Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

We thank reviewers for their comments and constructive criticisms of our study. We have implemented corrections* that were suggested for the manuscript, and we have also clarified any concerns that were raised in our responses below. *

*Reviewer #1 *

Overall technology development is good though as they claim that they are first is not true as it has been used earlier by https://doi.org/10.1128/msphere.00160-22. Hence may be that they have used to decipher the cell cycle.

The cited paper used FUCCI in the host cells and not in the parasites themselves. Our study thus reports the first FUCCI model in a unicellular *eukaryote. *

• *

The manuscript is extremely dense and at times very difficult to read and to be clear if they are focussing on the technology or cell cycle. The technology may be a better part of manuscript but the dissection of cell cycle is not very novel and at times very confusing to follow. Many of these aspects has been dissected out previously from their own group and many group in Toxoplasma and Plasmodium and it is quite known about that the cell cycle in Apicomplexa is very complex.

We adapted FUCCI to the Toxoplasma model to help dissect the organization of its cell cycle, which as the reviewer noted, is highly complex. While overlaps between some phases were anticipated based on prior data, these overlaps had not been measured. We were able to determine the extent of these overlaps in the post-G1 period and describe the organization of the non-conventional cell cycle of T. gondii.

Another aspect that most FUCCI use Geminin and CDT1 factors and since Geminin is not present it would have been better to validate that with CDT1 that is present in Apicomplexa and may be more relevant than PCNA1.

Unfortunately, the Toxoplasma ortholog of CDT1 (TgiRD1) cannot be used as a FUCCI marker for the reasons stated in lines 116-117; the expression of TgiRD1 is not limited to a specific cell cycle phase (Hawkins et al., 2024). PCNA1 can be (and has been) used as a FUCCI marker, but it was not considered an ideal marker in mammalian cells due to its relatively low expression levels. However, Toxoplasma PCNA1 is highly abundant in tachyzoites, and its expression correlates with the period of DNA replication. Furthermore, Plasmodium ortholog of PCNA1 had been used as a DNA replication sensor in the recent studies (35353560). *Altogether, it validates PCNA1 as an appropriate S-phase FUCCI probe. *

The first part of the manuscript only deals with first to identify the function and localisation of PCNA1 and then develop FUCCI technology and then go on to study cell cycle. So the focus of the manuscript is not clear. It seems three different results are just assembled together in one manuscript with out clear focus. In order to get clear focus the authors should clear set out the focus as to why they developed FUCCCI and how they decipher either replication, budding, apical or basal complex, centrosome or cytokinesis as well to be used for drug discovery The way it is organised it is not flowing well and confuses the reader who may not be aware of different compartment of Toxoplasma cell or not a molecular parasitologist.

We believe the reviewer has described the logic of our study. Our goal was to dissect the cell cycle. Consequently, we adapted a suitable technology, FUCCI. We described the relevant experiments that allowed us to produce a new molecular tool for an apicomplexan model, and illustrated how we used this tool to better understand the complicated processes of its cell division. Therefore, we organized our study accordingly and included our goal, plans, results, and conclusions that support the success of adopted technology and establishment of the cell cycle organization. We hope this brief explanation can provide some clarification for the reviewer.

Some of the conclusion on the that Replication starts at centromere region is not novel and has been studied previously.

We agree that the centromeric start of DNA replication is not a novel feature, which is stated in the text. This result was shown to demonstrate that Toxoplasma replicates its DNA according to the rules* conserved across eukaryotes. *

The manuscript needs revising by writing precisely eliminating too much literature reference in the result section with clear focus. Some of these references can be elaborated in the introduction and discussion to keep the focus.

We examined the results section, and as much as we wanted to comply with this reviewer, we found no references that could be eliminated or transferred to the introduction. We believe that to aid the reader, some foundational knowledge needs to be presented together with obtained results to support those findings.

• *

Some points with respect to figures: Generally with image panels, arrows don't stand out well

We* have adjusted the images.

*

Fig1: no scale bars and the green arrow do not stand out. So may be to make white.

*The scale bar can be found in the bottom right image, which applies to every image in the panel. We changed the color of the arrows. *

Fig 2E: state the time point in the fig without IAA treatment (-IAA)

The requested information was added to the figure legend.

Fig4: no bell shaped curve

We rephrased the description. The” bell-shape” analogy applies to the temporal dynamics of DNA replication, which starts with a single aggregate, expands to numerous replication foci, and is reduced to a few aggregates at the end of replication. We attempted to quantify aggregates, but their irregular shape makes this task impossible. Our statement is supported by steady-state images and real-time microscopy of the DNA replication included in the manuscript.

Fig 5D: it isn't obvious what the numbers on the right hand side of the graph mean. If it is size, there should be a unit given

We provided an explanation in the figure legend*.

*

Figure 6 - how do they determine that the tachyzoites have progressed through 61% of S phase? Make this clearer here.

*We examined only DNA replicating parasites (S-phase) and determined the fraction of BCC0-positive (39%) and BCC0-negative (61%) tachyzoites. Quantifications can be found in Table S4, in the S-C worksheet. *

• *

Fig7: it a strange way of ordering the figure as FigE is after Fig F hence no logical order. Thank you, we have corrected the order of these panels*. *

Fig 8H is not mentioned in the text

*Thank you, we referenced the wrong panel. Fig. 8H is now included in the text. *

Figure 9 is nice and useful but the arrows could be made proportional of time spent in each cell cycle phase. They're a little off in the conventional cell cycle at the minute

• *These schematics are intended to illustrate the dramatic difference in cell cycle organization rather than to directly describe cell cycle organization, the latter of which can be found in Figure 6.

Some comment on the text in the manuscript: Line 137: describing the expression pattern: the following papers first described the expression pattern of PCNA1 and 2 can be cited in the result. https://doi.org/10.1016/j.molbiopara.2005.03.020 We added the reference.

Line 154: Provide schematic for AID HA cloning and confirmation.

The schematics and PCR confirmations* can be found in the supplemental figure S2.

*

Line 157: Fig 2 after 4 h treatment FACS analysis shows more than 1 and less than 2n genomic content. Does this study have any -IAA treated control for 4h and 7h to compare as what should the standard genomic content to be there at this time point of development. At 4 h of development can the authors provide any statistical analysis with their 3 experiments to prove their point that the replication is actually stalled. Downregulation of TgPCNA1 as shown is western blot is still basal protein left to carry the genomic replication in 7 mins. Can authors also state that TgPCNA 2 which is although non-essential but has no redundant role in the replication machinery.

The -IAA control is indicated as 0h and is shown in blue. The statistical analysis of three independent experiments showing the increase of the S-phase population is included in Table S3. The Fig. 2 WB shows over 99% TgPCNA1 degradation, and the residual >1% would be insufficient to carry out full DNA replication. This residual signal is likely due to PCNA1 remaining in complex, which would resist *proteolysis. Unfortunately, we do not feel comfortable to make the final statement suggested. We believe that the lack of TgPCNA2 complementation with yeast PCNA1 (Guerini et al, 2005) is insufficient to draw the conclusion that TgPCNA2 plays a non-redundant role in Toxoplasma replication machinery. *

Line 178 : typing error "that that

Thank you, this has been corrected*.

*

Line 179: states the role of TgPCNA 1 in DNA1 replication, however line 159 and 160 states the TgPCNA1 deficient can fulfil DNA replication. Can author confirm this contrast in the results. Results trying to illustrate the same fact TgFUCCIs or TgPCNA1ng that TgPCNA1 first aggregates at centromeres and then distributed on many replication forks and disappears late during cytokinesis. The part of the result can be merged.

We apologize for the *confusion. We rephrased our statements and supported them by corresponding references. Although it may seem repetitive, but it was our intention to emphasize a consistent spatial-temporal expression of TgPCNA1-HA and TgPCNA1-NG. *

Line 189: Typing error, should say "such as nucleus", currently as is missing

Thank you, this has *been corrected.

*

Line 346-349: basically explaining the same thing twice.

We apologize for the confusion, the first sentence describes compartments where MORN1 is located. The second sentence describes how MORN1 localization changes during cell cycle progression, information which is used later in our quantitative IFA of cell cycle phases*. *

• *

Line 347 - immunfluorescent should be immunofluorescence

Thank you, this has been corrected*.

*

Line 395-399: does this study has any non-inhibited (-IAA control) at 4h and 7 h. for fig 7C & 7G. Can the authors provide any statistical analysis for the significance with their 3 experiments.

The untreated control (7h mock) is shown as 0h treatment (first bar in each panel). The figure also shows the results of the statistical analysis (t-test, numbers above) that can also be found in Table* S7.

*

Line 415: Why the authors have not used the TgFUUCI sc lines which expresses the TgPCNAng and IMCmch both. This could have helped to understand the real time dynamics of DNA replication and budding initiation (cytokenesis), rather then fixing and staining with TgIMC.

*The recent study by Gubbels lab identified the earliest known budding marker BCC0. Unfortunately, BCC0 is a low abundant factor and cannot be used in FUCCI. IMC3 emerges in the midst of budding when the daughter conoid and polar rings are assembled and thus does not signify either the beginning or the end of cytokinesis. We added IMC3 as a supporting budding marker, while our primary focus remains on the DNA replication marker PCNA1. *

Overall good technology development as FUCCI but the rest of the manuscript is extremely dense and the focus of the study is not clear after technology part. The complexity of the cell cycle is known and hence not much novelty here and extremely descriptive and hard read. Science can be simplified.

The reviewer agrees the apicomplexan cell cycle is highly complex, and the field has worked diligently to piece together what we can about it, which contributes to the density of the manuscript. We hope that the targeted audience will find it thoughtful, and we strove to provide sufficient information for those outside our field. We also respectfully disagree that our study offers little novelty; while it is known how complex the apicomplexan cell cycle is, there is still much to uncover. While overlapping cell cycle phases exist in other eukaryotes, there were no such studies that showed the degree of these overlaps across the entire T. gondii cell cycle. We believe there are valuable insights to be gained from the identification of the composite cell cycle phase, which in turn could help draw attention to other understudied features of the cell cycle in non-conventional eukaryotes*. *

*Reviewer #2 *

1. It is not always clear where apical and basal ends of the parasite are. E.g. in Fig 3F are the two parasites on the right facing down with their apical end? In Fig 4 it is even harder to see. Might be helpful to turn these images with their apical end up to make comparative interpretation of figures easier. In the text it mentions that PCNA1 concludes at the 'proximal' end of the nucleus (or with the nucleus proximal, which is not clear either??). Please define clearly where the proximal site is, as it is not clear in the figures or in the movie (the 'last focus' marker in Fig 4D??). Thank you for the suggestion. We rotated images in Fig. 3 and marked the parasite ends in Fig. 4. We also indicated parasites’ polarity in the movies.

Synchrony of replication cycle. Tight synchronization depends on the retention of the cytoplasmic bridge, as mentioned by the authors. In larger vacuoles, it is very conceivable not all parasites are connected with each other (notably in large cysts with bradyzoites), which could lead to loss of tight synchrony. The results section states "One plausible explanation is that the rosette split shortens the communication path between tachyzoites". This is somewhat cryptic language: does a 'rosette split' imply the rupture of the cytoplasmic bridge? This statement should be clarified. Another factor could be centrosome maturation, with the mother centrosome ready sooner than the daughter, which is a model proposed in schizogony, where the nuclear cycles in a shared cytoplasm are even more asynchronous/independent.

Yes, by ‘rosette split’, we refer to the break of the connection, or a cytoplasmic bridge. The model based on centrosome maturation is interesting, however, it does not explain the synchronization of a vacuole of 16, unless centrosome age resets at that point*. *

Centrosome duplication. This has been documented to occur at the basal side of the nucleus (the whole nucleus rotates for centrosome duplication). The images as depicted in Fig 6 do not seem to indicate this event, possibly because it is not easy to track apical and basal end of the cell (#1 above). Please comment, as this could be an additional spatial cue to the specific stage of the cycle.

This is a very interesting suggestion, thank you. Indeed, the centrosome often duplicates away from the apical end (disconnects from the Golgi), sometimes on the side or the basal end, but quickly rotates back to the apical position to reconnect with co-segregating organelles. Centrosome traveling is an interesting feature, and it is possible that this reorientation back to the apical end signifies budding initiation. We will explore this hypothesis in future studies.

• Specific experimental issues that are easily addressable.

• The term "Apicomplexan" should be spelled with a lower case "apicomplexan", which is not consistently applied throughout the manuscript. Thank you, we have corrected the spelling*. *

* 2. Line 567 the term used in 2008 was "tightly knit" not "closely woven". We wanted to avoid the exact citation and rephrased the title of the review.

*

*Reviewer #3 *

-The authors choose to describe PCNA1 and IMC3 as FUCCI markers. The efficiency of this system in mammalian cells is based on the proof that the markers are regulated through a rapid proteolysis process. However, the data available for these markers point toward a transcriptional regulation of these markers (Toxodb and (1)). In contrast, the authors do not provide any data indicating that these proteins are true FUCCI markers. Consequently, they should not use the term FUCCI throughout the paper unless they prove that the cell cycle expression depends on proteolysis. For example, the authors could express these genes with a promoter that is not cell cycle regulated.

PCNA1 was one of the original FUCCI markers for mammalian cells, later replaced by the more abundant geminin. PCNA1 ubiquitination is well supported across all eukaryotes, and we believe there is much data to support this same turnover mechanism acts to regulate PCNA1 in Toxoplasma. Transcriptional profiles show that TgPCNA1 mRNA is constantly present in cells, never dropping below 80%, making this mRNA is among the most abundant in the cell. It also indicates that proteolysis, rather than halted transcription, controls TgPCNA1 protein levels, since TgPCNA1 protein expression drops to nearly undetectable levels in early G1 and budding (Fig. 1). In addition, TgPCNA1 is highly conserved in structure (Fig. S1) and in function (TgPCNA1 interactome, Fig. 1). The TgPCNA1 Ub sites were detected in global ubiquitome analyses (ToxoDB), supporting the fact that TgPCNA1 protein abundance is regulated by ubiquitin-dependent degradation. Furthermore, PCNA1 as a FUCCI marker in model eukaryotes was not tested for proteolysis because it was unquestionable that PCNA1 is regulated by proteolysis. In addition, Plasmodium ortholog of PCNA1 had been used as a DNA replication sensor in the recent studies (35353560), which validates PCNA1 as an appropriate S-phase FUCCI probe. The modern FUCCI probes are fragments of CDT1 and Geminin mimicking the spatiotemporal expression of the corresponding cell cycle regulators. The transcriptional profile of TgIMC3 is also largely unchanged across the cell cycle, which heavily implies that proteolysis control*s its dynamic protein expression. Therefore, we believe that the term FUCCI applies to TgPCNA1 and TgIMC3. *

-The authors show that the localization of PCNA1 change during the cell cycle and indicate that the PCNA1 aggregates observed are replication forks. They do not provide data supporting this. They should co-localize these aggregates with other markers such as ORC, MCM proteins or DNA polymerase to better characterize these aggregates. There are number of techniques that could be used to localize the origin(s) of replication. Similarly, ExM should be used to characterize the colocalization between PCNA1 aggregates and the centromeres. As such, the images provided are of poor quality and do not support the author conclusions. The few PCNA1 aggregates toward the end of the S phase are also not characterized. Are they telomeres?

Although this is an important point, such detailed analyses of the DNA replication machinery is out of the scope of the current study and will be examined in a follow-up study. Data that suggest the aggregates correspond to replication forks include proteomics analyses of chromatin-bound PCNA1 that identified replisome components such as the MCM, high conservation of TgPCNA1 sequence and structure (Fig. S1), and its conserved interactions (Fig. 1). Recent studies used Plasmodium ortholog of PCNA1 to trace DNA replication dynamics during schizogony (35353560), *Therefore, we doubt that TgPCNA1 would perform functions outside of its role as a DNA replication factor, which has been extensively studied in other eukaryotes. *

• The authors characterized the proteins associated with PCNA1. All the proteins found to potentially interact are chromatin-bound and are not naturally found in other localization (2). It is unclear why the authors insist on the fact that there are two PCNA1 complexes (one chromatin-bound and one non-chromatin bound). More concerning is the lack of verification of this dataset through reciprocal IP for example.

The PCNA IP was used to confirm its conserved function as a DNA replication factor; similarly to what was observed in other eukaryotes, we detected PCNA in both a chromatin-bound and unbound state. PCNA1 is produced in late G1 (diffuse nuclear stain) but is engaged in the replisome only upon DNA replication initiation (aggregated form). Rather than characterize the function of the highly conserved PCNA1, our primary goal was to determine the Toxoplasma cell cycle organization, which explains our choice of the experimental design.

• Quantification of some of the phenotypes is lacking. For example, the DNA content analysis are shown but the change in number are not. Similarly, there is no quantification of the PCNA1 mutant phenotypes observed by ExM. Quantification of the bell shape observed by video-microscopy in figure 4 should also be provided.

The quantifications supporting the main claims of our study are included in the five supplemental Tables S3-S8, including DNA content and microscopy analysis of the phenotype. *The U-ExM microscopy has been solely used to visualize details of the phenotype. *

• The PCNA1 mutant phenotypes are not sufficiently explored by ExM. What happen to the mitotic spindle? What happens to kinetochore (CenH3 is a centromere protein and does not represent kinetochores)? Many markers for these structures have been described, see (3).

The primary goal of our study was to examine and map out the organization of the tachyzoite cell cycle. PCNA1 deficiency was used to demonstrate that Toxoplasma PCNA1 is a conserv*ed DNA replication factor and can be used as an S-phase marker in FUCCI. Thus, we focused on the mutant-induced changes in the dynamics of DNA replication (DNA content) and arrest prior to mitosis (unresolved centrocone). *

• TgPCNA1NG strain has a number of concerns. The localization to the daughter cells conoids seems artificial since not observed in the HA-AID mutant and the expression pattern seems different as well than the previous mutant suggesting the mNG tag is affecting the localization and expression dynamics. Did the authors explore other fluorescent proteins to verify that these discrepancies where not due to this tag ?

The conoidal PCNA1 accumulation was detected only with NeonGreen-tagged PCNA1. We also built and examined tdTomato- and mCherry-tagged versions and detected minor accumulations in the conoid of tdTomato-tagged PCNA1, but not with the mCherry-tagged variant. We believe these aggregations could be attributed to the partially degraded PCNA1-NeonGreen having an affinity to conoidal proteins, thus producing this unexpected signal. Although not included in the manuscript, our quantifications, based on both PCNA1-HA and PCNA1-NeonGreen, showed similar cell cycle organization (G1, S and budding phases) of tachyzoites. The FUCCI probe is an indicator of the cell cycle phase. It does not have to be a functional protein. As we mentioned before, many FUCCI probes are fragments of the factors that mimic the spatiotemporal expression of the corresponding cell cycle regulators.

-Cytokinesis seems to be only defined by the presence of IMC3. The marker appears early during the budding process and it is not normally considered as a cytokinesis marker. The author should the text to reflect this.

We agree with the reviewer that IMC3 is not a true budding marker, which is why we used BCC0 in our quantifications. IMC3 is proven to broadly define the mid-budding stage, making it a convenient supplemental marker. We are currently exploring and testing alternative and additional FUCCI markers. It is not an easy task, since these markers are required to have high expression levels and to be localized into large organelles. For instance, BCC0 was eliminated due to low abundance.

• Throughout the manuscript, the authors seems to ignore an essential characteristic of the tachyzoite cell cycle: the nuclear cycle and the budding cycle are independently regulated. It is therefore normal they overlap as it has been shown by the authors themselves in previous studies. This should be better described and discussed in the paper to understand the peculiarities of the parasite cell cycle.

We apologize for the confusion, but the tachyzoite cell cycle does not contain a nuclear cycle, it consists of a single budding cycle. The nuclear cycle is only a feature in multinuclear cell cycles such as schizogony and endopolygeny. This is the main reason why the overlap between phases is so surprising.

• l196: "The surface of the growing buds": could the authors rephrase?

We rephrased the statement.

-L217: proximal end of the nucleus rather than "parasite ".

*We clarified the statement. It is, in fact, the shift of the nucleus to the proximal end of the parasite.

*

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

This is a manuscript from Batra et al. entitled "A FUCCI sensor reveals complex cell cycle organization of Toxoplasma endodyogeny ". It describes the characterization of PCNA1 as cell cycle marker in the parasite Toxoplasma gondii. Tachyzoite endodyogeny is a simplified division process that is crucial for the proliferation of the parasite. Some studies have used fluorescent markers to describe the segregation of organelles and the nuclear division during endodyogeny but the production of more tools to dissect the cell cycle and better characterize mutants is timely. Most of the experiments are based on characterization of PCNA1 mutant and the use of a strain expressing a PCNA1-mNG construct. Unfortunately, there are a number of concerns in this study that need to be addressed.

Major concerns:

• The authors choose to describe PCNA1 and IMC3 as FUCCI markers. The efficiency of this system in mammalian cells is based on the proof that the markers are regulated through a rapid proteolysis process. However, the data available for these markers point toward a transcriptional regulation of these markers (Toxodb and (1)). In contrast, the authors do not provide any data indicating that these proteins are true FUCCI markers. Consequently, they should not use the term FUCCI throughout the paper unless they prove that the cell cycle expression depends on proteolysis. For example, the authors could express these genes with a promoter that is not cell cycle regulated.
• The authors show that the localization of PCNA1 change during the cell cycle and indicate that the PCNA1 aggregates observed are replication forks. They do not provide data supporting this. They should co-localize these aggregates with other markers such as ORC, MCM proteins or DNA polymerase to better characterize these aggregates. There are number of techniques that could be used to localize the origin(s) of replication. Similarly, ExM should be used to characterize the colocalization between PCNA1 aggregates and the centromeres. As such, the images provided are of poor quality and do not support the author conclusions. The few PCNA1 aggregates toward the end of the S phase are also not characterized. Are they telomeres?
• The authors characterized the proteins associated with PCNA1. All the proteins found to potentially interact are chromatin-bound and are not naturally found in other localization (2). It is unclear why the authors insist on the fact that there are two PCNA1 complexes (one chromatin-bound and one non-chromatin bound). More concerning is the lack of verification of this dataset through reciprocal IP for example.
• Quantification of some of the phenotypes is lacking. For example, the DNA content analysis are shown but the change in number are not. Similarly, there is no quantification of the PCNA1 mutant phenotypes observed by ExM. Quantification of the bell shape observed by video-microscopy in figure 4 should also be provided.
• The PCNA1 mutant phenotypes are not sufficiently explored by ExM. What happen to the mitotic spindle? What happens to kinetochore (CenH3 is a centromere protein and does not represent kinetochores)? Many markers for these structures have been described, see (3).
• TgPCNA1NG strain has a number of concerns. The localization to the daughter cells conoids seems artificial since not observed in the HA-AID mutant and the expression pattern seems different as well than the previous mutant suggesting the mNG tag is affecting the localization and expression dynamics. Did the authors explore other fluorescent proteins to verify that these discrepancies where not due to this tag ? -Cytokinesis seems to be only defined by the presence of IMC3. The marker appears early during the budding process and it is not normally considered as a cytokinesis marker. The author should the text to reflect this.
• Throughout the manuscript, the authors seems to ignore an essential characteristic of the tachyzoite cell cycle: the nuclear cycle and the budding cycle are independently regulated. It is therefore normal they overlap as it has been shown by the authors themselves in previous studies. This should be better described and discussed in the paper to understand the peculiarities of the parasite cell cycle.

Minor

• l196: "The surface of the growing buds": could the authors rephrase?

• L217: proximal end of the nucleus rather than "parasite ".

• Behnke,M.S., Wootton,J.C., Lehmann,M.M., Radke,J.B., Lucas,O., Nawas,J., Sibley,L.D. and White,M.W. (2010) Coordinated progression through two subtranscriptomes underlies the tachyzoite cycle of Toxoplasma gondii. PloS One, 5, e12354.

• Barylyuk,K., Koreny,L., Ke,H., Butterworth,S., Crook,O.M., Lassadi,I., Gupta,V., Tromer,E., Mourier,T., Stevens,T.J., et al. (2020) A Comprehensive Subcellular Atlas of the Toxoplasma Proteome via hyperLOPIT Provides Spatial Context for Protein Functions. Cell Host Microbe, 28, 752-766.e9.
• L,B., N,D.S.P., Ec,T., D,S.-F. and M,B. (2022) Composition and organization of kinetochores show plasticity in apicomplexan chromosome segregation. J. Cell Biol., 221.

Significance

This study provides the characterization of a new cell cycle marker to decipher the tachyzoite cell cycle of the apicomplexan parasite Toxoplasma gondii. A better understanding of the cell cycle is needed to prevent the proliferation of this parasite. This study builds on previous works characterizing organellar segregation in T. gondii. It provides data about the overlap of each cell cycle phase and the synchronicity of the cell cycle in a single vacuole. However, it is limited by the use of a single marker and more data are needed to support the conclusions of this study. This study can be of interest to a broad audience.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

• Are the key conclusions convincing?

The data support the new model put forward in the final figure: a composite cell cycle phase

There are couple of points that need attention:

1. It is not always clear where apical and basal ends of the parasite are. E.g. in Fig 3F are the two parasites on the right facing down with their apical end? In Fig 4 it is even harder to see. Might be helpful to turn these images with their apical end up to make comparative interpretation of figures easier. In the text it mentions that PCNA1 concludes at the 'proximal' end of the nucleus (or with the nucleus proximal, which is not clear either??). Please define clearly where the proximal site is, as it is not clear in the figures or in the movie (the 'last focus' marker in Fig 4D??).
2. Synchrony of replication cycle. Tight synchronization depends on the retention of the cytoplasmic bridge, as mentioned by the authors. In larger vacuoles, it is very conceivable not all parasites are connected with each other (notably in large cysts with bradyzoites), which could lead to loss of tight synchrony. The results section states "One plausible explanation is that the rosette split shortens the communication path between tachyzoites". This is somewhat cryptic language: does a 'rosette split' imply the rupture of the cytoplasmic bridge? This statement should be clarified. Another factor could be centrosome maturation, with the mother centrosome ready sooner than the daughter, which is a model proposed in schizogony, where the nuclear cycles in a shared cytoplasm are even more asynchronous/independent.
3. Centrosome duplication. This has been documented to occur at the basal side of the nucleus (the whole nucleus rotates for centrosome duplication). The images as depicted in Fig 6 do not seem to indicate this event, possibly because it is not easy to track apical and basal end of the cell (#1 above). Please comment, as this could be an additional spatial cue to the specific stage of the cycle.
4. Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

The authors are on the conservative end of interpretations and clearly outline the limitations of their approaches and observations, while discussing alternative interpretations. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

No, the presented experiments and data are very complete - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

n/a - Are the data and the methods presented in such a way that they can be reproduced?

yes - Are the experiments adequately replicated and statistical analysis adequate?

yes

Minor comments:

• Specific experimental issues that are easily addressable.
• The term "Apicomplexan" should be spelled with a lower case "apicomplexan", which is not consistently applied throughout the manuscript.
• Line 567 the term used in 2008 was "tightly knit" not "closely woven".
• Are prior studies referenced appropriately?

Yes - Are the text and figures clear and accurate?

Yes, exceptional - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

See major point #1 above.

Referees cross-commenting

Comment to Rev 1: https://doi.org/10.1128/msphere.00160-22. reports on use of FUCCI in the host cell, not in the parasite itself. This comment therefore does not apply.

Comment to Rev 3: the technicality on FUCCI acting on the protein level. That is a legit concern that needs attention, and could be fixed by avoiding the term FUCCI, or putting the term in the exact context.

Looks like a shared general concern is that it is not always clear where apical and basal ends are in the presented data. This should be addressed in revision.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

The presented manuscript reports on a technical innovation in Apicomplexa: establishing a FUCCI system. However they did not stop there and added additional markers to unravel the timing and nature of S/M/G2/C overlaps that illuminated previously underappreciated or unknow details. The tools assembled here will be of great value for understanding not only T. gondii endodyogeny checkpoints and sequence of events, but also paves the way for similar studies in more complex apicomplexan cell division modes, like schizogony and endopolygeny. - Place the work in the context of the existing literature (provide references, where appropriate).

The authors very appropriately provide the wider context and completely cover where the field stands. E.g. this protein microscopy-based work fills in the fine grain details where recent advances in transcriptional profiles by single cell experiments cannot provide resolution. The authors do also an outstanding job in providing the background on the general understanding of molecular players, structures and process controls across eukaryotes that pinpoint where the Apicomplexa are different. - State what audience might be interested in and influenced by the reported findings.

The audience comprises a wide array of people with interests in cell cycle regulation, cell cycle checkpoints, DNA replication, nuclear organization across biological systems, and Apicomplexa in particular - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Toxoplasma gondii cell biology - sufficient expertise across the board

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The manuscript by Batra et al have tried to dissect out two aspect to understand the complex cell cycle of Toxoplasma endodyogeny. One is to development of Fluorescent Ubiquitination-based Cell Cycle Indicator (FUCCI) technology for Toxoplasma gondii and then to use that for understanding the complex cell cycle. The authors have created ToxoFUCCIs and ToxoFUCCIsc probes using TgPCNA1 tagged with NeonGreen and TgIMC3 tagged with mCherry and used to dissect the different phases of cell cycle like S, G2, G1 and cytokinesis. Overall technology development is good though as they claim that they are first is not true as it has been used earlier by https://doi.org/10.1128/msphere.00160-22. Hence may be that they have used to decipher the cell cycle.

