure 5A, reproduced below for the reviewer’s convenience, now includes insets quantifying these latent-level correlations over time.

Author response image 1.

Modelling of univariate and bivariate change. A Univariate latent change score models for response speed (left) and neural filtering (right). All paths denoted with Latin letters refer to freely estimated but constrained to be equal parameters of the respective measurement models. Greek letters refer to freely estimated parameters of the structural model. Highlighted in black is the estimated mean longitudinal change from T1 to T2. Scatterplots in the top left corner illustrate how capturing T1 and T2 neural and behavioural functioning as latent factors improves their respective test-retest reliability. B Latent change score model (LCSM) relating two-year changes in neural filtering strength to changes in response speed. Black arrows indicate paths or covariances of interest. Solid black arrows reflect freely estimated and statistically significant effects, dashed black arrows reflect non-significant effects. All estimates are standardised. Grey arrows show paths that were freely estimated or fixed as part of the structural model but that did not relate to the main research questions. For visual clarity, manifest indicators of the measurement model and all symbols relating to the estimated mean structure are omitted but are identical to those shown in panel A. p<.001, p<.01, p<.05, p=.08. C Scatterplots of model-predicted factor scores that refer to the highlighted paths in panel B. Top panel shows that baseline-level neural filtering did not predict two-year change in behavioural functioning, bottom panel shows the absence of a significant change-change correlation.

Second, we ran a control analysis that includes the neural tracking of attended speech in selectiveattention trials rather than the neural filtering index averaged across all trials. The results are shown as part of a new main figure (and two new supplemental figures) reproduced below (see in particular Figure 6, panels C and D).

This analysis serves two purposes: On the one hand, it allows for a more direct evaluation of the actual strength of neural speech tracking as quantified by the Pearson’s correlation coefficient. Note that these individual averages fall well within the to be expected range given that the neural tracking estimates are based on relatively short sentences (i.e., duration of ~2.5 sec) (O’Sullivan et al., 2014).

On the other hand, neural tracking of attended speech showed a moderately high, r = .64, T1–T2 correlation even outside of latent modelling. Note that the magnitude of this T1–T2 reliability is close to the short-term test-retest reliability recently reported by Panela et al. (2023). Still, when including neural tracking of attended speech in the bivariate model of change, the change-change correlation with response speed was now estimated as close to 0 (𝜙 = –.03, n.s). This observation suggests that manifest-level high re-test reliability does not necessarily improve chances of observing a significant change-change correlation.

Lastly, we would like to point out that these bivariate model results also help to shed light on the question of whether non-linear effects of age on neural / behavioural change may affect the chance of observing a systematic change-change relationship. As shown in Fig. 6C, for neural tracking of attended speech, we observed a fairly consistent longitudinal increase across age groups. Yet, as detailed above, the change-change correlation was virtually absent.

In sum, these new results provide compelling evidence for the absence of a systematic changechange relationship.

The respective control analysis results section reads as follows, and is accompanied by Figure 6 reproduced below:

"Control analyses: The weak correlation of behavioural and neural change is robust against different quantifications of neural filtering

Taken together, our main analyses revealed that inter-individual differences in behavioural change could only be predicted by baseline age and baseline behavioural functioning, and did not correlate with contemporaneous neural changes.

However, one could ask in how far core methodological decisions taken in the current study, namely our focus on (i) the differential neural tracking of relevant vs. irrelevant speech as proxy of neural filtering, and (ii) on its trait-level characterization that averaged across different spatial-attention conditions may have impacted these results. Specifically, if the neural filtering index (compared to the neural tracking of attended speech alone) is found to be less stable generally, would this also impact the chances of observing a systematic change-change relationship? Relatedly, did the analysis of neural filtering across all trials underestimate the effects of interest?

To evaluate the impact of these consideration on our main findings, we conducted two additional control analyses: First, we repeated the main analyses using the neural filtering index (and response speed) averaged across selective-attention trials, only. Second, we repeated the main analyses using the neural tracking of attended speech, again averaged across selective-attention trials, only.

As shown in Figure 6, taken together, the control analyses provide compelling empirical support for the robustness of our main results: Linking response speed and neural filtering under selective attention strengthened their relationship at T1 (𝜙 = .54, SE = .15, Dc2(df = 1) = 2.74, p = .1; see. Fig 6B) but did not yield any significant effects for the influence of T1 neural filtering on behavioural change (β = .13, SE = .21, Dc2(df = 1) = .43, p = .51), or for the relationship of neural and behavioural change (𝜙 = .26, SE = .14, Dc2(df = 1) = 3.1, p = .08; please note the close correspondence to path estimates reported in Fig. 5). The second control analysis revealed a substantially higher manifest-level test-retest reliability of neural tracking of attended speech (r = .65, p<.001; Fig. 6C) compared to that of the neural tracking index. However, when linked to longitudinal changes in response speed, this analysis provided even less evidence for systematic change-related relationships: Baseline-levels of attended-speech tracking did not predict future change in response speed (β = .18, SE = .11, Dc2(df = 1) = 2.73, p = .10), and changes in neural and behavioural functioning occurred independently of one another (𝜙 = –.03, SE = .12, Dc2(df = 1) = .06, p = .81).

In sum, the two control analyses provide additional empirical support for the results revealed by our main analysis."

Author response image 2.

Control analyses corroborate the independence of neural and behavioural trajectories under selective attention. Cross-sectional and longitudinal change in neural filtering (A) and neural tracking of attended speech (C) averaged across selective-attention trials, only. Coloured vectors (colour-coding four age groups for illustrative purposes, only) in the left subpanels show individual T1–T2 change along with the cross-sectional trend plus 95% confidence interval (CI) separately for T1 (dark grey) and T2 (light grey). Top right, correlation of T1 and T2 as measure of test-retest reliability along with the 45° line (grey) and individual data points (black circles). Bottom right, mean longitudinal change per age group and grand mean change (grey). B, D Latent change score model (LCSM) relating two-year changes in neural filtering (B) /neural tracking (D) strength to changes in response speed. Black arrows show the paths or covariances of interest that were freely estimates, grey arrows show paths that were freely estimated or fixed as part of the structural model but did not relate to the main research questions. Solid arrows indicate statistically significant effects, dashed arrows reflect nonsignificant paths. All estimates are standardised. p<.001, p<.01, p<.05.

3) The authors conclude that the temporal instability of the neural filtering measure precludes its use for diagnostic/therapeutic intervention. I agree that test-retest reliability is needed for a clinical intervention. However, given the relationship with behavior at a specific point in time, would it not be a possible target for intervention to improve performance? Even if there are different trajectories, an individual may benefit from enhanced behavioral performance in the present.

We thank the reviewer for this comment. We would agree that the observation of robust betweensubject (or even more desirable: within-subject) brain–behaviour relationships is a key desideratum in identifying potential interventional targets. At the same time, we would argue that the most direct way of evaluating a neural signature’s translational potential is by focusing on how it predicts or is linked to individual change. In revising both the Introduction and Discussion section, we hope to now better motivate our reasoning.

Other minor comments:

4) Lines 106-107 What is the basis for the prediction regarding neural filtering?

In our previous analysis of T1 data (Tune et al., 2021), we found inter-individual differences in neural filtering itself, and also in its link to behaviour, to be independent of chronological age and hearing loss. On the basis of these results, we did not expect any systematic decrease or increase in neural filtering over time.<br /> We rephrased the respective sentence as follows:

Since we previously observed inter-individual differences in neural filtering to be independent of age and hearing status, we did not expect any systematic longitudinal change in neural filtering.

5) Line 414: Replace "relevant" with "relevance".

Thank you, this has been corrected.

6) What was the range of presentation levels? Stimuli presented at 50 dB above individual sensation level could result in uncomfortably loud levels for people with mild to moderate hearing loss.

Unfortunately, we didn’t have the means to estimate the precise dB SPL level at which our stimuli were presented. Due to the use of in-ear headphones, we did not aim to measure the exact sound pressure level of presentation but instead ensured that even if stimuli were presented at the maximally possible intensity given our hardware, this would not result in subjectively uncomfortably loud stimulus presentation levels. The described procedure estimated per individual how far the maximal sound pressure level needed to be attenuated to arrive at a comfortable and easy-tounderstand presentation level.

Reviewer #2 (Public Review):

Summary:

This study examined the longitudinal brain-behaviour link between attentional neural filtering and listening behaviour among a sample of aging individuals. The results based on the latent change score modeling showed that neither attentional neural filtering at T1 nor its T1-T2 change predicted individual two-year listening performance change. The findings suggest that neural filtering and listening behaviour may follow independent developmental trajectories. This study focuses on an interesting topic and has the potential to contribute a better understanding of the neurobiological mechanisms of successful communication across the lifespan.

Strengths:

Although research suggests that speech comprehension is neurally supported by an attentionguided filter mechanism, the evidence of their causal association is limited. This study addresses this gap by testing the longitudinal stability of neural filtering as a neural mechanism upholding listening performance, potentially shedding light on translational efforts aiming at the preservation of speech comprehension abilities among aging individuals.

The latent change score modeling approach is appropriately used as a tool to examine key developmental questions and distinguish the complex processes underlying lifespan development in brain and behaviour with longitudinal data.

Weaknesses:

Although the paper does have strengths in principle, the weaknesses of the paper are that the findings are merely based on a single listening task. Since both neural and behavioral indicators are derived from the same task, the results may be applicable only to this specific task, and it is difficult to extrapolate them to cognitive and listening abilities measured by the other tasks. Therefore, more listening tasks are required to comprehensively measure speech comprehension and neural markers.

The age span of the sample is relatively large. Although no longitudinal change from T1 to T2 was found at the group-level, from the cross-sectional and longitudinal change results (see Figure 3), individuals of different age groups showed different development patterns. Particularly, individuals over the age of 70 show a clear downward trend in both neural filtering index and accuracy. Therefore, different results may be found based on different age groups, especially older groups. However, due to sample limitations, this study was unable to examine whether age has a moderating effect on this brain-behaviour link.

In the Dichotic listening task, valid and invalid cues were manipulated. According to the task description, the former could invoke selective attention, whereas the latter could invoke divided attention. It is possible that under the two conditions, the neural filtering index may reflect different underlying cognitive processes, and thus may differ in its predictive effect on behavioral performance. The author could perform a more in-depth data analysis on indicators under different conditions.

We thank the reviewer for their critical yet positive assessment of our work that also appreciates its potential to further our understanding of key determinants of successful communication in healthy aging. Please also see our more in-depth responses to the detailed recommendations that relate to the three main concern raised above.

Regarding the first concern of the reviewer about the limited generalizability of our brain–behaviour results, we would argue that there are two sides to this argument.

On the one hand, the results do not directly speak to the generalizability of the observed complex brain–behaviour relationships to other listening tasks. This may be perceived as a weakness. Unfortunately, as part of our large-scale projects, we did not collect data from another listening task suitable for such a generalization test. Using any additional cognitive tests would shift the focus away from the goal of understanding the determinants of successful communication, and rather speak more generally to the relationship of neural and cognitive change.

On the other hand, we would argue the opposite, namely that the focus on the same listening task is in fact a major strength of the present study: The key research questions were motivated by our timepoint 1 findings of a brain-behaviour link both at the within-subject (state) and at the between subject (trait) level (Tune et al., 2021). Notably, in the current study, we show that both, the state- and the trait-level results, were replicated at timepoint 2. This observed stability of results provides compelling empirical evidence for the functional relevance of neural filtering to the listening outcome and critically sets the stage for the inquiry into the complex longitudinal change relationships. We now spell this out more clearly in the Introduction and the Discussion.

Here, we briefly summarise how we have addressed the two remaining main concerns.

(1) Please refer to our response R1’s comment #1 on the influence of (differential) age effects on brain and behaviour. These effects were in fact already accounted for by our modelling strategy which included the continuously (rather than binned by age group) modelled effect of age. We now communicate this more clearly in the revised manuscript.

(2) We added two control analyses, one of which replicated the main analysis using selective attention trials, only. Critically, as shown in Figure 6, while the strength of the relationship of neural filtering and behaviour at a given timepoint increased, the key change-related relationships of interest remained not only qualitatively unchanged, but resulted in highly similar quantitative estimates.

Reviewer #2 (Recommendations For The Authors):

1) Theoretically, the relationship between brain and behavior may not be just one-way, but probably bi-directional. In this study, the authors only considered the unidirectional predictive effect of neural filtering on changes in listening task performance. However, it is possible that lower listening ability may limit information processing in older adults, which may lead to a decline in neural filtering abilities. The authors may also consider this theoretical hypothesis.

We thank the reviewer for this comment. While we did not have any specific hypotheses about influence of the behavioural state at timepoint 1 on the change in neural filtering, we ran control analysis that freely estimates the respective path (rather than implicitly assuming it to be 0). However, the results did not provide evidence for such a relationship. We report the results on p. 14 of the revised manuscript:

"We did not have any a priori hypotheses on the influence of T1 speed on the individual T1–T2 change in neural filtering. Still in a control analysis that freely estimated the respective path, we found that an individual’s latent T1 level of response speed was not predictive of the ensuing latent T1–T2 change in neural filtering (β = –.11, SE = .21, Dc2(df = 1) = .31, p = .58)."

2) The necessity of exploring the longitudinal relationship between attentional neural filtering and listening behaviour needs to be further clarified. That is, why choose attentional filtering (instead of the others) as an indicator to predict listening performance?

We are not quite certain we understood which ‘other’ metrics the reviewer was referring to here exactly. But we would like to reiterate our argument from above: we believe that focusing on neural and behavioural metrics that are (i) derived from the same task, and (ii) were previously shown to be linked at both the trait- and state-level provided strong empirical ground for our inquiries into their longitudinal change-related relationships.

Please note that we agree that the neural filtering index as a measure of attention-guided neural encoding of relevant vs. irrelevant speech signals is only one potential candidate neural measure but one that was clearly motivated by previous results. Nevertheless, in the revised manuscript we now also report on the relationship of neural tracking of attended speech and listening performance (see also our response to the reviewer’s comment #5 below).

Apart of this, by making the entire T1–T2 dataset openly available, we invite researchers to conduct any potential follow-up analyses focused on metrics not reported here.

3) Regarding the Dichotic listening task, further clarification is needed.

(1) The task procedure and key parameters need to be supplemented.

We have added a new supplemental Figure S6 which details the experimental design and procedure. We have also added further listening task details to the Methods section on p.23:

At each timepoint, participants performed a previously established dichotic listening task20. We provide full details on trial structure, stimulus construction, recording and presentation in our previously published study on the first (N = 155) wave of data collection (but see also Fig. S6)12.

In short, in each of 240 trials, participants listened to two competing, dichotically presented five-word sentences spoken by the same female speaker. They were probed on the sentence-final noun in one of the two sentences. Participants were instructed to respond within a given 4 s time window beginning with the onset of a probe screen showing four alternatives. They were not explicitly instructed to respond as quickly as possible. The probe screen showed four alternative words presented either on the left or right side of the screen, indicating the probed ear. Two visual cues preceded auditory presentation (…)

We also note that the task and key parameters have been published additionally in (Tune et al., 2021) and Alavash et al. (2019). We have made sure these citations are placed prominently at the beginning of the methods section.

Author response image 3.

Experimental design and procedure.

(2) Prior to the task, were the participants instructed to respond quickly and correctly? Was there a speed-accuracy trade-off? Was it possible to consider an integrated ACC-RT indicator?

We instructed participants to respond within a 4-sec time window following the response screen onset but we did not explicitly instruct them to respond as quickly as possible. We also state this more explicitly in the revised Method section on p. 23 (see also our response to comment #3 by R3 on p. 15 below).

In a between-subjects analysis we observed, both within T1 and T2, a significant positive correlation (rT1 = .33, p<.01; rT2 = .40, p<.001) of participants’ overall accuracy and response speed, speaking against a speed-accuracy trade-off. For this reason, we did not consider an integrated speed–accuracy measure as behavioural indicator for modelling.

(3) The correlation between neural filtering at T1 and T2 was weak, which may be due to the low reliability of this indicator. The generally low reliability of the difference score is a notorious measurement problem recognized in the academic community.

We fully agree with the reviewer on their assessment of notoriously noisy difference scores. It is the very reason that motivated our application of the latent change score model approach. This framework elegantly supersedes the manual calculation of differences scores, and by explicitly

modelling measurement error also removes the impact of varying degrees of reliability on the estimation of change and how it varies as a function of different influences.

While we had already detailed this rationale in the original manuscript, we now more prominently describe the advantages of the latent variable approach in the first paragraph of the Results section:

Third and final, we integrate and extend the first two analysis perspectives in a joint latent change score model (LCSM) to most directly probe the role of neural filtering ability as a predictor of future attentive listening ability. Addressing our key change-related research questions at the latent rather than the manifest level supersedes the manual calculation of notoriously noisy differences scores, and effectively removes the influence of each metric’s reliability on the estimation of change-related relationships.

We also kindly refer the reviewer to our in-depth response to R1’s comment #2 regarding the concern of neural filtering’s low test-rest reliability and its impact on estimating change-change relationships.

1. For the latent change score model, it is recommended that the authors:<br /> (1) Supplement the coefficients of each path in Figure 5. For details, please refer to the figures in the papers of Kievit et al. (2017, 2019)

This information has been added to Figure 5.

(2) In Figure 5 and Figure S2, why should the two means of the observed 2nd half scores be estimated?

In longitudinal modelling, special care needs to be applied to the pre-processing/transformation of raw data for the purpose of change score modelling. While it is generally desirable to bring all variables onto the same scale (typically achieved by standardising all variables), one needs to be careful not to remove the mean differences of interest in such a data transformation step. We therefore followed the procedure recommended by Little (2013) and rescaled variables stacked across T1 and T2 using the proportion of maximum scale (‘POMS’) methods. This procedure, however, results in mean values per timepoint ≠ 0, so the mean of the second half needed to be freely estimated to avoid model misfit. Note that the mean of the first half manifest variables was set to 0 (using the ‘marker method’; see Little, 2013) to ensure model identification.

We have added the following more detailed description to the Method section on p. 26:

To bring all manifest variables onto the same scale while preserving mean differences over time, we first stacked them across timepoint and then rescaled them using the proportion of maximum scale (‘POMS’) method99,100 (…) Given our choice of POMS-transformation of raw to preserve mean differences over time, the mean of the second manifest variable had to be freely estimated (rather than implicitly assumed to be 0) to avoid severe model misfit.

(3) The authors need to clarify whether the latent change factor in Figure 5 is Δ(T1-T2) or Δ(T2-T1)?

Thank you for this comment. Our notation here was indeed confusing. The latent change factor quantifies the change from T1 to T2, so it is Δ(T2–T1). We have accordingly re-named the respective latent variables in all corresponding figures.

1. For data analysis, the author combined the trials under different conditions (valid and invalid cues) in the dichotic listening task and analyzed them together, which may mask the variations between different attention levels (selective vs. divided attention). It is recommended that the authors analyze the relationship between various indicators under different conditions.

We thank the reviewer for this comment which prompted us to (i) more clearly motivate our decision to model neural filtering across all trials, and (ii) nevertheless report the results of an additional control analyses that focused on neural filtering (or the neural tracking of attended speech) in selective-attention trials, only.

Our decision to analyse neural filtering across all spatial-attention conditions was motivated by two key considerations: First, previous T1 results (Tune et al., 2021) suggested that irrespective of the spatial-attention condition, stronger neural filtering boosted behavioural performance. Second, analysing neural filtering (and associated behaviour) across all trials provided the most direct way of probing the trait-like nature of individual neural filtering ability. <br /> We have included the following paragraph to the Results section on p. 6 to motivate this decision more clearly:

Our main analyses focus on neural filtering and listening performance averaged across all trials and thereby also across two separate spatial-attention conditions. This choice allowed us to most directly probe the trait-like nature and relationships of neural filtering. It was additionally supported by our previous observation of a general boost in behavioural performance with stronger neural filtering, irrespective of spatial attention.

On the other hand, one could argue that the effects of interest are underestimated by jointly analysing neural and behavioural functioning derived from both selective- and divided-attention conditions. After all, it is reasonable to expect a more pronounced neural filtering response in selective-attention trials.

For this reason, we now report, in the revised version, two additional control analyses that replicate the key analyses for the neural filtering index and for the tracking of attended speech, both averaged across selective-attention trials, only: In summary, analysing neural filtering under selective attention strengthened the brain-behaviour link within a given time-point but resulted in highly similar quantitative estimated for the key relationships of interest. The analysis of attended speech tracking notably improved the neural metric’s manifest-level re-test reliability (r = .64, p<.001) – but resulted in an estimated change-change correlation close to 0.

Taken together, these control analyses provide compelling support for our main conclusion that neural and behavioural functioning follow largely independent developmental trajectories.

We kindly refer the reviewer to our detailed response to R1 for the text of the added control analysis section on p. 4f. above. The additional Figure 6 is reproduced again below for the reviewer’s convenience.

Author response image 4.

Control analyses corroborate the independence of neural and behavioural trajectories under selective attention. Cross-sectional and longitudinal change in neural filtering (A) and neural tracking of attended speech (C) averaged across selective-attention trials, only. Coloured vectors (colour-coding four age groups for illustrative purposes, only) in the left subpanels show individual T1–T2 change along with the cross-sectional trend plus 95% confidence interval (CI) separately for T1 (dark grey) and T2 (light grey). Top right, correlation of T1 and T2 as measure of test-retest reliability along with the 45° line (grey) and individual data points (black circles). Bottom right, mean longitudinal change per age group and grand mean change (grey). B, D Latent change score model (LCSM) relating two-year changes in neural filtering (B) /neural tracking (D) strength to changes in response speed. Black arrows show the paths or covariances of interest that were freely estimates, grey arrows show paths that were freely estimated or fixed as part of the structural model but did not relate to the main research questions. Solid arrows indicate statistically significant effects, dashed arrows reflect nonsignificant paths. All estimates are standardised. p<.001, p<.01, p<.05.

Figure 6 has also been supplemented by two additional figures showing behavioural functioning (Fig. S4) and neural tracking of ignored speech (Fig. S5) under selective-attention trials, only. These figures are reproduced below for the reviewer’s convenience.

Author response image 5.

Cross-sectional and longitudinal change in listening behaviour under selective attention.

Author response image 6.

Cross-sectional and longitudinal change in neural tracking of ignored speech under selective attention.

6) As can be seen from the Methods section, there were still other cognitive tasks in this database that can be included in the data analysis to further determine the predictive validity of neural filtering.

We kindly refer the reviewer to our response to their public review and comment # 2 above where we motivate our decision to focus on manifest indicators of neural and behavioural functioning that are derived from the same task.

We believe that the analysis of several additional indicators of cognitive functioning would have distracted from our main goal of the current study focused on understanding how individual trajectories of listening performance may be explained and predicted.

7) "Magnitudes > 1 are taken as moderate, > 2.3 as strong evidence for either of the alternative or null hypotheses, respectively." Which papers are referenced by these criteria? The interpretation of BF values seems inconsistent with existing literature.

It may deserve emphasis that these are log Bayes Factors (logBF). Our interpretation of logarithmic Bayes Factors (logBF) follows Lee and Wagenmakers’ (2013) classic heuristic scheme for the interpretation of (non-logarithmic, ‘raw’) BF10 values. We have added the respective reference to the manuscript.

Reviewer #3 (Public Review):

Summary:

The study investigates the longitudinal changes in hearing threshold, speech recognition behavior, and speech neural responses in 2 years, and how these changes correlate with each other. A slight change in the hearing threshold is observed in 2 years (1.2 dB on average) but the speech recognition performance remains stable. The main conclusion is that there is no significant correlation between longitudinal changes in neural and behavioral measures.

Strengths:

The sample size (N>100) is remarkable, especially for longitudinal studies.

Weaknesses:

The participants are only tracked for 2 years and relatively weak longitudinal changes are observed, limiting how the data may shed light on the relationships between basic auditory function, speech recognition behavior, and speech neural responses.

Suggestions

First, it's not surprising that a 1.2 dB change in hearing threshold does not affect speech recognition, especially for the dichotic listening task and when speech is always presented 50 dB above the hearing threshold. For the same listener, if the speech level is adjusted for 1.2 dB or much more, the performance will not be influenced during the dichotic listening task. Therefore, it is important to mention in the abstract that "sensory acuity" is measured using the hearing threshold and the change in hearing threshold is only 1.2 dB.

We thank the reviewer for this comment. We have added the respective information to the abstract and have toned down our interpretation of the observed behavioural stability despite the expected decline in auditory acuity.

Second, the lack of correlation between age-related changes in "neuronal filtering" and behavior may not suggest that they follow independent development trajectories. The index for "neuronal filtering" does not seem to be stable and the correlation between the two tests is only R = 0.21. This low correlation probably indicates low test-retest reliability, instead of a dramatic change in the brain between the two tests. In other words, if the "neuronal filtering" index only very weakly correlates with itself between the two tests, it is not surprising that it does not correlate with other measures in a different test. If the "neuronal filtering" index is measured on two consecutive days and the index remains highly stable, I'm more convinced that it is a reliable measure that just changes a lot within 2 years, and the change is dissociated with the changes in behavior.

The authors attempted to solve the problem in the section entitled "Neural filtering reliably supports listening performance independent of age and hearing status", but I didn't follow the logic. As far as I could tell, the section pooled together the measurements from two tests and did not address the test-retest stability issue.

Please see our detailed response to R1’s comment #2 regarding the concern of how low (manifestlevel) reliability of our neural metric may have impacted the chance of observing a significant changechange correlation.

In addition, we would like to emphasize that the goal of the second step of our analysis procedure, featuring causal mediation analysis, was not to salvage the perhaps surprisingly low reliability of neural filtering. Instead, this section addressed a different research question, namely, whether the link of neural filtering to behaviour would hold across time, irrespective of the observed stability of the measure itself. The stability of the observed between-subjects brain-behaviour relationships was assessed by testing for an interaction with timepoint.

We have revised the respective Results section to more clearly state our scientific questions, and how our analysis procedure helped to address them:

"The temporal instability of neural filtering challenges its status as a potential trait-like neural marker of attentive listening ability. At the same time, irrespective of the degree of reliability of neural filtering itself, across individuals it may still be reliably linked to the behavioural outcome (see Fig. 1). This is being addressed next.

On the basis of the full T1–T2 dataset, we aimed to replicate our key T1 results and test whether the previously observed between-subjects brain-behaviour relationship would hold across time: We expected an individual’s neural filtering ability to impact their listening outcome (accuracy and response speed) independently of age or hearing status12. (…) To formally test the stability of direct and indirect relationships across time, we used a moderated mediation analysis. In this analysis, the inclusion of interactions by timepoint tested whether the influence of age, sensory acuity, and neural filtering on behaviour varied significantly across time."

Third, the behavioral measure that is not correlated with "neuronal filtering" is the response speed. I wonder if the participants are asked to respond as soon as possible (not mentioned in the method). If not, the response speed may strongly reflect general cognitive function or a personal style, which is not correlated with the changes in auditory functions. This can also explain why the hearing threshold affects speech recognition accuracy but not the response speed (lines 263-264).

Participants were asked to response within a given time window limited to 4 s but were not implicitly instructed to respond as quickly as possible. This is now stated more clearly in the Methods section (please also refer to our response to R2 on a similar question). It is important to emphasize—as shown in Figure 4A and Figure 5B —both at the manifest and latent variable level neural filtering (and in fact also the neural tracking of attended speech, see Fig. 6C) was reliably linked to response speed at T1 and T2. These results providing important empirical ground for the question of whether changes in neural filtering are systematically related to changes in response speed, and whether the fidelity of neural filtering at T1 represents a precursor of behavioural changes.

Moreover, an interpretation of response speed as an indicator of general cognitive function is not at all incompatible with the cognitive demands imposed by the task. As the reviewer rightly stated above, performance in a dichotic listening task does not simply hinge on how auditory acuity may limit perceptual encoding of speech inputs but also on how the goal-directed application of attention modulates the encoding of relevant vs. irrelevant inputs. We here focus on one candidate neural strategy we here termed ‘neural filtering’ in line with an influential metaphor of how auditory attention may be neurally implemented (Cherry, 1953; Erb & Obleser, 2020; Fernandez-Duque & Johnson, 1999).

Reviewer #3 (Recommendations For The Authors):

Other issues:

The authors should consider using terminology that the readers are more familiar with and avoid unsubstantiated claims.

For example, the Introduction mentions that "The observation of such brain-behaviour relationships critically advances our understanding of the neurobiological foundation of cognitive functioning. Their translational potential as neural markers predictive of behaviour, however, is often only implicitly assumed but seldomly put to the test. Using auditory cognition as a model system, we here overcome this limitation by testing directly the hitherto unknown longitudinal stability of neural filtering as a neural compensatory mechanism upholding communication success."

For the first sentence, please be clear about which aspects of "our understanding of the neurobiological foundation of cognitive functioning" is critically advanced by such brain-behaviour relationships, and why such brain-behaviour relationships are so critical given that so many studies have analyzed brain-behaviour relationships. The following two sentences seem to suggest that the current study is a translational study, but the later questions do not seem to be quite translational.

The uncovering of robust between- and within-subject brain behaviour-relationships is a key scientific goal that unites basic and applied neuroscience. From a basic neuroscience standpoint, the observation of such brain–behaviour links provides important mechanistic insight into the neurobiological implementation of higher order cognition – here the application of auditory spatial attention in the service of speech comprehension. At the same time, they provide fruitful ground for translational inquiries of applied neuroscience. We therefore don’t consider it contradictory at all that the current study addressed both more basic and applied/translational neuroscientific research questions.

We have rephrased the respective section as follows:

"The observation of such brain–behaviour relationships critically advances our understanding of the neurobiological foundation of cognitive functioning by showing, for example, how neural implementations of auditory selective attention support attentive listening. They also provide fruitful ground for scientific inquiries into the translational potential of neural markers. However, the potency of neural markers to predict future behavioural outcomes is often only implicitly assumed but seldomly put to the test15."

More importantly, "neuronal filtering" is a key concept in the paper but I'm not sure what it means. The authors have only mentioned that auditory cognition is a model system for "neuronal filtering", but not what "neuronal filtering" is. Even for auditory cognition, I'm not sure what "neuronal filtering" is and why the envelope response is representative of "neuronal filtering".

As spelled out in the Introduction, we define our ‘neural filtering’ metric of interest as neural manifestation of the attention-guided segregation of behaviourally relevant from irrelevant sounds. By terming this signature neural ‘filtering’, we take up on a highly influential algorithmic metaphor of how auditory attention may be implemented at the neurobiological level (Cherry, 1953; Erb & Obleser, 2020; Fernandez-Duque & Johnson, 1999).

We now provide more mechanistic detail in our description of the neural filtering signature analysed in the current study:

"Recent research has focused on the neurobiological mechanisms that promote successful speech comprehension by implementing ‘neural filters’ that segregate behaviourally relevant from irrelevant sounds. Such neural filter mechanisms act by selectively increasing the sensory gain for behaviourally relevant inputs or by inhibiting the processing of irrelevant inputs5-7. A growing body of evidence suggests that speech comprehension is neurally supported by an attention-guided filter mechanism that modulates sensory gain and arises from primary auditory and perisylvian brain regions: By synchronizing its neural activity with the temporal structure of the speech signal of interest, the brain ‘tracks’ and thereby better encodes behaviourally relevant auditory inputs to enable attentive listening 8-11."

Figure 1C should be better organized and the questions mentioned in the Introduction should be numbered.

We have revised both the respective section of the Introduction and corresponding Figure 1 in line with the reviewer’s suggestions. The revised text and figure are reproduced below for the reviewer’s convenience:

"First, by focusing on each domain individually, we ask how sensory, neural, and behavioural functioning evolve cross-sectionally across the middle and older adult life span (Fig. 1B). More importantly, we also ask how they change longitudinally across the studied two-year period (Fig. 1C, Q1), and whether aging individuals differ significantly in their degree of change (Q2). We expect individuals’ hearing acuity and behaviour to decrease from T1 to T2. Since we previously observed inter-individual differences in neural filtering to be independent of age and hearing status, we did not expect any systematic longitudinal change in neural filtering.

Second, we test the longitudinal stability of the previously observed age- and hearing-loss–independent effect of neural filtering on both accuracy and response speed (Fig. 1A). To this end, we analyse the multivariate direct and indirect relationships of hearing acuity, neural filtering and listening behaviour within and across timepoints.

Third, leveraging the strengths of latent change score modelling16,17, we fuse cross-sectional and longitudinal perspectives to probe the role of neural filtering as a precursor of behavioural change in two different ways: we ask whether an individual’s T1 neural filtering strength can predict the observed behavioural longitudinal change (Q3), and whether two-year change in neural filtering can explain concurrent change in listening behaviour (Q4). Here, irrespective of the observed magnitude and direction of T1–T2 developments, two scenarios are conceivable: Intra-individual neural and behavioural change may be either be correlated—lending support to a compensatory role of neural filtering—or instead follow independent trajectories18 (see Fig. 1C)."

Author response image 7.

Schematic illustration of key assumptions and research questions. A Listening behaviour at a given timepoint is shaped by an individuals’ sensory and neural functioning. Increased age decreases listening behaviour both directly, and indirectly via age-related hearing loss. Listening behaviour is supported by better neural filtering ability, independently of age and hearing acuity. B Conceptual depiction of individual two-year changes along the neural (blue) and behavioural (red) domain. Thin coloured lines show individual trajectories across the adult lifespan, thick lines and black arrows highlight two-year changes in a single individual. C Left, Schematic diagram highlighting the key research questions detailed in the introduction and how they are addressed in the current study using latent change score modelling. Right, across individuals, co-occurring changes in the neural and behavioural domain may be correlated (top) or independent of one another (bottom).

Figure 3, the R-value should also be labeled on the four main plots.

This information has been added to Figure 3, reproduced below.

Author response image 8.

Characterizing cross-sectional and longitudinal change along the auditory sensory (A), neural (B), and behavioural (C, D) domain. For each domain, coloured vectors (colour-coding four age groups for illustrative purposes, only) in the respective left subpanels show an individual’s change from T1 to T2 along with the cross-sectional trend plus 95% confidence interval (CI) separately for T1 (dark grey) and T2 (light grey). Top right subpanels: correlation of T1 and T2 as measure of test-retest reliability along with the 45° line (grey) and individual data points (black circles). Bottom right panels: Mean longitudinal change per age group (coloured vectors) and grand mean change (grey). Note that accuracy is expressed here as proportion correct for illustrative purposes, but was analysed logit-transformed or by applying generalized linear models.

T1 and T2 should be briefly defined in the abstract or where they first appear.

We have changed the abstract accordingly.

References

Alavash, M., Tune, S., & Obleser, J. (2019). Modular reconfiguration of an auditory control brain network supports adaptive listening behavior. [Clinical Trial]. Proceedings of the National Academy of Science of the United States of America, 116(2), 660-669. https://doi.org/10.1073/pnas.1815321116

Cherry, E. C. (1953). Some experiments on the recognition of speech, with one and with two ears. The Journal of the Acoustical Society of America, 25(5), 975-979. https://doi.org/10.1121/1.1907229

Erb, J., & Obleser, J. (2020). Neural filters for challening listening situations. In M. Gazzaniga, G. R. Mangun, & D. Poeppel (Eds.), The cognitive neurosciences (6th ed.). MIT Press.

Fernandez-Duque, D., & Johnson, M. L. (1999). Attention metaphors: How metaphors guide the cognitive psychology of attention. Cognitive Science, 23(1), 83-116. https://doi.org/10.1207/s15516709cog2301_4<br /> O’Sullivan, J. A., Power, A. J., Mesgarani, N., Rajaram, S., Foxe, J. J., Shinn-Cunningham, B. G., Slaney, M., Shamma,

S. A., & Lalor, E. C. (2014). Attentional Selection in a Cocktail Party Environment Can Be Decoded from Single-Trial EEG. Cerebral Cortex, 25(7), 1697-1706. https://doi.org/10.1093/cercor/bht355

Panela, R. A., Copelli, F., & Herrmann, B. (2023). Reliability and generalizability of neural speech tracking in younger and older adults. Nature Communications, 2023.2007.2026.550679. https://doi.org/10.1101/2023.07.26.550679

Tune, S., Alavash, M., Fiedler, L., & Obleser, J. (2021). Neural attentional-filter mechanisms of listening success in middle-aged and older individuals. Nature Communications, 1-14. https://doi.org/10.1038/s41467021-24771-9

Author Response

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

We greatly appreciate the reviewers' and editors' comments and suggestions on our manuscript "Transposable elements regulate thymus development and function." We performed additional analyses to validate our results and rephrased some manuscript sections according to the comments. We believe these changes significantly increase the solidity of our conclusions. Our point-by-point answer to the reviewers' and editors' comments is detailed below. New data and analyses are shown in Figure 1d, Figure 2g and h, Figure 5e and f, Figure 1 – figure supplement 1, Figure 2 – figure supplement 2, Figure 3 – figure supplement 1 and 2, Figure 4 – figure supplement 2, Figure 5 – figure supplement 1, as well as the corresponding text sections.

Reviewer #1:

(1) The authors sometimes made overstatements largely due to the lack or shortage of experimental evidence.

For example in figure 4, the authors concluded that thymic pDCs produced higher copies of TE-derived RNAs to support the constitutive expression of type-I interferons in thymic pDCs, unlike peripheral pDCs. However, the data was showing only the correlation between the distinct TE expression pattern in pDCs and the abundance of dsRNAs. We are compelled to say that the evidence is totally too weak to mention the function of TEs in the production of interferon. Even if pDCs express a distinct type and amount of TE-derived transcripts, it may be a negligible amount compared to the total cellular RNAs. How many TE-derived RNAs potentially form the dsRNAs? Are they over-expressed in pDCs?

The data interpretation requires more caution to connect the distinct results of transcriptome data to the biological significance.

We contend that our manuscript combines the attributes of a research article (novel concepts) and a resource article (datasets of TEs implicated in various aspects of thymus function). The critical strength of our work is that it opens entirely novel research perspectives. We are unaware of previous studies on the role of TEs in the human thymus. The drawback is that, as with all novel multi-omic systems biology studies, our work provides a roadmap for a multitude of future mechanistic studies that could not be realized at this stage. Indeed, we performed wet lab experiments to validate some but not all conclusions: i) presentation of TE-derived MAPs by TECs and ii) formation of dsRNAs in thymic pDCs. In response to Reviewer #1, we performed supplementary analyses to increase the robustness of our conclusions. Also, we indicated when conclusions relied strictly on correlative evidence and clarified the hypotheses drawn from our observations.

Regarding the Reviewer's questions about TE-derived dsRNAs, LINE, LTR, and SINE elements all have the potential to generate dsRNAs, given their highly repetitive nature and bi-directional transcription (1). As ~32% of TE subfamilies are overexpressed in pDCs, we hypothesized that these TE sequences might form dsRNA structures in these cells. To address the Reviewer's concerns regarding the amount of TE-derived RNAs among total cellular RNAs, we also computed the percentage of reads assigned to TEs in the different subsets of thymic APCs (see Reviewer 1 comment #4).

(2) Lack of generality of specific examples. This manuscript discusses the whole genomic picture of TE expression. In addition, one good way is to focus on the specific example to clearly discuss the biological significance of the acquisition of TEs for the thymic APC functions and the thymic selection.

In figure 2, the authors focused on ETS-1 and its potential target genes ZNF26 and MTMR3, however, the significance of these genes in NK cell function or development is unclear. The authors should examine and discuss whether the distinct features of TEs can be found among the genomic loci that link to the fundamental function of the thymus, e.g., antigen processing/presentation.

We thank the Reviewer for this highly relevant comment. We investigated the genomic loci associated with NK cell biology to determine if ETS1 peaks would overlap with TE sequences in protein-coding genes' promoter region. Figure 2h illustrates two examples of ETS1 significant peaks overlapping TE sequences upstream of PRF1 and KLRD1. PRF1 is a protein implicated in NK cell cytotoxicity, whereas KLRD1 (CD94) dimerizes with NKG2 and regulates NK cell activation via interaction with the nonclassical MHC-I molecule HLA-E (2, 3). Thus, we modified the section of the manuscript addressing these results to include these new analyses:

"Finally, we analyzed publicly available ChIP-seq data of ETS1, an important TF for NK cell development (4), to confirm its ability to bind TE sequences. Indeed, 19% of ETS1 peaks overlap with TE sequences (Figure 2g). Notably, ETS1 peaks overlapped with TE sequences (Figure 2h, in red) in the promoter regions of PRF1 and KLRD1, two genes important for NK cells' effector functions (2, 3)."

(3) Since the deep analysis of the dataset yielded many intriguing suggestions, why not add a discussion of the biological reasons and significance? For example, in Figure 1, why is TE expression negatively correlated with proliferation? cTEC-TE is mostly postnatal, while mTEC-TE is more embryonic. What does this mean?

We thank the Reviewer for this comment. To our knowledge, the relationship between cell division and transcriptional activity of TEs has not been extensively studied in the literature. However, a recent study has shown that L1 expression is induced in senescent cells. We therefore added the following sentences to our Discussion:

"The negative correlation between TE expression and cell cycle scores in the thymus is coherent with recent data showing that transcriptional activity of L1s is increased in senescent cells (5). A potential rationale for this could be to prevent deleterious transposition events during DNA replication and cell division."

We also added several discussion points regarding the regulation of TEs by KZFPs to answer concerns raised by Reviewer 2 (see Reviewer 2 comment #1).

(4) To consolidate the experimental evidence about pDCs and TE-derived dsRNAs, one option is to show the amount of TE-derived RNA copies among total RNAs. The immunohistochemistry analysis in figure 4 requires additional data to demonstrate that overlapped staining was not caused by technical biases (e.g. uneven fixation may cause the non-specifically stained regions/cells). To show this, authors should have confirmed not only the positive stainings but also the negative staining (e.g. CD3, etc.). Another possible staining control was showing that non-pDC (CD303- cell fractions in this case) cells were less stained by the ds-RNA probe.

We thank the Reviewer for this suggestion. We computed the proportion of reads in each cell assigned to two groups of sequences known to generate dsRNAs: TEs and mitochondrial genes (1). These analyses showed that the proportion of reads assigned to TEs is higher in pDCs than other thymic APCs by several orders of magnitude (~20% of all reads). In contrast, reads derived from mitochondrial genes had a lower abundance in pDCs. We included these results in Figure 4 – figure supplement 2 and included the following text in the Results section entitled "TE expression in human pDCs is associated with dsRNA structures":

"To evaluate if these dsRNAs arise from TE sequences, we analyzed in thymic APC subsets the proportion of the transcriptome assigned to two groups of genomic sequences known as important sources of dsRNAs, TEs and mitochondrial genes (1). Strikingly, whereas the percentage of reads from mitochondrial genes was typically lower in pDCs than in other thymic APCs, the proportion of the transcriptome originating from TEs was higher in pDCs (~22%) by several orders of magnitude (Figure 4 – figure supplement 2)."

As a negative control for the immunofluorescence experiments, we used CD123- cells. Indeed, flow cytometry analysis of the magnetically enriched CD303+ fraction was around 90% pure, as revealed by double staining with CD123 and CD304 (two additional markers of pDCs): CD123- cells were also CD304-/lo, showing that these cells are non-pDCs. Thus, we decided to compare the dsRNA signal between CD123+ cells (pDCs) and CD123- cells (non-pDCs). The difference between CD123+ and CD123- cells was striking (Figure 4d).

Author response image 1.

Reviewer #1 (Recommendations For The Authors):

It was sometimes difficult for me to recognize the dot plots representing low expression against the white background. e.g., figure 1 supplement 1.

We thank the Reviewer for their comment, and we modified Figure 1 – figure supplement 1 as well as Figure 3 – figure 3 supplement 2 to improve the contrast between dots and background.

Reviewer #2:

Reviewer #2 (Recommendations For The Authors):

(1) In the abstract, results and discussion, the following conclusions are drawn that are not supported by the data: a) TEs interact with multiple transcription factors in thymic cells, b) TE expression leads to dsRNA formation, activation of RIG-I/MDA5 and secretion of IFN-alpha, c) TEs are regulated by cell proliferation and expression of KZFPs in the thymus. All these statements derive from correlations. Only one TF has ChIP-seq data associated with it, dsRNA formation and/or IFN-alpha secretion could be independent of TE expression, and whilst KZFPs most likely regulate TEs in the thymus, the data do not demonstrate it. The authors also seem to suggests that AIRE, FEZF2 and CHD4 regulate TEs directly, but binding is not shown. The manuscript needs a thorough revision to be absolutely clear about the correlative nature of the described associations.

We agree with Reviewer #2 that some of the conclusions in our initial manuscript were not fully supported by experimental data. In the revised manuscript, we clearly indicated when conclusions relied strictly on correlative evidence and clarified the hypotheses drawn from our observations. Regarding the regulation of TE expression by AIRE, FEZF2, and CHD4, we reanalyzed publicly available ChIP-seq data of AIRE and FEZF2 in murine mTECs. For AIRE, we confirmed that ~30% of AIRE's statistically significant peaks overlap with TE sequences (see Reviewer 2, comment #6 for more details on read alignment and peak calling), confirming its ability to bind to TE sequences directly. We added these results to the main figures (Figure 5f) and modified the "AIRE, CHD4, and FEZF2 regulate distinct sets of TE sequences in murine mTECs" as follows:

“[…]. As a proof of concept, we validated that 31.42% of AIRE peaks overlap with TE sequences by reanalyzing ChIP-seq data, confirming AIRE's potential to bind TE sequences (Figure 5f)."

A reanalysis of FEZF2's ChIP-seq data yielded no significant peaks while using stringent criteria. For this reason, we decided to exclude these data and only use AIRE as a proof of concept.

Regarding KZFPs, we agree with Reviewer #2 that their impact on TE expression is probably significantly underestimated in our data. A potential reason for this is that KZFP expression is typically low; thus, transcriptomic signals from KZFPs could have been missed by the low depth of scRNA-seq. We mentioned this point in the Discussion:

"On the other hand, the contribution of KZFPs to TE regulation in the thymus is likely underestimated due to their typically low expression (6) and scRNA-seq's limit of detection."

(2) On the technical side, there are many dangers about analyzing RNA-seq data at the subfamily level and without stringent quality control checks. Outputs may be greatly confounded by pervasive transcription (see PMID 31425522), DNA contamination, and overlap of TEs with highly expressed genes. Whether TE transcripts are independent units or part of a gene also has important implications for the conclusions drawn. I would say that for most purposes of this work, an analysis restricted to independent TE transcripts, with appropriate controls for DNA contamination, would provide great reassurances that the results from subfamily-level analyses are sound. Showing examples from the genome browser throughout would also help.

We agree with the Reviewer that contamination could have interfered with TE quantification. We used FastQ Screen (7) to evaluate the contamination of our human scRNA-seq data. As illustrated in the Figure below, most reads aligned with the human genome, and there were no reads uniquely assigned to another species analyzed, confirming the high purity of our dataset.

Author response image 2.

As stated by the Reviewer, pervasive expression is another factor that can lead to overestimation of TE expression. To evaluate if pervasive expression impacted the results of our differential expression analysis of TEs between APC subsets, we visualized read alignment to TE sequences using a genome browser. We selected two samples containing the highest numbers of mTEC(II) and pDCs (T07_TH_EPCAM and FCAImmP7277556, respectively) and used STAR to align reads to the human genome (GRCh38). We then visualized read alignment to randomly selected loci of two subfamilies identified as overexpressed by mTEC(II) or pDCs (HERVE-int and Harlequin-int, respectively). The examples below show that the signal detected is specific to the TE sequences located in introns. Even though this visualization cannot guarantee that pervasive expression did not affect TE quantification in any way, it increases the confidence that the signal detected by our analyses genuinely originates from TE expression.

Author response image 3.

Author response image 4.

Author response image 5.

Author response image 6.

Author response image 7.

(3) Related to the above, it would be useful to describe in the main text (and methods) how multi-mapping reads are being handled. It wasn't clear to me how kallisto handles this, and it has implications for the results. In the analysis suggested above, only uniquely mapped reads would have to be used, despite its limitations.

We agree with the Reviewer that this information regarding assignment of multimapping reads is important. Kallisto uses an expectation-maximization (EM) algorithm to deal with multimapping reads, a strategy used by several algorithms developed to study TE expression (8). Briefly, the EM algorithm reassigns multimapping reads based on the number of uniquely mapped reads assigned to each sequence. Thus, we added the following details to the methods section:

"Preprocessing of the scRNA-seq data was performed with the kallisto (9), which uses an expectation-maximization algorithm to reassign multimapping reads based on the frequency of unique mappers at each sequence, and bustools workflow."

(4) Whilst I liked the basic idea, I am not convinced that correlating TE and TF expression is a good strategy for identifying TE-TF associations at enhancers. Enhancers express very low levels of short transcripts, which I doubt would be detected in low-depth scRNA-seq data. The transcripts the authors are using to make such associations may therefore have nothing to do with the enhancer roles of TEs. I would limit these analyses to cell types for which there is histone modification data and correlate TF expression with that instead.

We agree with the Reviewer that it would have been interesting to correlate the expression of TFs with signals of histone marks at TE sequences. However, we could not perform this analysis because we did not have matched data of histone marks throughout thymic development. Therefore, we adopted an alternative, well-suited strategy.

Our strategy to identify TE enhancer candidates is depicted in Figure 2a: i) correlation between the expression of the TF and the TE subfamily, ii) presence of the TF binding motif in the sequence of the TE enhancer candidate, and iii) colocalization of the TE enhancer candidate with significant peaks of H3K27ac and H3K4me3 in the same cell type from the ENCODE Consortium ChIP-seq data. We limited our analyses to the eight cell types present both in our dataset and the ENCODE Consortium: B cells, CD4 Single Positive T cells (CD4 SP), CD8 Single Positive T cells (CD8 SP), dendritic cells (DC), monocytes and macrophages (Mono/Macro), NK cells, Th17, and Treg.

(5) Figure 2G: binding of ETS1 is unconvincing. Were there statistically meaningful peaks called in these regions? It would be good to also show a metaplot/heatmap of ETS1 profile over all elements of relevant subfamilies. Showing histone marks on the genome browser snapshots would also be useful. Is there any transcriptional evidence that the specific Alus shown act as alternative promoters?

We agree with the Reviewer that the examples provided were not particularly convincing. Thus, we reanalyzed the data to determine if statistically significant ETS1 peaks (see the answer to Reviewer 2's comment #6 for details on the methods) located near gene transcription start sites overlapped with TEs. We thereby provided examples of significant ETS1 peaks overlapping TE sequences in the promoter region of two prototypical NK cell protein-coding genes (Figure 2h).

(6) Why was -k 10 used with bowtie2? This will map the same read to multiple locations in the genome, increasing read density at more repetitive (younger) TEs. The authors should use either default settings, being clear about the outcome (random assignment of multimapping reads to one location), or use only uniquely aligned reads.

We thank the Reviewer for their comment and agree that using the -k 10 parameter with bowtie2 was not optimal for TE analysis. To improve the strength of our analyses, we reanalyzed all ChIP-seq data of our manuscript (Figure 2g and h, Figure 5e and f) using the following strategy: alignment with bowtie2 using default parameters except –very-sensitive, multimapping read removal with samtools view -q 10, removal of duplicate reads with samtools markdup -r, peaks calling was performed with macs2 with the -m 5 50 parameter, and peaks overlapping ENCODE's blacklist regions were removed with bedtools intersect.

These new analyses strengthen our evidence that TEs interact with multiple genes that regulate thymic development and function. We updated the results sections concerning ChIP-seq data analyses and the Methods section to include this information:

"ChIP-seq reads were aligned to the reference Homo sapiens genome (GRCh38) using bowtie2 (version 2.3.5) (10) with the --very-sensitive parameter. Multimapping reads were removed using the samtools view function with the -q 10 parameter, and duplicate reads were removed using the samtools markdup function with the -r parameter (11). Peak calling was performed with macs2 with the -m 5 50 parameter (12). Peaks overlapping with the ENCODE blacklist regions (13) were removed with bedtools intersect (14) with default parameters. Overlap of ETS1 peaks with TE sequences was determined using bedtools intersect with default parameters. BigWig files were generated using the bamCoverage function of deeptools2 (15), and genomic tracks were visualized in the USCS Genome Browser (16)."

(7) Figure 1d needs a y axis scale. Could the authors also provide details of how the random distribution of TE expression was generated?

We agree that the Reviewer that Figure 1d was incomplete and made the appropriate modifications. Regarding the random distribution, we reproduced our dataset containing the expression of 809 TE subfamilies in 18 cell populations. For each combination of TE subfamily and cell type, we randomly assigned an "expression pattern" as identified by the hierarchical clustering of Figure 1b. Then, we computed the maximal occurrence of an expression pattern across cell types for each TE subfamily to generate the distribution curve in Figure 1d. We added the following details to the Methods section to clarify how the random distribution was generated:

"As a control, a random distribution of the expression of 809 TE subfamilies in 18 cell populations was generated. A cluster (cluster 1, 2, or 3) was randomly attributed for each combination of TE subfamily and cell type, and the maximal occurrence of a given cluster across cell types was then computed for each TE subfamily. Finally, the distributions of LINE, LTR, and SINE elements were compared to the random distribution with Kolmogorov-Smirnov tests."

(8) The motif analysis requires a minimum of 1 locus from each TE subfamily containing it in order to be reported, but this seems like a really low threshold that will output a lot of noise. What is the rationale here?

We agree with the Reviewer that this threshold might appear low. Nonetheless, these analyses ultimately aimed to identify TE promoter and enhancer candidates. Hence, we did not want to put an arbitrary threshold at a higher value (e.g., a certain number or percentage of all loci of a given TE subfamily), as this might create a bias based on the total number of loci of a given TE subfamily. Moreover, our rationale was that a TE locus might act as a promoter/enhancer even if it is the only locus of its subfamily containing a TF binding site.

Even though this strategy might have created some noise in the analyses of interactions between TFs and TEs of Figure 2 (panels a-e), we are confident that our bootstrap strategy efficiently removed low-quality identifications based on low correlations values or expression of TF and TE in low percentages of cells. Additionally, the subsequent analyses on TE promoter and enhancer candidates were performed exclusively for the TE loci containing TF binding sites to avoid adding noise to these analyses.

(9) Figure 4e: is this a log2 enrichment? If not, the enrichments for some of the gene sets are not so high.

The enrichment values represented in Figure 4e are not log-transformed. It is essential to highlight that gene set enrichment values were computed for each possible pair of thymic APCs (e.g., pDC vs. cDC1, pDC vs. mTEC(II), etc.), and the values represented in Figure 4e are an average of each comparison pictured at the bottom of the UpSet plot.

However, we agree with Reviewer 2 that the average enrichment value is not extremely high. We thus made the following modifications to the Results section ("TE expression in human pDCs is associated with dsRNA structures") to better represent it:

"Notably, thymic pDCs harbored moderate yet significant enrichment of gene signatures of RIG-I and MDA5-mediated IFN ɑ/β signaling compared to all other thymic APCs (Figure 4e and Supplementary file 1 – Table 8)."

(10) Please be clear on results subtitles when these refer to mouse.

We apologize for the confusion and modified the subtitles to clarify if the results refer to mouse or human data.

(11) Figure 1 - figure supplement 2: "assignation" should be 'assignment'.

We thank the Reviewer for their keen eye and changed the title of Figure 1 – figure supplement 2.

(1) Sadeq S, Al-Hashimi S, Cusack CM, Werner A. Endogenous Double-Stranded RNA. Noncoding RNA. 2021;7(1).

(2) Kim N, Kim M, Yun S, Doh J, Greenberg PD, Kim TD, et al. MicroRNA-150 regulates the cytotoxicity of natural killers by targeting perforin-1. J Allergy Clin Immunol. 2014;134(1):195-203.

(3) Gunturi A, Berg RE, Forman J. The role of CD94/NKG2 in innate and adaptive immunity. Immunol Res. 2004;30(1):29-34.

(4) Taveirne S, Wahlen S, Van Loocke W, Kiekens L, Persyn E, Van Ammel E, et al. The transcription factor ETS1 is an important regulator of human NK cell development and terminal differentiation. Blood. 2020;136(3):288-98.

(5) De Cecco M, Ito T, Petrashen AP, Elias AE, Skvir NJ, Criscione SW, et al. L1 drives IFN in senescent cells and promotes age-associated inflammation. Nature. 2019;566(7742):73-8.

(6) Huntley S, Baggott DM, Hamilton AT, Tran-Gyamfi M, Yang S, Kim J, et al. A comprehensive catalog of human KRAB-associated zinc finger genes: insights into the evolutionary history of a large family of transcriptional repressors. Genome Res. 2006;16(5):669-77.

(7) Wingett SW, Andrews S. FastQ Screen: A tool for multi-genome mapping and quality control. F1000Res. 2018;7:1338.

(8) Lanciano S, Cristofari G. Measuring and interpreting transposable element expression. Nat Rev Genet. 2020;21(12):721-36.

(9) Bray NL, Pimentel H, Melsted P, Pachter L. Near-optimal probabilistic RNA-seq quantification. Nat Biotechnol. 2016;34(5):525-7.

(10) Langmead B, Salzberg SL. Fast gapped-read alignment with Bowtie 2. Nat Methods. 2012;9(4):357-9.

(11) Danecek P, Bonfield JK, Liddle J, Marshall J, Ohan V, Pollard MO, et al. Twelve years of SAMtools and BCFtools. Gigascience. 2021;10(2).

(12) Zhang Y, Liu T, Meyer CA, Eeckhoute J, Johnson DS, Bernstein BE, et al. Model-based analysis of ChIP-Seq (MACS). Genome Biol. 2008;9(9):R137.

(13) Amemiya HM, Kundaje A, Boyle AP. The ENCODE Blacklist: Identification of Problematic Regions of the Genome. Sci Rep. 2019;9(1):9354.

(14) Quinlan AR, Hall IM. BEDTools: a flexible suite of utilities for comparing genomic features. Bioinformatics. 2010;26(6):841-2.

(15) Ramirez F, Ryan DP, Gruning B, Bhardwaj V, Kilpert F, Richter AS, et al. deepTools2: a next generation web server for deep-sequencing data analysis. Nucleic Acids Res. 2016;44(W1):W160-5.

(16) Kent WJ, Sugnet CW, Furey TS, Roskin KM, Pringle TH, Zahler AM, et al. The human genome browser at UCSC. Genome Res. 2002;12(6):996-1006.

Author Response

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

We are very grateful to the reviewers for their thorough assessment of our study, and their acknowledgment of its strengths and weaknesses. We did our best below to address the weaknesses raised in their public review, and to comply with their recommendations.

Reviewer #1 (Public Review):

Segas et al. present a novel solution to an upper-limb control problem which is often neglected by academia. The problem the authors are trying to solve is how to control the multiple degrees of freedom of the lower arm to enable grasp in people with transhumeral limb loss. The proposed solution is a neural network based approach which uses information from the position of the arm along with contextual information which defines the position and orientation of the target in space. Experimental work is presented, based on virtual simulations and a telerobotic proof of concept

The strength of this paper is that it proposes a method of control for people with transhumeral limb loss which does not rely upon additional surgical intervention to enable grasping objects in the local environment. A challenge the work faces is that it can be argued that a great many problems in upper limb prosthesis control can be solved given precise knowledge of the object to be grasped, its relative position in 3D space and its orientation. It is difficult to know how directly results obtained in a virtual environment will translate to real world impact. Some of the comparisons made in the paper are to physical systems which attempt to solve the same problem. It is important to note that real world prosthesis control introduces numerous challenges which do not exist in virtual spaces or in teleoperation robotics.

We agree that the precise knowledge of the object to grasp is an issue for real world application, and that real world prosthesis control introduces many challenges not addressed in our experiments. Those were initially discussed in a dedicated section of the discussion (‘Perspectives for daily-life applications’), and we have amended this section to integrate comments by reviewers that relate to those issues (cf below).

The authors claim that the movement times obtained using their virtual system, and a teleoperation proof of concept demonstration, are comparable to natural movement times. The speed of movements obtained and presented are easier to understand by viewing the supplementary materials prior to reading the paper. The position of the upper arm and a given target are used as input to a classifier, which determines the positions of the lower arm, wrist and the end effector. The state of the virtual shoulder in the pick and place task is quite dynamic and includes humeral rotations which would be challenging to engineer in a real physical prosthesis above the elbow. Another question related to the pick and place task used is whether or not there are cases where both the pick position and the place position can be reached via the same, or very similar, shoulder positions? i.e. with the shoulder flexion-extension and abduction-adduction remaining fixed, can the ANN use the remaining five joint angles to solve the movement problem with little to no participant input, simply based on the new target position? If this was the case, movements times in the virtual space would present a very different distribution to natural movements, while the mean values could be similar. The arguments made in the paper could be supported by including individual participant data showing distributions of movement times and the distances travelled by the end effector where real movements are compared to those made by an ANN.

In the proposed approach users control where the hand is in space via the shoulder. The position of the upper arm and a given target are used as input to a classifier, which determines the positions of the lower arm, wrist and the effector. The supplementary materials suggest the output of the classifier occurs instantaneously, in that from the start of the trial the user can explore the 3D space associated with the shoulder in order to reach the object. When the object is reached a visual indicator appears. In a virtual space this feedback will allow rapid exploration of different end effector positions which may contribute to the movement times presented. In a real world application, movement of a distal end-effector via the shoulder is not to be as graceful and a speed accuracy trade off would be necessary to ensure objects are grasped, rather than knocked or moved.