The manuscript is extremely dense and at times very difficult to read and to be clear if they are focussing on the technology or cell cycle. The technology may be a better part of manuscript but the dissection of cell cycle is not very novel and at times very confusing to follow. Many of these aspects has been dissected out previously from their own group and many group in Toxoplasma and Plasmodium and it is quite known about that the cell cycle in Apicomplexa is very complex. Another aspect that most FUCCI use Geminin and CDT1 factors and since Geminin is not present it would have been better to validate that with CDT1 that is present in Apicomplexa and may be more relevant than PCNA1. The first part of the manuscript only deals with first to identify the function and localisation of PCNA1 and then develop FUCCI technology and then go on to study cell cycle. So the focus of the manuscript is not clear. It seems three different results are just assembled together in one manuscript with out clear focus. Some of the conclusion on the that Replication starts at centromere region is not novel and has been studied previously.

In order to get clear focus the authors should clear set out the focus as to why they developed FUCCCI and how they decipher either replication, budding, apical or basal complex, centrosome or cytokinesisas well to be used for drug discovery The way it is organised it is not flowing well and confuses the reader who may not be aware of different compartment of Toxoplasma cell or not a molecular parasitologist.<br /> The manuscript needs revising by writing precisely eliminating too much literature reference in the result section with clear focus. Some of these references can be elaborated in the introduction and discussion to keep the focus.

Some points with respect to figures:

Generally with image panels, arrows don't stand out well

Fig1: no scale bars and the green arrow do not stand out. So may be to make white.

Fig 2E: state the time point in the fig without IAA treatment (-IAA)

Fig4: no bell shaped curve

Fig 5D: it isn't obvious what the numbers on the right hand side of the graph mean. If it is size, there should be a unit given

Figure 6 - how do they determine that the tachyzoites have progressed through 61% of S phase? Make this clearer here.

Fig7: it a strange way of ordering the figure as FigE is after Fig F hence no logical order.

Fig 8H is not mentioned in the text

Figure 9 is nice and useful but the arrows could be made proportional of time spent in each cell cycle phase. They're a little off in the conventional cell cycle at the minute

Some comment on the text in the manuscript:

Line 137: describing the expression pattern: the following papers first described the expression pattern of PCNA1 and 2 can be cited in the result. https://doi.org/10.1016/j.molbiopara.2005.03.020

Line 154: Provide schematic for AID HA cloning and confirmation.

Line 157: Fig 2 after 4 h treatment FACS analysis shows more than 1 and less than 2n genomic content. Does this study have any -IAA treated control for 4h and 7h to compare as what should the standard genomic content to be there at this time point of development. At 4 h of development can the authors provide any statistical analysis with their 3 experiments to prove their point that the replication is actually stalled. Downregulation of TgPCNA1 as shown is western blot is still basal protein left to carry the genomic replication in 7 mins. Can authors also state that TgPCNA 2 which is although non-essential but has no redundant role in the replication machinery.

Line 178 : typing error "that that

Line 179: states the role of TgPCNA 1 in DNA1 replication, however line 159 and 160 states the TgPCNA1 deficient can fulfil DNA replication. Can author confirm this contrast in the results. Results trying to illustrate the same fact TgFUCCIs or TgPCNA1ng that TgPCNA1 first aggregates at centromeres and then distributed on many replication forks and disappears late during cytokinesis. The part of the result can be merged.

Line 189: Typing error, should say "such as nucleus", currently as is missing

Line 346-349: basically explaining the same thing twice.

Line 347 - immunfluorescent should be immunofluorescence

Line 395-399: does this study has any non-inhibited (-IAA control) at 4h and 7 h. for fig 7C & 7G. Can the authors provide any statistical analysis for the significance with their 3 experiments.

Line 415: Why the authors have not used the TgFUUCI sc lines which expresses the TgPCNAng and IMCmch both. This could have helped to understand the real time dynamics of DNA replication and budding initiation (cytokenesis), rather then fixing and staining with TgIMC.

Overall good technology development as FUCCI but the rest of the manuscript is extremely dense and the focus of the study is not clear after technology part. The complexity of the cell cycle is known and hence not much novelty here and extremely descriptive and hard read. Science can be simplified.

Significance

The development of FUCCI technology is significant part of the manuscript and to understand cellcycle may be they could have used CDT1 rather than PCNA as there is another PCNA 2 that also exist. The authors have given some convincing result for some aspect of cell cycle of which most are known and only it is quite incremental.at some part. The technology may contribute to the methodology development in Apicomplexa.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a response at this time

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

This study by Mordier and colleagues represents an in depth analysis to clarify the evolutionary history and processes of the rapidly evolving Schlafen gene family with a strong focus on primates and rodents.

The study is of high quality in my opinion, though I do have some minor comments:

1. Fig 2 and Fig 4B present inferred phylogenetic trees of schalfens in primates and rodents - these trees appear to be unrooted or rooted on a single species rather than an outgroup/gene. I suggest that the authors consider whether an outgroup gene could be included or if an outgroup free approach could be used to estimate the position of the root. This is important because the use of an unrooted tree to make inferences on gene family evolution has important implications - for example, there are no clades in an unrooted tree (Wilkinson et al 2007, Trends Ecol Evol).
2. Schlafen proteins beyond mammals are referred to as SLFN11, it is not clear why this is the case because they seem to be co-orthologous to all mammal schalfen groups (except SLFNL1) based on supplementary figure S2. In this context, perhaps this image should form part of the main text?
3. For blast searches parameters should be included - what cutoffs were implied for similarity searches etc. Related to this on line 120-121 homology is described as 'significant'. Homology refers to an evolutionary relationship, sequence similarity may be significant or not based on the search performed but homology is qualitative and simply detectable or not.
4. The first results section describes the results of phylogenetic analyses, however this section relies heavily on what might better be considered interpretation of these analyses, this is great and should be included but I suggest that the branching patterns in the trees and bootstrap values supporting relationships between genes are also reported in the text to link interpretations to actual results.
5. Bustos 2009 included viral genes belonging to the family in their analyses and I think it may be pertinent to do so here also to determine if the results are consistent or not.
6. Was a rate heterogeneity (e.g. gamma rates / +G) parameter considered in phylogenetic analyses or model testing, it is not reported here and very rare for this not to improve model fit and phylogenetic accuracy.
7. The authors state that all data are available in public databases, but this is not the case for the results they generated. Making various file types produced in this study would be good - e.g. alignments, phylogenetic tree files, structures, etc.

Significance

This study is an important step forward in clarifying our understanding of schalfen evolution. I think the manuscript will be of interest to a number of research areas, including gene family evolution because of its focus on an unusually rapidly evolving gene cluster and to those working on the schalfen gene families functional importance in development and immunity. The results may also draw interest from those interested in the confluence of protein structure, function, and evolution. My expertise In the context of this study is in the phylogenetics and evolution of rapidly evolving gene families.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In the current manuscript, Mordier et al. combine bioinformatic searches, synteny, and phylogenetic analysis to reconstruct the duplicative history of the Schlafen Genes in rodents and primates and then use molecular evolution analyses in combination with structural modeling to make inferences regarding the role of natural selection in the evolution of this gene family. The study represents an update on Bustos et al. (2009), who had already presented evidence that Positive Darwinian selection was likely a factor in the diversification of these genes in mammals. In this context, the contribution of this paper is the identification of sites that are candidates to be evolving under natural selection, and the structural exploration of the location of these sites in the proteins. CODEML strength lies in the detection of signatures of positive selection at the codon level, but it is not that accurate when it comes to pinpointing the actual sites that might be under selection. Hence, without experimental data, these inferences remain speculative. The manuscript is well-written and represents an update on the evolution of this gene family.

Major Issues

The rationale for the choice of species included in the analyses is never presented, and some of it is hard to understand. Why do authors exclude the platypus but include non-mammalian lobe-finned vertebrates is not clear. If they are going to discuss the evolution of these genes outside mammals, the authors need to survey a much wider array of genomes. Even within mammals, there is little discussion on why some species were included and others not. I think that focusing the study on rodents and primates is OK, but I also think that providing a strong justification of the selection of species to include in the study and a tree that justifies splitting the focus on rodents and primates would also be important.

In the trees in Figures 2 and 4, several genes considered as orthologs are not in monophyletic groups. These pattern aligns well with the birth-and-death model of gene family evolution, and has implications for their molecular evolution analyses. The authors need to address this issue explicitly. I would use topology tests to evaluate whether these deviations from the expected topology are significant. In addition, the relevant tests to report here are M8 vs M7 and M8 vs M8a. The M0 vs M1a comparison does not provide evidence for positive Darwinian selection. If the M8 vs M7 and M8 vs M8a tests are not significant, the inferences about sites evolving with dN/dS>1 are not really valid.

CODEML can implements models that are designed to test patterns of gene family evolution, contrasting pre and post duplication branches, which I think would be of value in this family.

Some analyses are described very succinctly, which would make replication challenging.

Minor Issues

Could 2R be responsible for the emergence of SLFN and SLFNL1?

There are several minor issues authors should fix in a revised manuscript. In general, because results are presented before the materials and methods, I think it is easier for readers to have some of the information in the results section.

They need to be consistent in using italics for species names as well as for capitalization.

In the Alignment and maximum-likelihood phylogenies section the authors indicate that they used either Muscle or Mafft for the alignments. What was the rationale for picking one alignment over the other for a given gene? In this section, they also indicate the selected a best-fitting model of substitution using SMS, but then indicate that they used JTT for protein alignments and HKY for nucleotide alignments.

How did the authors ensure that nucleotide alignments remained in frame?

Significance

I think this is a significant contribution to our understanding of the evolution of the Schlafen gene family. There are two key contributions here: the demonstration that gene conversion is a factor obscuring relationships among genes in this gene family, and the mapping of amino acids inferred be evolving under positive selection to structurally important residues of the proteins. These residues should be of interest for functional assays that evaluate the functional role of these proteins.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Mordier et al. used in-depth phylogenomic methods to analyze the evolution of the mammalian Schlafen gene family. They identified a novel orphan Schlafen-related gene that arose in jawed vertebrates, and they assigned orthology between Schlafen cluster paralogs. This will allow for further accurate selection studies. Throughout the entire manuscript, the authors use nomenclature predating structural and biochemical studies. The nomenclature is purely based on sequence similarities, which are sometimes very weak and not convincing, and not based on the known function of the protein. In my opinion, this causes confusion and does not help scientists in the field. Especially in Figure 3, I wouldn't call it RNAse E (AlbA); instead, tRNA recognition site,endoribonuclease domain, SLFN core domain are the correct domain designations. Since SLFN11 is not a GTPase, why do the authors name the domain GTPase domain? Actually, the SWADL domain comprises a SWAVDL instead of a SWADL sequence motif. Hence, I would name the domain SWAVDL domain instead of SWADL domain, which is, in my opinion, misleading and was wrongly chosen in initial publications.

In e.g. Figure 3 SLFN11 structure it would be better if the authors illustrated the important residues concerning the known RNase active site and ssDNA binding site. Further, a close-up of the SLFN11 interface with labeled amino acids involved in the interaction and highlighting the residues undergoing positive selection would help understand the evolutionary adaptation.

Although, according to Metzner et al., the SLFN11 dimer is built up by two interfaces (I and II), where Interface I is situated in the C-terminal helicase domain and Interface II in the N-terminal SLFN11 core domain. It would be helpful for the reader if the authors stuck to this already introduced and widely accepted nomenclature in the field.

In addition to the antiviral function, SLFN11 expression levels have been reported to show a strong positive correlation with the sensitivity of tumor cells to DNA damaging agents (DDAs). Hence, SLFN11 can serve as a biomarker to predict the response to, e.g., platinum-based drugs. It was revealed that SLFN11 exerts its function by direct recruitment to sites of DNA damage and stalled replication forks in response to replication stress induced by DDAs. Could the authors include this different molecular function of SLFN11 in their discussion of SLFN11s evolution and positive selection?

Even though it seems unclear from the genetic and evolutionary aspect (Figure 4), mouse Slfn8 and Slfn9 complement human cells lacking SLFN11 during the replication stress response and seem to resemble the function of SLFN11 (Alvi et al. 2023). The authors of this study claim that Slfn8/9 genes may share an orthologous function with SLFN11. Could the authors comment on that discrepancy?

Significance

In general, the work is well conducted and provides valuable new insights in an important and growing field of research. However, there are some limitations to the study including the disregard of known protein function (e.g. SLFN11) and the usage of a purely sequence similarity based nomenclature.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

This is an interesting manuscript from two groups of experts in Notch signaling biology with complementary expertise in Drosophila genetics (Klein) and in biophysical studies of the Notch pathway (Sprinzak). The paper provides a cutting-edge structure-function dissection of the E3 ubiquitin ligase Neuralized and its mammalian homologs, Neurl1a and Neurl1a. The work is particularly relevant since the functions of mammalian Neurl1a and Neurl1b have been questioned, and more subtle altogether than those of fly Neuralized (as summarized by the authors in Fig. 1C). This is in part due to the dominant effects of the E3 ubiquitin ligase Mindbomb1 (Mib1) in Notch ligand-expressing cells from mammalian systems. The authors use careful structure-function work in fly development (mostly wing imaginal discs) and in mammalian cell culture systems, including a clever approach to study the function of mammalian Neurl1a and Neurl1b and mammalian/fly Notch ligand hybrids in Drosophila to draw new conclusions about the function of Neurl1a/b, showing that they can function as activators of Notch signaling mediated by the Notch ligands Dll1 and Jag1, and not by Dll4 and Jag2, tracing these differential effects to the recognition of a short NXXN consensus sequence in the N-terminal region of the ligand's intracellular domain.

__response: __We thank the reviewer for highlighting the novelty of our findings and experimental approach.

Specific questions: -The current title of the manuscript is not very information-rich and would not allow a reader to gather key information about the findings without reading at least the abstract. Could this be improved? For example, by referring to differential activation of individual Notch ligands, or some other more direct description of the key findings?

__Response: __We appreciate the reviewer's suggestion; however, we believe that the general nature of the title is appropriate in this case.

-The authors design most key experiments documenting agonistic effects of Neurl1a/1b in a Mib1-deficient background, both in flies and in cell culture systems. This is understandable experimentally to isolate Neurl1a/b's effects in these experimental systems. However, this leaves open questions as to the prevailing effects of Neurl1a/b in cells that also express Mib1 (which the authors comment on in the discussion based on past findings, including some suggesting that Neurl1a/1b can function as Notch inhibitors through a ligand ubiquitination mechanism that may differ from their activating function).

Do the authors actually have data that could shed light on this discussion? For example, have they performed cell coculture assays in which Neurl1a or Neurl1b is co-expressed with a Notch ligand, but in the presence of Mib1? This condition seems to be systematically omitted from all the coculture experiments that are presented. It would be interesting to evaluate the net effect of Neurl1a/Neurl1b expression in a Mib1-sufficient system as well.

Response: We have systematically removed MIB1 in our experiments because it activates all ligands, making its removal necessary to show the differential activity of Neurls. The question regarding competition between Mib1 and Neurls, as highlighted by the reviewer, is indeed intriguing. However, systematically investigating this competition would require varying the relative levels of the two proteins in a controlled manner, which is beyond the scope of this manuscript.

That said, we will perform the competition experiments suggested by the reviewers (co-expressing ligands with both Neurl1 and Mib1) and test their activity as controls. While these experiments may provide some insight into the competition, they will not comprehensively address the entire topic.

-The paper suggests important predictions about mammalian functions of Neurl1a/1b, including the neurological effects that have been reported, in double-deficient mice, namely that that there are cells that only express Neurl1a/1b and not Mib1 and do rely on Dll1 and Jag1 for signaling. Could the authors at least comment on this prediction? Are there are any single cell atlases where candidate cells like that can be identified? Or would the authors predict that Neurl1a/1b could actually function as Notch agonist even in cells expressing Mib1? (see also previous comment)

Response: This is an interesting suggestion. We will try to find if we can identify any specific expression patterns of E3 ubiquitin ligases across different tissues.

-Some minor typos: line 305 should likely read "flies homozygous for (...)". Line 408, "for providing" repeated twice.

Response: We thank the reviewer for pointing out this typo.

Reviewer #1 (Significance (Required)):

Thank you for the opportunity to review this lovely collaborative paper. As indicated in my comments to the authors, the findings provide novel structure-function information about an understudied aspect of Notch signaling and clarify conflicting past data about the mammalian homologs of fly Neuralized. The approach is elegant and multidisciplinary, notably in regards to the combination of cell co-culture systems and Drosophila as a platform to study mammalian Neuralized proteins and hybrid Notch ligand molecules. The findings will be interesting to the field and will generate discussion. I would suggest that some additional information would be a plus to substantiate predictions about mammalian functions of Neurl1a/b, and also to clarify its effects in the presence or absence of concomitant Mib1 expression.

We thank the reviewer for their positive evaluation of our work and for suggesting potential future direction regarding the concomitant expression of Mib1 and Neurls proteins.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary

The manuscript describes an analysis of specificity of functional interactions between mammalian Neuralized proteins and different human ligands for Notch. To investigate this, the authors take the approach of constructing hybrid proteins that contain the intracellular domain of the human ligands and the extracellular domain of the Drosophila Delta or Serrate, and investigate their activity in vivo, in the Drosophila wing disc. The latter is a well-established model tissue for assessing Notch ligand activity. As a second assay they express mammalian neutralized constructs in human cells for luciferase-based Notch signal reporter assays. The experiments are well presented and described and make a strong case for the conclusions that both Neurl1 and 2 can activate Notch signalling by Dll1 and Jag1 but not Dll4 and Jag2. Use of different mutant intracellular domains is used to show the importance of the NXXN motif, which in Drosophila is required for Neuralized interaction with Delta and Serrate. The use of missense mutations and in particular the reactivation of the cryptic NXXD site in Dll4 by substitution to N is convincing for establishing the importance of the motif. There is also colocalization data to support the conclusion that there is likely to be NXXN-dependent complex formation between the ligand and Neuralized proteins. This latter conclusion would be made firmer fi there were pull down data to support it, although to be fair it is most unlikely that another explanation, other than complex formation could account for the observation of both colocalization and ligand activation.

__Response: __We appreciate the reviewer's positive assessment of our manuscript and their support for the conclusions drawn from our experiments. We intend to conduct the suggested co-IP experiments with our cell culture assays to further supplement our current data.

__ Major comments__ The main limitation of the work is that it is mostly based on overexpression of constructs to activate ectopic expression rather than gene editing endogenous genes. It would be helpful if the authors could comment on the limitations of the work in discussion.

Two points of data included in the work are important in mitigating this limitation. Firstly, the experiments in the wing disc and cell culture are taking place in a mindbomb mutant background and the activation is observed is therefore a rescue of activity that has been lost.

Secondly, and importantly, the final experiment makes use of a Dl mutant Drosophila line which shows embryo lethality when homozygous, with the characteristic neurogenic phenotype. Rescue of lethality can be brought about by knock-in experiments which restore Dl function and this is also true for the ligand hybrid constructs that introduce mammalian ligand intracellular domains only when they include the NXXN motif This indicates the importance of the motif in normal development- Overall, the data presented in the paper is convincing as regards the conclusions made.

__Response: __We thank the reviewer for their very positive evaluation and his constructive suggestions, which have helped to improve the manuscript. In line with these suggestions, we will include additional data analyzing the bristle SOP selection, a process dependent on Neur. Our Results show that homozygosity of the DlattP-Dl-DLL1 allele, but not the DlattP-Dl-DLL4 allele, leads to correct Notch mediated selection. This finding provides further evidence that Neur requires the NxxN motif in the ICD of a ligand to activate DSL ligands. Notably, we previously showed that this selection relies on the NxxN motif of Dl (Troost et al., 2023). We will further emphasize in the discussion the ability of Dl-DLL4 hybrid ligands, containing a reconstructed NxxN motif, to rescue the neurogenic phenotype of Dl mutants.

Minor points In figure 1 the legend for D says that cryptic sites are substitutions of N for E or Q, but the figure and main text indicate that the substitutions are N to E or D.

Response: We thank the reviewer for pointing this out. We will correct this mistake.

In the remain figures it would be helpful to include in the figure legends and indications of the numbers of wing discs, embryos for which the images shown are representative of.

__Response: __We will quantify the experiments conducted in the wing imaginal discs of Drosophila by measuring the wing field size along the dorsal-ventral axis relative to the anterior-posterior axis. Statistical analysis will be performed to demonstrate statistical significance across n=5 experiments for each sample.

In Fg 3 The activation of Notch, by neural1 and Dl-Jag1 in B'" is stronger in the ventral side of the disc than the dorsal whereas, although activation of the same ligand by Neurl2 in C'" is weaker the majority of the ectopic wingless expression is on the dorsal compartment. Is there any reason for the switch in preference between the two neutralized proteins? Overgrowth of the wing disc seems to be similar on both sides and so am wondering if the picture is representative of the ectopic wingless distribution in this case.

Response: As discussed above we will perform quantification and statistical analysis across multiple experiments to confirm that our images are truly representative.

Reviewer #2 (Significance (Required)):

Significance

Previous work on double genetic knockouts of the two mouse Neuralized genes cast doubt as to whether Neuralized proteins play a role in Notch signal activation in mammals, unlike in Drosophila. There is, however, some genetic indications that spatial memory requires both Notch and neutralized proteins and may represent a specialised function limited to the Neuralized interaction. There are likely to be more subtle contexts waiting to be uncovered. The work is therefore showing important proof of principle for establishing the functionality of the mammalian Neurl proteins and highlights new findings indicting specialisation of the different ligands for interactions with Notch components. Elucidation of such specialisations will help understand why the diversity of different homologues of Notch and ligand have evolved and are maintained in the vertebrate genome compared to the single Notch and two ligands in Drosophila. Since Notch and it misregulation are widely involved in development, health and disease and there is much interest in developing therapeutic interactions that alter Notch activity then the work is likely of broad interest.

We thank the reviewer for the very positive evaluation and his useful suggestions which were helpful in improving the manuscript.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

**Summary**

Notch signalling is one of the major evolutionarily conserved signalling pathways involved in numerous developmental, physiological and pathological processes. Activation of the Notch receptor first requires ubiquitination of its ligands (collectively temed DSL), leading to a 'pulling force" that, upon ligand-receptor engagement, exposes Notch to intramembrane proteolysis leading to the nuclear translocation of the receptor's intracellular domain and activation of target genes with its DNA-binding co-factors.

While both Neuralized (Neurl) and Mind bomb are the E3 ubiquitin ligases for Notch ligands required for Drosphila development, in mammals, the Neur homologues Neur1 (officially Neurl1) and Neur2 (officially Neurl1B) are dispensable for development since double Neur1/2 knock-out mice have no developmental phenotype (but both Neur homologues are involved the the memory-related functions of Notch pathway in adulthood). Rather, just one of the two mammalian Mind bomb homologues, Mib1, functions as the chief E3 ligase for Notch ligands during mammalian development as evidenced by its Notch-related knockout phenotype.

Therefore, it has not been fully established whether and how the NEUR proteins regulate the mammalian Notch ligands. To clarify this issue, the authors assessed the capability of Drosophila Neur and mammalian NEUR1 and 2 proteins to activate the various hybrid Notch ligands (containing extracellularly Drosophila Delta and intracellularly the various Notch ligands' intracellular domains) in Drosophila wing dics and mammalian cell culture. The authors found that NEUR proteins only activate the Notch ligands containing a Neuralized binding motif, with the consensus sequence NxxN, that is present in DLL1 and JAG1, but not in DLL4 and JAG2. The authors also analyse the intracellular domains of mammalian Notch ligands DLL1, DLL4, JAG1 and JAG2 in Drosophila by generating knock-in alleles where endogenous Dl expression had been substituted for those of hybrid Notch ligands. This analysis showed that only in Dl-DLL1 and Dl-JAG1 flies but not in Dl-DLL4 and Dl-JAG" flies is the embryonic lethality rescued, the results being in agreement with the hybrid Dl-DLL experiments on wing dics reported earlier in this work.

The authors conclude that their findings suggest that the activation mechanism of Notch during development differs between Drosophila (where both Neur and Mib1 are required for Notch-related developmental processes ) and mammals and that this could possibly explain the apparently lesser relevance of mammalian NEUR proteins for developmental Notch signalling.

*Evidence and clarity*

The manuscript is quite laconic but clearly written. The evidence presented by the authors, given the heterologous and in vitro nature (i.e using mammalian or hybrid Notch ligands and mammalian E3 ligases thereof in Drosophila and cell cultures) of the study is generally trustworthy but limited in the sense that it probably does not allow definitive conclusions to be drawn as to the differing nature of the action of the E3 ligases of Notch ligands in flies vs mammals in vivo.

__Response: __We thank the reviewer for their positive evaluation of our work and their constructive criticism. We would like to clarify that we do not conclude that the activation mechanism differs between mammals and flies. Our findings demonstrate that the signalling mechanisms of fly Neur and mammalian Neurl's follow the same fundamental rules. Moreover, our study does not aim to provide a definitive answer to how signalling differs between species. Instead, we utilized the 'humanized fly' system to show that Neurl proteins specifically activate Dll1 and Jag1, but not Dll4 and Jag2, which lack a neuralized binding site.

*Reproducibility*

As will be mentioned a number of times, these reviewers would like to enquire as to the reasons for not providing a statistical analysis of variation in the fly wing disc-based experiments (where the readout was either resuce of Wg expression or induction of ectopic Wg expression).

Response: We thank the reviewer for raising this important point. As outlined below, we will quantify the fly experiments and conduct statistical analysis across multiple experimental datasets to further substantiate our claims.

Also, while the constructs used in the study were inserted into the same genomic landing sites to achieve comparable levels of expression of the various proteins, these reviewers would like to see data on the levels of expression of NEUR1 and 2 as well as the hybrid Notch ligands.

**Major comments**

Comment on fly wing disc experiments:

The authors study both the capability of two different mammalian E3 ubiquitin ligases, Neuralized-like 1 and 2 (mouse Neur1 and human NEUR2) to activate four different Notch receptors (DLL1 and 2, JAG1 and 2) in flies and mammalian cell culture system. In flies, they first analyse the capability of Drosophila Neur (as a positive control) and Neur1 and NEUR2 to activate the various Notch ligands (based on wingless activation as a readout) in wild-type wings (where, Mind bomb 1, or Mib1 is the only E3 ligase for Notch ligands present) and Mib1 mutant wing discs (which lack any E3 ligands of Notch receptors). The authors then test four humanised, hybrid Notch ligands (all five N ligands bar Dll3 since the latter does not transactivate the Notch receptor) - where mammalian Notch ligands' intracellular domains, or ICDs, have been attached to fly Dl (Dl-Dll1, Dl-Dll4, Dl-JAG1, Dl-JAG2) - for their capacity to mediate Mib1-dependent activation of Notch (with ectopic Wg expression in wing discs as its readout). They found that all 4 ligands can activate Nocth in wild-type wings (where Mib1 is present), with Dl-JAG2 being less effective than the other 3 hybrid ligands, implying that such hybrid, humanised ligands can be usd in studying Notch pathway activation in Drosophila (thereby constituting a mixed/heterologous experimental system). The reviewers would like to get a comment as to the reason for the weaker activity of Dl-JAG2 in this set-up?.

Response: We do not have a definitive answer as to why the ICDs differ in their activity within MIb1-dependent signalling, since this question was not addressed in the scope of this work. However, it our findings demonstrate that the hybrid ligands are functional in Drosophila and that their differential behavior in Neur-mediated signaling is not attributed to a trivial explanation, e. g. that the hybrid ligands generally display no activity. There are several potential explanations for these differences. One possibility is variations in position, arrangement, or number of targeted lysines among the ICDs. These lysines serve as substrates for ubiquitylation and determine the rate of endocytosis, which in turn impacts the signaling activity of the corresponding ligand/hybrid. Another plausible explanation is differences in affinity of the binding sites of Mib1, which would similarly result in variations in ubiquitylation and endocytosis rates. Regardless, we emphasize that resolving this question does not affect any of the conclusions of the manuscript.

Also, the reviewers would like to get a comment as to why was not a Neur mutant set-up used, only Mib1 mutant dics?

Response: Neur is only expressed at a very late stage in wing development and is restricted to specific single cells (sensory organ precursors). Consequently, even if mutants were present, their impact would be limited to these cells. Moreover, the Neur promoter has a highly complex architecture, which makes it exceedingly difficult to manipulate for experiments involving this mutation. We will address these considerations in the revised manuscript.

The authors then found that only two of these hybrid ligands - Dl-DLL1 and Dl-JAG1 but not Dl-DLL4 or Dl-JAG2 - can be used to activate Notch in the above wing assay when Mib1 was mutant. This is consistent with the fact that the NxxN-based Neuralized Binding motif (NBM) is present in DLL1 and JAG1 only. Using the wing paradigm, the authors also show by either mutating the full NBM (NxxN) in DLL1 or changing the cryptic, "weak" NBM in DLL4 (containing NxxD sequence) into "full/strong" NxxN one that the NBM in the various Notch ligands is required and sufficient for activation of the Notch pathway.

Overall, the fly experiments are convincing in showing diffrential activation of Notch ligands. However, no statistical analysis of the experimental variation in these studies - neither for the number of wing discs analysed per (hybrid) Notch ligand tested nor the extent of a given experimental manipulation's effect is included. We deem that if the images presented in Figures 2 and 3 are truly representative, this needs to be made explicitly clear.

Response: We thank the reviewer for their positive evaluation of our work and for the constructive comments, which we will consider and include into the manuscript. While we have repeated all experiments with multiple flies, we acknowledge the critique regarding the absence of statistical analysis.

To address this, we will quantify the experiments conducted in the wing imaginal discs of Drosophila. We will do that by measuring the wing field size along the dorsal-ventral axis relative to the anterior-posterior axis. We will perform statistical analysis to assess the statistical significance between experiments, using data from n=5 experiments for each sample.

Comment on fly embryonic Delta neurogenic phenotype's rescue experiments by replacing Dl with the hybrid ligands: The authors analysed the capacity of the ICDs of the mammalian ligands to rescue the Dl phenotype in Drosophila, ie. their activation capability at the organismal level. This was achieved by generating knock-in alleles expressing the hybrid ligands in place of Dl. The notion that only NBM-containing hybrid ligands was strengthened by this analysis since it showed that only NBM-containing hybrid ligands - Dl-DLL1 and Dl-JAG1 - but not Dl-DLL4 nor Dl-JAG2 rescued the Dl neurogenic embryonic lethal phenotype. Since this experimental set-up relied on the endogoneous Drosophila E3 ligases for activating the Notch ligands, the capacity of mammalian NEUR1 and 2 proteins to complement the capacity of the hybrid ligands to activate Notch to activate these ligands was not addressed. Please comment as to the reasons for this apparent omission and if such an analyis lies beyond the scope of current work, what would be the expected results of such experiment in the light of other experiments conducted in the course of this work?

Response: Testing whether mammalian Neurl1 and Neurl2 can replace Drosophila Neur in an endogenous setting is an intriguing question; however, it falls outside the focus of this study. Performing such an experiment would be highly challenging due to complex and not well understood architecture of Neur gene in Drosophila. Additionally, we believe it is highly unlikely that the mammalian NEURLs proteins would fully compensate for the loss of function in a Drosophila Neur mutant.

Journal-agnostic peer review: evaluate the paper as it stands independently from potential journal fit.

Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

Generaly yes, put please see the above comments on the absence of statistical analysis of reproducibility/ variation (if any) in fly wing disc experiments.

**Reviewer's additional recommendations:**

To publish in a higher-ranking journal, the co-localisation analyses of Notch ligands and its various E3 ubiquitin ligases studied probably needs to be replaced by a more rigorous, ideally FRET-based approach.

Response: We thank the reviewer for the comment. The co-localization assay is quite a robust and functional approach, as it provides clear evidence that endocytosis into a different compartment has occurred with functional ligands, as opposed to non-functional ligands. This serves as a quantitative and rigorous indicator for functional differences between these ligand types.

Nevertheless, we acknowledge that co-localization is not a direct measure of molecular interactions between Neurl1 and Notch ligands. To address this, as suggested by the reviewer, we will perform co-IP to show the differential interaction between Neurl1 and specific Notch ligands. Additionally, we will attempt a proximity ligation assay (PLA), which we consider to be a more direct and suitable method for detecting interactions between NEURLs and Notch ligands in this context, compared to FRET.

Since previous studies have shown that the Notch ligands are (mostly) poly- or mono-ubiquitylated by the E3 ubiquitin ligases Mib and the NEUR proteins, ideally, this or its follow-up study would benefit from analysis of the ubiquitylation status of the various hybrid Notch ligands.

Response: We thank the reviewer for the suggestion. The ubiquitylation pattern by Neurl1 is beyond the topic of the current manuscript.

Also, it would be useful to show the strength of interaction between the hybrid Notch ligands and NEUR1 and NEUR2 by ising a co-immunoprecipitation based approach.

Response: As suggested by the reviewer, we plan to perform co-IP and/or PLA to show the differential binding of NEURL1 to the different ligands. However, due to the observed toxicity of NEURL2 in our cells, it has been excluded from our assays.

Please request additional experiments only if they are essential for the conclusions. Alternatively, ask the authors to qualify their claims as preliminary or speculative, or to remove them altogether.

These reviewers do not strictly request any further rexperiments. However, since the mammalian NEUR2 could not be studied in cell cultures of U2OS cells due to its toxicity, we would like the auhtors to explain the choice of this cell line. Perhaps a cell line whose viability is not impaired by NEUR2 should be (or should have been) used?

Response: The decision not to use other cell lines was based on several strict experimental requirements. The most stringent requirement was the need to generate a MIB1 knockout cell line, as MIB1 strongly activates all ligands. The availability of having MIB1 KO U2OS cells enabled these experiments.

If you have constructive further reaching suggestions that could significantly improve the study but would open new lines of investigations, please label them as "OPTIONAL".

As mentioned above, the NEUR2's capacity to activate the hybrid ligands in U2OS cells could not be addressed to due to its toxicity. A more optimal cell line will have to be used in follow-up studies.

Also, these findings ultimately warrant in vivo studies using mice to definitively ascertain whether they also hold equally true there.

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated time investment for substantial experiments.

The suggested experiments are optional apart from statistical analysis of variation (if any) in the fly wing disc experiments. If there is no (apparently significant) variation in these data, this needs to explicitly stated.

Response: We thank the reviewer for their thoughtful assessment. We will conduct the requested statistical analysis and perform some of the suggested supporting experiments as detailed in the response.

Are the data and the methods presented in such a way that they can be reproduced?

Generally yes, but see above about the lack of statistical data on the variation (if any).

Are the experiments adequately replicated and statistical analysis adequate?

Generally yes, but again, please see above about the lack of statistical data on the variation (if any).

**Minor comments**

Comment#1 (on the abstract and introduction):

In the Abstract, the authors state that there are four Notch ligands in mammals (lines 21 and 22): "Thus, it is unclear how NEURL proteins regulate the four mammalian Notch ligands". In the Introduction, they correctly state that there are five Notch ligands in mammals (lines 38 and 39): „In mammals, there are five ligands, three from the Delta-like (Dll) family (Dll1, Dll3, Dll4), and two from the Jagged (Jag) family (Jag1 and Jag2)." There are five Notch ligands in mammals (Dll1, Dll3, Dll4, Jag1, Jag2), and it is obvious that the authors are very well aware of this (they state in lines 146-147): "We excluded the ICD of DLL3 since it is not a ligand capable of trans-activation of Notch" (the four ligands included were Dll1, Dll4, Jag1 and Jag2)." Therefore, a claricifaction is required in the part of Abstract (i.e lines 21 ansd 22) - did the authors mean the four mammalian Notch ligands they actually studied (i.e Dll1, Dll4, Jag1, Jag2) or is there an oversight and the auhtors actually intended to write "the five Nocth ligands in mammals".? In either case, a correction is required in this reviewer's opinion.

Response: We are fully aware of this point, and will address it by providing clarification in the abstract as suggested.

Specific experimental issues that are easily addressable.

NEUR2 could not be studied in mammalian cell cultures due to its toxicity in the U2OS cell line, the one used by the authors. The use of another cell line would not be probably overly time-consuming; however, if this experiment lies outside the scope of current work, we would like to hear the authors' comment on this matter.

Response: This is addressed above.

Are prior studies referenced appropriately? Generally yes, but four prior studies go unmentioned: the two 2001 mouse Neur1 knock-out studies reporting no Notch-like developmental phenotype (Ruan et al, PNAS; Vollrath et al, Mol Cell Biol), the 2002 study of mouse, rat and human NEUR1 expression, subcellular localisation (Timmusk et al, Mol Cell Neuroscience) and the 2009 cell culture-based study of NEUR2's interaction with DLL1 and DLL4 (Rullinkov et al, BBRC). The non-requirement of NEUR1 and 2 proteins in mammalian developmental Notch signalling could partly be explained by the fact that NEUR1 is not highly expressed during mouse embryonic/foetal development - its expression becomes considerably more pronounced only postnatally (Timmusk et al, 2002).

Response: We will incorporate these references into the introduction and discuss the low expression of Neurls during development as a possible reason for the non-requirement in this context.

Are the text and figures clear and accurate?

Yes. These reviewers find the cartoon-based explanations of the experimental set-up in each figure helpful for enhancing the manuscript's overall clarity.

Response: We thank the reviewers for the positive feedback!

Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Please see above about the lack of statistical data on the variation (if any) in fly wing dic experiments and referencing of the 4 papers that are currently excluded.

Response: These will be corrected in the revised version.

Reviewer #3 (Significance (Required)):

1. Significance Provide contextual information to readers (editors and researchers) about the novelty of the study, its value for the field and the communities that might be interested. The following aspects are important: General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed? This study uses the amenability of Drosophila to study the mammalian NEUR proteins' (NEUR1 and NEUR2) activity upon Notch ligands using hybrid Notch ligands containing mammalian ICDs (intracellular domains) fused to the extracellular domain of Drosophila Delta (Dl). It confirms and extends prior studies showing that Notch ligands can be (strongly) activated only by the E3 ubiquitin ligases containing the Neuralized Binding Motif (NBM).

Response: We respectfully disagree with the reviewer's assessment on this point. Our study is the first to demonstrate that Neurl proteins differentially activate Dll1 and Jag1, but not Dll4 and Jag2. This findings is further supported by the significance comments of the other reviewers.

However, since this study was based on using hybrid ligands containing mammalian ICDs of Notch ligands fused to the extracellular domain of Drosophila Delta (Dl), it is somewhat artificial. While NEUR1 was also studied in mammalian cell cultures (but not NEUR2 due to its toxicity), only an in vivo study using mice expressing with systematic changes to the Notch ligands' NBM will definitively reveal whether the conclusions reached by the authors hold true in vivo in a non-heterologous system.

Response: We firmly believe that our combined 'humanized fly' model and quantitative cell culture assay represents an innovative and rigorous approach for testing humanized proteins in in-vivo settings, without the need for extensive mouse genetics. The conclusions of our experiments should not be dismissed solely on the grounds of "not being performed in mice," as this would undermine much of current scientific research.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...). The study's advances are chiefly mechanistic and functional since they show more definitively that the reason underlying the differing activation of four mammalian Notch ligands by mammalian NEUR1 and NEUR2 is mostly based upon the presence or otherwise of a conserved Neuralized Binding Motif, NBM. Audience: describe the type of audience ("specialised", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

The audience for this study is the research studying the Notch signalling pathway. Since dysregulation of this pathway is implicated in a number of devastating diseases, any improved understanding of its mechanistic underpinnings could in the long run lead to better therapeutic management of diseases with significant involvement of malfunctioning Notch signalling.

Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. Molecular biology, molecular neuroscience, developmental biology, cell-cell signalling, Notch signalling. All parts of the manuscript fall within our expertise.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary

Notch signalling is one of the major evolutionarily conserved signalling pathways involved in numerous developmental, physiological and pathological processes. Activation of the Notch receptor first requires ubiquitination of its ligands (collectively temed DSL), leading to a 'pulling force" that, upon ligand-receptor engagement, exposes Notch to intramembrane proteolysis leading to the nuclear translocation of the receptor's intracellular domain and activation of target genes with its DNA-binding co-factors.

While both Neuralized (Neurl) and Mind bomb are the E3 ubiquitin ligases for Notch ligands required for Drosphila development, in mammals, the Neur homologues Neur1 (officially Neurl1) and Neur2 (officially Neurl1B) are dispensable for development since double Neur1/2 knock-out mice have no developmental phenotype (but both Neur homologues are involved the the memory-related functions of Notch pathway in adulthood). Rather, just one of the two mammalian Mind bomb homologues, Mib1, functions as the chief E3 ligase for Notch ligands during mammalian development as evidenced by its Notch-related knockout phenotype.

Therefore, it has not been fully established whether and how the NEUR proteins regulate the mammalian Notch ligands. To clarify this issue, the authors assessed the capability of Drosophila Neur and mammalian NEUR1 and 2 proteins to activate the various hybrid Notch ligands (containing extracellularly Drosophila Delta and intracellularly the various Notch ligands' intracellular domains) in Drosophila wing dics and mammalian cell culture. The authors found that NEUR proteins only activate the Notch ligands containing a Neuralized binding motif, with the consensus sequence NxxN, that is present in DLL1 and JAG1, but not in DLL4 and JAG2. The authors also analyse the intracellular domains of mammalian Notch ligands DLL1, DLL4, JAG1 and JAG2 in Drosophila by generating knock-in alleles where endogenous Dl expression had been substituted for those of hybrid Notch ligands. This analysis showed that only in Dl-DLL1 and Dl-JAG1 flies but not in Dl-DLL4 and Dl-JAG" flies is the embryonic lethality rescued, the results being in agreement with the hybrid Dl-DLL experiments on wing dics reported earlier in this work. The authors conclude that their findings suggest that the activation mechanism of Notch during development differs between Drosophila (where both Neur and Mib1 are required for Notch-related developmental processes ) and mammals and that this could possibly explain the apparently lesser relevance of mammalian NEUR proteins for developmental Notch signalling.

Evidence and clarity

The manuscript is quite laconic but clearly written. The evidence presented by the authors, given the heterologous and in vitro nature (i.e using mammalian or hybrid Notch ligands and mammalian E3 ligases thereof in Drosophila and cell cultures) of the study is generally trustworthy but limited in the sense that it probably does not allow definitive conclusions to be drawn as to the differing nature of the action of the E3 ligases of Notch ligands in flies vs mammals in vivo.

Reproducibility

As will be mentioned a number of times, these reviewers would like to enquire as to the reasons for not providing a statistical analysis of variation in the fly wing disc-based experiments (where the readout was either resuce of Wg expression or induction of ectopic Wg expression). Also, while the constructs used in the study were inserted into the same genomic landing sites to achieve comparable leves of expression of the various proteins, these reviewers would like to see data on the levels of expression of NEUR1 and 2 as well as the hybrid Notch ligands.

Major comments

Comment on fly wing disc experiments:

The authors study both the capability of two different mammalian E3 ubiquitin ligases, Neuralized-like 1 and 2 (mouse Neur1 and human NEUR2) to activate four different Notch receptors (DLL1 and 2, JAG1 and 2) in flies and mammalian cell culture system. In flies, they first analyse the capability of Drosophila Neur (as a positive control) and Neur1 and NEUR2 to activate the various Notch ligands (based on wingless activation as a readout) in wild-type wings (where, Mind bomb 1, or Mib1 is the only E3 ligase for Notch ligands present) and Mib1 mutant wing discs (which lack any E3 ligands of Notch receptors). The authors then test four humanised, hybrid Notch ligands (all five N ligands bar Dll3 since the latter does not transactivate the Notch receptor) - where mammalian Notch ligands' intracellular domains, or ICDs, have been attached to fly Dl (Dl-Dll1, Dl-Dll4, Dl-JAG1, Dl-JAG2) - for their capacity to mediate Mib1-dependent activation of Notch (with ectopic Wg expression in wing discs as its readout). They found that all 4 ligands can activate Nocth in wild-type wings (where Mib1 is present), with Dl-JAG2 being less effective than the other 3 hybrid ligands, implying that such hybrid, humanised ligands can be usd in studying Notch pathway activation in Drosophila (thereby constituting a mixed/heterologous experimental system). The reviewers would like to get a comment as to the reason for the weaker activity of Dl-JAG2 in this set-up?.

Also, the reviewers would like to get a comment as to why was not a Neur mutant set-up used, only Mib1 mutant dics? The authors then found that only two of these hybrid ligands - Dl-DLL1 and Dl-JAG1 but not Dl-DLL4 or Dl-JAG2 - can be used to activate Notch in the above wing assay when Mib1 was mutant. This is consistent with the fact that the NxxN-based Neuralized Binding motif (NBM) is present in DLL1 and JAG1 only. Using the wing paradigm, the authors also show by either mutating the full NBM (NxxN) in DLL1 or changing the cryptic, "weak" NBM in DLL4 (containing NxxD sequence) into "full/strong" NxxN one that the NBM in the various Notch ligands is required and sufficient for activation of the Notch pathway.

Overall, the fly experiments are convincing in showing diffrential activation of Notch ligands. However, no statistical analysis of the experimental variation in these studies - neither for the number of wing discs analysed per (hybrid) Notch ligand tested nor the extent of a given experimental manipulation's effect is included. We deem that if the images presented in Figures 2 and 3 are truly representative, this needs to be made explicitly clear. Comment on fly embryonic Delta neurogenic phenotype's rescue experiments by replacing Dl with the hybrid ligands: The authors analysed the capacity of the ICDs of the mammalian ligands to rescue the Dl phenotype in Drosophila, ie. their activation capability at the organismal level. This was achieved by generating knock-in alleles expressing the hybrid ligands in place of Dl. The notion that only NBM-containing hybrid ligands was strengthened by this analysis since it showed that only NBM-containing hybrid ligands - Dl-DLL1 and Dl-JAG1 - but not Dl-DLL4 nor Dl-JAG2 rescued the Dl neurogenic embryonic lethal phenotype. Since this experimental set-up relied on the endogoneous Drosophila E3 ligases for activating the Notch ligands, the capacity of mammalian NEUR1 and 2 proteins to complement the capacity of the hybrid ligands to activate Notch to activate these ligands was not addressed. Please comment as to the reasons for this apparent omission and if such an analsyis lies beyond the scope of current work, what would be the expected results of such experiment in the light of other experiments conducted in the course of this work? Journal-agnostic peer review: evaluate the paper as it stands independently from potential journal fit.

Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

Generaly yes, put please see the above comments on the absence of statistical analysis of reproducibility/ variation (if any) in fly wing disc experiments.

Reviewer's additional recommendations:

To publish in a higher-ranking journal, the co-localisation analyses of Notch ligands and its various E3 ubiquitin ligases studied probably needs to be replaced by a more rigorous, ideally FRET-based approach. Since previous studies have shown that the Notch ligands are (mostly) poly- or mono-ubiquitylated by the E3 ubiquitin ligases Mib and the NEUR proteins, ideally, this or its follow-up study would benefit from analysis of the ubiquitylation status of the various hybrid Notch ligands. Also, it would be useful to show the strength of interaction between the hybrid Notch ligands and NEUR1 and NEUR2 by ising a co-immunoprecipitation based approach. Please request additional experiments only if they are essential for the conclusions. Alternatively, ask the authors to qualify their claims as preliminary or speculative, or to remove them altogether. These reviewers do not strictly request any further rexperiments. However, since the mammalian NEUR2 could not be studied in cell cultures of U2OS cells due to its toxicity, we would like the auhtors to explain the choice of this cell line. Perhaps a cell line whose viability is not impaired by NEUR2 should be (or should have been) used? If you have constructive further reaching suggestions that could significantly improve the study but would open new lines of investigations, please label them as "OPTIONAL". As mentioned above, the NEUR2's capacity to activate the hybrid ligands in U2OS cells could not be addressed to due to its toxicity. A more optimal cell line will have to be used in follow-up studies. Also, these findings ultimately warrant in vivo studies using mice to definitively ascertain whether they also hold equally true there.

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated time investment for substantial experiments.

The suggested experiments are optional apart from statistical analysis of variation (if any) in the fly wing disc experiments. If there is no (apparently significant) variation in these data, this needs to explicitly stated.

Are the data and the methods presented in such a way that they can be reproduced?

Generally yes, but see above about the lack of statistical data on the variation (if any).

Are the experiments adequately replicated and statistical analysis adequate?

Generally yes, but again, please see above about the lack of statistical data on the variation (if any).

Minor comments

Comment#1 (on the abstract and introduction):

In the Abstract, the authors state that there are four Notch ligands in mammals (lines 21 and 22):<br /> "Thus, it is unclear how NEURL proteins regulate the four mammalian Notch ligands". In the Introduction, they correctly state that there are five Notch ligands in mammals (lines 38 and 39): „In mammals, there are five ligands, three from the Delta-like (Dll) family (Dll1, Dll3, Dll4), and two from the Jagged (Jag) family (Jag1 and Jag2)." There are five Notch ligands in mammals (Dll1, Dll3, Dll4, Jag1, Jag2), and it is obvious that the authors are very well aware of this (they state in lines 146-147): "We excluded the ICD of DLL3 since it is not a ligand capable of trans-activation of Notch" (the four ligands included were Dll1, Dll4, Jag1 and Jag2)." Therefore, a claricifaction is required in the part of Abstract (i.e lines 21 ansd 22) - did the authors mean the four mammalian Notch ligands they actually studied (i.e Dll1, Dll4, Jag1, Jag2) or is there an oversight and the auhtors actually intended to write "the five Nocth ligands in mammals".? In either case, a correction is required in this reviewer's opinion.

Specific experimental issues that are easily addressable.

NEUR2 could not be studied in mammalian cell cultures due to its toxicity in the U2OS cell line, the one used by the authors. The use of another cell line would not be probably overly time-consuming; however, if this experiment lies outside the scope of current work, we would like to hear the authors' comment on this matter. Are prior studies referenced appropriately? Generally yes, but four prior studies go unmentioned: the two 2001 mouse Neur1 knock-out studies reporting no Notch-like developmental phenotype (Ruan et al, PNAS; Vollrath et al, Mol Cell Biol), the 2002 study of mouse, rat and human NEUR1 expression, subcellular localisation (Timmusk et al, Mol Cell Neuroscience) and the 2009 cell culture-based study of NEUR2's interaction with DLL1 and DLL4 (Rullinkov et al, BBRC). The non-requirement of NEUR1 and 2 proteins in mammalian developmental Notch signalling could partly be explained by the fact that NEUR1 is not highly expressed during mouse embryonic/foetal development - its expression becomes considerably more pronounced only postnatally (Timmusk et al, 2002).

Are the text and figures clear and accurate?

Yes. These reviewers find the cartoon-based explanations of the experimental set-up in each figure helpful for enhancing the manuscript's overall clarity.

Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Please see above about the lack of statistical data on the variation (if any) in fly wing dic experiments and referencing of the 4 papers that are currently excluded.

Significance

Provide contextual information to readers (editors and researchers) about the novelty of the study, its value for the field and the communities that might be interested. The following aspects are important:

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed? This study uses the amenability of Drosophila to study the mammalian NEUR proteins' (NEUR1 and NEUR2) activity upon Notch ligands using hybrid Notch ligands containing mammalian ICDs (intracellular domains) fused to the extracellular domain of Drosophila Delta (Dl). It confirms and extends prior studies showing that Notch ligands can be (strongly) activated only by the E3 ubiquitin ligases containing the Neuralized Binding Motif (NBM). However, since this study was based on using hybrid ligands containing mammalian ICDs of Notch ligands fused to the extracellular domain of Drosophila Delta (Dl), it is somewhat artificial. While NEUR1 was also studied in mammalian cell cultures (but not NEUR2 due to its toxicity), only an in vivo study using mice expressing with systematic changes to the Notch ligands' NBM will definitively reveal whether the conclusions reached by the authors hold true in vivo in a non-heterologous system.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...). The study's advances are chiefly mechanistic and functional since they show more definitively that the reason underlying the differing activation of four mammalian Notch ligands by mammalian NEUR1 and NEUR2 is mostly based upon the presence or otherwise of a conserved Neuralized Binding Motif, NBM.

Audience: describe the type of audience ("specialised", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field? The audience for this study is the research studying the Notch signalling pathway. Since dysregulation of this pathway is implicated in a number of devastating diseases, any improved understanding of its mechanistic underpinnings could in the long run lead to better therapeutic management of diseases with significant involvement of malfunctioning Notch signalling.

Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. Molecular biology, molecular neuroscience, developmental biology, cell-cell signalling, Notch signalling. All parts of the manuscript fall within our expertise.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary

The manuscript describes an analysis of specificity of functional interactions between mammalian Neuralized proteins and different human ligands for Notch. To investigate this, the authors take the approach of constructing hybrid proteins that contain the intracellular domain of the human ligands and the extracellular domain of the Drosophila Delta or Serrate, and investigate their activity in vivo, in the Drosophila wing disc. The latter is a well-established model tissue for assessing Notch ligand activity. As a second assay they express mammalian neutralized constructs in human cells for luciferase-based Notch signal reporter assays. The experiments are well presented and described and make a strong case for the conclusions that both Neurl1 and 2 can activate Notch signalling by Dll1 and Jag1 but not Dll4 and Jag2. Use of different mutant intracellular domains is used to show the importance of the NXXN motif, which in Drosophila is required for Neuralized interaction with Delta and Serrate. The use of missense mutations and in particular the reactivation of the cryptic NXXD site in Dll4 by substitution to N is convincing for establishing the importance of the motif. There is also colocalization data to support the conclusion that there is likely to be NXXN-dependent complex formation between the ligand and Neuralized proteins. This latter conclusion would be made firmer fi there were pull down data to support it, although to be fair it is most unlikely that another explanation, other than complex formation could account for the observation of both colocalization and ligand activation.

Major comments

The main limitation of the work is that it is mostly based on overexpression of constructs to activate ectopic expression rather than gene editing endogenous genes. It would be helpful if the authors could comment on the limitations of the work in discussion. Two points of data included in the work are important in mitigating this limitation. Firstly, the experiments in the wing disc and cell culture are taking place in a mindbomb mutant background and the activation is observed is therefore a rescue of activity that has been lost. Secondly, and importantly, the final experiment makes use of a Dl mutant Drosophila line which shows embryo lethality when homozygous, with the characteristic neurogenic phenotype. Rescue of lethality can be brought about by knock-in experiments which restore Dl function and this is also true for the ligand hybrid constructs that introduce mammalian ligand intracellular domains only when they include the NXXN motif This indicates the importance of the motif in normal development

Overall, the data presented in the paper is convincing as regards the conclusions made.

Minor points

In figure 1 the legend for D says that cryptic sites are substitutions of N for E or Q, but the figure and main text indicate that the substitutions are N to E or D.

In the remain figures it would be helpful to include in the figure legends and indications of the numbers of wing discs, embryos for which the images shown are representative of.

In Fg 3 The activation of Notch, by neural1 and Dl-Jag1 in B'" is stronger in the ventral side of the disc than the dorsal whereas, although activation of the same ligand by Neurl2 in C'" is weaker the majority of the ectopic wingless expression is on the dorsal compartment. Is there any reason for the switch in preference between the two neutralized proteins? Overgrowth of the wing disc seems to be similar on both sides and so am wondering if the picture is representative of the ectopic wingless distribution in this case.

Significance

Previous work on double genetic knockouts of the two mouse Neuralized genes cast doubt as to whether Neuralized proteins play a role in Notch signal activation in mammals, unlike in Drosophila. There is, however, some genetic indications that spatial memory requires both Notch and neutralized proteins and may represent a specialised function limited to the Neuralized interaction. There are likely to be more subtle contexts waiting to be uncovered. The work is therefore showing important proof of principle for establishing the functionality of the mammalian Neurl proteins and highlights new findings indicting specialisation of the different ligands for interactions with Notch components. Elucidation of such specialisations will help understand why the diversity of different homologues of Notch and ligand have evolved and are maintained in the vertebrate genome compared to the single Notch and two ligands in Drosophila. Since Notch and it misregulation are widely involved in development, health and disease and there is much interest in developing therapeutic interactions that alter Notch activity then the work is likely of broad interest.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

This is an interesting manuscript from two groups of experts in Notch signaling biology with complementary expertise in Drosophila genetics (Klein) and in biophysical studies of the Notch pathway (Sprinzak). The paper provides a cutting-edge structure-function dissection of the E3 ubiquitin ligase Neuralized and its mammalian homologs, Neurl1a and Neurl1a. The work is particularly relevant since the functions of mammalian Neurl1a and Neurl1b have been questioned, and more subtle altogether than those of fly Neuralized (as summarized by the authors in Fig. 1C). This is in part due to the dominant effects of the E3 ubiquitin ligase Mindbomb1 (Mib1) in Notch ligand-expressing cells from mammalian systems. The authors use careful structure-function work in fly development (mostly wing imaginal discs) and in mammalian cell culture systems, including a clever approach to study the function of mammalian Neurl1a and Neurl1b and mammalian/fly Notch ligand hybrids in Drosophila to draw new conclusions about the function of Neurl1a/b, showing that they can function as activators of Notch signaling mediated by the Notch ligands Dll1 and Jag1, and not by Dll4 and Jag2, tracing these differential effects to the recognition of a short NXXN consensus sequence in the N-terminal region of the ligand's intracellular domain.

Specific questions:

• The current title of the manuscript is not very information-rich and would not allow a reader to gather key information about the findings without reading at least the abstract. Could this be improved? For example, by referring to differential activation of individual Notch ligands, or some other more direct description of the key findings?
• The authors design most key experiments documenting agonistic effects of Neurl1a/1b in a Mib1-deficient background, both in flies and in cell culture systems. This is understandable experimentally to isolate Neurl1a/b's effects in these experimental systems. However, this leaves open questions as to the prevailing effects of Neurl1a/b in cells that also express Mib1 (which the authors comment on in the discussion based on past findings, including some suggesting that Neurl1a/1b can function as Notch inhibitors through a ligand ubiquitination mechanism that may differ from their activating function). Do the authors actually have data that could shed light on this discussion? For example, have they performed cell coculture assays in which Neurl1a or Neurl1b is co-expressed with a Notch ligand, but in the presence of Mib1? This condition seems to be systematically omitted from all the coculture experiments that are presented. It would be interesting to evaluate the net effect of Neurl1a/Neurl1b expression in a Mib1-sufficient system as well.
• The paper suggests important predictions about mammalian functions of Neurl1a/1b, including the neurological effects that have been reported, in double-deficient mice, namely that that there are cells that only express Neurl1a/1b and not Mib1 and do rely on Dll1 and Jag1 for signaling. Could the authors at least comment on this prediction? Are there are any single cell atlases where candidate cells like that can be identified? Or would the authors predict that Neurl1a/1b could actually function as Notch agonist even in cells expressing Mib1? (see also previous comment)
• Some minor typos: line 305 should likely read "flies homozygous for (...)". Line 408, "for providing" repeated twice.