As correctly noted by the reviewer and easily visible on videos, the distal joints predicted by the ANN are realized instantaneously in the virtual arm avatar, and a discontinuity occurs at each target change whereby the distal part of the arm jumps to the novel prediction associated with the new target location. As also correctly noted by the reviewer, there are indeed some instances where minimal shoulder movements are required to reach a new target, which in practice implies that on those instances, the distal part of the arm avatar jumps instantaneously close to the new target as soon as this target appears. Please note that we originally used median rather than mean movement times per participant precisely to remain unaffected by potential outliers that might come from this or other situations. We nevertheless followed the reviewer’s advice and have now also included individual distributions of movement times for each condition and participant (cf Supplementary Fig. 2 to 4 for individual distributions of movement time for Exp1 to 3, respectively). Visual inspection of those indicates that despite slight differences between participants, no specific pattern emerges, with distributions of movement times that are quite similar between conditions when data from all participants are pooled together.

Movement times analysis indicates therefore that the overall participants’ behavior has not been impacted by the instantaneous jump in the predicted arm positions at each of the target changes. Yet, those jumps indicate that our proposed solution does not satisfactorily reproduce movement trajectory, which has implications for application in the physical world. Although we introduced a 0.75 s period before the beginning of each trial for the robotic arm to smoothly reach the first prediction from the ANN in our POC experiment (cf Methods), this would not be practical for a real-life scenario with a sequence of movements toward different goals. Future developments are therefore needed to better account for movement trajectories. We are now addressing this explicitly in the manuscript, with the following paragraph added in the discussion (section ‘Perspectives of daily-life applications’):

“Although our approach enabled participants to converge to the correct position and orientation to grasp simple objects with movement times similar to those of natural movements, it is important to note that further developments are needed to produce natural trajectories compatible with real-world applications. As easily visible on supplementary videos 2 to 4, the distal joints predicted by the ANN are realized instantaneously such that a discontinuity occurs at each target change, whereby the distal part of the arm jumps to the novel prediction associated with the new target location. We circumvented problems associated with this discontinuity on our physical proof of concept by introducing a period before the beginning of each trial for the robotic arm to smoothly reach the first prediction from the ANN. This issue, however, needs to be better handled for real-life scenarios where a user will perform sequences of movements toward different objects.”

Another aspect of the movement times presented which is of note, although it is not necessarily incorrect, is that the virtual prosthesis performance is close too perfect. In that, at the start of each trial period, either pick or place, the ANN appears to have already selected the position of the five joints it controls, leaving the user to position the upper arm such that the end effector reaches the target. This type of classification is achievable given a single object type to grasp and a limited number of orientations, however scaling this approach to work robustly in a real world environment will necessitate solving a number of challenges in machine learning and in particular computer vision which are not trivial in nature. On this topic, it is also important to note that, while very elegant, the teleoperation proof of concept of movement based control does not seem to feature a similar range of object distance from the user as the virtual environment. This would have been interesting to see and I look forward to seeing further real world demonstrations in the authors future work.

According to this comment, the reviewer has the impression that the ANN had already selected a position of the five joints it controls at the start of each trial, and maintained those fixed while the user operates the upper arm so as to reach the target. Although the jumps at target changes discussed in the previous comment might give this impression, and although this would be the case should we have used an ANN trained with contextual information only, it is important to stress that our control does take shoulder angles as inputs, and produced therefore changes in the predicted distal angles as the shoulder moves.

To substantiate this, we provide in Author response image 1 the range of motion (angular difference at each joint between the beginning and the end of each trial) of the five distal arm angles, regrouped for all angles and trials of Exp1 to 3 (one circle and line per participant, representing the median of all data obtained by that participant in the given experiment and condition, as in Fig. 3 of the manuscript). Please note that those ranges of motion were computed on each trial just after the target changes (i.e., after the jumps) for conditions with prosthesis control, and that the percentage noted on the figure below those conditions correspond to the proportion of the range of motion obtained in the natural movement condition. As can be seen, distal angles were solicited in all prosthesis control conditions by more than half the amount they moved in the condition of natural movements (between 54 and 75% depending on conditions).

Author response image 1.

With respect to the last part of this comment, we agree that scaling this approach to work robustly in a real world environment will necessitate solving a number of challenges in machine learning and in particular computer vision. We address those in a specific section of the discussion (‘Perspectives for daily-life application’) which has been further amended in response to the reviewers’ comments. As also mentioned earlier and at the occasion of our reply to other reviewers’ comments, we also agree that our physical proof of concept is quite preliminary, and we are looking forward to conduct future work in order to solve some of the issues discussed and get closer to real world demonstrations.

Reviewer #2 (Public Review):

Segas et al motivate their work by indicating that none of the existing myoelectric solution for people with transhumeral limb difference offer four active degrees of freedom, namely forearm flexion/extension, forearm supination/pronation, wrist flexion/extension, and wrist radial/ulnar deviation. These degrees of freedom are essential for positioning the prosthesis in the correct plan in the space before a grasp can be selected. They offer a controller based on the movement of the stump.

The proposed solution is elegant for what it is trying to achieve in a laboratory setting. Using a simple neural network to estimate the arm position is an interesting approach, despite the limitations/challenges that the approach suffers from, namely, the availability of prosthetic hardware that offers such functionality, information about the target and the noise in estimation if computer vision methods are used. Segas et al indicate these challenges in the manuscript, although they could also briefly discuss how they foresee the method could be expanded to enable a grasp command beyond the proximity between the end-point and the target. Indeed, it would be interesting to see how these methods can be generalise to more than one grasp.

Indeed, we have already indicated those challenges in the manuscript, including the limitation that our control “is suitable to place the hand at a correct position and orientation to grasp objects in a wide workspace, but not for fine hand and grasp control ...” (cf 4th paragraph of the ‘Perspectives for daily-life applications’ section of the discussion). We have nevertheless added the following sentence at the end of this paragraph to stress that our control could be combined with recently documented solutions for multiple grasp functions: “Our movement-based approach could also be combined with semi-autonomous grasp control to accommodate for multiple grasp functions39,42,44.”

One bit of the results that is missing in the paper is the results during the familiarisation block. If the methods in "intuitive" I would have thought no familiarisation would be needed. Do participants show any sign of motor adaptation during the familiarisation block?

Please note that the familiarization block indicated Fig. 3a contains approximately half of the trials of the subsequent initial acquisition block (about 150 trials, which represents about 3 minutes of practice once the task is understood and proficiently executed), and that those were designed to familiarize participants with the VR setup and the task rather than with the prosthesis controls. Indeed, it is important that participants were made familiar with the setup and the task before they started the initial acquisition used to collect their natural movements. In Exp1 and 2, there was therefore no familiarization to the prosthesis controls whatsoever (and thus no possible adaptation associated with it) before participants used them for the very first time in the blocks dedicated to test them. This is slightly different in Exp3, where participants with an amputated arm were first tested on their amputated side with our generic control. Although slight adaptation to the prosthesis control might indeed have occurred during those familiarization trials, this would be difficult in practice to separate from the intended familiarization to the task itself, which was deemed necessary for that experiment as well. In the end, we believe that this had little impact on our data since that experiment produced behavioral results comparable to those of Exp1 and 2, where no familiarization to the prosthesis controls could have occurred.

In Supplementary Videos 3 and 4, how would the authors explain the jerky movement of the virtual arm while the stump is stationary? How would be possible to distinguish the relative importance of the target information versus body posture in the estimation of the arm position? This does not seem to be easy/clear to address beyond looking at the weights in the neural network.

As discussed in our response to Reviewer1 and now explicitly addressed in the manuscript, there is a discontinuity in our control, whereby the distal joints of the arm avatar jumps instantaneously to the new prediction at each target change at the beginning of a trial, before being updated online as a function of ongoing shoulder movements for the rest of that trial. In a sense, this discontinuity directly reflects the influence of the target information in the estimation of the distal arm posture. Yet, as also discussed in our reply to R1, the influence of proximal body posture (i.e., Shoulder movements) is made evident by substantial movements of the predicted distal joints after the initial jumps occurring at each target change. Although those features demonstrate that both target information and proximal body posture were involved in our control, they do not establish their relative importance. While offline computation could be thought to quantify their relative implication in the estimation of the distal arm posture, we believe that further human-in-the-loop experiments with selective manipulation of this implication would be necessary to establish how this might affect the system controllability.

I am intrigued by how the Generic ANN model has been trained, i.e. with the use of the forward kinematics to remap the measurement. I would have taught an easier approach would have been to create an Own model with the native arm of the person with the limb loss, as all your participants are unilateral (as per Table 1). Alternatively, one would have assumed that your common model from all participants would just need to be 'recalibrated' to a few examples of the data from people with limb difference, i.e. few shot calibration methods.

AR: Although we could indeed have created an Own model with the native arm of each participant with a limb loss, the intention was to design a control that would involve minimal to no data acquisition at all, and more importantly, that could also accommodate bilateral limb loss. Indeed, few shot calibration methods would be a good alternative involving minimal data acquisition, but this would not work on participants with bilateral limb loss.

Reviewer #3 (Public Review):

This work provides a new approach to simultaneously control elbow and wrist degrees of freedom using movement based inputs, and demonstrate performance in a virtual reality environment. The work is also demonstrated using a proof-of-concept physical system. This control algorithm is in contrast to prior approaches which electrophysiological signals, such as EMG, which do have limitations as described by the authors. In this work, the movements of proximal joints (eg shoulder), which generally remain under voluntary control after limb amputation, are used as input to neural networks to predict limb orientation. The results are tested by several participants within a virtual environment, and preliminary demonstrated using a physical device, albeit without it being physically attached to the user.

Strengths:

Overall, the work has several interesting aspects. Perhaps the most interesting aspect of the work is that the approach worked well without requiring user calibration, meaning that users could use pre-trained networks to complete the tasks as requested. This could provide important benefits, and if successfully incorporated into a physical prosthesis allow the user to focus on completing functional tasks immediately. The work was also tested with a reasonable number of subjects, including those with limb-loss. Even with the limitations (see below) the approach could be used to help complete meaningful functional activities of daily living that require semi-consistent movements, such as feeding and grooming.

Weaknesses:

While interesting, the work does have several limitations. In this reviewer's opinion, main limitations are: the number of 'movements' or tasks that would be required to train a controller that generalized across more tasks and limbpostures. The authors did a nice job spanning the workspace, but the unconstrained nature of reaches could make restoring additional activities problematic. This remains to be tested.

We agree and have partly addressed this in the first paragraph of the ‘Perspective for daily life applications’ section of the discussion, where we expand on control options that might complement our approach in order to deal with an object after it has been reached. We have now amended this section to explicitly stress that generalization to multiple tasks including more constrained reaches will require future work: “It remains that generalizing our approach to multiple tasks including more constrained reaches will require future work. For instance, once an intended object has been successfully reached or grasped, what to do with it will still require more than computer vision and gaze information to be efficiently controlled. One approach is to complement the control scheme with subsidiary movements, such as shoulder elevation to bring the hand closer to the body or sternoclavicular protraction to control hand closing26, or even movement of a different limb (e.g., a foot45). Another approach is to control the prosthesis with body movements naturally occurring when compensating for an improperly controlled prosthesis configuration46.”

The weight of a device attached to a user will impact the shoulder movements that can be reliably generated. Testing with a physical prosthesis will need to ensure that the full desired workspace can be obtained when the limb is attached, and if not, then a procedure to scale inputs will need to be refined.

We agree and have now explicitly included this limitation and perspective to our discussion, by adding a sentence when discussing possible combination with osseointegration: “Combining those with osseointegration at humeral level3,4 would be particularly relevant as this would also restore amplitude and control over shoulder movements, which are essential for our control but greatly affected with conventional residual limb fitting harness and sockets. Yet, testing with a physical prosthesis will need to ensure that the full desired workspace can be obtained with the weight of the attached device, and if not, a procedure to scale inputs will need to be refined.”

The reliance on target position is a complicating factor in deploying this technology. It would be interesting to see what performance may be achieved by simply using the input target positions to the controller and exclude the joint angles from the tracking devices (eg train with the target positions as input to the network to predict the desired angles).

Indeed, the reliance on precise pose estimation from computer vision is a complicating factor in deploying this technology, despite progress in this area which we now discuss in the first paragraph of the ‘Perspective for daily life applications’ section of the discussion. Although we are unsure what precise configuration of input/output the reviewer has in mind, part of our future work along this line is indeed explicitly dedicated to explore various sets of input/output that could enable coping with availability and reliability issues associated with real-life settings.

Treating the humeral rotation degree of freedom is tricky, but for some subjects, such as those with OI, this would not be as large of an issue. Otherwise, the device would be constructed that allowed this movement.

We partly address this when referring to osseointegration in the discussion: “Combining those with osseointegration at humeral level3,4 would be particularly relevant as this would also restore amplitude and control over shoulder movements, which are essential for our control but greatly affected with conventional residual limb fitting harness and sockets.” Yet, despite the fact that our approach proved efficient in reconstructing the required humeral angle, it is true that realizing it on a prosthesis without OI is an open issue.

Overall, this is an interesting preliminary study with some interesting aspects. Care must be taken to systematically evaluate the method to ensure clinical impact.

Reviewer #1 (Recommendations For The Authors):

Page 2: Sentence beginning: "Here, we unleash this movement-based approach by ...". The approach presented utilises 3D information of object position. Please could the authors clarify whether or not the computer vision references listed are able to provide precise 3D localisation of objects?

While the references initially cited in this sentence do support the view that movement goals could be made available in the context of prosthesis control through computer vision combined with gaze information, it is true that they do not provide the precise position and orientation (I.e., 6d pose estimation) necessary for our movementbased control approach. Six-dimensional object pose estimation is nevertheless a very active area of computer vision that has applications beyond prosthesis control, and we have now added to this sentence two references illustrating recent progress in this research area (cf. references 30 and 31).

Page 6: Sentence beginning: "The volume spread by the shoulder's trajectory ...".

• Page 7: Sentence beginning: "With respect to the volume spread by the shoulder during the Test phases ...".

• Page 7: Sentence beginning: "Movement times with our movement-based control were also in the same range as in previous experiments, and were even smaller by the second block of intuitive control ...".

On the shoulder volume presented in Figure 3d. My interpretation of the increased shoulder volume in Figure 3D Expt 2 shown in the Generic ANN was that slightly more exploration of the upper arm space was necessary (as related to the point in the public review). Is this what the authors mean by the action not being as intuitive? Does the reduction in movement time between TestGeneric1 and TestGeneric 2 not suggest that some degree of exploration and learning of the solution space is taking place?

Indeed, the slightly increased shoulder volume with the Generic ANN in Exp2 could be interpreted as a sign that slightly more exploration of the upper arm space was necessary. At present, we do not relate this to intuitiveness in the manuscript. And yes, we agree that the reduction in movement time between TestGeneric1 and TestGeneric 2 could suggest some degree of exploration and learning.

Page 7: Sentence beginning: "As we now dispose of an intuitive control ...". I think dispose may be a false friend in this context!

This has been replaced by “As we now have an intuitive control…”.

Page 8: Section beginning "Physical Proof of Concept on a tele-operated robotic platform". I assume this section has been added based on suggestions from a previous review. Although an elegant PoC the task presented in the diagram appears to differ from the virtual task in that all the targets are at a relatively fixed distance from the robot. In respect to the computer vision ML requirements, this does not appear to require precise information about the distance between the user and an object. Please could this be clarified?

Indeed, the Physical Proof of Concept has been added after the original submission in order to comply with requests formulated at the editorial stage for the paper to be sent for review. Although preliminary and suffering from several limitations (amongst which a reduced workspace and number of trials as compared to the VR experiments), this POC is a first step toward realizing this control in the physical world. Please note that as indicated in the methods, the target varied in depth by about 10 cm, and their position and orientation were set with sensors at the beginning of each block instead of being determined from computer vision (cf section ‘Physical Proof of Concept’ in the ‘Methods’: “The position and orientation of each sponge were set at the beginning of each block using a supplementary sensor. Targets could be vertical or tilted at 45 and -45° on the frontal plane, and varied in depth by about 10 cm.”).

Page 10: Sentence beginning: "This is ahead of other control solutions that have been proposed ...". I am not sure what this sentence is supposed to convey and no references are provided. While the methods presented appear to be a viable solution for a group of upper-limb amputees who are often ignored by academic research, I am not sure it is appropriate for the authors to compare the results obtained in VR and via teleoperation to existing physical systems (without references it is difficult to understand what comparison is being made here).

The primary purpose of this sentence is to convey that our approach is ahead of other control solutions proposed so far to solve the particular problem as defined earlier in this paragraph (“Yet, controlling the numerous joints of a prosthetic arm necessary to place the hand at a correct position and orientation to grasp objects remains challenging, and is essentially unresolved”), and as documented to the best we could in the introduction. We believe this to be true and to be the main justification for this publication. The reviewer’s comment is probably directed toward the second part of this sentence, which states that performances of previously proposed control solutions (whether physical or in VR) are rarely compared to that of natural movements, as this comparison would be quite unfavorable to them. We soften that statement by removing the last reference to unfavorable comparison, but maintained it as we believe it is reflecting a reality that is worth mentioning. Please note that after this initial paragraph, and an exposition of the critical features of our control, most of the discussion (about 2/3) is dedicated to limitations and perspectives for daily-life application.

Page 10: Sentence: "Here, we overcame all those limitations." Again, the language here appears to directly compare success in a virtual environment with the current state of the art of physical systems. Although the limitations were realised in a virtual environment and a teleoperation PoC, a physical implementation of the proposed system would depend on advances in machine vision to include movement goal. It could be argued that limitations have been traded, rather immediately overcome.

In this sentence, “all those limitations” refers to all three limitations mentioned in the previous sentences in relation to our previous study which we cited in that sentence (Mick et al., JNER 2021), rather than to limitations of the current state of the art of physical systems. To make this more explicit, we have now changed this sentence to “Here, we overcome those three limitations”.

Page 11: Sentence beginning: "Yet, impressive progresses in artificial intelligence and computer vision ...".

• Page 11: Sentence beginning: "Prosthesis control strategies based on computer vision ..."

The science behind self-driving cars is arguably of comparable computational complexity to the real-world object detection and with concurrent real-time grasp selection. The market for self-driving cars is huge and a great deal of R&D has been funded, yet they are not yet available. The market for advanced upper-limb prosthetics is very small, it is difficult to understand who would deliver this work.

We agree that the market for self-driving cars is much higher than that for advanced upper-limb prosthetics. Yet, as mentioned in our reply to a previous comment, 6D object pose estimation is a very active area of computer vision that has applications far beyond prosthesis control (cf. in robotics and augmented reality). We have added two references reflecting recent progress in this area in the introduction, and have amended the discussion accordingly: “Yet, impressive progress in artificial intelligence and computer vision is such that what would have been difficult to imagine a decade ago appears now well within grasp38. For instance, we showed recently that deep learning combined with gaze information enables identifying an object that is about to be grasped from an egocentric view on glasses33, and this even in complex cluttered natural environments34. Six-dimensional object pose estimation is also a very active area of computer vision30,31, and prosthesis control strategies based on computer vision combined with gaze and/or myoelectric control for movement intention detection are quickly developing39–44, illustrating the promises of this approach.”

Page 15: Sentence beginning: "From this recording, 7 signals were extracted and fed to the ANN as inputs: ...".

• Page 15: Sentence beginning: "Accordingly, the contextual information provided as input corresponded to the ...".

The two sentences appear to contradict one another and it is difficult to understand what the Own ANN was trained on. If the position and the orientation of the object were not used due to overfitting, why claim that they were used as contextual information? Training on the position and orientation of the hand when solving the problem would not normally be considered contextual information, the hand is not part of the environment or setting, it is part of the user. Please could this section be made a little bit clearer?

The Own ANN was trained using the position and the orientation of a hypothetic target located within the hand at any given time. This approach has been implemented to increase the amount of available data. However, when the ANN is utilized to predict the distal part of the virtual arm, the position and orientation of the current target are provided. We acknowledge that the phrasing could be misleading, so we have added the following clarification to the first sentence: "… (3 Cartesian coordinates and 2 spherical angles that define the position and orientation of the hand as if a hypothetical cylindrical target was placed in it at any time, see an explanation for this choice in the next paragraph)".

Page 16: Sentence beginning: "A trial refers to only one part of this process: either ...". Would be possible to present these values separately?

Although it would be possible to present our results separately for the pick phase and for the place phase, we believe that this would overload the manuscript for little to no gain. Indeed, nothing differentiates those two phases other than the fact that the bottle is on the platform (waiting to be picked) in the pick phase, and in the hand (waiting to be placed) in the place phase. We therefore expect to have very similar results for the pick phase and for the place phase, which we verified as follows on Movement Time: Author response image 2 shows movement time results separated for the pick phase (a) and for the place phase (b), together with the median (red dotted line) obtained when results from both phases are polled together. As illustrated, results are very similar for both phases, and similar to those currently presented in the manuscript with both phases pooled (Fig3C).

Author response image 2.

Page 19: Sentence beginning "The remaining targets spanned a roughly ...". Figure 2 is a very nice diagram but it could be enhanced with a simple visual representation of this hemispherical region on the vertical and horizontal planes.

We made a few attempts at enhancing this figure as suggested. However, the resulting figures tended to be overloaded and were not conclusive, so we opted to keep the original.

Page 19: Sentence beginning "The Movement Time (MT) ..."

• Page 19: Sentence beginning "The shoulder position Spread Volume (SV) ..." Would it be possible to include a traditional timing protocol somewhere in the manuscript so that readers can see the periods over which these measures calculated?

We have now included Fig. 5 to illustrate the timing protocol and the periods over which MT and SV were computed.

Reviewer #2 (Recommendations For The Authors):

Minor comments

Page 6: "Yet, this control is inapplicable "as is" to amputees, for which recording ..." -> "Yet, this control is inapplicable "as is" to amputees, for WHOM recording ... "

This has been modified as indicated.

Throughout: "amputee" -> "people with limb loss" also "individual with limb deficiency" -> "individual with limb difference"

We have modified throughout as indicated.

It would have been great to see a few videos from the tele-operation as well. Please could you supply these videos?

Although we agree that videos of our Physical Proof of Concept would have been useful, we unfortunately did not collect videos that would be suitable for this purpose during those experimental phases. Please note that this Physical Proof of Concept was not meant to be published originally, but has been added after the original submission in order to comply with requests formulated at the editorial stage for the paper to be sent for review.

Reviewer #3 (Recommendations For The Authors):

Consider using the terms: intact-limb rather than able-bodied, residual limb rather than stump, congenital limb different rather than congenital limb deficiency.

We have modified throughout as indicated.

Author Response

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

We greatly appreciate the overwhelmingly positive summaries from all three reviewers and the eLife editorial team. All reviewers provided extremely detailed feedback regarding the initially submitted manuscript, we appreciate their efforts in helping us improve this manuscript. Below, are listed each of the specific comments made by the reviewers, and our responses to them in a point-by-point format.

The only notable change made to the manuscript that was not in response to comments from a reviewer was regarding nomenclature of the structure that we had previously called the nuclear microtubule organising centre (MTOC). We had used the term MTOC to describe the entire structure, which spans the nuclear envelope and comprises an intranuclear portion and cytoplasmic extensions. Given recent evidence, including findings from this study, it is possible that both the intranuclear region and cytoplasmic extensions both have microtubule nucleating capacity, and therefore both meet the definition of an MTOC. To disambiguate this, we now refer to the overall structure as the centriolar plaque (CP), consistent with previous literature. The intranuclear portion of the CP will be referred to as the inner CP, while the cytoplasmic portion will be referred to as the outer CP.

Reviewer #1 (Recommendations For The Authors):

1) In the first part of the result section, a paragraph on sample processing for U-ExM could be added, with reference to Fig 1b.

The following section has been added to the first paragraph of the results “…In this study all parasites were fixed in 4% paraformaldehyde (PFA), unless otherwise stated, and anchored overnight at 37 °C before gelation, denaturation at 95 °C and expansion. Expanded gels were measured, before shrinking in PBS, antibody staining, washing, re-expansion, and imaging (Figure 1b). Parasites were harvested at multiple time points during the intraerythrocytic asexual stage and imaged using Airyscan2 super-resolution microscopy, providing high-resolution three-dimensional imaging data (Figure 1c). A full summary of all target-specific stains used in this study can be found in Figure 1d.”

2) The order of the figures could be changed for more consistency. For example, fig 2b is cited before 2a.

An earlier reference to figure 2a was added to rectify this discrepancy.

3) In Fig 2b it is difficult to distinguish the blue (nuclear) and green (plasma membrane) lines.x

The thickness of these lines has been doubled.

4) It is unclear what the authors want to show in Fig 2a.

The intention of this figure, as with panel a of the majority of the organelle-specific figures in this manuscript, is simply to show what the target protein/structure looks like across intraerythrocytic development.

5) Lines 154-155, the numbers of MTOC observed do not match those in Supplt Fig2c.

This discrepancy has been addressed, the numbers in Supplementary Figure 2c were accurate so the text has been changed to reflect this.

6) Line 188: the authors should explain the principle of C1 treatment.

The following explanation of C1 treatment has been provided:

“To ensure imaged parasites were fully segmented, we arrested parasite development by adding the reversible protein kinase G inhibitor Compound 1 (C1). This inhibitor arrests parasite maturation after the completion of segmentation but before egress. When C1 is washed out, parasites egress and invade normally, ensuring that observations made in C1-arrested parasites are physiologically relevant and not a developmental artefact due to arrest.”

7) Lines 195-204: this part is rather difficult to follow as analysis of the basal complex is detailed later in the manuscript. The authors refer to Fig4 before describing Fig3.

This has been clarified in the text.

8) Lines 225 and 227, the authors cite Supplt Fig 2b about the Golgi, but probably meant Supplt Fig 4? In Supplt Fig 4, the authors could provide magnification in insets to better illustrate the Golgi-MTOC association.

This should have been a reference to Supplementary Figure 2e instead of 2b, which has now been changed. In Supplementary Figure 4, zooms into a single region of Golgi have been provided to more clearly show its MTOC association.

9) Supplt Fig8 is wrong (duplication of Supplt Fig6).

We apologise for this mistake, the correct figure is now present in Supplementary Figure 8.

10) Line 346: smV5 should be defined, and generation of the parasites should be described in the methods.

This has now been defined, but we have not described the generation of the parasites, as this was performed in a previous study that we have referenced.

11) Lines 361-362: "By the time the basal complex reaches its maximum diameter..." This sentence is not very clear, the authors could explain more precisely the sequence of events, indicating that the basal complex starts moving in the basal direction, as clearly illustrated in Fig 4a.

This has been prefaced with the following sentence “…As the parasite undergoes segmentation, the basal complex expands and starts moving in the basal direction.”

12) Supplt Fig6 comes after Supplt Fig9 in the narrative, and therefore could be placed after.

Supplementary Figure 6 and 9 follow the order in which they are referred to in the text.

13) Line 538: Supplt Fig9e instead of 9d.

This has been fixed.

14) Line 581: does the PFA-glutaraldehyde fixation allows visualizing other structures in addition to cytostome bulbs?

While PFA-glutaraldehyde fixation allows visualisation of cytostome bulbs, to date we have not observed any other structure that stains/preserves better using NHS Ester or BODIPY Ceramide in PFA-glutaraldehyde fixed parasites. As a general trend, all structures other than cytostomes become somewhat more difficult to identify using NHS Ester or BODIPY Ceramide in PFA-glutaraldehyde fixed samples due to the local contrast with the red blood cell cytoplasm. It seems likely that this is just due to the preservation of RBC cytoplasm, and would be expected from any fixation method that doesn’t result in RBC lysis, rather than anything unique to glutaraldehyde.

15) Line 652-653: It is unclear how the authors can hypothesize that rhoptries form de novo rather than splitting based on their observations.

This not something we can say with certainty, we have however, introduced the following paragraph to qualify our claims: “Overall, we present three main observations suggesting that rhoptry pairs undergo sequential de novo biogenesis rather than dividing from a single precursor rhoptry. First, the tight correlation between rhoptry and MTOC cytoplasmic extension number suggests that either rhoptry division happens so fast that transition states are not observable with these methods or that each rhoptry forms de novo and such transition states do not exist. Second, the heterogeneity in rhoptry size throughout schizogony favors a model of de novo biogenesis given that it would be unusual for a single rhoptry to divide into two rhoptries of different sizes. Lastly, well-documented heterogeneity in rhoptry density suggests that, at least during early segmentation, rhoptries have different compositions. Heterogeneity in rhoptry contents would be difficult to achieve so quickly after biogenesis if they formed through fission of a precursor rhoptry.”

16) Line 769: is expansion microscopy sample preparation compatible with FISH?

Yes, there are publications of expansion being done with both MERFISH and FISH. Though it has not yet been applied to plasmodium. See examples: Wang, Guiping, Jeffrey R. Moffitt, and Xiaowei Zhuang. "Multiplexed imaging of high-density libraries of RNAs with MERFISH and expansion microscopy." Scientific reports 8.1 (2018): 4847. And Chen, Fei, et al. "Nanoscale imaging of RNA with expansion microscopy." Nature methods 13.8 (2016): 679-684.

17) In the methods, the authors could provide details on the gel mounting step for imaging This is particularly important since this paper will likely serve as a reference standard for expansion microscopy in the field. Also, illustration that cryopreservation of gels does not modify the quality of the images would be useful.

The following section has been added to our “image acquisition” paragraph: “Immediately before imaging, a small slice of gel ~10mm x ~10mm was cut and mounted on an imaging dish (35mm Cellvis coverslip bottomed dishes NC0409658 - FisherScientific) coated with Poly-D lysine. The side of the gel containing sample is placed face down on the coverslip and a few drops of ddH20 are added after mounting to prevent gel shrinkage due to dehydration during imaging.”

We have decided not to illustrate that cryopreservation does not alter gel quality, as this is something that is already covered in the study that first cryopreserved gels, which is referenced in our methods section.

Reviewer #2 (Recommendations For The Authors):

1) Advantages and limitations of the expansion method are generally well discussed. The only matter in that respect that I was wondering is if expansion can always be assumed to be linear for all components of a cell. The hemozoin crystal does not expand (maybe not surprisingly), but could there also be other cellular structures that on a smaller scale separate or expand at a different rate than others? Is there any data on this from other organisms? I am raising this here not as a criticism of this work but if known to occur, it might need mentioning somewhere to alert the reader to it, particularly in regards to the many measurements in the paper (see also point 4). This might be a further factor contributing to the finding that the IMC and PPM could not be resolved.

This is an excellent point and, to our knowledge, one that is currently still under investigation in the field. It is well-documented that expansion protocols need to be customized to each cell type and tissue they are applied to. Each solution used for fixation and anchoring as well as timing and temperature of denaturation can affect the expansion factor achieved as well as how isotropic/anisotropic the expanded structures turn out. However, we do not know of any examples where isotropic expansion was achieved for everything but an organelle or component of the cell. It is our impression that if the cell seems to have attained isotropic expansion, this is assumed to also be the case for the subcellular structures within it. Nonetheless, we think it remains a possibility to be considered specially as more structures are characterized using these methods. In the case of our IMC/PPM findings, when we performed calculations taking into account our experimental expansion factor as well as antibody effects, it was clear that the resolution of our microscope was not enough to resolve the two structures using our current labelling methods. So, we suspect most of the effect is driven by that. However, this still needs to be validated by attempting to resolve the two structures though alternative labelling and imaging methods.

2) I understand that many things described in the results part are interconnected but still the level of hopping around between different figures/supp figures is considerable (see also point 6 on synchronicity of Figure parts). I do not have a simple fix, but maybe the authors could check if they could come up with a way to streamline parts of their results into a somewhat more reader friendly order.

This has been a problem we encountered from the beginning and, after trying multiple presentations of the results and discussion, we realized they all have drawbacks. We eventually settled on this presentation as the “least confusing”. We agree, however, that the figure references and order could be better streamlined and have addressed this to the best of our ability.

3) Are the authors sure the ER expands well and the BIP signal (Fig. S5) gives a signal reflecting the true shape of the ER? The signal in younger parasites seems rather extensive compared to what the ER (in my experience) typically looks like in these stages in live parasites.

While there may be a discrepancy between how the presumably dynamic ER appears in live cells, and how it appears using BiP staining, we think it is unlikely this is a product of expansion. Additionally, if there were to be an artefactual change in the ER, it would be likely under-expansion rather than over-expansion, which to our knowledge has not been reported. In our opinion, the BiP staining we observe is comparable between unexpanded and expanded samples. We have included comparative images in Author response image 1 with DNA in cyan and BiP in yellow, unexpanded (left) and expanded (right) using the same microscope and BiP antibody.

Author response image 1.

4) It is nice to have measurements of the apicoplast and mitochondria, but given their size, this could also have been done in unexpanded, ideally live parasites, avoiding expansion and fixing artifacts. While the expansion has many nice features, measuring area of large structures may not be one where it is strictly needed. I am not saying this is not useful information, but maybe a note could be added to the manuscript that the conclusions on mitochondria and apicoplast area and division might be worth confirming in live parasites. A brief mention on similarities and differences to previous work analysing the shape and multiplication of these organelles through blood stage development (van Dooren et al MolMicrobiol2005) might also be useful.

We agree with the reviewer that previous studies such as van Dooren et al. (2005) demonstrate that it is possible to track apicoplast and mitochondrial growth without expansion and share the opinion that live parasites are better for these measurements. Expansion only provides an advantage when more organelle-level resolution is needed. For example, in studying the association between these organelles and the MTOC or visualizing other branch-specific interactions.

5) I could not find the Supp Fig. 8 on the IMC, the current Supp Fig. 8 is a duplication of Supp Fig. 6

This has been addressed, Supplementary Figure 8 now refers to the IMC.

6) Figure order is not very synchronous with the text: Fig. 2a is mentioned after Fig. 2b, Fig. 4b is mentioned first for Fig. 4 (Fig. 4a is not by itself mentioned) and before Fig. 3 is mentioned; Fig. 3b is before Fig. 3a.

We have done our best to fix these discrepancies, but concede that we have not found a way to order these sections that doesn’t lead to some confusion.

7) Fig. S2a, The label "Centrin" on left image is difficult to read

We have increased the font size and changed colour slightly in the hope it is leigible.

8) In Fig. 2a, the centrin foci are very focal and difficult to see in these images, particularly when printed out but also on screen. To a lesser extent this is also the case for CINCH in Fig. 4a (particularly when printed; when zoomed-in on screen, the signal is well visible). This issue of difficulties in seeing the fluorescence signal of some markers, particularly when printed out, applies also to other images of the paper.

In the images of full size parasites, this is an issue that we cannot easily overcome as the fluorescent channels are already at maximum brightness without overexposure. To try and address this, we have provided zooms that we hope will more clearly show the fluorescence in these panels.

9) Expand "C1" in line 188 (first use).

This has been addressed in response to a previous comment.

10) Line 227; does Supp Fig. 2b really show Golgi- cytoplasmic MTOC association?

We have rephrased the wording of this section to clarify that we are observing proximity and not necessarily a physical tethering, however it is worth nothing that this was an accidental reference to Supplementary Figure 2b, and should’ve been Supplementary Figure 2e.

11) Line 230, in segmented schizonts the Golgi was considered to be at the apical end. It might be more precise to call its location to be close to the nucleus on the side facing the apical end of the parasite. It seems to me it often tends to be closer to the nucleus (in line with its proximity to the ER, see also point 13).

We have added more detail to this description clarifying that despite being at the apical end, the Golgi is closer to the nucleus.

12) Supp Fig. S5: Is the top cell indeed a ring? In the second cell there seem to be two nuclei, I assume this is a double infection (please indicate this in the legend or use images of a single infection).

In our opinion, the top cell in Supplementary Figure 5 is a ring. This is based on its size and its lack of an observable food vacuole (an area that lacks NHS ester staining). We typically showed images of ameoboid rings to avoid this ambiguity, but we think this parasite is a ring nonetheless. For the second image, this parasite is not doubly infected, as both DNA masses are actually contained within the same dumbbell shaped nuclear envelope. This parasite is likely undergoing its first anaphase (or the Plasmodium equivalent of anaphase) and will likely soon undergo its first nuclear division to separate these two DNA masses into individual nuclei.

13) Line 244: I would not call the Golgi a part of the apical cluster of organelles. All secretory cargo originates from the ER-Golgi-transGolgi axis in a directional manner and this axis is connected to the nucleus by the perinuclear ER. If seen from a secretory pathway centred view, it is the other way around and you could call the apical organelles part of the nuclear periphery which would be equally non-ideal.

Everything is close together in such a small cell. The secretory pathway likely is arranged in a serial manner starting from the perinuclear region to the transGolgi where cargo is sorted into vesicles for different destinations of which one is for the delivery of material to the apical organelles. The proposition that the Golgi is part of the apical cluster therefore somehow feels wrong, as the Golgi can still be considered to be upstream of the transGolgi before apical cargo branches off from other cargo destined for other destinations We agree with the reviewer that claiming a functional association between the Golgi and the apical organelles would be odd and we by no means meant to imply such functional grouping. Our intent was to confirm observations previously made about Golgi positioning by electron microscopy studies such as Bannister et al. (2000) at a larger spatial and temporal scale. These studies make the observation that the Golgi is spatially associated with the rhoptries at the apical end of the parasites. Logically, the Golgi is tied to the apical organelles through the secretory pathway as the reviewer suggests, but we claim no further relationship beyond that of organelle biogenesis. We have made modifications to the text to clarify these points.

14) Lines 300 - 308 (and thereafter): I assume these were also expanded parasites and the microtubule length is given after correction for expansion. I would recommend to indicate in line 274 (when first explaining the expansion factor) that all following measurements in the text represent corrected measures or, if this is not always the case, indicate on each occasion. Is the expansion factor accurate and homogenous enough to draw firm conclusions (see also point 1)? Could it be a reason for the variation seen with SPMTs? Could a cellular reference be used as a surrogate to account for cell specific expansion or would you assume that cellular substructure specific expansion differences exist and prevent this?

This is correct, the reported number is the number corrected for expansion factor, and the corresponding graphs with uncorrected data are present in the Supplementary Figures. We have clarified this in the text. Uneven expansion can be caused when certain organelles/structures do not properly denature. Given that out protocol denatures using highly concentrated SDS at 95 °C for 90 minutes, we do not anticipate that any subcellular compartments would expand significantly differently. In this study our expansion factors varied from ~4.1-4.7 across all gels, and for our corrected values we used the median expansion factor of 4.25. If we are interpreting the length of an interpolar spindle as 20 µm for example, the value would be corrected value would be 4.7 µm when divided by the median expansion factor, 4.9 µm when divided by the lowest, and 4.2 µm when divided by the highest. These values fall well within the measurement error, and so we expect that these small deviations in expansion factor between gels have a fairly minimal influence on variation in microtubule lengths.

15) Line 353: this is non-essential, but a 3D view of the broken basal ring might better illustrate the 2 semicircles

We have added the following panel to Supplementary Figure 3 to illustrate this more clearly:

Author response image 2.

16) The way the figure legends are shaped, it often seems only panel (a) is from expansion microscopy while the microscopy images in the other parts of the figures have no information on the method used. I assume all images are from expansion microscopy, maybe this could be clarified by placing this statement in a position of the legend that makes it clear it is for all images in a figure.

This has been clarified in the figure legends.

17) Fig. 8b, is it clear that internal RON4 is not below or above? Consider showing a 3D representation or side view of these max projections.

If in these images, we imagine we are looking at the ‘top’ of the rhoptries, our feeling is that the RON4 signal is on the ‘bottom’, at the part closest to the apical polar ring. We tried projecting this, however, but the images were not particularly due to spherical aberrations. Because of this, we have refrained from commenting on the RON4 location relative to the rhoptry bulb prior to elongation.

18) Line 684 "...distribution or RON4": replace or with of. The information of the next sentence is partly redundant, consider adding it in brackets.

This has been addressed.

19) Fig. 9a the EBA175 signal is not very prominent and a bit noisy, are the authors confident this is indeed showing only EBA175 or is there also some background?-AK

We agree with the reviewer that the EBA175 antibody shows a significant amount of background fluorescence, specially in the food vacuole area. However, we think the puncta corresponding to micronemal EBA175 can be clearly distinguished from background.

20) Fig. 9b, the long appearance of the micronemes in the z-dimension likely is due to axial stretch (due to point spread function in z and refractive index mismatch), in reality they probably are more spherical. It might be worth mentioning somewhere that this likely is not how these organelles are really shaped in that dimension (spherical fluorescent beads could give an estimation of that effect in the microscopy setup used).

After recently acquiring a water-immersion objective lens for comparison, it is clear that the transition from oil to hydrogel causes a degree of spherical aberration in the Z-plane, which in this instance causes the micronemes to be more oblong. As we make no conclusions based on the shape of the micronemes, however, we don’t think this is a significant consideration. This is an assumption that should be made when looking at any image whose resolution is not equal in all 3-dimensions. We also note that the more spherical shape of micronemes can be inferred from the max intensity projections in Figure 9c.

21) Fig. 9b, the authors mention in the text that there is NHS ester signal that overlaps with the fluorescence signal, can occasions of this be indicated in the figure?

Figure 9b was already quite busy, so we instead added the following extra panel to this figure that more clearly shows the NHS punctae we thought may have been micronemes:

Author response image 3.

22) Fig. 9, line 695, the authors write that the EBA puncta were the same size as AMA1 puncta. To me it seems the AMA1 areas are larger than the EBA foci, is their size indeed similar? Was this measured?

Since we did not conduct any measurements and doing so robustly would be difficult given the density of the puncta, we have decided to remove our comment on the relative size of the puncta.

23) Materials and methods: Remove "to" in line 871; explain bicarb and incomplete medium in line 885 (non-malaria researchers will not understand what is meant here); line 911 and start of 912 seem somewhat redundant

This has been addressed.

24) Is there more information on what the Airyscan processing at moderate filter level does? The background of the images seems to have an intensity of 0 which in standard microscopy images should be avoided (see for instance doi:10.1242/jcs.03433) similar to the general standard of avoiding entirely white backgrounds on Western blots. I understand that some background subtraction processes will legitimately result in this but then it would be nice to know a bit better what happened to the original image.

We have taken the following excerpt from a publication on Airyscan to help clarify:

"Airyscan processing consists of deconvolution and pixel reassignment, which yield an image with higher resolution and reduced noise. This can be a contributor to the low background in some channels. The level of filtering is the processing strength, with higher filtering giving higher resolution but increased chances of artefacts. More information about the principles behind Airyscan processing can be found in the following two publications, though details on the algorithm itself seem to be proprietary: Huff, Joseph. "The Airyscan detector from ZEISS: confocal imaging with improved signal-to-noise ratio and super-resolution." (2015): i-ii. AND Wu, Xufeng, and John A. Hammer. "Zeiss airyscan: Optimizing usage for fast, gentle, super-resolution imaging." Confocal Microscopy: Methods and Protocols. New York, NY: Springer US, 2021. 111-130."

We cannot find any further information about the specifics of Airyscan filtering, however, the moderate filter that we used is the default setting. This information was included just for clarity, rather than something we determined by comparison to other filtering settings.

In regards to the background, the majority of some images having an intensity value of 0 is partially out of our control. For all NHS Ester images, the black point of the images was 0 so areas that lack signal (white in the case of NHS Ester) truly had no signal detected for those pixels. While we appreciate that never altering the black point of images displays 100% of the data in the image, images with any significant background can become impossibly difficult to interpret. We have done our best to try and present images where the black point is modified to remove background for ease of interpretation by the readers only.

Reviewer #3 (Public Review):

1) Most importantly, in order to justify the authors claim to provide an "Atlas", I want to strongly suggest they share their raw 3D-imaging data (at least of the main figures) in a data repository. This would allow the readers to browse their structure of interest in 3D and significantly improve the impact of their study in the malaria cell biology field.

We agree completely that the potential impact of this study is magnified by public sharing of the data. The reason that this was not done at the time of submission is that most public repositories do not allow continued deposition of data, and so new images included in response to reviewers comments would’ve been separated from the initial submission, which we saw as needlessly complicated. All 647 images that underpin the results discussed in this manuscript are now publicly available in Dryad (https://doi.org/10.5061/dryad.9s4mw6mp4)

2) The organization of the manuscript can be improved. Aside some obvious modifications as citing the figures in the correct order (see also further comments and recommendations), I would maybe suggest one subsection and one figure per analyzed cellular structure/organelle (i.e. 13 sections). This would in my opinion improve readability and facilitate "browsing the atlas".

This is actually how we had originally formatted this manuscript, but this structure made discussing inter-connected organelles, such as the IMC and basal complex, impossibly difficult to navigate. We have done our best to make the manuscript flow better, but have not come up with any way to greatly restructure the manuscript so to increase its readability.

3) Considering the importance of reliability of the U-ExM protocol for this study the authors should provide some validation for the isotropic expansion of the sample e.g. by measuring one well defined cellular structure.

The protocol we used comes from the Bertiaux et al., 2021 PLoS Biology study. In this study they show isotropic expansion of blood-stage parasites.

4) In the absence of time-resolved data and more in-depth mechanistic analysis the authors must down tone some of their conclusions specifically around mitochondrial membrane potential, subpellicular microtubule depolymerization, and kinetics of the basal complex.

Our conclusions regarding mitochondrial membrane potential and basal complex kinetics have been dampened. We have not, however, changed our wording around microtubule depolymerisation. Partial depolymerisation of microtubules during fixation is a known phenomenon in Plasmodium, and in our opinion, our explanation of this offers a hypothesis that is balanced with respective to evidence: “we hypothesise that most SPMTs measured in our C1-treated schizonts had partially depolymerised. P. falciparum microtubules are known to rapidly depolymerise during fixation10,29. It is unclear, however, why this depolymerization was observed most often in C1-arrested parasites. Thus, we cannot determine whether these shorter microtubules are a by-product of drug-induced arrest or a biologically relevant native state that occurs at the end of segmentation.”

5) The observation that the centriolar plaque extensions remains consistently tethered to the plasma membrane is of high significance. To more convincingly demonstrate this point, it would be very helpful to show one zoomed-in side view of nucleus with a mitotic spindle were both centriolar plaques are in contact with the plasma membrane.

We of course agree that this is one of our most important observations, but in our opinion this is already demonstrated in Figure 2b. The third panel from the right shows a mitotic spindle and has the location of the cytoplasmic extensions, nuclear envelope and parasite plasma membranes annotated.

6) Please verify the consistent use of the term trophozoite and schizont. In Fig. 1c a parasite with two nuclei, likely in the process of karyofission is designated as trophozoite, which contrasts with the mononucleated trophozoite shown in Fig. 1a. The reviewer is aware of the more "classical" description of the schizont as parasite with more than 2 nuclei, but based on the authors advanced knowledge of cell cycle progression and mitosis I would encourage them to make a clear distinction between parasites that have entered mitotic stages and pre-mitotic parasites (e.g. by applying the term schizont, and trophozoite, respectively).

For this study, we have interpreted any parasite having three or more nuclei as being a schizont. We are aware this morphological interpretation is not universally held and indeed suboptimal for studying some aspects of parasite development, but all definitions of a schizont have some drawbacks. Whether a parasite has entered mitosis or not is obviously a hugely significant event in the context of cell biology, but in a mononucleated parasite this could only be determined using immunofluorescence microscopy with cell cycle or DNA replication markers.

7) Aldolase does not localize diffusely in the cytoplasm in schizont stages as in contrast to earlier stage. The authors should comment on that.

We are unclear if this is an interpretation of the images in supplementary figure 1, or inferred from other studies. If this is an interpretation of the images in Supplementary Figure 1, we do not agree that the images show a significant change in the localisation of aldolase. It is possible that this difference in interpretation comes from the strong punctate signal observed more readily in the schizont images. This is the strong background signal in or around the food vacuole we mention in the text. These punctae are significantly brighter than the cytosolic aldolase signal, making it difficult to see them on the aldolase only channel, but aldolase signal can clearly be seen in the cytoplasm on the merge images.

8) Line 79. Uranyl acetate is just one of the contrasting agents used in electron microscopy. The authors might reformulate this statement. Possibly this would also be a good opportunity to briefly mention that electron density measured in EM and protein-density labeled by NHS-Ester can be similar but are not equivalent.

We have expanded on this in the text.

9) The authors claim that they investigate the association between the MTOC and the APR (line 194), but strictly speaking only look at subpellicular microtubules and an associated protein density. The argument that there is a "NHS ester-dense focus" (line 210) without actual APR marker is not quite convincing enough to definitively designate this as the APR.

While an APR marker would of course be very useful, there are currently no published examples of APR markers in blood-stage parasites. We therefore think that the timing of appearance, location, and staining density are sufficient for identifying this structure as the APR, as it has previously been designated through EM studies. We have nonetheless softened our language around APR-related observations.

10) Line 226: The authors should also discuss the organization of the Golgi in early schizonts (Fig. S4). (not only 2 nuclei and segmenter stages).

We did not mean to imply that all 22 parasites had only 2 nuclei, but instead that they had 2 or more nuclei. Therefore, early schizonts are included in this analysis, with Golgi closely associated with all their MTOCs.

11) Line 242: To the knowledge of the reviewer the nuclear pore complexes, although clustered in merozoites and ring stages, don't particularly "define the apical end of the parasite".

The MTOC is surrounded by NPCs, which because of the location of the MTOC end up being near the forming apical end of the merozoite, but we have removed this as it was needlessly confusing.

12) Supplementary Figure 8 is missing (it's a repetition of Fig. S6).

This has been addressed.

13) Line 253: asexual blood stage parasites have two classes of MTs. Other stages can have more.

This has been clarified.

14) Fig. 3f: Please comment how much of these observations of "only one" SPMT could result from suboptimal resolution (e.g. in z-direction) or labeling. Otherwise use line profiles to argue that you can always safely distinguish SPMT pairs.

In the small number of electron tomograms of merozoites where the subpellicular microtubules have been rendered, they have been seen to have 2 or 3 SPMTs. Despite this, we don’t think it is likely that the single SPMT merozoites observed in this study are caused by a resolution limitation. SPMTs were measured in 3D, rather than from projections, and any schizont where the SPMTs were pointing towards the objective lens, elongating the parasite in Z, were not imaged. Additionally, our number of merozoites with a single SPMT correspond with the same data collected in the Bertiaux et al., 2021 PLoS Biology study. We cannot rule this out as a possibility, as sometimes SPMTs cross over each other in three-dimensions, and at these intersection points they cannot be individually resolved. We, however, think it is very unlikely that two SPMTs would be so close that they can never be resolved across any part of their length.

15) Lines 302ff: the claim that variability in SPMT size must be a consequence of depolymerzation is unfounded. The dynamics of SPMT are unknown at this point. Similarly unfounded is the definitive claim that it is known that P.f. MTs depolymerize upon fixation. Other possibilities should be considered. SPMT could also simply shorten in C1-arrested parasites.

While we agree with the reviewer that much about SPMT dynamics in schizonts remains unknown, we disagree with the claim that our consideration of SPMT depolymerization as a possible explanation for our observations is unfounded. Microtubule depolymerization is a well-known fixation and sample preparation artefact in both mammalian cells and a well-documented phenomenon in Plasmodium when parasites are washed with PBS prior to fixation. We convey in the text our belief that it is possible that SPMTs shorten in C1-arrested parasites as a result of drug treatment. However, it is our opinion that there simply is not enough evidence at this moment to conclusively pinpoint the cause of our observed depolymerization. As we mention in the text, further experiments are needed in order to determine with confidence whether depolymerization is a consequence of our fixation protocol, a consequence of C1 treatment (or the length of that treatment), or a biological phenomenon resulting from parasite maturation.

16) Line 324: "up to 30 daughter merozoites"

Schizonts can have more than 30 daughter merozoites, so we have not altered this statement.

17) Figure 4b. Line 354 The postulated breaking in two is not well visible and here the authors should attempt a more conservative interpretation of the data (especially with respect to those early basal complex dynamics).

We think that the basal complex dividing or breaking in two is the more conservative interpretation of our data. There is no evidence to suggest that a second basal complex is formed de novo and, while never before described using a basal complex protein, the cramp-like structure and dynamics we observe are consistent with that observed in early IMC proteins. We have updated the text to provide additional context and make the reasoning behind our hypothesis clearer.

18) Line 365: Commenting on their relative size would require a quantification of APR and basal complex size (can be provided in the text).

We are unsure what this is in reference to, as there is no mention of the APR in the basal complex section.

19) Lines 375ff: The claim that NHS Ester is a basal complex marker should be mitigated or more convincing images without the context of anti-CINCH staining being sufficient to identify the ring structure should be presented.

We have provided high quality, zoomed-in images without anti-CINCH staining in Fig. 5D&E, 6C, 7b, and Supplementary Fig. 8 that show that even in the absence of a basal complex antibody, the basal complex still stains densely by NHS ester.

20) Line 407: The claim that there are differences in membrane potential along the mitochondria needs to be significantly mitigated. There are several alternative explanations of this staining pattern (some of which the authors name themselves). Differences in local compartment volume, differences in membrane surface, diffusibility/leakage of the dye can definitively play a role in addition to fixation and staining artefacts (also brought forward recently for U-ExM by Laporte et al. 2022 Nat Meth). Confirming the hypothesis of the authors would need significantly more experimental evidence that is outside the scope of this study.

We have significantly dampened and qualified the wording in this section. It now reads: “These clustered areas of Mitotracker staining were highly heterogeneous in size and pattern. Small staining discontinuities like these are commonly observed in mammalian cells when using Mitotracker dyes due to the heterogeneity of membrane potential from cristae to cristae as well as due to fixation artifacts. At this point, we cannot determine whether the staining we observed represents a true biological phenomenon or an artefact of this sample preparation approach. Our observed Mitotracker-enriched pockets could be an artifact of PFA fixation, a product of local membrane depolarization, a consequence of heterogeneous dye retention, or a product of irregular compartments of high membrane potential within the mitochondrion, to mention a few possibilities. Further research is needed to conclusively pinpoint an explanation.”

21) Fig. 7e: The differences in morphology using different fixation methods are interesting. Can the authors provide a co-staining of K13-GFP together with the better-preserved structures in the GA-containing fixation protocol to demonstrate that these are indeed cytostome bulbs?

Figure 7 has been changed substantially to show more clearly the preservation of the red blood cell membrane following PFA-GA fixation, followed by direct comparison of K13-GFP stained parasites fixed in either PFA only or PFA-GA. The cytostome section of the results has also changed to reflect this, the changed section now reads:

“PFA-glutaraldehyde fixation allows visualization of cytostome bulb The cytostome can be divided into two main components: the collar, a protein dense ring at the parasite plasma membrane where K13 is located, and the bulb, a membrane invagination containing red blood cell cytoplasm {Milani, 2015 #63;Xie, 2020 #62}.While we could identify the cytostomal collar by K13 staining, these cytostomal collars were not attached to a membranous invagination. Fixation using 4% v/v paraformaldehyde (PFA) is known to result in the permeabilization of the RBC membrane and loss of its cytoplasmic contents65. Topologically, the cytostome is contiguous with the RBC cytoplasm and so we hypothesised that PFA fixation was resulting in the loss of cytostomal contents and obscuring of the bulb. PFA-glutaraldehyde fixation has been shown to better preserve the RBC cytoplasm65. Comparing PFA only with PFA-glutaraldehyde fixed parasites, we could clearly observe that the addition of glutaraldehyde preserves both the RBC membrane and RBC cytoplasmic contents (Figure 7c). Further, while only cytostomal collars could be observed with PFA only fixation, large membrane invaginations (cytostomal bulbs) were observed with PFA-glutaraldehyde fixation (Figure 7d). Cytostomal bulbs were often much longer and more elaborate spreading through much of the parasite (Supplementary Video 1), but these images are visually complex and difficult to project so images displayed in Figure 7 show relatively smaller cytostomal bulbs. Collectively, this data supports the hypothesis that these NHS-ester-dense rings are indeed cytostomes and that endocytosis can be studied using U-ExM, but PFA-glutaraldehyde fixation is required to maintain cytostome bulb integrity.”

22) It would be helpful to the readers to indicate in the schematic in Fig. 1b at which point NHS-Ester staining is implemented.

Figure 1b is slightly simplified in the sense that it doesn’t differentiate primary and secondary antibody staining, but we have updated it to reflect that antibody and dye staining are concurrent, rather than separate.

23) In Fig. 2B the second panel from the right the nuclear envelope boundary does not seem to be accurately draw as it includes the centrin signal of the centriolar plaque.

Thank you for pointing this out, it has now been redrawn.

24) Line 44-45: should read "up to 30 new daughter merozoites" (include citations).

We have included a citation here, but left it as approximately 30 daughter merozoites as the study found multiple cells with >30 daughter merozoites.

25) Line 49: considering its discovery in 2015 the statement that it has gained popularity in the last decade can probably be omitted.

This has been removed.

26) Fig S1 should probably read "2N" (instead of "2n"). Or alternatively "2C" could be fine.

27) Line 154: To help comprehension please define the term "branch number" in this context when it comes up.

A definition for branch has now been provided.

28) Fig. S5: To my estimation it is not an "early trophozoite", which is depicted.

While this parasite technically fits our definition of trophozoite, as it has not yet undergone nuclear division, we have swapped it for a visibly earlier parasite for clarity. This is the new parasite depicted

Author response image 4.

29) Fig. 2a is not referenced before Fig. 2b in the text.

This has been addressed.

30) I could not find the reference to Fig. S2e and its discussion.

It was wrongly labelled as Supplementary Figure 2b in the text, this has now been addressed.

31) The next Figure referenced in the text after Fig. 2b is Fig. 4b. Fig.3 is only referenced and discussed later, which was quite confusing.

The numbering discrepancies have been addressed.

32) Line 196: Figure reference is missing.

This data did not have a figure reference, but the numbers have now been provided in-text.

33) Fig. 3c: Is "Branches per MTOC" not just total branches divided by two? If so it can be omitted. If not so please explain the difference.

Yes it was total branched divided by two, this has been removed from Figure 3c.

34) Figure 5c and 6d: The authors should show examples of the image segmentation used to calculate the surface area.

Surface area calculation was done in an essentially one step process. From maximum intensity projections, free-hand regions of interest were drawn, from which ZEN automatically calculates their area. Example as Author response image 5:

Author response image 5.

35) Figure 7b should also show the NHS Ester staining alone for the zoom in.

We have included the NHS ester staining alone on the zoom on, but we have slightly changed the presentation of these two panels to show both the basal complex and cytostomes as follows:

Author response image 6.

36) To which degree are Rhoptry necks associated with MTOC extensions?

This cannot easily be determined with the images we have so far. Before elongated necks are visible, the RON4 signal does appear pointed towards the MTOC extensions. Rhoptry necks don’t seem to elongate until segmentation, when the MTOC starts to move away from the apical end of the parasite. So it is possible there is a transient association, but we cannot easily discern this from our data.

Author response:

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

Reviewer #1 (Public Review):

This publication applies 3D super-resolution STORM imaging to understanding the role of developmental neural activity in the clustering of retinal inputs to the mouse dorsal lateral geniculate nucleus (dLGN). The authors argue that retinal ganglion cell (RGC) synaptic boutons start forming clusters early in postnatal development (P2). They then argue that these clusters contribute to eye-specific segregation of retinal inputs by activity-dependent stabilization of nearby boutons from the same eye. The data provided is N=3 animals for each condition of P2, P4, and P8 animals in wild-type mice and in mice where early patterns of structured retinal activity are blocked.

Strengths:

The 3D storm imaging of pre and postsynaptic elements provides convincing high-resolution localization of synapses.

The experimental design of comparing ipsilateral and contralateral RGC axon boutons in a region of the dLGN that is known to become contralateral is elegant. The design makes it possible to relate fixed time point structural data to a known outcome of activity-dependent remodeling.

Weaknesses:

Based on previous literature, it is known that synapse density, synapse clustering, and synaptic specificity increase during postnatal development. Previous work has also shown that both the changes in synaptic clustering and synaptic specificity are affected by retinal activity. The data and analysis provided by the authors add little unambiguous evidence that advances this understanding.

We agree with the reviewer that previous literature shows that synapse density, synapse clustering, and synaptic specificity increase during postnatal development and that these processes are affected by retinal activity. The majority of studies on synaptic refinement have been performed after eye-opening, when eye-specific segregation is already complete. In contrast, most studies of eye-specific segregation focus on axonal refinement phenotypes. To our knowledge, only a small number of experiments have examined retinogeniculate synaptic properties at the nanoscale during eye-specific segregation (1-4). Our broad goal is to understand the mechanisms of synaptogenesis and competition at the earliest stages of eye-specific refinement, when spontaneous retinal activity is a major driver of activity-dependent remodeling. We hope that readers will appreciate that there is still much to discover in this fascinating model system of synaptic competition.

General problem 1: Most of the statistical analysis is limited to ANOVA comparison of axons from the contralateral and ipsilateral retina in the contralateral dLGN. The hypothesis that ipsilateral and contralateral axons would be statistically identical in the contralateral dLGN is not a plausible hypothesis so rejecting the hypothesis with P < X does not advance the authors' arguments beyond what was already known.

General problem 2: Most of the interpretation of data is qualitative. While error bars are provided, these error bars are not used to draw conclusions. Given the small sample size (N=3), there is a large degree of uncertainty regarding the magnitude of changes (synapse size, number, specificity). The authors base their conclusions on the averages of these values when the likely degree of uncertainty could allow for the opposite interpretation.

We appreciate the reviewer’s concerns regarding the use of ANOVA for statistical testing in the original submission. We have generated new figures that show confidence intervals for each analysis in the manuscript and these are included in the response to reviewers document below. To address the underlying concern that our N=3 sample size limits the interpretation of our results, we have revised the manuscript to be cautious in our interpretations and to discuss additional possibilities that are consistent with the anatomical data.