Significance

Thank you for the opportunity to review this lovely collaborative paper. As indicated in my comments to the authors, the findings provide novel structure-function information about an understudied aspect of Notch signaling and clarify conflicting past data about the mammalian homologs of fly Neuralized. The approach is elegant and multidisciplinary, notably in regards to the combination of cell co-culture systems and Drosophila as a platform to study mammalian Neuralized proteins and hybrid Notch ligand molecules. The findings will be interesting to the field and will generate discussion. I would suggest that some additional information would be a plus to substantiate predictions about mammalian functions of Neurl1a/b, and also to clarify its effects in the presence or absence of concomitant Mib1 expression.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

We thank the reviewers for their insightful comments, and we address all their comments in the detailed point-by-point responses provided below.

---

Reviewer #1

__Evidence, reproducibility and clarity __

*In the manuscript entitled "Inhibition of glycolysis in tuberculosis-mediated metabolic rewiring reduces HIV-1 spread across macrophages", Vahlas and colleagues investigated the hypothesis that Mtb interferes with HIV-1 infection of human macrophages, as they represent a common target cell type. In particular, they observed that a conditioned medium generated from Mtb-infected macrophages (Mtb-CM) induces tunneling nanotubes (TNT) in HIV-infected macrophages thereby facilitating viral spreading. At the same time, Mtb-CM induced a glycolytic pathway leading to ATP accumulation in HIV-infected macrophages, an essential pathway for TNT induction whereas pharmacological interference with such a metabolic switch resulted in a reduced viral production.

Experimental approach: primary human monocytes differentiated into monocyte-derived macrophages (MDM) in the presence of a TB-dominated microenvironment (Mtb-CM). The intracellular rate of ATP production was evaluated by the Seahorse technology at day 3 of MDM differentiation. The measurements of basal extracellular acidification rate (ECAR) and basal oxygen consumption rate (OCR) were used to calculate ATP production rate from glycolysis (GlycoATP) and mitochondrial OXPHOS (MitoATP).*

* This is a well-conducted, innovative study exploring the interaction of two main human pathogens, i.e. Mtb and HIV, sharing macrophages as common target cell. The manuscript is clearly written and the conclusions and hypotheses are supported by experimental evidence. I have two general points that I encourage the authors to address.*

We thank the Reviewer for his/her valuable comments and address all provided comments below.

1. __ As mentioned in the Discussion, macrophage infection by HIV is characterized by the accumulation of preformed, infectious virions in VCC (Virus Containing Compartments) that can be pharmacologically modulated both in terms of accumulation and rapid release in the absence of cell cytopathicity. Although the modulation of VCC was not the objective of the present study, it would be important to discuss their role and their potential modulation by Mtb and/or metabolic modifications, if known.__ In the discussion, we mentioned that “In HIV-1 infected macrophages, ATP is also vital for the release of particles from virus-containing compartments (Graziano et al., 2015)”. Graziano et al. (PMID 26056317) showed that extracellular ATP favors the release of virions actively accumulating within the VCC of infected macrophages through its interaction with the P2X7 receptor. This study will be discussed more in detail in the revised version of the manuscript.

In addition, we fully agree with the reviewer that exploring potential modifications in the formation of virus containing compartments (VCC) following Mtb infection, CmMTB treatment or metabolic alterations is highly relevant. Importantly, VCCs are specific compartments in infected macrophages where new virions are generated and protected from the immune system and antiretroviral therapies. Interestingly, Siglec-1 was shown to be involved in VCC formation in infected macrophages (Jason E Hammonds et al., 2017; PMID 28129379), and we demonstrated that the level of expression of this lectin is increased in CmMTB-treated cells (Dupont et al., PMID: 32223897). We propose to perform new experiments during the revision process to look whether the formation of VCC is disturbed in CmMTB-treated macrophages upon HIV-1 infection, using the tetraspanin CD81 and/or Siglec-1 along with HIV-Gag to assess VCC formation (as in Reviewer Figure 1).

Reviewer Figure 1: VCC formation in multinucleated HIV-1 infected macrophages. Human macrophages were infected with HIV-1 (NLAd8-VSVG, 3 days) and stained with HIV-gag and CD81 to stain the VCC.

__ Understanding the purpose of using a VSV-g based infection system, nonetheless it would be important to know whether metabolic modulation does affect CD4 and CCR5 expression on MDM and its consequence for their susceptibility to HIV infection, in addition to the effects on TNT formation and viral transfer between cells.__

We appreciate this comment. The reviewer correctly understands that we used VSVG pseudotyped virus in this study to eliminate the effect of metabolic modulation on the expression of HIV entry receptors and potentially on virus entry. It has been previously demonstrated in CD4 T cells that the nutrient modulation does not affect HIV entry when the Blam-Vpr assay is used (Clerc et al., 2019, PMID 32373781, supplemental Figure 6).

In addition, as demonstrated in our earlier work (Souriant et al. Cell Reports, 2019), CmMTB treatment increases the levels of both CD4 and CCR5 on the surface of macrophages. However, it does not impact HIV entry, as shown using the same Blam-Vpr assay. Therefore, the exacerbation of HIV-1 infection in the TB-environment is not a consequence of increased viral entry. This will be clarified in the revised version of the manuscript.

As suggested by the reviewer, we will also conduct new experiments during the revision process. Specifically, we will assess the levels of entry receptors using flow cytometry analysis and measure virus entry using the Blam-Vpr fusion assay in CmMTB-treated cells, with or without Oxamate treatment (to inhibit glycolysis).

Specific points:

1. __ "TB-PE" (pleural effusion) is neither specified in the Results nor in the Methods sections.__ We thank the reviewer for pointing out this omission. TB-PE refers to pleural effusions from TB patients, a term we had previously defined only in the introduction and figure legends. We will ensure that this definition is explicitly stated in the Result and Methods sections of the revised manuscript.

__ Figure 3A does not seem to display cell viability, but rather HIV Gag expression by IFA. __

Indeed, there is an error in the text regarding cell viability. Cell viability following drug treatments was assessed by flow cytometry, as shown in Figure S2C. In Figure 3A, we included nuclear staining (in addition to HIV Gag) to confirm that cell density is not affected. This will be corrected in the revised manuscript. Additionally, we will perform F-actin staining to evaluate cell morphology and further confirm that all key parameters, i.e., viability, cell density, and cell morphology, are unaffected by the drugs used in Figure 3.

---

Furthermore, Figure 3C indicates Gag expression, not "HIV infection" (see page 8, Results).

We thank the reviewer for helping us to clarify this issue. In Figure 3C, the term “infection index” refers to the percentage of HIV Gag-positive cells resulting from productive infection. This is calculated as the total number of nuclei in HIV Gag-stained cells divided by the total number of nuclei, multiplied by 100, as described in the Methods section.

We have previously used this method to estimate the HIV infection rate in our published studies (Souriant et al., 2019; Dupont et al., 2020; Mascarau et al., 2023). To further improve the clarity and interpretation of the figure, we will include a clear definition of the infection index in the figure legend in the revised version of the manuscript.

Significance

The paper addresses a poorly explored area, i.e. the interaction of Mtb and HIV during infection of macrophages. The authors focused on a specific aspect of such an interaction (I,e, the modulation of nanotubes formation and transfer of virions to target cells), but their results can be extrapolated in a broader context, particularly if the authors will be willing to address my general questions. Although specific in its experimental approach, the implication of the study will be of interest to a general audience.

We appreciate this positive comment.__ __

Reviewer #2

__Evidence, reproducibility and clarity __

The current work is based on previous observations that the abundance of lung macrophages is augmented in NHPs with active TB and exacerbated in those coinfected with SIV (Dupont et al., 2022; Dupont et al., 2020; Souriant et al., 2019). Further work with these TB-induced immunomodulatory macrophages demonstrated an increased susceptibility to HIV-1 replication and spread via the formation of tunneling nanotubes (TNTs), (Souriant et al., 2019). In the present manuscript, the authors connected these findings with the metabolic state of macrophages (glycolysis vs OXPHOS). Using a range of metabolic inhibitors coupled with seahorse assays and microscopy confirmed the role of Mtb-induced glycolytic shift in inducing the formation of TNTs and the spread of HIV. The work is well-planned and executed. However, the study is mainly correlative without any molecular insights. The knowledge generated is important and valuable for future studies to understand the molecular players in regulating immunometabolism during HIV-TB coinfection.

We thank the Reviewer for his/her valuable comments, and we address all provided comments below.

Major Comments:

There are conflicting reports about Mtb's impact on macrophage ECAR and OXPHOS, which authors have acknowledged. Therefore, including OCR and ECAR plots along with the glycoATP and MitoATP data will be useful. Similarly, OCR/ECAR plots without any conditioned medium should be included to clarify the role of Mtb infection on OCR/ECAR.

In this manuscript, we evaluated the intracellular rate of ATP production in macrophages (day 3 of differentiation) treated with either cmCTR or cmMTB using Seahorse technology. Measurements of extracellular acidification rate (ECAR) and oxygen consumption rate (OCR), both before and after the addition of oligomycin (an ATP synthase inhibitor), were used to calculate the contributions of glycolysis (GlycoATP, Figure 1B) and mitochondrial OXPHOS (MitoATP, Figure S1C) to total ATP production (Figure 1A).

We agree with the reviewer that displaying basal OCR/ECAR plots (bioenergetic profiles) would help characterize the overall energy phenotypes of macrophages. These graphs will be prepared and included in Figure S1. Furthermore, we will enhance the discussion and interpretation of these findings in the Results section of the revised manuscript.

As suggested, we will also assess ATP production using Seahorse technology for control cells (day 3 differentiated in RPMI) and provide OCR/ECAR plots for these new experiments.

__Fig 2G image is not convincing. While HIF1 alpha seems more in the nucleus, the overall morphology of the cell is more compact. Additional verification is needed. __

Regarding the specific comment on Fig. 2G, the reviewer is correct that the morphology of CmMTB-treated cells differs from that of CmCTR-treated cells. We have previously shown that CmMTB-treated macrophages display an M(IL-10) phenotype, characterized by a CD16+CD163+MerTK+PD-L1+ signature, morphological changes (cells appear rounder and form more TNTs), nuclear translocation of phosphorylated STAT3, and increased susceptibility to Mtb or HIV-1 infection (Dupont et al., 2022; Dupont et al., 2020; Lastrucci et al., 2015; Souriant et al., 2019).

As shown in Figure 2H, HIF1-α is predominantly cytoplasmic in most control cells, whereas an increased number of cells with nuclear HIF-1α staining were observed in CmMTB-treated cells. To quantify this observation, we manually assessed the ratio of HIF-1α signal intensity between the nucleus and cytoplasm in over 50 cells from three different donors. This methodology was not adequately explained in the Methods section and will be clarified in the revised manuscript. We also propose to include more representative images of HIF-1α-stained cells to support these findings.

Furthermore, genetic evidence is required in order to confirm if HIF1 alpha is the primary regulator of glycolytic shift by cmMTB/PE-TB, leading to more HIV dissemination by the TNT formation.

We fully agree that further experiments are essential to formally demonstrate that HIF-1α activation is responsible for the observed increase in HIV-1 infection and TNT formation in CmMTB-treated cells. To address this hypothesis, we propose conducting key experiments during the revision process

We will first use pharmacological approaches to modulate HIF-1α levels, as described in our recent publication (Maio et al., eLife, PMID 38922679). Specifically, we will test the HIF-1α inhibitor PX-478 as well as dimethyloxalylglycine (DMOG), a compound that stabilizes HIF-1α expression. These drugs will be applied 24h prior to HIV-1 infection in CmMTB-treated cells, and we will quantify HIV-1 infection and TNT formation on day 6 using immunofluorescence (IF).

In parallel, though technically challenging, we will attempt to reduce HIF-1α expression (and consequently its activity) in primary human monocytes using a siRNA-mediated depletion approach. This method has been successfully employed in our previous studies to target STAT3, STAT1 and Siglec-1 (Dupont et al., 2020; Lastrucci et al., 2015; Dupont et al., 2022). Under these conditions, we will measure HIV-1 infection and TNT formation on day 6 by IF.

Also, the authors have used only one tool to measure HIV levels -microscopy. While important, another method for verifying findings is needed. This is important as the effect of inhibitors (UK5099) is marginal.

In the present manuscript, we assess HIV-1 infection levels using two methods: microscopy (Figure 3 and 4I) and flow cytometry (Figure S2H-I). To address the reviewer’s comment, we propose to complement our current analysis of HIV-1 infection by evaluating HIV-1 replication through the measurement of HIV-p24 release in the supernatant of CmMTB-treated macrophages following drug treatments, as previously performed (Dupont et al., 2020; Souriant et al., 2019; Dupont et al., 2022; Mascarau et al., 2024; Raynaud-Messina et al., 2018).

Regarding the slight increase of HIV-1 infection (Gag expression by IF, Figure 3A) upon UK5099 treatment, we appreciate the reviewer’s valuable observation. Enhancing glycolysis levels remains a considerable challenge in studies targeting metabolic pathways, as most approaches focus on inhibiting glycolysis. However, in our study, the effect UK5099 on HIV-1 infection is reproducible and statistically significant, as demonstrated by analyzes of data from more than ten donors using IF (Figure 3C) and eight donors by flow cytometry (Figure S2H-I).

We acknowledge that the specific image provided in Fig. 3A for the UK5099 condition may not be the most representative and could cause confusion. To address this, we will replace the current image with a more representative one in the revised version of the manuscript.

---

Authors have used oxamate to inhibit glycolysis. Inhibition of LDH could lead to inhibition of NAD/NADH regeneration, thereby slowing down glycolysis. However, lack of lactate could have wide-ranging influence on cells as lactate could regulate several post-translational modifications, including lactylation. While the authors argued against using 2-DG, several findings confirm the glycolysis inhibitory potential of 2-DG when infected with Mtb. This should be included.

We understand the reviewer’s comment regarding the glucose analog 2-DG, which is widely used to inhibit glycolysis. Notably, recent studies have used it to show that glycolytic activity is critical for reactivating HIV-1 in macrophage reservoirs (Real et al., 2022, PMID 36220814).

In our study, we did not initially use 2-DG because it also inhibits glucose contribution to OXPHOS, making it challenging to distinguish between the roles of glycolysis and OXPHOS in macrophages (Wang et al., Cell Metabolism, PMID 30184486). Unlike Oxamate or GSK 2837, which specifically target LDHA, 2-DG does not exclusively affect glycolysis. Furthermore, inhibiting glucose metabolism with 2-DG is expected to yield similar results to glucose deprivation, as demonstrated in Figures 3H-K.

To address this, we propose conducting the suggested experiments using 2-DG in CmMTB-treated macrophages during the revision process. This will allow to assess their susceptibility to HIV-1 under this treatment. We will subsequently discuss the effects of 2-DG and integrate these results into the revised version of the manuscript.

A standard glycolytic function test (glucose, oligomycin and 2-DG injection) should be performed to assess the effect of TB-PE and cmMTB on the macrophages directly.

We appreciate the reviewer’s comment and will address it by testing the ability of CmMTB to alter the glycolytic activity of macrophages using the Seahorse Glycolytic Rate Assay. This assay, a refined version of the classical Seahorse Glycolysis Stress Test (see https://www.agilent.com/en/products/cell-analysis/glycolysis-assays-using-cell-analysis-technology), relies on an algorithm that generates the Proton Efflux Rate (PER), providing a robust quantitative measurement of glycolytic function. PER is directly correlated with lactate accumulation, enabling us to calculate glycolytic parameters that will complement our existing assays aimed at characterizing the glycolytic pathway in CmMTB-treated macrophages. We plan to perform these measurements and include the results in Figure 2.

__ Depriving glucose is not the best way to show the effect of glucose on HIV infection and MGC formation, as it can affect other aspects of cellular physiology, such as redox and bioenergetics. Instead, the use of galactose in place of glucose would generate ATP only by ____OXPHOS. Some key experiments should be repeated using galactose as a sole C source.__

We agree with this comment. In M2 macrophages, it has been shown that both glucose deprivation (as demonstrated in this study, Figure 3H-K) and glucose substitution with galactose (Wang et al., Cell Metabolism, PMID 30184486) effectively suppress glycolytic activity. Galactose must first be metabolized by the Leloir pathway before entering glycolysis, resulting in a significant reduction in glycolytic flux.

As suggested by the reviewer, we will complement our study by using galactose as the carbon source instead of glucose in a new set of experiments during the revision process.

__ UK5099 and oxamate nuclei seem smaller and less bright compared to the control. Images between control and UK5099 appear marginally different (non-significant).__

Figure 3A may not clearly convey that the nuclei are unaffected by the treatment. To address this, we will adjust the images, particularly the DAPI staining settings, to ensure accurate interpretation.

Regarding the slight effect of UK5099 treatment on Gag expression (infection index), as discussed above, this effect is reproducible and significant. We will replace the current image in Figure 3A with a more representative one.

The overall impact of the study is limited as the authors provide no evidence on the mechanism of how glycolysis induces TNT formation, which needs to be more characterized.

We fully agree that understanding how glycolysis induces tunneling nanotubes (TNTs) is a crucial and challenging question. This challenge stems from the incomplete understanding of the molecular mechanisms underlying TNT formation and the contradictory results reported across different cell types.

In our study, we demonstrated that inhibiting glycolysis—using Oxamate, GSK, or glucose deprivation—reduces TNT formation, whereas promoting glycolysis with UK5099 enhances their formation. We discuss in the manuscript that glycolysis likely provides the energy required for actin cytoskeletal rearrangements, which are essential for TNT formation.

Moreover, ATP plays a critical role in supporting cellular functions depending on actin remodeling, such as cell migration and the epithelial-to-mesenchymal transition (DeWane et al., 2021, PMID__33558441).__

To try to investigate the molecular mechanisms underlying TNT formation in our model, we propose the following experiments during the revision process:

• HIF1-α and TNT formation: IF staining of HIF1-α will be performed to correlate TNT formation with the level of HIF1-α nuclear translocation (as quantified in Figure 2I). This experiment aims to demonstrate a link between HIF1-α activation and TNT formation.
• Effect of HIF1-α inhibition: TNT formation will be quantified upon inhibiting HIF1-α activity using pharmacological approaches and/or siRNA-mediated gene silencing in HIV-1-infected CmMTB-treated cells.
• GLUT-1 focalization and TNT formation: To establish a connection between glycolysis and TNT formation, we will localize the primary glucose transporter GLUT-1 in relation to TNTs in CmMTB-treated macrophages. This approach builds on previous work on microvilli, which are F-actin structures with similarities to TNTs (Hexige et al., 2015, PMID: 25561062). Confocal or super-resolution microscopy will be employed to determine whether GLUT-1 accumulates at specific TNT sites. Through these experiments, we aim to provide deeper insights into the role of glycolysis in TNT formation.

__Minor comments:

The manuscript does not clearly show how the total ATP was calculated from the ATP rate assay.__

We will ensure that the method for calculating total ATP is explicitly described in the Methods section of the revised manuscript. __ In figure 1 (and everywhere else) the units on the y-axis should be corrected to [pmol/min] instead of pmol and the Seahorse profiles should mention whether the axis represents OCR or ECAR.__

The reviewer is correct. The axes in the relevant figures for ATP rate results (Figure 1A, B, C, D and Figure S1A, B, C) will be revised in the updated version of the manuscript.

The authors have called the macrophages highly glycolytic in first set of results which is misleading. Although the glycoATP contribution is increasing, overall ATP production is still majorly through oxidative phosphorylation (70% vs 25%).

We fully agree with the reviewer’s comment. As mentioned in the Result section “Approximately 90% of ATP production in macrophages differentiated with cmCTR came from OXPHOS; this parameter was reduced to 70% when conditioned with cmMTB (Figure 1E-F).” CmMTB and TB-PE drive macrophages toward an M2/M(IL-10) phenotype (Lastrucci et al. 2015), and based on the extensive literature on metabolism of anti-inflammatory M2 macrophages, this phenotype primarily relies on OXPHOS and fatty acid oxidation (for review see Biswas and Mantovani, Cell Metabolism, 2012).

It is therefore logical that overall ATP production in these cells remains predominantly through OXPHOS. However, we observe a significant decrease in OXPHOS activity following CmMTB treatment, alongside a marked increase in glycolysis (Figure 1).

Referring to CmMTB-treated macrophages as highly glycolytic was inaccurate, indeed, and this terminology will be corrected, with a clearer explanation provided in the revised manuscript.

Fig 3: Why does the HIV gag protein signal appear as irregular large spots?

In Figure 3A, the resolution used is sufficient to quantify the number of cells positive for HIV Gag (and thus the infection index). However, it does not allow for detailed examination of the intracellular localization of Gag as “spots”. The reviewer is correct that, within macrophages, the Gag signal often appears as large and intense cytoplasmic “spots” corresponding to the VCC, as illustrated in Reviewer Figure 1 in response to Reviewer 1.

__Referees cross-commenting:

I agree with the reviewer# 1 assessment. However, I feel that mechanistically paper could be improved and by performing more experiments.__

We fully agree that additional experiments are essential to improve the manuscript. We will address all comments and perform the experiments suggested by Reviewer 2, particularly to better characterize the metabolic state of our cells, provide evidence for the role of glycolysis in HIV-1 exacerbation, and further elucidate the mechanism by which glycolysis induces TNT formation.

---

Significance

The knowledge generated is important and valuable for future studies to understand the molecular players in regulating immunometabolism during HIV-TB coinfection.

We appreciate this positive comment.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The current work is based on previous observations that the abundance of lung macrophages is augmented in NHPs with active TB and exacerbated in those coinfected with SIV (Dupont et al., 2022; Dupont et al., 2020; Souriant et al., 2019). Further work with these TB-induced immunomodulatory macrophages demonstrated an increased susceptibility to HIV-1 replication and spread via the formation of tunneling nanotubes (TNTs), (Souriant et al., 2019). In the present manuscript, the authors connected these findings with the metabolic state of macrophages (glycolysis vs OXPHOS). Using a range of metabolic inhibitors coupled with seahorse assays and microscopy confirmed the role of Mtb-induced glycolytic shift in inducing the formation of TNTs and the spread of HIV. The work is well-planned and executed. However, the study is mainly correlative without any molecular insights. The knowledge generated is important and valuable for future studies to understand the molecular players in regulating immunometabolism during HIV-TB coinfection.

Major Comments

There are conflicting reports about Mtb's impact on macrophage ECAR and OXPHOS, which authors have acknowledged. Therefore, including OCR and ECAR plots along with the glycoATP and MitoATP data will be useful. Similarly, OCR/ECAR plots without any conditioned medium should be included to clarify the role of Mtb infection on OCR/ECAR.

Fig 2G image is not convincing. While HIF1 alpha seems more in the nucleus, the overall morphology of the cell is more compact. Additional verification is needed. Furthermore, genetic evidence is required in order to confirm if HIF1 alpha is the primary regulator of glycolytic shift by cmMTB/PE-TB, leading to more HIV dissemination by the TNT formation.

Also, the authors have used only one tool to measure HIV levels -microscopy. While important, another method for verifying findings is needed. This is important as the effect of inhibitors (UK5099) is marginal.

Authors have used oxamate to inhibit glycolysis. Inhibition of LDH could lead to inhibition of NAD/NADH regeneration, thereby slowing down glycolysis. However, lack of lactate could have wide-ranging influence on cells as lactate could regulate several post-translational modifications, including lactylation. While the authors argued against using 2-DG, several findings confirm the glycolysis inhibitory potential of 2-DG when infected with Mtb. This should be included.

A standard glycolytic function test (glucose, oligomycin and 2-DG injection) should be performed to assess the effect of TB-PE and cmMTB on the macrophages directly.

Depriving glucose is not the best way to show the effect of glucose on HIV infection and MGC formation, as it can affect other aspects of cellular physiology, such as redox and bioenergetics. Instead, the use of galactose in place of glucose would generate ATP only by OXPHOS. Some key experiments should be repeated using galactose as a sole C source.

UK5099 and oxamate nuclei seem smaller and less bright compared to the control. Images between control and UK5099 appear marginally different (non-significant).

The overall impact of the study is limited as the authors provide no evidence on the mechanism of how glycolysis induces TNT formation, which needs to be more characterized.

Minor comments:

The manuscript does not clearly show how the total ATP was calculated from the ATP rate assay.

In figure 1 (and everywhere else) the units on the y-axis should be corrected to [pmol/min] instead of pmol and the Seahorse profiles should mention whether the axis represents OCR or ECAR.

The authors have called the macrophages highly glycolytic in first set of results which is misleading. Although the glycoATP contribution is increasing, overall ATP production is still majorly through oxidative phosphorylation (70% vs 25%).

Fig 3: Why does the HIV gag protein signal appear as irregular large spots?

Referees cross-commenting

I agree with the reviewer# 1 assessment. However, i feel that mechanistically paper could be improved and by performing more experiments.

Significance

The knowledge generated is important and valuable for future studies to understand the molecular players in regulating immunometabolism during HIV-TB coinfection.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In the manuscript entitled "Inhibition of glycolysis in tuberculosis-mediated metabolic rewiring reduces HIV-1 spread across macrophages", Vahlas and colleagues investigated the hypothesis that Mtb interferes with HIV-1 infection of human macrophages, as they represent a common target cell type. In particular, they observed that a conditioned medium generated from Mtb-infected macrophages (Mtb-CM) induces tunneling nanotubes (TNT) in HIV-infected macrophages thereby facilitating viral spreading. At the same time, Mtb-CM induced a glycolytic pathway leading to ATP accumulation in HIV-infected macrophages, an essential pathway for TNT induction whereas pharmacological interference with such a metabolic switch resulted in a reduced viral production.

Experimental approach: primary human monocytes differentiated into monocyte-derived macrophages (MDM) in the presence of a TB-dominated microenvironment (Mtb-CM). The intracellular rate of ATP production was evaluated by the Seahorse technology at day 3 of MDM differentiation. The measurements of basal extracellular acidification rate (ECAR) and basal oxygen consumption rate (OCR) were used to calculate ATP production rate from glycolysis (GlycoATP) and mitochondrial OXPHOS (MitoATP).

This is a well-conducted, innovative study exploring the interaction of two main human pathogens, i.e. Mtb and HIV, sharing macrophages as common target cell. The manuscript is clearly written and the conclusions and hypotheses are supported by experimental evidence. I have two general points that I encourage the authors to address.

1. As mentioned in the Discussion, macrophage infection by HIV is characterized by the accumulation of preformed, infectious virions in VCC (Virus Containing Compartments) that can be pharmacologically modulated both in terms of accumulation and rapid release in the absence of cell cytopathicity. Although the modulation of VCC was not the objective of the present study, it would be important to discuss their role and their potential modulation by Mtb and/or metabolic modifications, if known.
2. Understanding the purpose of using a VSV-g based infection system, nonetheless it would be important to know whether metabolic modulation does affect CD4 and CCR5 expression on MDM and its consequence for their susceptibility to HIV infection, in addition to the effects on TNT formation and viral transfer between cells.

Specific points:

1. "TB-PE" (pleural effusion) is neither specified in the Results nor in the Methods sections.
2. Figure 3A does not seem to display cell viability, but rather HIV Gag expression by IFA. Furthermore, Figure 3C indicates Gag expression, not "HIV infection" (see page 8, Results).

Significance

The paper addresses a poorly explored area, i.e. the interaction of Mtb and HIV during infection of macrophages. The authors focused on a specific aspect of such an interaction (I,e, the modulation of nanotubes formation and transfer of virions to target cells), but their results can be extrapolated in a broader context, particularly if the authors will be willing to address my general questions.

Although specific in its experimental approach, the implication of the study will be of interest to a general audience.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reply to the Reviewers

We thank all the reviewers for their time and their constructive criticism. We are encouraged by the overall positive and enthusiastic responses from the reviewers. We have taken all comments and suggestions seriously and revised the manuscript. These revisions include adding more explanation for the meaning of synaptic learning rules, language definitions, and model characteristics and limitations with more detailed figure legends. We are confident that we have addressed all the reviewer’s concerns by incorporating the reviewer’s suggestions into the revised manuscript. All changes are indicated in red font in the revised manuscript. The point-by-point response to all concerns raised by the reviewers follows. The line numbers indicated here refer to those in the revised manuscript.

Reviewer #1

Major comments:

1. Introduction, line 64 and further: An important omission in the introduction is that several studies have shown that sleep deprivation, i.e., extended wakefulness, results in a loss of spines in some brain regions such as the hippocampus, which is directly opposing the SHY hypothesis (for review, see Raven et al. Sleep Med Rev 39: 3-11, 2018).

Response:

We appreciate the reviewer’s valuable comment. Indeed, as correctly pointed out, several studies have reported synaptic weakening in the hippocampus and cortical regions following sleep deprivation, which appears to contradict the SHY.

We have incorporated this point into the introduction section (lines 64-67), adding several articles, including Raven et al., the reviewer suggested.

1. Introduction, line 85-87: A short explanation of what exactly the anti-Hebbian and anti-STDP rules are, is important here. It may seem obvious to the authors, but it is best to spell it out for the potential broad readership interested in this paper.

Response:

We appreciate the reviewer’s important suggestion.

Previous studies reported that Anti-Hebbian plasticity, which leads to depression when synapses are presented with correlated activity, serves critical functions in the discrimination of specific spike sequences in the cortico-striatal synapses (G. Vignoud et al., Commun. Biol, 2024) and the detection of novel stimuli in mormyrid fish (P. D. Roberts et al., Biol. Cybern, 2008; P. D. Roberts et al, Front. Comput. Neurosci, 2010).

We have added the explanations for Anti-Hebbian and Anti-STDP rules into the introduction section (lines 87-89).

1. Results, line 116, 129/130, 333, 395, 400, figure captions: Pleases explain what is meant with the terms 'pre-neuronal synapse' and 'post-neuronal synapses'.

Response:

We appreciate the reviewer’s advice. We have replaced ‘pre-neuronal synapse’ and ‘post-neuronal synapse’ with ‘pre-synaptic’、’post-synaptic’, respectively, for readability in the Results section (lines 118-119, 131-133, 368, 371, 432, 436 and 437) and Figure legends.

1. Results, line 121-124 say that synaptic efficacy became higher in sleep-like states than in wake-like states under Hebbian and STDP learning rules and opposite results were observed with anti-Hebbian and anti-STDP learning rules. While these relative differences are indeed visible in Figure 1H, the figure also suggests that synaptic efficacy during sleep was largely independent of the average firing frequency. In other words, synaptic efficacy seems to be dependent on firing frequency only during wakefulness. Is that correct?

Response:

The reviewer raised an important point. As shown in Fig. 1H, synaptic efficacy during sleep appears to be largely independent of mean firing rates. Here, the firing rates were adjusted by varying Down-state durations. Regarding the relationship between firing patterns and synaptic efficacy, synaptic efficacy is influenced not only by firing frequency but also by how firing patterns are generated. When firing rates are adjusted by changing ISI, synaptic efficacy during sleep also increases with higher firing rates as wake-like patterns (Fig. 5). In Fig. 2D and E, we demonstrated that the synaptic efficacy during sleep becomes higher than during wakefulness regardless of whether the spike patterns were generated with changing Down-state duration or ISI, assuming the same mean firing rates during the sleep-like and wake-like states. We have clarified this point by adding the explanation in the Discussion section (lines 318-323).

1. Results, line 199 and down model the effect of differences in mean firing rate between sleep and waking, which is a crucial addition and more realistic approach for most brain regions that have lower average firing rates during sleep. It is interesting that in this case the relative effects of sleep and wakefulness can change direction, depending on the average firing frequency. Would the authors argue that this may even result in opposite effects in different brain regions after waking or sleep deprivation?

Response:

We appreciate the reviewer raising the interesting point. Our model predicted that the direction of synaptic changes depends on learning rules and firing rates. This prediction indicated that different brain regions may exhibit synaptic changes even in opposite directions after prolonged wakefulness or sleep deprivation. For example, under Hebbian and STDP, our model predicted that brain regions with firing rates increased during wakefulness or sleep deprivation compared to sleep would follow SHY, while brain regions where firing rates remain unchanged or decreased compared to sleep would follow WISE. The experimental validation of these predictions, focusing on brain regions with different activation states during wakefulness, is an interesting future work. We have clarified this point into the Discussion section (lines 260-262).

1. Figure 1: The caption needs more details to help understand the different panels. some work. (B) What is a post-neuronal synapse? (C) How exactly is synaptic efficacy defined? (E) Not totally clear what the colored top panels represent.

Response:

We sincerely appreciate the reviewer’s thoughtful feedback. We agreed that Figure 1 required a more thorough explanation. In response, we have expanded the figure legend to provide more detailed information for readers to easily understand.

1. Figure 5B. Since this appears to be a graphical abstract and unified framework for all the modelled parameters and learning rules, should this not be a separate figure?

__Response: __We thank the reviewer for the helpful suggestion. We have renumbered Figure 5B as Figure 6.

1. Figures captions: The information provided in the figure captions is in many cases quite minimal and does not reflect the complexity of some of the figure panels. This often makes it hard for a reader to extract all the relevant information without thumbing back and forth between figures, captions and main text. I strongly suggest to add more detail to the figure captions to make them more stand-alone and self-explanatory.

__Response: __We sincerely appreciate the reviewer’s significant feedback. We have added detailed explanations in the figure legends, including Supplementary Figures, for readers to understand easily.

Reviewer #2

Major comments:

1. I am not qualified to review this manuscript because I'm not sufficiently familiar with the type of modelling performed here and the specific use of terms. For example, without providing any explanation, I cannot reconstruct whether the estimates of synaptic efficacy (eq.1) are valid and applicable to the questions asked. I do have 2 general comments. I do find the premise of WISE intriguing and understand the attractiveness of the idea of opposing 'WISE' to SHY. Nevertheless, SHY is a theory that does not discount the occurrence of synaptic strengthening during sleep. It is rather that during sleep there is a net down-scaling. Therefore, the assumptions, as they are presented here, are confusing the issue.

Response:

We are deeply grateful that the reviewer found WISE intriguing and appreciate the insightful comment. We agree that SHY does not deny the occurrence of synaptic strengthening during sleep, but rather proposes a net downward scaling under the assumption of the overall synaptic homeostasis. In the present study, we assumed that SHY describes a net downscaling during sleep (and does not deny the occurrence of synaptic strengthening of some synapses during sleep) while WISE describes a net upscaling during sleep (and does not deny the occurrence of synaptic weakening of some synapses during sleep). Both SHY and WISE fulfill synaptic homeostasis. For example, SHY upscales synaptic strength during wakefulness and downscales during sleep to achieve synaptic homeostasis. On the other hand, WISE upscales synaptic strength during sleep and downscales during wakefulness __to achieve synaptic homeostasis. Our study demonstrated that __WISE is compatible with Hebbian and STDP learning rules when average neuron firing frequency is similar between sleep and wakefulness, and SHY is not compatible with Hebbian and STDP learning rules, but rather compatible with Anti-Hebbian and __Anti-STDP __learning rules.

We agreed with the reviewer that the lack of an explicit definition of SHY and WISE in the context of the present study could cause confusion for readers. Therefore, we have added a sentence to clarify SHY and WISE in the present study in the first paragraph of the Results section (lines 127-128), specifically defining them in terms of relative net synaptic changes within local neural network.

1. SHY was, in part, inspired by a type of plasticity that is not considered here, namely synaptic homeostasis. Would adding such a mechanism to the model alter any of the predictions?"

__Response: __

We appreciate the reviewer raising an important point on synaptic homeostasis. In this study, we did not explicitly include synaptic homeostasis in the preposition but consider synaptic homeostasis in the definitions of SHY and WISE. For example, we assume that SHY upscales synaptic strength during wakefulness and downscales during sleep to achieve synaptic homeostasis while WISE upscales synaptic strength during sleep and downscales during wakefulness to achieve synaptic homeostasis. Importantly, since both SHY and WISE can achieve synaptic homeostasis, there are two types of synaptic homeostasis. In our study, WISE-type synaptic homeostasis is compatible with Hebbian and STDP learning rules when average neuron firing frequency is similar between sleep and wakefulness, and SHY-type synaptic homeostasis is compatible with Anti-Hebbian and __Anti-STDP __learning rules. Since our studies already consider two types of synaptic homeostasis, adding the further mechanism of synaptic homeostasis in the preposition would not alter our predictions. We described these points in the Model characteristics and limitations part in the Discussion section (lines 332-339).

Reviewer #3

Major comments:

1. This is a well-written manuscript that is easily to follow and amply illustrated. The study seems very exciting but unfortunately I am not a mathematician so I cannot attest to the veracity or originality of the model. Assuming it is robust, it does appear to account for a quite a few anomalies (and inaccuracies depicted in textbooks). It would be helpful to discuss the limitations of other models that have been suggested to synaptic functions of sleep.

__Response: __

We appreciated the reviewer’s constructive suggestions. Some computational studies have investigated synaptic changes in neural networks under STDP protocols using Ca2+-based plasticity models (M. Graupner et al., PNAS, 2012; G. Chindemi et al., Nat. Commun, 2022), while other studies have examined how SWO affects synaptic plasticity under STDP conditions (T. Tadros et al., J.Neurosci, 2022). However, these previous studies were limited to a single synaptic learning rule or firing pattern. Our study is the first to comprehensively investigate synaptic dynamics during the sleep-wake cycle by integrating a Ca2+-based plasticity model to represent various types of synaptic learning rules and various simulated sleep-wake firing patterns.

We have added the sentences related to the reviewer’s comments in the Model characteristics and limitations part in the Discussion section (lines 306-312).

1. Much of the neurophysiological data comes from recordings in rodents, so the model is simulating rat EEG signatures-how readily applicable is this to the human condition? Indeed, how readily can they compare between mouse and rat? The authors should expand on this in the discussion section.

Another potential weakness or limitation is the unanswered question of the model can account for sleep/wake changes in other areas of the cortex or thalamus etc.

Does this model apply equally to males and females?

__Response: __

We appreciate the reviewer for raising this significant point. As the reviewer pointed out, we generated firing patterns using parameters derived from rat firing patterns (B. O. Watson et al., Neuron, 2016), such as ISI, Up-state duration, and Down-state duration. While we started our simulations from those parameter sets, we tested a range of different values for each parameter and found consistent results (detailed in Supplementary Materials, Generation of sleep and wake-like firing patterns). The ranges of Up-state and Down-state durations during SWO in mice, rats, and cats are approximately 100-500 milliseconds (M. Steriade et al., J. Neurophysiol, 2001; V. Crunelli et al., Pflugers Arch, 2012), while in humans, Up-state durations range from 250-1000 milliseconds (B. A. Riedner et al., Sleep, 2007), all of which fall within the ranges examined in Figs. 2 D and E. Similarly, wake-state ISI across various species typically range from 2-100 milliseconds (M. Steriade et al., J. Neurophysiol, 2001; G. Maimon et al., Neuron, 2009), mostly within the scope covered in Fig. 2E. Therefore, we suppose our finding in the present study captured universal aspects of synaptic dynamic in the sleep and wake cycles regardless of species, brain region, or sex.

We have added the description in the Model characteristics and limitations part in the Discussion section (lines 312-331).

Minor comments:

Minor typo: ref. 24 is missing page and volume numbers.

__Response: __

Thank you for pointing out this typo. We corrected this by adding the page and volume numbers in Ref. 28 in the revised manuscript.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Understanding the functions of sleep has and remains a key question in neuroscience. A popular hypothesis is that sleep is fundamental to learning and memory and that this can be detected and measured at the level of neural networks and connections as increased synaptic weights across waking states and reduced synaptic weights or depression during sleep states. However, there are many contradictions in the literature and while it is accepted that sleep plays a role in memory consolidation, the molecular/cellular basis of this is far from clear. As considerable experimental data on synaptic function have been collected during sleep and wake states, here the authors turned to modelling how manipulating the rules of synaptic plasticity can illuminate the problem. In this manuscript, the authors report the outcomes of these simulations neuronal oscillations, firing, and synaptic plasticity across sleep-like and wake-like neural states. They report that their simulations can account for several irregularities and highlight differential involvement of spike-firing dependent plasticity (STDP) and anti-STDP in wake and NREM sleep. In particular they note that under Hebbian and STDP rules, firing patterns associated with wake lead to decreased synaptic weights, while sleep-like patterns bolster synaptic weights and collectively they describe this tendency as WISE. They also note that under Anti-Hebbian and Anti-STDP rules, synaptic depression was observed under NREM. The chief strength of this study is shows how simulation can aid in bringing together disparate observations into a well-worked study space.

This is a well-written manuscript that is easily to follow and amply illustrated. The study seems very exciting but unfortunately I am not a mathematician so I cannot attest to the veracity or originality of the model. Assuming it is robust, it does appear to account for a quite a few anomalies (and inaccuracies depicted in textbooks). It would be helpful to discuss the limitations of other models that have been suggested to synaptic functions of sleep.

Much of the neurophysiological data comes from recordings in rodents, so the model is simulating rat EEG signatures-how readily applicable is this to the human condition? Indeed how readily can they compare between mouse and rat? The authors should expand on this in the discussion section.

Another potential weakness or limitation is the unanswered question of the model can account for sleep/wake changes in other areas of the cortex or thalamus etc.

Does this model apply equally to males and females? Minor typo: ref. 24 is missing page and volume numbers.

Significance

As noted above, there are discrepancies in the literature regarding synaptic plasticity and its mechanisms across the sleep-wake cycle. This model appears to answer some of the reasons for these and provides a framework for further experimental research to interrogate these mechanisms.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

I am not qualified to review this manuscript because I'm not sufficiently familiar with the type of modelling performed here and the specific use of terms. For example, without providing any explanation, I cannot reconstruct whether the estimates of synaptic efficacy (eq.1) are valid and applicable to the questions asked.

I do have 2 general comments. I do find the premise of WISE intriguing and understand the attractiveness of the idea of opposing 'WISE' to SHY. Nevertheless, SHY is a theory that does not discount the occurrence of synaptic strengthening during sleep. It is rather that during sleep there is a net down-scaling. Therefore, the assumptions, as they are presented here, are confusing the issue. SHY was, in part, inspired by a type of plasticity that is not considered here, namely synaptic homeostasis. Would adding such a mechanism to the model alter any of the predictions?"

Significance

I do find the premise of WISE intriguing and understand the attractiveness of the idea of opposing 'WISE' to SHY. Nevertheless, SHY is a theory that does not discount the occurrence of synaptic strengthening during sleep. It is rather that during sleep there is a net down-scaling. Therefore, the assumptions, as they are presented here, are confusing the issue. SHY was, in part, inspired by a type of plasticity that is not considered here, namely synaptic homeostasis. Would adding such a mechanism to the model alter any of the predictions?"

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

While the function of sleep is still an unresolved mystery, some of the most influential theories propose that sleep serves a crucial role in regulating neuronal plasticity and synaptic strength. However, the exact way how synaptic strength is affected by sleep and impaired by sleep deprivation is a topic of much controversy and ongoing debate in the field of sleep research (SHY vs WISE). Using computation models, the manuscript illustrates that opposite effects of sleep on synaptic efficacy can be found, depending on the firing patterns and learning rules. Specifically, sleep promotes synaptic strength and efficacy under Hebbian and spike-timing dependent plasticity rules and it resulted in synaptic depression under anti-Hebbian and anti-STDP rules.

Major comments:

Introduction, line 64 and further: An important omission in the introduction is that several studies have shown that sleep deprivation, i.e., extended wakefulness, results in a loss of spines in some brain regions such as the hippocampus, which is directly opposing the SHY hypothesis (for review, see Raven et al. Sleep Med Rev 39: 3-11, 2018).

Introduction, line 85-87: A short explanation of what exactly the anti-Hebbian and anti-STDP rules are, is important here. It may seem obvious to the authors, but it is best to spell it out for the potential broad readership interested in this paper.

Results, line 116, 129/130, 333, 395, 400, figure captions: Pleases explain what is meant with the terms 'pre-neuronal synapse' and 'post-neuronal synapses'.

Results, line 121-124 say that synaptic efficacy became higher in sleep-like states than in wake-like states under Hebbian and STDP learning rules and opposite results were observed with anti-Hebbian and anti-STDP learning rules. While these relative differences are indeed visible in Figure 1H, the figure also suggests that synaptic efficacy during sleep was largely independent of the average firing frequency. In other words, synaptic efficacy seems to be dependent on firing frequency only during wakefulness. Is that correct?

Results, line 199 and down model the effect of differences in mean firing rate between sleep and waking, which is a crucial addition and more realistic approach for most brain regions that have lower average firing rates during sleep. It is interesting that in this case the relative effects of sleep and wakefulness can change direction, depending on the average firing frequency. Would the authors argue that this may even result in opposite effects in different brain regions after waking or sleep deprivation?

Figure 1: The caption needs more details to help understand the different panels. some work. (B) What is a post-neuronal synapse? (C) How exactly is synaptic efficacy defined? (E) Not totally clear what the colored top panels represent.

Figure 5B. Since this appears to be a graphical abstract and unified framework for all the modelled parameters and learning rules, should this not be a separate figure?

Figures captions: The information provided in the figure captions is in many cases quite minimal and does not reflect the complexity of some of the figure panels. This often makes it hard for a reader to extract all the relevant information without thumbing back and forth between figures, captions and main text. I strongly suggest to add more detail to the figure captions to make them more stand-alone and self-explanatory.

Significance

This paper addresses a major controversy in the field of sleep research: does sleep strengthen neuronal connections in the brain or does it downscale and weaken them (Raven et al. 2018)? Using computation models, the current paper shows that both options are possible and it does an admirable job in bridging the different views on sleep and synaptic strength. As such, the conceptual value of this paper can hardly be overestimated and provides an important framework for future experimental studies.

This paper is of interest for most everybody interested in sleep and brain function, as well as neuroscientist with a broader interest in brain plasticity.

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2024-02465

Corresponding author(s): Saravanan, Palani

1. General Statements

We would like to thank the Review Commons Team for handling our manuscript and the Reviewers for their constructive feedback and suggestions. In our revised manuscript, we have addressed and incorporated all the major suggestions of the reviewers, and we have also added new significant data on the role of Tropomyosin in regulation of endocytosis through its control over actin monomer pool maintenance and actin network homeostasis. We believe that with all these additions, our study has significantly gained in quality, strength of conclusions made, and scope for future work.

2. Point-by-point description of the revisions

Reviewer #1

Evidence, reproducibility and clarity

There are 2 Major issues -

Having an -ala-ser- linker between the GFP and tropomyosin mimics acetylation. This is not the case, and more likely the this linker acts as a spacer that allows tropomyosin polymers to form on the actin, and without it there is steric hindrance. A similar result would be seen with a simple flexible uncharged linker. It has been shown in a number of labs that the GFP itself masks the effect of the charge on the amino terminal methionine. This is consistent with NMR, crystallographic and cryo structural studies. Biochemical studies should be presented to demonstrate that the impact of a linker for the conclusions stated to be made, which provide the basis of a major part of this study.

Response: We would like to clarify that all mNG-Tpm constructs used in our study contain a 40 amino-acid (aa) flexible linker between the N-terminal mNG fluorescent protein and the Tpm protein as per our earlier published study (Hatano et al., 2022). During initial optimization, we have also experimented with linker length and the 40aa-linker length works optimally for clear visualization of Tpm onto actin cable structures in budding yeast, fission yeast (both S. pombe and S. japonicus), and mammalian cells (Hatano et al., 2022). These constructs have also been used since in other studies (Wirshing et al., 2023; Wirshing and Goode, 2024) and currently represents the best possible strategy to visualize Tpm isoforms in live cells. In our study, we characterized these proteins for functionality and found that both mNG-Tpm1 and mNG-Tpm2 were functional and can rescue the synthetic lethality observed in Dtpm1Dtpm2 cells. During our study, we observed that mNG-Tpm1 expression from a single-copy integration vector did not restore full length actin cables in Dtpm1 cells (Fig. 1B, 1C). We hypothesized that this could be a result of reduced binding affinity of the tagged tropomyosin due to lack of normal N-terminal acetylation which stabilizes the N-terminus. The 40aa linker is unstructured and may not be able to neutralize the charge on the N-terminal Methionine, thus, we tried to insert -Ala-Ser- dipeptide which has been routinely used in vitro biochemical studies to stabilize the N-terminal helix and impart a similar effect as the N-terminal acetylation (Alioto et al., 2016; Palani et al., 2019; Christensen et al., 2017) by restoring normal binding affinity of Tpm to F-actin (Monteiro et al., 1994; Greenfield et al., 1994). We observed that addition of the -Ala-Ser- dipeptide to mNG-Tpm fusion, indeed, restored full length actin cables when expressed in Dtpm1 cells, performing significantly better in our in vivo experiments (Fig. 1B, 1C). We agree with the reviewer that the -AS- dipeptide addition may not mimic N-terminal acetylation structurally but as per previous studies, it may stabilize the N-terminus of Tpm and allow normal head-to-tail dimer formation (Greenfield et al., 1994; Monteiro et al., 1994; Frye et al., 2010). We have discussed this in our new Discussion section (Lines 350-372). Since, the addition of -AS- dipeptide was referred to as "acetyl-mimic (am)" in a previous study (Alioto et al., 2016), we continued to use the same nomenclature in our study. Now as per your suggestions and to be more accurate, we have renamed "mNG-amTpm" constructs as "mNG-ASTpm" throughout the study to not confuse or claim that -AS- addition mimics acetylation. In any case, we have not seen any other ill effect of -AS- dipeptide introduction in addition to our 40 amino acid linker suggesting that it can also be considered part of the linker. Although, we agree with the reviewer that biochemical characterization of the effect of linker would be important to determine, we strongly believe that it is currently outside the scope of this study and should be taken up for future work with these proteins. Our study has majorly aimed to understand the functionality and utility of these mNG-Tpm fusion proteins for cell biological experiments in vivo, which was not done earlier in any other model system.

My major issue however is making the conclusions stated here, using an amino-terminal fluorescent protein tag that s likely to impact any type of isoform selection at the end of the actin polymer. Carboxyl terminal tagging may have a reduced effect, but modifying the ends of the tropomyosin, which are integral in stabilising end to end interactions with itself on the actin filament, never mind any section systems that may/maynot be present in the cell, is not appropriate.

Response: __ We agree with the reviewer that N-terminal tagging of tropomyosin may have effects on its function, but these constructs represent the only fluorescently tagged functional tropomyosin constructs available currently while C-terminal fusions are either non-functional (we were unable to construct strains with endogenous Tpm1 gene fused C-terminally to GFP) or do not localize clearly to actin structures (See __Figure R1 showing endogenous C-terminally tagged Tpm2-yeGFP that shows almost no localization to actin cables). To our knowledge, our study represents a first effort to understand the question of spatial sorting of Tpm isoforms, Tpm1 and Tpm2, in S. cerevisiae and any future developments with better visualization strategies for Tpm isoforms without compromising native N-terminal modifications and function will help improve our understanding of these proteins in vivo. We have also discussed these possibilities in our new Discussion section (Lines 391-396).

Significance

This paper explores the role of formin in determining the localisation of different tropomyosins to different actin polymers and cellular locations within budding yeast. Previous studies have indicated a role for the actin nucleating proteins in recruiting different forms of tropomyosin within fission yeast. In mammalian cells there is variation in the role of formins in affiecting tropomyosin localisation - variation between cell type. There is also evidence that other actin binding proteins, and tropomyosin abundance play roles in regulating the tropomyosin-actin association according to cell type. Biochemical studies have previously been undertaken using budding yeast and fission yeast that the core actin polymerisation domain of formins do not interact with tropomyosin directly. The significance of this study, given the above, and the concerns raised is not clear to this reviewer.

Response: __Our study explores multiple facets of Tropomyosin (Tpm) biology. The lack of functional tagged Tpm has been a major bottleneck in understanding Tpm isoform diversity and function across eukaryotes. In our study, we characterize the first functional tagged Tpm proteins (Fig. 1, Fig. S1) and use them to answer long-standing questions about localization and spatial sorting of Tpm isoforms in the model organism S. cerevisiae (Fig. 2, Fig. 3, Fig. S2, Fig. S3). We also discover that the dual Tpm isoforms, Tpm1 and Tpm2, are functionally redundant for actin cable organization and function, while having gained divergent functions in Retrograde Actin Cable Flow (RACF) (Fig. 4, Fig. 5A-D, Fig. S4, Fig. S5, Fig. S6). We have now added new data on role of global Tpm levels controlling endocytosis via maintenance of normal linear-to-branched actin network homeostasis in S. cerevisiae (Fig. 5E-G)__. We respectfully differ with the reviewer on their assessment of our study and request the reviewer to read our revised manuscript which discusses the significance, limitations, and future perspectives of our study in detail.

Reviewer #2

Evidence, reproducibility and clarity

This manuscript by Dhar, Bagyashree, Palani and colleagues examines the function of the two tropomyosins, Tpm1 and Tpm2, in the budding yeast S. cerevisiae. Previous work had shown that deletion of tpm1 and tpm2 causes synthetic lethality, indicating overlapping function, but also proposed that the two tropomyosins have distinct functions, based on the observation that strong overexpression of Tpm2 causes defects in bud placement and fails to rescue tpm1∆ phenotypes (Drees et al, JCB 1995). The manuscript first describes very functional mNeonGreen tagged version of Tpm1 and Tpm2, where an alanine-serine dipeptide is inserted before the first methionine to mimic acetylation. It then proposes that the Tpm1 and Tpm2 exhibit indistinguishable localization and that low level overexpression (?) of Tpm2 can replace Tpm1 for stabilization of actin cables and cell polarization, suggesting almost completely redundant functions. They also propose on specific function of Tpm2 in regulating retrograde actin cable flow.

Overall, the data are very clean, well presented and quantified, but in several places are not fully convincing of the claims. Because the claims that Tpm1 and Tpm2 have largely overlapping function and localization are in contradiction to previous publication in S. cerevisiae and also different from data published in other organisms, it is important to consolidate them. There are fairly simple experiments that should be done to consolidate the claims of indistinguishable localization, and levels of expression, for which the authors have excellent reagents at their disposal.

1. Functionality of the acetyl-mimic tagged tropomyosin constructs: The overall very good functionality of the tagged Tpm constructs is convincing, but the authors should be more accurate in their description, as their data show that they are not perfectly functional. For instance, the use of "completely functional" in the discussion is excessive. In the results, the statement that mNG-Tpm1 expression restores normal growth (page 3, line 69) is inaccurate. Fig S1C shows that tpm1∆ cells expressing mNG-Tpm1 grow more slowly than WT cells. (The next part of the same sentence, stating it only partially restores length of actin cables should cite only Fig S1E, not S1F.) Similarly, the growth curve in Fig S1C suggests that mNG-amTpm1, while better than mNG-Tpm1 does not fully restore the growth defect observed in tpm1∆ (in contrast to what is stated on p. 4 line 81). A more stringent test of functionality would be to probe whether mNG-amTpm1 can rescue the synthetic lethality of the tpm1∆ tpm2∆ double mutant, which would also allow to test the functionality of mNG-amTpm2.

__Response: __We would like to thank the reviewer for his feedback and suggestions. Based on the suggestions, we have now more accurately described the growth rescue observed by expression of mNG-ASTpm1 in Dtpm1 cells in the revised text. We have also removed the use of "completely functional" to describe mNG-Tpm functionality and corrected any errors in Figure citations in the revised manuscript.

As per reviewers' suggestion, we have now tested rescue of synthetic lethality of Dtpm1Dtpm2 cells by expression of all mNG-Tpm variants and we find that all of them are capable of restoring the viability of Dtpm1Dtpm2 cells when expressed under their native promoters via a high-copy plasmid (pRS425) (Fig. S1E) but only mNG-Tpm1 and mNG-ASTpm1 restored viability of Dtpm1Dtpm2 cells when expressed under their native promoters via an integration plasmid (pRS305) (Fig. S1F). These results clearly suggest that while both mNG-Tpm1 and mNG-Tpm2 constructs are functional, Tpm1 tolerates the presence of the N-terminal fluorescent tag better than Tpm2. These observations now enhance our understanding of the functionality of these mNG-Tpm fusion proteins and will be a useful resource for their usage and experimental design in future studies in vivo.

---

It would also be nice to comment on whether the mNG-amTpm constructs really mimicking acetylation. Given the Ala-Ser peptide ahead of the starting Met is linked N-terminally to mNG, it is not immediately clear it will have the same effect as a free acetyl group decorating the N-terminal Met.

Response: __We agree with the reviewer's observation and for the sake of clarity and accuracy, we have now renamed "mNG-amTpm" with "mNG-ASTpm". The use of -AS- dipeptide is very routine in studies with Tpm (Alioto et al., 2016; Palani et al., 2019; Christensen et al., 2017) and its addition restores normal binding affinities to Tpm proteins purified from E. coli (Monteiro et al., 1994). We agree with the reviewer that the -AS- dipeptide addition may not mimic N-terminal acetylation structurally but as per previous studies, it may help neutralize the impact of a freely protonated Met on the alpha-helical structure and stabilize the N-terminus helix of Tpm and allow normal head-to-tail dimer formation (Monteiro et al., 1994; Frye et al., 2010; Greenfield et al., 1994). Consistent with this, we also observe a highly significant improvement in actin cable length when expressing mNG-ASTpm as compared to mNG-Tpm in Dtpm1 cells, suggesting an improvement in function probably due to increased binding affinity (Fig. 1B, 1C). We have also discussed this in our answer to Question 1 of Reviewer 1 and the revised manuscript (Lines 350-372)__.

__ Localization of Tpm1 and Tpm2:__Given the claimed full functionality of mNG-amTpm constructs and the conclusion from this section of the paper that relative local concentrations may be the major factor in determining tropomyosin localization to actin filament networks, I am concerned that the analysis of localization was done in strains expressing the mNG-amTpm construct in addition to the endogenous untagged genes. (This is not expressly stated in the manuscript, but it is my understanding from reading the strain list.) This means that there is a roughly two-fold overexpression of either tropomyosin, which may affect localization. A comparison of localization in strains where the tagged copy is the sole Tpm1 (respectively Tpm2) source would be much more conclusive. This is important as the results are making a claim in opposition to previous work and observation in other organisms.