General problem 3: Two of the four results sections depend on using the frequency of single active zone vGlut2 clusters near multiple active zone vGlut2 as a proxy for synaptic stabilization of the single active zone vGlut2 clusters by the multiple active zone vGlut2 clusters. The authors argue that the increased frequency of same-eye single active zone clusters relative to opposite-eye single active zone clusters means that multiple active zone vGlut2 clusters are selectively stabilizing single active zone clusters. There are other plausible explanations for this observation that are not eliminated. An increased frequency of nearby single active zone clusters would also occur if RGC axons form more than one synapse in the dLGN. Eye-specific segregation is, by definition, a relative increase in the frequency of nearby boutons from the same eye. The authors were, therefore, guaranteed to observe a non-random relationship between boutons from the same eye. The authors do compare their measures to a random model, but I could not find a description of the model. I would expect that the model would need to account for RGC arbor size, arbor structure, bouton number, and segregation independent of multi-active-zone vGlut2 clusters. The most common randomization for the type of analysis described here, a shift in the positions of single-active zone boutons, would not be adequate.<br /> In discussing the claimed cluster-induced stabilization of nearby boutons, the authors state that the specificity increases with age due to activity-dependent refinement. Their quantification does not support an increase in specificity with age. In fact, the high degree of clustering "specificity" they observe at P2 argues for the trivial same axon explanation.

We agree with the reviewer that individual RGC axons form multiple synapses and that, over time, eye-specific segregation must increase the frequency of like-eye synapses relative to opposite-eye synapses. Indeed, our previous study of eye-specific refinement showed that at P8, the density of eye-specific inputs had increased for the dominant-eye and decreased for the non-dominant-eye (1). However, at postnatal day 4, contralateral and ipsilateral input densities were the same in the future contralateral-eye territory. One of our goals in this study was to determine if the process of synaptic clustering begins at these earliest stages of synaptic competition and, if so, whether it is influenced by retinal wave activity. It is plausible that the RGC axons from the same eye could initially form synapses randomly and, at some later stage, synapses may be selectively added to produce mature glomeruli. Consistent with this possibility, previous analysis of JAM-B RGC axon refinement showed the progressive clustering of axonal boutons at later stages of development after eye-specific segregation (5).

Regarding the randomization that we employed, we performed a repositioning of synapse centroids within the volume of the neuropil after accounting for neuronal soma volumes and edge effects. We agree that this type of randomization cannot account for the fine scale structure of axons and dendrites, which we did not have access to in this four-color volumetric super-resolution data set. To address this, we have performed additional clustering analyses surrounding both single-active zone and multi-active zone synapses. This new analysis showed that there is a modest clustering effect around single-active zone synapses compared to complete randomization described above. We now present this information using a normalized clustering index for direct comparison of clustering between multi-active zone and single-active zone synapses. We have measured effect sizes and confidence intervals, which we present in point-by-point responses below. We have restructured the manuscript figures and discussion to provide a balanced interpretation of our results and the limitations of our study.

Analysis of specific claims:

Result Section 1

Most of the figures show mean, error bars, and asterisks, but not the three data points from which these statistics are derived. Large changes in variance from condition to condition suggest that displaying the data points would provide more useful information.

We thank the reviewer for their suggestion. We have updated all figures to display the means of all biological replicates as individual data points.

Claim 1: Contralateral density increases more than ipsilateral in the contralateral region over the course of development. This claim is supported by the qualitative comparison of means and error bars in Figure 2D. The argument could be made quantitative by providing a confidence interval for synapse density increase for dominant and non-dominant synapse density. A confidence interval could then be generated for the difference in this change between the two groups. Currently, the most striking effect is a big difference in variance between P4 and P8 for dominant eye complex synapses. Given that N=3, I assume there is one extreme outlier here.

We appreciate the comment and believe the reviewer was referring to the data presented in the original Figure 1D, rather than Figure 2D.

We agree with the reviewer that our comment on the change in synapse density across ages was not quantitatively supported by the figure as we did not perform a proper age-wise statistical comparison. We have removed this claim in the revised manuscript.

We also appreciate the suggestions to clarify the presentation of our statistical analyses and to utilize confidence interval measurements wherever possible. We present Author response image 1 below, showing the density of multi-AZ synapses in the contralateral-eye territory over time (P2-P8), for both CTB(+) contralateral (black) and CTB(-) ipsilateral inputs (red) featuring 5/95% confidence intervals:

Author response image 1.

More broadly, the reviewer has raised the concern that the low number of biological replicates (N=3) presents challenges in the use of ANOVA for statistical testing. We agree with the concern and have revised the manuscript to be cautious in our statistical tests and resulting claims. We have chosen to use paired T-tests to compare measurements of eye-specific synapse properties because these measurements were always made within each individual biological replicate (paired measurements). Below, we discuss our logic for this change and the effects on the results we present in the revised manuscript.

Considering the above image:

(1) ANOVA: In our initial submission, we used an ANOVA test which showed P<0.05 for the CTB(+) P4 vs. P8 comparison above, leading to our statement about an age-dependent increase in multi-AZ density. However, the figure above shows that P8 data has higher variance. Thus, the homogeneity of variance assumption of ANOVA may lead to false positives in this comparison.

(2) Confidence interval for N=3: We calculated confidence intervals for P4 and P8 data (5/95% CI shown above). Overlap between the two groups indicates the true mean values of the two groups could be identical. However, the P8 confidence intervals (as well as other confidence intervals across other comparisons in the manuscript) also include the value of 0. This indicates there actually might be no multi-active zone synapses in the mouse dLGN. The failure arises because the low number of biological replicates (N=3 data points) precludes a reliable confidence interval measurement. CI measurements require sufficient sample sizes to determine the true population variance.

(3) Difficulty in achieving sufficient sample sizes for CI analysis in ultrastructural studies of the brain: volumetric STORM experiments are technically complex and make use of sample preparation and analysis methods that are similar to volumetric electron microscopy (physical ultrathin sectioning and computational 3D stack alignment). For these technical reasons, it is difficult to collect imaging data from >10 mice for each group of data (e.g. age and tissue location) in one single project. Because of the technical challenges, most ultrastructural studies published to date present results from single biological replicates. In our STORM dataset, we collected imaging data of N=3 biological replicates for each age and genotype. We agree that in the future the collection of additional replicates will be important for improving the reliability of statistical comparisons in super-resolution and electron-microscopy studies. Continued advances in the throughput of imaging/analysis should help to make this easier over time. 

(4) The use of paired T-tests: In this study, we have eye-specific CTB(+) and CTB(-) synapse imaging data from the same STORM fields within single biological replicates. When there is only one measurement from each replicate (e.g. synapse density, ratio of total synapses), using paired tests to compare these groups increases statistical power and does not assume similar variance. However, this limits our analysis to comparisons within each age, and not between ages. Accordingly, we have revised our discussion of the results and interpretations throughout the manuscript. When there are thousands of measurements of synapses from each replicate (e.g. Figure 2A-B on synapse volumes), we use a mixed linear model to analyze the variance. In the revised figures we present the results using standard error of the mean and link measurements from within the same individual replicates to show the paired data structure. In cases where specific comparisons are made across ages, we present 5/95% confidence interval measurements.

Claim 2: The fraction of multiple-active zone vGlut2 clusters increases with age. This claim is weakly supported by a qualitative reading of panel 1E. The error bars overlap so it is difficult to know what the range of possible increases could be. In the text, the authors report mean differences without confidence intervals (or any other statistics). The reported results should, therefore, be interpreted as a description of their three mice and not as evidence about mice in general.

We appreciate the reviewer’s concern that statistical accuracy of our synapse density comparisons over age is limited by the small sample size as discussed above. We have removed all strong claims about age-dependent changes in the density of multi-active zone and single-active zone synapses. Instead, we focus our analyses on comparisons between CTB(+) and CTB(-) synapse measurements, which are paired within each biological replicate. To specifically address the reviewer’s concern about figure panel 1E, we present Author response image 2 with confidence intervals below.

Author response image 2.

Figure S1. Panel A makes the point that the study could not be done without STORM by comparing the STORM images to "Conventional" images. The images are over-saturated low-resolution images. A reasonable comparison would be to a high-quality quality confocal image acquired with a high NA objective (~1.4) and low laser power (PSF ~ 0.2 x 0.2 x 0.6 um) that was acquired over the same amount of time it takes to acquire a STORM volume.

We agree with the reviewer that the presentation of low-resolution conventional images is not necessary. We have deleted the panel and modified the text accordingly.

Result section 2.

Claim 1: The ipsi/contra (in contra LGN) difference in VGluT2 cluster volume increases with development. While there are many p-values listed, the main point is not directly quantified. A reasonable way to quantify the relative increase in volume could be in the form: the non-dominant volumes were 75%-95%(?) of the dominant volume at P2 and 60%-80% (?) at P8. The difference in change was -5 to 15%(?).

We thank the reviewer for their helpful suggestion to improve the clarity of the results presented in this analysis of eye-specific synapse volumes. In our original report, we found differences in eye-specific VGluT2 volume at each time point (P2/P4/P8) in control mice (1). The original measurements used the entire synapse population. Here, we aimed to determine whether eye-specific differences in VGluT2 volumes were present for both multi-AZ synapses and single-AZ synapses, and whether one population may have a greater contribution to the previous population measurement that we reported. We found that at P4 (a time when the overall eye-specific synapse density is equivalent for both eyes in the dLGN), WT multi-AZ synapses showed a greater difference (372%) in eye-specific VGluT2 volume compared with single-AZ synapses (135%). In β2KO mice multi-AZ synapses showed a greater difference (110%) in eye-specific VGluT2 volume compared with single-AZ synapses (41%). In our initial manuscript submission, we included statistical comparisons of eye-specific volume differences across ages, but we did not highlight these differences in our discussion of the results. For clarity, we have removed all statistical comparisons across ages in the revised manuscript. We have modified the text to focus on eye-specific VGluT2 volume differences at P4 described above. To specifically address the reviewer’s question, we provide the percentage differences between multi- and single-AZ eye-specific synapses for each age/genotype below:

Author response table 1.

Claim 2: Complex synapses (vGlut2 clusters with multiple active zones) represent clusters of simple synapses and not single large boutons with multiple active zones. The authors argue that because vGlut2 cluster volume scales roughly linearly with active zone number, the vGlut2 clusters are composed of multiple boutons each containing a single active zone. Their analysis does not rule out the (known to be true) possibility that RGC bouton sizes are much larger in boutons with multiple active zones. The correlation of volume and active zone number, by itself, does not resolve the issue. A good argument for multiple boutons might be that the variance is smallest in clusters with 4 active zones (looks like it in the plot) since they would be the average of four active zones to vesicle pool ratios. It is very likely that the multi-active zone vGlut2 clusters represent some clustering and some multi-synaptic boutons. The reference cited by the authors as evidence for the presence of single active zone boutons in young tissue does not rule out the existence of multiple active zone boutons.

We agree with the reviewer’s comments on the challenges of classifying multi-active zone synapses in STORM images as single terminals versus aggregates of terminals. To help address this, we have performed electron microscopy imaging of genetically labeled RGC axons and identified the existence of single retinogeniculate terminals with multiple active zones. Our EM imaging was limited to 2D sections and does not rule out the clustering of small, single- active zone synapses within 3D volumes. Future volumetric EM reconstructions will be informative for this question. We have significantly updated the figures and text to discuss the new results and provide a careful interpretation of the nature of multi-AZ synapses in STORM imaging data. 

Several arguments are made that depend on the interpretation of "not statistically significant" (n.s.) meaning that "two groups are the same" instead of "we don't know if they are different". This interpretation is incorrect and materially impacts the conclusions.

Several arguments are made that interpret statistical significance for one group and a lack of statistical significance for another group meaning that the effect was bigger in the first group. This interpretation is incorrect and materially impacts the conclusions.

We thank the reviewer for raising these concerns. We have extensively revised the manuscript text to report the data in a more precise way without overinterpreting the results. All references to “N.S.” and associated conclusions have been either removed or substantiated with 5/95% confidence interval testing.

Result Section 3.

Claim 1: Complex synapses stabilize simple synapses. There are alternative explanations (mentioned above) for the observed clustering that negate the conclusions. 1) Boutons from the same axon tend to be found near one another. 2) Any form of eye-specific segregation would produce non-random associations in the analysis as performed. The authors compare each observation to a random model, but I cannot determine from the text if the model adequately accounts for alternative explanations.

We thank the reviewer for their suggestion to consider alternative explanations for our results. We agree that our study does not provide direct molecular mechanistic data demonstrating synaptic stabilization effects. We have significantly revised the manuscript to be more cautious in our interpretations and specifically address alternative biological mechanisms that are consistent with the non-random arrangement of retinogeniculate synapses in our data.

We agree with the reviewer that individual RGC axons form multiple synapses, however, nascent synapses might not always form close together. If synapses are initially added randomly within RGC axons, eye-specific segregation may conclude with a still-random pattern of dominant-eye inputs. At some later stage, synapses may be selectively refined to produce mature glomeruli. Consistent with this, individual RGCs undergo progressive clustering of axonal boutons at later stages of development after eye-specific segregation (5). One of our goals in this work was to determine if the process of synaptic clustering begins at the earliest stages of synapse formation and, if so, whether it is influenced by retinal wave activity.

To measure synaptic clustering in our STORM data, we used a randomization of single-AZ synapse centroids within the volume of the neuropil after accounting for neuronal soma volumes and edge effects. Multi-AZ centroid positions were held fixed. Comparing the randomized result to the original distribution, we found a higher fraction of single-AZ synapse associated with multi-AZ synapses, arguing for a non-random clustering effect. However, we agree with the reviewer’s concern that this type of randomization cannot account for the fine scale structure of axons, which we did not have access to in this four-color volumetric super-resolution data set. Thus, there could still be errors in a purely volumetric randomization (e.g. the assignment of synapses to regions in the volume that would not be synaptic locations in the original neuropil), which would effectively decrease the measured degree of clustering after the randomization. To address this, we have revised our analysis to measure the degree of synapse clustering nearby both multi-AZ and single-AZ synapses after an equivalent randomization of single-AZ synapse positions in the volume. 

We now present the revised results as a “clustering index” for both multi-AZ and single-AZ synapses. This measurement was performed in several steps: 1) randomization of single-AZ position with the imaging volume while holding multi-AZ centroid positions fixed, 2) independent measurements of the fraction of single-AZ synapses within the local shell (1.5 μm search radius) around multi-AZ and single-AZ synapses within the random distribution, 3) comparison of the result from (2) with the actual fractional measurements in the raw STORM data to compute a “clustering index” value. 4) Because the randomization is equivalent for both multi-AZ and single-AZ synapse measurements, any measured differences in the degree of clustering reflect the synapse type.

We have updated Figure 3 in the revised manuscript to present the relative clustering index described above. We have updated the results, discussion, and methods sections accordingly.

The authors claim that specificity increases over time. Figure 3b (middle) shows that the number of synapses near complex synapses might increase with time (needs confidence interval for effect size), but does not show that specificity (original relative to randomized) increases with time. The fact that nearby simple synapse density is always (P2) very different from random suggests a primarily non-activity-dependent explanation. The simplest explanation is that same-side boutons could be from the same axon whereas different-side axons could not be.

We have significantly revised the analysis and presentation of results in Figure 3 to include a comparative measurement of synaptic clustering between multi-AZ and single-AZ synapses (discussed above). The data presented in the original Figure 3B have been moved to Supplemental Figure 4. Statistical comparisons in Figure S4 between the original and randomized synapse distributions are limited to within-age measurements. Cross-age comparisons were not performed or presented. To address the reviewer’s question concerning CI analysis in the original Figure 3B, we provide Author response image 3 below showing 5/95% confidence intervals for WT mice:

Author response image 3.

Claim 2: vGlut2 clusters more than 1.5 um away from multi-active zone vGlut2 clusters are not statistically significantly different in size than vGlut2 clusters within 1.5 um of multi-active zone vGlut2 clusters. Therefore "activity-dependent synapse stabilization mechanisms do not impact simple synapse vesicle pool size". The specific measure of 1.5 um from multi-active zone vGlut2 clusters does not represent all possible synapse stabilization mechanisms.

We agree with the reviewer that this specific measure does not capture all possible synapse stabilization mechanisms. We have modified the text in the revised manuscript throughout to be more cautious in our data interpretation and have included additional discussion of alternative mechanisms consistent with our results.

Result Section 4.

Claim: The proximity of complex synapses with nearby simple synapses to other complex synapses with nearby simple synapses from the same eye is used to argue that activity is responsible for all this clustering.

It is difficult to derive anything from the quantification besides 'not-random'. That is a problem because we already know that axons from the left and right eye segregate during the period being studied. All the measures in Section 4 are influenced by eye-specific segregation. Given this known bias, demonstrating a non-random relationship (P<X) doesn't mean anything. The test will reveal any non-random spatial relationship between same-eye and opposite-eye synapses.

The results can be stated as: If you are a contralateral complex synapse, contralateral complex synapses that are also close to contralateral simple synapses will, on average, be slightly closer to you than contralateral complex synapses that are not close to contralateral ipsilateral synapses. That would be true if there is any eye-specific segregation (which there is).

We appreciate the reviewer’s comments that our anatomical data are consistent with several possible mechanisms, suggesting the need for alternative interpretations of the results. In the original writing, we interpreted our results in the context of activity-dependent mechanisms of like-eye stabilization and opposite-eye competition. However, our results are also consistent with other mechanisms, including non-random molecular specification of eye-specific inputs onto subregions of postsynaptic target cells (e.g. distinct relay neuron dendrites). We have rewritten the manuscript to be more cautious in our interpretations and to provide a balanced discussion of alternative possibilities.

Regarding the concern that the data in section four are influenced by eye-specific segregation, we previously found synapse density from both eyes is equivalent in the contralateral region at the P4 time point presented (1), which is consistent with binocular axonal overlap at this age. Within our imaging volumes, ipsilateral and contralateral inputs were broadly intermingled throughout the volume, and we did not find evidence for regional segregation with the imaging fields. By these metrics, retraction of ipsilateral inputs from the contralateral territory has not yet occurred.

It is an overinterpretation of the data to claim that the lack of a clear correlation between vGlut2 cluster volume and distance to vGlut2 clusters with multiple active zones provides support for the claim that "presynaptic protein organization is not influenced by mechanisms governing synaptic clustering".

We agree with the reviewer that our original language was imprecise in referring to presynaptic protein organization broadly. We have revised this text to present a more accurate description of the results.

Reviewer #2 (Public Review):

In this manuscript, Zhang and Speer examine changes in the spatial organization of synaptic proteins during eye-specific segregation, a developmental period when axons from the two eyes initially mingle and gradually segregate into eye-specific regions of the dorsal lateral geniculate. The authors use STORM microscopy and immunostain presynaptic (VGluT2, Bassoon) and postsynaptic (Homer) proteins to identify synaptic release sites. Activity-dependent changes in this spatial organization are identified by comparing the β2KO mice to WT mice. They describe two types of presynaptic organization based on Bassoon clustering, the complex and the simple synapse. By analyzing the relative densities and distances between these proteins over age, the authors conclude that the complex synapses promote the clustering of simple synapses nearby to form the future mature glomerular synaptic structure.

Strengths:

The data presented is of good quality and provides an unprecedented view at high resolution of the presynaptic components of the retinogeniculate synapse during active developmental remodeling. This approach offers an advance to the previous mouse EM studies of this synapse because of the CTB label allows identification of the eye from which the presynaptic terminal arises. Using this approach, the authors find that simple synapses cluster close to complex synapses over age, that complex synapse density increases with age.

Weaknesses:

From these data, the authors conclude that the complex synapse serves to "promote clustering of like-eye synapses and prohibit synapse clustering from the opposite eye". However, the authors show no causal data to support these ideas. There are a number of issues that the authors should consider:

(1) Clustering of retinal synapses is in part due to the fact that retinal inputs synapse on the proximal dendrites. With increased synaptogenesis, there will be increased density of retinal terminals that are closely localized. And with development, perhaps simple synapses mature into complex synapses. Simple synapses may also represent ones that are in the process of being eliminated as previously described by Campbell and Shatz, JNeurosci 1992 (consider citing). Can the authors distinguish these scenarios from the ones that they conclude?

We thank the reviewer for their thoughtful commentary and suggestions to improve our manuscript. We agree with the reviewer that our original interpretation of synaptic clustering by activity-dependent stabilization and punishment mechanisms is not directly supported by causal data. We have extensively revised the manuscript to take a more cautious view of the results and to discuss alternative mechanisms that are consistent with our data.

During eye-specific circuit development, there is indeed increased synaptogenesis and, ultimately, RGC terminals are closely clustered within synaptic glomeruli. This process involves the selective addition and elimination of synapses. Bouton clustering has been shown to occur within individual RGC axons after eye-opening in the mouse (5). The convergence of other RGC types into clustered boutons has been shown at eye-opening by light and electron microscopy (3). There is also qualitative evidence that synaptic clusters may form earlier during eye-specific segregation in the cat (4). Our data provide additional evidence that synaptic clustering begins prior to eye-opening in the mouse (P2-P8). Although synapse numbers also increase during this period, the distribution of synapse addition is non-random. 

Single-active zone synapses (we previously called these “simple”) may indeed mature into multi-active zone synapses (we previously called these “complex”). At the same time, single-active zone synapses may be eliminated. We believe that each of these events occurs as part of the synaptic refinement process. Our STORM images are static snapshots of eye-specific refinement, and we cannot infer the dynamic developmental trajectory of an individual synapse in our data. Future live imaging experiments in vivo/in situ will be needed to track the maturation and pruning of individual connections. We have expanded our discussion of these limitations and future directions in the manuscript.

(2) The argument that "complex" synapses are the aggregate of "simple" synapses (Fig 2, S2) is not convincing.

We agree with the reviewer’s concern about the ambiguous identity of complex synapses. To clarify the nature of multi-active zone synapses, we have performed RGC-specific dAPEX2 labeling to visualize retinogeniculate terminals by electron microscopy (EM). These experiments revealed the presence of synaptic terminals with multiple active zones. We have added images and text to the results section describing these findings. Our 2D EM images do not rule out the possibility that some multi-active zone synapses observed in STORM images are in fact clusters of individual RGC terminals. We have revised the text to provide a more accurate discussion of the nature of multi-active zone synapses.  

(3) The authors use of the β2KO mice to assess changes in the organization of synaptic proteins in retinal terminals that have disrupted retinal waves. However, β2-nAChRs are also expressed in the dLGN and other areas of the brain and glutamatergic synapse development has been reported in the CNS independent of the disruption in retinal waves. This issue should be considered when interpreting the total reduced retinal synapse density in the dLGN of the mutant.

We thank the reviewer for their suggestion to consider non-retinal effects of the germline deletion of the beta 2 subunit of the nicotinic acetylcholine receptor. Previously, Xu and colleagues reported the development of a conditional transgenic mouse model lacking β2-nAChR expression specifically in the retina (6). These retina-specific β2-nAChR mutant mice (Rx-β2cKO) have disrupted retinal wave properties and defects in eye-specific axonal segregation in binocular anterograde tracing experiments. This work suggests that the defects seen in germline β2-nAChR KO mice arise from defects in retinal wave activity rather than the loss of nicotinic receptors elsewhere in the brain. Additionally, the development of brainstem cholinergic inputs to the dLGN is delayed until the closure of the eye-specific segregation period (7), further suggesting a limited role for cholinergic transmission in the retinogeniculate refinement process.

(4) Outside of a total synapse density difference between WT and β2KO mice, the changes in the spatial organization of synaptic proteins over development do not seem that different. In fact % simple synapses near complex synapses from the non-dominant eye in the mutant is not that different from WT at P8 (Fig 3C), an age when eye-specific segregation is very different between the genotypes. Can the authors explain this discrepancy?

We thank the reviewer for their question concerning differences between synapse organization in WT versus β2KO mice. In the original presentation of Figure 3C at P4, the percentage of non-dominant eye single-AZ synapses near multi-AZ synapses increased at P4 in WT mice, but this did not occur in β2KO mice. This is consistent with our previous results showing that there is an increase in non-dominant eye synaptic density at this age, which does not occur in β2KO mice (1). At P8, this clustering effect is lost in WT as eye-specific segregation has taken place and non-dominant eye inputs have been eliminated. However, in β2KO mice, the overall synapse density is still low at this age. We interpret this result as a failure of synaptogenesis in the β2KO line, which leads to increased growth of individual RGC axons (8) and eye-specific overlap at P8 (9, 10). Evidence in support of this interpretation comes from live dynamic imaging studies of RGC axon branching in Xenopus and Zebrafish, showing that synapse formation stabilizes local axon branching and that disruptions of synapse formation or neurotransmission lead to enlarged axons (11-13).

Our anatomical results do not provide a specific biological mechanism for the remaining clustering observed in the β2KO mice. We have revised our discussion of the fact that individual RGC axons may form multiple synaptic connections leading to clustering, which may be independent of changes in retinal wave properties in the β2KO mouse. We have also extensively revised the analysis and presentation of results in Figure 3 to directly compare synaptic clustering around both multi-AZ synapses and single-AZ synapses within the same imaging volumes.

(5) The authors use nomenclature that has been previously used and associated with other aspects of retinogeniculate properties. For example, the phrases "simple" and "complex" synapses have been used to describe single boutons or aggregates of boutons from numerous retinal axons, whereas in this manuscript the phrases are used to describe vesicle clusters/release sites with no knowledge of whether they are from single or multiple boutons. Likewise, the use of the word "glomerulus" has been used in the context of the retinogeniculate synapse to refer to a specific pattern of bouton aggregates that involves inhibitory and neuromodulatory inputs. It is not clear how the release sites described by the authors fit in this picture. Finally the use of the word "punishment" is associated with a body of literature regarding the immune system and retinogeniculate refinement-which is not addressed in this study. This double use of the phrases can lead to confusion in the field and should be clarified by clear definitions of how they are used in the current study.

We appreciate the reviewer’s concern that the terminology we used in the initial submission may cause confusion. We have revised the text throughout for clarity. “Simple” synapses are now referred to as “single-active zone synapses”. “Complex” synapses are now referred to as “multi-active zone synapses”. We have removed all text that previously referred to synaptic clusters in STORM images as glomeruli. We agree that we have not provided causal evidence for synaptic stabilization and punishment mechanisms, which would require additional molecular genetic studies. We have restructured the manuscript to remove these references and discuss our anatomical results impartially.  

Reviewer #3 (Public Review):

This manuscript is a follow-up to a recent study of synaptic development based on a powerful data set that combines anterograde labeling, immunofluorescence labeling of synaptic proteins, and STORM imaging (Cell Reports 2023). Specifically, they use anti-Vglut2 label to determine the size of the presynaptic structure (which they describe as the vesicle pool size), anti-Bassoon to label a number of active zones, and anti-Homer to identify postsynaptic densities. In their previous study, they compared the detailed synaptic structure across the development of synapses made with contra-projecting vs ipsi-projecting RGCs and compared this developmental profile with a mouse model with reduced retinal waves. In this study, they produce a new analysis on the same data set in which they classify synapses into "complex" vs. "simple" and assess the number and spacing of these synapses. From these measurements, they make conclusions regarding the processes that lead to synapse competition/stabilization.

Strengths:

This is a fantastic data set for describing the structural details of synapse development in a part of the brain undergoing activity-dependent synaptic rearrangements. The fact that they can differentiate eye of origin is also a plus.

Weaknesses:

The lack of details provided for the classification scheme as well as the interpretation of small effect sizes limit the interpretations that can be made based on these findings.

We thank the reviewer for their reading of the manuscript and helpful comments to improve the work. We provide details on how single-active zone and multi-active zone synapses are classified in the methods section. We agree with the suggestion to be more careful in interpreting the results. We have extensively revised the manuscript to 1) include additional electron microscopy data demonstrating the presence of multi-active zone retinogeniculate synapses, 2) extend the synaptic clustering analysis to both single-active zone and multi-active zone synapses for comparison, and 3) improve the clarity and accuracy of the discussion throughout the manuscript.

(1) The criteria to classify synapses as simple vs. complex is critical for all of the analysis in this study. Therefore this criteria for classification should be much more explicit and tested for robustness. As stated in the methods, it is based on the number of active zones which are designated by the number of Bassoon clusters associated with a Vglut2 cluster (line 697). A second part of the criteria is the size of the presynaptic terminal as assayed by "greater Vglut2 signal" (line 116). So how are these thresholds determined? For Bassoon clusters, is one voxel sufficient? Two? If it's one, how often do they see a Bassoon positive voxel with no Vglut2 cluster and therefore may represent "noise"? There is no distribution of Bassoon volumes that is provided that might be the basis for selecting this number of sites. Unfortunately, the images are not helpful. For example, does P8 WT in Figure 1B have 7 or 2? According to Figure 2C, it appears the numbers are closer to 2-4.

The Vglut volume measurements also do not seem to provide a clear criterion. Figure 2 shows that the distributions of Vglut2 cluster volumes for complex and for simple synapses are significantly overlapping.

The authors need to clarify the quantitative approach used for this classification strategy and test how sensitive the results of the study are to how robust this strategy is

We thank the reviewer for their question concerning the STORM data analysis. Here we provide a brief overview of the complete analysis details, which are provided in the methods section.

Our raw STORM data sets consisted of spectrally separate volumetric imaging channels of VGluT2, Bassoon, and Homer1 signals. For each of these channels, raw STORM data were processed by 1) application of the corresponding low-resolution conventional image of each physical section to the STORM data to filter artifacts in the STORM image which do not appear in the conventional image, 2) STORM images are then thresholded using a 2-factor Otsu threshold that removes low-intensity background noise while preserving all single-molecule localizations that correspond to genuine antibody labeling as well as non-specific antibody labeling in the tissue, 3) application of the MATLAB function “conncomp” to identify connected component voxel in 3D across the image stack. Clusters are only kept for further analysis steps if they are connected across at least 2 continuous physical sections (140 nm Z depth). 4) for every connected component (clusters corresponding to genuine antibody labeling and background labeling), we measure the volume and signal density (intensity/volume) for every cluster in the dataset, 5) a threshold is applied to retain clusters that have a higher volume and lower signal density. We exclude signals that have low-volume and high-density, which correspond to single antibody labels. This analysis retains larger clusters that correspond to synaptic objects and excludes non-specific antibody background. 

The average size of WT synaptic Bassoon clusters ranges from 55 - 3532 voxels (0.00092~0.059 μm³), with a median size of 460 voxels (0.0077 μm³).

The average size of WT synaptic VGluT2 clusters ranges from 50 -73752 voxels (0.00084~1.2 μm³), with a median size of 980 voxels (0.016 μm³).

The average size of WT synaptic Homer1 clusters ranges from 63-7118 (0.0010~0.12 μm3), with a median size of 654 voxels (0.011 μm³).

In practice, any Bassoon/VGluT2/Homer1 clusters with <10 voxels are immediately filtered at the Otsu thresholding step (2) above.

The reviewer is correct that we often see Bassoon(+) clusters that are not associated with VGluT2, and these may reflect synapses of non-retinal origin or retinogeniculate synapses that lack VGluT2 expression. To identify retinogeniculate synapses containing VGluT2, we performed a synapse pairing analysis that measured the association between VGluT2 and Bassoon clusters after the synapse cluster filtering described above. We first measured the centroid-centroid distance from each VGluT2 cluster to the closest cluster in the Bassoon channel. We next quantified the signal intensity of the Bassoon channel within a 140 nm shell surrounding each VGluT2 cluster. A 2D histogram was plotted based on the measured centroid-centroid distances and opposing channel signal densities of each cluster. Paired clusters with closely positioned centroids and high intensities of apposed channel signal were identified using the OPTICS algorithm (14).

In the original Figure 1B, the multi-active zone synapse in WT at P8 had two Bassoon clusters. To clarify this, we have revised the images in Figure 1 to include arrowheads that point to individual active zones. We have also revised Supplemental Figure 1 to show volumetric renderings of individual example synapses that help illustrate the 3D structure of these multi-active zone inputs. All details about synapse analysis and synapse pairing are provided in the methods section.

(2) Effect sizes are quite small and all comparisons are made on medians of distributions. This leads to an n=3 biological replicates for all comparisons. Hence this small n may lead to significant results based on ANOVAS/t-tests, but the statistical power of these effects is quite weak. To accurately represent the variance in their data, the authors should show all three data points for each category (with a SD error bar when possible). They should also include the number of synapses in each category (e.g. the numerators in Figure 1D and the denominators for Figure 1E). For other figures, there are additional statistical questions described below.

We thank the reviewer for their suggestion to improve the presentation of our results. We have added all three data points (individual biological replicates) to each figure plot when applicable. We have also included a supplemental table (Table S1) listing total eye-specific synapse numbers of each type (mAZ and sAZ) and AZ number for each biological replicate in both genotypes.

(3) The authors need to add a caveat regarding their classification of synapses as "complex" vs. "simple" since this is a terminology that already exists in the field and it is not clear that these STORM images are measuring the same thing. For example, in EM studies, "complex" refers to multiple RGCs converging on the same single postsynaptic site. The authors here acknowledge that they cannot assign different AZs to different RGCs so this comparison is an assumption. In Figure 2 they argue this is a good assumption based on the finding that the Vglut column/active zone is constant and therefore each represents a single RGC. However, the authors should acknowledge that they are actually seeing quite different percentages than those in EM studies. For example, in Monavarfeshani et al, eLife 2018, there were no complex synapses found at P8. (Note this study also found many more complex vs. simple synapses in the adult - 70% vs. the 20% found in the current study - but this difference could be a developmental effect). In the future, the authors may want to take another data set in the adult dLGN to make a direct comparison based on numbers and see if their classification method for complex/simple maps onto the one that currently exists in the literature.

We appreciate the reviewer’s comment that the use of the terms “complex” and “simple” may cause confusion. We have significantly revised the manuscript for clarity: 1) we now refer to “complex” synapses as “multi-active zone synapses” and “simple” synapses as “single-active zone synapses. 2) We have performed electron microscopy analysis of dAPEX2-labeled retinogeniculate projections to confirm the existence of large synaptic terminals with multiple active zones. 3) We have expanded our discussion of previous electron microscopy results describing a lack of axonal convergence at P8 (3). 4) We have added a discussion on how individual RGCs may form multiple synapses in close proximity within their axonal arbor, which would create a clustering effect.

We agree that it will be informative to collect a STORM data set in the adult mouse dLGN and we look forward to working on this project to compare with EM results in the future.  

(4) Figure 3 assays the relative distribution of simple vs. complex synapses. They found that a larger percentage of simple synapses were within 1.5 microns of complex synapses than you would expect by chance for both ipsi and contra projecting RGCs, and hence conclude that complex synapses are sites of synaptic clustering. In contrast, there was no clustering of ipsi-simple to contra-complex synapses and vice versa. The authors also argue that this clustering decreases between P4 and P8 for ipsi projecting RGCs.

This analysis needs much more rigor before any conclusions can be drawn. First, the authors need to justify the 1.5-micron criteria for clustering and how robust their results are to variations in this distance. Second, these age effects need to be tested for statistical significance with an ANOVA (all the stats presented are pairwise comparisons to means expected by random distributions at each age). Finally, the authors should consider what n's to use here - is it still grouped by biological replicate? Why not use individual synapses across mice? If they do biological replicates, then they should again show error bars for each data point in their biological replicates. And they should include the number of synapses that went into these measurements in the caption.

We appreciate the suggestion to improve the rigor of our analysis of synaptic clustering presented in Figure 3. We have revised our analysis to measure the degree of synapse clustering nearby both multi-AZ and single-AZ synapses after an equivalent randomization of single-AZ synapse positions in the volume. 

We now present the revised results as a “clustering index” for both multi-AZ synapses and single-AZ synapses. This measurement was performed in several steps: 1) randomization of single-AZ positions within the imaging volume while holding multi-AZ centroid positions fixed, 2) independent measurements of the fraction of single-AZ synapses within the local shell (1.5 μm search radius) around multi-AZ and single-AZ synapses within the random distribution, 3) comparison of the result from (2) with the actual fractional measurements in the raw STORM data to compute a “clustering index” value. 4) Because the randomization is equivalent for both multi-AZ and single-AZ synapse measurements, the measured differences in the degree of clustering reflect a synapse type-specific effect.

We have also updated Supplemental Figure 3 showing the results of varying the search radius from 1-4 μm for both contralateral- and ipsilateral-eye synapses. The results showed that a search radius of 1.5 μm resulted in the largest difference between the original synapse distribution and a randomized synapse distribution (shuffling of single-active zone synapse position while holding multi-active zone synapse position fixed).

Finally, we have removed all statistical comparisons of single measurements (means or ratios) across ages from the manuscript. We focus our statistical analysis on paired data comparisons within individual biological replicates.

For the analysis of synapse clustering, we grouped the data by biological replicates (N=3) to look for a global effect on synapse clustering. In the revised manuscript, we added data points for each replicate in the figure and included the number of synapses in Supplementary Table 1.

(5) Line 211-212 - the authors conclude that the absence of clustered ipsi-simple synapses indicates a failure to stabilize (Figure 3). Yet, the link between this measurement and synapse stabilization is not clear. In particular, the conclusion that "isolated" synapses are the ones that will be eliminated seems to be countered by their finding in Figure 3D/E which shows that there is no difference in vesicle pool volume between near and far synapses. If isolated synapses are indeed the ones that fail to stabilize by P8, wouldn't you expect them to be weaker/have fewer vesicles? Also, it's hard to tell if there is an age-dependent effect since the data presented in Figures 3D/E are merged across ages.

We thank the reviewer for their suggestion to clarify the results in Figure 3. Based on the measured eye-specific differences in vesicle pool size and organization, we also expected that synapses outside of clusters would show a reduced vesicle population. However, across all ages, we found no differences in the vesicle pool size of single-active zone synapses based on their proximity to multi-active zone synapses. Below, we show cumulative distributions of these results across all ages (P2/P4/P8) for WT mice CTB(+) data. Statistical tests (Kolmogorov-Smirnov tests) show no significant differences. P = 0.880, 0.767, 0.494 respectively. Separate 5/95% confidence interval calculations showed overlap between far and near populations at each age.

Author response image 4.

To clarify the presentation of the results, we have changed the text to state that the “vesicle pool size of sAZ synapses is independent of their distance to mAZ synapses”. We have removed references to stabilization and punishment from the results section of the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Because none of the phenomena being measured can be expected to behave randomly (given what is already known about the system) and the sample size is small, I believe quantification of the data requires confidence intervals for effect sizes. Resolving the multi-bouton vs multi-active zone bouton with EM would also help.

We thank the reviewer for their thorough reading of the manuscript and many helpful suggestions. We provide analysis with confidence intervals in a point-by-point response below. In the manuscript we revised our results and focused our statistical analyses on comparisons within the same biological replicate (paired effects). In addition, we have performed electron microscopy of RGC inputs to the dLGN at postnatal day 8 to demonstrate the presence of retinogeniculate synapses with multiple active zones.

Figure 1:

Please show data points in scatter bar plots and not just error bars.

We have updated all plots to show data points for independent biological replicates.

Please describe the image processing in more detail and provide an image in which the degree of off-target labeling can be evaluated.

We have updated the description of the image processing in the methods sections. We have made all the code used in this analysis freely available on GitHub (https://github.com/SpeerLab). We have uploaded the raw STORM images of the full data set to the open-access Brain Imaging Library (16). These images can be accessed here: https://api.brainimagelibrary.org/web/view?bildid=ace-dud-lid (WTP2A data for example). All 18 datasets are currently searchable on the BIL by keyword “dLGN” or PI last name “Speer” and a DOI for the grouped dataset is pending.

How does panel 1D get very small error bars with N = 3? Please provide scatter plots.

We have updated panel 1D to show the means for each independent biological replicate.

Line 129: over what volume is density measured? What are the n's? What is the magnitude (with confidence intervals) of increase?

The volume we collected from each replicate was ~80μm*80μm*7μm (total volume ~44,800 μm3). N=3 biological replicates for each age, genotype, and tissue location. Because of concerns with the use of ANOVA for low sample numbers, we have removed a majority of the age-wise comparisons from the manuscript and instead focus on within-replicate paired data comparisons. Author response image 5 showa 5/95% confidence intervals for WT data (left panel) and β2KO data (right panel) is shown below:

Author response image 5.

The 5/95% CI range for the increase in synapse density from P2 to P8 for CTB(+) synapses is ~ -0.001 ~ 0.037 synapses / μm³.

Line 131: You say that non-dominant increases and then decreases. It appears that the error bars argue that you do not have enough information to reliably determine how much or little density changes.

Line 140: No confidence intervals. It appears the error bars allow both for the claimed effect of increased fraction and the opposite effect of decreased density.

Because of concerns with the use of ANOVA for low sample numbers, we have removed age-wise comparisons of single-measurements (means and ratios) from the manuscript and instead focus on within-replicate paired data comparisons.

Line 144: Confidence intervals would be a reasonable way to argue that fraction is not changed in KO: normal fraction XX%-XX%. KO fraction XX%-XX%.

Author response image 6 shows panels for WT (left) and β2KO mice (right) with 5/95% CIs.

Author response image 6.

In the revised manuscript, we have updated the text to report the measurements, but we do not draw conclusions about changes over development.

I find it hard to estimate magnitudes on a log scale.

We appreciate the reviewer’s concern with the presentation of results on a log scale. Because the measured synapse properties are distributed logarithmically, we have elected to present the data on a log scale so that the distribution(s) can be seen clearly. Lognormal distributions enable us to use a mixed linear model for statistical analysis.

Line 156: Needs confidence interval for difference.

Line 158: Needs confidence interval for difference of differences.

Line 160: Needs confidence interval for difference of differences.

Why only compare at P4 where there is the biggest difference? The activity hypothesis would predict an even bigger effect at P8.

Below is a table listing the mean volume (log10μm3) and [5/95%] confidence intervals for comparisons of VGluT2 signal between CTB(+) and CTB(-) synapses from Figure 2A and 2B:

Author response table 2.

Based on the values given above, the mean difference of differences and [5/95%] confidence intervals are listed below:

Author response table 3.

We added these values to the manuscript. We have also reported the difference in median values on a linear scale (as below) so that the readers can have a straightforward understanding of the magnitude.

Author response table 4.

We elected to highlight the results at P4 based on our previous finding that the synapse density from each eye-of-origin is similar at this time point (1).

At P8, there is a decrease in the magnitude of the difference between CTB(+)/CTB(-) synapses compared to P4. This may be due to an increase in VGluT2 volume within non-dominant eye synapses that survive competition between P4-P8.

At P8 in the mutant, there is an increase in the magnitude of the difference between CTB(+)/CTB(-) synapses compared to P4. This may be due to delayed synaptic maturation in β2KO mice.

Line 171: The correct statistical comparison was not performed for the claim. Lack of * at P2 does not mean they are the same. Why do you get the same result for KO?

We have revised the statistical analysis, figure presentation, and text to remove discussion of changes in the number of active zones per synapse over development based on ANOVA. We now report eye-specific differences at each time point using paired T-test analysis, which is mathematically equivalent to comparing the 5/95% confidence interval in the difference.

Line 175: Qualitative claim. Correlation coefficients and magnitudes of correlation coefficients are not reported.

Linear fitting slop and R square values are attached:

Author response table 5.

The values are added to the manuscript to support the conclusions.

Line 177: n.s. does not mean that you have demonstrated the values are the same. An argument for similarity could be made by calculating a confidence interval a for potential range of differences. Example: Complex were 60%-170% of Simple.

Author response image 7 with 5/95% CI is shown below (WT and B2KO):

Author response image 7.

Comparing the difference between multi-AZ synapse and single-AZ synapse revealed that the difference in average VGluT2 cluster volume per AZ is:

Author response table 6.

The values are added to the manuscript for discussion.

Line 178: There is no reason to think that the vesical pool for a single bouton does not scale with active zone number within the range of uncertainty presented here.

We have collected EM images of multi-AZ zone synapses and modified our discussion and conclusions in the revised text.

Line 196: "non-random clustering increased progressively" is misleading. The density of the boutons increases for both the Original and Randomized. Given the increase in variance at P8, it is unlikely that the data supports the claim that the non-randomness increased. Would be easy to quantify with confidence intervals for a measure of specificity (O/R).

We have revised the manuscript to remove analysis and discussion of changes in clustering over development. We have modified this section of the manuscript and figures to present a normalized clustering index that describes the non-random clustering effect present at each time point.

Line 209: Evidence is for correlation, not causation and there is a trivial potential explanation for correlation.

We appreciate the reviewer’s concern with over interpretation of the results. We have changed the text to more accurately reflect the data.

Line 238:239: Authors failed to show effect is activity-dependent. Near/Far distinction is not necessarily a criterion for the effect of activity. The claim is likely false in other systems.

We agree with the reviewer that the original text overinterpreted the results. We have changed the text to more accurately reflect the data. 

Line 265-266: Assumes previous result is correct and measure of vGlut2 provides information about all presynaptic protein organization.

We thank the reviewer for pointing out the incorrect reference to all presynaptic protein organization. We have corrected the text to reference only the VGluT2 and Bassoon signals that were measured.

Line 276: There are many other interpretations that include trivial causes. It is unclear what the measure indicates about the biology and there is no interpretable magnitude of effect.

We agree with the reviewer that the original text overinterpreted the results. We have changed the text to remove references to mechanisms of synaptic stabilization.

Line 289: Differences cannot be demonstrated by comparing P-values. Try comparing confidence intervals for effect size or generate a confidence interval for the difference between the two groups.

5/95% confidence intervals are given below for Figure 4C/D:

Author response table 7.

We have added these values to the manuscript to support our conclusion.

Line 305: "This suggests that complex synapses from the non-dominant-eye do not exert a punishment effect on synapses from the dominant-eye" Even if all the other assumptions in this claim were true, "n.s." just means you don't know something. It cannot be compared with an asterisk to claim a lack of effect.

We thank the reviewer for raising this concern. We have modified the text to remove references to synaptic punishment mechanisms in the results section.

Below are the 5/95% confidence intervals for the results in Figure 4F:

Author response table 8.

We have added these values to the manuscript to support our conclusion.

Line 308: "mechanisms that act locally". 6 microns is introduced based on differences in curves above(?). I don't see any analysis that would argue that longer-distance effects were not present.

The original reference referred to the differences in the cumulative distribution measurements between multi-active zone synapses versus single-active zone synapses in their distance to the nearest neighboring multi-active zone synapse. For clarity, we have deleted the reference to the 6 micron distance in the revised text.

Reviewer #2 (Recommendations For The Authors):

(1) This data set would be valuable to the community. However, unless the authors can show experiments that manipulate the presence of complex synapses to test their concluding claims, the manuscript should be rewritten with a reassessment of the conclusions that is more grounded in the data.

We thank the reviewer for their careful reading of the manuscript and we agree the original interpretations were not causally supported by the experimental results. We have made substantial changes to the text throughout the introduction, results, and discussion sections so that the conclusions accurately reflect the data.

(2) To convincingly address the claim that "complex synapse" are aggregates of simple synapses, the authors should perform experiments at the EM level showing what the bouton correlates are to these synapses.

We thank the reviewer for their suggestion to perform EM to gain a better understanding of retinogeniculate terminal structure. We generated an RGC-specific transgenic line expressing the EM reporter dAPEX2 localized to mitochondria. We have collected EM images of retinogeniculate terminals that demonstrate the presence of multiple active zones within individual synapses. These results are now presented in Figure 1. The text has been updated to reflect the new results.

(3) Experiments using the conditional β2KO mice would help address questions of the contribution of β2-nAChRs in dLGN to the synaptic phenotype.

We appreciate the reviewer’s concern that the germline β2KO model may show effects that are not retina-specific. To address this, Xu and colleagues generated a retina-specific conditional β2KO transgenic and characterized wave properties and defective eye-specific segregation at the level of bulk axonal tracing (6). The results from the conditional mutant study suggest that the main effects on eye-specific axon refinement in the germline β2KO model are likely of retinal origin through impacts on retinal wave activity. Additionally, anatomical data shows that brainstem cholinergic axons innervate the dLGN toward the second half of eye-specific segregation and are not fully mature at P8 when eye-specific refinement is largely complete (7). We agree with the reviewer that future synaptic studies of previously published wave mutants, including the conditional reporter line, would be needed to conclusively assess a contribution of non-retinal nAChRs. These experiments will take significant time and resources and we respectfully suggest this is beyond the scope of the current manuscript.

Reviewer #3 (Recommendations For The Authors):

(1) The authors need to be more transparent that they are using the same data set from the previous publication (right now it does not appear until line 471) and clarify what was found in that study vs what is being tested here.

We thank the reviewer for their thoughtful reading of the manuscript and helpful recommendations to improve the clarity of the work. We have edited the text to make it clear that this study is a reanalysis of an existing data set. We have revised the text to discuss the results from our previous study and more clearly define how the current analysis builds upon that initial work. 

(2) The authors restricted their competition argument in Figure 4 to complex synapses, but why not include the simple ones? This seems like a straightforward analysis to do.

We appreciate the reviewer’s suggestion to measure spatial relationships between “clustered” and “isolated” single-AZ synapses as we have done for multi-AZ synapses in Figure 4. However, we are not able to perform a direct and interpretable comparison with the results shown for multi-AZ synapses. First, we would need to classify “clustered” and “isolated” single-AZ synapses. This classification convolves two effects: 1) a distance threshold to define clustering and 2) subsequent distance measurements between clustered synapses.

If we apply an equivalent 1.5 μm distance threshold (or any other threshold) to define clustered synapses, the distance from each “clustered” single-AZ synapse to the nearest other single-AZ synapse will always be smaller than the defined threshold (1.5 μm). Alternatively, if all of the single-AZ synapses within each local 1.5 μm shell are excluded from the subsequent intersynaptic distance measurements, this will set a hard lower boundary on the distance between synaptic clusters (1.5 μm minimum). The two effects discussed above were separated in our original analysis of multi-AZ synapses defined as “clustered” and “isolated” based on their relationship to single-AZ synapses, but these effects cannot be separated when analyzing single-AZ distributions alone.

(3) The Discussion seems much too long and speculative from the current data that is represented - particularly without verification of complex synapses actually being inputs from different RGCs. Along the same lines, figure captions are misleading. For example, for Figure 4 - the title indicates that the complex synapses are driving the rearrangements. But of course, these are static images. The authors should use titles that are more reflective of their findings rather than this interpretation.

We thank the reviewer for these helpful suggestions. We have changed each of the figure captions to more accurately reflect the results. We have deleted all of the speculative discussion and revised the remaining text to improve the accuracy of the presentation.

(4) In the future, the authors may want to consider an analysis as to whether ipsi and contra projection contribute to the same synapses

We agree with the reviewer that it is of interest to investigate the contribution of binocular inputs to retinogeniculate synaptic clusters during development. At maturity, some weak binocular input remains in the dominant-eye territory (15). To look for evidence of binocular synaptic interactions, we measured the percentage of the total small single-active zone synapses that were within 1.5 micrometers of larger multi-active zone synapses of the opposite eye. On average, ~10% or less of the single-active zone synapses were near multi-active zone synapses of the opposite eye. This analysis is presented in Supplemental Figure S3C/D.

It is possible that some large mAZ synapses might reflect the convergence of two or more smaller inputs from the two eyes. Our current analyses do not rule this out. However, previous EM studies have found limited evidence for convergence of multiple RGCs (3) at P8 and our own EM images show that larger terminals with multiple active zones are formed by a single RGC bouton. Future volumetric EM reconstructions with eye-specific labels will be informative to address this question.

References

(1) Zhang C, Yadav S, Speer CM. The synaptic basis of activity-dependent eye-specific competition. Cell Rep. 2023;42(2):112085.

(2) Bickford ME, Slusarczyk A, Dilger EK, Krahe TE, Kucuk C, Guido W. Synaptic development of the mouse dorsal lateral geniculate nucleus. J Comp Neurol. 2010;518(5):622-35.

(3)Monavarfeshani A, Stanton G, Van Name J, Su K, Mills WA, 3rd, Swilling K, et al. LRRTM1 underlies synaptic convergence in visual thalamus. Elife. 2018;7.

(4) Campbell G, Shatz CJ. Synapses formed by identified retinogeniculate axons during the segregation of eye input. J Neurosci. 1992;12(5):1847-58.

(5) Hong YK, Park S, Litvina EY, Morales J, Sanes JR, Chen C. Refinement of the retinogeniculate synapse by bouton clustering. Neuron. 2014;84(2):332-9.

(6) Xu HP, Burbridge TJ, Chen MG, Ge X, Zhang Y, Zhou ZJ, et al. Spatial pattern of spontaneous retinal waves instructs retinotopic map refinement more than activity frequency. Dev Neurobiol. 2015;75(6):621-40.

(7) Sokhadze G, Seabrook TA, Guido W. The absence of retinal input disrupts the development of cholinergic brainstem projections in the mouse dorsal lateral geniculate nucleus. Neural Dev. 2018;13(1):27.

(8) Dhande OS, Hua EW, Guh E, Yeh J, Bhatt S, Zhang Y, et al. Development of single retinofugal axon arbors in normal and beta2 knock-out mice. J Neurosci. 2011;31(9):3384-99.

(9) Rossi FM, Pizzorusso T, Porciatti V, Marubio LM, Maffei L, Changeux JP. Requirement of the nicotinic acetylcholine receptor beta 2 subunit for the anatomical and functional development of the visual system. Proc Natl Acad Sci U S A. 2001;98(11):6453-8.

(10) Muir-Robinson G, Hwang BJ, Feller MB. Retinogeniculate axons undergo eye-specific segregation in the absence of eye-specific layers. J Neurosci. 2002;22(13):5259-64.

(11) Fredj NB, Hammond S, Otsuna H, Chien C-B, Burrone J, Meyer MP. Synaptic Activity and Activity-Dependent Competition Regulates Axon Arbor Maturation, Growth Arrest, and Territory in the Retinotectal Projection. J Neurosci. 2010;30(32):10939.

(12) Hua JY, Smear MC, Baier H, Smith SJ. Regulation of axon growth in vivo by activity-based competition. Nature. 2005;434(7036):1022-6.

(13) Rahman TN, Munz M, Kutsarova E, Bilash OM, Ruthazer ES. Stentian structural plasticity in the developing visual system. Proc Natl Acad Sci U S A. 2020;117(20):10636-8.

(14) Ankerst M, Breunig MM, Kriegel H-P, Sander J. OPTICS: ordering points to identify the clustering structure. SIGMOD Rec. 1999;28(2):49–60.

(15) Bauer J, Weiler S, Fernholz MHP, Laubender D, Scheuss V, Hübener M, et al. Limited functional convergence of eye-specific inputs in the retinogeniculate pathway of the mouse. Neuron. 2021;109(15):2457-68.e12.

(16) Benninger K, Hood G, Simmel D, Tuite L, Wetzel A, Ropelewski A, et al. Cyberinfrastructure of a Multi-Petabyte Microscopy Resource for Neuroscience Research.  Practice and Experience in Advanced Research Computing; Portland, OR, USA: Association for Computing Machinery; 2020. p. 1–7.

Author response:

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

We thank the reviewers for their overall careful evaluation of our work, the constructive criticism, and their many helpful suggestions. We feel that our revision built on the strengths identified by the reviewers, and addressed all the concerns they have raised. Both reviewers recognize that our revisions have improved the paper.  Since the first submission we have:

• Rewritten large parts of the papers to improve clarity and make it more concise where possible

• Simulated an alternative working memory model, as recommended by Reviewer 1

• Included 4 new/revised supplementary figures, following the reviewer’s suggestions for additional analysis.

Below we provide a brief response to the Reviewers’ comments on our manuscript revision.

Reviewer #1: Public Review:

Strengths:

Overall, the work offers a very interesting approach of a topic which is hard to accomplish experimentally --therefore the computational take is entirely justified and extremely useful. The authors carefully designed the computational experiments to shed light into the demyelination effects on working memory from multiple levels of description, increasing the reliability of their conclusions. I think this work provides now convincing evidence and has the potential to be influential in future studies of myelin alterations (and related disorders such as multiple sclerosis).

Weaknesses:

In its current form, the authors have improved the clarity of the results and the model details, and have provided a new set of simulations to complement and reinforce the original ones (including the development of a new spatial working memory model based on silent working memory principles). I do not appreciate any significant weaknesses at this point.

We thank the reviewer for these positive comments on our revision and for the suggestion of adding the silent memory model, as we feel this has strengthened our findings.

Reviewer #2: Public Review:

This paper analyzes the effect of axon de-myelination and re-myelination on action potential speed, and propagation failure. Next, the findings are then incorporated in a standard spiking ring attractor model of working memory.

I think the results are not very surprising or solid and there are issues with method and presentation.

The authors did many simulations with random parameters, then averaged the result, and found for instance that the Conduction Velocity drops in demyelination. It gives the reader little insight into what is really going on. My personal preference is for a well understood simple model rather than a poorly understood complex model. The link between the model outcome of WM and data remains qualitative and is further weakened by the existence of known other age-related effects in PFC circuits.

Comments on revised version:

The paper has improved in the revision, although I still think a reduced model would have been nice.

As noted above, in addition to our spiking bump attractor model, our revision includes a second network-level model:  an activity-silent working memory model for continuous features.  We found qualitatively similar effects as in our bump attractor network model, showing that our main conclusions do not critically depend on the exact working memory mechanism (active vs. activity-silent).  This new model was described in two new supplementary figures and a new paragraph in the Results section.

We did not add a reduced model in our revision to this paper, since neither reviewer explicitly recommended that we add one.  As we noted in our private response to reviewers that accompanied our revision: we share the view that understanding simple models can provide critical insights into brain function (and we believe that many of our papers related to attractor dynamics in working memory and decision-making fall into this category, e.g. Wimmer et al. 2014, Esnaola-Acebes et al. 2022, Ibañez et al 2020). We disagree with the reviewer on an important point: we feel that the model complexity that we have chosen is appropriate and necessary to study the phenomenon at hand. Our modeling efforts are principled, with complexity added as necessary. We started with a biophysical single neuron model with firing dynamics fit to empirical data in pyramidal neurons of rhesus monkey dlPFC (Rumbell et al. 2016) – the same type of neurons and cortical region analyzed in the Peters et al. work on structural changes to myelin seen during aging (e.g., Figure 1).  Because simple models do not accurately capture the CV along thin axons like those in the PFC, we attached a multicompartment axon with detailed myelinated segments, and constructed a cohort of feasible models. We then used this cohort to get quantitative estimates of the effects of variable degrees of demyelination and remyelination. This would not be possible with a simpler model. We then study the consequences of de- and re-myelination in a spiking neural network model. Again, we could not use a simpler model (e.g. a firing rate attractor model) without making gross assumptions about how demyelination affects circuit function. In sum, we believe that our models are relatively simple but comprehensive given the phenomenon that we are studying.

The reviewer is correct in that there exist “known other age-related effects in PFC circuits”. These are reviewed in the introduction and we discuss future extensions of our model that would incorporate those effects as well. It is important to note that this is the first comprehensive study of demyelination effects in aging PFC, demonstrating that myelin changes alone predict working memory changes associated with aging.

While we agree that averaging results about different parameter sets provide a limited understanding of the system, we persist in our belief that such analyses provide an important baseline.  We acknowledge that results vary across our model cohort; this is why we included the heatmaps of our single cell model perturbation results (Figure 3 and Supplementary Figure 3), and simulated network models representing a heterogeneity of neuronal axons with healthy and altered myelin sheaths in different degrees, as likely occurs in the aging brain (Figures 7 and 8).  The model framework we present here is well-suited for more targeted analyses and better insights, including those which we are pursuing currently.

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

We thank the reviewers for their careful evaluation of our work, the constructive criticism, and their many helpful suggestions. We feel that our revision builds on the strengths identified by the reviewers, and addresses all the concerns they have raised. We have:

• Rewritten large parts of the papers to improve clarity and make it more concise where possible

• Simulated an alternative working memory model

• Included 4 new/revised supplementary figures, following the reviewer’s suggestions for additional analysis

Reviewer #1 (Public Review):

Summary:

The authors study the effects of myelin alterations in working memory via the complementary use of two computational approaches: one based on the de- and re-myelination in multicompartmental models of pyramidal neurons, and one based on synaptic changes in a spiking bump attractor model for spatial working memory. The first model provides the most precise angle (biophysically speaking) of the different effects (loss of myelin lamella or segments, remyelination with thinner and shorter nodes, etc), while the second model allows to infer the consequences of myelin alterations in working memory performance, including memory stability, duration, and bump diffusion. The results indicate (i) a slowing down and failure of propagation of spikes with demyelination and partial recovery with remyelination, with detailed predictions on the role of nodes and myelina lamella, and (ii) a decrease in memory duration and an increase in memory drift as a function of the demyelination, in agreement with multiple experimental studies.

Strengths:

Overall, the work offers a very interesting approach of a topic which is hard to accomplish experimentally --therefore the computational take is entirely justified and extremely useful. The authors carefully designed the computational experiments to shed light into the demyelination effects on working memory from multiple levels of description, increasing the reliability of their conclusions. I think this work is solid and has the potential to be influential in future studies of myelin alterations (and related disorders such as multiple sclerosis).

We thank the reviewer for these positive comments on our manuscript.

Weaknesses:

In its current form, the study still presents several issues which prevent it from achieving a higher potential impact. These can be summarized in two main items. First, the manuscript is missing some important details about how demyelination and remyelination are incorporated in both models (and what is the connection between both implementations). For example, it is unclear whether an unperturbed axon and a fully remyelinated axon would be mathematically equivalent in the multicompartment model, or how the changes in the number of nodes, myelin lamella, etc, are implemented in the spiking neural network model.

We thank the reviewer for these suggestions to improve the clarity of our manuscript. A ‘fully remyelinated’ axon is not mathematically equivalent to the unperturbed axon: it has shorter and thinner myelinated segments, and additional nodes in between. This is consistent with empirical observations in rhesus monkey dlPFC, as reviewed in Peters et al. (2009): a 90% increase in paranode profiles, and myelin sheaths that were thinner than expected for the size of the enclosed axon. With no empirical observations of fewer numbers of nodes (but rather, the opposite) or bare sections of axon, we assumed that the remyelination process also creates new nodes (which are identical to existing nodes), as also modeled in Scurfield & Latimer (2018). We have added two new sentences to the results to clarify this fact, before presenting the first set of results for the single cell model: (starting at line 137):

“To simulate demyelination, we removed lamellae from selected myelinated segments; for remyelination we replaced a fraction of myelinated segments by two shorter and thinner segments with a node in between. As such, a ‘fully remyelinated axon’ had all the demyelinated segments subsequently remyelinated, but with fewer lamellae and additional nodes compared to the unperturbed control case, consistent with empirical observations (Peters, 2009).”