Response: __We thank the reviewer for this observation and their suggestions. We agree that relative concentrations of functional Tpm1 and Tpm2 in cells may influence the extent of their localizations. As per the reviewer's suggestion, we have now conducted our quantitative analysis in cells lacking endogenous Tpm1 and only expressing mNG-ASTpm1 from an integrated plasmid copy at the leu2 locus and the data is presented in new __Figure S3. We compared Tpm-bound cable length (Fig. S3A, S3B) __and Tpm-bound cable number (Fig. S3A, S3C) along with actin cable length (Fig. S3D, S3E) and actin cable number (Fig. S3D, S3F) in wildtype, Dbnr1, and Dbni1 cells. Our analysis revealed that mNG-ASTpm1 localized to actin cable structures in wildtype, Dbnr1, and Dbni1 cells and the decrease observed in Tpm-bound cable length and number upon loss of either Bnr1 or Bni1, was accompanied by a corresponding decrease in actin cable length and number upon loss of either Bnr1 or Bni1. Thus, this analysis reached the same conclusion as our earlier analysis (Fig. 2) that mNG-ASTpm1 does not show preference between Bnr1 and Bni1-made actin cables. mNG-ASTpm2 did not restore functionality, when expressed as single integrated copy, in Dtpm1Dtpm2 cells (new results in __Fig. S1E, S1F, S5A) thus, we could not conduct a similar analysis for mNG-ASTpm2. This suggests that use of mNG-ASTpm2 would be more meaningful in the presence of endogenous Tpm2 as previously done in Fig. 2D-F.

We have now also performed additional yeast mating experiments with cells lacking bnr1 gene and expressing either mNG-ASTpm1 or mNG-ASTpm2 and the data is shown in new Figure 3. From these observations, we observe that both mNG-ASTpm1 and mNG-ASTpm2 localize to the mating fusion focus in a Bnr1-independent manner (Fig. 3B, 3D) and suggests that they bind to Bni1-made actin cables that are involved in polarized growth of the mating projection. These results also add strength to our conclusion that Tpm1 and Tpm2 localize to actin cables irrespective of which formin nucleates them. Overall, these new results highlight and reiterate our model of formin-isoform independent binding of Tpm1 and Tpm2 in S. cerevisiae.

In fact, although the authors conclude that the tropomyosins do not exhibit preference for certain actin structures, in the images shown in Fig 2A and 2D, there seems to be a clear bias for Tpm1 to decorate cables preferentially in the bud, while Tpm2 appears to decorate them more in the mother cell. Is that a bias of these chosen images, or does this reflect a more general trend? A quantification of relative fluorescence levels in bud/mother may be indicative.

Response: __We thank the reviewer for pointing this out. Our data and analysis do not suggest that Tpm1 and Tpm2 show any preference for decoration of cables in either mother or bud compartment. As per the reviewer's suggestion, we have now quantified the ratio of mean mNG fluorescence in the bud to the mother (Bud/Mother) and the data is shown in __Figure. S2G. The bud-to-mother ratio was similar for mNG-ASTpm1 and mNG-ASTpm2 in wildtype cells, and the ratio increased in Dbnr1 cells and decreased in Dbni1 cells for both mNG-ASTpm1 and mNG-ASTpm2 (Fig. S2G). __This is consistent with the decreased actin cable signal in the mother compartment in Dbnr1 cells and decreased actin cable signal in the bud compartment in Dbni1 cells (Fig. S2A-D). Thus, our new analysis shows that both mNG-ASTpm1 and mNG-ASTpm2 have similar changes in their concentration (mean fluorescence) upon loss of either formins Bnr1 and Bni1 and show similar ratios in wildtype cells as well, suggesting no preference for binding to actin cables in either bud or mother compartment. The preference inferred by the reviewer seems to be a bias of the current representative images and thus, we have replaced the images in __Fig. 2A, 2D to more accurately represent the population.

The difficulty in preserving mNG-amTpm after fixation means that authors could not quantify relative Tpm/actin cable directly in single fixed cells. Did they try to label actin cables with Lifeact instead of using phalloidin, and thus perform the analysis in live cells?

__Response: __We did not use LifeAct for our analysis as LifeAct is known to cause expression-dependent artefacts in cells (Courtemanche et al., 2016; Flores et al., 2019; Xu and Du, 2021) and it also competes with proteins that regulate normal cable organization like cofilin. Use of LifeAct would necessitate standardization of expression to avoid such artefacts in vivo. Also, phalloidin staining provides the best staining of actin cables and allows for better quantitative results in our experiments. The use of LifeAct along with mNG-Tpm would also require optimization with a red fluorescent protein which usually tend to have lower brightness and photostability. However, during the revision of our study, a new study from Prof. Goode's lab has developed and optimized expression of new LifeAct-3xmNeonGreen constructs for use in S. cerevisiae (Wirshing and Goode, 2024). Thus, a similar strategy of using tandem copies of bright and photostable red fluorescent proteins can be explored for use in combination with mNG-Tpm in the future studies.

__ Complementation of tpm1∆ by Tpm2:__

I am confused about the quantification of Tpm2 expression by RT-PCR shown in Fig S3F. This figure shows that tpm2 mRNA expression levels are identical in cells with an empty plasmid or with a tpm2-encoding plasmid. In both strains (which lack tpm1), as well as in the WT control, one tpm2 copy is in the genome, but only one strain has a second tpm2 copy expressed from a centromeric plasmid, yet the results of the RT-PCR are not significantly different. (If anything, the levels are lower in the tpm2 plasmid-containing strain.) The methods state that the primers were chosen in the gene, so likely do not distinguish the genomic from the plasmid allele. However, the text claims a 1-fold increase in expression, and functional experiments show a near-complete rescue of the tpm1∆ phenotype. This is surprising and confusing and should be resolved to understand whether higher levels of Tpm2 are really the cause of the observed phenotypic rescue.

The authors could for instance probe for protein levels. I believe they have specific nanobodies against tropomyosin. If not, they could use expression of functional mNG-amTpm2 to rescue tpm1∆. Here, the expression of the protein can be directly visualized.

Response: __We thank the reviewer for pointing this out. We would like to clarify that in our RT-qPCR experiments, the primers were chosen within the Tpm1 and Tpm2 gene and do not distinguish between transcripts from endogenous or plasmid copy. We have now mentioned this in the Materials and Methods section of the revised manuscript. So, they represent a relative estimate of the total mRNA of these genes present in cells. We were consistently able to detect ~19 fold increase in Tpm2 total mRNA levels as compared to wildtype and ∆tpm1 cells (Fig. S4D) when tpm2 was expressed from a high-copy plasmid (pRS425). This increase in Tpm2 mRNA levels was accompanied by a rescue in growth (Fig. S4A) and actin cable organization (Fig. S4B) of ∆tpm1 cells containing pRS425-ptpm2TPM2. When tpm2 was expressed from a low-copy number centromeric plasmid (pRS316), we detected a ~2 fold increase in Tpm2 transcript levels when using the tpm1 promoter and no significant change was detected when using tpm2 promoter (Fig. S4E)__. We have made sure that these results are accurately described in the revised manuscript.

As per the reviewer's suggestion, we have now conducted a more extensive analysis to ascertain the expression levels of Tpm2 in our experiments and the data is now presented in new Figure S5. We used mNG-ASTpm1 and mNG-ASTpm2 to rescue growth of ∆tpm1 (Fig. S5A) and correlated growth rescue with protein levels using quantified fluorescence intensity (Fig. S5B, S5C) and western blotting (anti-mNG) (Fig. S5D, S5E). We find that ∆tpm1 cells containing pRS425-ptpm1mNG-ASTpm1 had the highest protein level followed by pRS425-ptpm2 mNG-ASTpm2, pRS305-ptpm1mNG-ASTpm1, and the least protein levels were found in pRS305-ptpm2 mNG-ASTpm2 containing ∆tpm1 cells in both fluorescence intensity and western blotting quantifications (Fig. S5C, S5E). Surprisingly, we were not able to detect any protein levels in ∆tpm1 cells containing pRS305-ptpm2 mNG-ASTpm2 with western blotting (Fig. S5D) which was also accompanied by a lack of growth rescue (Fig. S5A). This most likely due to weak expression from the native Tpm2 promoter which is consistent with previous literature (Drees et al., 1995). Taken together, this data clearly shows that the rescue observed in ∆tpm1 cells is caused due to increased expression of mNG-ASTpm2 in cells and supports our conclusion that increase in Tpm2 expression leads to restoration of normal growth and actin cables in ∆tpm1 cells.

__ Specific function of Tpm2:__

The data about the retrograde actin flow is interpreted as a specific function of Tpm2, but there is no evidence that Tpm1 does not also share this function. To reach this conclusion one would have to investigate retrograde actin flow in tpm1∆ (difficult as cables are weak) or for instance test whether Tpm1 expression restores normal retrograde flow to tpm2∆ cells.

Response: __We agree with the reviewer and as per the reviewer's suggestion, we have performed another experiment which include wildtype, ∆tpm2 cells containing empty pRS316 vector or pRS316-ptpm2TPM1 or pRS316-ptpm1TPM1. We find that RACF rate increased in ∆tpm2 cells as compared to wildtype and was restored to wildtype levels by exogenous expression of Tpm2 but not Tpm1 (Fig. S6E, S6F). Since, actin cables were not detectable in ∆tpm1 cells, we measured RACF rates in ∆tpm1 cells expressing Tpm1 or Tpm2 from a plasmid copy, which restored actin cables as shown previously in __Fig. 5A-C. We observed that RACF rates were similar to wildtype in ∆tpm1 cells expressing either Tpm1 or Tpm2 (Fig. S6E, S6F), suggesting that Tpm1 is not involved in RACF regulation. Taken together, these results suggest a specific role for Tpm2, but not Tpm1, in RACF regulation in S. cerevisiae, consistent with previous literature (Huckaba et al., 2006).

Minor comments: __1.__The growth of tpm1∆ with empty plasmid in Fig S3A is strangely strong (different from other figures).

Response: __ We thank the reviewer for pointing this out. We have now repeated the drop test multiple times (__Fig. R2), but we see similar growth rates as the drop test already presented in Fig. S4A. __At this point, it would be difficult to ascertain the basis of this difference observed at 23{degree sign}C and 30{degree sign}C, but a recent study that links leucine levels to actin cable stability (Sing et al., 2022) might explain the faster growth of these ∆tpm1 cells containing a leu2 gene carrying high-copy plasmid. However, there is no effect on growth rate at 37{degree sign}C which is consistent with other spot assays shown in __Fig. S1D, S4F, S5A.

---

Significance

I am a cell biologist with expertise in both yeast and actin cytoskeleton.

The question of how tropomyosin localizes to specific actin networks is still open and a current avenue of study. Studies in other organisms have shown that different tropomyosin isoforms, or their acetylated vs non-acetylated versions, localize to distinct actin structures. Proposed mechanisms include competition with other ABPs and preference imposed by the formin nucleator. The current study re-examines the function and localization of the two tropomyosin proteins from the budding yeast and reaches the conclusion that they co-decorate all formin-assembled structures and also share most functions, leading to the simple conclusion that the more important contribution of Tpm1 is simply linked to its higher expression. Once consolidated, the study will appeal to researchers working on the actin cytoskeleton.

We thank the reviewer for their positive assessment of our work and the constructive feedback that has greatly improved the quality of our study. After addressing the points raised by the reviewer, we believe that our study has significantly gained in consolidating the major conclusions of our work.

**Referees cross-commenting**

Having read the other reviewers' comments, I do agree with reviewer 1 that it is not clear whether the Ala-Ser linker really mimics acetylation. I am less convinced than reviewer 3 that the key conclusions of the study are well supported, notably the issue of Tpm2 expression levels is not convincing to me.

Response: __We acknowledge the reviewer's point about the effect of Ala-Ser dipeptide and would request the reviewer to refer to our response to Reviewer 1 (Question 1) for a more detailed discussion on this. We have also extensively addressed the question of Tpm2 expression levels as suggested by the reviewer (new data in __Figure S5) which has further strengthened the conclusions of our study.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Summary:__ The study presents the first fully functional fluorescently tagged Tpm proteins, enabling detailed probing of Tpm isoform localization and functions in live cells. The authors created a modified fusion protein, mNG-amTpm, which mimicked native N-terminal acetylation and restored both normal growth and full-length actin cables in yeast cells lacking native Tpm proteins, demonstrating the constructs' full functionality. They also show that Tpm1 and Tpm2 do not have a preference for actin cables nucleated by different formins (Bnr1 and Bni1). Contrary to previous reports, the study found that overexpressing Tpm2 in Δtpm1 cells could restore growth rates and actin cable formation. Furthermore, it is shown that despite its evolutionary divergence, Tpm2 retains actin-protective functions and can compensate for the loss of Tpm1, contributing to cellular robustness.

Major and Minor Comments: 1. The key conclusions of this paper are convincing. However, I suggest that more detail be provided regarding the image analysis used in this study. Specifically, since threshold settings can impact the quality of the generated data and, therefore, its interpretation, it would be useful to see a representative example of the quantification methods used for actin cable length/number (as in refs. 80 and 81) and mitochondria morphology. These could be presented as Supplemental Figures. Additionally, it would help to interpret the results if the authors could be more specific about the statistical tests that were used.

Response: __We agree with the reviewer's suggestions and have now updated our Materials and Methods section to describe the image analysis pipelines used in more detail. We have also added examples of quantification procedure for actin cable length/number and mitochondrial morphology as an additional Supplementary __Figure S7. Briefly, the following pipelines were used:

• Actin cable length and number analysis: This was done exactly as mentioned in McInally et al., 2021, McInally et al., 2022. Actin cables were manually traced in Fiji as shown in __ S7A__, and then the traces files for each cell were run through a Python script (adapted from McInally et al., 2022) that outputs mean actin cable length and number per cell.
• Mitochondria morphology: Mitochondria Analyzer plug-in in Fiji was used to segment out the mitochondrial fragments. The parameters used for 2D segmentation of mitochondria were first optimized using "2D Threshold Optimize" to find the most accurate segmentation and then the same parameters were run on all images. After segmentation of the mitochondrial network, measurements of fragment number were done using "Analyze Particles" function in Fiji. An example of the overall process is shown in __ S7B.__ As per the reviewer's suggestion, we have now included the description of the statistical test used in the Figure Legends of each Figure in the revised manuscript. We have used One-Way Anova with Tukey's Multiple Comparison test, Kruskal-Wallis test with Dunn's Multiple Comparisons, and Unpaired Two-tailed t-test using the in-built functions in GraphPad Prism (v.6.04).

**Referees cross-commenting**

I agree with both reviewers 1 and 2 regarding the issues with the Ala-Ser acetylation mimic and Tpm2 expression levels, respectively. I think the authors should be more careful in how they frame the results, but I consider that these issues do not invalidate the main conclusions of this study.

Response: __We acknowledge the reviewer's concern about the Ala-Ser dipeptide and would request them to refer our earlier discussion on this in response to Reviewer 1 (Question 1) and Reviewer 2 (Question 2). We would also request the reviewer to refer to our answer to Reviewer 2 (Question 6) where we have extensively addressed the question of Tpm2 expression levels and their effect on rescue of Dtpm1 cells. This data is now presented as new __Figure S5 in our revised manuscript.

Reviewer#3 (Significance (Required)):

The finding that Tpm2 can compensate for the loss of Tpm1, restoring actin cable organization and normal growth rates, challenges previous assumptions about the non-redundant functions of these isoforms in Saccharomyces cerevisiae (ref. 16). It also supports a concentration-dependent and formin-independent localization of Tpm isoforms to actin cables in this species. The development of fully functional fluorescently tagged Tpm proteins is a significant methodological advancement. This advancement overcomes previous visualization challenges and allows for accurate in vivo studies of Tpm function and regulation in S. cerevisiae.

The findings will be of particular interest to researchers in the field of cellular and molecular biology who study actin cytoskeleton dynamics. Additionally, it will be relevant for those utilizing advanced microscopy and live-cell imaging techniques.

As a researcher, my experience lies in cytoskeleton dynamics and protein interactions, though I do not have specific experience related to tropomyosin. I use different yeast species as models and routinely employ live-cell imaging as a tool.

We thank the reviewer for their positive outlook and assessment of our study. We have incorporated all their suggestions, and we are confident that the revised manuscript has significantly improved in quality due to these additions.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

The study presents the first fully functional fluorescently tagged Tpm proteins, enabling detailed probing of Tpm isoform localization and functions in live cells. The authors created a modified fusion protein, mNG-amTpm, which mimicked native N-terminal acetylation and restored both normal growth and full-length actin cables in yeast cells lacking native Tpm proteins, demonstrating the constructs' full functionality. They also show that Tpm1 and Tpm2 do not have a preference for actin cables nucleated by different formins (Bnr1 and Bni1). Contrary to previous reports, the study found that overexpressing Tpm2 in Δtpm1 cells could restore growth rates and actin cable formation. Furthermore, it is shown that despite its evolutionary divergence, Tpm2 retains actin-protective functions and can compensate for the loss of Tpm1, contributing to cellular robustness.

Major and Minor Comments:

The key conclusions of this paper are convincing. However, I suggest that more detail be provided regarding the image analysis used in this study. Specifically, since threshold settings can impact the quality of the generated data and, therefore, its interpretation, it would be useful to see a representative example of the quantification methods used for actin cable length/number (as in refs. 80 and 81) and mitochondria morphology. These could be presented as Supplemental Figures. Additionally, it would help to interpret the results if the authors could be more specific about the statistical tests that were used.

Referees cross-commenting

I agree with both reviewers 1 and 2 regarding the issues with the Ala-Ser acetylation mimic and Tpm2 expression levels, respectively. I think the authors should be more careful in how they frame the results, but I consider that these issues do not invalidate the main conclusions of this study.

Significance

The finding that Tpm2 can compensate for the loss of Tpm1, restoring actin cable organization and normal growth rates, challenges previous assumptions about the non-redundant functions of these isoforms in Saccharomyces cerevisiae (ref. 16). It also supports a concentration-dependent and formin-independent localization of Tpm isoforms to actin cables in this species. The development of fully functional fluorescently tagged Tpm proteins is a significant methodological advancement. This advancement overcomes previous visualization challenges and allows for accurate in vivo studies of Tpm function and regulation in S. cerevisiae.

The findings will be of particular interest to researchers in the field of cellular and molecular biology who study actin cytoskeleton dynamics. Additionally, it will be relevant for those utilizing advanced microscopy and live-cell imaging techniques.

As a researcher, my experience lies in cytoskeleton dynamics and protein interactions, though I do not have specific experience related to tropomyosin. I use different yeast species as models and routinely employ live-cell imaging as a tool.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

This manuscript by Dhar, Bagyashree, Palani and colleagues examines the function of the two tropomyosins, Tpm1 and Tpm2, in the budding yeast S. cerevisiae. Previous work had shown that deletion of tpm1 and tpm2 causes synthetic lethality, indicating overlapping function, but also proposed that the two tropomyosins have distinct functions, based on the observation that strong overexpression of Tpm2 causes defects in bud placement and fails to rescue tpm1∆ phenotypes (Drees et al, JCB 1995). The manuscript first describes very functional mNeonGreen tagged version of Tpm1 and Tpm2, where an alanine-serine dipeptide is inserted before the first methionine to mimic acetylation. It then proposes that the Tpm1 and Tpm2 exhibit indistinguishable localization and that low level overexpression (?) of Tpm2 can replace Tpm1 for stabilization of actin cables and cell polarization, suggesting almost completely redundant functions. They also propose on specific function of Tpm2 in regulating retrograde actin cable flow.

Overall, the data are very clean, well presented and quantified, but in several places are not fully convincing of the claims. Because the claims that Tpm1 and Tpm2 have largely overlapping function and localization are in contradiction to previous publication in S. cerevisiae and also different from data published in other organisms, it is important to consolidate them. There are fairly simple experiments that should be done to consolidate the claims of indistinguishable localization, and levels of expression, for which the authors have excellent reagents at their disposal.

Functionality of the acetyl-mimic tagged tropomyosin constructs:

The overall very good functionality of the tagged Tpm constructs is convincing, but the authors should be more accurate in their description, as their data show that they are not perfectly functional. For instance, the use of "completely functional" in the discussion is excessive. In the results, the statement that mNG-Tpm1 expression restores normal growth (page 3, line 69) is inaccurate. Fig S1C shows that tpm1∆ cells expressing mNG-Tpm1 grow more slowly than WT cells. (The next part of the same sentence, stating it only partially restores length of actin cables should cite only Fig S1E, not S1F.) Similarly, the growth curve in Fig S1C suggests that mNG-amTpm1, while better than mNG-Tpm1 does not fully restore the growth defect observed in tpm1∆ (in contrast to what is stated on p. 4 line 81). A more stringent test of functionality would be to probe whether mNG-amTpm1 can rescue the synthetic lethality of the tpm1∆ tpm2∆ double mutant, which would also allow to test the functionality of mNG-amTpm2.

It would also be nice to comment on whether the mNG-amTpm constructs really mimicking acetylation. Given the Ala-Ser peptide ahead of the starting Met is linked N-terminally to mNG, it is not immediately clear it will have the same effect as a free acetyl group decorating the N-terminal Met.

Localization of Tpm1 and Tpm2:

Given the claimed full functionality of mNG-amTpm constructs and the conclusion from this section of the paper that relative local concentrations may be the major factor in determining tropomyosin localization to actin filament networks, I am concerned that the analysis of localization was done in strains expressing the mNG-amTpm construct in addition to the endogenous untagged genes. (This is not expressly stated in the manuscript, but it is my understanding from reading the strain list.) This means that there is a roughly two-fold overexpression of either tropomyosin, which may affect localization. A comparison of localization in strains where the tagged copy is the sole Tpm1 (respectively Tpm2) source would be much more conclusive. This is important as the results are making a claim in opposition to previous work and observation in other organisms.

In fact, although the authors conclude that the tropomyosins do not exhibit preference for certain actin structures, in the images shown in Fig 2A and 2D, there seems to be a clear bias for Tpm1 to decorate cables preferentially in the bud, while Tpm2 appears to decorate them more in the mother cell. Is that a bias of these chosen images, or does this reflect a more general trend? A quantification of relative fluorescence levels in bud/mother may be indicative.

The difficulty in preserving mNG-amTpm after fixation means that authors could not quantify relative Tpm/actin cable directly in single fixed cells. Did they try to label actin cables with Lifeact instead of using phalloidin, and thus perform the analysis in live cells?

Complementation of tpm1∆ by Tpm2:

I am confused about the quantification of Tpm2 expression by RT-PCR shown in Fig S3F. This figure shows that tpm2 mRNA expression levels are identical in cells with an empty plasmid or with a tpm2-encoding plasmid. In both strains (which lack tpm1), as well as in the WT control, one tpm2 copy is in the genome, but only one strain has a second tpm2 copy expressed from a centromeric plasmid, yet the results of the RT-PCR are not significantly different. (If anything, the levels are lower in the tpm2 plasmid-containing strain.) The methods state that the primers were chosen in the gene, so likely do not distinguish the genomic from the plasmid allele. However, the text claims a 1-fold increase in expression, and functional experiments show a near-complete rescue of the tpm1∆ phenotype. This is surprising and confusing and should be resolved to understand whether higher levels of Tpm2 are really the cause of the observed phenotypic rescue. The authors could for instance probe for protein levels. I believe they have specific nanobodies against tropomyosin. If not, they could use expression of functional mNG-amTpm2 to rescue tpm1∆. Here, the expression of the protein can be directly visualized.

Specific function of Tpm2:

The data about the retrograde actin flow is interpreted as a specific function of Tpm2, but there is no evidence that Tpm1 does not also share this function. To reach this conclusion one would have to investigate retrograde actin flow in tpm1∆ (difficult as cables are weak) or for instance test whether Tpm1 expression restores normal retrograde flow to tpm2∆ cells.

Minor comments:

The growth of tpm1∆ with empty plasmid in Fig S3A is strangely strong (different from other figures).

Referees cross-commenting

Having read the other reviewers' comments, I do agree with reviewer 1 that it is not clear whether the Ala-Ser linker really mimics acetylation. I am less convinced than reviewer 3 that the key conclusions of the study are well supported, notably the issue of Tpm2 expression levels is not convincing to me.

Significance

I am a cell biologist with expertise in both yeast and actin cytoskeleton.

The question of how tropomyosin localizes to specific actin networks is still open and a current avenue of study. Studies in other organisms have shown that different tropomyosin isoforms, or their acetylated vs non-acetylated versions, localize to distinct actin structures. Proposed mechanisms include competition with other ABPs and preference imposed by the formin nucleator. The current study re-examines the function and localization of the two tropomyosin proteins from the budding yeast and reaches the conclusion that they co-decorate all formin-assembled structures and also share most functions, leading to the simple conclusion that the more important contribution of Tpm1 is simply linked to its higher expression. Once consolidated, the study will appeal to researchers working on the actin cytoskeleton.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

There are 2 Major issues:

1. Having an -ala-ser- linker between the GFP and tropomyosin mimics acetylation. This is not the case, and more likely the this linker acts as a spacer that allows tropomyosin polymers to form on the actin, and without it there is steric hindrance. A similar result would be seen with a simple flexible uncharged linker. It has been shown in a number of labs that the GFP itself masks the effect of the charge on the amino terminal methionine. This is consistent with NMR, crystallographic and cryo structural studies. Biochemical studies should be presented to demonstrate that the impact of a linker for the conclusions stated to be made, which provide the basis of a major part of this study.
2. My major issue however is making the conclusions stated here, using an amino-terminal fluorescent protein tag that s likely to impact any type of isoform selection at the end of the actin polymer. Carboxyl terminal tagging may have a reduced effect, but modifying the ends of the tropomyosin, which are integral in stabilising end to end interactions with itself on the actin filament, never mind any section systems that may/maynot be present in the cell, is not appropriate.

Significance

This paper explores the role of formin in determining the localisation of different tropomyosins to different actin polymers and cellular locations within budding yeast. Previous studies have indicated a role for the actin nucleating proteins in recruiting different forms of tropomyosin within fission yeast. In mammalian cells there is variation in the role of formins in affiecting tropomyosin localisation - variation between cell type. There is also evidence that other actin binding proteins, and tropomyosin abundance play roles in regulating the tropomyosin-actin association according to cell type. Biochemical studies have previously been undertaken using budding yeast and fission yeast that the core actin polymerisation domain of formins do not interact with tropomyosin directly.

The significance of this study, given the above, and the concerns raised is not clear to this reviewer.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Response to reviewers’ comments for Isbilir et al

We thank the reviewers for their insightful comments and advice. In light of the reviewers’ constructive suggestions, we have revised our manuscript as detailed below.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Summary: In this manuscript, the authors investigate the unique Mycobacteriaceae cell envelope using cryo-tomography/cryo-electron microscopy with Corynebacterium glutamicum as a model organism. Cryo-EM images of C. glutamicum cells successfully resolved previously observed densities corresponding to the MM, arabinogalactan, peptidoglycan, and inner membrane layers of the cell envelope along with the S-layer. The authors found that the S-layer is patchy in a manner dependent on growth phase (i.e. liquid versus solid growth). Intriguingly, when the S-layer was present, the leaflets of the MM appeared to be disrupted. The authors solved the structure of purified S-layer protein PS2 by cryo-EM, however they could not resolve the C-terminal membrane interaction domain. The authors found that PS2 is hexameric and different hexamers are linked by trimeric interface to create a porous structure. Phylogenetic analysis showed conservation of PS2 within corynebacteria and suggested a signature for MM-association.

Major comments:

(1) The S-layer structure is porous and the authors suggest that it may function as a molecular sieve or permeability barrier. This hypothesis should either be tested experimentally, or further discussion is needed regarding what small molecules (chemical features, size) would be able to penetrate.

This is a misunderstanding; we rather expect the opposite scenario in which the dimensions of the PS2 S-layer pores are too large to act as a molecular sieve. We are sorry for the confusion and have further clarified this part of the results and discussion.

Line 258: “The combination of hexameric and trimeric interfaces results in varying pores sizes of 6 Å, 27 Å, and 81 Å within the lattice (Fig. 3A). Some of these pores are relatively large and are reminiscent of the porous S-layer of Deinococcus radiodurans, which is also patchy on the cell surface (von Kügelgen et al., 2023). This suggests that C. glutamicum S-layer likely does not function as a molecular sieve, i.e. it has no protective role due to large pore dimensions and patchy cellular coating of the S-layer.”

and

Line 470: “The large pores (especially the 27 Å- and 81 Å-pores) in the S-layer suggest that its role is not to protect the cells from invading molecules or phages.”

(2) The authors show cryo-EM images of dividing C. glutamicum cells but don't make any statements as to the presence, morphology, and measurements of the different cell envelope layers. This analysis should be included.

We thank the reviewer for pointing this out. As suggested, we modified Figure S1 to highlight further details, and we have added the sentences below into the manuscript text.

Line 175: “To probe the plasticity of the cell envelope during the cell cycle, we analysed the cell envelope layers within the dividing septum (Fig. S1E). The thickness of the septum (~55 nm) was found to be greater than the usual thickness of the cell envelope (~42 nm on the same cell, see also Fig. 1A). The septum is composed of unseparated cell envelopes of the daughter cells that appear to contain a single ‘outer’ membrane, which is likely composed of mycolic acids. Presumably, this membrane will form the future MM once division is completed. Notably, the putative mycolic acid-containing bilayer within the septum was not connected to the MM on the other parts of the cell, whereas the remaining cell envelope layers appeared to be continuous with the rest of the cell. While IM and the putative future MM were clearly distinguishable, PG and AG could not be differentially identified in the dividing septum.”

and

Line 422: “In addition to cell envelopes of non-dividing cells, the dividing C. glutamicum septum shows two daughter cell envelopes separated by a bilayer likely containing mycolic acids. Notably, this bilayer was not connected to the MM on the rest of the cell (Fig. S1E). This observation is in line with the previous studies showing that at septal junctions, a contiguous PG layer acts as a diffusion barrier for the MM, and during separation of daughter cells, the PG in the septal junctions is displaced, allowing the bilayer at the septum to merge with the rest of the MM (Zhou et al., 2019).”