We also state the maximal amount of remyelination more explicitly in the Results, starting on lines 164-165: "We next examined the extent to which remyelination with shorter and thinner segments, occurring after demyelination, restored axonal AP propagation (Figure 4).”

Also on line 192-193: “Remyelinating all affected segments with 75% of lamellae (the maximal amount of remyelination) nearly eliminated AP failures (1.8 ± 1.1%).”

Finally, in Methods we also clarified the structure of the added node (starting at line 634): “Remyelination was performed by replacing an affected (previously demyelinated) segment with two shorter segments, each including paranodes, juxtaparanodes, and an internode, and a new node between them that was identical to existing nodes.”

We have also provided further details describing how myelin dystrophy was simulated in the network model in Results (lines 243 - 249) and in Methods (lines 722 - 747). How myelin alterations have been implemented in the network model is one of the questions of the reviewer (Question 5 in Reviewer #1: Recommendations for the Authors_)._ We have addressed this question by describing in detail how we adjusted CV and AP failure rate to the values produced by the multicompartment neuron model. Please see our answer to Question 5 for the details.

Second, it is unclear whether some of the conclusions are strong computational predictions or just a consequence of the model chosen. For example, the lack of effect of decreasing the conduction velocity on working memory performance could be due to the choice of considering a certain type of working memory model (continuous attractor), and therefore be absent under other valid assumptions (i.e. a silent working memory model, which has a higher dependence on temporal synaptic dynamics).

Whether some conclusions are strong predictions or just a consequence of the model chosen is an important concern and indeed a general problem of computational modeling of working memory. For example, Stein et al. (Stein et al. Towards biologically constrained attractor models of schizophrenia, Curr. Opin. Neurobiol. 2021) showed that opposed manipulations of E/I ratio can produce the same behavioral pattern in different alternative, plausible biological network models. As long as we do not fully understand the neural mechanisms underlying working memory, modeling studies of how alterations (e.g. in E/I ratio or in the reliability and timing of axonal transmission, as we did here) affect circuit function need to be interpreted critically and tested against new experimental data.

One way to strengthen model predictions is by showing that different computational models make similar predictions. To do this, we implemented an activity-silent working memory model for continuous features, as suggested by the reviewer, and we found qualitatively similar effects as in our bump attractor network model. Thus, our main conclusions do not critically depend on the exact working memory mechanism (active vs. activity-silent).

In the revised manuscript, we have added two new supplementary figures (Supplementary Figure 8 and 9, see the next page) and a new paragraph in the Results section about activity silent working memory (starting at line 319):

“Alternative working memory mechanisms. Working memory in our neural network is maintained in an attractor state with persistent neural activity (Compte et al., 2000; Hansel and Mato, 2013). Other mechanisms have been proposed, including that working memory maintenance may rely on activity-silent memory traces (Mongillo et al., 2008; Stokes, 2015; Barbosa et al., 2020). In activity-silent models, a slowly decaying transient of synaptic efficacy preserves information without the need for persistent ongoing activity. We implemented an activity-silent model, to our knowledge the first one for continuous spatial locations, and tested how working memory performance is affected by AP failures and propagation delays. We found that AP failures corresponding to demyelination caused working memory errors qualitatively similar to the delay-active network (Supplementary Figure 8). On the other hand, increasing propagation delays did not lead to additional working memory errors, unless we include unrealistically high values (uniform distribution in the range of 0 to 100 ms; Supplementary Figure 9). These results are qualitatively similar to the delay active network model. Thus, our main findings do not critically depend on the exact working memory mechanism (active vs. activity-silent).”

Author response image 1.

Action potential failures impair working memory performance in a network model with activity-silent memory traces. (A) Spiking and synaptic activity in an unperturbed, activity-silent working memory model. Top: Raster plot showing the activity for each excitatory neuron (labeled by its preferred direction) in a single trial with a cue stimulus presented at 180°. We modified our spiking neural network model such that it does not show elevated persistent firing throughout the delay period (see Figure 5B for comparison). In particular, we reduced the external background input to excitatory neurons by a factor of 3.61% and we increased the cue stimulus amplitude by 12.5%. Even though spiking activity decays to baseline (close to 0 Hz), a memory trace is imprinted in enhanced synaptic strength due to short-term synaptic facilitation (Mongillo et al., 2008). Selective spiking activity is recovered by a non-selective constant input applied during 300 ms to all excitatory neurons during the two reactivation periods (marked by yellow and green rectangles in the raster plot). The amplitude of the input was 11 mV during the first and 13 mV during the second reactivation period. Reactivation periods are marked in light gray shading in the remaining panels below and the cue period is indicated by dark gray shading. Firing rates (second row), synaptic facilitation variable u (third row), and synaptic depression variable x (bottom row) for the same trial, averaged for 500 neurons around the neuron with 180° as preferred direction (solid lines) and around the neuron with 0° as preferred direction (dashed lines). Note that reactivation recovers the activity bump (C) but also causes elevated firing and subsequent enhancement of synapses at all positions in the networks. (B) Activity in a network with demyelination of 50% of the myelinated segments by removing 60% of the myelin lamellae. AP failures lead to reduced firing rates in the cue and early delay periods and consequently to weaker synaptic enhancement. (C) Average spike counts of the excitatory neurons during the cue period (black lines), and the two reactivation periods indicated in the raster plots in A and B (yellow and green lines). Solid lines correspond to the control network and dashed lines to the perturbed network. (D) Memory strength as a function of time for the control and perturbed networks. (E-F) Trajectories of the bump center (i.e., remembered cue location) read out from the neural activity across the cue and delay periods using a population vector (see Methods). Cue position was 180° in all trials. The perturbed network (F) shows larger working memory errors towards the end of the delay period compared to the control network (E).

Author response image 2.

Effect of propagation delays on control and perturbed activity-silent network models. (A) Memory strength during the whole simulation time for the young, control networks relying on activity-silent working memory (Supplementary Figure 8) with zero propagation delays (blue line), and with propagation delays from a uniform distribution with a range between 0 and 40 ms (yellow line) and between 0 and 100 ms (orange line). (B) Memory strength for perturbed networks when demyelinating 25% of the myelinated segments by removing 50% of the myelin lamellae, without delays (red line), and with uniformly distributed delays between 0 and 40 ms (light gray line) and between 0 and 100 ms (black line). The cue period is indicated by dark gray shading and reactivation periods are marked in light gray. Memory strength was calculated by averaging across 280 trials for one network. Shaded areas indicate SEM for each case. For the young, control networks (A), working memory was not affected by including delays of up to 40 ms. Unrealistically long delays ranging up to 100 ms did cause an impairment (the longest delays found for the most extreme perturbation condition – demyelination of 75% of the segments by removing 100% of the myelin lamellae – were of 49.9 ms on average). When also incorporating AP failures to the networks (B), we observed a similar trend. For this perturbation condition, delays of up to 40 ms were already much larger than the delays quantified in the single neuron model (for the case of 25% of the segments demyelinated by removing 50% of the myelin lamellae, the average delay in the cohort was 3.75 ms).

With additional simulations to address these issues, I consider that the present study would become a convincing milestone in the computational modeling of myelin-related models, and an important study in the field of working memory.

Again, we would like to thank the reviewer for the positive comments. We have addressed all the main issues raised (see below our response to the “recommendations for the authors”).

Reviewer #2 (Public Review):

This paper analyzes the effect of axon de-myelination and re-myelination on action potential speed, and propagation failure. Next, the findings are then incorporated in a standard spiking ring attractor model of working memory.

I think the results are not very surprising or solid and there are issues with method and presentation.

The authors did many simulations with random parameters, then averaged the result, and found for instance that the Conduction Velocity drops in demyelination. It gives the reader little insight into what is really going on. My personal preference is for a well understood simple model rather than a poorly understood complex model. The link between the model outcome of WM and data remains qualitative, and is further weakened by the existence of known other age-related effects in PFC circuits.

We thank the reviewer for the critical assessment of our work. We share the view that understanding simple models can provide critical insights into brain function (and we believe that many of our papers related to attractor dynamics in working memory and decision making fall into this category, e.g. Wimmer et al. 2014, Esnaola-Acebes et al. 2022, Ibañez et al 2020). However, we respectfully disagree with the reviewer on an important point: the model complexity that we have chosen is appropriate and necessary to study the phenomenon at hand. Our modeling efforts are principled, with complexity added as necessary. We started with a biophysical single neuron model with firing dynamics fit to empirical data in pyramidal neurons of rhesus monkey dlPFC (Rumbell et al. 2016) – the same type of neurons and cortical region analyzed in the Peters et al. work on structural changes to myelin seen during aging (e.g., Figure 1). Because simple models do not accurately capture the CV along thin axons like those in the PFC, we attached a multicompartment axon with detailed myelinated segments, and constructed a cohort of feasible models. We then used this cohort to get quantitative estimates of the effects of variable degrees of demyelination and remyelination. This would not be possible with a simpler model. We then study the consequences of de- and re-myelination in a spiking neural network model. Again, we could not use a simpler model (e.g. a firing rate attractor model) without making gross assumptions about how demyelination affects circuit function. In sum, we believe that our models are relatively simple but comprehensive given the phenomenon that we are studying.

The reviewer is correct in that there exist “known other age-related effects in PFC circuits”. These are reviewed in the introduction and we discuss future extensions of our model that would incorporate those effects as well. It is important to note that this is the first comprehensive study of demyelination effects in aging PFC, demonstrating that myelin changes alone predict working memory changes associated with aging.

The specific issues about modeling choices and interpretation of the results are discussed below.

Both for the de/re myelination the spatial patterns are fully random. Why is this justified?

We agree that myelin dystrophy during aging could be non-random, that is, localized to certain regions of an axon. Our collaborators (Drs Jennifer Luebke, Maya Medalla, and Patrick Hof) are currently addressing this question using 3D electron microscopy and immunohistochemistry on axons of individual neurons and their associated myelin, but results are not available yet. Early on in this study we examined how the location of myelin alterations affected AP propagation. Focusing demyelination along a section of axon led to more AP slowing and failure than when spatially randomized. Likewise, remyelination of such spatially localized dystrophy led to greater recovery, as there were fewer transitions between long and short internodes (Supplemental Figure 4). Since otherwise the effects in the localized cases were largely similar to those in the spatially random case (see Author response image 3 below), for brevity in this paper we assumed myelin alterations were randomly distributed. Our next paper, extending this study to collateralized axons and which was presented as a poster at the 2023 Society for Neuroscience meeting, will include an examination of localized myelin dystrophy.

Author response image 3.

Effect of localized myelin alterations on CV change. Myelin alterations were either focused on the third of myelinated segments closest to the initial segment (‘proximally clustered’), the third of myelinated segments furthest from the initial segment (‘distally clustered’), or distributed according to a uniform distribution as in the current study. For demyelination, all lamellae were removed from 25% of myelinated segments (showing mean +/- SEM of all 50 cohort models, 30 randomized trials each). For remyelination, affected segments were replaced by two shorter segments with 75% of the original lamellae thickness and a node in between.

We have added two sentences in Methods to justify this assumption more clearly (line 510): “Evidence suggests that aging affects oligodendrocytes in several ways, including the ability for oligodendrocyte precursor cells to mature (Dimovasili et al., 2022). Knowing that individual oligodendrocytes myelinate axons of many different neurons, but without data quantifying how oligodendrocyte dystrophy affects myelination in individual axons, we assumed that myelin alterations were randomly distributed.”

We have also added a sentence in the Discussion alluding to our upcoming study (line 434): “Our model can also be extended to explore interactions between spatially localized myelin perturbations (such as those seen in multiple sclerosis) and axon collateralization (Sengupta et al., 2023), which would affect the distance-dependence of AP failures.”

Similarly, to model the myelin parameters were drawn from uniform distributions, Table 1 (I guess). Again, why is this reasonable?

The reviewer is correct that our initial Latin hypercube sample generated a uniform distribution. However, parameters of the random sample of models selected as biologically feasible were not uniformly distributed. We have added a new figure (Supplementary Figure 1A) to illustrate the parameter distributions, and have added two sentences in Methods (starting on line 596):

“Of the 1600 simulated models, 138 met these criteria; for the present study, we randomly selected 50 models to comprise the young, control model cohort. Along most dimensions, the chosen cohort was approximately normally distributed (Supplementary Figure 1). The g-ratio (ratio of axon to fiber diameter) among models in the cohort was 0.71 ± 0.02, with total axon lengths of 1.2 ± 0.1 cm.”

Author response image 4.

Distribution of parameters and conduction velocities in the single neuron model cohort. (A) Histograms of axon morphology parameters of models selected for the single neuron cohort. Top: axon diameter: middle, length of unperturbed myelin segments; bottom: total myelin thickness in unperturbed segments, computed as the product of lamella thickness and number of lamellae. (B) Histograms of the CV for the 50 axons of the unperturbed model cohort (top), and representative demyelination and remyelination perturbations: mild demyelination (removing 25% of lamellae from 25% of the myelinated segments, second row); severe demyelination (removing all lamellae from 75% of the myelinated segments, third row); and complete (100%) remyelination (where the demyelinated segments from the third row were remyelinated by two shorter segments with 75% of lamellae). CVs averaged over 30 trials in each case. (C) Changes in CV (measured in %) in response to demyelination and remyelination versus the magnitude of current clamp step (+180, +280, or +380 pA). Shown are mean +/- SEM for demyelinating 50% of myelinated segments (removing all lamellae), and subsequent remyelination of those segments by shorter segments with 75% of lamellae.

The focus of most analysis is on the conduction velocity but in the end, this has no effect on WM, so the discussion of CV remains sterile.

CV delays likely do affect brain functions that rely on neuronal oscillations and synchrony, as mentioned in the Discussion. As such, we feel that our single neuron model results on CV delays as well as AP failures are valuable for the scientific community. Yet, given the results of our network models here, the reviewer has a valid point. We have clarified in the introduction that AP failures but not CV delays affected the network output (line 115):

“Higher degrees of demyelination led to slower propagation and eventual failure of APs along the axons of the multicompartment models. In the network models, an increase in AP failure rate resulted in progressive working memory impairment, whereas slower conduction velocities, in the range observed in the multicompartment models, had a negligible effect.”

We have also revised the single neuron section of the Results throughout, to better highlight the effects of myelin dystrophy on AP failures. Revisions to address this in the demyelination section start on line 148:

“AP propagation was progressively impaired as demyelination increased (Figure 3): CV became slower, eventually leading to AP failure. Removing 25% of lamellae had a negligible effect on CV, regardless of how many segments were affected. However, when all lamellae were removed, CV slowed drastically – by 38 ± 10% even when just 25% of the segments were demyelinated in this way, and 35 ± 13% of APs failed. When 75% of segments lost all their lamellae, CV slowed by 72 ± 8% and 45 ± 13% of APs failed.”

Similiarly, we have added several sentences about AP failures that remain after remyelination of the single neuron model (starting on line 190):

“Results for the percentage of AP failures (Figure 4C,F) were consistent with those for CV recovery. Remyelinating all previously demyelinated segments, even adding just 10% of lamellae, brought AP failure rates down to 14.6 ± 5.1%. Remyelinating all affected segments with 75% of lamellae (the maximal amount of remyelination) nearly eliminated AP failures (1.8 ± 1.1%). Incomplete remyelination, where some segments were still demyelinated, still had relatively high AP failure rates. For example, when one eighth of segments were remyelinated with the maximal amount of lamellae and one eighth were left bare, 25.7 ± 11.5% of APs failed across the cohort (Figure 4C, red dashed line and arrow). AP failure rates were slightly lower when starting with partial demyelination: 10.6 ± 7.6% of APs failed in the analogous paradigm (Figure 4F, red dashed line and arrow). In short: combinations of demyelinated and remyelinated segments often led to sizable CV delays and AP failures.”

The more important effect of de/re myelination is on failure. However, the failure is, AFAIK, just characterized by a constant current injection of 380pA. From Fig 2 it seems however that the first spike is particularly susceptible to failure. In other words, it has not been justified that it is fine to use the failure rates from this artificial protocol in the I&F model. I would expect the temporal current trace to affect whether the propagation fails or not.

In general, we did not find the first spike to be more susceptible to failure than latter spikes; the trace in Figure 2 is a representative snapshot intended to illustrate CV slowdown, AP failure, and recovery. Regarding the constant current injection: while the reviewer is correct that neurons do not receive such inputs in vivo, the applied current injections were designed to match in vitro current clamp protocols for these rhesus monkey neurons. While our future studies will include responses to more realistic synaptic inputs, we focused on somatic current injections here. We have added a new panel (C) to Supplementary Figure 1 (see previous response above) showing that the current step magnitude had little effect on the CV change after myelin perturbations; there was little effect on AP failure rates too. We now also state this finding more explicitly in Methods (starting on line 561):

“As done during in vitro electrophysiological experiments (Chang et al., 2005; Ibanez et al., 2020) and past modeling studies (Coskren et al., 2015; Rumbell et al., 2016), we first applied a holding current to stabilize the somatic membrane potential at -70 mV, then injected a current step into the somatic compartment for 2 seconds. …The CV changes in response to myelin alterations were relatively insensitive to variations in the magnitude of suprathreshold somatic current steps (Supplementary Figure 1C), and whether the current was constant or included Gaussian noise. Therefore, here we quantified CV changes and AP failures from responses to constant +380 pA current steps only.”

I don't know if there are many axon-collaterals in the WM circuits and or distance dependence in the connectivity, but if so, then the current implementation of failure would be questionable.

We agree that axon collaterals may affect our results; our unpublished morphological analyses of individual neuron axons indicate that there is a high degree of local axon collateralization in Layer 3 pyramidal neurons in LPFC. In this first study from our group on myelin perturbations, we chose to focus here on unbranched axons. There was some distance dependence of AP failure along the length of the axon. For example, in our most extreme demyelination case (75% of segments losing all their lamellae), about 14% of the axons showed more AP failure at their distal ends relative to the middle (mean difference 6.33%). We are examining this distance dependence more broadly in our next study, now cited in the Discussion (line 434): “Our model can also be extended to explore interactions between spatially localized myelin perturbations (such as those seen in multiple sclerosis) and axon collateralization (Sengupta et al., 2023), which would affect the distance-dependence of AP failures.”

I would also advise against thresholding at 75% failure in Fig3C. Why don't the authors not simply plot the failure rate?

We thank the reviewer for this suggestion, and have made this change. As suggested by the reviewer, we now show the AP failure rate in Figure 3 and Figure 4. The trends shown are nearly identical to those from the high failure trials.

Regarding the presentation, there are a number of dead-end results that are not used further on. The paper is rather extensive, and it would be clearer if written up in half the space. In addition, much information is really supplementary. The issue of the CV I already mentioned, also the Lasso regression for instance remains unused.

We understand the reviewer’s perspective, and we do value brevity when possible. During the revision process we examined the paper carefully, and made things more concise when it was feasible. As mentioned above, reporting CV results is important, though these revisions increased emphasis on results for AP failures in our revision. We combined the two Supplementary Figures about remyelination in the single neuron model into one (Supplementary Figure 3). We also moved the Lasso figure and associated methods to the Supplementary Material (Supplementary Figure 2), and have separated the Lasso results for demyelination and remyelination into their respective paragraphs (lines 154-160 and lines 200-204 respectively). While we do not use the Lasso explicitly later in Results, we cite them in the Discussion when comparing our findings to previous work (starting on line 417):

“Since our single neuron cohort sampled a wide range of parameter space, we used Lasso regression to identify which of the complex, interacting parameters contributed most to CV delays (which preceded AP failures). Parameters including axon diameter, node length, length of myelinated segments, and nodal ion channel densities predicted how our models responded to demyelination and remyelination; these findings are consistent with past modeling studies over more limited parameter ranges (e.g., Goldman and Albus, 1968; Moore et al., 1978; Babbs and Shi, 2013; Young et al., 2013; Schmidt and Knösche, 2019).”

We hope that our revision has struck an appropriate balance between clear and concise writing, and addressing concerns from both reviewers. We greatly value the time you have given to help us to improve our manuscript.

Response to Recommendations for the Authors:

Reviewer #1 (Recommendations for the Authors):

As I mentioned above, I consider that this study is well designed and it offers very interesting results. I have detailed below some of the issues that should be addressed to improve its potential impact in the field:

(1) Across the manuscript, it is not entirely clear how the results of the multicompartmental model compare to existing modeling results on demyelination and CV changes (such as in the papers cited by the authors). Is this section confirming previous results with a new (more accurate) computational model, or are there any new insights previously unreported? A new paragraph in the Discussion putting these results in context would be very useful for the reader.

We thank the reviewer for this suggestion. We have added two new subheadings to organize the Discussion better, and have expanded the single neuron section to three paragraphs. We feel this now clarifies how our model fits in with previous work while stating its novelty more explicitly. Starting on line 391:

“Myelin changes affect AP propagation in a cohort of model neurons

The novelty of our neuron model lies in its systematic exploration of a combination of different myelin perturbation types known to occur in myelin dystrophies, across a wide range of biologically feasible models. Our single neuron model assumed that age-related myelin dystrophies (e.g., Figure 1) alter the insulative properties of lamellae analogously to demyelination, and examined interactions between demyelination and remyelination. Past studies of myelin dystrophy examined how either demyelination or remyelination of all segments affected AP propagation for a few representative axon morphologies. For example, Scurfield and Latimer (2018) explored how remyelination affected CV delays, finding that axons with more transitions between long and short myelinated segments had slower CV (Supplementary Figure 4), and was first to explore how remyelination interacts with tight junctions. However, their study did not couple remyelination and demyelination together or examine AP failures. Other basic findings from our single neuron cohort are consistent with past modeling studies, including that demyelination caused CV slowing and eventual AP failures (Stephanova et al., 2005; Stephanova and Daskalova, 2008; Naud and Longtin, 2019), and, separately, that remyelination with shorter and thinner myelinated segments led to CV slowing (Lasiene et al., 2008; Powers et al., 2012; Scurfield and Latimer, 2018). However, by assuming that some previously demyelinated segments were remyelinated while others were not, we found that models could have much higher AP failure rates than previously reported. Such a scenario, in which individual axons have some segments that are normal, some demyelinated, and some remyelinated, is likely to occur. We also found a few neurons in our cohort showing a CV increase after remyelination, which has not generally been reported before and is likely due to an interplay between ion channels in the new nodes and altered electrotonic lengths in the perturbed myelinated segments (e.g., Waxman, 1978; Naud and Longtin, 2019).

Since our single neuron cohort sampled a wide range of parameter space, we used Lasso regression to identify which of the complex, interacting parameters contributed most to CV delays (which preceded AP failures). Parameters including axon diameter, node length, length of myelinated segments, and nodal ion channel densities predicted how our models responded to demyelination and remyelination; these findings are consistent with past modeling studies over more limited parameter ranges (e.g., Goldman and Albus, 1968; Moore et al., 1978; Babbs and Shi, 2013; Young et al., 2013; Schmidt and Knösche, 2019). Better empirical measurements of these parameters in monkey dlPFC, for example from 3-dimensional electron microscopy studies or single neuron axon studies combined with markers for myelin, would help predict the extent to which myelin dystrophy and remyelination along individual axons with aging affect AP propagation.

Another important feature of our multicompartment model is that it was constrained by morphologic and physiological data in rhesus monkey dlPFC —an extremely valuable dataset from an animal model with many similarities to humans (Upright and Baxter, 2021; Tarantal et al., 2022). While beyond the scope of the current study, this computational infrastructure –with a detailed axon, initial segment, soma, and apical and basal dendrites– enables simultaneous investigations of signal propagation through the dendritic arbor and axon. Our model can also be extended to explore interactions between spatially localized myelin perturbations (such as those seen in multiple sclerosis) and axon collateralization (Sengupta et al., 2023), which would affect the distance-dependence of AP failures. Integrating such results from single neuron models into network models of working memory, as we have done here, is a powerful way to connect empirical data across multiple scales.”

(2) Although the authors provide a well-designed study for the multi-compartmental model, it would be useful to add more details about how an unperturbed model and a completely remyelinated model differ in practice, perhaps right before the first results on the single cell model are presented. Are the new myelin sheaths covering the same % of axon as in the original case? Are there the same number of nodes? It is hard to distinguish which of these results are due to a compensation by the new myelin sheaths and which ones are just the model coming back to its original (and mathematically equivalent) starting point.

A ‘fully remyelinated’ axon is not mathematically equivalent to the unperturbed axon. Newly remyelinated segments had at most 75% of the original number of myelin wraps, with a new node in between, consistent with empirical observations in rhesus monkey dlPFC. Our manuscript changes in response to this recommendation are described in detail above in our response to the public review of the same reviewer.

(3) The authors observe a directed component in the bias that is known to be caused by heterogeneities in network connectivity, as stated in the text. It occurs to me that similar effects could be also caused by an heterogeneous demyelination in parts of the network. Inducing these biases could be another potential effect of demyelination in practice, and could be easily revealed by the author's current model (and displayed in a supplementary figure).

As suggested by the reviewer, we have tested heterogeneous demyelination in parts of the network and the results confirm the reviewer’s intuition. We have included these new results as new Supplementary Figure 7 (see below) and we have added the following sentences in the Legend of Figure 5, line 1265: “When demyelination is restricted to a part of the network, diffusion only increases in the perturbed zone (Supplementary Figure 7).” and in the Discussion (line 457): “In addition to age-related changes in memory duration and precision, our network model predicts an age-related increase in systematic errors (bias) due to an increased drift of the activity bump (Supplementary Figure 11). Moreover, if demyelination is spatially localized in a part of the network, the model predicts a repulsive bias away from the memories encoded in the affected zone (Supplementary Figure 7).”

Author response image 5.

Effect of spatially heterogeneous demyelination of the model neurons according to their preferred angle. We also tested working memory performance in the network when demyelination affects only parts of the network. The figure shows the decoded bump center position during the cue and delay period for the eight possible cue directions when a fraction of neurons was perturbed and the rest of the neurons in the circuit were unaltered (Figure 5B). We perturbed 10% of the neurons around the neuron with preferred direction 90° (left panel), 25% of the neurons around -90° (middle panel), and 50% of the neurons around 180° (right panel). Bump traces for cues that lie inside the perturbed portion of the circuit are shown in blue. Network perturbation in the three cases consisted in demyelinating 25% of the segments along the axons of model neurons, by removing 70% of the myelin lamellae. In each case, 280 trials were simulated for one network. These simulations show an increased drift and diffusion inside the perturbed zone, consistent with the increased drift and diffusion when perturbing the entire network (Figure 6B and Supplementary Figure 11). In particular, spatially heterogeneous demyelination in our network leads to a bias away from the affected zone and to increased trial-to-trial variability. Note that this is a model prediction, but we are not aware of empirical data showing heterogeneous demyelination with aging. Further, note that while our network model has a topological ring structure, neurons in PFC are not anatomically arranged depending on their preferred features. Thus, spatially heterogeneous demyelination would likely affect neurons with different feature preferences (i.e., neurons throughout our ring model).

(4) The bump attractor model of WM relies on a continuous attractor dynamics to encode the information stored in memory --a fixed point dynamics that can only vary via the slow noise-driven drift. This means, as the authors mention, that changes in CV won't affect the performance of WM in their model. This seems to be a limitation of the model, or at least an effect which is highly dependent on the modeler's choice, rather than an accurate prediction. While testing the effects of oscillations (as the authors argue in the Discussion) might be out of the scope of this work, there are other WM models which are more sensitive to temporal differences in activity. The authors should test whether the same (lack of) effects are also found in other WM models. A silent WM model seems to be the ideal candidate for this, as the authors already have the key dynamics of that model incorporated in their computational framework (namely, short-term synaptic facilitation in excitatory synapses).

We fully agree that considering the effects of demyelination in networks with alternative mechanisms would strengthen our manuscript. As suggested by the reviewer, we have simulated demyelination effects (AP failures and changes in CV) in an activity silent working memory model. The results are described in detail above in our response to the public review of the same reviewer.

We also would like to mention that we have now also tested larger conduction delays in the bump attractor model, revealing additional working memory errors. This is shown in the revised version of Supplementary Figure 6 (see below). However, those delays are unrealistically large and thus the main effect in both the bump attractor and the activity-silent model is due to AP failures.

Author response image 6.

Effect of propagation delays on control and perturbed networks. (A) Memory strength (left panels) and diffusion (right panels) for the young, control networks with zero propagation delays (blue solid line), as in Figure 5, and with propagation delays from a uniform distribution with a range between 0 and 100 ms (yellow dashed line). (B) Memory strength and diffusion for perturbed networks when demyelinating 50% of the segments along the axons of model neurons, by removing 60% of the myelin lamellae without delays (red solid line), and with delays from a uniform distribution with a range between 0 and 40 ms (gray dashed line) and between 0 and 85 ms (black dash-dotted line). The measures of working memory performance were calculated by averaging across 20 networks and 280 trials for each network. Shaded areas indicate SEM for each case. For the young, control networks, there was no difference with and without propagation delays, even though the delays used in the network simulations were much larger than the delays quantified in the single neuron model (the longest delays found for the most extreme perturbation condition –demyelination of 75% of the segments by removing 100% of the myelin lamellae– were of 49.9 ms on average; A). Working memory performance was also unaffected in the perturbed network with AP failures for delays ranging between 0 and 40 ms, also larger than the ones quantified in the single neuron model (for the case of 50% of the segments demyelinated by removing 60% of the myelin lamellae, the average delay in the cohort was 4.6 ms and the maximum delay was 15.7 ms; B). However, including extremely long delays of up to 85 ms did further impair memory compared to the impairment level introduced by AP failures alone (B).

(5) Impact of demyelination and remyelination on working memory: Could the authors explain here how these biologically detailed alterations are implemented in the bump attractor model? Is the CV and AP failure rate adjusted to the values produced by the multicompartment neuron model with these myelin alterations?

Yes, the reviewer is right, the CV and AP failure rate have been adjusted to the values produced by the multicompartment neuron model. To clarify this in the manuscript, we have restated the text as follows:

Lines 243 - 249 (Results):

To investigate how myelin alterations affect working memory maintenance, we explored in the network model the same demyelination and remyelination conditions as we did in the single neuron model. Because our network model consists of point neurons (i.e., without detailed axons), we incorporated CV slowing as an effective increase in synaptic transmission delays (see Methods). To simulate AP failures, we adjusted the AP failure rate to the values given by the single neuron model, by creating a probabilistic model of spike transmission from the excitatory presynaptic neurons to both the excitatory and inhibitory postsynaptic neurons (see Methods).

Lines 722 - 747 (Methods):

Modeling action potential propagation failures in the network. The network model is composed of point neurons without an explicit model of the axon. To effectively model the action potential failures at the distal end of the axons quantified with the single neuron model under the different demyelination and remyelination conditions, the AP failure rate was adjusted to the values produced by the single neuron model. To do this, we perturbed the 10 control networks by designing a probabilistic model of spike transmission from the excitatory presynaptic neurons to both the excitatory and inhibitory postsynaptic neurons. From the single neuron model, for each demyelination/remyelination condition, we quantified the probability of AP failure for each of the neurons in the control cohort, as well as the percentage of those neurons that shared the same probabilities of failure. That is, the percentage of neurons that had probability of failure = 0, probability of failure = 1 or any other probability. Then, we computed the probability of transmission, , and we specified for the corresponding percentages of excitatory neurons in the networks. Thus, in the network model, we took into account the heterogeneity observed in the single neuron model under each demyelination/remyelination condition.

Modeling conduction velocity slowing in the network. To explore the effect of CV slowing along the axons of model neurons, we simulated 20 young, control networks and 20 perturbed networks with AP failure rates adjusted for the case of single model neurons with 50% of the segments demyelinated along the axons by removing 60% of the myelin lamellae (we ran 280 trials for each network). Then, we added random delays uniformly distributed with a minimum value of 0 ms in both cases, a maximum value of 100 ms in the control networks, and a maximum values of 40 ms and 85 ms in the perturbed networks, in both the AMPA and NMDA excitatory connections to both E and I neurons (Supplementary Figure 6). These large values were chosen because we wanted to illustrate the potential effect of CV slowing in our network and smaller, more realistic, values did not have any effect.

(6) "We also sought to reveal the effect on working memory performance of more biologically realistic network models with AP transmission probabilities matched to both axons with intact and with altered myelin sheaths, as likely occurs in the aging brain (Figure 1). Thus, we ran network model simulations combining AP failure probabilities corresponding to groups of neurons containing intact axons and axons presenting different degrees of demyelination." I fail to see the difference with respect to the results in previous sections. Is it that now we have subnetworks in which axons are intact and subnetworks with significant AP failures, while before there was no topological separation between both cases? Please clarify.

In Figures 5 and 6 the AP failure rate of the neural population in the network simulations was matched to the AP failure rate of the cohort of single model neurons for each demyelination/remyelination condition. Since not all model neurons have equal features, a given condition produces different levels of impairment in its neuron. Thus, we quantified the probability of AP failure for each neuron in the control cohort, as well as the percentage of those neurons that shared the same probabilities of failure. Then, we computed the probability of AP transmission for the corresponding percentages of excitatory neurons in the networks. Thus, in the network model, we took into account the heterogeneity observed in the single neuron model under each demyelination/remyelination condition.

However, In Figures 7 and 8, we consider additional heterogeneity due to a different degree of demylination/remyelination of different neurons. Here, excitatory neurons in the network model are not perturbed according to a single demyelination/remyelination condition. Instead, we allowed that different percentages of excitatory neurons had AP failure rates corresponding to different demyelination/remyelination conditions: some were unperturbed, while others had different degrees of demyelination (Figure 7) and different degrees of remyelination (Figure 8). We have modified the text for clarification in several places.

First, when we describe the impact of demyelination on working memory, we already mention that (line 271): “In each of the 10 networks, we set the AP failure rate of the excitatory neurons according to the distribution of failure probabilities of the neurons in the single neuron cohort for the given demyelination or remyelination condition. Thus, we took into account the heterogeneity of demyelination and remyelination effects from our single neuron cohort (Figure 3A; Supplementary Figure 3). Note that this heterogeneity originates from differences in axon properties, but probabilities of failure for all neurons in the network correspond to the same degree of demyelination (Figure 6). We will also consider networks that contain different combinations of axons with either intact or perturbed myelin (Figure 7 and Figure 8).”

Second, we have combined the text describing Figures 7 and 8 under a single section title, which reads “Simulated heterogenous myelin alterations match empirical data” (line 334) and start this section with (line 337): “Up to this point we have studied network models with AP failure probabilities corresponding to a single degree of myelin alterations (i.e., with all excitatory neurons in the network having AP failure rates matched to those of the single neuron cohort for one particular demyelination or remyelination condition). Next, we sought to reveal the effect on working memory performance of more biologically realistic network models, where excitatory neurons in the networks were perturbed according to a combination of different demyelination or remyelination conditions. That is, we simulated networks with excitatory neurons having AP failure probabilities matched to both neuronal axons with intact and with altered myelin sheaths in different degrees, as likely occurs in the aging brain (Figure 1).”

(7) "Unexpectedly, our model indicates that compared to the performance of networks composed of neurons possessing axons with intact myelin sheaths, both demyelination and remyelination leads to an impaired performance." This conclusion is quite interesting, but I lack intuition from the paper as of why it is happening. In fact, the authors say in the Discussion that "complete remyelination of all the previously demyelinated segments with sufficient myelin, with fewer transitions between long and short segments, recovered working memory function." Would we then see a minimum and then an increase in memory duration in Figure 9B if we extended the X-axis until we hit 100% of new myelin sheaths?

This is a very important question that we have carefully addressed in Results and Discussion. We distinguish between two remyelination cases in the models. Complete remyelination: when all (100%) the previously demyelinated segments have been subsequently remyelinated, and incomplete remyelination: when less than 100% (25%, 50% or 75%) of the demyelinated segments have been remyelinated. Figure 6 (middle and right columns) shows the two cases (black lines for any percentage of lamellae added vs. colored lines): for 100% of the segments remyelinated, the network performance is nearly or completely (when enough lamellae are added) recovered to the young network performance. In fact, with the single neuron model we observe that (lines 192 - 193 in Results): “Remyelinating all affected segments with 75% of lamellae (the maximal amount of remyelination) nearly eliminated AP failures (1.8 ± 1.1%)”. However, incomplete remyelination recovers the performance compared to demyelination (middle and right columns in Figure 6 vs left column), but this performance is worse than the performance of the young networks. The single neuron model shows that (lines 194 - 197 in Results): “Incomplete remyelination, where some segments were still demyelinated, still had relatively high AP failure rates. For example, when one eighth of segments were remyelinated with the maximal amount of lamellae and one eighth were left bare, 25.7 ± 11.5% of APs failed across the cohort (Figure 4C, red dashed line and arrow).”

In Figure 9B (now Figure 8B), we combine intact axons with axons that are only partially remyelinated (i.e., incomplete remyelination). Extending the X-axis in Figure 8B until 100% of new myelin sheaths would not imply a minimum and a subsequent increase, but a continuous impairment: the more axons we perturb (remyelinate) the higher is the impairment compared to the young cases where all the axons are intact.

The sentence "Unexpectedly, our model indicates that compared to the performance of networks composed of neurons possessing axons with intact myelin sheaths, both demyelination and remyelination leads to an impaired performance.", now reads as (lines 379 380 in Results): “Therefore, both demyelination and incomplete remyelination lead to impaired performance in our networks, compared to networks with intact myelin sheaths”. We have also rewritten the corresponding section in Discussion (lines 486 - 489) as follows: “Therefore, it is reasonable to assume that ineffective remyelination may lead to working memory impairment. In fact, complete remyelination of all previously demyelinated segments with sufficient myelin, with fewer transitions between long and short segments, led to full recovery of working memory function.”

(8) [minor] "Our recent network model found that age-related changes in firing rates and synapse numbers in individual neurons can lead to working memory impairment (Ibañez et al., 2020), but did not consider myelin dystrophy." Could you be more precise about which age-related changes were studied in Ibanez et al. 2020? From the paper it seems like it was mostly cellular excitability and synaptic density, so this should be added here for more context.

To clarify this, we have added the following sentences in the Introduccion (line 105):

“Our recent network model revealed that the empirically observed age-related increase in AP firing rates in prefrontal pyramidal neurons (modeled through an increased slope of the f-I curve) and loss of up to 30% of both excitatory and inhibitory synapses (modeled as a decrease in connectivity strength) can lead to working memory impairment (Ibañez et al., 2020), but this model did not incorporate the known changes to myelin structure that occur during normal

aging.”

(9) [minor] "Recurrent excitatory synapses are facilitating, which promotes robust and reliable persistent activity despite spatial heterogeneities in the connectivity or in the intrinsic properties of the neurons." It would be great to add a reference here to justify the inclusion of this type of plasticity in the excitatory circuit (for example Wang, Markram et al. Nat Neuro 2006).

We have added the references suggested by the reviewer and a further one in the Results (line 216):

“Recurrent excitatory synapses are facilitating, as has been empirically observed in PFC (Hempel et al., 2000; Wang et al., 2006), which promotes robust and reliable persistent activity despite spatial heterogeneities in the connectivity or in the intrinsic properties of the neurons.”

References:

Hempel, C. M., Hartman, K. H., Wang, X. J., Turrigiano, G. G., and Nelson, S. B. (2000). Multiple forms of short-term plasticity at excitatory synapses in rat medial prefrontal cortex. J. Neurophysiol. 83, 3031–3041. doi: 10.1152/jn.2000.83.5.3031

Wang, Y., Markram, H., Goodman, P. H., Berger, T. K., Ma, J., and Goldman- Rakic, P. S.(2006). Heterogeneity in the pyramidal network of the medial prefrontal cortex. Nat.Neurosci. 9, 534–542. doi: 10.1038/nn1670

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript examines the contribution of the dorsal and intermediate hippocampus to goal-directed navigation in a wide virtual environment where visual cues are provided by the scenery on the periphery of a wide arena. Among a choice of 2 reward zones located near the arena periphery, rats learn to navigate from the center of the arena to the reward zone associated with the highest reward. Navigation performance is largely assessed from the rats' body orientation when they leave the arena center and when they reach the periphery, as well as the angular mismatch between the reward zone and the site rats reach the periphery. Muscimol inactivation of the dorsal and intermediate hippocampus alters rat navigation to the reward zone, but the effect was more pronounced for the inactivation of the intermediate hippocampus, with some rat trajectories ending in the zone associated with the lowest reward. Based on these results, the authors suggest that the intermediate hippocampus is critical, especially for navigating to the highest reward zone.

Strengths:

-The authors developed an effective approach to study goal-directed navigation in a virtual environment where visual cues are provided by the peripheral scenery.

- In general, the text is clearly written and the figures are well-designed and relatively straightforward to interpret, even without reading the legends.

- An intriguing result, which would deserve to be better investigated and/or discussed, was that rats tended to rotate always in the counterclockwise direction. Could this be because of a hardware bias making it easier to turn left, some aspect of the peripheral landscape, or a natural preference of rats to turn left that is observable (or reported) in a real environment?

Thank you for the insightful question. As the reviewer mentioned, the counterclockwise rotation behavior was intriguing and unexpected. To answer the reviewer’s question properly, we examined whether such stereotypical turning behavior appeared before the rats acquired the task rule and reward zones in the pre-surgical training phase of the task. Data from the last day of shaping and the first day of the pre-surgical main task day showed no significant difference in the number of trials in which the first body-turn was either clockwise or counterclockwise, suggesting that the rats did not have a bias toward a specific side (p=0.46 for Shaping; p=0.76 for the Main task, Wilcoxon signed-rank test). These results excluded the possibility that there was something in the apparatus's hardware that made the rats turn only to the left. Also, since we used the same peripheral landscape for the shaping and main task, we could assume that the peripheral landscape did not cause movement bias.

Author response image 1.

Although it remains inconclusive, we have noticed that some prior studies alluded to a phenomenon similar to this issue, framed as the topic of lateralization or spatial preference by comparing left and right biases. For example, Wishaw et al. (1992) suggested that there was natural lateralization in rats (“Most of the rats displayed either a strong right limb bias or a strong left limb bias.”) but no dominance to a specific side. Andrade et al. (2001) also claimed that “83% of Wistar rats spontaneously showed a clear preference for left or right arms in the T-maze.” However, to the best of our knowledge, there has been no direct evidence that rats have a dominant natural preference only to one side.

Therefore, while the left-turning behavior remains an intriguing topic for further investigation, we find it difficult to pinpoint the reason behind the behavior in the current study. However, we would like to emphasize that this behavior did not interrupt testing our hypothesis. Nonetheless, we agree with the reviewer’s point that the counterclockwise rotation needs to be discussed more, so we revised the manuscript as follows:

“To rule out the potential effect of hardware bias or any particular aspect of peripheral landscape to make rats turn only to one side, we measured the direction of the first body-turn in each trial on the last day of shaping and the first day of the main task (i.e., before rats learned the reward zones). There was no significant difference between the clockwise and counterclockwise turns (p=0.46 for shaping, p=0.76 for main task; Wilcoxon signed-rank test), indicating that the stereotypical pattern of counterclockwise body-turn appeared only after the rats learned the reward locations.” (p.6)

- Another interesting observation, which would also deserve to be addressed in the discussion, is the fact that dHP/iHP inactivations produced to some extent consistent shifts in departing and peripheral crossing directions. This is visible from the distributions in Figures 6 and 7, which still show a peak under muscimol inactivation, but this peak is shifted to earlier angles than the correct ones. Such change is not straightforward to interpret, unlike the shortening of the mean vector length.

Maybe rats under muscimol could navigate simply by using the association of reward zone with some visual cues in the peripheral scene, in brain areas other than the hippocampus, and therefore stopped their rotation as soon as they saw the cues, a bit before the correct angle. While with their hippocampus is intact, rats could estimate precisely the spatial relationship between the reward zone and visual cues.

We agree with the possibility suggested by the reviewer. However, although not described in the original manuscript, we performed several different control experiments in a few rats using various visual stimulus manipulations to test how their behaviors change as a result. One of the experiments was the landmark omission test, where one of the landmarks was omitted. The landmark to be made disappear was pseudorandomly manipulated on a trial-by-trial basis. We observed that the omission of one landmark, regardless of its identity, did not cause a specific behavioral change in finding the reward zones, suggesting that the rats were not relying on a single visual landmark when finding the reward zone.

Author response image 2.

Therefore, it is unlikely that rats used the spatial relationship between the reward zone and a specific visual cue to solve the task in our study. However, the result was based on an insufficient sample size (n=3), not permitting any meaningful statistical testing. Thus, we have now updated this information in the manuscript as an anecdotal result as follows:

“Additionally, to investigate whether the rats used a certain landmark as a beacon to find the reward zones, we conducted the landmark omission test as a part of control experiments. Here, one of the landmarks was omitted, and the landmark to be made disappear was pseudorandomly manipulated on a trial-by-trial basis. The omission of one landmark, regardless of its identity, did not cause a specific behavioral change in finding the reward zones, suggesting that the rats were not relying on a single visual landmark when finding the reward zones. The result can be reported anecdotally only because of an insufficient sample size (n=3), not permitting any meaningful statistical testing.” (p.9)

Weaknesses:

-I am not sure that the differential role of dHP and iHP for navigation to high/low reward locations is supported by the data. The current results could be compatible with iHP inactivation producing a stronger impairment on spatial orientation than dHP inactivation, generating more erratic trajectories that crossed by chance the second reward zone.

To make the point that iHP inactivation affects the disambiguation of high and low reward locations, the authors should show that the fraction of trajectories aiming at the low reward zone is higher than expected by chance. Somehow we would expect to see a significant peak pointing toward the low reward zone in the distribution of Figures 6-7.

We thank the reviewer for the valuable comments. We agree that it is difficult to rigorously distinguish the loss of value representation from spatial disorientation in our experiment. Since the trial ended once the rat touched either reward zone, it was difficult to specify whether they intended to arrive at the location or just moved randomly and arrived there by chance. Moreover, it is possible that the drug infusion did not completely inactivate the iHP but only partially did so.

To investigate this issue further, we checked whether the distribution of the departure direction (DD) differed between the trials in which rats initially headed north (NW, N, NE) and south (SE, S, SW) at the start. In the manuscript, we demonstrated that DD aligned with the high-value zone, indicating that the rat remembered the scenes associated with the high-value zone (p.8). Based on the rats’ characteristic counterclockwise rotation, the reward zone rats would face first upon starting while heading north would be the high-value zone. On the other hand, the rat would face the low-value reward zone when starting while heading south. In this case, normal rats would inhibit leaving the start zone and rotate further until they face the high-value zone before finally departing the start location. If the iHP inactivation caused a more severe impairment in spatial orientation but not in value representation, it is likely that the iHP-inactivated rats in both north- and south-starting trials would behave similarly with the dHP-inactivated rats, but producing a larger deviation from the high-value zone. However, if the iHP inactivation affected the disambiguation of high and low reward locations, north and south-starting trials would show different DD distributions.

The circular plots shown below are the DD distributions of dMUS and iMUS. We could see that when they started facing north, iHP-inactivated rats still aligned themselves towards the high-value zone and thus remained spatially oriented, similar to the dHP inactivation session. However, in the south-starting trials, the DD distribution was completely different from the north-starting trials; the rats failed in body alignment towards the high-value zone. Instead, they departed the start point while heading south in most trials. This pattern was not seen in dMUS sessions, even in their south-starting trials, illustrating the distinct deficit caused by iHP inactivation. Additionally, most of the rats with iHP inactivation visited the low-value zone more in south-headed starting trials than in the north-headed trials, except for one rat.

Author response image 3.

Furthermore, we would like to clarify that we do not limit the effect of iHP inactivation to the impairment in distinguishing the high and low reward zones. It is possible that iHP inactivation resulted in the loss of a global value-representing map, leading to the impairment in distinguishing both reward zones from other non-rewarded areas in the environment. Figures 6 and 7 implicated this possibility by showing that the peaks are not restricted only to the reward zones. Unfortunately, we cannot rigorously address this in the current study because of the limitations of our experimental design mentioned above.

Nonetheless, we agree with the reviewer that this limitation needs to be addressed, so we now added how the current study needs further investigation to clarify what causes the behavioral change after the iHP inactivation in the Limitations section (p.21).

Reviewer #2 (Public Review):

Summary:

The aim of this paper was to elucidate the role of the dorsal HP and intermediate HP (dHP and iHP) in value-based spatial navigation through behavioral and pharmacological experiments using a newly developed VR apparatus. The authors inactivated dHP and iHP by muscimol injection and analyzed the differences in behavior. The results showed that dHP was important for spatial navigation, while iHP was critical for both value judgments and spatial navigation. The present study developed a new sophisticated behavioral experimental apparatus and proposed a behavioral paradigm that is useful for studying value-dependent spatial navigation. In addition, the present study provides important results that support previous findings of differential function along the dorsoventral axis of the hippocampus.

Strengths:

The authors developed a VR-based value-based spatial navigation task that allowed separate evaluation of "high-value target selection" and "spatial navigation to the target." They were also able to quantify behavioral parameters, allowing detailed analysis of the rats' behavioral patterns before and after learning or pharmacological inactivation.

Weaknesses:

Although differences in function along the dorsoventral axis of the hippocampus is an important topic that has received considerable attention, differences in value coding have been shown in previous studies, including the work of the authors; the present paper is an important study that supports previous studies, but the novelty of the findings is not that high, as the results are from pharmacological and behavioral experiments only.

We appreciate the reviewer's insightful comments. In response, we would like to emphasize that a very limited number of studies investigated the function of the intermediate hippocampus, especially in spatial memory tasks. We tested the differential functions of the dorsal and intermediate hippocampus using a within-animal design and used reversible inactivation manipulation (i.e., muscimol injection) to prevent potential compensation by other brain regions when using irreversible manipulation techniques (i.e., lesion). Also, very few studies have analyzed the navigation trajectories of animals as closely as in the current study. We emphasize the novelty of our study by comparing it with prior studies, as shown below in Table 1.

Author response table 1.

Comparison of our study with those from prior studies

Moreover, to the best of our knowledge, the current manuscript is the first to investigate the hippocampal subregions along the long axis in a VR environment using a hippocampal-dependent spatial memory task. Nonetheless, we agree that the current study has a limitation as a behavior-only experiment. We now have added a comment on how other techniques, such as electrophysiology, would develop our findings in the Limitation section (p.21).

Reviewer #3 (Public Review):

Summary:

The authors established a new virtual reality place preference task. On the task, rats, which were body-restrained on top of a moveable Styrofoam ball and could move through a circular virtual environment by moving the Styrofoam ball, learned to navigate reliably to a high-reward location over a low-reward location, using allocentric visual cues arranged around the virtual environment.

The authors also showed that functional inhibition by bilateral microinfusion of the GABA-A receptor agonist muscimol, which targeted the dorsal or intermediate hippocampus, disrupted task performance. The impact of functional inhibition targeting the intermediate hippocampus was more pronounced than that of functional inhibition targeting the dorsal hippocampus.

Moreover, the authors demonstrated that the same manipulations did not significantly disrupt rats' performance on a virtual reality task that required them to navigate to a spherical landmark to obtain reward, although there were numerical impairments in the main performance measure and the absence of statistically significant impairments may partly reflect a small sample size (see comments below).

Overall, the study established a new virtual-reality place preference task for rats and established that performance on this task requires the dorsal to intermediate hippocampus. They also established that task performance is more sensitive to the same muscimol infusion (presumably - doses and volumes used were not clearly defined in the manuscript, see comments below) when the infusion was applied to the intermediate hippocampus, compared to the dorsal hippocampus, although this does not offer strong support for the authors claim that dorsal hippocampus is responsible for accurate spatial navigation and intermediate hippocampus for place-value associations (see comments below).

Strengths:

(1) The authors established a new place preference task for body-restrained rats in a virtual environment and, using temporary pharmacological inhibition by intra-cerebral microinfusion of the GABA-A receptor agonist muscimol, showed that task performance requires dorsal to intermediate hippocampus.

(2) These findings extend our knowledge about place learning tasks that require dorsal to intermediate hippocampus and add to previous evidence that, for some place memory tasks, the intermediate hippocampus may be more important than other parts of the hippocampus, including the dorsal hippocampus, for goal-directed navigation based on allocentric place memory.

(3) The hippocampus-dependent task may be useful for future recording studies examining how hippocampal neurons support behavioral performance based on place information.

Weaknesses:

(1) The new findings do not strongly support the authors' suggestion that the dorsal hippocampus is responsible for accurate spatial navigation and the intermediate hippocampus for place-value associations.

The authors base this claim on the differential effects of the dorsal and intermediate hippocampal muscimol infusions on different performance measures. More specifically, dorsal hippocampal muscimol infusion significantly increased perimeter crossings and perimeter crossing deviations, whereas dorsal infusion did not significantly change other measures of task performance, including departure direction and visits to the high-value location. However, these statistical outcomes offer only limited evidence that dorsal hippocampal infusion specifically affected the perimeter crossing, without affecting the other measures. Numerically the pattern of infusion effects is quite similar across these various measures: intermediate hippocampal infusions markedly impaired these performance measures compared to vehicle infusions, and the values of these measures after dorsal hippocampal muscimol infusion were between the values in the intermediate hippocampal muscimol and the vehicle condition (Figures 5-7). Moreover, I am not so sure that the perimeter crossing measures really reflect distinct aspects of navigational performance compared to departure direction and hit rate, and, even if they did, which aspects this would be. For example, in line 316, the authors suggest that 'departure direction and PCD [perimeter crossing deviation] [are] indices of the effectiveness and accuracy of navigation, respectively'. However, what do the authors mean by 'effectiveness' and 'accuracy'? Accuracy typically refers to whether or not the navigation is 'correct', i.e. how much it deviates from the goal location, which would be indexed by all performance measures.

So, overall, I would recommend toning down the claim that the findings suggest that the dorsal hippocampus is responsible for accurate spatial navigation and the intermediate hippocampus for place-value associations.

The reviewer mentioned that the statistical outcomes offer limited evidence as the dHP inactivation results were always positioned between the results of the iHP inactivation and controls. However, we would like to emphasize that, projecting to each other, the two subregions are not completely segregated anatomically. It is highly likely this is also true functionally and there should be some overlap in their roles. Considering such relationships between the dHP and iHP, it could be natural to see an intermediate effect after inactivating the dHP, and that is why we focused on the “magnitude” of behavioral changes after inactivation instead of complete dissociation between the two subregions in our manuscript. Unfortunately, because of the nature of the drug infusion study, further dissociation would be difficult, requiring further investigation with different experimental techniques, such as physiological examinations of the neural firing patterns between the two regions. We mentioned this caveat of the current study in the Limitations as follows:

“However, our study includes only behavioral results and further mechanistic explanations as to the processes underlying the behavioral deficits require physiological investigations at the cellular level. Neurophysiological recordings during VR task performance could answer, for example, the questions such as whether the value-associated map in the iHP is built upon the map inherited from the dHP or it is independently developed in the iHP.” (p.21)

Regarding the reviewer’s comment on the meaning of measuring the perimeter crossing directions, we would like to draw the reviewer’s attention to the individual trajectories during the iMUS sessions described in Figure 5. Particularly when they were not confident with the location of the higher reward, rats changed their heading directions during the navigation, which resulted in a less efficient route to the goal location. Rats showing this type of behavior tended to hit the perimeter of the arena first before correcting their routes toward the goal zone. In contrast, rats showing effective navigation hardly bumped into the wall or perimeter before hitting the goal zone. Thus, their PCDs matched DDs almost always. When considered together with DD, our PCD measure could tell whether rats not hitting the goal zone directly after departure were impaired in either maintaining the correct heading direction to the goal zone at the start location or orienting themselves to the target zone accurately from the start. Our results suggest that the latter is the case. We included the relevant explanation in the Discussion section as follows:

“Particularly, rats changed their heading directions during the navigation when they were not confident with the location of the higher reward, resulting in a less efficient route to the goal location. Rats showing this type of behavior tended to hit the perimeter of the arena first before correcting their routes. Therefore, when considered together with DD, our PCD measure could tell that the rats not hitting the goal zone directly after departure were impaired in orienting themselves to the target zone accurately from the start, not in maintaining the correct heading direction to the goal zone at the start location.” (p.19)

Nonetheless, we agree with the reviewer that the term ‘accuracy’ might be confusing with performance accuracy, so we replaced the term with ‘precision’ throughout the manuscript, referring to the precise targeting of the reward zones.

(2) The claim that the different effects of intermediate and dorsal hippocampal muscimol infusions reflect different functions of intermediate and dorsal hippocampus rests on the assumption that both manipulations inhibit similar volumes of hippocampal tissue to a similar extent, but at different levels along the dorso-ventral axis of the hippocampus. However, this is not a foregone conclusion (e.g., drug spread may differ depending on the infusion site or drug effects may differ due to differential expression of GABA-A receptors in the dorsal and intermediate hippocampus), and the authors do not provide direct evidence for this assumption. Therefore, a possible alternative account of the weaker effects of dorsal compared to intermediate hippocampal muscimol infusions on place-preference performance is that the dorsal infusions affect less hippocampal volume or less markedly inhibit neurons within the affected volume than the intermediate infusions. I would recommend that the authors briefly consider this issue in the discussion. Moreover, from the Methods, it is not clear which infusion volume and muscimol concentration were used for the different infusions (see below, 4.a.), and this must be clarified.

We appreciate these insightful comments from the reviewer and agree that we do not provide direct evidence for the point raised by the reviewer. To the best of our knowledge, most of the behavioral studies on the long axis of the hippocampus did not particularly address the differential expression of GABA-A receptors along the axis. We could not find any literature that specifically introduced and compared the levels of expression of GABA-A receptors or the diffusion range of muscimol in the intermediate hippocampus to the other subregions. However, we found that Sotiriou et al. (2005) made such comparisons with respect to the expression of different GABA-A receptors. They concluded that the dorsal and ventral hippocampi have different levels of the GABA-A receptor subtypes. The a1/b2/g2 subtype was dominant in the dorsal hippocampus, while the a2/b1/g2 subtype was prevalent in the ventral hippocampus. Sotiriou and colleagues also mentioned the lower affinity of GABA-A receptor binding in the ventral hippocampus, and this result is consistent with the Papatheodoropoulos et al. (2002) study that showed a weaker synaptic inhibition in the ventral hippocampus compared to the dorsal hippocampus. Papatheodoropoulos et al. speculated differences in GABA receptors as one of the potential causes underlying the differential synaptic inhibition between the dorsal and ventral hippocampal regions. Based on these findings, the same volume of muscimol is more likely to cause a more severe effect on the ventral hippocampus than the dorsal hippocampus. Therefore, we do not believe that the less significant changes after the dorsal hippocampal inactivation were induced by the expression level of GABA-A receptors. Additionally, we have demonstrated in our previous study that muscimol injections in the dorsal hippocampus impair performance to the chance level in scene-based behavioral tasks (Lee et al., 2014; Kim et al., 2012).

Nonetheless, we mentioned the possibility of differential muscimol expressions between the two target regions. Following the suggestion of the reviewer, we now included this information in the Discussion as follows:

“Although there is still a possibility that the levels of expression of GABA-A receptors might be different along the longitudinal axis of the hippocampus, …” (p.20)

Regarding the drug infusion volume and concentration, we included these details in the Methods. Please see our detailed response to 4.a. below.

(3) It is good that the authors included a comparison/control study using a spherical beacon-guided navigation task, to examine the specific psychological mechanisms disrupted by the hippocampal manipulations. However, as outlined below (4.b.), the sample size for the comparison study was lower than for the main study, and the data in Figure 8 suggest that the comparison task may be affected by the hippocampal manipulations similarly to the place-preference task, albeit less markedly. This would raise the question as to which mechanisms that are common to the two tasks may be affected by hippocampal functional inhibition, which should be considered in the discussion.

The sample size for the object-guided navigation task was smaller because we initially did not plan the experiment, but later in the study decided to conduct the control test. Therefore, the object-guided navigation task was added to the study design after finishing the first three rats, resulting in a smaller sample size than the place preference task. We included this detail in the manuscript, as follows:

“Note the smaller sample size in the object-guided navigation task. This was because the task was later added to the study design.” (p.24)

Regarding the mechanism behind the two different tasks, we did not perform the same heading direction analysis here as in the place preference task because the two tasks have different characteristics such as task complexity. The object-guided navigation task is somewhat similar to the visually guided (or cued) version of the water maze task, which is widely known as hippocampal-independent (Morris et al., 1986; Packard et al., 1989; also see our descriptions on p.15). Therefore, we would argue that the two tasks (i.e., place preference task and object-guided navigation task) used in the current manuscript do not share neural mechanisms in common. Additionally, we confirmed that several behavioral measurements related to motor capacity, such as travel distance and latency, along with the direct hit proportion provided in Figure 8, did not show any statistically significant changes across drug conditions.

4. Several important methodological details require clarification:

a. Drug infusions (from line 673):

- '0.3 to 0.5 μl of either phosphate-buffered saline (PBS) or muscimol (MUS) was infused into each hemisphere'; the authors need to clarify when which infusion volume was used and why different infusion volumes were used.

We thank the reviewer for carefully reading our manuscript. We were cautious about side effects, such as suppressed locomotion or overly aggressive behavior, since the iHP injection site was close to the ventricle. We were keenly aware that the intermediate to ventral hippocampal regions are sensitive to the drug dosage from our previous experiments. Thus, we observed the rat’s behavior for 20 minutes after drug injection in a clean cage. We started from 0.5 μl, based on our previous study, but if the injected rat showed any sign of side effects in the cage, we stopped the experiment for the day and tried with a lower dosage (i.e., 0.4 μl first, then 0.3 μl, etc.) until we found the right dosage under which the rat did not show any side effect. This procedure is necessary because cannula tip positions are slightly different from rat to rat. When undergoing this procedure, five out of eight rats received 0.4 μl, two received 0.3 μl, and one received 0.5 μl. Still, there was no significant difference in performance, including the high-value visit percentage, departing and perimeter crossing directions, across all dosages. This information is now added in the Methods section as follows:

“If the rat showed any side effect, particularly sluggishness or aggression, we reduced the drug injection amount in the rat by 0.1 ml until we found the dosage with which there was no visible side effect. As a result, five of the rats received 0.4 ml, two received 0.3 ml, and one received 0.5 ml.” (p.25)

- I could not find the concentration of the muscimol solution that was used. The authors must clarify this and also should include a justification of the doses used, e.g. based on previous studies.

Thank you for the suggestion. We used the drug concentration of 1mg/ml, which was adapted from our previous muscimol study (Lee et al., 2014; Kim et al., 2012). The manuscript is now updated, as follows:

“…or muscimol (MUS; 1mg/ml, dissolved in saline) was infused into each hemisphere via a 33-gauge injection cannula at an injection speed of 0.167 ml/min, based on our previous study (Lee et al., 2014; Kim et al., 2012).” (p.25)

-  Please also clarify if the injectors and dummies were flush with the guides or by which distance they protruded from the guides.

The injection and dummy cannula both protruded from the guide cannula by 1 mm, and this information is now added to the Methods section, as follows:

“The injection cannula and dummy cannula extended 1 mm below the tip of the guide cannula.” (p.25)

b. Sample sizes: The authors should include sample size justifications, e.g. based on considerations of statistical power, previous studies, practical considerations, or a combination of these factors. Importantly, the smaller sample size in the control study using the spherical beacon-guided navigation task (n=5 rats) limits comparability with the main study using the place-preference task (n=8). Numerically, the findings on the control task (Figure 8) look quite similar to the findings on the place-preference task, with intermediate hippocampal muscimol infusions causing the most pronounced impairment and dorsal hippocampal muscimol infusions causing a weaker impairment. These effects may have reached statistical significance if the same sample size had been used in the place-preference study.

We set the current sample size for several reasons. First, based on our previous studies, we assumed that eight, or more than six, would be enough to achieve statistical power in a “within-animal design” study. Also, considering the ethical commitments, we tried to keep the number of animals used in the study to the least. Last, our paradigm required very long training periods (3 months on average per animal), so we could not increase the sample size for practical reasons. Regarding the reasons for the smaller sample size for the object-guided navigation task, please see the previous response to 3 above. The manuscript is now revised as follows:

“Based on our prior studies (Park et al., 2017; Yoo and Lee, 2017; Lee et al., 2014), the sample size of our study was set to the least number to achieve the necessary statistical power in the current within-subject study design for ethical commitments and practical considerations (i.e., relatively long training periods).” (p.22)

c. Statistical analyses: Why were the data of the intermediate and dorsal hippocampal PBS infusion conditions averaged for some of the analyses (Figure 5; Figure 6B and C; Figure 7B and C; Figure 8B) but not for others (Figure 6A and Figure 7A)?

The reviewer is correct that we only illustrated the separate dPBS and iPBS data for Figures 6A and 7A. Since the directional analysis is the main focus of the current manuscript, we tried to provide better visualization and more detailed examples of how the drug infusion changed the behavioral patterns between the PBS and MUS conditions in each region. Except for the visualization of DD and PCD, we averaged the PBS sessions to increase statistical power, as described in p.9. We added a detailed description of the reasons for illustrating dPBS and iPBS data separately in the manuscript, as follows:

“Note that dPBS and iPBS sessions were separately illustrated here for better visualization of changes in the behavioral pattern for each subregion.” (p.12)

Reviewing Editor (Recommendations For The Authors):

The strength of evidence rating in the assessment is currently noted as "incomplete." This can be improved following revisions if you amend your conclusions in the paper, including in the title and abstract, such that the paper's major conclusions more closely match what is shown in the Results.

Following the suggestions of the reviewing editor, we have mentioned the caveats of our study in the Limitations section of our revised manuscript (p.21). In addition, the manuscript has been revised so that the conclusions in the paper match more closely to the experimental results as can been seen in some of the relevant sentences in the abstract and main text as follows:

“Inactivation of both dHP and iHP with muscimol altered efficiency and precision of wayfinding behavior, but iHP inactivation induced more severe damage, including impaired place preference. Our findings suggest that the iHP is more critical for value-dependent navigation toward higher-value goal locations.” (Abstract; p.2)

“Whereas inactivation of the dHP mainly affected the precision of wayfinding, iHP inactivation impaired value-dependent navigation more severely by affecting place preference.” (p.5)

“The iHP causes more damage to value-dependent spatial navigation than the dHP, which is important for navigational precision” (p.12)

However, we haven’t changed the title of the manuscript as it carries what we’d like to deliver in this study accurately.

Reviewer #1 (Recommendations For The Authors):

- What were the dimensions of the environment? What distance did rats typically run to reach the reward zone? A scale bar would be helpful in Figure 1.

We used the same circular arena from the shaping session, which was 1.6 meters in diameter (p.23), and the shortest path between the start location and either reward zone was 0.62 meters. We revised the manuscript for clarification as follows:

“For the pre-training session, rats were required to find hidden reward zones…, on the same circular arena from the shaping session.” (p.23)

“Therefore, the shortest path length between the start position and the reward zone was 0.62 meters.” (p.23)

We also added a scale bar in Figure 1C for a better understanding.

- Line 169: "The scene rotation plot covers the period from the start of the trial to when the rat leaves the starting point at the center and the departure circle (Figure 2B)."

The sentence is unclear. Maybe it should be "... from the start of the trial to when the rat leaves the departure circle”.

The sentence has been revised following the reviewer's suggestion. (p.7)

- Line 147: "First, they learned to rotate the spherical treadmill counterclockwise to move around in the virtual environment (presumably to perform energy-efficient navigation)."

It is not clear from this sentence if rats naturally preferred the counterclockwise direction or if the counterclockwise direction was a task requirement.

We now clarified in our revised manuscript that it was not a task requirement to turn counterclockwise, as follows:

“First, although it was not required in the task, they learned to rotate the spherical treadmill counterclockwise…” (p.6)

- Line 149: "Second, once a trial started, but before leaving the starting point at the center, the animal rotated the treadmill to turn the virtual environment immediately to align its starting direction with the visual scene associated with the high-value reward zone."

The sentence is unclear. Maybe "Second, once a trial started, the animal rotated the treadmill immediately to align its starting direction with the visual scene associated with the high-value reward zone.”

We have updated the description following the suggestion. (p.6)

Reviewer #2 (Recommendations For The Authors):

- There are some misleading descriptions of the conclusion of the results in this paper. In this study, the functions of (a) selection of high-value target and (b) spatial navigation to the target were assessed in the behavioral experiments. The results of the pharmacological experiments showed that dHP inactivation impaired (b) and iHP inactivation impaired both (a) and (b) (Figures 5 B & D). However, the last sentence of the abstract states that dHP is important for the functions of (a) and iHP for (b). There are several other similar statements in the main text. Since the separation of (a) and (b) is an important and original aspect of this study, the description should clearly show the conclusion that dHP is important for (a) and iHP is important for both (a) and (b).

Related to the above, the paragraph title in the Discussion "The iHP may contain a value-associated cognitive map with reasonable spatial resolution for goal-directed navigation (536-537)" is also somewhat misleading: "with reasonable resolution for goal-directed behavior" seems to reflect the results of an object-guided navigation task (Figure 8). However, the term "goal-directed behavior" is also used for value-dependent spatial navigation (i.e., the main task), which causes confusion. I would like to suggest clarifying the wording on this point.

First, we need to correct the reviewer’s statement regarding our descriptions of the results. As the reviewer mentioned, our results indicated that the dHP inactivation impaired (b) but not (a), while the iHP inactivation impaired both (a) and (b). Regarding the iHP inactivation result, we focused on the impairment of (a) since our aim was to investigate spatial-value association in the hippocampus. Also, it was more likely that (a) affected (b), but not the other way, because (a) remained intact when (b) was impaired after dHP inactivation. We emphasized this difference between dHP and iHP inactivation, which was (a). Therefore, we mentioned in the last sentence of the abstract that the dHP is important for (b), which is the precision of spatial navigation to the target location, and the iHP is critical for (a).

Moreover, we would like to clarify that we were not referring to the object-guided navigation task in Figure 8 in the phrase ‘with a reasonable spatial resolution for goal-directed navigation.’ Please note that the object-guided navigation task did not require fine spatial resolution to find the reward. The phrase instead referred to the dHP inactivation result (Figure 5 and 6), where the rats could find the high-value zone even with dHP inactivation, although the navigational precision decreased. Nonetheless, we agree with the reviewer for the confusion that the title might cause, so now have updated the title as follows:

“The iHP may contain a value-associated cognitive map with reasonable spatial resolution for value-based navigation” (p.19)

- As an earlier study focusing on the physiology of iHP, Maurer et al, Hippocampus 15:841 (2005) is also a pioneering and important study, and I suggest citing it.

Thank you for the suggestion. We included the Maurer et al. (2005) study in the Introduction section as follows:

“…Specifically, there is physiological evidence that the size of a place field becomes larger as recordings of place cells move from the dHP to the vHP (Jung et al., 1994; Maurer et al., 2005; Kjelstrup et al., 2008; Royer et al., 2010).” (p.4)

- One of the strengths of this paper is that we have developed a new control system for the VR navigation task device, but I cannot get a very detailed description of this system in the Methods section. Also, no information about the system control has been uploaded to GitHub. I would suggest adding a description of the manufacturer, model number, and size of components, such as a rotary encoder and ball, and information about the software of the control system, with enough detail to allow the reader to reconstruct the system.

We have now added detailed descriptions of the VR system in the Methods section (see “2D VR system). (p.22)

Reviewer #3 (Recommendations For The Authors):

(1) Some comments on specific passages of text:

Lines 87 to 89: 'Surprisingly, beyond the recognition of anatomical divisions, little is known about the functional differentiation of subregions along the dorsoventral axis of the hippocampus. Moreover, the available literature on the subject is somewhat inconsistent.'

I would recommend to rephrase these statements. Regarding the first statement, there is substantial evidence for functional differentiation along the dorso-ventral axis of the hippocampus (e.g., see reviews by Moser and Moser, 1998, Hippocampus; Bannerman et al., 2004, Neurosci Biobehav Rev; Bast, 2007, Rev Neurosci; Bast, 2011, Curr Opin Neurobiol; Fanselow and Dong, 2010, Neuron; Strange et al., 2014, Nature Rev Neurosci). Regarding the second statement, the authors may consider being more specific, as the inconsistencies demonstrated seem to relate mainly to the hippocampal representation of value information, instead of functional differentiation along the dorso-ventral hippocampal axis in general.

We agree with the reviewer that the abovementioned statements need further clarification. The manuscript is now revised as follows:

“Surprisingly, beyond the recognition of anatomical divisions, the available literature on the functional differentiation of subregions along the dorsoventral axis of the hippocampus, particularly in the context of value representation, is somewhat inconsistent.” (p.4)

Lines 92 to 93: 'Thus, it has been thought that the dHP is more specialized for precise spatial representation than the iHP and vHP.'

I think 'fine-grained' may be the more appropriate term here. Also, check throughout the manuscript when referring to the differences of spatial representations along the hippocampal dorso-ventral axis.

Thank you for the insightful suggestion. We changed the term to ‘fine-grained’ throughout the manuscript, as follows:

“Thus, it has been thought that the dHP is more specialized for fine-grained spatial representation than the iHP and vHP.” (p.4)

“Consequently, the fine-grained spatial map present in the dHP…” (p.20)

Line 217: well-'trained' rats?

We initially used the term ‘well-learned’ to focus on the effect of learning, not training. Please note that the rats were already adapted to moving freely in the VR environment during the Shaping sessions, but the immediate counterclockwise body alignment only appeared after they acquired the reward locations for the main task. Nonetheless, we agree that the term might cause confusion, so we revised the manuscript as the reviewer suggested, as follows:

“This implies that well-trained rats aligned their bodies more efficiently…” (p.8)

Lines 309 to 311: 'Taken together, these results indicate that iHP inactivation severely damages normal goal-directed navigational patterns in our place preference task.'

Consider to mention that dHP inactivation also causes impairments, albeit weaker ones.

We thank the reviewer for the suggestion. We revised the manuscript by mentioning dHP inactivation as follows:

“Taken together, these results indicate that iHP inactivation more severely damages normal goal-directed navigational patterns than dHP inactivation in our place-preference task.” (p.11-12)

Lines 550 to 552: 'The involvement of the iHP in spatial value association has been reported in several studies. For example, Bast and colleagues reported that rapid place learning is disrupted by removing the iHP and vHP, even when the dHP remains undamaged (Bast et al., 2009).'

Bast et al. (2009) did not directly show the role of iHP in 'spatial value associations'. They suggested that the importance of iHP for behavioral performance based on rapid, one-trial, place learning may reflect neuroanatomical features of the intermediate region, especially the combination of afferents that could convey the required fine-grained visuo-spatial information with relevant afferent and efferent connections that may be important to translate hippocampal place memory into appropriate behavioral performance (this may include afferents conveying value information). More recent theoretical and empirical research suggests that projections to the (ventral) striatum may be relevant (see Tessereau et al., 2021, BNA and Bauer et al., 2021, BNA).

We appreciate the reviewer for this insightful comment. We agree with the reviewer that Bast et al. (2009) did not directly mention spatial value association; however, learning a new platform location needs an update of value information in the spatial environment. Therefore, we thought the study, though indirectly, suggested how the iHP contributes to spatial value associations. Nonetheless, to avoid confusion, we revised the manuscript, as follows:

“The involvement of the iHP in spatial value association has been reported or implicated in several studies” (p.20)

(2) Figures and legends:

Figure 2B: What do the numbers after novice and expert indicate?

The numbers indicate the rat ID, followed by the session number. We added the details to the Figure legend, as follows:

“The numbers after ‘Novice’ and ‘Expert’ indicate the rat and session number of the example.” (p.34)

Figure 2C: Please indicate units of the travel distance and latency measurements.

The units are now described in the Figure legends, as follows:

“Mean travel distance in meters and latency in seconds are shown below the VR arena trajectory.” (p.34)

Figure 3Aii: Here and in other figures - do the vector lengths have a unit (degree?)?

No, the mean vector length is an averaged value of the resultant vectors, thus having no specific unit.

Figure 5A: Please explain what the numbers on top of the individual sample trajectories indicate.

The numbers are IDs for rats, sessions, and trials of specific examples. We added the explanation to the Figure legends, as follows:

“Numbers above each trajectory indicate the identification numbers for rat, session, and trial.” (p.35)

(3) Additional comments on some methodological details:

a. Why was the non-parametric Wilcoxon signed-rank test used for the planned comparison between intermediate and dorsal hippocampal PBS infusions, whereas parametric ANOVA and post-hoc comparisons were used for other analyses? This probably doesn't make a big difference for the interpretation of the present data (as a parametric pairwise comparison would also not have revealed any significant difference between intermediate and dorsal hippocampal PBS infusions), but it would nevertheless be good to clarify the rationale for this.

We used the non-parametric statistics since our sample size was rather small (n=8) to use the parametric statistics, although we used the parametric ANOVA for some of the results because it is the most commonly known and widely used statistical test in such comparisons. However, we also checked the statistics with the alternatives (i.e., non-parametric Wilcoxon signed-rank test to parametric paired t-test and parametric One-way RM ANOVA with Bonferroni post hoc test to non-parametric Friedman’s test with Dunn’s post hoc test), and the statistical significance did not change with any of the tests. We now added the explanation in the manuscript, as follows:

“Although most of our statistics were based on the non-parametric tests for the relatively small sample size (n=8), we used the parametric RM ANOVA for comparing three groups (i.e., PBS, dMUS, and iMUS) because it is the most commonly known and widely used statistical test in such comparison. However, we also performed statistical tests with the alternatives for reference, and the statistical significances were not changed with any of the results.” (p.26)

b. Single housing of rats:

Why was this chosen? Based on my experience, this is not necessary for studies involving cannula implants and food restriction. Group housing is generally considered to improve the welfare of rats.

We chose single housing of rats because our training paradigm required precise restrictions on the food consumption of individual rats, which could be difficult in group housing.

c. Anesthesia:

Why was pentobarbital used, alongside isoflurane, to anesthetize rats for surgery (line 663)? The use of gaseous anesthesia alone offers very good control of anesthesia and reduces the risk of death from anesthesia compared to the use of pentobarbital.

Why was anesthesia used for the drug infusions (line 674)? If rats are well-habituated to handling by the experimenter, manual restraint is sufficient for intra-cerebral infusions. Therefore, anesthesia could be omitted, reducing the risk of adverse effects on the experimental rats.

I do not think that points b. and c. are relevant for the interpretation of the present findings, but the authors may consider these points for future studies to improve further the welfare of the experimental rats.

We appreciate the reviewer’s careful suggestions. For both the use of pentobarbital during surgery and anesthesia for the drug infusion, we chose to do so to avoid any risk of rats being awake and becoming anxious and to ensure safety during the procedures. They might not be necessary, but they were helpful for the experimenters to proceed with sufficient time to maintain precision. Nonetheless, we agree with the reviewer’s concern, which was the reason why we monitored the rats’ behavior for 20 minutes in the cage after drug infusion to minimize any potential influence on the task performance. We updated the relevant details in the Methods section, as follows:

“The rat was kept in a clean cage to recover from anesthesia completely and monitored for side effects for 20 minutes, then was moved to the VR apparatus for behavioral testing.” (p.25)

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Neuronal activity spatiotemporal fine-tuning of cerebral blood flow balances metabolic demands of changing neuronal activity with blood supply. Several 'feed-forward' mechanisms have been described that contribute to activity-dependent vasodilation as well as vasoconstriction leading to a reduction in perfusion. Involved messengers are ionic (K+), gaseous (NO), peptides (e.g., NPY, VIP), and other messengers (PGE2, GABA, glutamate, norepinephrine) that target endothelial cells, smooth muscle cells, or pericytes. Contributions of the respective signaling pathways likely vary across brain regions or even within specific brain regions (e.g., across the cortex) and are likely influenced by the brain's physiological state (resting, active, sleeping) or pathological departures from normal physiology.

The manuscript "Elevated pyramidal cell firing orchestrates arteriolar vasoconstriction through COX-2derived prostaglandin E2 signaling" by B. Le Gac, et al. investigates mechanisms leading to activitydependent arteriole constriction. Here, mainly working in brain slices from mice expressing channelrhodopsin 2 (ChR2) in all excitatory neurons (Emx1-Cre; Ai32 mice), the authors show that strong optogenetic stimulation of cortical pyramidal neurons leads to constriction that is mediated through the cyclooxygenase-2 / prostaglandin E2 / EP1 and EP3 receptor pathway with contribution of NPY-releasing interneurons and astrocytes releasing 20-HETE. Specifically, using a patch clamp, the authors show that 10-s optogenetic stimulation at 10 and 20 Hz leads to vasoconstriction (Figure 1), in line with a stimulation frequency-dependent increase in somatic calcium (Figure 2). The vascular effects were abolished in the presence of TTX and significantly reduced in the presence of glutamate receptor antagonists (Figure 3). The authors further show with RT-PCR on RNA isolated from patched cells that ~50% of analyzed cells express COX-1 or -2 and other enzymes required to produce PGE2 or PGF2a (Figure 4). Further, blockade of COX-1 and -2 (indomethacin), or COX-2 (NS-398) abolishes constriction. In animals with chronic cranial windows that were anesthetized with ketamine and medetomidine, 10-s long optogenetic stimulation at 10 Hz leads to considerable constriction, which is reduced in the presence of indomethacin. Blockade of EP1 and EP3 receptors leads to a significant reduction of the constriction in slices (Figure 5). Finally, the authors show that blockade of 20-HETE synthesis caused moderate and NPY Y1 receptor blockade a complete reduction of constriction.

The mechanistic analysis of neurovascular coupling mechanisms as exemplified here will guide further in-vivo studies and has important implications for human neuroimaging in health and disease. Most of the data in this manuscript uses brain slices as an experimental model which contrasts with neurovascular imaging studies performed in awake (headfixed) animals. However, the slice preparation allows for patch clamp as well as easy drug application and removal. Further, the authors discuss their results in view of differences between brain slices and in vivo observations experiments, including the absence of vascular tone as well as blood perfusion required for metabolite (e.g., PGE2) removal, and the presence of network effects in the intact brain. The manuscript and figures present the data clearly; regarding the presented mechanism, the data supports the authors' conclusions.

We thank the reviewer for his/her supportive comments as well as for pointing out pros and cons of the brain slice preparation.

Some of the data was generated in vivo in head-fixed animals under anesthesia; in this regard, the authors should revise the introduction and discussion to include the important distinction between studies performed in slices, or in acute or chronic in-vivo preparations under anesthesia (reduced network activity and reduced or blockade of neuromodulation, or in awake animals (virtually undisturbed network and neuromodulatory activity).

We have now added a paragraph in the introduction (lines 52-64) to highlight the distinction between ex vivo and in vivo models. We now also discuss that anesthetized animals exhibit slower NVC (Line 308-309).

Further, while discussed to some extent, the authors could improve their manuscript by more clearly stating if they expect the described mechanism to contribute to CBF regulation under 'resting state conditions' (i.e., in the absence of any stimulus), during short or sustained (e.g., visual, tactile) stimulation, or if this mechanism is mainly relevant under pathological conditions; especially in the context of the optogenetic stimulation paradigm being used (10-s long stimulation of many pyramidal neurons at moderate-high frequencies) and the fact that constriction leading to undersupply in response to strongly increased neuronal activity seems counterintuitive?

We now discuss more extensively the physiological relevance (lines 422-434 and 436-439) and the conditions where the described mechanisms of neurogenic vasoconstriction may occur.

We agree with the reviewer that vasoconstriction in response to a large increase in neuronal activity is counterintuitive as it leads to undersupply despite an increased energy demand. We now discuss its potential physio/pathological role in attenuating neuronal activity by reducing energy supply (lines 453-464).

Reviewer #2 (Public review):

Summary:

The present study by Le Gac et al. investigates the vasoconstriction of cerebral arteries during neurovascular coupling. It proposes that pyramidal neurons firing at high frequency lead to prostaglandin E2 (PGE2) release and activation of arteriolar EP1 and EP3 receptors, causing smooth muscle cell contraction. The authors further claim that interneurons and astrocytes also contribute to vasoconstriction via neuropeptide Y (NPY) and 20-hydroxyeicosatetraenoic acid (20-HETE) release, respectively. The study mainly uses brain slices and pharmacological tools in combination with Emx1Cre; Ai32 transgenic mice expressing the H134R variant of channelrhodopsin-2 (ChR2) in the cortical glutamatergic neurons for precise photoactivation. Stimulation with 470 nm light using 10-second trains of 5-ms pulses at frequencies from 1-20 Hz revealed small constrictions at 10 Hz and robust constrictions at 20 Hz, which were abolished by TTX and partially inhibited by a cocktail of glutamate receptor antagonists. Inhibition of cyclooxygenase-1 (COX-1) or -2 (COX-2) by indomethacin blocked the constriction both ex vivo (slices) and in vivo (pial artery), and inhibition of EP1 and EP3 showed the same effect ex vivo. Single-cell RT-PCR from patched neurons confirmed the presence of the PGE2 synthesis pathway.

While the data are convincing, the overall experimental setting presents some limitations. How is the activation protocol comparable to physiological firing frequency? 

As also suggested by Reviewer #1 we have now discussed more extensively the physiological relevance of our observations (lines 422-434 and 436-439).

The delay (minutes) between the stimulation and the constriction appears contradictory to the proposed pathway, which would be expected to occur rapidly. The experiments are conducted in the absence of vascular "tone," which further questions the significance of the findings. 

The slow kinetics observed ex vivo are probably due to the low recording temperature and the absence of pharmacologically induced vascular tone, as already discussed (lines 312-317). Furthermore, as recommended by reviewer #1, we have presented the advantages and limitations of ex vivo and in vivo approaches (lines 52-64).

Some of the targets investigated are expressed by multiple cell types, which makes the interpretation difficult; for example, cyclooxygenases are also expressed by endothelial cells.

Under normal conditions, endothelial cells only express COX-1 and barely COX-2, whose expression is essentially observed in pyramidal cells (see Tasic et al. 2016, Zeisel et al. 2015, Lacroix et al., 2015). As pointed out by Reviewer # 1, our ex vivo pharmacological data clearly indicate that vasoconstriction is mostly due to COX-2 activity, and to a much lesser extent to COX-1. Since it is well established that the previously described vascular effects of pyramidal cells are essentially mediated by COX-2 activity (Iadecola et al., 2000; Lecrux et al., 2011; Lacroix et al., 2015), we are quite confident that vasoconstriction described here is mainly due COX-2 activity of pyramidal cells.

Finally, how is the complete inhibition of the constriction by the NPY Y1 receptor antagonist BIBP3226 consistent with a direct effect of PGE2 and 20-HETE in arterioles? 

We agree with both reviewers that the complete blockade of the constriction by the NPY Y1 receptor antagonist BIBP3226 needs to be more carefully discussed. We have now included in the discussion the possible involvement of Y1 receptors in pyramidal cells, which could promote glutamate release and possibly COX-2, thereby contributing to PGE2 and 20-HETE signaling (lines 402-409).

Overall, the manuscript is well-written with clear data, but the interpretation and physiological relevance have some limitations. However, vasoconstriction is a rather understudied phenomenon in neurovascular coupling, and the present findings may be of significance in the context of pathological brain hypoperfusion.

We thank the reviewer for his/her comment and suggestions, which have helped us to improve our manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Methods:

It is not clear if brain slices (or animals) underwent one, two, or several optogenetic stimulations - especially for experiments where 'control' is compared to 'treated' - does this data come from the same vessels (before and after treatment) or from two independent groups of vessels? If repeated stimulations are performed, do these repeated stimulations cause the same vascular response?

As indicated in the Materials and Methods section, line 543: “Only one arteriole was monitored per slice” implies that the comparisons between the ‘control’ and ‘treated’ groups were made from independent groups of vessels. To clarify this point, we have added “receiving a single optogenetic or pharmacological stimulation” to this sentence lines 543-544.

For in vivo experiments, animals underwent 10-20 optogenetic stimulations with a 5-minute interstimulus interval during an experiment lasting 2 hours for maximum. Trials from the same vessel were averaged (with a 0.1 s interpolation) for analysis, and the mean per vessels is presented in the graphics.

Figure 2:

Can the authors speculate about the cause for the slow increase in indicator fluorescence from minute 1.5 onward, which seems dependent on stimulation frequency? Is this increase also present when slices from a ChR2-negative animal undergo the same stimulation paradigm?

Rhod2 was delivered by the patch pipette as indicated in the Materials and Methods section (line 514). Although a period of “at least 15 min after passing in whole-cell configuration to allow for somatic diffusion of the dye” (line 551-552) was observed, this single-wavelength Ca2+ indicator likely continued to diffuse into the cells during the optical recording thereby, inducing a slight increase in delta F/F0, which is consistent with the positive slopes of the mean fluorescence changes observed during the 30-s control baseline (Fig. 2b).

Figure 4: Why did the authors include panel a) here? Also, do the authors observe that cells with different COX-1 or -2 expression profiles show different (electrical, morphological) properties?

The purpose of panel a) in Fig. 4 was to ensure the regular spiking electrophysiological phenotype of the pyramidal neurons whose cytoplasm was harvested for subsequent RT-PCR analysis. Despite our efforts, we found no difference in the 32 electrophysiological features between COX-1 or COX-2 positive and negative cells. This is now clearly stated in the result section (lines 210-212) and a supplementary table of electrophysiological features is now provided. Because it is difficult to determine the morphology of neurons analyzed by single-cell RT-PCR (Devienne et al. 2018), these cells were not processed for biocytin labeling.

Figure 5: (1) Maybe the authors could highlight panels b-f as in vivo experiments to emphasize that these are in-vivo observations while the other experiments (especially panels g, h) are made in slices? 

We thank the reviewer for this suggestion. A black frame is now depicted in Figure 5 to emphasize in vivo experiments.

(2) What is the power of the optogenetic stimulus in this experiment? 

The power of the optogenetic stimulus was 38 mW/mm² in ex vivo experiments (see Line 527). For in vivo experiments, 1 mW pulses of 5 ms were used, the intensity being measured at the fiber end. We now provide the information for in vivo experiments in the Methods lines 639-640.

(3) Experiments were performed with Fluorescein-Dextran at 920-nm excitation which would overlap with EYFP fluorescence from the ChR2-EYFP transgene. Did the authors encounter any issues with crosstalk between the two labels? 

Crosstalk between EYFP and fluorescein fluorescence was indeed an issue. This is why arterioles were monitored at the pial level to avoid fluorescence contamination from the cortical parenchyma. Because of the perivascular space around pial arterioles, it was possible to measure vessel diameter without pollution for the parenchyma (see Author response image 1 below). To clarify this point we added the statement “which are not compromised by the fluorescence from the ChR2-EYFP transgene in the parenchyma (Madisen et al. 2012),” Line 628-629. Note that line scan acquisitions without photoactivation stimulation did not trigger any progressive change in the vessel size or resting fluorescence.

Author response image 1.

Example of a pial arteriole filled with fluorescein dextran (cyan) in an Emx1-EYFP mouse (parenchyma labeled with YFP, in cyan). The red line represents a line scan to record the change in diameter. Due to the perivascular space surrounding the arterioles, the vessel walls are clearly identified and separated from the fluorescent parenchyma.

(4) Could the authors potentially extend the time course in panel e) to show the recovery of the preparation to the baseline? 

Because arterioles were only monitored for a 40-s period during a session of optogenetic stimulation/imaging we cannot extend panel e. Nonetheless, a 5 minutes interstimulus interval was observed to allow the full recovery of the preparation to the baseline. This now clarified line 640. Of note, the arteriole shown in panel d before indomethacin treatment fully recovered to baseline after this treatment.

Also, did the authors observe any 'abnormal' behavior of the vasculature after stimulation, such as large-amplitude oscillations? (5) 

We did not specifically investigate resting state oscillations, such as vasomotion, but the 10-s long baseline recording for each measurement indicates no long lasting, abnormal and de novo behavior with a frequency higher than 0.1-0.2 Hz.

Can the authors show in vivo data from control experiments in EYFP-expressing or WT mice that underwent the same stimulation paradigm (Supplementary Figure 1 shows data from brain slices)?

The reviewer is correct to point out this important control, as optogenetic stimulation can induce a vascular response without channel rhodopsin activation at high power (see our study on the topic, Rungta et al, Nat Com 2017). We therefore tested this potential artefact in a WT mouse using our setup, with different intensities and durations of optogenetic stimulation.

Author response image 2A shows that stimulations of 10 seconds, 10 Hz, 1 mW, 5 ms pulses, i.e. the conditions we used for the experiments in Emx1 mice, did not induce dilation or constriction. Stimulation for 5 seconds with the same number of pulses, but with a higher power (4 mW), longer duration (20 ms pulses) and at a higher frequency elicited a small dilation in 1 of 2 pial arterioles (Author response image 2B). For this reason, we used only shorter (5ms) and less intense (1 mW) optogenetic stimulation to ensure that the observed dilation was solely due to Emx1 activation and not to light-induced artefactual dilation.

Author response image 2.

Optogenetic stimulation in a wild-type mouse. A. No diameter changes upon stimulations of 10 seconds, 10 Hz, 1 mW, 5 ms pulses, i.e. the conditions we used for the experiments in Emx1 mice. B. Stimulation of higher power (4 mW), longer duration (20 ms pulses) and at a higher frequency elicited a small dilation in 1 (grey traces) of 2 pial arterioles.

Figures 6 and 7: It is surprising that blockade of NPY Y1 receptors leads to a complete loss of the constriction response. As shown in Figure 7, the authors suggest that pyramidal neuron-released PGE2 (and glutamate) initiate several cascades acting on smooth muscle directly (PGE2-EP1/EP3), through astrocytes (Glu/COX-1/PGE2 or 20-HETE), or through NPY interneurons (Glu/NPY/Y1 or PGE2/NPY/Y1). This would imply that COX-1/2 and NPY/Y1 pathways act in series (as discussed by the authors). Besides the potential effects on NPY release mentioned in the discussion, could the authors comment if both (NPY and PGE2) pathways need to be co-activated in smooth muscle cells to cause constriction?

We thank the reviewer for raising this surprising complete loss of vasoconstriction by Y1 antagonism, despite the contribution of other vasoconstrictive pathways. We now discuss (lines 402-409) the possibility that activation of the neuronal Y1 receptors in pyramidal cells may also have contributed to the vasoconstriction by promoting glutamate and possibly PGE2 release. The combined activation of vascular and neuronal Y1 receptors may explain the complete blockage of optogenetically induced vasoconstriction by BIBP3226.

Reviewer #2 (Recommendations for the authors):

The complete block of the constriction by BIBP3226 needs to be carefully considered.

We thank the reviewer for stressing this point also raised by Reviewer #1. As mentioned above we now discuss (lines 402-409) the possibility that activation of the neuronal Y1 receptors in pyramidal cells may also have contributed to the vasoconstriction by promoting glutamate and possibly PGE2 release. The combined activation of vascular and neuronal Y1 receptors may explain the complete blockage of optogenetically induced vasoconstriction by BIBP3226.

Author response:

The following is the authors’ response to the previous reviews

We thank the Reviewers and the Editor for their thoughtful and constructive feedback. In the revised manuscript, we have addressed all comments thoroughly and made several substantial improvements:

● Benchmarking against state-of-the-art methods: We now provide a detailed comparison of our method, PGBAR, with MLspike and CASCADE using our cerebellar dataset recorded at high sampling rates. This comparison demonstrates that PGBAR offers more reliable spike time estimates with significantly lower variability in temporal accuracy (Figure 9).

● Quantitative analyses: We replaced qualitative statements with quantitative metrics. For example, we now report Pearson’s correlation (>0.95) of spike probabilities across trials and 100% of posterior samples with correct spike number detection during low SNR conditions (Figures 7 and 8).

● Clarified modeling rationale: We elaborated on the motivation behind modeling bursting dynamics using a hidden two-state process, which helps mitigate bias in spike detection under non-stationary firing conditions.

● Model identifiability and robustness: We demonstrate that our approach avoids parameter degeneracy through careful model design and parameter reparameterization. Sensitivity analyses (Figure 10) show that PGBAR is more robust to hyperparameter variation than MLspike.

● Improved clarity and accessibility: We revised the Introduction and Results sections to better explain the context, goals, and implications of our method, and clarified the advantages of joint parameter and state inference within our Bayesian framework.

We believe that these additions significantly strengthen our manuscript and demonstrate the utility of PGBAR for high-temporal-precision spike inference. Please find below our detailed responses to both Public Reviews and Recommendations for the authors.

Public Reviews

Reviewer #1 (Public Review):

Summary:

In this study, Diana et al. present a Monte Carlo-based method to perform spike inference from calcium imaging data. A particular strength of their approach is that they can estimate not only averages but also uncertainties of the modelled process. The authors then focus on the quantification of spike time uncertainties in simulated data and in data recorded with a high sampling rate in cerebellar slices with GCaMP8f.

Strengths:

- The authors provide a solid groundwork for sequential Monte Carlo-based spike inference, which extends previous work of Pnevmatikakis et al., Greenberg et al., and others.

- The integration of two states (silence vs. burst firing) seems to improve the performance of the model.

- The acquisition of a GCaMP8f dataset in the cerebellum is useful and helps make the point that high spike time inference precision is possible under certain conditions.

Weaknesses:

- The algorithm is designed to predict single spike times. Currently, it is not benchmarked against other algorithms in terms of single spike precision and spike time errors. A benchmarking with the most recent other SMC model and another good model focused on single spike outputs (e.g., MLSpike) would be useful to have.

We thank the reviewer for the observation. In our revised manuscript, we have included a detailed comparison of spike time accuracy between our method, MLspike, and the supervised method, CASCADE, now summarized in Figure 9. In this analysis, we used our in vitro dataset to estimate the average temporal accuracy of spike detection across the three methods. As discussed in the main text, the average temporal accuracy was defined as the time difference between ground truth and the nearest detected spikes averaged across the ground truth. The distributions of temporal accuracies across our experiments obtained from MLspike, Cascade, and PGBAR differ in their spread, with 10th-to-90th percentile ranges of 14 ms, 8 ms, and 3 ms, respectively. This result demonstrates that PGBAR spike time estimates are more reliable than MLspike and CASCADE across trials, with a narrower unbiased distribution of temporal accuracy. 

A direct comparison of PGBAR with the Sequential Binding Model (SBM) developed by Greenberg et al. was not possible since the biophysical model is designed around early GCaMP variants and thus not suitable for inference with our GCaMP8f dataset. We generally agree that employing realistic models of the calcium indicator can improve inference, however, PGBAR responds to a different question, namely how to simultaneously infer spike times and model parameters, which was still an issue with the SBM approach. 

Some of the analyses and benchmarks seem too cursory, and the reporting simply consists of a visual impression of results instead of proper analysis and quantification. For example, the authors write "The spike patterns obtained using our method are very similar across trials, showing that PGBAR can reliably detect single-trial action potential-evoked GCaMP8f fluorescence transients." This is a highly qualitative statement, just based on the (subjective) visual impression of a plot. Similarly, the authors write "we could reliably identify the two spikes in each trial", but this claim is not supported by quantification or a figure, as far as I can see. 

We thank the reviewer for this remark. We have now justified quantitatively our statement regarding the similarity across trials. In the revised preprint, we explain that in the specific experiment illustrated in Figure 7, Pearson’s pairwise correlation between spike probabilities (Gaussian filtered with 20 ms bandwidth) across trials is always larger than 0.95. The statement quoted by the reviewer, "we could reliably identify the two spikes in each trial" refers to the fact that in 100% of the posterior samples, generated from the analysis of each trial, we detected 2 spikes in the time window considered. The temporal accuracy of our detection was then illustrated for all trials in Figure 7H, where we compared the posterior distribution of the inter-spike interval between the first two spikes across trials. 

The statement referred by the Reviewer has been revised to read

(line 319) “The Pearson’s pairwise correlation between spike probabilities (Gaussian filtered with 20 ms bandwidth) across trials is always larger than 0.95, which demonstrates that PGBAR provides robust predictions across trials and it can reliably detect single-trial action potential-evoked GCaMP8f fluorescence transients.”

We revised the second statement as:

(line 324) “Despite the relatively low SNR, 100% of the posterior samples contained two spikes in the considered time interval.” 

The authors write "but the trade-off between temporal accuracy, SNR and sampling frequency must be considered", but they don't discuss these trade-offs systematically.

We thank the reviewer for the comment. We have now removed the quoted sentence in the updated preprint. We revised this statement to read: 

(line 302) “Based on this analysis we expect PGBAR to provide accurate estimates of inter-spike intervals down to 5 ms.”

It has been shown several times from experimental data that spike inference with single spike resolution does not work well (Huang et al. eLife, 2021; Rupprecht et al., Nature Neuroscience, 2021) in general. This limitation should be discussed with respect to the applicability of the proposed algorithm for standard population calcium imaging data.

We thank the reviewer for this comment. Detecting single spike times is indeed a difficult task. Compared to previous methods for single spike estimation, the advantage of our statistical approach is the rigorous analysis of uncertainties propagated by unknown model parameters and noisy recordings. This is an important aspect that was missing in previous approaches and that we were able to address thanks to our fully probabilistic approach. 

Several analyses are based on artificial, simulated data with simplifying assumptions. Ever since Theis et al., Neuron, 2016, it has been known that artificially generated ground truth data should not be used as the primary means to evaluate spike inference algorithms. It would have been informative if the authors had used either the CASCADE dataset or their cerebellum dataset for more detailed analyses, in particular of single spike time precision.

We thank the reviewer for this comment. 

To address the reviewer’s concern about single spike time precision, we have added to our revised preprint a further comparison between the temporal accuracy of PGBAR, CASCADE, and MLspike for our cerebellar dataset (Fig. 9, already discussed above). 

Nevertheless, as pointed out by the reviewer, simulated data should not be used as the primary means to evaluate the performance of an inference algorithm. However, it is standard practice in the field of model-based inference to validate the approach first with data generated by the same model used for inference. This step is usually done for two main reasons: first, for internal consistency of the method, and second, to explore the regimes where inference is achievable. We made use of simulated data to address specific questions. Specifically, in Figure 2, we illustrate the analysis of data simulated using the same model for inference. In Figure 3, we used simulated data to highlight the importance of modeling bursting activity to avoid biases induced by non-homogeneous firing rates. In Figure 6, we used simulated data to explore the theoretical accuracy of PGBAR under different conditions of signal-to-noise ratio and acquisition frequencies.

In its current state, the sum of the current weaknesses makes the suggested method, while interesting for experts, rather unattractive for experimentalists who want to perform spike inference on their recorded calcium imaging data.

In our preprint, we illustrated the application of PGBAR to benchmark data and our cerebellar recordings. Therefore, our approach can be part of the calcium imaging data analysis pipeline. The advantage of estimating statistical uncertainties and model parameters makes PGBAR an attractive tool for the wide neuroscience community interested in spike inference and statistical accuracy. In addition, as noted by Reviewer 2, our code is well documented. User-friendliness and integrating our method within GUI analysis software might be the next step if there is increasing interest in using this method.

Other comments:

One of the key features of the SMC model is the assumption of two states (bursting vs. non-bursting). However, while it seems clear that this approach is helpful, it is not clear where this idea comes from, from an observation of the data or another concept.

We thank the reviewer for this comment. As the reviewer pointed out, accounting for two firing regimes is helpful as it prevents biases in estimating the number of spikes when the firing rate is non-stationary and does not follow single-frequency Poisson statistics (as shown in Figure 3 of our preprint), as expected during in vivo recordings. Animals can alter their behavioral state and be exposed to different sensory stimulations, which condition the activity of neurons. A first step beyond the assumption of a steady firing rate is indeed to introduce a hidden two-state process to separate periods of high and low firing rates. In our revised text, we explicitly discuss the rationale behind this choice. We want to emphasize that PGBAR is the only model-based approach that accounts for nonhomogeneous firing rates. In addition, due to the binary character of the underlying bursting state and the high dimensionality of the problem, traditional optimization methods would not be applicable. We solved this problem by applying modern sequential Monte Carlo algorithms (PGAS, Lindsten 2014, for joint estimation for time-varying signals and model parameters) for the first time in the context of spike inference. In summary, the novelty of our work is both in modeling the firing statistics and the inference strategy used.

Another SMC algorithm (Greenberg et al., 2018) stated that the fitted parameters showed some degeneracy, resulting in ambiguous fitting parameters. It would be good to know if this problem was avoided by the authors.

As the reviewer pointed out, one of the weaknesses of the SBM approach is the optimization of the model parameters. This is expected, as SBM uses a biophysical model of the calcium indicator, and a general issue of dynamical models is the presence of so-called sloppy directions in the parameter space, which leads to ambiguous estimations. This is an intrinsic problem due to the model complexity also associated with poorly known parameters such as kinetic constants, which are hard to constrain experimentally. PGBAR uses a much simpler model to describe calcium transients (a second-order autoregressive process) precisely to avoid the non-identifiability of model parameters. Furthermore, we employed a parameterization of the autoregressive model (discussed in the Reparameterization section of Materials and Methods) regarding peak response to a single action potential, decay constant, and rise time (i.e., time to peak). These phenomenological parameters are well documented for different calcium indicators, which enables us to design appropriate prior distributions that significantly facilitate the identifiability of parameters.

Reviewer #2 (Public Review):

Summary:

Methods to infer action potentials from fluorescence-based measurements of intracellular calcium dynamics are important for optical measurements of activity across large populations of neurons. The variety of existing methods can be separated into two broad classes: a) model-independent approaches that are trained on ground truth datasets (e.g., deep networks), and b) approaches based on a model of the processes that link action potentials to calcium signals. Models usually contain parameters describing biophysical variables, such as rate constants of the calcium dynamics and features of the calcium indicator. The method presented here, PGBAR, is model-based and uses a Bayesian approach. A novelty of PGBAR is that static parameters and state variables are jointly estimated using particle Gibbs sampling, a sequential Monte Carlo technique that can efficiently sample the latent embedding space.

Strengths:

A main strength of PGBAR is that it provides probability distributions rather than point estimates of spike times. This is different from most other methods and may be an important feature in cases when estimates of uncertainty are desired. Another important feature of PGBAR is that it estimates not only the state variable representing spiking activity but also other variables such as baseline fluctuations and stationary model variables, in a joint process. PGBAR can therefore provide more information than various other methods. The information in the GitHub repository is well-organised.

Weaknesses:

On the other hand, the accuracy of spike train reconstructions is not higher than that of other model-based approaches, and clearly lower than the accuracy of a model-independent approach based on a deep network. The authors demonstrate convincingly that PGBAR can resolve inter-spike intervals in the range of 5 ms using fluorescence data obtained with a very fast genetically encoded calcium indicator at very high sampling rates (line scans at >= 1 kHz). It would be interesting to more systematically compare the performance of PGBAR to other methods in this regime of high temporal resolution, which has not been explored much.

We appreciate the Reviewer’s comment. In response to this observation, we have now included a thorough comparison of PGBAR, MLspike, and CASCADE in addition to the analysis of our cerebellar dataset acquired with a high sampling rate (Figure 9 in the revised preprint). PGBAR and CASCADE predictions are comparable in terms of correlation with the ground truth spikes, and both outperform MLspike. We have also quantified the spike time accuracy as the average distance between ground-truth spikes and the nearest prediction for all the methods. Among the three, PGBAR has the lowest variability of spike time accuracy across our experimental trials. We concluded that while PGBAR and CASCADE show comparable correlations with ground truth, our method provides more reliable spike time estimates.  

Recommendations for the authors

Reviewing Editor (Recommendations For The Authors):

In the discussion with reviewers, it was also suggested that while the manuscript emphasized the high temporal resolution of the method (5 ms), this was achieved under favorable conditions (very high sampling rate, fast indicator). Results cannot be compared easily to alternative methods based on published data because these conditions are unusual. Do other methods (at least some of which are presumably easier to use) achieve similar temporal resolution when applied to the same dataset? I feel this could be addressed easily and add valuable information.

We thank the Reviewing Editor for the suggestion. In our revised preprint, we have now added a full comparison between the performance of PGBAR, MLspike (as an alternative Bayesian approach), and CASCADE (as a state-of-the-art supervised method) tested on our cerebellar dataset. This analysis highlights the improved reliability of our method in terms of temporal accuracy and trial-to-trial variability.

Reviewer #1 (Recommendations For The Authors):

- It is in several places difficult to understand the bigger context of some details. For example, the authors write "In this work, we use Monte Carlo methods to approximate the posterior distribution in Eq. (13)." It would be helpful to state what the bigger goal behind this procedure is, here and at other places. Please go through the Introduction and the Results, there is some room for improvement in terms of accessibility.

We thank the Reviewer for the comment. Monte Carlo methods are generally used when dealing with intractable (non-analytical) probability distributions, which is the case for the models used for spike inference. The “bigger goal behind this procedure” is just the numerical approximation of posterior probabilities, which simply formalizes the question of estimating unknowns from data given a statistical model according to the Bayesian theorem. The advantage of Monte Carlo methods, compared to other techniques (e.g., variational methods), is to be statistically unbiased, which is one of the main reasons why we developed this approach. We clarified the goal of the Monte Carlo inference In the introduction, by adding the following text:

(line 79) “In this work we employ the particle Gibbs (PG) sampler on a bursting autoregressive (BAR) model of time series calcium-dependent fluorescence to provide not only point estimates of spike times but also quantify the statistical uncertainty of each estimate. This is important for downstream analyses such as comparing activity across neurons or conditions.”

We introduce the Results/Model section with the sentence:

(line 91) “To infer spike times and their uncertainty from noisy fluorescence traces, we first build a probabilistic generative model that captures the main dynamics underlying the fluorescence signal.”

And later on in the Results/Sequential Monte Carlo section, we added:

(line 156) “The model described in the previous section is analytically intractable, therefore we employ Monte Carlo methods to sample from the posterior distribution in Eq. (13) of spike times and model parameters, allowing us to make probabilistic inferences rather than relying on point estimates alone.”

In the Abstract: "it provides a flexible statistical framework to test more specific models of calcium indicators". What is meant by this sentence? I was unable to find any results related to this statement.

In our work, we propose a statistical model (depicted in Figure 1A) that accounts for a binary model for non-homogeneous firing, a Gaussian random walk to describe the modulation of the baseline fluorescence coupled to an autoregressive process to link spikes to fluorescence. The phrase quoted by the Reviewer refers to the possibility of replacing the autoregressive model with more specific models of calcium indicators in the future. For instance, employing the biophysical models  of calcium indicators to refine the link between spikes and calcium fluorescence. The inference algorithm does not depend on the specific spike-to-fluorescence model. In this sense, our framework is flexible as it offers the opportunity to analyze data acquired using other calcium indicators.  

The authors write "One of the key advantages of our sampling algorithm is the joint estimation of latent states and time-independent model parameters." Why is this an advantage? Advantage compared to which alternative algorithm?

We thank the reviewer for this comment. All existing spike inference algorithms use ad-hoc techniques to choose or calibrate the hyperparameters introduced. The estimation of spike times is in general highly sensitive to parameters such as the peak fluorescence in response to single action potentials, kinetic constants, noise levels, baseline, or any regularization or model parameter. These parameters are usually unknown, and all available inference methods provide additional prescriptions to calibrate them. This problem can lead to the propagation of errors and systematic biases. Modern Monte Carlo algorithms, such as the ones employed in our work, address specifically this problem by targeting the joint posterior distribution of all time-dependent variables and the model parameters. Compared to previous approaches, our method offers a statistically rigorous algorithm to identify the parameters. Furthermore, this approach enables us to use Bayesian priors to constrain their ranges without introducing ad-hoc biases and reducing the sensitivity to inaccurate choices of hyperparameters compared to other methods (MLspike), as shown in our new Figure 10 (following a suggestion from Reviewer 2), where we illustrate a parameter sensitivity analysis across MLspike and PGBAR (see responses to Reviewer 2 for further details). We clarified this in the Introduction by adding the sentence:

(line 60) “[...] Moreover, current Bayesian methods do not treat time-independent model parameters (e.g. rate constants) and dynamic variables equally. Instead, they require additional optimization procedures to calibrate model parameters, typically relying on ad-hoc tuning or grid search. This separation can lead to biased inference and poorly calibrated uncertainty estimates, particularly when parameters such as calcium decay time or spike amplitude are inaccurately specified. In contrast, our approach jointly infers both spike times and model parameters within a unified Bayesian framework, enabling uncertainty-aware estimation and avoiding separate, error-prone calibration steps.”

and In the section “Validation and performance of PGBAR” we added the text:

(line 201) “One of the key advantages of our sampling algorithm is the joint estimation of latent states and time-independent model parameters, such as spike amplitude, decay time, noise level, and baseline variance. This stands in contrast to most existing spike inference algorithms, which rely on fixed or externally calibrated parameters. Such fixed-parameter methods are vulnerable to systematic errors when parameter values are uncertain or misestimated. By jointly sampling from the posterior of all variables and parameters, our method propagates uncertainty correctly and mitigates bias due to manual tuning or poor initialization.”

We also added the following text in the discussion:

(line 411) “The estimation of time-independent model parameters is a well-known issue in spike detection algorithms, typically requiring ad-hoc calibration procedures, grid search, or manual settings. Because spike inference is sensitive to parameters such as the calcium response amplitude, rise and decay kinetics, and noise level, errors in these parameters can substantially affect the accuracy of spike time estimates. By jointly sampling model parameters and latent variables, PGBAR eliminates the need for separate calibration and ensures that uncertainty in parameters is propagated to spike time estimates in a principled way. As illustrated in Figure 10, this leads to a more robust inference compared to existing methods like MLSpike, which show greater sensitivity to parameter variation. In addition, PGBAR enables the users to calibrate the inference of action potentials by setting prior mean and variance of phenomenological parameters (e.g. rise and decay constants, firing rates, bursting frequencies).”

The authors write "We tested our approach on the fast calcium indicator GCaMP8f (...)". Be more precise. Why exactly were these experiments done, what aspects of the algorithm were supposed to be tested? It is left to the reader to make sense out of these experiments. Please provide the logic of this experiment.

We thank the reviewer for the comment. We developed our method specifically for regimes of high firing rates. For this reason, in addition to the CASCADE benchmark dataset, we have tested our approach on recordings of cerebellar granule cells due to their fast spiking patterns. For this purpose, we have employed the ultrafast state-of-the-art calcium indicator GCaMP8f combined with linescan imaging techniques to enable fast acquisition rates. We added the following text in the manuscript to clarify:

(line 306) “We tested our approach on the fast calcium indicator GCaMP8f by performing high-speed (2.8 kHz) two-photon linescan calcium imaging of cerebellar granule cells in vitro. GCaMP8f was expressed in the Crus I region of the cerebellum using adeno-associated virus (AAV) injection (Fig. 7A). Compared to GCaMP6f, GCaMP8f exhibits a rise time that is nearly an order of magnitude faster, which we expected to translate into substantially improved temporal accuracy in spike time detection.”

The authors write "If we consider as reference correlation the average across the CASCADE dataset (0.75) (...)". Why would this threshold be appropriate? This sounds arbitrary; this experiment was conducted with 2.8 kHz line scan imaging of GCaMP8, while the reference stems from low-rate imaging of older indicators.

We thank the reviewer for the remark. In the sentence quoted, we have used 0.75 as a reference for the state-of-the-art correlation between ground truth and predicted spikes and indicated the lowest temporal resolution (10 ms) where the PGBAR correlation is larger than the reference value. As the Reviewer correctly pointed out, the reference 0.75 refers to datasets with much lower acquisition frequency; therefore, in our revised preprint, we have added a comparison of the correlations obtained from PGBAR, CASCADE, and MLspike using high-speed recordings of cerebellar GCs (Figure 9), showing the increased performance of our method at high temporal resolution.  

How was PGBAR evaluated using a given dataset in Figure 4c or in Figure 7? It is unclear to the reviewer whether the priors were automatically/manually adjusted for each data set.

We thank the Reviewer for this comment. Briefly, for the CASCADE dataset, we have designed the priors for all parameters according to the existing characterization of the calcium indicator used in each experiment (Chen et al. 2013). For our cerebellar data, we have performed single stimulation trials for each recording, which we used to design priors on peak fluorescence response, decay constant, and time to peak fluorescence. In the Results section of the revised preprint, we clarified more specifically how priors were designed for the CASCADE and our cerebellar datasets. We have added the following statements:

(line 239) “Bayesian priors for all PGBAR parameters were adapted to each experiment according to the existing characterization of the different calcium indicators used (Chen et al., 2013).”

(line 314) “For each recorded soma and bouton we applied two types of stimulations. Single time point stimulation and a fixed stimulation pattern generated from a 20 Hz Poisson process with 29 stimulation time points. First, we used the single-stimulation trials to design prior distributions of amplitudes, rise and decay constants (Fig. 7C). Next, we used PGBAR to analyze independently each Poisson stimulation trial in Figure 7E. By generating thousands of posterior samples of spike time patterns, we obtained the spike probability for all time frames and trials (Fig. 7F).” 

The authors write "This analysis illustrates the variability expected when analyzing multiple trials of the same neuron." Variability across trials of neuronal activity? Or variability of spike inference?

We thank the reviewer for the comment. In the revised text, we clarify that we refer to the variability of spike inference across trials.

The original statement has been revised to read: 

(line 301) “This analysis illustrates the expected variability of spike inference when analyzing multiple trials of the same neuron.”

Technical question: How can the authors be sure that glass electrode stimulation only elicits a single AP per stimulation? This was not clear to me from the manuscript alone.

We thank the reviewer for the question. Our experimental protocol is designed in a way that in each trial we make sure a single electrical stimulation elicits a single AP. We adjust our stimulation strength until we see an all-or-none calcium transient in response to a single AP. Given the fast temporal properties of GCaMP8f, we could distinguish a single AP response from multiple APs during a single electrical stimulation. We then introduced a single stim trial ahead of each Poisson-train trial to see whether our stimulation strength could elicit a single AP response reliably and consistently. In this way, we ensured that every single stim was producing a single AP. 

Figure 8: Please explain what you mean by "bouton". What is the dashed line in (A)? Why is it interesting to look at the differences between bouton and soma?

We thank the Reviewer for the comment. In the updated text we clarified that we refer to synaptic boutons along the parallel fiber (line 311) and that the dashed line in Figure 8 refers to the ground-truth number of spikes (29). We also pointed out that the estimated delay between somas and boutons is compatible with the proximity of synaptic boutons to the stimulation site along the parallel fiber by adding the following text: 

(line 340) “This result is compatible with the proximity of synaptic boutons to the electrical stimulation along the parallel fiber. We analyzed both signals from somata and synaptic boutons because in vivo two-photon imaging can be made from both parts of the cell. Here we showed that our method performs reliably on both, demonstrating its robustness across recording sites.”

Reviewer #2 (Recommendations For The Authors):

The authors emphasised the result that PGBAR can resolve spike timing differences of 5 ms. However, this result was obtained based on fluorescence data measured with a very fast calcium indicator at very high sampling rates. It remains unclear how the performance of PGBAR compares to other methods in this regime of high temporal resolution, which has not been explored much in previous comparisons of methods. Potential users interested in this regime would benefit from a direct comparison to other approaches.

We thank the Reviewer for this suggestion. In our revised manuscript, we have included a detailed comparison of spike time accuracy between our method, MLspike, and Cascade, summarized in Figure 9. In this analysis, we used our in vitro dataset to estimate the average temporal accuracy of spike detection across the three methods. As discussed in the main text, the average temporal accuracy was defined as the temporal offset between the ground truth and the nearest detected spikes averaged across the ground truth. The distributions of temporal accuracies across our experiments obtained from MLspike, Cascade, and PGBAR differ in their spread, with 10th-to-90th percentile ranges of 14 ms, 8 ms, and 3 ms, respectively. This result demonstrates that PGBAR estimates are more reliable than MLspike and CASCADE across trials, with a narrower unbiased distribution of temporal accuracy. 

In practice, approaches are more appealing to users when they do not require dedicated measurements to estimate parameters such as rise/decay time constants of calcium fluorescence signals within cells. Users may therefore be interested to know how results would be affected if these parameters are estimated only crudely. It would thus be useful to know how spike probability estimates vary as a function of these parameters, which should be easy to test systematically, and whether the sensitivity of PGBAR to inaccurate initial parameter estimates is lower or higher than that of other methods, which should also be easy to test. As PGBAR jointly estimates spike probabilities and model parameters, it may have an advantage here over other methods.

We thank the Reviewer for this suggestion. In the new Figure 10, we show a parametric sensitivity analysis for both PGBAR and MLspike. For PGBAR, we considered the hyperparameters of the Bayesian priors associated with the peak response to a single spike and the baseline variance, which influences how much of the fluorescence can be attributed to baseline modulation. For MLspike, we considered the transient amplitude and the decay time constant. For both methods, we varied the parameters between -50% and +50% of their optimal value and estimated the correlation between predictions and ground truth as well as the number of spikes (Figure 10A). Next, we calculated the coefficient of variation across all parameter configurations for each trial (Figure 10B). Our analysis shows that, compared to previous methods, PGBAR has a much lower sensitivity to the initial choices of the hyperparameters, confirming the intuition of the Reviewer thanks to the simultaneous inference of spike times and model parameters. This result provides an important addition to our work.  

Equation 10: -1 should be in subscript (t-1). Remark: I have not fully verified the mathematical parts because some of it is beyond my expertise. 

We thank the Reviewer for pointing out the typo. This has been corrected in the revised preprint.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors intended to prove that gut GLP-1 expression and secretion can be regulated by Piezo1, and hence by mechanistic/stretching regulation. For this purpose, they have assessed Piezo1 expression in STC-1 cell line (a mouse GLP-1 producing cell line) and mouse gut, showing the correlation between Piezo1 level and Gcg levels (Figure S1). They then aimed to generate gut L cell-specific Piezo1 KO mice, and claimed the mice show impaired glucose tolerance and GLP-1 production, which can be mitigated by Ex-4 treatment (Figures 1-2). Pharmacological agents (Yoda1 and GsMTx4) and mechanic activation (intestinal bead implantation) were then utilized to prove the existence of ileal Piezo1-regulated GLP-1 synthesis (Figure 3). This was followed by testing such mechanism in a limited amount of primary L cells and mainly in the STC-1 cell line (Figures 4-7).

While the novelty of the study is somehow appreciable, the bio-medical significance is not well demonstrated in the manuscript. The authors stated (in lines between lines 78-83) a number of potential side effects of GLP-1 analogs, how can the mechanistic study of GLP-1 production on its own be essential for the development of new drug targets for the treatment of diabetes. Furthermore, the study does not provide a clear mechanistic insight on how the claimed CaMKKbeta/CaMKIV-mTORC1 signaling pathway upregulated both GLP-1 production and secretion. This reviewer also has concerns about the experimental design and data presented in the current manuscript, including the issue of how proglucagon expression can be assessed by Western blotting.

Strengths:

The novelty of the concept.

Weaknesses:

Experimental design and key experiment information.

We appreciate the reviewer's comments. Nowadays, GLP-1-based therapy is well-recognized and commonly used in treatment of Type 2 Diabetes Mellitus (T2DM). Therefore, elucidation of the mechanism that regulates GLP-1 production is essential for the development of new drug targets for the treatment of diabetes. We have revised the relevant wording in the manuscript.