__Figure S1. Cryo-FIB milling of C. glutamicum cells. __

… E) Septum of a dividing C. glutamicum cell. Ten 0.85 nm thick-slices of the tomogram were averaged and bandpass-filtered to boost contrast. Zoomed view of the septum is shown on the right.

(3) The authors should include more discussion as to the patchiness or "wavy" MM near sites of PS2 contact. Cryo-EM of cells that express a variant of PS2 that lack the membrane anchoring domain would demonstrate that this is specific to PS2-membrane contacts. Minimally, providing some quantification for this phenotype would strengthen the claim (for instance, does the spacing between the perturbations match the expected scale of distance between S-layer membrane contacts).

We agree with reviewer that demonstrating the “wavy” nature of the MM requires further analysis. While it is our strong impression that the wavy nature is increased underneath the PS2 S-layer, we could not find a suitable metric to show this convincingly, i.e. all our analyses (real space averaging or averaging of power spectra) did not give clear-cut results. This is probably due to the inherent variability in the MM around the cell. In line with this, we have decided to tone down the relevant text in the manuscript.

Line 151: “Although we cannot be certain given the existing data, we suppose that this perturbation of the MM directly beneath the patchy S-layer could arise due to the interaction of the S-layer anchoring domain with the MM, which has been predicted to be present in the coiled coil part of the PS2 protein forming the S-layer using bioinformatics (Johnston et al., 2024).”

(4) The authors speculate on complete conservation of certain residues in the C-terminal domain of PS2 and hypothesize that they may be important for maturation or targeting of MM-associated proteins. Two additional examples of proteins with this motif are mentioned as evidence. Authors should search for this motif in pre-existing lists of MM proteins in the literature to test if this hypothesis is robust. Experiments to test if the conserved C-terminal residues of PS2 are required for export or assembly into an S-layer are feasible but optional given the scope of the paper.

We thank the reviewer for raising this point. Upon thoroughly re-examining the literature, we identified a previous study by Marchand et al. (J Bacteriol., 2012) that characterized MM-associated proteins in C. glutamicum. The proteins reported in this study as associated with the inner leaflet of the MM, including the mycoloyltransferases MytA and MytB, as well as those involved in pore formation, such as PorA and PorB, do not possess a phenylalanine as their terminal residue. This observation suggests that the invariant phenylalanine in PS2 does not represent a universal mechanism for targeting proteins to the MM. However, we also noted that several putative cell-surface proteins identified in this study, which feature a PS2-like C-terminal hydrophobic anchor preceded by a disordered segment, harbor a phenylalanine, proline, or lysine at their C-terminus. Additionally, the targeting of porins such as PorA, PorH, PorB, and PorC to the MM in C. glutamicum is known to depend on posttranslational O-mycoloylation. Based on these findings, we speculate that the conserved phenylalanine in PS2 may contribute to its anchoring and stabilization within the MM, rather than functioning as a universal targeting signal—a hypothesis we plan to investigate in future studies. We have revised the manuscript to incorporate these points and provide additional context.

Line 377: “To explore this hypothesis, we analysed MM-associated proteins of C. glutamicum identified in a previous study (Marchand et al., 2012). Proteins associated with the inner leaflet of the MM, such as the mycoloyltransferases MytA, MytB, MytC, MytD, and MytF, or those involved in pore formation, such as PorA and PorB, do not possess a phenylalanine as their terminal residue, suggesting that the invariant phenylalanine in PS2 does not represent a general mechanism for targeting proteins to the MM. However, several putative cell-surface proteins with a PS2-like C-terminal hydrophobic anchor preceded by a disordered segment were found to harbor a phenylalanine, proline, or lysine at their C-terminus. Examples include a prenyltransferase/squalene oxidase repeat-containing protein (NCBI: WP_011013715.1) and a metallophosphoesterase family protein (WP_011015494.1) (Fig. S8). Based on this conservation, we identified additional putative MM-associated cell-surface proteins in C. glutamicum (Fig. S8), such as an ExeM/NucH family extracellular endonuclease (WP_003854007.1) and a lamin tail domain-containing protein (WP_004567709.1). Interestingly, the targeting of porins PorA, PorH, PorB, and PorC to the MM in C. glutamicum has been shown to depend on posttranslational O-mycoloylation, which facilitates their proper localization and integration into the mycomembrane (Carel et al., 2017). Whether O-mycoloylation is also involved in the targeting of PS2 remains an open question and warrants further investigation. We speculate that terminal residues such as phenylalanine, proline, and lysine may contribute to anchoring cell-surface proteins within the MM by stabilizing interactions with the hydrophobic membrane environment or acting as signals for specific sorting or assembly mechanisms.”

(5) The authors do not draw the distinction between MM-associated and integral MM proteins (that contain a transmembrane domain). Is the C-terminal membrane anchoring domain of PS2 likely to span the entire bilayer or just be associated by a few amino acids?

The MM-anchoring hydrophobic segment is approximately 25 residues long across PS2 homologs, corresponding to a ~3.75 nm α-helix. In comparison, the MM has a thickness of 4–5 nm. This suggests that, while the MM-anchoring segment may not strictly qualify as a transmembrane domain integral to the MM, it is sufficiently long to embed deeply into the membrane and potentially span much of its bilayer thickness. To address this, we have added the following clarification to the manuscript:

Line 363: “The MM-binding segment is predicted by AlphaFold2 models to comprise an N-terminal hydrophobic a-helix and a short C-terminal amphipathic a-helix; however, in the MM, these may function as a single continuous helix. The MM-binding segment of PS2 homologs in Corynebacterium is consistently approximately 25 amino acid residues long, corresponding to a ~3.75 nm α-helix—sufficiently long to nearly traverse the 4–5 nm thickness of the MM.”

Minor comments:

(1) The authors comment that the thickness of the MM both with and without the S-layer is the similar and conclude that there is no change in mycolic acid length. The resolution of the technique is not sufficient to make this statement.

We agree with the reviewer in this point, while we can only measure the thickness of bilayer, we cannot comment on the thickness of each leaflet of the mycomembrane. Therefore, we have revised the text accordingly.

Line 144: “In 2D projection images of FIB-milled cells, the two leaflets of the MM were clearly resolved (Figs. 1C-D). The thickness of the MM in both cell envelopes with and without S-layer was between 4-5 nm (Table S1).”

(2) It would be helpful if the authors could comment if their membrane dimension measurements agree with previously published results in the main text of the manuscript. It is currently only included in the legend of Table S1.

Specifically regarding the MM, the measurements from both studies are quite similar; compare 4-5 nm from our study with 4.7 nm from Zuber et al., 2008. As the reviewer suggested, we have revised the discussion to include the comparison of the measurements with Zuber et al., 2008.

Line 413: “Our measurements are largely consistent with previous results (Zuber et al., 2008), except that in our data the IWZ was significantly thinner (~9.8 nm in this study vs. ~18 nm in Zuber et al., 2008), which is possibly due to strain differences. Moreover, our measurement of MWZ was slightly different because we could resolve OWZ as a separate layer, which was included into the MWZ measurement in the previous study (~15nm in this study vs. ~20.9 nm in Zuber et al., 2008) (Zuber et al., 2008).”

Reviewer #1 (Significance (Required)):

The manuscript provides compelling images and structures of the C. glutamicum cell envelope and S-layer protein PS2, respectively. These cryo-EM images of the cell envelope appear to agree nicely with pre-existing studies in the field. The introduction of the manuscript was well-written and the data in the manuscript is of broad interest to those who study the Mycobacteriaceae cell envelope. There is a lot of compelling data included in the paper, but the study would be strengthened by further analysis of the data as well as additional experiments to support some of the hypotheses suggested.

Thank you.

Reviewer expertise: bacterial genetics, bacterial cell envelope, protein transport

__ __

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Corynebacterium glutamicum is an organism with important industrial application, and it shares its complex cell-envelop architecture with organism of great relevance in human health such Corynebacterium diphtheriae and pathogenic mycobacteria. Using a cryo-EM and cryo-ET approaches together with phylogenetic studies, the authors provide of an in-deep structural characterization of the cell envelop of C. glutamicum. The authors map the different components of the cell envelope using high-resolution tomography, revealing unseen details of the outer wall zone, previously unsolved and attributed to the AG molecule. They provide with an atomic model of the PS2 S-layer at 3.1 A global resolution. The later discloses key features of the S-layer architecture, consisting of a hexagonal scaffold built by the PS2 protein, and its interaction with the mycolic membrane. The phylogenetic and bioinformatic studies show PS2 S-layer to be exclusively found within the Corynebacterium genus, although sporadically, and a correlation of PS2 presence/absence with other genetic differences. Despite PS2 homologues are shown to share common regions, which suggests all PS2 S-layers to exhibit a hexagonal lattice like the described in this study, but with divergent lattice parameters.

Major comments:

The authors provide with solid data supporting the structural models and conclusions stated. Text and figures are clear and nicely presented. I have however an important question regarding a the cryo-EM model. In Figure 3 B-C and Figure S3D-H, the authors depict protein details including hydrogen atoms, which make me question if the PS2 S-layer structure has been modeled including hydrogen atoms. The resolution of the cryo-EM data does not enable to model hydrogens that, if were included in the structure, should be removed of the coordinate file of the S-layer model and figures.

We agree with the reviewer that the current resolution of the cryo-EM map is not sufficient to model hydrogen atoms. The hydrogens were added to PS2 S-layer model during refinement in ISOLDE (Croll, 2018), and retained during Phenix real space refinement (Afonine et al., 2018; Liebschner et al., 2019). We agree with the reviewer that hydrogens should not be shown in the figures, since their positions have not been determined experimentally in our cryo-EM map. We have therefore removed these atoms from Figures 3 and S4.

__ “Figure 3. The PS2 S-layer Lattice. …“__

“Figure S4. Features of the PS2 S-layer lattice”

Minor comments

• Regarding the proposed calcium atoms at the S-Layer. The authors should provide further analysis to support the presence of calcium/divalent atoms proposed. Please show how is the coordination around the blobs spotted as potential calcium (or any other potential divalent that might be interacting at those positions). Does the coordination observed fit with the expected for a calcium/divalent binding site? Are the residues coordinating to those blobs well defined in density? Are the blobs of density of the potential cations observed across all the protomers of the PS2 S-layer? Figure 3D-F depicting the proposed cation-binding sites are too busy and unclear, they should focus on the proposed binding sites showing the interacting side/main-chains involved in the proposed coordination.

This is an interesting point. To investigate, we performed EDTA/EGTA treatment of the purified PS2 S-layer to see whether there would be any observable effect on the S-layer. We observed that S-layer lattices were still intact after EDTA or EGTA treatment. Therefore, we concluded that either cations do not play a role in stabilizing this S-layer or they are not accessible for chelation by EDTA or EGTA. This experiment unfortunately did not allow us to identify the ionic species. About the coordination: in the unknown densities 1 and 2 in the new Fig. S4, the coordination is clearer when compared to unknown density 3, however we cannot say for certain that these ions are calcium ions. Considering this, we have changed the text accordingly.

Line 237: “At the sequence level, the PS2 protein is enriched in acidic amino acid residues, giving it an overall negative charge, with an estimated isoelectric point of 4.25 (Fig. S4B-C). Consistent with this overall negative charge, we observed putative cationic densities at various locations along the PS2 sequence in the cryo-EM map, which are surrounded and stabilized by negatively charged amino acid residues (Figs. S4D-F). The identity of these cations cannot be ascertained at the current resolution of our cryo-EM map; however, previous studies on other bacterial S-layers suggest that they may correspond to calcium (Baranova et al., 2012; Herdman et al., 2022; Sogues et al., 2023). These cations may further stabilize the lattice, similar to other S-layers where cations were found to be essential for lattice formation (Baranova et al., 2012; Herdman et al., 2022; Sogues et al., 2023; von Kügelgen et al., 2021). To probe this further, we incubated purified PS2 S-layers with either 10 mM EDTA or 10 mM EGTA and examined the effect on the treated S-layers. Following the chemical treatment, S-layer lattices were still intact, with no observable differences under both conditions (Fig. S4I). This suggests that either these putative cations do not play a major role in stabilizing the PS2 S-layer or they are not accessible for chelation by EDTA or EGTA under the chosen experimental conditions”

and

“Figure S4. Features of the PS2 S-layer lattice… D, E, F) __Putative densities possibly corresponding to cations and G) SDS detergent molecules are shown, with the respective sigma values of the maps shown in the bottom right. The potential densities are denoted with an “*”, and the surrounding residues also labelled. H) __The coiled-coil segment (residues 405-445) is shown in side view (left) and bottom view (right). __I) __Purified PS2 S-layer sheets incubated with EDTA (middle) and EGTA (right) show no discernible differences from native S-layers (left).”

• Regarding the potential SDS density. Looking at Figure 3G, it is not clear how the morphology of the density shown (with a T-shape) would fit a linear molecule of SDS (could be the view selected?). Have the authors performed any attempt of modelling the SDS molecule to assess this and/or those PS2 residues contributing to stabilize the SDS? Is this density consistently observed across the other interfaces of the hexamer? That would support their hypothesis.

This density is observed in the other interfaces of the hexamer as well, and it is also seen in maps that were produced from refinements without any symmetry applied, i.e. when the processing was performed in C1. Nevertheless, taking on board the criticism about the ambiguity of both the putative SDS and calcium densities, combined with the inconclusive results of our EDTA/EGTA treatment, we have changed the panel titles of Fig. S4D-G to “Unknown density 1-4” in revised the manuscript (see above), making sure to not claim more than what is revealed by the density.

Reviewer #2 (Significance (Required)):

As structural biologist I consider that this study constitutes an important advance in our understanding of the complex architecture and function of the cell-envelop of C. glutamicum. Knowledge that can help to better understand this intricate envelop present in other Mycobacteriaceae relatives, which include important human pathogen such as Mycobacterium tuberculosis or Corynebacterium diphtheriae. This study is most relevant for the scientific community investigating on the bacterial cell envelop (structure, evolution and function) as well as in host-pathogen interactions. Moreover, the cell envelop constitutes a target for bacteriostatics and thus, this study may be relevant for the scientific community working on antimicrobial development.

Thank you.

__ __

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Summary: In the manuscript from Isbilir et al, the authors investigate the cell envelope of Corynebacterium glutamicum, a bacterium extensively used in biotechnological applications, using state-of-the-art cryo-electron microscopy methodologies as well as bioinformatics. They convincingly demonstrate that the C. glutamicum S-layer consists of hexagonal PS2 arrays and provide the underlying structural basis of this intriguing assembly. Bioinformatic analysis further revealed conserved and divergent elements of PS2 across Corynebacteria.

Major comments:

• My main point of criticism relates to the first part of the results, in which the authors attempt to characterize the cell envelope using cryo-electron tomography. From my own experience, plunge-freezing bacterial lawns often results in bad ice quality (crystalline ice) between the bacterial cells. This seems to be also the case here, looking at the 2D images in Fig. S1D revealing clear Bragg reflections. While often not a problem if interested in intracellular features, the authors are drawing conclusions on the cell envelope, which is in direct contact with these ice crystals, known to be destructive for ultrastructural features. For example, this could be the reason for the "wavy" mycomembrane in Fig. 1A and 1B as well as Fig. S1C. On top, it also might affect their observations of interrupted and discontinuous mycomembranes covered by an S-layer in Fig. 1D. The authors should discuss this limitation, and I would highly recommend rephrasing their conclusions made from this data more carefully.

We would like to thank the reviewer for their constructive criticism. We agree that it is difficult to vitrify a lawn of bacteria without formation of crystalline ice in all areas of the specimen. In our lamellae, we have primarily vitreous ice (see Fig. S1B, lower right panel for example) but the reviewer has correctly pointed out observed crystalline ice in some areas on the edges of the lamellae. As suggested, we included the following text in the legend to Fig. S1B to warn the readers about this potential shortcoming.

Line 562: “After milling, lamellae with a 150-200 nm thickness were retained for cryo-ET investigations. Each lamella contained multiple cells suitable for imaging. Although vitreous ice was observed in most lamellae, the edges of some lamellae showed signs of crystalline ice formation…”

The reviewer’s comment about the MM perturbations is well taken, this was also raised by reviewer 1. Although we attempted to quantify this effect by various image analysis tools, in the end we feel that it is not possible to make clear-cut conclusions about the MM-waviness based on our data. We have therefore toned down our interpretations about the “wavy” nature of the MM in the manuscript text (see also our response to reviewer 1 above).

Line 151: “Although we cannot be certain given the existing data, we suppose that this perturbation of the MM directly beneath the patchy S-layer could arise due to the interaction of the S-layer anchoring domain with the MM, which has been predicted to be present in the coiled coil part of the PS2 protein forming the S-layer using bioinformatics (Johnston et al., 2024).”

• The single-particle cryoEM data and the bioinformatic analysis are very well presented, analyzed in much detail, and convincing. While the authors state that the S-layer most probably does not serve to protect the cells from invading molecules or phages, additional experiments to figure out the function of the S-layer would be desirable. However, this might be beyond the scope of this paper but the authors should at least include a clearer discussion about potential function(s).

As suggested by the reviewer, we have extended the discussion about the potential function of the PS2 S-layer in C. glutamicum.

Line 465: “We also observed that S-layer coverage appeared to increase when C. glutamicum cells were grown on solid media (Fig. S2A-B). This suggests that the S-layer could be useful for the bacteria to grow in in a colony or in a surface-attached biofilm community, as shown for other bacteria including Clostridium difficile and Tannerella forsythia (Ðapa et al., 2013; Honma et al., 2007; Wong et al., 2023).”

and

Line 474: “…Slightly at odds with the large pores, it has been shown that the presence of the PS2 S-layer renders cells more resistant towards lysozyme (Sogues et al., 2024; Theresia et al., 2018). Although lysozyme is much smaller than the pore sizes, it is possible that the S-layer might biochemically sequester such undesirable molecules.”

• The authors speculate about cations stabilizing the S-layer. To provide further evidence, an optional but straightforward experiment would be to treat the purified S-layer with EDTA and subsequently analyze it with negative stain EM or cryoEM.

As suggested, we incubated the purified PS2 S-layer with 10 mM EDTA or 10 mM EGTA and imaged the resulting specimens with cryoEM. We found intact S-layers in these treated samples, therefore, we have concluded that either cations do not play a role in stabilizing this S-layer or they are not accessible for chelation by EDTA or EGTA -

Line 246: “To probe this further, we incubated purified PS2 S-layers with either 10 mM EDTA or 10 mM EGTA and examined the effect on the treated S-layers. Following the chemical treatment, S-layer lattices were still intact, with no observable differences under both conditions (Fig. S4I). This suggests that either these putative cations do not play a major role in stabilizing the PS2 S-layer or they are not accessible for chelation by EDTA or EGTA under the chosen experimental conditions.”

and

Figure S4. Cryo-EM of C. glutamicum cells. … I) Purified PS2 S-layer sheets incubated with EDTA (middle) and EGTA (right) show no discernible differences from native S-layers (left).

• The anchoring of the S-layer to the characteristic mycomembrane is only discussed very briefly. As this is a unique feature, it would be of high interest to understand how the anchoring is different from other S-layer carrying Gram-positive/negative bacteria.

We agree with the reviewer and have extended our discussion of this unique feature of the PS2 S-layer.

Line 359: “…the length of the coiled-coil stalk and the MM-binding segment is highly conserved among PS2 homologs across species (Figs S5-S6). This is in line with the fact that the underlying cell envelope architecture, including the MM, is preserved among different Corynebacterium species, necessitating the conservation of the MM anchoring segments in PS2. The MM-binding segment is predicted by AlphaFold2 models to comprise an N-terminal hydrophobic α-helix and a short C-terminal amphipathic α-helix; however, in the MM, these may function as a single continuous helix. The MM-binding segment of PS2 homologs in Corynebacterium is consistently approximately 25 amino acid residues long, corresponding to a ~3.75 nm α-helix—sufficiently long to nearly traverse the 4–5 nm thickness of the MM. Notably, this segment includes the last residue of PS2, a phenylalanine (F), which is remarkably conserved across all PS2 homologs (Figs S5-S6). While the functional significance of this invariant phenylalanine residue remains unclear, the conservation of the preceding residues, particularly the penultimate residue, which is typically either a proline (P) or lysine (K), suggests a potential functional role. It is plausible that these terminal residues collectively contribute to the sorting, export, and insertion of PS2 into the MM or help ensure its stable anchoring within the lipid-rich MM.”

and

Line 444: “The PS2 S-layer protein has a distinctive mode of attachment to the prokaryotic cell envelope. In most archaea, S-layers are directly attached to the cytoplasmic membrane (Bharat et al., 2021), either through lipid modification of the SLP (von Kügelgen et al., 2021) or through the action of a secondary protein (von Kügelgen et al., 2024). In Gram-negative bacteria such as C. crescentus, S-layers are non-covalently attached to the O-antigen of lipopolysaccharide layer covering the outer membrane (von Kügelgen et al., 2020). In turn, in Gram-positive bacterial S-layers are non-covalently anchored via SLH domains to the PG-linked secondary cell wall polymers (Blackler et al., 2018). In other diderm bacteria that are positive for Gram-staining such as Deinococcus radiodurans, the SLP HPI (Bharat et al., 2023) is lipidated at its N-terminus (von Kügelgen et al., 2023), allowing the protein to interact with the cell membrane. In the case of C. glutamicum, the attachment of the PS2 S-layer is achieved through the insertion of the C-terminal hydrophobic helix into the MM, which is a distinctive feature for bacterial S-layers that have been studied in detail using structural biology.”

• Remove the word "accurately" in the second sentence of the second paragraph in the abstract.

Changed as requested.

Line 28: “Our cellular imaging allowed us to map the different components of the cell envelope onto the tomographic density.”

• Remove the word "strong" in the last sentence of the abstract.

Done.

Line 41: “This study, therefore, provides an experimental framework for understanding cell envelopes that contain mycolic acids.”

• As this is a back-to-back submission, the manuscript from Sogues et al. should be cited.

Done, as requested.

Line 191: “Purified S-layers were deposited on cryo-EM grids and vitrified using methods previously described for other S-layers (von Kügelgen et al., 2023, 2024), and specifically for the C. glutamicum S-layer concurrently with this study (Johnston et al., 2024; Sogues et al., 2024).”

and

Line 474: “…Slightly at odds with the large pores, it has been shown that the presence of the PS2 S-layer renders cells more resistant towards lysozyme (Sogues et al., 2024; Theresia et al., 2018). Although lysozyme is much smaller than the pore sizes, it is possible that the S-layer might biochemically sequester such undesirable molecules.”

Minor comments:

• Line numbers are missing, making the manuscript more complicated to review.

Sorry about that, the updated version of the manuscript has line numbers included.

• In the abstract, in the last paragraph of the introduction, and in the first sentence of the discussion, the authors use the term "high-resolution" in conjunction with their cryo-electron tomography imaging. This might be correct if you compare the data to light microscopy or conventional EM imaging. However, given the fact that the authors also used single-particle cryoEM, their cryoET data cannot be called "high-resolution," and they should remove this term as used here.

We agree with the reviewer and change the text accordingly:

Line 28: “Our cellular imaging allowed us to map the different components of the cell envelope onto the tomographic density.”

and

Line 39: “Our structural and cellular data collectively provide a topography of the unusual C. glutamicum cell surface, features of which are shared by many pathogenic and microbiome-associated bacteria, as well as by several industrially significant bacterial species.”

and

Line 102: “Building on these foundational studies, we have used C. glutamicum as a model for MM-containing organisms to perform characterisation of this unusual cell envelope.”

and

Line 110: “By combining our S-layer structure with cryo-ET of the cell envelope and bioinformatics analyses, we provide further clues regarding the MM-anchoring mechanisms of the S-layer and offer insights into its conservation and evolution in corynebacteria.”

and

Line 124: “To overcome this limitation, we employed FIB milling to create thin sections of the cells, which allowed us to obtain images with enhanced contrast of the cell envelope.”

and

Line 401: “In this study, we visualized the C. glutamicum cell envelope by imaging FIB-milled cells using...”

Reviewer #3 (Significance (Required)):

The single-particle cryoEM and bioinformatics analysis are convincing, but this manuscript resides at a rather descriptive level on the S-layer of C. glutamicum and some major comments should be addressed.

The findings in this manuscript are exciting for a specialized audience interested in bacterial cell surfaces/surface appendages and S-layers. On top, as C. glutamicum is widely used in biotechnological applications, the results have clear significance within this field.

Contrary to what the authors claimed, the general insights gained on cell envelopes containing mycolic acids are limited. Only very few insights reported here will advance our understanding of the cell envelope of important human pathogens such as Mycobacterium tuberculosis, as this manuscript focuses on the S-layer, which is absent from these strains.

Thank you for your comments, we have reworded the discussion section with more cautionary statements to present a balanced picture to readers of this manuscript.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

In the manuscript from Isbilir et al, the authors investigate the cell envelope of Corynebacterium glutamicum, a bacterium extensively used in biotechnological applications, using state-of-the-art cryo-electron microscopy methodologies as well as bioinformatics. They convincingly demonstrate that the C. glutamicum S-layer consists of hexagonal PS2 arrays and provide the underlying structural basis of this intriguing assembly. Bioinformatic analysis further revealed conserved and divergent elements of PS2 across Corynebacteria.

Major comments:

• My main point of criticism relates to the first part of the results, in which the authors attempt to characterize the cell envelope using cryo-electron tomography. From my own experience, plunge-freezing bacterial lawns often results in bad ice quality (crystalline ice) between the bacterial cells. This seems to be also the case here, looking at the 2D images in Fig. S1D revealing clear Bragg reflections. While often not a problem if interested in intracellular features, the authors are drawing conclusions on the cell envelope, which is in direct contact with these ice crystals, known to be destructive for ultrastructural features. For example, this could be the reason for the "wavy" mycomembrane in Fig. 1A and 1B as well as Fig. S1C. On top, it also might affect their observations of interrupted and discontinuous mycomembranes covered by an S-layer in Fig. 1D. The authors should discuss this limitation, and I would highly recommend rephrasing their conclusions made from this data more carefully.
• The single-particle cryoEM data and the bioinformatic analysis are very well presented, analyzed in much detail, and convincing. While the authors state that the S-layer most probably does not serve to protect the cells from invading molecules or phages, additional experiments to figure out the function of the S-layer would be desirable. However, this might be beyond the scope of this paper but the authors should at least include a clearer discussion about potential function(s).
• The authors speculate about cations stabilizing the S-layer. To provide further evidence, an optional but straightforward experiment would be to treat the purified S-layer with EDTA and subsequently analyze it with negative stain EM or cryoEM.
• The anchoring of the S-layer to the characteristic mycomembrane is only discussed very briefly. As this is a unique feature, it would be of high interest to understand how the anchoring is different from other S-layer carrying Gram-positive/negative bacteria.
• Remove the word "accurately" in the second sentence of the second paragraph in the abstract.
• Remove the word "strong" in the last sentence of the abstract.
• As this is a back-to-back submission, the manuscript from Sogues et al. should be cited.

Minor comments:

• Line numbers are missing, making the manuscript more complicated to review.
• In the abstract, in the last paragraph of the introduction, and in the first sentence of the discussion, the authors use the term "high-resolution" in conjunction with their cryo-electron tomography imaging. This might be correct if you compare the data to light microscopy or conventional EM imaging. However, given the fact that the authors also used single-particle cryoEM, their cryoET data cannot be called "high-resolution," and they should remove this term as used here.

Significance

The single-particle cryoEM and bioinformatics analysis are convincing, but this manuscript resides at a rather descriptive level on the S-layer of C. glutamicum and some major comments should be addressed.

The findings in this manuscript are exciting for a specialized audience interested in bacterial cell surfaces/surface appendages and S-layers. On top, as C. glutamicum is widely used in biotechnological applications, the results have clear significance within this field.

Contrary to what the authors claimed, the general insights gained on cell envelopes containing mycolic acids are limited. Only very few insights reported here will advance our understanding of the cell envelope of important human pathogens such as Mycobacterium tuberculosis, as this manuscript focuses on the S-layer, which is absent from these strains.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Corynebacterium glutamicum is an organism with important industrial application, and it shares its complex cell-envelop architecture with organism of great relevance in human health such Corynebacterium diphtheriae and pathogenic mycobacteria. Using a cryo-EM and cryo-ET approaches together with phylogenetic studies, the authors provide of an in-deep structural characterization of the cell envelop of C. glutamicum. The authors map the different components of the cell envelope using high-resolution tomography, revealing unseen details of the outer wall zone, previously unsolved and attributed to the AG molecule. They provide with an atomic model of the PS2 S-layer at 3.1 A global resolution. The later discloses key features of the S-layer architecture, consisting of a hexagonal scaffold built by the PS2 protein, and its interaction with the mycolic membrane. The phylogenetic and bioinformatic studies show PS2 S-layer to be exclusively found within the Corynebacterium genus, although sporadically, and a correlation of PS2 presence/absence with other genetic differences. Despite PS2 homologues are shown to share common regions, which suggests all PS2 S-layers to exhibit a hexagonal lattice like the described in this study, but with divergent lattice parameters.