In our previous studies, we have elucidated the role of mTOR/S6K pathway in regulating GLP-1 production in L cells. Using STC-1 cell line and different mouse models, including Neurog3-Tsc1−/− mice, rapamycin or L-lucine treatment to stimulate mTOR activity, we have demonstrated that mTOR stimulates proglucagon gene expression and thus GLP-1 production (Diabetologia 2015;58(8):1887-97； Mol Cell Endocrinol. 2015 Nov 15:416:9-18.). Based on our previous studies, we found that Piezo1 regulated mTOR/S6K pathway and thus proglucagon expression and GLP-1 production through a Ca2+/CaMKKbeta/CaMKIV pathway in our present study. Although we could not exclude involvement of other signaling pathways downstream of Piezo1 in regulating the cleavage of proglucagon, granule maturation and the final release of GLP-1, our present study provided evidence to support the involvement of the Ca2+/CaMKKbeta/CaMKIV/mTOR pathway in mediating the role Piezo1 in proglucagon expression and GLP-1 production.

The reviewer also expressed concerns on the use of western blot to detect proglucagon expression. Proglucagon is encoded by the GCG gene and is cleaved by PC1/3 in L cells to form mature GLP-1. In fact, measurement of intestinal proglucagon protein is a common approach for assessing GLP-1 production in the intestine. Here are some examples from other researchers: Diabetes. 2013 Mar;62(3):789-800. Gastroenterology. 2011 May;140(5):1564-74. 2004 Jul 23;279(30):31068-75. The proglucagon antibody used in our study was purchased from abcam (Cat#ab23468), which can detect proglucagon at 21 kDa.

Reviewer #2 (Public Review):

Summary:

The study by Huang and colleagues focuses on GLP-1 producing entero-endocrine (EEC) L-cells and their regulation of GLP-1 production by a mechano-gated ion channel Piezo1. The study describes Piezo1 expression by L-cells and uses an exciting intersectional mouse model (villin to target epithelium and Gcg to target GLP-1-producing cells and others like glucagon-producing pancreatic endocrine cells), which allows L-cell specific Piezo1 knockout. Using this model, they find an impairment of glucose tolerance, increased body weight, reduced GLP-1 content, and changes to the CaMKKbeta-CaMKIV-mTORC1 signaling pathway using a normal diet and then high-fat diet. Piezo1 chemical agonist and intestinal bead implantation reversed these changes and improved the disrupted phenotype. Using primary sorted L-cells and cell model STC-1, they found that stretch and Piezo1 activation increased GLP-1 and altered the molecular changes described above.

Strengths:

This is an interesting study testing a novel hypothesis that may have important mechanistic and translational implications. The authors generated an important intersectional genetics mouse model that allowed them to target Piezo1 L-cells specifically, and the surprising result of impaired metabolism is intriguing.

Weaknesses:

However, there are several critical limitations that require resolution before making the conclusions that the authors make.

(1) A potential explanation for the data, and one that is consistent with existing literature [see for example, PMC5334365, PMC4593481], is that epithelial Piezo1, which is broadly expressed by the GI epithelium, impacts epithelial cell density and survival, and as such, if Piezo1 is involved in L-cell physiology, it may be through regulation of cell density. Thus, it is critical to determine L-cell densities and epithelial integrity in controls and Piezo1 knockouts systematically across the length of the gut, since the authors do not make it clear which gut region contributes to the phenotype they see. Current immunohistochemistry data are not convincing.

We appreciate the reviewer's comment and agree that Piezo1 may impact L-cell density and epithelial integrity. To address this, we have incorporated quantification of L-cell density in new Figure Supplement 7. The quantitative results demonstrate that the specific deletion of the piezo1 gene in L cells did not significantly impact L-cell density.

Regarding epithelial integrity, we assessed the expression of tight junction proteins (ZO-1 and Occludin). As demonstrated in new Figure Supplement 8, the expression of tight junction proteins such as ZO-1 and Occludin did not show significant changes in IntL-Piezo1-/- mice compared to littermate controls.

Furthermore, we conducted double immunofluorescence of Piezo1 and GLP-1 in the duodenum, jejunum, ileum, and colon of control and IntL-Piezo1-/- mice. As illustrated in new Figure Supplement 5, Piezo1 is expressed in GLP-1-positive cells of the duodenum, jejunum, ileum, and colon of control mice, but not in IntL-Piezo1-/- mice.

(2) Calcium signaling in L-cells is implicated in their typical role of being gut chemo-sensors, and Piezo1 is a calcium channel, so it is not clear whether any calcium-related signaling mechanism would phenocopy these results.

We agree with the reviewer that Piezo1 is a calcium channel (validation of the Ca2+ influx-mediated Piezo1 in primary L cells and STC-1 cells are shown in figure 4A-C and figure 5A-C). According to our study, calcium-related signaling mechanism such as calcium/calmodulin-dependent protein kinase kinase 2 (CaMKKβ) -Calcium/Calmodulin Dependent Protein Kinase IV (CaMKIV) may contribute the phenotype seen in the _IntL-Piezo1-/_mice. In addition, we also discussed other potential calcium-related signaling mechanisms in the article's discussion section (lines645-656).

(3) Intestinal bead implantation, while intriguing, does not have clear mechanisms and is likely to provide a point of intestinal obstruction and dysmotility.

We appreciate the reviewer’s comment. To ascertain if intestinal bead implantation led to intestinal obstruction and dysmotility, we conducted a bowel transit time test and detected the postoperative defecation (As shown in new Figure Supplement 9). The results revealed no difference in bowel transit time and fecal mass between the sham-operated mice and those implanted with beads. Furthermore, to assess whether the animals were in pain or under any discomfort after intestinal bead implantation, we performed abdominal mechanical sensitivity test three days after the surgery. As indicated in Figure Supplement 9C, no difference in abdominal pain threshold was observed between sham and bead-implanted mice. These results suggest that the mice did not experience discomfort during the experiment.

(4) Previous studies, some that are very important, but not cited, contradict the presented results (e.g., epithelial Piezo1 role in insulin secretion) and require reconciliation.

Thanks a lot for the point. We have cited more previous studies. The lack of changes in blood glucose seen in Villin-Piezo1-/- mice reported by Sugisawa et. al. is not surprising (Cell. 2020 Aug 6;182(3):609-624.e21.). Actually, in another recent study from our group, we found similar results when the Villin-Piezo1-/- mice Piezo1fl/fl control mice were fed with normal chow diet. Since Villin-1 is expressed in all the epithelial cells of the gut, including enterocytes and various types of endocrine cells, the effect of L-cell Piezo1 loss may be masked by other cell types under normal condition. However, impaired glucose tolerance was seen in Villin-Piezo1-/- mice compared to the Piezo1fl/fl control mice after high fat diet for 8 weeks. We further found that Piezo1 in enterocytes exerted a negative effect on the glucose and lipid absorption. Loss of Piezo1 in enterocytes led to over-absorption of nutrients under high-fat diet. （Tian Tao, Qing Shu, Yawen Zhao, Wenying Guo, Jinting Wang, Yuhao Shi, Shiqi Jia, Hening Zhai, Hui Chen, Cunchuan Wang*, Geyang Xu*, Mechanical regulation of lipid and sugar absorption by Piezo1 in enterocytes, Acta Pharmaceutica Sinica B , Accepted, 2024. (https://doi.org/10.1016/j.apsb.2024.04.016).

Overall, this study makes an interesting observation but the data are not currently strong enough to support the conclusions.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major concerns

(1) Figure 1L was labeled wrong, and the co-localization was not clear. The KO leads to such a strong effect on the percentage of GLP-1 positive cells (panel M) but was not clearly demonstrated with immune-staining. Additional experiments are needed to prove tissue-specific knockout in gut GLP-1-producing cells only, but not in other cell lineages or elsewhere. If so, how was the change in gut Gcg mRNA expression? Importantly, this review is not clear on how to use Western blotting to measure proglucagon expression in the tissue samples. What is the size of the product? The antibody information was not provided in the manuscript. Figure 1N, a potential mechanism that affects GLP-1 production involving mTORC and downstream molecules. This comes from nowhere.

We appreciate the reviewer's feedback. The incorrect label has been corrected in the new Figure 1L. As suggested, we have performed additional experiments to demonstrate tissue-specific knockout of Piezo1 in gut GLP-1-producing cells exclusively, excluding other cell lineages or locations.

As shown in Figure Supplement 6, Piezo1 remains expressed in ileal ghrelin-positive cells and pancreatic glucagon-positive cells of IntL-Piezo1-/mice, suggesting that Piezo1 was specifically knocked out in L cells, but not in other endocrine cell types. Furthermore, the decrease was only observed in GLP-1 levels, but not PYY levels, in L cells of IntL-Piezo1-/- mice compared to controls, suggesting that the loss of Piezo1 in L cells affects GLP-1 levels specifically, but not the secretion of other hormones produced by L cells (Figure Supplement 7A-D).

In our previous studies, we have elucidated the role of mTOR/S6K pathway in regulating GLP-1 production in L cells. Using STC-1 cell line and different mouse models, including Neurog3-Tsc1−/− mice, rapamycin or L-lucine treatment to stimulate mTOR activity, we have demonstrated that mTOR stimulates proglucagon gene expression and thus GLP-1 production (Diabetologia 2015;58(8):1887-97； Mol Cell Endocrinol. 2015 Nov 15:416:9-18.). Based on our previous studies, we found that Piezo1 regulated mTOR/S6K pathway and thus proglucagon expression and GLP-1 production through a Ca2+/CaMKKbeta/CaMKIV pathway in our present study.

Although we could not exclude involvement of other signaling pathways downstream of Piezo1 in regulating the cleavage of proglucagon, granule maturation and the final release of GLP-1, our present study provided evidence to support the involvement of the Ca2+/CaMKKbeta/CaMKIV/mTOR pathway in mediating the role Piezo1 in proglucagon expression and GLP-1 production.

The reviewer also expressed concerns on the use of western blot to detect proglucagon expression. Proglucagon is encoded by the GCG gene and is cleaved by PC1/3 in L cells to form mature GLP-1. In fact, measurement of intestinal proglucagon protein is a common approach for assessing GLP-1 production in the intestine. Here are some examples from other researchers: Diabetes. 2013 Mar;62(3):789-800. Gastroenterology. 2011 May;140(5):1564-74. 2004 Jul 23;279(30):31068-75. The proglucagon antibody used in our study was purchased from abcam (Cat#ab23468), which can detect proglucagon at 21 kDa.

(2) In Figure 2, the LFD control mouse group was missing. Again, I don't understand the detection of proglucagon by Western blotting in this figure.

We appreciate the reviewer's comments. The figure 1 presents the phenotypic changes of transgenic mice under low-fat diet feeding, while figure 2 focuses on the phenotypic changes of transgenic mice under high-fat diet feeding. As we mentioned before, western blot is often used in detection of the precursor of GLP-1 named proglucagon.

(3) Why show body weight change but not body weight itself? How are the changes compared (which one serves as the control)? Again, how to do Western blotting on pro-glucagon detection?

We appreciate the reviewer's comments. Body weight has been added in new figure3. Proglucagon is the precursor of GLP-1. Intestinal proglucagon protein measurement is commonly used to assess GLP-1 production in the intestine.

(4) After reading the whole manuscript, this reviewer cannot get a clear picture of how the claimed CaMKKbeta-mTORC1 pathway mediates the function of Pieo1 activation (via the utilization of Yoda1 or intestinal bead implantation) on Gcg expression (at the transcription level or mRNA stability level?), hormone production, the genesis of GLP-1 producing cells, and the secretion of the hormone.

We appreciate the reviewer's comments. Figure 7 showed that overexpression of CaMKKbeta and CaMKIV enhanced mTOR and S6K phosphorylation, proglucagon expression and GLP-1 secretoin, while CaMKKbeta inhibitor STO609 inhibited mTOR and S6K phosphorylation, proglucagon expression and GLP-1 secretoin, suggesting CaMKKbeta and CaMKIV was involved in GLP-1 production. Moreover, mTOR inhibitor rapamycin inhibited Yoda1-induced proglucagon expression and GLP-1 secretion. These results suggested that CaMKKbeta/CaMKIV/mTOR mediated the effect of Piezo1 on GLP-1 production.

I strongly suggest that authors focus on more solid findings and dissect the mechanistic insight on something more meaningful, but not on everything (hormone coding gene expression, hormone production, and hormone secretion).

GLP-1 production involves multiple steps, including proglucagon expression, protein cleavage, granule packaging and final release. In our present study, we focused on how mechanical signals regulated proglucagon expression in L-cells and thus promote GLP-1 production. We did not exclude the possibility that mechanical signals could also affect other step of GLP-1 production and we discussed this possibility in the discussion section.

Minor concerns

(1) Figure S1A. STC-1 is a Gcg expression cell line, which shows less amount of Peio1 mRNA when compared with most primary tissue samples tested. This does not support the fundamental role of Peio1 in regulating Gcg expression. Maybe qRT-PCR will be more helpful for establishing the correlation.

Thanks a lot for the comments. As suggested, the results of qRT-PCR have been added in new Figure S1A.

(2) There are numerous scientific presentation problems in the written manuscript. Necessary literature citations are missing especially for key methods (such as bean implantation).

Thank you very much for your comments. We have made every effort to enhance the scientific presentation and have included the necessary literature citations.

Reviewer #2 (Recommendations For The Authors):

Overall, this study makes an interesting observation but the data are not currently strong enough to support the conclusions.

(1) There needs to be data localizing Piezo1 to L-cells and importantly, this needs to be quantified - are all L-cells (small bowel and colon) Piezo1 positive?

Thank you very much for your comments. We performed double immunofluorescence of Piezo1 and GLP-1 in the duodenum, jejunum, ileum, and colon of control and IntL-Piezo1-/- mice. As shown in new Figure Supplement 5, Piezo1 is expressed in about 90% of GLP-1-positive cells in the duodenum, jejunum, ileum, and colon of control mice, but not in IntL-Piezo1-/- mice.

(2) The intersectional model for L-cell transduction needs deeper validation. Images in Figure 1e are not convincing for the transduction of GFP in L-cells. The co-localization studies are not convincing, especially because Piezo1 labeling is very broad. There needs to be stronger validation of the intersectional Gcg-Villin-Piezo1 KO model. It is important to determine whether L-cell Piezo1 localization epithelium in the small bowel and colon is present (above) and affected specifically in the knockout.

Thanks a lot for the comments. In our study, we conducted a double immunofluorescence analysis for Piezo1 and GLP-1 across various segments of the gastrointestinal tract, including the duodenum, jejunum, ileum, and colon, in both control and IntL-Piezo1-/- mice. As illustrated in the newly incorporated Figure Supplement 5, it was observed that Piezo1 is indeed expressed within the cells of the aforementioned gastrointestinal segments in control mice, which are also positive for GLP-1 expression. In stark contrast, no evidence of Piezo1 expression was detected in the IntL-Piezo1-/- mice. Consistent with these findings, in situ hybridization experiments corroborated the absence of Piezo1 expression within GLP-1 positive cells in the IntL-Piezo1-/- mice, offering evidence for the successful knockout of Piezo1 in the L cells of these knockout mice. (Figure 1L and M).

In Figure 1E, IntL-Cre mice were bred with mT/mG reporter mice to further validate Cre recombinase activity and specificity. All tissues and cells of mT/mG mice express red fluorescence (membrane-targeted tdTomato; mT) at baseline, and switch to membrane-targeted EGFP in the presence of cell-specific Cre. EGFP expression was only observed scatteredly in the intestine, but not in the pancreas, indicating the intestinal-specific Cre activity in the IntL-Cre mice (Figure 1E). We have revised the relevant expressions in the main text.

(3) The authors state that "Villin-1 (encoded by Vill1 gene) is expressed in the gastrointestinal epithelium, including L cells, but not in pancreatic α cells" (lines 378-379). However, Villin is highly expressed in whole mouse islets (https://doi.org/10.1016/j.molmet.2016.05.015, Figure 1A).

Thanks a lot for the comments. Although Hassan Mziaut et al. reported that Villin is highly expressed in whole mouse islets, in that article, only the co-localization of insulin cells with Villin is mentioned, while the co-localization of glucagon and Villin is lacking.

According to our research (refer to Author response image 1 below) and previous study (Rutlin, M. et al, 2020, The Villin1 Gene Promoter Drives Cre Recombinase Expression in Extraintestinal Tissues. Cell Mol Gastroenterol Hepatol, 10(4), 864-867.e865. ), Villin is sparsely expressed in pancreatic tissue but not highly expressed in islets. We did not observed co-localization of glucagon and Villin in the pancreas (see Author response image 1A and B below). The same antibody was used to stain intestine, which show specific expression on the apical side of the intestinal villi (see Author response image 1C below).

Author response image 1.

(4) There needs to be quantification of L-cells in Piezo1 knockout. This is because several studies show Piezo1 affecting epithelial cell densities. If there are changes in L-cell or other EEC densities in Piezo1 knockout, that shift can potentially explain the changes that the authors see in glucose metabolism and weight.

We appreciate the reviewer’s comment. We agree that Piezo1 may affect L-cell density and epithelial integrity.

To assess epithelial integrity we examined the expression of tight junction proteins (ZO-1 and Occludin). As shown in new Figure Supplement 8, the expression of tight junction proteins, including ZO-1 and Occludin, remained unchanged in IntL-Piezo1-/- mice when compared to littermate controls.

To assess the L-cell density, we stained PYY, another hormone mainly secreted by L cells, in both control and IntL-Piezo1-/- mice. As shown in new Figure Supplement 7A and B, the percentage of PYY positive cells were not significantly different between control and IntL-Piezo1-/- mice, suggesting that the L-cell density was not affected by Piezo1 knockout.

(5) L-cells are classically considered to be chemosensors. Do nutritive signals, which presumably also increase calcium compete or complement or dominate L-cell GLP1 synthesis regulation?

We appreciate the reviewer ’ s comment and agree that L-cells are traditionally considered to be chemosensors. It is also recognized that nutritive signals regulate L-cell GLP1 synthesis. We have addressed these points in lines 568-595. Both nutritive and mechanical signals regulate GLP-1 production. While the food needs to be digested and nutrients absorbed before L-cells can detect the nutritive signals, mechanical stimulation provides a more direct and rapid response. However, determining whether nutritive signals compete, complement with mechanical signals or dominate in L-cell GLP-1 production will require to be further explored.

(6) The mechanism of Glp1 synthesis vs release downstream of Piezo1 is not clear. The authors hypothesize that "Piezo1 might regulate GLP-1 synthesis through the CaMKKβ/CaMKIV-mTOR signaling pathway". However, references cited suggest that Ca2+ or cAMP leads to GLP-1-release, while mTOR primarily acts on the regulation of gene expression by promoting Gcg gene expression. These pathways do not clearly link to Piezo1 GLP-1 production. These mechanisms need to be reconciled.

Thanks a lot for the point. The effect of Piezo1-mediated Ca2+ increase on GLP-1 production may be two-fold: promote Gcg gene expression through CaMKKβ/CaMKIV-mTOR and promote GLP-1 release by degranulation. Both gene expression and release are important to sustained GLP-1 production.

(7) Previous study PMID 32640190 (not cited here) found that Villin-driven Piezo1 knockout, which knocks out Piezo1 from all epithelial intestinal cells (including L-cells), showed no significant alterations in blood glucose or body weight. This is the opposite of the presented findings and therefore the current results require reconciliation.

We have cited PMID 32640190 in our revised manuscript. The lack of changes in blood glucose seen in Villin-Piezo1-/- mice reported by Sugisawa et. al. is not surprising (Cell. 2020 Aug 6;182(3):609-624.e21.). Actually, in another recent study from our group, we found similar results when the Villin-Piezo1-/_mice _Piezo1fl/fl control mice were fed with normal chow diet. Since Villin-1 is expressed in all the epithelial cells of the gut, including enterocytes and various types of endocrine cells, the effect of L-cell Piezo1 loss may be masked by other cell types under normal condition. However, impaired glucose tolerance was seen in Villin-Piezo1-/- mice compared to the Piezo1fl/fl control mice after high fat diet for 8 weeks. We further found that Piezo1 in enterocytes exerted a negative effect on the glucose and lipid absorption. Loss of Piezo1 in enterocytes led to over-absorption of nutrients under high-fat diet (Tian Tao, Qing Shu, Yawen Zhao, Wenying Guo, Jinting Wang, Yuhao Shi, Shiqi Jia, Hening Zhai, Hui Chen, Cunchuan Wang, Geyang Xu, Mechanical regulation of lipid and sugar absorption by Piezo1 in enterocytes, Acta Pharmaceutica Sinica B, Accepted, 2024, https://doi.org/10.1016/j.apsb.2024.04.016).

Reviewing Editor (Recommendations For The Authors):

Your paper - while innovative in concept and interesting - has many flaws that in my opinion need to be corrected before the paper and pre-print should be published or uploaded as pre-print. Can you please make every effort to address the missing data that the Reviewers have asked for and correct the lack of references as noted in the reviews? Thank you.

Thank you for the invaluable suggestions provided by the editors and reviewers. In response to these suggestions, we have included the missing data as requested and rectified the lack of references to the best of our ability. We hope that these revisions will effectively address the concerns raised by the editors and reviewers.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Although the use of antimony has been discontinued in India, the observation that there are Leishmania parasites that are resistant to antimony in circulation has been cited as evidence that these resistant parasites are now a distinct strain with properties that ensure their transmission and persistence. It is of interest to determine what are the properties that favor the retention of their drug resistance phenotype even in the absence of the selective pressure that would otherwise be conferred by the drug. The hypothesis that these authors set out to test is that these parasites have developed a new capacity to acquire and utilize lipids, especially cholesterol which affords them the capacity to grow robustly in infected hosts.

We sincerely appreciate Reviewer 1's thoughtful and positive evaluation of our manuscript. We acknowledge that the reviewer has a few major concerns, and we would like to address them one by one in the following section.

Major issues:

(1) There are several experiments for which they do not provide sufficient details, but proceed to make significant conclusions.

Experiments in section 5 are poorly described. They supposedly isolated PVs from infected cells. No details of their protocol for the isolation of PVs are provided. They reference a protocol for PV isolation that focused on the isolation of PVs after L. amazonensis infection. In the images of infection that they show, by 24 hrs, infected cells harbor a considerable number of parasites. Is it at the 24 hr time point that they recover PVs? What is the purity of PVs? The authors should provide evidence of the success of this protocol in their hands. Earlier, they mentioned that using imaging techniques, the PVs seem to have fused or interconnected somehow. Does this affect the capacity to recover PVs? If more membranes are recovered in the PV fraction, it may explain the higher cholesterol content.

We would like to thank the reviewer for correctly pointing out lack of details regarding PV isolation and its purity. There are multiple questions raised by the reviewer and we will answer them one by one in a point wise manner:

Firstly, “Is it at the 24 hr time point that they recover PVs?”

In the ‘Methods’ section of the original submission (Line number 606-611), there is a separate section on “Parasitophorous vacuole (PV) Isolation and cholesterol measurement”, where it is clearly mentioned, “24Hrs LD infected KCs were lysed by passing through a 22-gauge syringe needle to release cellular contents. Parasitophorous vacuoles (PV) were then isolated using a previously outlined protocol [Ref: 73].” However, we do acknowledge further details might be useful to enrich this section, and hence we would like to include the following details in the Methods section of the revised manuscript, Line 663-678 “Parasitophorous vacuoles (PV) were isolated using a previously outlined protocol with slight modifications [76]. 107 KCs were seeded in a 100 mm plate and allowed to adhere for 24Hrs. Following this infection was performed with Leishmania donovani (LD) for 24Hrs, the infected KCs were then harvested by gentle scraping and lysed through five successive passages through an insulin needle to ensure membrane disruption while preserving organelle integrity. The lysate was centrifuged at 200 × g for 10mins at 4°C to remove intact cells and large debris. The resulting supernatant was carefully collected and subjected to a discontinuous sucrose density gradient (60%, 40%, and 20%). The gradient was centrifuged at 700 × g for 25mins at 4°C to facilitate organelle separation. The interphase between the 40% and 60% sucrose layers, enriched with PVs, was carefully collected and subjected to a final centrifugation step at 12,000 × g for 25mins at 4°C. The supernatant was discarded, and the resulting pellet was enriched for purified parasitophorous vacuoles, suitable for downstream biochemical and molecular analyses. Cholesterol and protein contents in PV were determined by an Amplex Red assay kit and Bradford assay, respectively. Resulting data were represented as micrograms of cholesterol per microgram of protein.”

Secondly, What is the purity of PVs? Earlier, they mentioned that using imaging techniques, the PVs seem to have fused or interconnected somehow. Does this affect the capacity to recover PVs? If more membranes are recovered in the PV fraction, it may explain the higher cholesterol content.

We appreciate the reviewer for pointing this critical lack of data in the submitted manuscript. In the revised manuscript, we have now provided data on the purity of isolated fraction by performing Confocal imaging and Western blot against PV and cytoplasmic fraction in the revised manuscript. We admit, as rightly pointed out by the reviewer we need to access the purity of isolated PV in our experiment. As suggested by the reviewer, we have included the results of this experiment in the Figure 3C i, C ii and C iii. Our results clearly showed an efficient PV isolation with demarcating LAMP-1 positive staining around LD amastigotes, which was further validated by Western Blot showing a significant enrichment of LAMP-1 specifically in the PV fraction. This has been included as (Line 225-234), in the revised manuscript which read as, “Parasitophorous vacuole fractions were isolated from LD-S and LD-R-infected KCs at 24Hrs p.i. using a previously established protocol [35]. Following isolation, PV purity was confirmed through LAMP-1 staining which showed a significant enrichment around isolated PV in Confocal microscopy (Figure 3C i). Purity of isolated PV fractions was further confirmed by Western blot which showed an enhanced enrichment of LAMP-1 for LD-R-PV fraction as compared to LD-S-PV fraction, while PV excluded cellular fraction showed residual LAMP-1 expression confirming the purity of the isolated PV fractions (Figure 3C ii, iii). Following isolation, protein concentration was measured for isolated PV fractions using the Bradford assay, and PV fractions from both LD-S- and LD-R-infected KCs were normalized accordingly.”

(2) In section 6 they evaluate the mechanism of LDL uptake in macrophages. Several approaches and endocytic pathway inhibitors are employed. The authors must be aware that the role of cytochalasin D in the disruption of fluid phase endocytosis is controversial. Although they reference a study that suggests that cytochalasin D has no effect on fluid-phase endocytosis, other studies have found the opposite (doi: 10.1371/journal.pone.0058054). It wasn't readily evident what concentrations were used in their study. They should consider testing more than 1 concentration of the drug before they make their conclusions on their findings on fluid phase endocytosis.

We thank the reviewer for this insightful comment and we apologise for missing out mentioning Cytochalasin-D concentration. To clarify, LDL uptake by LD-R infected KCs is LDL-receptor independent as clearly shown in Section 6, Figure 4A, Figure S4A, Figure S4B i and Figure S4B ii in the  submitted manuscript. In (Figure 4F and Figure S4D) of the  submitted manuscript, as referred by the Reviewer, Cytochalasin-D was used at a concentration of 2.5µg/ml. At this concentration, we did not observe any effect of Cytochalasin-D on LDL-receptor independent fluid phase endocytosis as intracellular LD-R amastigotes was able to uptake LDL successfully and proliferate in infected Kupffer cells, unlike Latranculin-A (5µM) treatment which completely inhibited intracellular proliferation of LD-R amastigotes by blocking only receptor independent Fluid phase endocytosis (Video 2A and 2B and Figure 4E in the  submitted manuscript). In fact, the study referred by the reviewer (doi: 10.1371/journal.pone.0058054), used a concentration of 4µg/ml Cytochalasin-D which did affect both LDL-receptor dependent and also receptor independent endocytosis in bone marrow derived macrophages. We would also like to clarify that in this work during our preliminary experiments we have also tested higher concentration Cytochalasin-D (5µg/ml). However, even at this higher concentration there were no significant effect of Cytochalasin-D on LD-R induced LDL-receptor independent fluid phase endocytosis as observed from intracellular LD-R amastigote count. Thus, we strongly believe that Cytochalasin-D does not have any impact on LD-R induced fluid phase endocytosis even at higher concentration. We have now included this data as Figure 4F and Figure S4E in the revised manuscript. Further, to clear out any confusion that readers might have, and also concentration of all the inhibitors used in the study will be mentioned in the Result section (Line 278 and 284), as well as in the revised Figure labels.

(3) In Figure 5 they present a blot that shows increased Lamp1 expression from as early as 4 hrs after infection with LD-R and by 12 hrs after infection of both LD-S and LD-R. Increased Lamp1 expression after Leishmania infection has not been reported by others. By what mechanism do they suggest is causing such a rapid increase (at 4hrs post-infection) in Lamp-1 protein? As they report, their RNA seq data did not show an increase in LAMP1 transcription (lines 432-434).

We would like to express our gratitude to the reviewer for highlighting the novelty of this observation. Indeed, to the best of our knowledge, no similar findings (we could not find reference of any quantitative Western blot for LAMP-1) have been reported previously in primary macrophages infected with Leishmania donovani (LD). Firstly, we would like to point out, as stated in the Methods section (Lines 556–566) of the  submitted manuscript: "Flow-sorted metacyclic LD promastigotes were used at a MOI of 1:10 (with variations of 1:5 and 1:20 in some cases) for 4 hours, which was considered the 0th point of infection. Macrophages were subsequently washed to remove any extracellular loosely attached parasites and incubated further as per experimental requirements.” This indicates that our actual study points correspond to approximately the 8th and 28th hours post-infection”. We just wanted to clarify the time point just to prevent any potential confusion.

Now regarding LAMP1 expression, although we could not find any previous reports of its expression in LD infected primary macrophages, we would like to mention that there is a previous report (doi.org/10.1128/mBio.01464-20), which shows a similar punctuated LAMP-1 upregulation (as observed by us in Figure 5A i of the  submitted manuscript) in response to leishmania infection in nonphagocytic fibroblast. It is tempting to speculate that increased LAMP-1 expression observed in response to LD-R infected macrophages might be due to increased lysosomal biogenesis, required for degrading increased endocytosed-LDL into bioavailable cholesterol. However, since no change in LAMP-1 expression in RNA seq data (Figure 6, of the  submitted manuscript), we can only speculate that this is happening due to some post transcriptional or post translational modifications. But further work will definitely require to investigate this mechanism in details which is beyond the scope of this work. That is why, in the  submitted manuscript, (Line 432-435), we have discussed this, “Although available RNAseq analysis (Figure 6) did not support this increased expression of lamp-1 in the transcript level, it did reflect a notable upregulation of vesicular fusion protein (VSP) vamp8 and stx1a in response to LD-R-infection. LD infection can regulate LAMP-1 expression, and the role of VSPs in LDLvesicle fusion with LD-R-PV is worthy of further investigation.”

However, we agree with the reviewer that this might not be enough for the clarification. Hence in the revised manuscript this has been updated in the Discussion section (Line 465-472) as follows, “Although available RNAseq analysis (Figure 6) did not support this increased expression of lamp-1 in the transcript level, it did reflect a notable upregulation of vesicular fusion protein (VSP) vamp8 and stx1a in response to LD-R-infection. How, LD infection can regulate LAMP-1 expression, and the role of VSPs in LDL-vesicle fusion with LD-R-PV is worthy of further investigation. It is possible and has been earlier reported that LD infection can regulate host proteins expression through post transcriptional and post translational modifications [61-63]. It is tempting to speculate that LD-R amastigote might be promoting an increased lysosomal biogenesis through any such mechanism to increase supply of bioavailable cholesterol through action of lysosomal acid hydrolases on LDL.”

(4) In Figure 6, amongst several assays, they reported on studies where SPC-1 is knocked down in PECs. They failed to provide any evidence of the success of the knockdown, but nonetheless showed greater LD-R after NPC-1 was knocked down. They should provide more details of such experiments.

Although we do understand the concern raised by the reviewer, this statement in question is factually incorrect. We would like to point out that in Figure 6F i, of the  submitted manuscript (Figure 6G ii in the revised manuscript), we have demonstrated decreased NPC-1 staining following transfection with NPC-1-specific siRNA, whereas no such reduction was observed with scrambled RNA. Similar immunofluorescence data confirming LDL-receptor knockdown has also been provided in Figure S4B i of the  submitted manuscript (Figure S4B ii in the revised manuscript). However, we acknowledge that the reviewer may be referring to the lack of quantitative validation of the knockdown via Western blot. We would like to clarify although, we already had this data, but we did not include it to avoid duplication to reduce the data density of the MS. But as suggested by the reviewer, we have included western blot for both NPC-1 and LDL-receptor knock down in the revised manuscript as Figure 6G i and Figure S4B i which again confirms an efficient Knock down of NPC-1 and LDLr as we have observed with IFA.

Additionally, as suggested by the reviewer, we also noticed lack of details in Methods section of the  submitted manuscript, concerning siRNA mediated Knock down (KD). Therefore, we have included more details in the revised manuscript (Line 821-828), which read as, “For all siRNA transfections, Lipofectamine® RNAiMAX Reagent (Life Technologies, 13778100) specifically designed for knockdown assays in primary cells was used according to the manufacturer's instructions with slight modifications. PECs were seeded into 24-well plates at a density of 1x10⁵ per well, and incubated at 37°C with 5% CO2. The transfection complex, comprising (1µl Lipofectamine® RNAiMAX and 50µl Opti MEM) and (1 µl siRNA and 50µl Opti MEM) mixed together directly added to the incubated PECs. Gene silencing was checked by IFA and by Western blot as mentioned previously.”

Minor issues

(1) There is an implication that parasite replication occurs well before 24hrs post-infection?

Studies on Leishmania parasite replication have reported on the commencement of replication after 24hrs post-infection of macrophages (PMCID: PMC9642900). Is this dramatic increase in parasite numbers that they observed due to early parasite replication?

We thank the reviewer for this insightful comment and appreciate the opportunity to clarify our findings. Indeed, as rightly assumed by the Reviewer, as our data suggest, and we also believe that this increase intracellular amastigotes number is a consequence of early replication of Leishmania donovani. As already mentioned in response to Point number 3 raised by Reviewer 1, we would again like to highlight that in the Methods section (Lines 562–566), it is clearly stated: "Flow-sorted metacyclic LD promastigotes were used at a MOI of 1:10 (with variations of 1:5 and 1:20 in some cases) for 4 hours, which was considered the 0th point of infection. Macrophages were subsequently washed to remove any extracellular loosely attached parasites and incubated further as per experimental requirements.” This effectively means that our actual study points correspond to approximately the 8th and 28th hours post-infection and we just want to mention it to avoid any confusion regarding experimental time points.

Now, regarding specific concern related to Leishmania parasite replication, we would like to point out that the study referred by the reviewer on the commencement of replication after 24hrs, was conducted on Leishmania major, which may differ significantly from Leishmania donovani owing to its species and strain-specific characteristics (PMCID: PMC9642900). In fact, doubling time of Leishmania donovani (LD) has been previously reported to be approximately 11.4 hours (doi: 10.1111/j.1550-7408. 1990.tb01147.x). Moreover, multiple studies have indicated an exponential increase in intracellular LD amastigote number (more than two-fold increase) by 24Hrs post infection. (doi:10.1128/AAC.0119607, doi.org/10.1016/j.ijpara.2011.07.013). We also have a similar observation for both infected PEC and KC as depicted in Figure 1C and Figure S1C in the  submitted and revised manuscript) indicating that active replication is happening in this time frame for Leishmania donovani. Hence it was an informed decision from our side to focus on 24Hrs time point to perform the analysis on intracellular LD proliferation.

(2) Several of the fluorescence images in the paper are difficult to see. It would be helpful if a blown-up (higher magnification image of images in Figure 1 (especially D) for example) is presented.

We apologise for the inconvenience. Although we have provided Zoomed images for several other Figures in the  submitted manuscript and revised manuscript, like Figure 4, Figure 5, Figure 6 and Figure 8. However, this was not always doable for all the figures (like for Figure 1D), due to lack of space and Figure arrangements requirements. However, to accommodate Reviewer’s request we have provide a blown-up image for Figure 1D iii in the revised manuscript.

(3) The times at which they choose to evaluate their infections seem arbitrary. It is not clear why they stopped analysis of their KC infections at 24 hrs. As mentioned above, several studies have shown that this is when intracellular amastigotes start replicating. They should consider extending their analyses to 48 or 72 hrs post-infection. Also, they stop in vitro infection of Apoe/- mice at 11 days. Why? No explanation is given for why only 1 point after infection.

Reviewer has raised two independent concerns and we would like to address them individually.

Firstly, “The times at which they choose to evaluate their infections seem arbitrary. It is not clear why they stopped analysis of their KC infections at 24 hrs. As mentioned above, several studies have shown that this is when intracellular amastigotes start replicating. They should consider extending their analyses to 48 or 72 hrs post-infection.”

We have already provided a detail justification for time point selection in our response to Reviewer 1, Minor Comment 1. As mentioned already we observed a significant and sharp rise in the number of intracellular amastigotes between 4Hrs and 24Hrs post-infection in KC, with replication rate appeared to be not increasing proportionally (not doubling) after that (Figure 1C in the revised manuscript). This early stage of rapid replication of LD amastigotes, therefore likely coincides with a critical period of lipid acquisition by intracellular amastigotes (Video 3A and 3B and Figure 4E in the  submitted manuscript and revised manuscript) and thus 24Hrs infected KC was specifically selected. In this regard, we would further like to add that at 72Hrs post-infection, we noticed a notable number of infected Kupffer cells began detaching from the wells with extracellular amastigotes probably egressing out. This phenomenon potentially reflects the severe impact of prolonged infection on Kupffer cell viability and adhesion properties as shown in Video 2 in the revised manuscript and Author response image 1. This observation further influenced our decision to conclude all infection studies in Kupffer cells by the 48Hrs post-infection, which necessitate to complete the infection time point at 24 Hrs, for allowing treatment of Amp-B for another 24 Hrs (Figure 8, and Figure S5, in the  submitted manuscript and revised manuscript). We acknowledge that we should have been possibly clearer on our selection of infection time points and as the Reviewer have suggested we have included this information in the revised manuscript (Line 134-141) for clear understanding of the reader. This read as, “Interestingly, as compared to a significant and sharp rise in the number of intracellular amastigotes between 4Hrs and 24Hrs post infected KC in response to LD-R infection, the number of intracellular amastigotes although increased significantly did not doubled from 24Hrs to 48Hrs p.i. suggesting exponential LD amastigote replication between 4Hrs and 24Hrs time frame and slowing down after that (Figure 1Ci, ii). Moreover, it was also noticed that at 72Hrs p.i. a notable number of infected-KC began detaching from the wells with extracellular amastigotes probably egressing out from the infected-KCs (Video 2). Thus, 24Hrs time point was selected to conduct all further infection studies involving KCs.”

Author response image 1.

Representative images of Kupffer cells infected with Leishmania donovani at 72Hrs post-infection showing a significant morphological change. Infected cells exhibit a rounded morphology and progressive detachment. Scale bar 10µm.

Secondly “Also, they stop in vitro infection of Apoe-/- mice at 11 days. Why? No explanation is given for why only 1 point after infection.”

We apologize for not providing an explanation regarding the selection of the 11-day time point for  Apoe^-/- experiments (Figure 2 of the  submitted and revised manuscript). Our rationale for this choice is based on both previous literature and the specific objectives of our study. Previous report suggests that Leishmania donovani infection in hypercholesteraemic Apoe^-/- mice triggers a heightened inflammatory response at approximately six weeks’ post-infection compared to C57BL/6 mice, leading to more efficient parasite clearance. This is owing to unique membrane composition of Apoe^-/- which rectifies leishmania mediated defective antigen presentation at a later stage of infection (DOI 10.1194/jlr.M026914). Additionally, previous studies have also indicated that Leishmania donovani infection is well-established in vivo within 6 to 11 days post-infection in murine models (doi: 10.1128/AAC.47.5.1529-1535.2003). Given that in this experiment we particularly aimed to assess the early infection status (parasite load) in diet-induced hypercholesterolemic mice, we would like to argue that the selection of the 11-day time point was rational and well-aligned with our study objectives as this time point within this window are optimal for capturing initial parasite burden depending on initial lipid utilization, before host-driven immune clearance mechanisms could significantly alter infection dynamics. We have included this explanation in the revised manuscript (Line 170-179) as suggested by the Reviewer and this read as, “Previous report has suggested that LD infection in hypercholesteremic Apoe^-/- mice triggers a heightened inflammatory response at approximately six weeks’ post-infection compared to wild type BL/6 mice, leading to more efficient parasite clearance. This is owing to unique membrane composition of Apoe-/- which rectifies leishmania mediated defective antigen presentation at a later stage of LD infection [20]. Additionally, previous studies have also indicated that LD infection is well-established in mice within 6 to 11 days post-infection in murine models [33]. Thus to evaluate impact of initial lipid utilization on LD amastigote replication in vivo, BL/6 and diet-induced hypercholesterolemic Apoe^-/- mice were infected with GFP expressing LD-S or LD-R promastigotes and sacrificed 11 days p.i.”

Reviewer #2 (Public review):

Summary:

This study by Pradhan et al. offers critical insights into the mechanisms by which antimonyresistant Leishmania donovani (LD-R) parasites alter host cell lipid metabolism to facilitate their own growth and, in the process, acquire resistance to amphotericin B therapy. The authors illustrate that LD-R parasites enhance LDL uptake via fluid-phase endocytosis, resulting in the accumulation of neutral lipids in the form of lipid droplets that surround the intracellular amastigotes within the parasitophorous vacuoles (PV) that support their development and contribute to amphotericin B treatment resistance. The evidence provided by the authors supporting the main conclusions is compelling, presenting rigorous controls and multiple complementary approaches. The work represents an important advance in understanding how intracellular parasites can modify host metabolism to support their survival and escape drug treatment.

We would like to sincerely thank the reviewer for appreciating our work and find the evidence compelling to address the issue of emergence of drug resistance in infection with intracellular protozoan pathogens.

Strengths:

(1) The study utilizes clinical isolates of antimony-resistant L. donovani and provides interesting mechanistic information regarding the increased LD-R isolate virulence and emerging amphotericin B resistance.

(2) The authors have used a comprehensive experimental approach to provide a link between antimony-resistant isolates, lipid metabolism, parasite virulence, and amphotericin B resistance. They have combined the following approaches:

a) In vivo infection models involving BL/6 and Apoe-/- mice.

b) Ex-vivo infection models using primary Kupffer cells (KC) and peritoneal exudate macrophages (PEC) as physiologically relevant host cells.

c) Various complementary techniques to ascertain lipid metabolism including GC-MS, Raman spectroscopy, microscopy.

d) Applications of genetic and pharmacological tools to show the uptake and utilization of host lipids by the infected macrophage resident L. donovani amastigotes.

(3) The outcome of this study has clear clinical significance. Additionally, the authors have supported their work by including patient data showing a clear clinical significance and correlation between serum lipid profiles and treatment outcomes.

(4) The present study effectively connects the basic cellular biology of host-pathogen interactions with clinical observations of drug resistance.

(5) Major findings in the study are well-supported by the data:

a) Intracellular LD-R parasites induce fluid-phase endocytosis of LDL independent of LDL receptor (LDLr).

b) Enhanced fusion of LDL-containing vesicles with parasitophorous vacuoles (PV) containing LD-R parasites both within infected KCs and PECs cells.

c) Intracellular cholesterol transporter NPC1-mediated cholesterol efflux from parasitophorous vacuoles is suppressed by the LD-R parasites within infected cells.

d) Selective exclusion of inflammatory ox-LDL through MSR1 downregulation.

e) Accumulation of neutral lipid droplets contributing to amphotericin B resistance.

Weaknesses:

The weaknesses are minor:

(1) The authors do not show how they ascertain that they have a purified fraction of the PV postdensity gradient centrifugation.

(2) The study could have benefited from a more detailed analysis of how lipid droplets physically interfere with amphotericin B access to parasites.

We have addressed both these concerns in the revised Version of this work as elaborated in the following section.

Impact and significance:

This work makes several fundamental advances:

(1) The authors were able to show the link between antimony resistance and enhanced parasite proliferation.

(2) They were also able to reveal how parasites can modify host cell metabolism to support their growth while avoiding inflammation.

(3) They were able to show a certain mechanistic basis for emerging amphotericin B resistance.

(4) They suggest therapeutic strategies combining lipid droplet inhibitors with current drugs.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Experimental suggestions:

a) The authors could have provided a more detailed analysis of lipid droplet composition. This is a critically missing piece in this nice study.

We completely agree with the Reviewer on this, a more detailed analysis of lipid droplets composition, dynamics of its formation and mechanism of lipid transfer to amastigotes residing within the PV would be worthy of further investigation. To answer the Reviewer, we are already conducting investigation in this direction and have very promising initial results which we are willing to share with the Reviewer as unpublished communication if requested. Since, we plan to address these questions independently, we hope Reviewer will understand our hesitation to include these data into the present work which is already data dense. We sincerely believe existence of lipid droplet contact sites with the PV along with the specific lipid type transfer to amastigotes and its mechanism requires special attention and could stand out as an independent work by itself.

b) The macrophages (PEC, KC) could have been treated with latex beads as a control, which would indicate that cholesterol and lipids are indeed utilized by the Leishmania parasitophorous vacuole (PV) and essential for its survival and proliferation.

We thank the reviewer for this nice suggestion, which we believe will further strengthen the conclusion of this work. We have now included this data as Figure 5E in the revised manuscript. Our data showed that infected KC harbouring both LD-R amastigotes and Fluorescent Latex Beads, showed a concentrated staining of Cholesterol around amastigotes, with no positive Cholesterol staining around internalized latex beads similar to LD-S amastigotes. This observation clearly confirmed specific lipid uptake in LD-R-PV, which can not be replicated by phagocytosed Latex Beads.

c) HMGCoA reductase is an important enzyme for the mevalonate pathway and cholesterol synthesis. The authors have not commented on this enzyme in either host or parasite. Additionally, western blots of these enzymes along with SREBP2 could have been performed.

We appreciate the concern and do see the point why reviewer is suggesting this. We would like to mention that regarding HMGCoA we already do have real time qPCR data which perfectly aligns with our RNAseq data (Figure 6 A i, in the  submitted and revised manuscript), showing significant downregulation specifically in LD-R infected KC as compared to uninfected control. We are including this data as Author response image 2. However, we did not proceed with checking the level of HMGCoA at the protein level as we noticed several previous reports have suggested that HMGCoA reductase remains under transcriptional control of SERBP2 (doi.org/10.1016/j.cmet.2011.03.005, doi: 10.1194/jlr.C066712, doi:10.1194/jlr.RA119000201), which acts the master regulator of mevalonate pathway and cholesterol synthesis (doi.org/10.1161/ATVBAHA.122.317320) and SERBP2 remains significantly downregulated in response to LD-R infection (Figure 6B i and Figure 6C in the  submitted and revised manuscript). However, as suggested by the Reviewer, we have updated this data in the revised manuscript as Figure 6D. Western blot data further confirmed a significant expected downregulation of HMGCoA in response to LD-R infection.

Author response image 2.

qPCR Analysis of HMGCR Expression Following Leishmania donovani Infection: Quantitative PCR analysis showing the relative expression of hmgcr (3-hydroxy-3-methylglutaryl-CoA reductase) in Kupffer cells after 24 hours of Leishmania donovani (LD) infection compared to uninfected control cells. Gene expression levels are normalized to β-actin as an internal control, and fold change is represented relative to the uninfected condition.

d) The authors should discuss the expression pattern of any enzyme of the mevalonate pathway that they have found to be dysregulated in the transcript data.

As per the reviewer’s suggestion, we have looked into the RNA seq data and observed that apart from hmgcr, hmgcs (3-hydroxy-3methylglutaryl-CoA synthase), another key enzyme in the mevalonate pathway, is significantly downregulated in host PECs in response to LD-R infection compared to the LD-S infection. We have Discussed this in the revised manuscript (Line 484-490), which read as “Further RNA sequencing data also revealed a significant downregulation of hmgcs (3-hydroxy-3-methylglutarylCoA synthase) in LD-R infected PECs as compared to LD-S infection. Downregulation of HMGCS which catalyzes the condensation of acetyl-CoA with acetoacetyl-CoA to form 3-hydroxy-3-methylglutaryl-CoA (HMG-CoA), which serves as an intermediate in both cholesterol biosynthesis and ketogenesis further supports our observation that LD-R-infected PECs preferentially rely on endocytosed low-density lipoprotein (LDL)-derived cholesterol rather than de novo synthesized cholesterol to support their metabolic needs.”

e) The authors have followed a previously published protocol by Real F (reference 73) to enrich for parasitophorous vacuole (PV). However, they do not show how they ascertain that they have a purified fraction of the PV post-density gradient centrifugation. The authors should at least show Western blot data for LAMP1 for different fractions of density gradient from which they enriched the PV.

As we previously stated in our response to Reviewer 1, in the revised manuscript we have included a detailed analysis of purity for different fractions during PV isolation. We sincerely appreciate the reviewer for highlighting this important concern and for suggesting an approach to conduct the experiment. We have included this data as Figure 3C i, ii, iii) in the revised manuscript. Our Imaging and Western blot data showed a significant enrichment of LAMP-1 in PV fraction, and we believe this result further reinforce the conclusions of our study on increased Cholesterol.

(2) Presentation improvements:

a) Add a clear timeline for infection experiments.

As suggested by the Reviewer, we have included a schematic of Timelines for all the animal infection experiment (Figure 2Ci and Figure 7A,Fi) in the revised manuscript.

b) Provide more details on patient sample collection and analysis.

We have included more details on the sample collection in the Method section of the revised manuscript (Line 830-835), “Blood samples were collected from a total of 22 individuals spanning a diverse age range (8 to 70 years) by RMRI, Bihar, India. Among these, nine samples were obtained from healthy individuals residing in endemic regions to serve as controls. Serum was isolated from each blood sample through centrifugation, and the lipid profile was subsequently analysed using a specialized diagnostic kit (Coral Clinical System) following the manufacturer's protocol.”

c) Consider reorganizing figures to better separate mechanistic and clinical findings.

We would like to thank the reviewer for this suggestion. We felt that a major arrangement altering the sequence of the Figures as presented in the Original Submission will impact smooth flow of the story and hence, we did not disturb that. However, as suggested by the Reviewer we have performed major rearrangement within Figure 2, Figure 5 and Figure 6 and Figure 9 of the revised manuscript for a better representation of the data and convenience of the reader. Also, if the reviewer has specific suggestion regarding rearrangement of any particular figure, we will be happy to consider that.

(3) Technical clarifications needed:

a) Specify exact concentrations used for inhibitors.

We apologise for this unwanted and unnecessary mistake. Please note we have now clearly mentioned the concentration of all the inhibitors used in this study in Result section and in the Figures of the revised manuscript. For easy understanding The revised section (Line 281-287) read as, “Finally, we infected the KCs with GFP expressing LD-R for 4Hrs, washed and allowed the infection to proceed in presence of fluorescent red-LDL and Latrunculin-A (5µM), a compound which specifically inhibits fluid phase endocytosis by inducing actin depolymerization [41]. Real-time fluorescence tracking demonstrated that Latrunculin-A treatment not only prevented the uptake of fluorescent red-LDL but also severely impacted intracellular proliferation of LD-R amastigotes (Video 2A and 2B and Figure 4E). In contrast, treatment with Cytochalasin-D, which alters cellular F-actin organization but does not affect fluid phase endocytosis [41], had no effect on the intracellular proliferation of LD-R irrespective of Cytochalasin-D concentrations (2.5µg/ml and 5µg/ml respectively) (Figure 4F and Figure S4D).”

b) Include more details on image analysis methods.

Please note that in specific sections like in Line numbers 574-579, 653-658, 10471049 of the  submitted manuscript, we have put special attention in describing the Image analysis process. However, we agree that in some particular cases more details will be appreciated by the reader. Hence, we have included an additional section of Image Analysis in the Methods section of the revised manuscript. This section (Line 727-739) read as, “Image processing and analysis were conducted using Fiji (ImageJ). For optimal visualization, Giemsa-stained macrophages (MΦs) were represented in grayscale to enhance contrast and structural clarity. To improve the distinction of different fluorescent signals, pseudo-colors were assigned to fluorescence images, ensuring better differentiation between various cellular components. For colocalization analysis (Figures 3, Figure 5, Figure 6, and Figure S2), we utilized the RGB profile plot plugin in ImageJ, which allows for the precise assessment of signal overlap by generating fluorescence intensity profiles across selected regions of interest. This approach provided quantitative insights into the spatial relationship between labelled molecules within infected cells. Additionally, for analyzing the distribution of cofilin in Figure 4, the ImageJ surface plot plugin was employed. This tool enabled three-dimensional visualization of fluorescence intensity variations, facilitating a more detailed examination of cofilin localization and its potential reorganization in response to infection.”

c) Clarify statistical analysis procedures.

We have already provided a dedicated section of Statistical Analysis in the Methods section of the Original Submission and also have also shown the groups being compared to determine the statistical analysis in the Figure and in the Figure Legends of the  submitted manuscript. Furthermore, as suggested by the Reviewer we have now also add additional clarification regarding the statistical analysis performed in the revised manuscript (Line 737-749). In the revised manuscript this section read as, “All statistical analyses were performed using GraphPad Prism 8 on raw datasets to ensure robust and reproducible results. For datasets involving comparisons across multiple conditions, one-way or two-way analysis of variance (ANOVA) was conducted, followed by Tukey’s post hoc test to assess pairwise differences while controlling for multiple comparisons. A 95% confidence interval (CI) was applied to determine the statistical reliability of the observed differences. For non-parametric comparisons across multiple groups, Wilcoxon rank-sum tests were employed, maintaining a 95% confidence interval, which is particularly useful for analysing skewed data distributions. In cases where only two groups were compared, Student’s t-test was used to determine statistical significance, ensuring an accurate assessment of mean differences. All quantitative data are represented as mean ± standard error of the mean (SEM) to illustrate variability within experimental replicates. Statistical significance was determined at P ≤ 0.05. Notation for significance levels: *P ≤ 0.05; **P ≤ 0.001; ***P ≤ 0.0001.”

(4) Minor corrections:

a) Methods section could benefit from more details on Raman spectroscopy analysis.

We agree with this suggestion of the Reviewer. For providing more clarity have incorporate additional details in the Methodology for the Raman section of the revised manuscript (Line 638-649). The updated section will read as follows in the revised manuscript. “For confocal Raman spectroscopy, spectral data were acquired from individual cells at 1000× magnification using a 100 × 100 μm scanning area, following previously established specifications. After spectral acquisition, distinct Raman shifts corresponding to specific biomolecular signatures were extracted for further analysis. These included: Cholesterol (535–545 cm¹), Nuclear components (780–790 cm¹), Lipid structures (1262–1272 cm¹), Fatty acids (1436–1446 cm¹) Following spectral extraction, pseudo-color mapping was applied to highlight the spatial distribution of each biomolecular component within the cell. These processed spectral images are presented in Figure 3D1, where the first four panels illustrate the individual biomolecular distributions. A merged composite image was then generated to visualize the co-localization of these biomolecules within the cellular microenvironment, with the final panel specifically representing the spatial distribution of key biomolecules.”

b) In the methods section line 609, page 14, the authors cite Real F protocol as reference 73 for PV enrichment. However, in the very next section on GC-MS analysis (lines 615-616, page 15), they state they have used reference 74 for PV enrichment. Can they explain why a discrepancy in PV isolation references this? Reference 74 does not mention anything related to PV isolation.

Response: We would like to sincerely apologise for this confusion which probably raised from our writing of this section. We would like to confirm that our PV isolation protocol is based on the published work of Real F protocol (reference 73). However, in the next section of the submitted manuscript, GC-MS analysis was described and that was performed based on protocol referenced in 74. In the revised manuscript, we have avoided this confusion and made correction by putting the references in the proper places. In the revised manuscript, this section (Line 663-678) read as,

“GC-MS analysis of LD-S and LD-R-PV

Following a 24Hrs infection period, KCs were harvested, washed with phosphate-buffered saline (PBS), and pelleted. Subsequent to this, PV isolation was carried out using the previously described protocol [35]. After PV isolation Bradford assay was carried out for normalizing the protein concentration. The resulting equal volume of PV pellet was suspended in 20 ml of dichloromethane: methanol (2:1, vol/vol) and incubated at 4°C for 24hours. After centrifugation (11,000 g, 1 hour, 4°C), the supernatant was checked through thin layer chromatography (TLC) and subsequently evaporated under vacuum. The residue and pellet were saponified with 30% potassium hydroxide (KOH) in methanol at 80°C for 2 hours. Sterols were extracted with n-hexane, evaporated, and dissolved in dichloromethane. A portion of the clear yellow sterol solution was treated with N, O-bis(trimethylsilyl)trifluoroacetamide (BSTFA) and heated at 80°C for 1 hour to form trimethylsilyl (TMS) ethers. Gas chromatography/mass spectrometry (GC/MS) analysis was performed using a Varian model 3400 chromatograph equipped with DB5 columns (methyl-phenylsiloxane ratio, 95/5; dimensions, 30 m by 0.25 mm). Helium was used as the gas carrier (1 ml/min). The column temperature was maintained at 270°C, with the injector and detector set at 300°C. A linear gradient from 150 to 180°C at 10°C/min was used for methyl esters, with MS conditions set at 280°C, 70 eV, and 2.2 kV[77].

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors aim to assess the effect of salt stress on root:shoot ratio, identify the underlying genetic mechanisms, and evaluate their contribution to salt tolerance. To this end, the authors systematically quantified natural variations in salt-induced changes in root:shoot ratio. This innovative approach considers the coordination of root and shoot growth rather than exploring biomass and the development of each organ separately. Using this approach, the authors identified a gene cluster encoding eight paralog genes with a domain-of-unknown-function 247 (DUF247), with the majority of SNPs clustering into SR3G (At3g50160). In the manuscript, the authors utilized an integrative approach that includes genomic, genetic, evolutionary, histological, and physiological assays to functionally assess the contribution of their genes of interest to salt tolerance and root development.

Strengths:

The holistic approach and integrative methodologies presented in the manuscript are essential for gaining a mechanistic understanding of a complex trait such as salt tolerance. The authors focused on At3g50160 but included in their analyses additional DUF247 paralogs, which further contributes to the strength of their approach. In addition, the authors considered the developmental stage (young seedlings, early or late vegetative stages) and growth conditions of the plants (agar plates or soil) when investigating the role of SR3G in salt tolerance and root or shoot development.

Weaknesses:

The authors' claims and interpretation of the results are not fully supported by the data and analyses. In several cases, the authors report differences that are not statistically significant (e.g., Figures 4A, 7C, 8B, S14, S16B, S17C), use inappropriate statistical tests (e.g., t-test instead of Dunnett Test/ANOVA as in Figures 10B-C, S19-23), present standard errors that do not seem to be consistent with the post-hoc Tukey HSD Test (e.g., Figures 4, 9B-C, S16B), or lack controls (e.g., Figure 5C-E, staining of the truncated versions with FM4-64 is missing).

We thank the reviewer for their critical thoughts on the presented data. We have revised our data interpretation in the main text to more accurately reflect the results. Given the nature of our experimental setup, where we trace the roots of individual Arabidopsis seedlings grown on plates, there is considerable biological variation, which makes achieving strong statistical significance between samples or genotypes challenging. However, we think that the representation of the data as transparently as possible is necessary to provide the readers and reviewers a true picture of the variability that we are observing.  Consequently, we have centered our data interpretation around observable trends that facilitate drawing conclusions.

The choice of statistical test is closely tied to the specific biological question being addressed. In Figures 10A-C, as in Figures 6A-B, we compared all genotypes to the wild-type Col-0 within each condition, and thus ANOVA analysis, testing the general effect of the genotype across both mutants and Col-0 wild-type is not appropriate. Similarly, in Figures S19-S23, we compared each mutant line to the wild-type Col-0 under each condition.

We repeated the post-hoc Tukey HSD Test for Figures 4, 9B-C, and S16B and made adjustments where necessary (see tracked changes manuscript).

The truncated versions do not localize to the plasma membrane; instead, they are targeted to the nucleus and cytosol, mimicking the localization pattern of free GFP, which was used as a control in Panel F. Therefore, we believe that having FM4-64 as a control for these specific images is not informative, but instead using free GFP is serving as a better control in that particular construct.

In other cases, traits of root system architecture and expression patterns are inconsistent between different assays despite similar growth conditions (e.g., Figures S17A-B vs. 10A-C vs. 6A, and Figures S16B vs. 4A/9B), or T-DNA insertion alleles of WRKY75 that are claimed to be loss-of-function show comparable expression of WRKY75 as WT plants. Additionally, several supplemental figures are mislabeled (Figures S6-9), and some figure panels are missing (e.g., Figures S16C and S17E).

We thank the reviewer for raising these points and noticing the inconsistency between different assays (e.g., Figures S17A-B vs. 10A-C vs. 6A, and Figures S16B vs. 4A/9B). As mentioned above, considerable biological variation makes achieving strong statistical significance between samples, genotypes, or experiments challenging. Thus, we have centered our data interpretation around observable “trends” between experiments to facilitate drawing conclusions. Considering Figures S17A-B, 10A-C, and 6A, we acknowledge the reviewer's concern about inconsistencies in root system architecture across experiments. Initially, we observed that the sr3g mutant had reduced lateral root length compared to Col-0 under salt stress. This led us to focus on this specific phenotypic trait rather than the overall root system architecture. Despite some variation, the sr3g mutant consistently showed a similar trend/phenotype when compared to Col-0 under salt stress. We believe the variation in main root length and lateral root number between experiments is due to inherent differences between biological replicates.

Regarding gene expression patterns between Figures S16B and 4A/9B, we included part of Figure 9B (SR3G gene expression in Col-0) in Figure 4A. Figure S16B represents a completely different assay. Despite variations between assays, the overall message remains consistent: SR3G gene expression is induced under salt stress in the root but not in the shoot.

Both SR3G and WRKY75 are expressed at very low levels, even under the 75 mM salt stress condition we tested. When gene expression is so low, detecting changes is challenging due to inherent variations. Nonetheless, we observed a reduction in WRKY75 expression in the mutant lines compared to wild-type Col-0, though this reduction was not statistically significant. More importantly, we observed a similar phenotype in the wrky75 mutant, specifically reduced main root length under salt stress, consistent with the findings of the published paper in The Plant Cell by Lu et al. (2023) “Lu, K.K., Song, R.F., Guo, J.X., Zhang, Y., Zuo, J.X., Chen, H.H., Liao, C.Y., Hu, X.Y., Ren, F., Lu, Y.T. and Liu, W.C., 2023. CycC1; 1–WRKY75 complex-mediated transcriptional regulation of SOS1 controls salt stress tolerance in Arabidopsis. The Plant Cell, 35(7), pp.2570-2591”.

We appreciate the reviewer for spotting the missing labels for Figures S6-9. We corrected them at the main text, figures, and legends. We added panel C to Figure S16 and removed panel E from Figure S17 legend,  now they match to actual figures and legends.

Consequently, the authors' decisions regarding subsequent functional assays, as well as major conclusions about gene function, including SR3G function in root system architecture, involvement in root suberization, and regulation of cellular damage are incomplete.

We greatly appreciate the reviewer's thorough review of our manuscript and their critical comments. We have carefully addressed all comments and concerns.

Reviewer #2 (Public Review):

Salt stress is a significant and growing concern for agriculture in some parts of the world. While the effects of sodium excess have been studied in Arabidopsis and (many) crop species, most studies have focused on Na uptake, toxicity, and overall effects on yield, rather than on developmental responses to excess Na, per se. The work by Ishka and colleagues aims to fill this gap.

Working from an existing dataset that exposed a diverse panel of A. thaliana accessions to control, moderate, and severe salt stress, the authors identify candidate loci associated with altering the root:shoot ratio under salt stress. Following a series of molecular assays, they characterize a DUF247 protein which they dub SR3G, which appears to be a negative regulator of root growth under salt stress.

Overall, this is a well-executed study that demonstrates the functional role played by a single gene in plant response to salt stress in Arabidopsis.

The abstract and beginning of the Discussion section highlight the "new tool" developed here for measuring biomass accumulation. I feel that this distracts from the central aims of the study, which is really about the role of a specific gene in root development under salt stress. I would suggest moving the tool description to less prominent parts of the manuscript.

We appreciate the reviewer's suggestion. We believe that the innovative tool used to extract shoot-to-root ratio data from previous experiments underscores the value of reutilizing previously acquired data for new discoveries and demonstrates how reanalyzing the same data can provide fresh insights, such as identification of new allelic variation. Therefore, we decided to retain this section, as our discovery of the SR3G gene originated from this innovative tool.

Recommendations for the authors:

Reviewer #3 (Recommendations For The Authors):

Line 58 (opening sentence) - salt accumulation in the soil is not caused by evaporation exceeding input; that scenario results in soil water deficit. The issue is when the input water has dissolved ions.

We thank the reviewer for raising this important point. While this point is theoretically true, all of the water that is found in natural environments contains some dissolved ions. Therefore, drought conditions will lead, over time, to increased soil salinization. We have amended this sentence to represent our point better.

“Salt stress is predominant in the dryland areas where evaporation rate exceeds water input. As all water contains dissolved ions, the prolonged exposure to drought stress results in increased accumulation of salts in the upper soil layers 1–3.”

I feel that it would be helpful, for replication and for interpretation, if the authors could provide water potentials for the growing media used throughout. What water potentials are the plants experiencing when grown in 1/2 MS + agar at 0, 75, and 150mM NaCl? Juenger and Verslues present a great recent discussion of the importance of reporting these values (Juenger, T. E. and P. E. Verslues (2023). "Time for a drought experiment: Do you know your plants' water status?" Plant Cell 35(1): 10-23.)

Critically, how do the water potentials experienced by agar-grown plants compare to those experienced in soil-grown plants? As a stated aim of this study is to allow translation to crops these data are very important to convince physiologists of the relevance of the results.

We thank the reviewer for raising this important point. We completely agree that growing plants on agar plates is an artificial setup and knowing the water potential of the plants within this setup would be highly informative. However, as indicated in review by Juenger and Verslues 2023, the agar plate setup is much more reproducible compared to various soil conditions, and we report the media composition in sufficient detail for it to be reproduced in other laboratory conditions.

Furthermore, while investigating the water status of plants and soil is indeed intriguing, it is beyond the scope of this study and would require us to redo the experiments with specific tools listed within the Juennger and Verslues review, which are currently not within our laboratory equipment list.

Importantly, any changes reported in this manuscript apply equally to both wild-type and mutant lines under all conditions. We provide extensive report on the soil type used, as well as soil quantity. We are using the gravimetric method to determine the water content, and salt stress application, as described in previous works from our lab (Yu and Sussman et al., 2024 Plant Physiology and Awlia et al., 2016 Frontiers in Plant Science). 

Nonetheless, we have now included water content measurements for soil-grown plants under different conditions, calculated by subtracting dry weight from fresh weight (new Fig. S24). Although plant water content may not fully capture the water status of the media or soil, our measurements did not reveal any significant differences in water content between genotypes across the various conditions tested.

Line 69- missing an "and" after "(ABA)."

Thanks. We added the missing “and”.

Line 79 - I think the association being made is between natural variation in root and shoot growth and genetic variants, not "underlying genes."

We thank the reviewer for this suggestion. The cause for the identified association indeed relies on allelic variation within the genetic region. We have re-phrased this sentence within the manuscript.

“Many forward genetic studies were highly successful in associating natural variation in root and shoot growth with allelic variation in gene coding and promoter regions, thereby identifying potential new target traits for improved stress resilience 18,20,21.”

Figure 1 - what do "seGF" and "reGF" stand for? Shoot and root growth rate, respectively, but there are extra letters in there…

The abbreviations stand for shoot exponential Growth Factor and root exponential Growth factor. An explanation of the acronym has been added to the text.

“The increase in the projected area of shoot and root (Fig. S2) was used to estimate (A) shoot and (B) root exponential growth rate (seGR and reGR respectively).”

Figure 1 legend - there's an "s" missing in "across." And two "additionally" in the penultimate sentence.

Thanks for spotting the errors. We fixed these errors.

Line 109 - how was the white balance estimated for the images on the flatbed scanner?

Within the developed tool, we have not adjusted or controlled for white balance in any way, as the white balance from the flatbed scanner is kept at one value. The tool transforms the imaged pixels into bins consisting of white (root), green (shoot), and blue (place) pixels based on the closest distance in the RGB scale to the particular color, which makes correcting for white balance obsolete. We have provided an additional explanation for this within the M&M section.

“A Matlab-based tool was developed to simplify and speed up the segmentation and analysis pipeline. For automatic segmentation, the tool uses a combination of image operations (histogram equalization), thresholding on different color spaces (e.g., RGB, YCbCr, Lab, HSV), and binary image processing (boundary and islands removal). As the tool is digitalizing various color scales and classifies pixels into either white (root), green (shoot) or blue (background) categories, the adjustment for white balance is obsolete. ”

GWAS was performed separately on traits measured at control, 75mM, and 150mM NaCl treatments. Would it also be informative to map the STI measurement (i.e. plasticity) introduced here?

We thank the reviewer for this important point. We have performed GWAS on both “raw” and STI traits, however, we found that the identified associations were not as abundant as the ones identified with “raw traits”. This makes sense, as we are compounding the root or shoot growth under both conditions, and plastic responses to the environment are expected to be genetically more complex, as they involve more genetic regulators compared to phenotypes that have low plasticity. We have added this as a part of the result description, as we acknowledge that this might be an interesting observation for the field to build upon, and might provide fodder for new methods to deconvolute the complexity in mapping the plastic traits. 

“To identify genetic components underlying salt-induced changes in root:shoot ratio, we used the collected data as an input for GWAS. The associations were evaluated based on the p-value, the number of SNPs within the locus, and the number of traits associated with individual loci. As Bonferroni threshold differs depending on the minor allele count (MAC) considered, we identified significant associations based on a Bonferroni threshold for each subpopulation of SNPs based on MAC (Table S3). While we conducted a GWAS on directly measured traits, as well as their Salt Tolerance Index (STI) values, however the amount of associations with STI was much lower compared to directly measured traits (Table S3). This observation aligns with the understanding that plastic responses to environmental conditions tend to be genetically more complex. This complexity likely stems from the involvement of more genetic regulators compared to low-plasticity phenotypes.”

Line 167 - how was LD incorporated into this analysis? Did you use a genome average? Or was LD allowed to vary (as it does) across the genome?

Initially, we have used genome average LD for this purpose (10 kbp for Arabidopsis), and extended the region of interest based on the number of coding genes within the window. We have added this as a part of description to our manuscript.

“For the most promising candidate loci (Table S4), we have identified the gene open reading frames that were located within the genome-wide linkage-disequilibrium (LD) of the associated SNPs. The LD was expanded if multiple SNPs were identified within the region, and the region of interest was expanded based on the number of coding genes within the LD window. ”

Line 291 - I think the water potentials are essential, here. What does 50% of soil water holding capacity equal in these soils? In the substrate that we use in our lab, that would represent a considerable soil water deficit even without any salts in the soil.

We thank the reviewer for this comment. As Arabidopsis is occurring naturally in low soil water holding capacity soils (i.e. sandy soils), it is typically growing better in soils that are not very saturated with the water. Throughout many experiments, performed within this study, and other studies performed in our lab (results reported in Awlia et al., 2016 Frontiers in Plant Science and Yu & Sussman et al., 2024 Plant Physiology), we have not observed any drought like symptoms at 50% soil water holding capacity. The fact that this is reproducible across similar soil types across two laboratories (one in Saudi Arabia and one in the USA) is not to be dismissed. Again - we are currently not equipped to measure water potentials for these plants, as this is not a standard practice (yet) for stress experiments, but we are taking these comments on board for all of our future experiments.

Moreover, our control plants are also “dried down” to 50% of SWHC, and soaked in non-saline water during the “salt stress treatment” to make sure that the soil water saturation is accounted for within the experimental setup. This “dry down” of soil is necessary to ensure equal and effective salt penetration into the soil particles. More details on this method can be found in Awlia et al., 2016.

Again - We have added a new dataset measuring water content in individually soil-grown plants under different conditions as a proxy for soil water status (see new Fig. S24). While we did not observe any significant differences in water content between genotypes under the various conditions, the sr3g mutant showed a slightly higher, though non-significant, water content compared to wild-type Col-0 under control conditions.

We have provided additional information and comments to warn the readers about this method:

“The seeds were germinated in ½ MS media for one week, as described for the agar-based plate experiments. One week after germination, the seedlings were transplanted to the pot (12 x 4 cm insert) containing the Cornell Mix soil (per batch combine: 0.16 m3 of peat moss, 20.84 kg of vermiculite, 0.59 kg of Uni-Mix fertilizer, and 2.27 kg of lime) watered to 100% water holding capacity and placed in the walk-in growth chamber with the 16 h light / 8 h dark period, 22°C and 60% relative humidity throughout the growth period. When all of the pots dried down to the weight corresponding to 50% of their water holding capacity, they were soaked for 1 h in tap water or a 200 mM NaCl solution, resulting in an effective concentration of 100 mM NaCl based on the 50% soil water holding capacity, which corresponded to a moderate level of salt stress (Awlia et al., 2016). The control pots were soaked for the same length of time in 0 mM NaCl solution, to account for the soil saturation effect. We then allowed the pots to be drained for 2-3 h to eliminate excess moisture. The pots were placed under phenotyping rigs equipped with an automated imaging system (Yu et al., 2023) and the pot weight was measured daily to maintain the reference weight corresponding to 50% of the soil water holding capacity throughout the experiment. We would like to note that this gravimetric based method for application of salt stress has been developed for soils typically used for pot-grown plants, with relatively high water holding capacity (Awlia et al. 2016). Within these specific conditions, no drought stress symptoms were observed.”

Lines 415-416 - are these contrasts significant? Figure S3 likewise does not have any notation for significant differences in the means.

We have previously not tested the stronger effect of 125 mM vs 75 mM on relative root and shoot growth, and thus these test results were initially not included in Fig. S3. We have now added the tests and included them within Fig. S3, and added description of their significance into the main body of the manuscript:

“In comparison, the growth rates of the shoot were significantly reduced to 0.71 and 0.43 of the control in 75 and 125 mM NaCl treatments, respectively (Fig. S3). While the mean value of root:shoot growth rate did not change upon salt stress treatment, the variance in the root:shoot ratio significantly expanded with the increasing concentrations of salt (Fig. 1C). These results suggest that while root and shoot growth are well coordinated under non-stress conditions, salt stress exposure results in loss of coordination of organ growth across Arabidopsis accessions.”

Line 418 - same comment as preceding. Is this change in variance significant?

We have previously not tested this. We have now added the ANOVA tests and included them within each figure, and added description of their significance into the main body of the manuscript. (see text above)

Line 421 - why would we expect there to be a correlation between root:shoot growth ratio and seedling size?

We were trying to use the seedling size as a proxy for “fitness” - or how well the plants can survive under these specific conditions. We were testing here whether any simple and directional strategy - such as increase or decrease in root:shoot ratio under salt stress - is resulting in better salt tolerance - which would translate into larger overall seedlings. We have rephrased this within the manuscript, to better explain the hypothesis being tested within this specific figure:

“To test whether there is a clear directional correlation between the change in root:shoot ratio and overall salt stress tolerance, we have used the overall seedling size as a proxy for plant salt tolerance (Fig. S4, S5). No significant correlation was found between the root:shoot growth ratio and total seedling size (Fig. S4, S5), indicating that the relationship between coordination of root and shoot growth and salt tolerance during the early seedling establishment is complex.”

Line 438 - I think a stable web link would be more appropriate than listing Dr. Nordborg's email address.

Sorry about this. There is a glitch with our reference citing software. We agree, and thank the reviewer for noticing this! We assigned reference number 43 to it.

Line 439 - I expect that many of your readers may not be experienced with GWAS. Can you provide an explanation as to why only one locus was detected with both the 250K SNP panel and the 4M SNP panel?

We thank the reviewer for raising this point. We have added additional explanation to this observation:

“Increased SNP density can provide more potential associations, highlighting the associated loci with more confidence, due to more SNPs being detected within specific region. The different panels could capture different LD blocks across the genome. If the locus detected by both panels is in a region of strong LD or under selection, it could be detected consistently. In contrast, other loci may not be captured well by the lower-density 250K SNP panel. The new GWAS revealed 32 additional loci, with only one significantly associated locus being picked up by both 250k and 4M SNPs GWAS (locus 30, Table S3). The detection of only one common locus between the two SNP panels is likely due to differences in resolution, statistical power, and how well each panel captures the genomic regions associated with the trait. ”

Figure 2A and B - I suggest adding the p-value cutoff to the y-axis of the Manhattan Plots

We thank the reviewer for this suggestion, however this is not appropriate. The genome wide p-value cutoffs for GWAS studies are arbitrary, and we have not used a genome-wide cutoff for our SNPs, but rather used cutoffs depending on the minor allele frequency. Therefore, we think adding a straight line to the graphs in Fig. 2A-B representing the overall cutoff, would be misleading. Please see below the text where we explain how the threshold was calculated for individual groups of SNPs with varying MAF:

“The GWAS associations were evaluated for minor allele count (MAC) and association strength above the Bonferroni threshold with -log10(p-value/#SNPs), calculated for each sub-population of SNPs above threshold MAC (Table S3, Bonf.threshold.MAC.specific)”

Line 490-492 - Presents the results of the gene tree to support a model in which SR3G diverged from AT3G50150 prior to the speciation events leading to Capsella and Arabidopsis. But this topology requires at least two independent losses of SR3G - can you rule out the hypothesis that the position of SR3G on the gene tree is a result of long branch attraction? Given the syntenic orientation of AT3G50150 and SR3G, and apparent directional selection experienced by the latter lineage, it seems more parsimonious that AT3G50150 and SR3G arose from a very recent duplication event.

We agree with the reviewer that it seemed most parsimonious for AT3G50160 (SR3G) to be a recent tandem duplication of AT3G50150 – and this was certainly our expectation given the other tandem duplications that have occurred in this genomic region. However, irrespective of the type of alignment from which we built the phylogeny (nucleotide vs AA; sometimes nucleotide is noisier but provides more information) we were never able to recapitulate a tree where AT3G50160 was immediately sister to AT3G50150 – even with a long branch for AT3G50160 indicating a rapid pace of nucleotide/AA change relative to AT3G50150. In regards to long branch attraction, it is our interpretation that long branch attraction typically requires multiple long branches that get placed together at a poorly supported node where sampling is sparse (https://www.nature.com/articles/s41576-020-0233-0), whereas we have the single long branch for AT3G50160, and all other A/C clade (Arabidopsis/Camelina/Capsella) members forming a lineage with a much shorter branch. To test the possibility of long branch attraction we subtracted out individual members of the AT3G50150/160 clade to see if there was algorithmic uncertainty in the placement of AT3G50160. We did not observe this in any of the branch subtractions that we performed (see below). Thus, it appears that we must stick with our original interpretation. If the reviewer would like us to soften this interpretation, we would be more than happy to do so, as it does not impact the overall conclusions for AT3G50160 being a rapidly evolving member of this clade.

Author response image 1.

Line 494 (and throughout) - I expect that all of the genes being studied herein are "experiencing selection," even if it's boring-old purifying selection on functionally conserved proteins. I think you mean to say "directional selection."

We thank the reviewer for this comment and completely agree that we lacked precision on our statement. We have corrected this throughout the manuscript.

Line 497 - state the background and foreground values of omega, here.

We apologize for not including these values and have added them at this point in the manuscript (new Table S6).

Line 511 and Line 673 - Inspection of Figure S13B suggests that SR3G is not "predominantly" expressed nor does it have the "highest enrichment" in the root stele. Certainly, among root cell types, this is predominant. But it appears to be quite highly expressed in late-stage seeds and some floral organs, as well.

We appreciate the reviewer for recognizing that SR3G is not a highly expressed gene. In root cell types, its expression is enriched in the root stele. Overall, SR3G is expressed at both early and later developmental stages. Our investigation of later developmental stages related to seed production did not reveal any significant phenotypic differences in fertility.

Line 514 - "54-folds" should be "54-fold."

Thanks. We made corrections.

Figure 7 - For symmetry, I suggest adding the "Beginning of salt stress" arrow to the "Early Stress" panel as well (even if it's right at day 0).

Thanks. We added the arrow to Early Stress in both Panels A and B.

Figure S2 - both graphs should have the same scale on the y-axis

Thanks - we have now re-plotted the graph with the matching y-axis scales.

Line 531 - I feel that this is a significant overstatement. The strongest statement supported by the results presented here is that SR3G is the most prominent DUF247 studied herein in root development under salt stress.

Thanks for the comments. We rephrase the statement.

“These results suggest that SR3G is the most prominent DUF247 studied within our study to affect root development under salt stress.”

Lines 583-605 - These data seem to me to be tangential to the central aims of the study. I suggest removing them for clarity/brevity.

We greatly appreciate the reviewer's suggestion. Our study primarily focused on characterizing the main GWAS candidate, SR3G. Since SR3G is located within a cluster of other DUF247 genes on chromosome 3, we believe that screening the neighboring DUF247 genes could provide further insights into SR3G’s role in root development. Additionally, we believe that the generated data and lines will serve as a valuable resource for other researchers interested in studying these genes. For these reasons, we have decided to retain these datasets in the manuscript.

Lines 650-652 - these sections 1-3 differences in suberization between SR3G and Col-0 under control conditions are not significant. At best, this may be described as a "trend" and not "higher levels." In section 4, it is VERY marginally significant (and probably not at all after the large number of tests performed, here.)

We appreciate the reviewer's feedback and have revised the wording accordingly.

Line 660 - this statement is only true for Section 1. I suggest adding this caveat.

We appreciate the reviewer's comments on this matter. We quantified four suberin monomers in whole root seedlings rather than in individual root sections due to the technical challenges of separating the sections without microscopy and the limited availability of samples for GS-MS analysis.

Author Response

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

We want to thank the Editor and Reviewers for their thorough assessment of the manuscript as well as their constructive critiques. We have collated below the public review and recommendations from each Reviewer as well as our responses to them.

eLife assessment

This study by Verdikt et al. provided solid evidence demonstrating the potential impacts of Δ9-tetrahydrocannabinol (Δ9-THC) on early embryonic development using mouse embryonic stem cells (mESCs) and in vitro differentiation. Their results revealed that Δ9-THC enhanced mESCs proliferation and metabolic adaptation, possibly persisting through differentiation to Primordial Germ Cell-Like Cells (PGCLCs), though the evidence supporting this persistence was incomplete. Although the study is important, it was limited by being conducted solely in vitro and lacking parallel human model experiments.

Reviewer #1 (Public Review):

The authors investigated the metabolic effects of ∆9-THC, the main psychoactive component of cannabis, on early mouse embryonic cell types. They found that ∆9-THC increases proliferation in female mouse embryonic stem cells (mESCs) and upregulates glycolysis. Additionally, primordial germ cell-like cells (PGCLCs) differentiated from ∆9-THC-exposed cells also show alterations to their metabolism. The study is valuable because it shows that physiologically relevant ∆9-THC concentrations have metabolic effects on cell types from the early embryo, which may cause developmental effects. However, the claim of "metabolic memory" is not justified by the current data, since the effects on PGCLCs could potentially be due to ∆9-THC persisting in the cultured cells over the course of the experiment, even after the growth medium without ∆9-THC was added.

The study shows that ∆9-THC increases the proliferation rate of mESCs but not mEpiLCs, without substantially affecting cell viability, except at the highest dose of 100 µM which shows toxicity (Figure 1). Treatment of mESCs with rimonabant (a CB1 receptor antagonist) blocks the effect of 100 nM ∆9-THC on cell proliferation, showing that the proliferative effect is mediated by CB1 receptor signaling. Similarly, treatment with 2-deoxyglucose, a glycolysis inhibitor, also blocks this proliferative effect (Figure 4G-H). Therefore, the effect of ∆9-THC depends on both CB1 signaling and glycolysis. This set of experiments strengthens the conclusions of the study by helping to elucidate the mechanism of the effects of ∆9-THC.

Although several experiments independently showed a metabolic effect of ∆9-THC treatment, this effect was not dose-dependent over the range of concentrations tested (10 nM and above). Given that metabolic effects were observed even at 10 nM ∆9-THC (see for example Figure 1C and 3B), the authors should test lower concentrations to determine the dose-dependence and EC50 of this effect. The authors should also compare their observed EC50 with the binding affinity of ∆9-THC to cellular receptors such as CB1, CB2, and GPR55 (reported by other studies).

The study also profiles the transcriptome and metabolome of cells exposed to 100 nM ∆9-THC. Although the transcriptomic changes are modest overall, there is upregulation of anabolic genes, consistent with the increased proliferation rate in mESCs. Metabolomic profiling revealed a broad upregulation of metabolites in mESCs treated with 100 nM ∆9-THC.

Additionally, the study shows that ∆9-THC can influence germ cell specification. mESCs were differentiated to mEpiLCs in the presence or absence of ∆9-THC, and the mEpiLCs were subsequently differentiated to mPGCLCs. mPGCLC induction efficiency was tracked using a BV:SC dual fluorescent reporter. ∆9-THC treated cells had a moderate increase in the double positive mPGCLC population and a decrease in the double negative population. A cell tracking dye showed that mPGCLCs differentiated from ∆9-THC treated cells had undergone more divisions on average. As with the mESCs, these mPGCLCs also had altered gene expression and metabolism, consistent with an increased proliferation rate.

My main criticism is that the current experimental setup does not distinguish between "metabolic memory" vs. carryover of THC (or its metabolites) causing metabolic effects. The authors assume that their PGCLC induction was performed "in the absence of continuous exposure" but this assumption may not be justified. ∆9-THC might persist in the cells since it is highly hydrophobic. In order to rule out the persistence of ∆9-THC as an explanation of the effects seen in PGCLCs, the authors should measure concentrations of ∆9-THC and THC metabolites over time during the course of their PGCLC induction experiment. This could be done by mass spectrometry. This is particularly important because 10 nM of ∆9-THC was shown to have metabolic effects (Figure 1C, 3B, etc.). Since the EpiLCs were treated with 100 nM, if even 10% of the ∆9-THC remained, this could account for the metabolic effects. If the authors want to prove "metabolic memory", they need to show that the concentration of ∆9-THC is below the minimum dose required for metabolic effects.

Overall, this study is promising but needs some additional work in order to justify its conclusions. The developmental effects of ∆9-THC exposure are important for society to understand, and the results of this study are significant for public health.

*Reviewer #1 (Recommendations For The Authors):

This has the potential to be a good study, but it's currently missing two key experiments:

What is the minimum dose of ∆9-THC required to see metabolic effects?

We would like to thank Reviewer 1 for their insightful comments. We have included exposures to lower doses of ∆9-THC in Supplementary Figure 1. Our data shows that ∆9-THC induces mESCs proliferation from 1nM onwards. However, when ESCs and EpiLCs were exposed to 1nM of ∆9-THC, no significant change in mPGCLCs induction was observed (updated Figure 6B). Of note, in their public review, Reviewer 1 mentioned that “The authors should also compare their observed EC50 with the binding affinity of ∆9-THC to cellular receptors such as CB1, CB2, and GPR55 (reported by other studies).” According to the literature, stimulation of non-cannabinoid receptors and ion channels (including GPR18, GPR55, TRPVs, etc.) occurs at 40nM-10µM of ∆9-THC (Banister et al., 2019). We therefore expect that at the lower nanomolar range tested, CB1 is the main receptor stimulated by ∆9-THC, as we showed for the 100nM dose in our rimonabant experiments (Fig. 2).

Is the residual THC concentration during the PGCLC induction below this minimum dose? Even if the effects are due to residual ∆9-THC, this would not undermine the overall study. There would simply be a different interpretation of the results.

This experiment was particularly important to distinguish between a “true” ∆9-THC metabolic memory or residual ∆9-THC leftover during PGCLCs differentiation. Our mass spectrometry quantification revealed that no significant ∆9-THC could be detected in day 5 embryoid bodies compared to treated EpiLCs prior to differentiation (Supplementary Figure 13). These results support the existence of ∆9-THC metabolic memory across differentiation.

You also do not mention whether you tested your cells for mycoplasma. This is important since mycoplasma contamination is a common problem that can cause artifactual results. Please test your cells and report the results.

All cells were tested negative for mycoplasma by a PCR test (ATCC® ISO 9001:2008 and ISO/IEC 17025:2005 quality standards). This information has been added in the Material and Methods section.

Minor points:

1. I don't think it's correct to say that cannabis is the most commonly used psychoactive drug. Alcohol and nicotine are more commonly used. See: https://nida.nih.gov/research-topics/alcohol and https://www.cancer.gov/publications/dictionaries/cancer-terms/def/psychoactive-substance I looked at the UN drugs report [ref 1] and alcohol or nicotine were not included on that list of drugs, so the UN may use a different definition. This doesn't affect the importance or conclusions of this study, but the wording should be changed.

We agree and are now following the WHO description of cannabis (https://www.who.int/teams/mental-health-and-substance-use/alcohol-drugs-and-addictive-behaviours/drugs-psychoactive/cannabis) by referring to it as the “most widely used illicit drug in the world”. (Line 44).

1. It would be informative to use your RNA-seq data to examine the expression of receptors for ∆9-THC such as CB1, CB2, and GPR55. CB1 might be the main one, but I am curious to see if others are present.

We have explored the protein expression of several cannabinoid receptors, including CB2, GPR18, GPR55 and TRPV1 (Bannister et al., 2019). These proteins, except TRPV1, were lowly expressed in mouse embryonic stem cells compared to the positive control (mouse brain extract, see Author response image 1). Furthermore, our experiment with Rimonabant showed that the proliferative effects of ∆9-THC are mediated through CB1.

Author response image 1.

Cannabinoid receptors and non-cannabinoid receptors protein expression in mouse embryonic stem cells.

1. Make sure to report exact p-values. You usually do this, but there are a few places where it says p<0.0001. Also, report whether T-tests assumed equal variance (Student's) or unequal variance (Welch's). [In general, it's better to use unequal variance, unless there is good reason to assume equal variance.]

Prism, which was used for statistical analyses, only reports p-values to four decimal places. For all p-values that were p<0.0001, the exact decimals were calculated in Excel using the “=T.DIST.2T(t, df)” function, where the Student’s distribution and the number of degrees of freedom computed by Prism were inputted. Homoscedasticity was confirmed for all statistical analyses in Prism.

1. Figure 2A: An uncropped gel image should be provided as supplementary data. Additionally, show positive and negative controls (from cells known to either express CB1 or not express CB1)

The uncropped gel image is presented in Author response image 2. The antibody was validated on mouse brain extracts as a positive control as shown in Figure 1.

Author response image 2.

Uncropped gel corresponding to Fig. 2A where an anti-CB1 antibody was used.

1. Figure 6B: Please show a representative gating scheme for flow cytometry (including controls) as supplementary data. Also, was a live/dead stain used? What controls were used for compensation? These details should be reported.

The gating strategy is presented in Supplementary Figure 11. The Material and Methods section has also been expanded.

1. As far as I can tell, you only used female mESCs. It would be good to test the effects on male mESCs as well since these have some differences due to differences in X-linked gene expression (female mESCs have two active X chromosomes). I understand that you might not have a male BV:SC reporter line, so it would be acceptable to omit the mPGCLC experiments on male cells.

We have tested the 10nM-100µM dose range in the male R8 mESCs (Supplementary Figure 3). Similar results as with the female H18 cells were observed. Accordingly, PGCLCs induction was increased when R8 ESCs + EpiLCs were exposed to 100nM of ∆9-THC (Supplementary Figure 12). This is in line with ∆9-THC impact on fundamentally conserved metabolic pathways across species and sex, although it should be noted that one representative model of each sex is not sufficient to exclude sex-specific effects.

Reviewer #2 (Public Review):

In the study conducted by Verdikt et al, the authors employed mouse Embryonic Stem Cells (ESCs) and in vitro differentiation techniques to demonstrate that exposure to cannabis, specifically Δ9-tetrahydrocannabinol (Δ9-THC), could potentially influence early embryonic development. Δ9-THC was found to augment the proliferation of naïve mouse ESCs, but not formative Epiblast-like Cells (EpiLCs). This enhanced proliferation relies on binding to the CB1 receptor. Moreover, Δ9-THC exposure was noted to boost glycolytic rates and anabolic capabilities in mESCs. The metabolic adaptations brought on by Δ9-THC exposure persisted during differentiation into Primordial Germ Cell-Like Cells (PGCLCs), even when direct exposure ceased, and correlated with a shift in their transcriptional profile. This study provides the first comprehensive molecular assessment of the effects of Δ9-THC exposure on mouse ESCs and their early derivatives. The manuscript underscores the potential ramifications of cannabis exposure on early embryonic development and pluripotent stem cells. However, it is important to note the limitations of this study: firstly, all experiments were conducted in vitro, and secondly, the study lacks analogous experiments in human models.

Reviewer #2 (Recommendations For The Authors):

1. EpiLCs, characterized as formative pluripotent stem cells rather than primed ones, are a transient population during ESC differentiation. The authors should consider using EpiSCs and/or formative-like PSCs (Yu et al., Cell Stem Cell, 2021; Kinoshita et al., Cell Stem Cell, 2021), and amend their references to EpiLCs as "formative".

Indeed, EpiLCs are a transient pluripotent stem cell population that is “functionally distinct from both naïve ESCs and EpiSCs” and “enriched in formative phase cells related to pre-streak epiblast” (Kinoshita et al., Cell Stem Cell, 2021). Here, we used the differentiation system developed by M. Saitou and colleagues to derive PGCLCs (Hayashi et al, 2011). Since EpiSCs are refractory to PGCLCs induction (Hayashi et al, 2011), we used the germline-competent EpiLCs and took advantage of a well-established differentiation system to derive mouse PGCLCs. Most authors, however, agree that in terms of epigenetic and metabolic profiles, mouse EpiLCs represent a primed pluripotent state. We have added that PGCs arise in vivo “from formative pluripotent cells in the epiblast” on lines 85-86.

1. Does the administration of Δ9-THC, at concentrations from 10nM to 1uM, alter the cell cycle profiles of ESCs?

The proliferation of ESCs was associated with changes in the cell cycle, as presented in the new Supplementary Figure 2, which we discuss in lines 118-123.

1. Could Δ9-THC treatment influence the differentiation dynamics from ESCs to EpiLCs?

No significant changes were observed in the pluripotency markers associated with ESCs and EpiLCs (Supplementary Figure 9). We have added this information in lines 277-279.

1. The authors should consider developing knockout models of cannabinoid receptors in ESCs and EpiLCs (or EpiSCs and formative-like PSCs) for control purposes.

This is an excellent suggestion. Due to time and resource constraints, however, we focused our mechanistic investigation of the role of CB1 on the use of rimonabant which revealed a reversal of Δ9-THC-induced proliferation at 100nM.

1. Lines 134-136: "Importantly, SR141716 pre-treatment, while not affecting cell viability, led to a reduced cell count compared to the control, indicating a fundamental role for CB1 in promoting proliferation." Regarding Figure 2D, does the Rimonabant "+" in the "mock" group represent treatment with Rimonabant only? If that's the case, there appears to be no difference from the Rimonabant "-" mock. The authors should present results for Rimonabant-only treatment.

To be able to compare the effects +/- Rimonabant and as stated in the figure legend, each condition was normalized to its own control (mock with, or without Rimonabant). Author response image 3 is the unnormalized data showing the same effects of Δ9-THC and Rimonabant on cell number.

Author response image 3.

Unnormalized data corresponding to the Figure 2D.

1. In Figure 3, both ESCs and EpiLCs show a significant decrease in oxygen consumption and glycolysis at a 10uM concentration. Do these conditions slow cell growth? BrdU incorporation experiments (Figure 1) seem to contradict this. With compromised bioenergetics at this concentration, the authors should discuss why cell growth appears unaffected.

Indeed, we believe that cell growth is progressively restricted upon increasing doses of ∆9-THC (consider Supplementary Figure 2). In addition, oxygen consumption and glycolysis can be decoupled from cellular proliferation, especially considering the lower time ranges we are working with (44-48h).

1. Beyond Δ9-THC exposure prior to PGCLCs induction, it would be also interesting to explore the effects of Δ9-THC on PGCLCs during their differentiation.

We agree with the Reviewer. Our aim was to study whether exposure prior to differentiation could have an impact, and if so, what are the mediators of this impact. Full exposure during differentiation is another exposure paradigm that is relevant but would not have allowed us to show the metabolic memory of ∆9-THC exposure. Future work, however, will be dedicated to analyzing the effect of continuous exposure through differentiation.

1. As PGC differentiation involves global epigenetic changes, it would be interesting to investigate how Δ9-THC treatment at the ESCs/EpiLCs stage may influence PGCLCs' transcriptomes.

We also agree with the Reviewer. While this paper was not primarily focused on Δ9-THC’s epigenetic effects, we have explored the impact of Δ9-THC on more than 100 epigenetic modifiers in our RNA-seq datasets. These results are shown in Supplementary Table 1 and Supplementary Figure 10 and discussed in lines 301-316.

1. Lines 407-408: The authors should exercise caution when suggesting "potentially adverse consequences" based solely on moderate changes in PGCLCs transcriptomes.

We agree and have modified the sentence as follows: “Our results thus show that exposure to Δ9-THC prior to specification affects embryonic germ cells’ transcriptome and metabolome. This in turn could have adverse consequences on cell-cell adhesion with an impact on PGC normal development in vivo.“

1. Investigating the possible impacts of Δ9-THC exposure on cultured mouse blastocysts, implantation, post-implantation development, and fertility could yield intriguing findings.

We thank the Reviewer for this comment. We have amended our discussion to include these points in the last paragraph.

1. Given that naïve human PSCs and human PGCLCs differentiation protocols have been established, the authors should consider carrying out parallel experiments in human models.

We have performed Δ9-THC exposures in hESCs (Supplementary Figure 4 and Supplementary Figure 5), showing that Δ9-THC alters the cell number and general metabolism of these cells. We present these results in light of the differences in metabolism between mouse and human embryonic stem cells on lines 135-141 and 185-188. Implications of these results are discussed in lines 474-486.

Reviewer #3 (Public Review):

Verdikt et al. focused on the influence of Δ9-THC, the most abundant phytocannabinoid, on early embryonic processes. The authors chose an in vitro differentiation system as a model and compared the proliferation rate, metabolic status, and transcriptional level in ESCs, exposure to Δ9-THC. They also evaluated the change of metabolism and transcriptome in PGCLCs derived from Δ9-THC-exposed cells. All the methods in this paper do not involve the differentiation of ESCs to lineage-specific cells. So the results cannot demonstrate the impact of Δ9-THC on preimplantation developmental stages. In brief, the authors want to explore the impact of Δ9-THC on preimplantation developmental stages, but they only detected the change in ESCs and PGCLCs derived from ESCs, exposure to Δ9-THC, which showed the molecular characterization of the impact of Δ9-THC exposure on ESCs and PGCLCs.

Reviewer #3 (Recommendations For The Authors):

1. To demonstrate the impact of Δ9-THC on preimplantation developmental stages, ESCs are an appropriate system. They have the ability to differentiate three lineage-specific cells. The authors should perform differentiation experiments under Δ9-THC-exposure, and detect the influence of Δ9-THC on the differentiation capacity of ESCs, more than just differentiate to PGCLCs.

We apologize for the lack of clarity in our introduction. We specifically looked at the developmental trajectory of PGCs because of the sensitivity of these cells to environmental insults and their potential contribution to transgenerational inheritance. We have expanded on these points in our introduction and discussion sections (lines 89-91 and 474-486). Because our data shows the relevance of Δ9-THC-mediated metabolic rewiring in ESCs subsisting across differentiation, we agree that differentiation towards other systems (neuroprogenitors, for instance) would yield interesting data, albeit beyond the scope of the present study.

1. Epigenetics are important to mammalian development. The authors only detect the change after Δ9-THC-exposure on the transcriptome level. How about methylation landscape changes in the Δ9-THC-exposure ESCs?

We have explored the impact of Δ9-THC on more than 100 epigenetic modifiers in our RNA-seq datasets. These results are shown in Supplementary Table 1 and Supplementary Figure 10, discussed in lines 301-316. While indeed the changes in DNA methylation profiles appear relevant in the context of Δ9-THC exposure (because of Tet2 increased expression in EpiLCs), we highlight that other epigenetic marks (histone acetylation, methylation or ubiquitination) might be relevant for future studies.

1. In the abstract, the authors claimed that "the results represent the first in-depth molecular characterization of the impact of Δ9-THC exposure on preimplantation developmental stages." But they do not show whether the Δ9-THC affects the fetus through the maternal-fetal interface.

We have addressed the need for increased clarity and have modified the sentence as follows: “These results represent the first in-depth molecular characterization of the impact of Δ9-THC exposure on early stages of the germline development.”

1. To explore the impact of cannabis on pregnant women, the human ESCs may be a more proper system, due to the different pluripotency between human ESCs and mouse ESCs.

We have performed Δ9-THC exposures in hESCs (Supplementary Figure 4 and Supplementary Figure 5). These preliminary results show that Δ9-THC exposure negatively impacts the cell number and general metabolism of hESCs. With the existence of differentiation systems for hPGCLCs, future studies will need to assess whether Δ9-THC-mediated metabolic remodelling is also carried through differentiation in human systems. We discuss these points in the last paragraph of our discussion section.

1. All the experiments are performed in vitro, and the authors should validate their results in vivo, at least a Δ9-THC-exposure pregnant mouse model.

Our work is the first of its kind to show that exposure to a drug of abuse can alter the normal development of the embryonic germline. We agree with the Reviewer that to demonstrate transgenerational inheritance of the effects reported here, future experiments in an in vivo mouse model should be conducted. The metabolic remodeling observed upon cannabis exposure could also be directly studied in a human context, although these experiments would be beyond the scope of the present study. For instance, changes in glycolysis may be detected in pregnant women using cannabis, or directly measured in follicular fluid in a similar manner as done by Fuchs-Weizman and colleagues (Fuchs-Weizman et al., 2021). We hope that our work can provide the foundation to inform such in vivo studies.

Author Response

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

eLife assessment

The study is an important advancement to the consideration of antimalarial drug resistance: the authors make use of both modelling results and supporting empirical evidence to demonstrate the role of malaria strain diversity in explaining biogeographic patterns of drug resistance. The theoretical methods and the corresponding results are convincing, with the novel model presented moving beyond existing models to incorporate malaria strain diversity and antigen-specific immunity. This work is likely to be interesting to malaria researchers and others working with antigenically diverse infectious diseases.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The paper is an attempt to explain a geographic paradox between infection prevalence and antimalarial resistance emergence. The authors developed a compartmental model that importantly contains antigenic strain diversity and in turn antigen-specific immunity. They find a negative correlation between parasite prevalence and the frequency of resistance emergence and validate this result using empirical data on chloroquine-resistance. Overall, the authors conclude that strain diversity is a key player in explaining observed patterns of resistance evolution across different geographic regions.

The authors pose and address the following specific questions:

1. Does strain diversity modulate the equilibrium resistance frequency given different transmission intensities?

2. Does strain diversity modulate the equilibrium resistance frequency and its changes following drug withdrawal?

3. Does the model explain biogeographic patterns of drug resistance evolution?

Strengths:

The model built by the authors is novel. As emphasized in the manuscript, many factors (e.g., drug usage, vectorial capacity, population immunity) have been explored in models attempting to explain resistance emergence, but strain diversity (and strain-specific immunity) has not been explicitly included and thus explored. This is an interesting oversight in previous models, given the vast antigenic diversity of Plasmodium falciparum (the most common human malaria parasite) and its potential to "drive key differences in epidemiological features".

The model also accounts for multiple infections, which is a key feature of malarial infections, with individuals often infected with either multiple Plasmodium species or multiple strains of the same species. Accounting for multiple infections is critical when considering resistance emergence, as with multiple infections there is within-host competition which will mediate the fitness of resistant genotypes. Overall, the model is an interesting combination of a classic epidemiological model (e.g., SIR) and a population genetics model.

In terms of major model innovations, the model also directly links selection pressure via drug administration with local transmission dynamics. This is accomplished by the interaction between strain-specific immunity, generalized immunity, and host immune response.

R: We thank the reviewer for his/her appreciation of the work.

Weaknesses:

In several places, the explanation of the results (i.e., why are we seeing this result?) is underdeveloped. For example, under the section "Response to drug policy change", it is stated that (according to the model) low diversity scenarios show the least decline in resistant genotype frequency after drug withdrawal; however, this result emerges mechanistically. Without an explicit connection to the workings of the model, it can be difficult to gauge whether the result(s) seen are specific to the model itself or likely to be more generalizable.

R: We acknowledge that the explanation of certain results needs to be improved. We have now added the explanation of why low diversity scenarios show the least decline in resistance frequency after drug withdrawal: “Two processes are responsible for the observed trend: first, resistant genotypes have a much higher fitness advantage in low diversity regions even with reduced drug usage because infected hosts are still highly symptomatic; second, due to low transmission potential in low diversity scenarios (i.e., longer generation intervals between transmissions), the rate of change in parasite populations is slower.” (L243-247). We also compared the drug withdrawal response to that of the generalized-immunity-only model (L268-271). The medium transmission region has the fastest reduction in resistance frequency, followed by the high and low transmission regions, which differs from the full model that incorporates strain-specific diversity.

In addition, to provide the context of different biogeographic transmission zones, we now include a new figure (now Fig. 3) that presents the parameter space of transmission potential and strain diversity of different continents, which demonstrates that PNG and South America have less strain diversity than expected by transmission potential (L179-184 and L198-202). Therefore, these two regions have low disease prevalence and high resistance frequency.

The authors emphasize several model limitations, including the specification of resistance by a single locus (thus not addressing the importance of recombination should resistance be specified by more than one locus); the assumption that parasites are independently and randomly distributed among hosts (contrary to empirical evidence); and the assumption of a random association between the resistant genotype and antigenic diversity. However, each of these limitations is addressed in the discussion.

R: As pointed out by the referee, our model presents several limitations that have all been addressed in the discussion and considered for future extensions.

Did the authors achieve their goals? Did the results support their conclusion?

Returning to the questions posed by the authors:

1. Does strain diversity modulate the equilibrium resistance frequency given different transmission intensities? Yes. The authors demonstrate a negative relationship between prevalence/strain diversity and resistance frequency (Figure 2).

2. Does strain diversity modulate the equilibrium resistance frequency and its changes following drug withdrawal? Yes. The authors find that, under resistance invasion and some level of drug treatment, resistance frequency decreased with the number of strains (Figure 4). The authors also find that lower strain diversity results in a slower decline in resistant genotypes after drug withdrawal and higher equilibrium resistance frequency (Figure 6).

3. Does the model explain biogeographic patterns of drug resistance evolution? Yes. The authors find that their full model (which includes strain-specific immunity) produces the empirically observed negative relationship between resistance and prevalence/strain diversity, while a model only incorporating generalised immunity does not (Figure 8).

Utility of work to others and relevance within and beyond the field?

This work is important because antimalarial drug resistance has been an ongoing issue of concern for much of the 20th century and now 21st century. Further, this resistance emergence is not equitably distributed across biogeographic regions, with South America and Southeast Asia experiencing much of the burden of this resistance emergence. Not only can widespread resistant strains be traced back to these two relatively low-transmission regions, but these strains remain at high frequency even after drug treatment ceases.

Reviewer #2 (Public Review):

Summary:

The evolution of resistance to antimalarial drugs follows a seemingly counterintuitive pattern, in which resistant strains typically originate in regions where malaria prevalence is relatively low. Previous investigations have suggested that frequent exposures in high-prevalence regions produce high levels of partial immunity in the host population, leading to subclinical infections that go untreated. These subclinical infections serve as refuges for sensitive strains, maintaining them in the population. Prior investigations have supported this hypothesis; however, many of them excluded important dynamics, and the results cannot be generalized. The authors have taken a novel approach using a deterministic model that includes both general and adaptive immunity. They find that high levels of population immunity produce refuges, maintaining the sensitive strains and allowing them to outcompete resistant strains. While general population immunity contributed, adaptive immunity is key to reproducing empirical patterns. These results are robust across a range of fitness costs, treatment rates, and resistance efficacies. They demonstrate that future investigations cannot overlook adaptive immunity and antigenic diversity.

R: We thank the reviewer for his/her appreciation of the work.

Strengths:

Overall, this is a very nice paper that makes a significant contribution to the field. It is well-framed within the body of literature and achieves its goal of providing a generalizable, unifying explanation for otherwise disparate investigations. As such, this work will likely serve as a foundation for future investigations. The approach is elegant and rigorous, with results that are supported across a broad range of parameters.

Weaknesses:

Although the title states that the authors describe resistance invasion, they do not support or even explore this claim. As they state in the discussion (line 351), this work predicts the equilibrium state and doesn't address temporal patterns. While refuges in partially immune hosts may maintain resistance in a population, they do not account for the patterns of resistance spread, such as the rapid spread of chloroquine resistance in Africa once it was introduced from Asia.

R: We do agree that resistance invasion is not the focus of our manuscript. Rather we mainly investigate the maintenance and decline after drug withdrawal. Therefore, we changed the title to “Antigenic strain diversity predicts different biogeographic patterns of maintenance and decline of anti-malarial drug resistance” (L1-4).

We did, however, present a fast initial invasion phase for the introduction of resistant genotypes regardless of transmission scenarios in Fig. 5 (now Fig. 6). Even though the focus of the manuscript is to investigate long term persistence of resistant genotypes, we did emphasize that the initial invasion phase and how that changes the host immunity profile are key to the coexistence of resistant and wild-type genotypes (L228-239).

As the authors state in the discussion, the evolution of compensatory mutations that negate the cost of resistance is possible, and in vitro experiments have found evidence of such. It appears that their results are dependent on there being a cost, but the lower range of the cost parameter space was not explored.

R: It is true that compensatory mutations might mitigate the negative fitness consequences. We didn’t add a no-cost scenario because in general if there is no cost but only benefit (survival through drug usage), then resistant haplotypes will likely be fixed in the population. This is contingent on the assumption that these compensatory mutations are in perfect linkage with resistant alleles, which is unlikely in high-transmission scenarios. Our model does not incorporate recombination, but earlier models (Dye & Williams 1997, Hastings & D’Alessandro 2000) have demonstrated that recombination will delay the fixation of resistant alleles in high-transmission.

As suggested, we ran our model with costs equal 0 and 0.01 (Fig. 2C and L189-191). We found that resistant alleles almost always fix except for when diversity is extremely high, treatment/resistance efficacy is low. In these cases, additional benefits brought by more transmission from resistant alleles do not bring many benefits (as lower GI classes have a very small number of hosts). This finding does not contradict a wider range of coexistence between wild-type and resistant alleles when the cost is higher. We therefore added these scenarios to our updated results.

Author response image 1.

The use of a deterministic, compartmental model may be a structural weakness. This means that selection alone guides the fixation of new mutations on a semi-homogenous adaptive landscape. In reality, there are two severe bottlenecks in the transmission cycle of Plasmodium spp., introducing a substantial force of stochasticity via genetic drift. The well-mixed nature of this type of model is also likely to have affected the results. In reality, within-host selection is highly heterogeneous, strains are not found with equal frequency either in the population or within hosts, and there will be some linkage between the strain and a resistance mutation, at least at first. Of course, there is no recourse for that at this stage, but it is something that should be considered in future investigations.

R: We thank the reviewer for their insightful comments on the constraints of the deterministic modeling approach. We’ve added these points to discussion in the paragraph discussing the second limitation of the model (L359-364).

The authors mention the observation that patterns of resistance in high-prevalence Papua New Guinea seem to be more similar to Southeast Asia, perhaps because of the low strain diversity in Papua New Guinea. However, they do not investigate that parameter space here. If they did and were able to replicate that observation, not only would that strengthen this work, it could profoundly shape research to come.

R: We appreciate the suggestion to investigate the parameter space of Papua New Guinea. We now include a new figure (now Fig. 3) that presents the parameter space of transmission potential and strain diversity of different continents, which demonstrates that PNG and South America have less strain diversity than expected by transmission potential (L179-184 and L198-202). This translates to low infectivity for most mosquito bites, and most infections only occur in hosts with lower generalized immunity. Therefore resistant genotypes will help ensure disease transmission in these symptomatic hosts and be strongly selected to be maintained.

Reviewer #1 (Recommendations For The Authors):

1. I found lines 41-49 difficult to follow. Please rephrase (particularly punctuation) for clarity.

R: We have edited the lines to improve the writing (L41-50)):

“Various relationships between transmission intensity and stable frequencies of resistance were discovered, each of which has some empirical support: 1) transmission intensity does not influence the fate of resistant genotypes [Models: Koella and Antia (2003); Masserey et al. (2022); Empirical: Diallo et al. (2007); Shah et al. (2011, 2015)]; 2) resistance first increases in frequency and slowly decreases with increasing transmission rates [Models: Klein et al. (2008, 2012)]; and 3) Valley phenomenon: resistance can be fixed at both high and low end of transmission intensity [Model: Artzy-Randrup et al. (2010); Empirical: Talisuna et al. (2002)]. Other stochastic models predict that it is harder for resistance to spread in high transmission regions, but patterns are not systematically inspected across the parameter ranges [Model: Whitlock et al. (2021); Model and examples in Ariey and Robert (2003)].”

1. Line 65: There should be a space after "recombination" and before the citation.

R: Thank you for catching the error. We’ve added the space (L64).

1. I'm interested in the dependency of the results on the assumption that there is a cost to resistance via lowered transmissibility (lines 142-145). I appreciate that variation in the cost(s) of resistance in single and mixed infections is explored; however, from what I can tell the case of zero cost is not explored.

R: As suggested, we have now added the no-cost scenario. Please see the response to the Reviewer2 weaknesses paragraph 2.

1. I felt the commentary/explanation of the response to drug policy change was a bit underdeveloped. I would have liked a walk-through of why in your model low diversity scenarios show the slowest decline in resistant genotypes after switching to different drugs.

R: We acknowledge that the explanation of the response to drug policy change needs to be improved. We have now added the explanation of why we observe low diversity scenarios show the least decline in resistance frequency after drug withdrawal: “Two processes are responsible for the seen trend: first, resistant genotypes have a much higher fitness advantage in low diversity regions even with reduced drug usage because infected hosts are still highly symptomatic; second, due to low transmission potential in low diversity scenarios (i.e., longer generation intervals between transmissions), the rate of change in parasite populations is slower.” (L243-247). We also compared the drug withdrawal response to that of the generalized-immunity-only model. The medium transmission region has the fastest reduction in resistance frequency, followed by the high and low transmission regions, which differs from the full model that incorporates strain-specific diversity.

1. Line 352: persistent drug usage?

R: Yes, we meant persistent drug usage. We’ve clarified the writing (L389-391).

1. The organisation of the manuscript would benefit from structuring around the focal questions so that the reader can easily find the answers to the focal questions within the results and discussion sections.

R: This is a great suggestion. We modified the subheadings of results to provide answers to focal questions (L151, L179, L203-204, and L240).

1. Line 353: Please remove either "shown" or "demonstrated".

R: Thank you for catching the grammatical error, we’ve retained “shown” only for the sentence (L391-392).

Reviewer #2 (Recommendations For The Authors):

Overall, this was very nice work and a pleasure to read.

Major:

1. Please provide a much more thorough explanation of how resistance invasions are modeled. It is not clear from the text and could not be replicated.

R: We have now added a section “drug treatment and resistance invasion” in Methods and Materials to explain how resistance invasions are modeled (L488-496):

“Given each parameter set, we ran the ODE model six times until equilibrium with the following genotypic compositions: 1) wild-type only scenario with no drug treatment; 2) wild-type only scenario with 63.2% drug treatment (0.05 daily treatment rate); 3) wild-type only scenario with 98.2% drug treatment (0.2 daily treatment rate); 4) resistant-only scenario with no drug treatment; 5) resistance invasion with 63.2% drug treatment; 6) resistance invasion with 98.2% drug treatment. Runs 1-4 start with all hosts in G0,U compartment and ten parasites. Runs 5 and 6 (resistance invasion) start from the equilibrium state of 2 and 3, with ten resistant parasites introduced. We then followed the ODE dynamics till the next equilibrium.”

1. Please make your raw data, code, and replicable examples that produce the figures in the manuscript available.

R: We have added the data availability session, which provides the GitHub site with all the code for the model, data processing, and figures: All the ODE codes, numerically-simulated data, empirical data, and analyzing scripts are publicly available at https://github.itap.purdue.edu/HeLab/MalariaResistance.

1. Regarding the limitations described in the paragraph about the model in the public response, these results would be strengthened if there were separate compartments for strains which could be further divided into sensitive and resistant. Could you explore this for at least a subset of the parameter space?

R: In our model, sensitive and resistant pathogens are always modeled as separate compartments (Fig. S1B and Appendix 1). In Results/Model structure, L135-136, we stated the setup:

“The population sizes of resistant (PR) or sensitive (wild-type; PW) parasites are tracked separately in host compartments of different G and drug status.”

1. To what extent do these results rely on a cost to resistance? Were lower costs explored? This would be worth demonstrating. If this cannot be maintained without cost, do you think this is because there is no linkage between strain and resistance?

R: As suggested, we have now added the no-cost scenario (Fig. 2C and L189-191). Please see the response to the Reviewer1 weaknesses paragraph 2. In sum, under a no-cost scenario, if treatment rate is low, then wild-type alleles will still be maintained in high transmission scenarios; when treatment rate is high, resistant alleles will always be fixed.

Minor:

1. "Plasmodium" should be italicized throughout. Ironically, italics aren't permitted in this form.

R: We did italicize “Plasmodium” or “P. falciparum” throughout the text. If the reviewer is referring to “falciparum malaria”, the convention is not to italicize falciparum in this case.

1. Fig 1A: the image is reversed for the non-infected host with prior exposure to strain A. Additionally, the difference between colors for WT and resistant is not visible in monochrome.

R: Thank you for pointing out the problem of color choice in monochrome. We have modified the figure. The image in Fig 1A is not reversed for non-infected hosts with prior exposure to strain A. We now spell out “S” to be “specific immunity”, and explain it better in the figure legend.

1. Fig 2B: add "compare to the pattern of prevalence shown in Fig 2A" or something similar to make the comparison immediately clear.

R: We thank the reviewer’s suggestion. We’ve added a sentence to contrast Fig 2A and B in the Figure legend: “A comparison between the prevalence pattern in (A) and resistance frequency in (B) reveals that high prevalence regions usually correspond to low resistance frequency at the end of resistance invasion dynamics.”

1. Figs 2B & C: Please thoroughly explain how you produced this data in the methods section and briefly describe it in the results sections.

R: We agree that the modeling strategies need to be explained better. Since we explained the rationale for the parameter ranges and the prevalence patterns we observe in the results section “Appropriate pairing of strain diversity and vectorial capacity” (now “Impact of strain diversity and transmission potential on disease prevalence”), we added sentences in this section to explain how we run models until equilibrium for wild-only infections with or without drug treatment (L152-178). Then in the following section “Drug-resistance and disease prevalence” section, we explain how we obtained the resistance invasion data:

“To investigate resistance invasion, we introduce ten resistant infections to the equilibrium states of drug treatment with wild-type only infections, and follow the ODE dynamics till the next equilibrium” (L180-181).

1. Fig 3: The axis labels are not particularly clear. For the Y axis, please state in the label what it is the frequency of (either the mutation or the phenotype). In the X axis, it is better to spell that out in words, like "P. falciparum prevalence in children".

R: Thank you for pointing this out. We’ve modified the axes labels of Fig. 3 (now Fig. 4): X-axis: “P. falciparum prevalence in children aged 2-10”; Y-axis: “Frequency of resistant genotypes (pfcrt 76T)”.

1. Fig 4 and the rest of the figures of this nature: Showing an equilibrium-state timestep before treatment was introduced would improve the readers' understanding of the dynamics.

R: We agree that the equilibrium state before treatment is important. In fact, we have those states in our figure 4 (now figure 5): the left panel- “Daily treatment rate 0” indicates the equilibrium-state timestep before treatment. We clarified this point in the caption.

1. Fig 5 is very compelling, but the relationships in Fig 5 would be clearer if the Y axes were not all different. Consider using the same scale for the hosts, and the same scale for resistant parasites (both conditions) and WT parasites, 113 strains. It may be clearer to reference them if they are given as A-F instead of three figures each for A and B.

R: We agree with the suggested changes and have modified figure 5 (now Fig. 6): we used one Y-axis scale for the hosts, and one Y-axis scale for the parasites. The wild-type one is very low for the low diversity scenario, thus we included one inset plot for that case.

1. Fig 5 caption: High immune protection doesn't select against resistance. The higher relative fitness of the sensitive strain selects against resistance in a high-immunity environment.

R: Thank you for pointing this out. Here we meant that a reduction in resistant population after the initial overshoot occurs in both diversity levels. We are not comparing resistant strains to sensitive ones. We’ve modified the sentence to: “The higher specific immunity reduces the infectivity of new strains, leading to a reduction of the resistant parasite population regardless of the diversity level”.

1. Line 242: "keep" should be plural.

R: We’ve corrected “keep” to “keeps” (L267).

1. Line 360 and elsewhere: The strength of the results is somewhat overstated at times. This absolutely supports the importance of strain-specific immunity, but these results do not explain patterns of the origin of resistance and there are a number of factors that are not incorporated (a necessary evil of modeling to be sure).

R: Thank you for pointing this out. We’ve modified discussion to remove the overstated strength of results:

1) Original: “The inclusion of strain diversity in the model provides a new mechanistic explanation as to why Southeast Asia has been the original source of resistance to certain antimalarial drugs, including chloroquine.”

Modified: “The inclusion of strain diversity in the model provides a new mechanistic explanation as to why Southeast Asia has persisting resistance to certain antimalarial drugs, including chloroquine, despite a lower transmission intensity than Africa. “ (L328-330)

2) In sum, we show that strain diversity and associated strain-specific host immunity, dynamically tracked through the macroparasitic structure, can explainpredict the complex relationship between transmission intensity and drug-resistance frequencies.

1. The color palettes are not discernible in grayscale, especially the orange/blue/gray in Fig 2. The heatmaps appear to be in turbo, the only viridis palette that isn't grayscale-friendly. Just something to keep in mind for the accessibility of individuals with achromatopsia and most people who print out papers.

R: Thank you for the visualization suggestions. We updated all the figures with the “viridis:magma” palette. As for the orange/blue/gray scale used in Fig 2C, it is difficult to pick nine colors that are discernable in brightness in grayscale. Currently, the four colors correspond to clonal genotype cost (i.e. green, red, grey, and blue), and the three-level brightness maps to mixed genotype cost.

Author Response

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

Reviewer #1 (Public Review):

Summary:

Heitmann et al introduce a novel method for predicting the potential of drug candidates to cause Torsades de Pointes using simulations. Despite the fact that a multitude of such methods have been proposed in the past decade, this approach manages to provide novelty in a way that is potentially paradigm-shifting. The figures are beautiful and manage to convey difficult concepts intuitively.

Strengths:

(1) Novel combination of detailed mechanistic simulations with rigorous statistical modeling

(2) A method for predicting drug safety that can be used during drug development (3) A clear explication of difficult concepts.

Weaknesses:

(1) In this reviewer's opinion, the most important scientific issue that can be addressed is the fact that when a drug blocks multiple channels, it is not only the IC50 but also the Hill coefficient that can differ. By the same token, two drugs that block the same channel may have identical IC50s but different Hill coefficients. This is important to consider since concentration-dependence is an important part of the results presented here. If the Hill coefficients were to be significantly different, the concentration- dependent curves shown in Figure 6 could look very different.

See our response below.

(2) The curved lines shown in Figure 6 can initially be difficult to comprehend, especially when all the previous presentations emphasized linearity. But a further issue is obscured in these plots, which is the fact that they show a two-dimensional projection of a 4dimensional space. Some of the drugs might hit the channels that are not shown (INaL & IKs), whereas others will not. It is unclear, and unaddressed in the manuscript, how differences in the "hidden channels" will influence the shapes of these curves. An example, or at least some verbal description, could be very helpful.

See our response below.

Reviewer #1 (Recommendations For The Authors):

The manuscript is generally well-written (with one important exception, see below). The manuscript can be improved with a few suggested modifications, ordered from most important to least important.

(1) In this reviewer's opinion, the most important scientific issue that the authors need to address is the fact that when a drug blocks multiple channels, it is not only the IC50 but also the Hill coefficient that can differ. By the same token, two drugs that block the same channel may have identical IC50s but different Hill coefficients. This is important to consider since concentration-dependence is an important part of the results presented here.

In a recent study (Varshneya et al, CPT PSP 2021 (PMID: 33205613)) they originally ran simulations with Hill coefficients of 1 for all the 4 drugs and 7 channels, then re-ran the simulations with differing Hill coefficients. The results were quantitatively quite different than what was originally obtained, even though the overall trends were identical. A look at the table provided in that paper's supplement shows that the estimated Hill coefficients range from 0.5 to 1.9, which is a pretty wide range.

In this case, I don't think the authors should re-run the entire analysis. That would require entirely too much work and potentially detract from the elegant presentation of the manuscript in its current form. Although I haven't looked at the Llopis-Lorente dataset recently, I doubt that reliable Hill coefficients have been obtained for all 105 drugs. However, the Crumb et al dataset (PMID: 27060526) does provide this information for 30 drugs.

Perhaps the authors could choose an example of two drugs that affect similar channels but with differences in the estimated Hill coefficients. Or even a carefully-designed hypothetical example could be of value. At the very least, Hill coefficients need to be mentioned as a limitation, but this would be stronger if it were coupled with at least some novel analyses.

We fixed the Hill coefficients to h=1 because there is no evidence for co-operative drug binding in the literature that would require coefficients other than one. There is also the practical matter that only 17 of the 109 drugs in the dataset have a complete set of Hill coefficients. We have revised the Methods (Drug datasets) to make these justifications explicit:

Lines 560-566: “… We also fixed the Hill coefficients at h = 1 because (i) there is no evidence for co-operative drug binding in the literature, and thus no theoretical justification for using coefficients other than one; (ii) only 17 of the 109 drugs in the dataset had a complete set of Hill coefficients (hCaL, hKr, hNaL, hKs) anyway. …”

Out of interest, we re-ran our analysis using only those n=17 drugs (Amiodarone, Amitriptyline, Bepridil, Chlorpromazine, Diltiazem, Dofetilide, Flecainide, Mibefradil, Moxifloxacin, Nilotinib, Ondansetron, Quinidine, Quinine, Ranolazine, Saquinavir, Terfenadine and Verapamil). When the Hill coefficients were fixed at h=1, the prediction accuracy was 88.2% irrespective of the dosage (Author response image 1). When we used the estimated (free) Hill coefficients, the prediction accuracy remained unchanged (88.2%) for all doses except the lowest (1x to 2x) where it dropped to 82.4%. We concluded that using the Hill coefficients from the dataset made little difference to the results.

Author response image 1.

(2) I initially had a hard time understanding the curved lines shown in Figure 6 when all the previous presentations emphasized linearity. After thinking for a while, I was able to get it, but there was a further issue that I still struggle with. That is the fact that the plots all show a two-dimensional projection of a 4-dimensional space. Some of the drugs might hit the channels that are not shown (INaL & IKs), whereas others will not. How will differences in the "hidden channels" influence the shapes of these curves? An example, or at least some verbal description, could be very helpful.

We omitted GKs and GNaL from Figure 6 because they added little to the story. Those “hidden” channels operate in the same manner as GKr and GNaL. They are shown in Supplementary Dataset S1. We have included more explicit references to the Supplementary in both the main text and the caption of Figure 6. We have also rewritten the section on ‘The effect of dosage on multi-channel block’ (lines 249-268) to better convey that the drug acts in four dimensions.

(3) I also struggled a bit with Figure 3 and the section "Drug risk metric." What made this confusing was the PQR notation on the figure and the equations represented as A and B. Can these be presented in a common notation, or can the relationship be defined?

We have replaced the PQR notation in Figure 3A with vector notation A and B to be consistent with the equations.

Also in Figure 3B, I was unclear about the units on the x-axis. Is each step (e.g. from 0 to 1) the same distance as a single log unit along the abscissa or ordinate in Figure 3A?

Yes it is. We have revised the caption for Figure 3B to explain it better.

(4) The manuscript manages to explain difficult concepts clearly, and it is generally wellwritten. The important exception, however, is that the manuscript contains far too many sentence fragments. These often occur when the authors explain a difficult concept, then follow up with something that is essentially "and this in addition" or "with the exception of this."

Lines 220-223: "In comparison, Linezolid is an antibacterial agent that has no clinical evidence of Torsades (Class 4) even though it too blocks IKr. Albeit less than it blocks ICaL (Figure 5A, right)."

Lines 242-245: "Conversely, Linezolid shifts the population 1.18 units away from the ectopic regime. So only 0.0095% of those who received Linezolid would be susceptible. A substantial drop from the baseline rate of 0.93%."

There are several others that I didn't note, so the authors should perform a careful copy edit of the entire manuscript.

Thank you. We have remediated the fragmented sentences throughout.

Reviewer #2 (Public Review):

Summary:

In the paper from Hartman, Vandenberg, and Hill entitled "assessing drug safety, by identifying the access of arrhythmia and cardio, myocytes, electro physiology", the authors, define a new metric, the axis of arrhythmia" that essentially describes the parameter space of ion channel conductance combinations, where early after depolarization can be observed.

Strengths:

There is an elegance to the way the authors have communicated the scoring system. The method is potentially useful because of its simplicity, accessibility, and ease of use. I do think it adds to the field for this reason - a number of existing methods are overly complex and unwieldy and not necessarily better than the simple parameter regime scan presented here.

Weaknesses:

The method described in the manuscript suffers from a number of weaknesses that plague current screening methods. Included in these are the data quality and selection used to inform the drug-blocking profile. It's well known that drug measurements vary widely, depending on the measurement conditions.

We agree and have added a new section to describe these limitations, as follows:

Lines 467-478: Limitations. The method was evaluated using a dataset of drugs that were drawn from multiple sources and diverse experimental conditions (LlopisLorente et al., 2020). It is known that such measurements differ prominently between laboratories and recording platforms (Kramer et al., 2020). Some drugs in the dataset combined measurements from disparate experiments while others had missing values. Of all the drugs in the dataset, only 17 had a complete set of IC50 values for ICaL, IKr, INaL and IKs. The accuracy of the predictions are therefore limited by the quality of the drug potency measurements.

There doesn't seem to be any consideration of pacing frequency, which is an important consideration for arrhythmia triggers, resulting from repolarization abnormalities, but also depolarization abnormalities.

It is true that we did not consider the effect of pacing frequency. We have included this in the limitations:

Lines 479-485: The accuracy of the axis of arrhythmia is likewise limited by the quality of the biophysical model from which it is derived. The present study only investigated one particular variant of the ORd model (O’Hara et al., 2011; KroghMadsen et al., 2017) paced at 1 Hz. Other models and pacing rates are likely to produce differing estimates of the axis.

Extremely high doses of drugs are used to assess the population risk. But does the method yield important information when realistic drug concentrations are used?

Yes it does. The drugs were assessed across a range of doses from 1x to 32x therapeutic dose (Figure 8A). The prediction accuracy at low doses is 88.1%.

In the discussion, the comparison to conventional approaches suggests that the presented method isn't necessarily better than conventional methods.

The comparison is not just about accuracy. Our method achieves the same results at greatly reduced computational cost without loss of biophysical interpretation. We emphasise this in the Conclusion:

Lines 446-465: Conclusion. Our approach resolves the debate between model complexity and biophysical realism by combining both approaches into the same enterprise. Complex biophysical models were used to identify the relationship between ion channels and torsadogenic risk — as it is best understood by theory. Those findings were then reduced to a simpler linear model that can be applied to novel drugs without recapitulating the complex computer simulations. The reduced model retains a bio-physical description of multi-channel drug block, but only as far as necessary to predict the likelihood of early after-depolarizations. It does not reproduce the action potential itself. Our approach thus represents a convergence of biophysical and simple models which retains the essential biophysics while discarding the unnecessary details. We believe the benefits of this approach will accelerate the adoption of computational assays in safety pharmacology and ultimately reduce the burden of animal testing.

In conclusion, I have struggled to grasp the exceptional novelty of the new metric as presented, especially when considering that the badly needed future state must include a component of precision medicine.

Safety pharmacology has a different aim to precision medicine. The former concerns the population whereas the latter concerns the individual. The novelty of our metric lies in reducing the complexity of multi-channel drug effects to a linear model that retains a biophysical interpretation.

Reviewer #2 (Recommendations For The Authors):

A large majority of drugs have more complex effects than a simple reduction and channel conductance. Some of these are included in the 109 drugs shown in Figure 7. An example is ranolazine, which is well known to have potent late sodium channel blocking effects - how are such effects included in the model as presented? I think at least suggesting how the approach can be expanded for broader applicability would be important to discuss.

Our method does consider the simultaneous effect of the drug on multiple ion channels, specifically the L-type calcium current (ICaL), the delayed rectifier potassium currents (IKr and IKs), and the late sodium current (INaL). In the case of ranolazine (class 3 risk), the dose-responses for all four ion channels, based on IC50s published in Llopis-Lorente et al. are given in Supplementary Dataset S1.

The response curves in Author response image 2 show that in this dataset, ranolazine blocks IKr and INaL almost equally - being only slightly less potent against IKr. There are two issues to consider here that potentially contribute to ranolazine being misclassified as pro-arrhythmic. First, the cell model is more sensitive to block of IKr than INaL. As a result, in the context of an equipotent drug, the prolonging effect of IKr block outweighs the balancing effect of INaL block, resulting in a pro-arrhythmic risk score. Second, the potency of IKr block in this dataset may be overestimated which in turn exaggerates the risk score. For example, measurements of ranolazine block of IKr from our own laboratory (Windley et al J Pharmacol Toxicol 87, 99–107, 2017) suggest that the IC50 of IKr is higher (35700 nM) than that reported in the LlopisLorente dataset (12000 nM). If this were taken into account, there would be less block of IKr relative to INaL, resulting in a safer risk score.

Author response image 2.

Author Response

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

eLife assessment

This valuable paper examines the Bithorax complex in several butterfly species, in which the complex is contiguous and not split, as it is in the well-studied fruit fly Drosophila. Based on genetic screens and genetic manipulations of a boundary element involved in segment-specific regulation of Ubx, the authors provide solid evidence for their conclusions, which could be further strengthened by additional data and analyses. The data presented are relevant for those interested in the evolution and function of Hox genes and of gene regulation in general.

We are deeply grateful to the eLife editorial team and the two reviewers for their thoughtful and constructive feedback. We have used this feedback to improve our manuscript and have provided a point-by-point response below.

Public Reviews:

Reviewer #1 (Public Review):

In their article, "Cis-regulatory modes of Ultrabithorax inactivation in butterfly forewings," Tendolkar and colleagues explore Ubx regulation in butterflies. The authors investigated how Ubx expression is restricted to the hindwing in butterflies through a series of genomic analyses and genetic perturbations. The authors provide evidence that a Topologically Associated Domain (TAD) maintains a hindwing-enriched profile of chromatin around Ubx, largely through an apparent boundary element. CRISPR mutations of this boundary element led to ectopic Ubx expression in forewings, resulting in homeotic transformation in the wings. The authors also explore the results of the mutation in two non-coding RNA regions as well as a possible enhancer module. Each of these induces homeotic phenotypes. Finally, the authors describe a number of homeotic phenotypes in butterflies, which they relate to their work.

Together, this was an interesting paper with compelling initial data. That said, I have several items that I feel would warrant further discussion, presentation, or data.

First, I would not state, "Little is known about how Hox genes are regulated outside of flies." They should add "in insects" since so much in known in vertebrates

Corrected

For Figure 1, it would aid the readers if the authors could show the number of RNAseq reads across the locus. This would allow the readership to evaluate the frequency of the lncRNAs, splice variants, etc.

We have found it useful in the past to feature “Sashimi Plots”, as they provide a good overview of transcript splicing junctions and read support. Here we could not accommodate this in our Fig. 1A as this would require compiling the RNAseq reads from many tissues and stages to be meaningful, and we would lose the resolution on forewing vs hindwing tissues that is important in this article (only the Kallima inachus dataset allows this comparison, and was used in Fig 1B). More specifically, the wing transcriptomes available for J. coenia and V. cardui are not deep enough to provide a good visualization of Antp alternative promoter usage or on AS5’ transcription.

How common are boundary elements within introns? Typically, boundary elements are outside gene bodies, so this could be explored further. This seems like an interesting bit of biology which, following from the above point, it would be interesting to, at a minimum, discuss, but also relate to how transcription occurs through a possible boundary element (are there splice variants, for example?).

We do not see evidence of alternative splicing, and prefer to avoid speculating on transcriptional effects, but we agree that the intragenicity of the TAD boundary is interesting. We briefly highlighted this point in the revised Discussion:

"Lastly, it is worth noting that the Antp/Ubx TAD boundary we identified is intragenic, within the last intron of Ubx. It is unclear if this feature affects Ubx transcription, but this configuration might be analogue to the Notch locus in Drosophila, which includes a functional TAD boundary in an intronic position (Arzate-Mejía et al. 2020)."

The CRISPR experiments led to compelling phenotypes. However, as a Drosophila biologist, I found it hard to interpret the data from mosaic experiments. For example, in control experiments, how often do butterflies die? Are there offsite effects? It's striking that single-guide RNAs led to such strong effects. Is this common outside of this system? Is it possible to explore the function effects at the boundary element - are these generating large deletions (for example, like Mazo-Vargas et al., 2022)? For the mosaic experiments, how frequent are these effects in nature or captive stocks? Would it be possible to resequence these types of effects? At the moment, this data, while compelling, was hard to put into the context of the experiments above without understanding how common the effects are. Ideally, there would be resequencing of these tissues, which could be targeted, but it was not clear to me the general rates of these variants.

We agree with this assessment completely: mosaics complicate the proper interpretation of CRISPR based perturbation assays in regulatory regions. Here, unlike in Mazo-Vargas et al. (2022), we were unable to breed homeotic effects to a G1 generation, possibly because the phenotypes are dominant and lethal at the embryonic stage (see also our reply to Reviewer 2). This means that mosaic mutants are often survivors with clones of restricted size in the wing, and they are probably rare, but we are unable to meaningfully measure a mutation spectrum frequency (e.g. how often large deletions are generated). As mentioned in the first paragraph of our Discussion, we think that many of the phenotypes we observed (besides the Ubx GOF effects from the BE targeting) were confounded by alleles that could include large SVs. We aim to address these questions in an upcoming manuscript, at a locus where regulatory perturbation does not impact survival, including using germline mutants and unbiased genotyping (whole genome resequencing).

We elaborated on this issue in our Discussion:

"It is crucial here to highlight the limitations of the method, in order to derive proper insights about the functionality of the regulatory regions we tested. In essence, butterfly CRISPR experiments generate random mutations by non-homologous end joining repair, that are usually deletions (Connahs et al. 2019; Mazo-Vargas et al. 2022; Van Belleghem et al. 2023). Ideally, regulatory CRISPR-induced alleles require genotyping in a second (G1) generation to be properly matched to a phenotype (Mazo-Vargas et al. 2022). Possibly because of lethal effects, we failed to pass G0 mutations to a G1 generation for genotyping, and were thus limited here to mosaic analysis. As adult wings have lost scale building cells that may underlie a given phenotype, we circumvented this issue by genotyping a pupal forewing displaying an homeotic phenotype in the more efficient Antp-Ubx_BE perturbation experiment (Fig. S4). In this case, PCR amplification of a 600 bp fragment followed by Sanger sequencing recovered signatures of indel variants, with mixed chromatograms starting at the targeted sites. But in all other experiments (CRM11, IT1, and AS5’ targets), we did not genotype mutant tissues, as they were only detected in adult stages and generally with small clone sizes. Some of these clones may have been the results of large structural variants, as data from other organisms suggests that Cas9 nuclease targeting can generate larger than expected mutations that evade common genotyping techniques (Shin et al. 2017; Adikusuma et al. 2018; Kosicki et al. 2018; Cullot et al. 2019; Owens et al. 2019). Even under the assumption that such mutations are relatively rare in butterfly embryos, the fact we injected >100 embryos in each experiment makes their occurrence likely (Fig. 9), and we are unable to assign a specific genotype to the homeotic effects we obtained in CRM11, IT1 and AS5’ perturbation assays."

Our revision also includes a new Fig. S4 that features the mosaic genotyping of a G0 Antp-Ubx_BE mutant tissue. While this does not fully address the reviewer questions, it provides reasonable validation that the frequent GOF effects we observed upon perturbation at this target site are generated by on-target indels from DNA repair.

Author response image 1.

Validation of CRISPR-induced DNA Lesions in an Antp-Ubx_BE crispant pupat forewing. (A-A') Pupal forewing cuticle phenotype of an Antp-Ubx_BE J. coenia crispant, as in Fig. S3. (B-B") Aspect of the same forewing under trans-illumination following dissection out of the pupal case. Regions from mutant clones have a more transparent appearance. (C). Sanger sequencing of an amplicon targeting the Antp-Ubx_BE region in the mutant tissue shown in panel B", compared to a control wing tissue, showing mixed chromatogram around the expected CRISPR cutting site due to indel mutations from non-homologous end-joining.

In sum, I enjoyed the extensive mosaic perturbations. However, I feel that more molecular descriptions would elevate the work and make a larger impact on the field.

Reviewer #2 (Public Review):

Summary:

The existence of hox gene complexes conserved in animals with bilateral symmetry and in which the genes are arranged along the chromosome in the same order as the structures they specify along the anteroposterior axis of organisms is one of the most spectacular discoveries of recent developmental biology. In brief, homeotic mutations lead to the transformation of a given body segment of the fly into a copy of the next adjacent segment. For the sake of understanding the main observation of this work, it is important to know that in loss-of-function (LOF) alleles, a given segment develops like a copy of the segment immediately anterior to it, and in gain-of-function mutations (GOF), the affected segment develops like a copy of the immediately posterior segment. Over the last 30 years the molecular lesions associated with GOF alleles led to a model where the sequential activation of the hox genes along the chromosome result from the sequential opening of chromosomal domains. Most of these GOF alleles turned out to be deletions of boundary elements (BE) that define the extent of the segment-specific regulatory domains. The fruit fly Drosophila is a highly specialized insect with a very rapid mode of segmentation. Furthermore, the hox clusters in this lineage have split. Given these specificities it is legitimate to question whether the regulatory landscape of the BX-C we know of in D.melanogaster is the result of very high specialization in this lineage, or whether it reflects a more ancestral organization. In this article, the authors address this question by analyzing the continuous hox cluster in butterflies. They focus on the intergenic region between the Antennapedia and the Ubx gene, where the split occurred in D.melanogaster. Hi-C and ATAC-seq data suggest the existence of a boundary element between 2 Topologically-Associated-Domain (TAD) which is also characterized by the presence of CTCF binding sites. Butterflies have 2 pairs of wings originating from T2 (forewing) specified by Antp and T3 specified by Ubx (hindwing). Remarkably, CRISPR mutational perturbation of this boundary leads to the hatching of butterflies with homeotic clones of cells with hindwings identities in the forewing (a posteriorly oriented homeotic transformation). In agreement with this phenotype, the authors observe ectopic expression of Ubx in these clones of cells. In other words, CRISPR mutagenesis of this BE region identified by molecular tool give rise to homeotic transformations directed towards more posterior segment as the boundary mutations that had been 1st identified on the basis of their posterior oriented homeotic transformation in Drosophila. None of the mutant clones they observed affect the hindwing, indicating that their scheme did not affect the nearby Ubx transcription unit. This is reassuring and important first evidence that some of the regulatory paradigms that have been proposed in fruit flies are also at work in the common ancestor to Drosophilae and Lepidoptera.

Given the large size of the Ubx transcription unit and its associated regulatory regions it is not surprising that the authors have identified ncRNA that are conserved in 4 species of Nymphalinae butterflies, some of which also present in D.melanogaster. Attempts to target the promoters by CRISPR give rise to clones of cells in both forewings and hindwings, suggesting the generation of regulatory mutations associated with both LOF and GOF transformations. The presence of clones with dual homeosis suggests the targeting of Ubx activator and repression CRMs. Unfortunately, these experiments do not allow us to make further conclusions on the role of these ncRNA or in the identification of specific regulatory elements. To the opinion of this reviewer, some recent papers addressing the role that these ncRNA may play in boundary function should be taken with caution, and evidence that ncRNA(s) regulate boundaries in the BX-C in a WT context is still lacking.

Strengths:

The convincing GOF phenotype resulting from the targeting of the Antp-Ubx_BE.

Weaknesses:

The lack of comparisons with the equivalent phenotypes obtained in D.melanogaster with for example the Fub mutation.

We are grateful for this excellent contextualization of our findings and have incorporated some of the historical elements into our revision, as detailed below.

Reviewer #2 (Recommendations For The Authors):

In the whole paper, the authors bring the notion of boundaries through the angle of the existence of TADs and ignore almost entirely to explain the characteristics of boundary mutation in the BX-C. To my knowledge examples where targeted boundary deletions between TADs result in misregulation of the neighboring genes, and/or a phenotype, are extremely sparse (especially in the context of the mouse hox genes). Given the extensive litterature describing the boundary mutations and their associated GOF phenotypes, the paper would certainly gain strength if the authors justify their approach through this wealth of information. I must admit that this referee is surprised by the absence of any references to the founding work of the Karch and Bender laboratories on this topic. As a matter of fact, one of the founding members of the boundary class of regulatory elements was already brought in 1993 with the Fab-7 and Mcp elements of the BX-C. Based on gain-of-function homeotic phenotypes, additional Fab boundaries were added to the list. Finally, in 2013, Bender and Lucas (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3606092/) identified the Fub boundary element that delimits the Ubx and abd-A domains in the BX-C. Fub fulfills the criterium of lying at the border of 2 neighboring TADs. Significantly, a deletion of Fub leads to a very penetrant and strong homeotic gain-of-function phenotype in which the flies hatch with a 1st abdominal segment transformed into the 2nd. In agreement with this, abd-A is expressed one parasegment too anterior in embryos. This is exactly the observation gathered from the targeted mutations in the Antp-Ubx_BE; a dominant transformation of anterior to posterior wing accompanied by an ectopic expression of Ubx in the forming primordia of the forwing where it is normally silenced. I believe the paper would gain credibility if the results were reported with the knowledge of the similarities with Fub.

Line 53, I am not aware of the existence of TADs for each of the 9 regulatory domains. The insulators delimit the extent of the regulatory domains but certainly not of TADs.

We thank the reviewer for these suggestions, as well as for the correction – we agree our previous text suggested that all BX-C boundaries are TAD boundaries, which was incorrect. We added a new introduction paragraph that combines classic literature on GOF mutations at boundary elements with recent evidence these are TAD insulators, including Fub (as suggested), and adding Fab-7 for breadth of scope.

"For instance, the deletion of a small region situated between Ubx and abd-A produces the Front-ultraabdominal phenotype (Fub) where the first abdominal segment (A1) is transformed into a copy of the second abdominal segment A2, due to a gain-of-expression of abd-A in A1 where it is normally repressed (Bender and Lucas 2013). At the molecular level, the Fub boundary is enforced by insulating factors that separate Topologically Associating Domains (TADs) of open-chromatin, while also allowing interactions of Ubx and abd-A enhancers with their target promoters (Postika et al. 2018; Srinivasan and Mishra 2020). Likewise, the Fab-7 deletion, which removes a TAD boundary insulating abd-A and Abd–B (Moniot-Perron et al. 2023), transforms parasegment 11 into parasegment 12 due to an anterior gain-of-expression of Abd-B (Gyurkovics et al. 1990). By extrapolation, one may expect that if the Drosophila Hox locus was not dislocated into two complexes, Antp and Ubx 3D contact domains would be separated by a Boundary Element (BE), and that deletions similar with Fub and Fab-7 mutations would result in gain-of-function mutations of Ubx that could effectively transform T2 regions into T3 identities."

A reference to the 1978 Nature article of Lewis should be added after line 42 of introduction.

Added

Line 56-57; the BX-C encoded miRNAs are known to regulate Ubx and abd-A, but not Abd-B.

Corrected

From lines 57 to 61, the authors mention reports aimed at demonstrating a role of ncRNA into Ubx regulation. To my eyes, these gathered evidences are rather weak. A reference to the work of Pease et al in Genetics in 2013 should be mentioned (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3832271/).

Added. Our paragraph includes qualifier language about the functionality of the Ubx-related ncRNAs (“are thought to”, “appears to”), and updated references regarding bxd (Petruk et al. 2006; Ibragimov et al. 2023).

Line 62 authors, should write "Little is known about how Hox genes are regulated outside of Drosophila" and not flies.

Corrected

Lines 110-112 could lncRNA:Ubx-IT1 correspond to PS4 antisense reported by Pease et al in 2023 (see URL above)? Lines 115-117, could lncRNA:UbxAS5' correspond to bxd antisense of Pease et al in 2023 (see above)?

As we could not detect sequence similarities, we preferred to avoid drawing homology, and we intentionally avoided reference to the fly transcripts when we named IT1 and AS5’. This said, we agree it is important to clarify that further studies are needed to clarify this relationship. We elaborated on this point in our discussion:

"Of note, a systematic in-situ survey (Pease et al. 2013) showed that Drosophila embryos express an antisense transcripts in its 5’ region (lncRNA:bxd), as well as within its first intron (lncRNA:PS4). It is thought that Drosophila bxd regulates Ubx, possibly by transcriptional interference or by facilitation of the Fub-1 boundary effect (Petruk et al. 2006; Ibragimov et al. 2023), while the possible regulatory roles of PS4 remain debated (Hermann et al. 2022). While these dipteran non-coding transcripts lack detectable sequence similarity with the lepidopteran IT1 and AS5’ transcripts, further comparative genomics analyses of the Ubx region across the holometabolan insect phylogeny should clarify the extent to which Hox cluster lncRNAs have been conserved or independently evolved."

Lines 154-155: "This concordance between Hi-C profiling and CTCF motif prediction thus indicates that Antp-Ubx_BE region functions as an insulator between regulatory domains of Antp and Ubx ». This is only correlative, I would write "suggests" instead of "indicates" and add a "might function".

Corrected as suggested.

Line 254, I assume the authors wish to write Ubx-IT1 in V. cardui instead of Ubx-T1.

Typo corrected

Line 255 : Fig.5 is absent from the pdf file and replaced by table 1. I did not find a legend for Table 1.

Corrected, with our sincere apologies for the loss of this image in our first submission.

Line 293 "Individual with hindwing clones 2.75 times more common than...." "are" is missing?

Corrected

Lines 303-313, it is not entirely clear how many guide RNAs were injected. Would be useful to indicate the sites targeted in Fig.S8.

We specify in the revised text : using a single guide RNA (Ubx11b9)

Lines 323-337: it is not entirely clear to this referee (a drosophilist) if those spontaneous mutations can be inbred or whether these individuals are occasional mosaics. In general, did anyone try to derive lines from those mosaic animals? Is it possible to hit the germline at the syncitial stages at which the guides are injected? Are the individuals with wing phenotype fertile? Given the fact that the Antp-Ubx_BE mutations should be dominant, I wonder if this characteristic would not help in identifying germline transmission. Similar remark for the discussion where the authors explain at line 360, that genotyping can only be done in the progeny of the Go. I do not have the impression that the authors have performed this genotyping and if I am right, I do not understand why.

We improved our discussion section on this topic (new text in orange):

"It is crucial here to highlight the limitations of the method, in order to derive proper insights about the functionality of the regulatory regions we tested. In essence, butterfly CRISPR experiments generate random mutations by non-homologous end joining repair, that are usually deletions (Connahs et al. 2019; Mazo-Vargas et al. 2022; Van Belleghem et al. 2023). Ideally, regulatory CRISPR-induced alleles require genotyping in a second (G1) generation to be properly matched to a phenotype (Mazo-Vargas et al. 2022). Possibly because of lethal effects, we failed to pass G0 mutations to a G1 generation for genotyping, and were thus limited here to mosaic analysis. As adult wings have lost scale building cells that may underlie a given phenotype, we circumvented this issue by genotyping a pupal forewing displaying an homeotic phenotype in the more efficient Antp-Ubx_BE perturbation experiment (Fig. S4). In this case, PCR amplification of a 600 bp fragment followed by Sanger sequencing recovered signatures of indel variants, with mixed chromatograms starting at the targeted sites. But in all other experiments (CRM11, IT1, and AS5’ targets), we did not genotype mutant tissues, as they were only detected in adult stages and generally with small clone sizes. Some of these clones may have been the results of large structural variants, as data from other organisms suggests that Cas9 nuclease targeting can generate larger than expected mutations that evade common genotyping techniques (Shin et al. 2017; Adikusuma et al. 2018; Kosicki et al. 2018; Cullot et al. 2019; Owens et al. 2019). Even under the assumption that such mutations are relatively rare in butterfly embryos, the fact we injected >100 embryos in each experiment makes their occurrence likely (Fig. 9), and we are unable to assign a specific genotype to the homeotic effects we obtained in CRM11, IT1 and AS5’ perturbation assays."

We agree that the work we conducted with mosaics has important caveats. So far, our attempts at breeding homeotic G0 mutants have not been fruitful at this locus, while less deleterious loci can yield viable alleles into further generations, such as WntA (published) and cortex (in prep.). We prefer to stay vague about negative data here, as it is difficult to disentangle if they were due to real mutational effects (e.g. the alleles can be dominant and lethal in the G1 generation) to failure to germline carriers of mutations as founders, or to health issues that are often amplified by inbreeding depression (including a possible iflavirus in our V. cardui cultures).

We concur with the prediction that Antp-Ubx_BE mutations are probably dominant, and intend to follow up with similar GOF experiments in the Plodia pantry moth, a laboratory model for lepidopteran functional genomics that is more amenable than butterflies to inbreeding and long-term studies in mutant lines. In our experience (https://www.frontiersin.org/articles/10.3389/fevo.2021.643661/full), Ubx coding knock-out can be more extensive in Plodia than in butterflies, so we think these animals will also be more resilient to the deleterious effects of the GOF phenotype.

Line 423, 425, I am not a fan of the term "de-insulating!!!!!

We replaced this neologism by Similar deletion alleles resulting in a TAD fusion and misexpression effect (see below).

Line 425, why bring the work on Notch while there are so many examples in the BX-C itself....

Our revised sentence makes it more clear we are referring here to documented examples of deletion-mediated TAD fusion (ie. featuring a conformation capture assay such as HiC/micro-C):

This suggests a possible loss of the TAD boundary in the crispant clones, resulting in a TAD fusion or in a long-range interaction between a T2-specific enhancer and Ubx promoter. Similar deletion alleles resulting in a TAD fusion and misexpression effect have been described at the Notch locus in Drosophila (Arzate-Mejía et al. 2020), in digit-patterning mutants in mice and humans (Lupiáñez et al. 2015; Anania et al. 2022), or at murine and fly Hox loci depleted of CTCF-mediated regulatory blocking (Narendra et al. 2015; Gambetta and Furlong 2018; Kyrchanova et al. 2020).

Our revision also includes more emphasis on the Drosophila BX-C boundary elements Fub and Fab-7 (see above).

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):

Summary:

This study investigates the hypoxia rescue mechanisms of neurons by non-neuronal cells in the brain from the perspective of exosomal communication between brain cells. Through multi-omics combined analysis, the authors revealed this phenomenon and logically validated this intercellular rescue mechanism under hypoxic conditions through experiments. The study proposed a novel finding that hemoglobin maintains mitochondrial function, expanding the conventional understanding of hemoglobin. This research is highly innovative, providing new insights for the treatment of hypoxic encephalopathy.

Overall, the manuscript is well organized and written, however, there are some minor/major points that need to be revised before this manuscript is accepted.

We thank the reviewer for the detailed analysis of our study. Please find our answers to the points raised by the reviewer below.

Major points:

(1) Hypoxia can induce endothelial cells to release exosomes carrying hemoglobin, however, how neurons are able to actively take up these exosomes? It is possible for other cells to take up these exosomes also? This point needs to be clarified in this study.

We sincerely appreciate the reviewer’s valuable comments. Regarding the question of how neurons actively uptake extracellular vesicles (EVs) carrying hemoglobin mRNA, existing studies suggest that EVs can enter cells via three main pathways: direct fusion, receptor-mediated endocytosis, and phagocytosis (PMID: 25288114). Our experimental results show that neurons are able to actively uptake EVs from endothelial cells without any treatment, and hypoxic conditions did not significantly increase the uptake of endothelial EVs by neurons (Fig. 5A and I). As for the specific uptake mechanism, there is currently no definitive conclusion. Some studies have found that hypoxic-ischemic injury may induce neurons to upregulate Cav-1, which could enhance the uptake of endothelial-derived EVs via Cav-1-mediated endocytosis (PMID: 31740664), but this mechanism still requires further validation.

Regarding whether other cell types also take up these EVs, we focused on neurons based on existing literature and our own data, which show that the increased hemoglobin in the brain under hypoxic conditions is primarily found in neurons (Fig. 4H-J, PMID: 19116637). Moreover, we observed that, under hypoxic conditions, almost all non-neuronal supporting cells in the brain transcribe hemoglobin in large amounts and release it via EVs (Fig. 3J). Furthermore, we would like to emphasize that although neurons do not transcribe hemoglobin, we observed substantial expression of hemoglobin within neurons. This suggests that it may serve as an important protective mechanism for the brain. Therefore, the focus of our study is on the protective effect of EVs carrying hemoglobin mRNA on neurons, and the uptake by other cell types was not explored. We greatly appreciate the reviewer’s question, and we believe this is an intriguing avenue for further investigation. This could provide new insights for interventions in hypoxic brain injury, and we plan to delve into this topic in future studies.

(2) The expression of hemoglobin in neurons is important for mitochondrial homeostasis, but its relationship with mitochondrial homeostasis needs to be further elucidated in the study.

We sincerely appreciate the reviewer’s valuable comments. We fully agree with the importance of hemoglobin expression in neurons for mitochondrial homeostasis. In this study, we have confirmed through in vitro experiments that when neurons are treated with conditioned medium from endothelial cells, they exhibit increased hemoglobin expression. This, in turn, enhances their resistance to hypoxia by restoring mitochondrial membrane potential and increasing mitochondrial numbers, thereby effectively improving neuronal viability. Notably, this protective effect disappears when EVs are removed from the endothelial-conditioned medium or when hemoglobin in endothelial cells is disrupted, further supporting the notion that endothelial cells transfer hemoglobin via EVs, helping neurons express hemoglobin under hypoxic conditions and exert protective effects.

In summary, hemoglobin primarily helps maintain mitochondrial membrane potential, thereby supporting the restoration of energy metabolism and production under hypoxic conditions, which effectively improves the neuronal resistance to hypoxia. Although we were unable to explore the specific mechanisms of hemoglobin’s role in mitochondrial homeostasis in detail within this study, we recognize the importance of this aspect and plan to further investigate how hemoglobin regulates mitochondrial homeostasis and function in neurons in future research.

Once again, we greatly appreciate the reviewer’s insightful comments. We will continue to optimize our research direction and look forward to further elucidating these important biological mechanisms in future studies.

Minor points:

(1) In Figures 1-3, the authors use "Endo" to represent endothelial cells, while in Figures 4-7, the abbreviation "EC" is used. Please standardize the format.

Thank you for the reviewer’s suggestion. We will use “EC” consistently to refer to endothelial cells throughout the manuscript to ensure uniformity.

(2) In all qPCR statistical results, please italicize the gene names on the axis.

Thank you for the reviewer’s valuable suggestion. We will make sure to italicize the gene names on the axis in all qPCR statistical results to adhere to the formatting requirements.

(3) In the Western blot result of Figure 3C, what type of cell-derived exosomes does the Control group represent, and why can it be used as a control group for brain-derived exosomes?

Thank you for the reviewer’s insightful question. In Fig. 3C, the control group (Control) represents the cell lysate sample, which serves as a positive control in the EVs Western blot analysis. In this experiment, the positive control is primarily used to validate the specificity of the antibody and the accuracy of the experimental procedure. We used cell lysate as the control to confirm that the antibody can detect EV-associated markers in the cell lysates, thus providing a comparative basis for the identification of brain-derived EVs.

(4) In Figure 4F, the morphology of hemoglobin in the Con group and the H28d group is not entirely consistent with Figure 4H. Is this difference due to different experimental batches?

Thank you for the reviewer’s careful observation. The observed difference may indeed be due to variations between different experimental batches. To ensure consistency of the results, we have updated the representative immunofluorescence images, which are now presented in Fig. 4H.

(5) Supplement the transcription and expression levels of hemoglobin in neurons under different treatment conditions after medium exchange with exosome removal and medium exchange after HBA1 interference.

Thank you for the reviewer’s valuable suggestions. We have added the experimental data regarding the exchange of culture medium after the removal of EVs. As shown in Fig. S6, the endothelial-derived medium without EVs does not enhance the hemoglobin levels in neurons under hypoxic conditions. Additionally, we have included the detection results of hemoglobin expression in neurons after HBA1 interference, as shown in Fig. S7E-F. The results indicate that the culture medium derived from HBA1-interfered endothelial cells also fails to help neurons increase hemoglobin expression under hypoxic conditions.

(6) Figure S3 should be split to separately explain the increased exosome release induced by hypoxia, the non-toxic effect of endothelial cell culture medium on neurons, and the successful screening of the HBA1 interference plasmid.

Thank you for the reviewer’s suggestions. Based on your feedback, we have split the original Fig. S3 into multiple parts to more clearly present the different experimental results. Specifically, the results of hypoxia-induced EVs release increase have been updated in Fig. S4, the non-toxic effects of endothelial cell culture medium on neurons are shown in Fig. S5, and the successful screening of the HBA1 interference plasmid is presented in Fig. S7.

(7) Regarding the extracellular vesicles/exosomes, it should be expressed consistently in the whole manuscript.

Thank you for the reviewer’s reminder. We will ensure that the term “extracellular vesicles” is used consistently throughout the manuscript.

(8) In lines 70 and 80, the O2 should be changed to "O₂".

Thank you for the reviewer’s careful observation. We have corrected the formatting of “O2” to “O₂” in lines 70 and 80.

We would like to thank the Reviewer for taking the time to thoroughly examine our work, for their helpful feedback that has significantly contributed to improving our manuscript, and for their kind and encouraging words.

Reviewer #2 (Public Review):

Summary:

This is an interesting study with a lot of data. Some of these ideas are intriguing. But a few major points require further consideration.

We thank the reviewer for the detailed assessment of our study and pinpointing its current weaknesses. Please find our answers to all comments below.

Major points:

(1) What disease is this model of whole animal hypoxia supposed to mimic? If one is focused on the brain, can one just use a model of focal or global cerebral ischemia?

Thank you for the reviewer’s insightful question. The chronic hypoxia model we employed is designed to mimic the multi-organ damage caused by systemic hypoxia, which is relevant to clinical conditions such as high-altitude hypoxia, chronic obstructive pulmonary disease, and acute hypoxic brain injury. In contrast to focal or global cerebral ischemia models, the focus of our study is on how the brain, under extreme systemic hypoxia, utilizes endothelial cell-derived extracellular vesicles (EVs) to transfer hemoglobin mRNA, thereby protecting neurons and aiding the brain’s response to hypoxia-induced damage.

We understand the reviewer’s concern that focal or global ischemia models are typically used to simulate localized brain hypoxia or ischemic injury. However, the core of our research is to explore the brain’s overall adaptive mechanisms under systemic hypoxic conditions. By using a systemic hypoxia model, we can more comprehensively simulate the effects of global hypoxia on the brain and uncover how the brain engages specific molecular mechanisms for self-protection. This approach offers a novel perspective on brain hypoxic-ischemic diseases and holds potential clinical applications, particularly in the study of stroke, vascular cognitive impairment and dementia (VCID), and related conditions.

Additionally, we have observed that hemoglobin significantly increases in the brain in an animal model of focal ischemia (as shown in Author response image 1 below). This finding further supports the idea that hemoglobin upregulation may be a universal protective mechanism for the brain’s response to hypoxic damage. While this part of the research is still ongoing, preliminary results suggest that both systemic hypoxia and focal ischemia might trigger protective effects through hemoglobin regulation.

Author response image 1.

The expression level of Hba-a1 in the brain of VCID mouse.

Therefore, the core of our study is to elucidate the brain’s self-protection mechanisms under systemic hypoxia, rather than focusing solely on cerebral ischemia models. We believe this approach provides new insights into the prevention and treatment of brain hypoxic-ischemic diseases, with significant clinical application potential.

In light of this, we have added a related discussion to the manuscript, clearly explaining the rationale for choosing the systemic hypoxia model. The updated content can be found on P11, Line 13-21 as follows: “To investigate this phenomenon, we employed a chronic hypoxia model in which mice were exposed to 7% oxygen for 28 days. This model aims to mimic systemic hypoxia-induced multi-organ damage, a condition observed in diseases such as high-altitude hypoxia, chronic obstructive pulmonary disease, and acute hypoxic brain injury. The primary goal of this model is to explore how the brain adapts under extreme low-oxygen conditions and employs specific mechanisms to protect itself from hypoxia-induced damage. This approach provides valuable insight into diseases related to hypoxic-ischemic injury in the brain, including stroke and vascular dementia, offering a novel perspective for potential clinical applications.”

(2) If this model subjects the entire animal to hypoxia, then other organs will also be hypoxic. Should one also detect endothelial upregulation and release of extracellular vesicles containing hemoglobin mRNA in non-CNS organs? Where do these vesicles go? Into blood?

Thank you for the reviewer’s valuable feedback. Indeed, in a whole-body hypoxia model, other organs are also affected by hypoxia. Therefore, future research may need to investigate the upregulation of endothelial cells in organs other than the central nervous system, as well as the release of EVs containing hemoglobin mRNA from these organs. However, in this study, we isolated EVs from the brain tissue in situ following perfusion with physiological saline, a method that effectively eliminates the influence of EVs from blood or other organs. As a result, our primary focus was on studying how EVs released by brain endothelial cells are actively taken up by neurons to exert neuroprotective effects. The potential for these EVs to enter the bloodstream and their subsequent fate is indeed a topic worthy of further investigation. Future research could offer new insights into the cross-organ effects of systemic hypoxia.

(3) What other mRNA are contained in the vesicles released from brain endothelial cells?

Thank you for the reviewer’s valuable suggestions. We have further analyzed EVs derived from brain endothelial cells, and in addition to hemoglobin mRNA, these EVs also contain a variety of other mRNAs, including Vwf, Hbb-bt, Hba-a1, Hbb-bs, Hba-a2, Acer2, Angpt2, Ldha, Gm42418, Slc16a1, Cxcl12, B2m, Ctla2a, Ccnd1, and Hmgcs2 (Log2FC > 1.2). The biological processes associated with these mRNAs primarily involve: cell-substrate adhesion, regulation of cellular amide metabolic process, negative regulation of cell migration, negative regulation of cell motility, and negative regulation of cellular component movement. These processes may be closely related to the neuroprotective effects of endothelial cell EVs in a hypoxic environment, especially in terms of regulating cell behavior and maintaining cell structure and function. Additionally, these EVs contain multiple key factors associated with intracellular metabolism, movement, and migration, which may collectively influence neuronal function and survival. Notably, our study also found that mRNA of various hemoglobin subunits ranks among the top five in terms of abundance in the mRNA secreted by hypoxic endothelial EVs, further emphasizing the importance of hemoglobin mRNA in endothelial-derived EVs. Therefore, future research may explore the functions of these mRNAs and reveal how they act in concert to protect neurons from hypoxia-induced damage.

We have updated and added these results in Fig. S4, and have further elaborated on the findings in the revised figure. Once again, we thank the reviewer for the attention and valuable suggestions regarding our work.

(4) Where do the endothelial vesicles go? Only to neurons? Or to other cells as well?

Thank you for the reviewer’s important question. As previously mentioned, the focus of this study is to investigate how EVs carrying hemoglobin mRNA influence neuronal function. Through a combined analysis of single-cell transcriptomics and EV transcriptomics from brain tissue, we found that, besides neurons, almost all types of supportive cells in the brain and their secreted EVs contain a significant amount of hemoglobin mRNA (Fig. 3J, 4B). Notably, although neurons do not transcribe hemoglobin mRNA themselves, under hypoxic conditions, neurons significantly increase hemoglobin expression, resulting in a phenomenon where the transcription and expression levels of hemoglobin in neurons are inconsistent. This phenomenon has been observed both in our study and others (Fig. 4H-J, PMID: 19116637). This observation led us to focus on the active uptake of EVs by neurons and the potential neuroprotective effects they might bring.

Regarding whether other cell types uptake these EVs and their potential functions, although our current research is focused on neurons, this is indeed an important area for further investigation. Given that non-neuronal supportive cells may also transfer hemoglobin mRNA via EVs under hypoxic conditions, future research will further explore the uptake of EVs by different cell types and their roles in hypoxic adaptation.

We are particularly interested in the hemoglobin expression in neurons under hypoxic conditions and consider neurons to be the primary expressers of hemoglobin, providing a new perspective for exploring the neuroprotective role of hemoglobin. We plan to delve deeper into these issues in future studies.

(5) Neurons can express endogenous hemoglobin. Is it useful to subject neurons to hypoxia and then see how much the endogenous mRNA goes up? How large is the magnitude of endogenous hemoglobin gene upregulation compared to the hypothesized exogenous mRNA that is supposed to be donated from endothelial vesicles?

Thank you for the reviewer’s valuable question. We have observed that, in the absence of treatment with endothelial cell-derived conditioned medium, there is no significant change in the transcription and expression levels of endogenous hemoglobin in neurons under hypoxic conditions (Fig. 5I, 6C-D). However, when neurons were treated with endothelial cell-conditioned medium, under the same hypoxic conditions, the transcription levels of hemoglobin increased by approximately 1.2-fold, and the expression levels increased by approximately 3.8-fold (Fig. 6B-D). Additionally, we have added pre-treatment experiments involving EVs depletion from the endothelial culture medium and HBA interference. The results show that, after these two pre-treatments, the conditioned medium lost its ability to enhance the transcription and expression of hemoglobin in neurons under hypoxic conditions (Fig. S6, S7D-F), further emphasizing the important role of endothelial EVs in this process. This finding indicates that endothelial-derived EVs significantly promote hemoglobin expression in neurons, and this effect is far greater than the upregulation of endogenous hemoglobin in neurons. Therefore, while neurons can express endogenous hemoglobin, exogenous hemoglobin significantly enhances its expression, which may help neurons tolerate the hypoxic environment and provide additional protection.

(6) Finally, it may be useful to provide more information and data to explain how the expression of this exogenous endothelial-derived hemoglobin binds to neuronal mitochondria to alter function.

Thank you for the reviewer’s valuable suggestion. As we previously mentioned, hemoglobin plays a protective role in neurons by maintaining mitochondrial membrane potential, helping neurons restore energy metabolism and energy production under hypoxic conditions. We fully agree on the importance of this research direction. Several studies have shown that when hemoglobin is expressed in neurons, it predominantly localizes to mitochondria, which aligns with the physiological process of heme synthesis within mitochondria (PMID: 23187133). Furthermore, in the brains of Parkinson’s disease patients, the localization of hemoglobin in neuronal mitochondria is altered compared to normal conditions (PMID: 27181046). Therefore, the interaction between hemoglobin and mitochondria plays a crucial role in neuronal function.

Although existing research indicates the role of hemoglobin in neuronal mitochondria, studies in this area remain limited. We plan to further investigate how hemoglobin binds to mitochondria and its specific effects on mitochondrial function in our future work. We believe that a deeper understanding of this mechanism will provide essential theoretical insights into the effects of hypoxia on neurons and offer new potential strategies for neuroprotective therapies.

We would like to thank the Reviewer for taking the time to thoroughly examine our work, for their helpful feedback that has significantly contributed to improving our manuscript, and for their kind and encouraging words.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

(1) Some details are not described for experimental procedures. For example, what were the pharmacological drugs dissolved in, and what vehicle control was used in experiments? How long were pharmacological drugs added to cells?

We apologise for the oversight. These details have now been added to the methods section of the manuscript as well as to the relevant figure legends.

Briefly, latrunculin was used at a final concentration of 250 nM and Y27632 at a final concentration of 50 μM. Both drugs were dissolved in DMSO. The vehicle controls were effected with the highest final concentration of DMSO of the two drugs.

The details of the drug treatments and their duration was added to the methods and to figures 6, S10, and S12.

(2) Details are missing from the Methods section and Figure captions about the number of biological and technical replicates performed for experiments. Figure 1C states the data are from 12 beads on 7 cells. Are those same 12 beads used in Figure 2C? If so, that information is missing from the Figure 2C caption. Similarly, this information should be provided in every figure caption so the reader can assess the rigor of the experiments. Furthermore, how heterogenous would the bead displacements be across different cells? The low number of beads and cells assessed makes this information difficult to determine.

We apologise for the oversight. We have now added this data to the relevant figure panels.

To gain a further understanding of the heterogeneity of bead displacements across cells, we have replotted the relevant graphs using different colours to indicate different cells. This reveals that different cells appear to behave similarly and that the behaviour appears controlled by distance to the indentation or the pipette tip rather than cell identity.

We agree with the reviewer that the number of cells examined is low. This is due to the challenging nature of the experiments that signifies that many attempts are necessary to obtain a successful measurement.

The experiments in Fig 1C are a verification of a behaviour documented in a previous publication [1]. Here, we just confirm the same behaviour and therefore we decided that only a small number of cells was needed.

The experiments in Fig 2C (that allow for a direct estimation of the cytoplasm’s hydraulic permeability) require formation of a tight seal between the glass micropipette and the cell, something known as a gigaseal in electrophysiology. The success rate of this first step is 10-30% of attempts for an experienced experimenter. The second step is forming a whole cell configuration, in which a hydraulic link is formed between the cell and the micropipette. This step has a success rate of ~ 50%. Whole cell links are very sensitive to any disturbance. After reaching the whole cell configuration, we applied relatively high pressures that occasionally resulted in loss of link between the cell and the micropipette. In summary, for the 12 successful measurements, hundreds of unsuccessful attempts were carried out.

(3) The full equation for displacement vs. time for a poroelastic material is not provided. Scaling laws are shown, but the full equation derived from the stress response of an elastic solid and viscous fluid is not shown or described.

We thank the reviewer for this comment. Based on our experiments, we found that the cytoplasm behaves as a poroelastic material. However, to understand the displacements of the cell surface in response to localised indentation, we show that we also need to take the tension of the submembranous cortex into account. In summary, the interplay between cell surface tension generated by the cortex and the poroelastic cytoplasm controls the cell behaviour. To our knowledge, no simple analytical solutions to this type problem exist.

In Fig 1, we show that the response of the cell to local indentation is biphasic with a short time-scale displacement followed by a longer time-scale one. In Figs 2 and 3, we directly characterise the kinetics of cell surface displacement in response to microinjection of fluid. These kinetics are consistent with the long time-scale displacement but not the short time-scale one. Scaling considerations led us to propose that tension in the cortex may play a role in mediating the short time-scale displacement. To verify this hypothesis, we have now added new data showing that the length-scale of an indentation created by an AFM probe depends on tension in the cortex (Fig S5).  

In a previous publication [2], we derived the temporal dynamics of cell surface displacement for a homogenous poroelastic material in response to a change in osmolarity. In the current manuscript, the composite nature of the cell (membrane, cortex, cytoplasm) needs to be taken into account as well as a realistic cell shape. Therefore, we did not attempt to provide an analytical solution for the displacement of the cell surface versus time in the current work. Instead, we turned to finite element modelling to show that our observations are qualitatively consistent with a cell that comprises a tensed submembranous actin cortex and a poroelastic cytoplasm (Fig 4). We have now added text to make this clearer for the reader.

Reviewer #2 (Public review):

Comments & Questions:

The authors state, "Next, we sought to quantitatively understand how the global cellular response to local indentation might arise from cellular poroelasticity." However, the evidence presented in the following paragraph appears more qualitative than strictly quantitative. For instance, the length scale estimate of ~7 μm is only qualitatively consistent with the observed ~10 μm, and the timescale 𝜏𝑧 ≈ 500 ms is similarly described as "qualitatively consistent" with experimental observations. Strengthening this point would benefit from more direct evidence linking the short timescale to cell surface tension. Have you tried perturbing surface tension and examining its impact on this short-timescale relaxation by modulating acto-myosin contractility with Y-27632, depolymerizing actin with Latrunculin, or applying hypo/hyperosmotic shocks?

Upon rereading our manuscript, we agree with the reviewer that some of our statements are too strong. We have now moderated these and clarified the goal of that section of the text.

The reviewer asks if we have examined the effect of various perturbations on the short time-scale displacements. In our experimental conditions, we cannot precisely measure the time-scale of the fast relaxation because its duration is comparable to the frame rate of our image acquisition. However, we examined the amplitude of the displacement of the first phase in response to sucrose treatment and we have carried out new experiments in which we treat cells with 250nM Latrunculin to partially depolymerise cellular F-actin. Neither of these treatments had an impact on the amplitude of vertical displacements (Fig. S3).

The absence of change in response to Latrunculin may be because the treatment decreases both the elasticity of the cytoplasm  and the cortical tension . As the length-scale  of the deformation of the surface scales as , the two effects of latrunculin treatment may therefore compensate one another and result in only small changes in . We have now added this data to supplementary information and comment on this in the text.   

The reviewer’s comment also made us want to determine how cortical tension affects the length-scale of the cell surface deformation created by localised microindentation. To isolate the role of the cortex from that of cell shape, we decided to examine rounded mitotic cells. In our experiments, we indented a mitotic cell expressing a membrane targeted GFP with a sharp AFM tip (Fig. S5).

In our experiments, we adjusted force to generate a 2μm depth indentation and we imaged the cell profile with confocal microscopy before and during indentation. Segmentation of this data allowed us to determine the cell surface displacement resulting from indentation and measure a length scale of deformation. In control conditions, the length scale created by deformation is on the order of 1.2μm. When we inhibited myosin contractility with blebbistatin, the length-scale of deformation decreased significantly to 0.8 μm, as expected if we decrease the surface tension γ without affecting the cytoplasmic elasticity. We have now added this data to our manuscript.

The authors demonstrate that the second relaxation timescale increases (Figure 1, Panel D) following a hyperosmotic shock, consistent with cytoplasmic matrix shrinkage, increased friction, and consequently a longer relaxation timescale. While this result aligns with expectations, is a seven-fold increase in the relaxation timescale realistic based on quantitative estimates given the extent of volume loss?

We thank the reviewer for this interesting question. Upon re-examining our data, we realised that the numerical values in the text related to the average rather than the median of our measurements. The median of the poroelastic time constant increases from ~0.4s in control conditions to 1.4s in sucrose, representing approximately a 3.5 fold increase.

Previous work showed that HeLa cell volume decreases by ~40% in response to hyperosmotic shock [3]. The fluid volume fraction in cells is ~65-75%. If we assume that the water is contained in N pores of volume , we can express the cell volume as with the volume of the solid fraction. We can rewrite .

With ∅ = 0.42  -0.6.  As  does not change in response to osmotic shock, we can rewrite the volume change to obtain the change in pore size .

The poroelastic diffusion constant scales as and the poroelastic timescale scales as . Therefore, the measured change in volume leads to a predicted increase in poroelastic diffusion time of 1.7-1.9 fold, smaller than observed in our experiments. This suggests that some intuition can be gained in a straightforward manner assuming that the cytoplasm is a homogenous porous material.

However, the reality is more complex and the hydraulic pore size is distinct from the entanglement length of the cytoskeleton mesh, as we discussed in a previous publication [4]. When the fluid fraction becomes sufficiently small, macromolecular crowding will impact diffusion further and non-linearities will arise. We have now added some of these considerations to the discussion.

If the authors' hypothesis is correct, an essential physiological parameter for the cytoplasm could be the permeability k and how it is modulated by perturbations, such as volume loss or gain. Have you explored whether the data supports the expected square dependency of permeability on hydraulic pore size, as predicted by simple homogeneity assumptions?

We thank the reviewer for this comment. As discussed above, we have explored such considerations in a previous publication (see discussion in [4]). Briefly, we find that the entanglement length of the F-actin cytoskeleton does play a role in controlling the hydraulic pore size but is distinct from it. Membrane bounded organelles could also contribute to setting the pore size. In our previous publication, we derived a scaling relationship that indicates that four different length-scales contribute to setting cellular rheology: the average filament bundle length, the size distribution of particles in the cytosol, the entanglement length of the cytoskeleton, and the hydraulic pore size. Many of these length-scales can be dynamically controlled by the cell, which gives rise to complex rheology. We have now added these considerations to our discussion.

Additionally, do you think that the observed decrease in k in mitotic cells compared to interphase cells is significant? I would have expected the opposite naively as mitotic cells tend to swell by 10-20 percent due to the mitotic overshoot at mitotic entry (see Son Journal of Cell Biology 2015 or Zlotek Journal of Cell Biology 2015).

We thank the reviewer for this interesting question. Based on the same scaling arguments as above, we would expect that a 10-20% increase in cell volume would give rise to 10-20% increase in diffusion constant. However, we also note that metaphase leads to a dramatic reorganisation of the cell interior and in particular membrane-bounded organelles. In summary, we do not know why such a decrease could take place. We now highlight this as an interesting question for further research.

Based on your results, can you estimate the pore size of the poroelastic cytoplasmic matrix? Is this estimate realistic? I wonder whether this pore size might define a threshold above which the diffusion of freely diffusing species is significantly reduced. Is your estimate consistent with nanobead diffusion experiments reported in the literature? Do you have any insights into the polymer structures that define this pore size? For example, have you investigated whether depolymerizing actin or other cytoskeletal components significantly alters the relaxation timescale?

We thank the reviewer for this comment. We cannot directly estimate the hydraulic pore size from the measurements performed in the manuscript. Indeed, while we understand the general scaling laws, the prefactors of such relationships are unknown.

We carried out experiments aiming at estimating the hydraulic pore size in previous publications [3,4] and others have shown spatial heterogeneity of the cytoplasmic pore size [5]. In our previous experiments, we examined the diffusion of PEGylated quantum dots (14nm in hydrodynamic radius). In isosmotic conditions, these diffused freely through the cell but when the cell volume was decreased by a hyperosmotic shock, they no longer moved [3,4]. This gave an estimate of the pore radius of ~15nm.

Previous work has suggested that F-actin plays a role in dictating this pore size but microtubules and intermediate filaments do not [4].

There are no quantifications in Figure 6, nor is there a direct comparison with the model. Based on your model, would you expect the velocity of bleb growth to vary depending on the distance of the bleb from the pipette due to the local depressurization? Specifically, do blebs closer to the pipette grow more slowly?

We apologise for the oversight. The quantifications are presented in Fig S10 and Fig S12. We have now modified the figure legends accordingly.

Blebs are very heterogenous in size and growth velocity within a cell and across cells in the population in normal conditions [6]. Other work has shown that bleb size is controlled by a competition between pressure driving growth and actin polymerisation arresting it[7]. Therefore, we did not attempt to determine the impact of depressurisation on bleb growth velocity or size.

In experiments in which we suddenly increased pressure in blebbing cells, we did notice a change in the rate of growth of blebs that occurred after we increased pressure (Author response image 1). However, the experiments are technically challenging and we decided not to perform more.

Author response image 1.

A. A hydraulic link is established between a blebbing cell and a pipette. At time t>0, a step increase in pressure is applied. B. Kymograph of bleb growth in a control cell (top) an in a cell subjected to a pressure increase at t=0s (bottom). Top: In control blebs, the rate of growth is slow and approximately constant over time. The black arrow shows the start of blebbing. Bottom: The black arrow shows the start of blebbing. The dashed line shows the timing of pressure application and the red arrow shows the increase in growth rate of the bleb when the pressure increase reaches the bleb. This occurs with a delay δt.

I find it interesting that during depressurization of the interphase cells, there is no observed volume change, whereas in pressurization of metaphase cells, there is a volume increase. I assume this might be a matter of timescale, as the microinjection experiments occur on short timescales, not allowing sufficient time for water to escape the cell. Do you observe the radius of the metaphase cells decreasing later on? This relaxation could potentially be used to characterize the permeability of the cell surface.

We thank the reviewer for this comment.

First, we would like to clarify that both metaphase and interphase cells increase their volume in response to microinjection. The effect is easier to quantify in metaphase cells because we assume spherical symmetry and just monitor the evolution of the radius (Fig 3). However, the displacement of the beads in interphase cells (Fig 2) clearly shows that the cell volume increases in response to microinjection. For both interphase and metaphase cells, when the injection is prolonged, the membrane eventually detaches from the cortex and large blebs form until cell lysis. In contrast to the reviewer’s intuition, we never observe a relaxation in cell volume, probably because we inject fluid faster than the cell can compensate volume change through regulatory mechanisms involving ion channels.

When we depressurise metaphase cells, we do not observe any change in volume (Fig S10). This contrasts with the increase that we observe upon pressurisation. The main difference between these two experiments is the pressure differential. During depressurisation experiments, this is the hydraulic pressure within the cell ~500Pa (Fig 6A); whereas during pressurisation experiments, this is the pressure in the micropipette, ranging from 1.4-10 kPa (Fig 3). We note in particular that, when we used the lowest pressures in our experiments, the increase in volume was very slow (see Fig 3C). Therefore, we agree with the reviewer that it is likely the magnitude of the pressure differential that explains these differences.