Major comments:

The authors provide with solid data supporting the structural models and conclusions stated. Text and figures are clear and nicely presented. I have however an important question regarding a the cryo-EM model. In Figure 3 B-C and Figure S3D-H, the authors depict protein details including hydrogen atoms, which make me question if the PS2 S-layer structure has been modeled including hydrogen atoms. The resolution of the cryo-EM data does not enable to model hydrogens that, if were included in the structure, should be removed of the coordinate file of the S-layer model and figures.

Minor comments

• Regarding the proposed calcium atoms at the S-Layer. The authors should provide further analysis to support the presence of calcium/divalent atoms proposed. Please show how is the coordination around the blobs spotted as potential calcium (or any other potential divalent that might be interacting at those positions). Does the coordination observed fit with the expected for a calcium/divalent binding site? Are the residues coordinating to those blobs well defined in density? Are the blobs of density of the potential cations observed across all the protomers of the PS2 S-layer? Figure 3D-F depicting the proposed cation-binding sites are too busy and unclear, they should focus on the proposed binding sites showing the interacting side/main-chains involved in the proposed coordination.
• Regarding the potential SDS density. Looking at Figure 3G, it is not clear how the morphology of the density shown (with a T-shape) would fit a linear molecule of SDS (could be the view selected?). Have the authors performed any attempt of modelling the SDS molecule to assess this and/or those PS2 residues contributing to stabilize the SDS? Is this density consistently observed across the other interfaces of the hexamer? That would support their hypothesis.

Significance

As structural biologist I consider that this study constitutes an important advance in our understanding of the complex architecture and function of the cell-envelop of C. glutamicum. Knowledge that can help to better understand this intricate envelop present in other Mycobacteriaceae relatives, which include important human pathogen such as Mycobacterium tuberculosis or Corynebacterium diphtheriae. This study is most relevant for the scientific community investigating on the bacterial cell envelop (structure, evolution and function) as well as in host-pathogen interactions. Moreover, the cell envelop constitutes a target for bacteriostatics and thus, this study may be relevant for the scientific community working on antimicrobial development.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript, the authors investigate the unique Mycobacteriaceae cell envelope using cryo-tomography/cryo-electron microscopy with Corynebacterium glutamicum as a model organism. Cryo-EM images of C. glutamicum cells successfully resolved previously observed densities corresponding to the MM, arabinogalactan, peptidoglycan, and inner membrane layers of the cell envelope along with the S-layer. The authors found that the S-layer is patchy in a manner dependent on growth phase (i.e. liquid versus solid growth). Intriguingly, when the S-layer was present, the leaflets of the MM appeared to be disrupted. The authors solved the structure of purified S-layer protein PS2 by cryo-EM, however they could not resolve the C-terminal membrane interaction domain. The authors found that PS2 is hexameric and different hexamers are linked by trimeric interface to create a porous structure. Phylogenetic analysis showed conservation of PS2 within corynebacteria and suggested a signature for MM-association.

Major comments:

1. The S-layer structure is porous and the authors suggest that it may function as a molecular sieve or permeability barrier. This hypothesis should either be tested experimentally, or further discussion is needed regarding what small molecules (chemical features, size) would be able to penetrate.
2. The authors show cryo-EM images of dividing C. glutamicum cells but don't make any statements as to the presence, morphology, and measurements of the different cell envelope layers. This analysis should be included.
3. The authors should include more discussion as to the patchiness or "wavy" MM near sites of PS2 contact. Cryo-EM of cells that express a variant of PS2 that lack the membrane anchoring domain would demonstrate that this is specific to PS2-membrane contacts. Minimally, providing some quantification for this phenotype would strengthen the claim (for instance, does the spacing between the perturbations match the expected scale of distance between S-layer membrane contacts).
4. The authors speculate on complete conservation of certain residues in the C-terminal domain of PS2 and hypothesize that they may be important for maturation or targeting of MM-associated proteins. Two additional examples of proteins with this motif are mentioned as evidence. Authors should search for this motif in pre-existing lists of MM proteins in the literature to test if this hypothesis is robust. Experiments to test if the conserved C-terminal residues of PS2 are required for export or assembly into an S-layer are feasible but optional given the scope of the paper.
5. The authors do not draw the distinction between MM-associated and integral MM proteins (that contain a transmembrane domain). Is the C-terminal membrane anchoring domain of PS2 likely to span the entire bilayer or just be associated by a few amino acids?

Minor comments:

1. The authors comment that the thickness of the MM both with and without the S-layer is the similar and conclude that there is no change in mycolic acid length. The resolution of the technique is not sufficient to make this statement.
2. It would be helpful if the authors could comment if their membrane dimension measurements agree with previously published results in the main text of the manuscript. It is currently only included in the legend of Table S1.

Significance

The manuscript provides compelling images and structures of the C. glutamicum cell envelope and S-layer protein PS2, respectively. These cryo-EM images of the cell envelope appear to agree nicely with pre-existing studies in the field. The introduction of the manuscript was well-written and the data in the manuscript is of broad interest to those who study the Mycobacteriaceae cell envelope. There is a lot of compelling data included in the paper, but the study would be strengthened by further analysis of the data as well as additional experiments to support some of the hypotheses suggested.

Reviewer expertise: bacterial genetics, bacterial cell envelope, protein transport

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Response to Reviewers

We thank all three reviewers for their time and engagement, for their generally supportive comments, and for raising some important concerns. We are pleased to submit a significantly revised manuscript where we tried to accommodate all suggested changes and extensions. Importantly, we have included additional experiments that support the relevance of FACT for the overall stability of the inner kinetochore. Below is a detailed point-to-point response. Changes to the manuscript relative to the original submission have been highlighted at the end of this response.

---

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

Summary: The authors investigated molecular interactions between CCAN and FACT complexes. They revealed contact domains in FACT and the cognate subcomplexes of CCAN by in vitro reconstitution from recombinant proteins followed by SEC and pull-down assay.

They also revealed a couple of potential means to control interactions between FACT and the CCAN. They conclude that phosphorylation of FACT by CK2 is essential for binding to the CCAN; and CENP-A nucleosomes or DNA prevent CCAN from interacting with FACT.

Major comments:

The authors show that phosphorylation of FACT is essential for interaction with CCAN.

They argue that this phosphorylation is partly catalysed by CK2.

My concerns are:

-1- The authors assume that the sites phosphorylated in insect cell are also phosphorylated in human cells. However, it is not demonstrated which residues are phosphorylated in human cells and whether they match those from insect cells. Whether phosphorylation of recombinant proteins in insect cells is physiologically relevant to mammalian is uncertain. Kinetochore components are not very well conserved evolutionarily, thus their regulation may be different.

We thank the reviewer for these remarks, which we answer together with point 2 below.

-2- They identify several residues which are phosphorylated by CK2 in vitro. However, these are not necessarily the same sites as those phosphorylated in insect cells or more importantly in human cells. The in vitro phosphorylation by CK2 did not restore binding affinity in full, suggesting phosphorylation at other sites may be critical for interaction with CCAN. Further evidence is required to support the claim that those sites are phosphorylated in vivo and important for integrity of kinetochores in mitosis.

Our analysis of FACT phosphorylation represents a relatively small part of a very data-rich paper, and was not meant to be exhaustive. Nonetheless, the reviewer's comments are important and well received. We agree that we have no definitive evidence that the same sites are phosphorylated in insect cells, in vitro, and in human cells. However, it is quite remarkable, and supports specificity, that the interaction with FACT, lost after dephosphorylation in vitro, is restored with CK2 and not with three additional mitotic kinases (CDK1, Aurora B, and PLK1 - Figure S8D). We also note that S437, S444 and S667 of SSRP1, which were phosphorylated by CK2 in vitro, were also detected as phosphorylated sites on recombinant FACT purified from insect cells (Table S1). So collectively, while we agree with the reviewer that the analysis of FACT phosphorylation is not complete, it does significantly add to the manuscript and more generally to the FACT field.

Minor comments:

Figure 1H

I am confused with 4 stars shown at the top of the right plot. If the 4 stars are meant to show a significant difference, then the statement in the text (line 123) is not correct.

"SSRP1 localization was also largely unaffected ..."

Similar discrepancies are found in Figures 3H (line 212), Figures S2 (line 122), S5I (line 197), and S6I (line209). Figure S6H is not referred to anywhere.

There is no description for the numbers at the top. Are they mean values? Do red bars represent S.D.?

We thank the reviewer for these comments. In this revised version of the manuscript, we have substantially improved the quantification and statistical analysis. The main problem with the previous automated analysis is that the non-circular shape of the CREST-staining led to inconsistencies with the statistical analysis and the statement. In contrast, the same analysis works well when the CENP-C signal was used for KT identification (e.g. in Figure 3), as CENP-C staining yields well separated circular signals ideally suited for our automated identification of individual KTs and subsequent retrieval of fluorescence intensities. We have therefore modified our analysis macro for all experiments where CREST was used as a reference. We used Othsu-thresholding of the DAPI signal for generating a segmentation mask per each cell. Then, integrated cell intensities were calculated for each fluorescence channel based on the DAPI reference mask. With these adjustments, the statistical analyses (Figures 1, S2, S3) support the claim presented. We have updated the Methods and Results sections to reflect the revised analysis.

The numbers on top of the graphs are median values, bars represent interquartile ranges. We have now included the description in figure legends.

We appreciate your feedback, which prompted us to clarify and enhance the rigor of our approach.

We are now referring to Fig. S6H in the text.

Figure 1D

There is no description of R* to the right of gels.

We have added a description of R* to the relevant figure legend.

Figure S2

A 4 hour nocodazole treatment is too short to drive all cells into mitosis. Is the data taken from mitotic cells only?

Yes, the data are taken only from the mitotic population. We have now clarified this in the figure legend.

Reviewer #1 (Significance (Required)):

The interaction of FACT with kinetochore components has been known for several years. However how FACT contributes to architecture or function of kinetochore is not very well understood. How the FACT complex, which is known for its established role as a histone chaperone, is involved in kinetochore assembly/architecture will attract interest in several fields of basic research including epigenetics, mitosis, structural biology.

We are grateful to the reviewer for this supportive statement that recognizes the broad potential interest of the manuscript.

Identification of CCAN subunits that interact with FACT is important for future analysis to understand the kinetochore function of FACT. The authors identified OPQRU and CHIKM subcomplex in addition to TW as FACT-interacting domains. These subcomplexes are geographically scattered in a 3D model of CCAN holocomplex. Stoichiometry of CCAN and FACT might be informative whether a single or multiple FACT binds to the multiple sites of CCAN. The authors do not address whether these multiple sites are occupied simultaneously, separately or sequentially.

We thank the reviewer for raising this point. As mentioned in the discussion, we have not yet been able to perform a structural analysis of the FACT/CCAN complex to determine its stoichiometry. However, we have now added a newexperiment (Figure S1B,C) where we quantified in-gel tryptophan fluorescence after analytical size-exclusion chromatography. This strongly suggests that FACT and CCAN form a complex with a 1:1 stoichiometry. Nevertheless, we cannot comment on which sites are occupied.

The statement at the end of Abstract (lines 23-25) is a speculative hypothesis without evidence for "a pool of CCAN that is not stably integrated into chromatin", "chaperoning CCAN", and "stabilisation of CCAN".

We agree with the reviewer that this is speculative, and have therefore modified the Abstract to clearly indicate this point.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

FACT is a histone chaperone and is involved in various events on chromatin such as transcription and replication. In addition, FACT interacts with various kinetochore components, suggesting potential functions at the kinetochore. However, it is largely unclear how FACT functions in the kinetochore. Authors of this MS took the biochemical approach to understand roles of FACT in the kinetochore.

Authors demonstrated that FACT forms a complex with the constitutive centromere associated network (CCAN), which contains 16 subunits on centromeric chromatin, using multiple binding sites. They also showed that casein kinase II (CK2) phosphorylated FACT and dephosphorylated FACT did not bind to CCAN. Furthermore, they displayed that DNA addition disrupt the stable FACT-CCAN complex.

Overall, while authors have done solid and high-quality biochemical analyses (these are elegant), it is still unclear how FACT plays its roles in the kinetochore. Simple knockout or knockdown study on FACT might be complicated, because FACT has multi-functions. If authors can identify specific regions of FACT for interaction with CCAN, they would put specific mutations into FACT to analyze phenotype. Although they did not reach a high-resolution structure for the FACT-CCAN complex, they can utilize AlphaFold and test specific interaction regions, biochemically. Then, using such information, significance of FACT-CCAN interaction might be testable in cells. Such a kind of study would be expected. In summary, biochemical parts are beautiful, but the paper did not address significance of FACT-CCAN interaction.

We thank the reviewer for praising the biochemical work in our manuscript. The reviewer, however, also underscored the limits of our functional analysis. The reviewer proposes generating separation-of-function mutants in a minimal kinetochore-binding region. Indeed, we have identified the minimal domain for the interaction of FACT with kinetochores. However, this information is insufficient for a reliable functional analysis at this stage, as the region we identified encompasses the AIDs and the phosphorylation-rich region, both of which have been previously shown to be important for transcription and other functions. Furthermore, any suitable mutant should be tested in cells devoid of endogenous FACT, raising the concern that the resulting phenotype may be indirect.

Nonetheless, as we wanted to provide at least an initial answer to the reviewer's concern, we enriched the manuscript by adding experiments in a recently published cell line (K562-SSRP1-dTAG) where FACT levels can be controlled with a small molecule (Žumer et al. Mol Cell., 2024) and that the authors generously shared with us. In this line, which grows in suspension and that we had to adapt to grow on a substrate for imaging, we were able to deplete FACT while cells were arrested in mitosis. We are glad to report that we found a significant reduction in the kinetochore levels of CENP-TW after this treatment, which is consistent with other conclusions from our study. These experiments add an initial functional characterization of the interaction of FACT with kinetochores, and extend the significance of the manuscript. We refer to these results again below in response to specific point 5.

Specific point

Authors showed nice mitotic localization of FACT. Can they observe this localization by a usual IF? Using GFP fusion, do they observe kinetochore localization like IF experiments?

The localization of FACT was observed using pre-extraction and fixation followed by antibody staining. We have now added a panel demonstrating mitotic localization of GFP-SSRP1 at the kinetochore in transiently transfected RPE-1 cells (Fig. S2A).

On page 7, authors tested CENP-C binding to FACT and they conclude that C-teminal region of CENP-C preferentially binds to FACT. However, they used N-terminal region of CENP-C (2-545) for CCAN-FACT complex formation in entire MS. therefore, this is complicated, and story on CENP-C N-terminal region can be removed from this MS.

We were only able to purify full-length CENP-C with tags at the N- and C-terminus, including an MBP tag with a stabilizing effect. At the time of our first successful purification of full-length CENP-C, we had already established the solid phase assay using MBPFACT as a bait on amylose beads and CENP-C2-545HIKM as one of the preys. As we cannot obtain stable full-length CENP-C without MBP, this form of CENP-C is incompatible with our pull-down assay. Nevertheless, CENP-C2-545 still has low affinity for FACT, influencing the FACT/CCAN interaction independent of the PEST-rich region. We, therefore, opted for keeping this information in the manuscript.

On page 9, authors suddenly focus on N-terminal tails of CENP-Q and CENP-U. Why did they focus on this region. They should explain this. If they perform a structural prediction, they should describe this point.

Thanks for raising this point. We focused on the N-terminal tails of CENP-QU because they are known interaction hubs. We have now added a sentence to introduce this concept and citing the appropriate literature.

I agree the fact that FACT phosphorylation is required for FACT-CCAN interaction. They may explain how the phosphorylation contributes to stable FACT-CCAN interaction.

We have added a sentence explaining that FACT is known to mimic DNA, and negative charges due to phosphorylation could drive this effect. A more detailed mechanistic understanding will require identifying specific phosphorylation sites required for the interaction.

Readers really want to know phenotype, if FACT-CCAN interaction was compromised without disruption pf CCAN assembly in cells. Although I agree that FACT has some functions in the kinetochore, it is still unclear what FACT does in the kinetochore.

We wholeheartedly agree with the reviewer. As depletion of FACT by RNAi required 48 h, an unreasonably long time for this multifunctional protein. We therefore turned to engineering RPE-1 cells for rapid degradation of SSRP1. While these attempts were unsucessful, earlier this year, Žumer et al. Mol Cell., 2024 reported generating a K562-SSRP1-dTAG cell line growing in suspension. As already reported, this cell line now allowed to demonstrate a significant effect on the kinetochore stability of CENP-TW upon mitotic depletion of FACT.

Reviewer #2 (Significance (Required)):

As mentioned above, biochemical parts are beautiful, but the paper did not address significance of FACT-CCAN interaction.

We thank the reviewer for this positive assessment. In this revision, we have obtained initial evidence that FACT contributes to kinetochore stability.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __

Main findings:

The major findings of this paper are:

Detailed dissection of CCAN subunit interactions and requirements to bind the FACT complex using in vitro reconstituted components Binding of FACT and nucleosomes to CENP-C are mutually exclusive FACT phosphorylation by CK2 enhances interaction with CCAN FACT localization in mitosis depends on the CCAN CCAN binding to FACT is outcompeted by DNA and CENP-A nucleosomes The claims and conclusions of the paper are supported by the data and do not require additional experiments. All experiments include biological replicates and appropriate controls.

We are thankful to the reviewer for this very positive assessment of our work.

Minor comments

Intro: • Line 81: In humans [...], here it is worth mentioning that in Drosophila, FACT subunits have been shown to interact directly with the CENP-A assembly factor CAL1 (Ref 61). This paper is perfunctorily cited once in the context of its implication of FACT in CENP-A deposition, but it merits more consideration when setting up the foundational context for the present work.

We have extended the Introduction and discuss the specified paper more thoroughly.

Figure 1:

1F: Add insets.

Done.

1G and all other figures containing IFs: Avoid red/green color scheme (red-green colorblindness is fairly common, affecting about 8% of men).

Done.

1E: Please add a table summarizing interactions.

We have included this table as Fig. S1E.

Results: • It's fine to direct readers to previous work in which you reconstituted the CCAN, but the text should mention how proteins are exogenously expressed and purified (as done for FACT in line 247).

Done.

Line 113: FACT has been shown to localize to the mitotic kinetochore also in Drosophila (Ref 61).

We have included this information now.

Line 132: The authors should cite work from the Drosophila system as well when they mention centromere transcriptional activity in mitosis (e.g. https://doi.org/10.1083/jcb.201404097; https://doi.org/10.1083/jcb.201611087; and Ref 61).

We have added these citations.

Figure 2F: The authors could use a line to mark the region interacting with FACT and that interacting with CENP-A to help summarize the data in this diagram.

Done.

Figure 4: Highlight constructs n.2 (FACT^TRUNC) since these are sufficient for interaction (e.g., use a box around them).

Done.

Line 276: "CCAN decodes CENP-A^NCP..." What do the authors mean by "decodes"? This whole sentence would benefit from clearer language.

We thank the reviewer for this suggestion and have aimed for clearer language.

Figure 6: There's a lot of information in these experiments that would benefit from two schematics, one showing the mechanism of FACT + CCAN binding with DNA and one with CENP-A nucleosomes.

Done.

Discussion: The authors discuss FACT localization at kinetochores in mitosis. In Drosophila Schneider cells, FACT is observed enriched at the centromeres in both mitosis and interphase (Ref 61). The authors mention their inability to detect FACT in interphase in the discussion, but I did not find this mentioned in the results. The authors state that FACT "redistributes to the entire chromosome" upon entry into interphase. They cite Figure 1F in reference to this statement, but the staining in the early G1 panel is difficult to interpret with the low signal/noise scaling of CENP-C and the lack of zoom insets. Their protocol uses a pre-extraction step with Triton prior to fixation. Apparently, this was not enough to reveal FACT in interphase, but better images and a brief description are warranted.

We have now added a staining of SSRP1 in interphase in the panel.

It is unlikely that FACT would change its localization pattern in mitosis. A more likely possibility is that in mitosis FACT is not redistributed, but rather more tightly bound (and thus less easily extracted by Triton treatment) at kinetochores, while along the arms FACT is more readily removed by extraction because at this time transcription is repressed and FACT is likely less engaged in transcription-mediated histone destabilization.

We thank the reviewer for these remarks and have updated the Discussion.

Given the well-known function of FACT in transcription and the many studies linking transcription to centromere maintenance, including with the involvement of FACT, the model that "the localization of FACT at the kinetochore coincides with active centromeric transcription in mitosis and interphase" is very tempting. A speculative model would go a long way to help the reader visualize all these complex aspects of FACT's interactions and possible functions.

We agree with the reviewer that such a model is tempting. However, we also feel that it would be rather speculative at this stage and we feel that the manuscript does not provide sufficient data to support the model.

Reviewer #3 (Significance (Required)):

The strongest aspect of the study is the detailed characterization of protein-protein interactions, as well as competition with DNA and CENP-A nucleosomes. The siRNA experiments in cells complement this largely in vitro study. However, a limitation of the study is that it does not shed light on what FACT might be doing at the centromere. Additionally, it does not sufficiently provide context for these findings in relation to previous studies that have demonstrated the roles of FACT at the centromere in budding yeast, fission yeast, and Drosophila. Nonetheless, this study provides valuable insights into the details of FACT interactions at the kinetochore and will be of interest to readers interested in centromeres and kinetochore. I am a centromere biologist with molecular and cell biology expertise.

We are very grateful to the reviewer for his/her support.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Main findings:

The major findings of this paper are:

• Detailed dissection of CCAN subunit interactions and requirements to bind the FACT complex using in vitro reconstituted components
• Binding of FACT and nucleosomes to CENP-C are mutually exclusive
• FACT phosphorylation by CK2 enhances interaction with CCAN
• FACT localization in mitosis depends on the CCAN
• CCAN binding to FACT is outcompeted by DNA and CENP-A nucleosomes The claims and conclusions of the paper are supported by the data and do not require additional experiments. All experiments include biological replicates and appropriate controls.

Minor comments

Intro:

• Line 81: In humans [...], here it is worth mentioning that in Drosophila, FACT subunits have been shown to interact directly with the CENP-A assembly factor CAL1 (Ref 61). This paper is perfunctorily cited once in the context of its implication of FACT in CENP-A deposition, but it merits more consideration when setting up the foundational context for the present work.

Figure 1:

• 1F: Add insets.
• 1G and all other figures containing IFs: Avoid red/green color scheme (red-green colorblindness is fairly common, affecting about 8% of men).
• 1E: Please add a table summarizing interactions.

Results:

• It's fine to direct readers to previous work in which you reconstituted the CCAN, but the text should mention how proteins are exogenously expressed and purified (as done for FACT in line 247).
• Line 113: FACT has been shown to localize to the mitotic kinetochore also in Drosophila (Ref 61).
• Line 132: The authors should cite work from the Drosophila system as well when they mention centromere transcriptional activity in mitosis (e.g., https://doi.org/10.1083/jcb.201404097; https://doi.org/10.1083/jcb.201611087; and Ref 61).
• Figure 2F: The authors could use a line to mark the region interacting with FACT and that interacting with CENP-A to help summarize the data in this diagram.
• Figure 4: Highlight constructs n.2 (FACT^TRUNC) since these are sufficient for interaction (e.g., use a box around them).
• Line 276: "CCAN decodes CENP-A^NCP..." What do the authors mean by "decodes"? This whole sentence would benefit from clearer language.
• Figure 6: There's a lot of information in these experiments that would benefit from two schematics, one showing the mechanism of FACT + CCAN binding with DNA and one with CENP-A nucleosomes.

Discussion:

The authors discuss FACT localization at kinetochores in mitosis. In Drosophila Schneider cells, FACT is observed enriched at the centromeres in both mitosis and interphase (Ref 61). The authors mention their inability to detect FACT in interphase in the discussion, but I did not find this mentioned in the results. The authors state that FACT "redistributes to the entire chromosome" upon entry into interphase. They cite Figure 1F in reference to this statement, but the staining in the early G1 panel is difficult to interpret with the low signal/noise scaling of CENP-C and the lack of zoom insets. Their protocol uses a pre-extraction step with Triton prior to fixation. Apparently, this was not enough to reveal FACT in interphase, but better images and a brief description are warranted. It is unlikely that FACT would change its localization pattern in mitosis. A more likely possibility is that in mitosis FACT is not redistributed, but rather more tightly bound (and thus less easily extracted by Triton treatment) at kinetochores, while along the arms FACT is more readily removed by extraction because at this time transcription is repressed and FACT is likely less engaged in transcription-mediated histone destabilization. Given the well-known function of FACT in transcription and the many studies linking transcription to centromere maintenance, including with the involvement of FACT, the model that "the localization of FACT at the kinetochore coincides with active centromeric transcription in mitosis and interphase" is very tempting. A speculative model would go a long way to help the reader visualize all these complex aspects of FACT's interactions and possible functions.

Significance

The strongest aspect of the study is the detailed characterization of protein-protein interactions, as well as competition with DNA and CENP-A nucleosomes. The siRNA experiments in cells complement this largely in vitro study. However, a limitation of the study is that it does not shed light on what FACT might be doing at the centromere. Additionally, it does not sufficiently provide context for these findings in relation to previous studies that have demonstrated the roles of FACT at the centromere in budding yeast, fission yeast, and Drosophila. Nonetheless, this study provides valuable insights into the details of FACT interactions at the kinetochore and will be of interest to readers interested in centromeres and kinetochore.

I am a centromere biologist with molecular and cell biology expertise.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

FACT is a histone chaperone and is involved in various events on chromatin such as transcription and replication. In addition, FACT interacts with various kinetochore components, suggesting potential functions at the kinetochore. However, it is largely unclear how FACT functions in the kinetochore. Authors of this MS took the biochemical approach to understand roles of FACT in the kinetochore.

Authors demonstrated that FACT forms a complex with the constitutive centromere associated network (CCAN), which contains 16 subunits on centromeric chromatin, using multiple binding sites. They also showed that casein kinase II (CK2) phosphorylated FACT and dephosphorylated FACT did not bind to CCAN. Furthermore, they displayed that DNA addition disrupt the stable FACT-CCAN complex.

Overall, while authors have done solid and high-quality biochemical analyses (these are elegant), it is still unclear how FACT plays its roles in the kinetochore. Simple knockout or knockdown study on FACT might be complicated, because FACT has multi-functions. If authors can identify specific regions of FACT for interaction with CCAN, they would put specific mutations into FACT to analyze phenotype. Although they did not reach a high-resolution structure for the FACT-CCAN complex, they can utilize AlphaFold and test specific interaction regions, biochemically. Then, using such information, significance of FACT-CCAN interaction might be testable in cells. Such a kind of study would be expected. In summary, biochemical parts are beautiful, but the paper did not address significance of FACT-CCAN interaction.

Specific point

1. Authors showed nice mitotic localization of FACT. Can they observe this localization by a usual IF? Using GFP fusion, do they observe kinetochore localization like IF experiments?
2. On page 7, authors tested CENP-C binding to FACT and they conclude that C-teminal region of CENP-C preferentially binds to FACT. However, they used N-terminal region of CENP-C (2-545) for CCAN-FACT complex formation in entire MS. therefore, this is complicated, and story on CENP-C N-terminal region can be removed from this MS.
3. On page 9, authors suddenly focus on N-terminal tails of CENP-Q and CENP-U. Why did they focus on this region. They should explain this. If they perform a structural prediction, they should describe this point.
4. I agree the fact that FACT phosphorylation is required for FACT-CCAN interaction. They may explain how the phosphorylation contributes to stable FACT-CCAN interaction.
5. Readers really want to know phenotype, if FACT-CCAN interaction was compromised without disruption pf CCAN assembly in cells. Although I agree that FACT has some functions in the kinetochore, it is still unclear what FACT does in the kinetochore.

Significance

As mentioned above, biochemical parts are beautiful, but the paper did not address significance of FACT-CCAN interaction.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

The authors investigated molecular interactions between CCAN and FACT complexes. They revealed contact domains in FACT and the cognate subcomplexes of CCAN by in vitro reconstitution from recombinant proteins followed by SEC and pull-down assay.

They also revealed a couple of potential means to control interactions between FACT and the CCAN. They conclude that phosphorylation of FACT by CK2 is essential for binding to the CCAN; and CENP-A nucleosomes or DNA prevent CCAN from interacting with FACT.

Major comments:

The authors show that phosphorylation of FACT is essential for interaction with CCAN. They argue that this phosphorylation is partly catalysed by CK2.

My concerns are:

1. The authors assume that the sites phosphorylated in insect cell are also phosphorylated in human cells. However, it is not demonstrated which residues are phosphorylated in human cells and whether they match those from insect cells. Whether phosphorylation of recombinant proteins in insect cells is physiologically relevant to mammalian is uncertain. Kinetochore components are not very well conserved evolutionarily, thus their regulation may be different.
2. They identify several residues which are phosphorylated by CK2 in vitro. However, these are not necessarily the same sites as those phosphorylated in insect cells or more importantly in human cells. The in vitro phosphorylation by CK2 did not restore binding affinity in full, suggesting phosphorylation at other sites may be critical for interaction with CCAN. Further evidence is required to support the claim that those sites are phosphorylated in vivo and important for integrity of kinetochores in mitosis.

Minor comments:

Figure 1H

I am confused with 4 stars shown at the top of the right plot. If the 4 stars are meant to show a significant difference, then the statement in the text (line 123) is not correct. "SSRP1 localization was also largely unaffected ..." Similar discrepancies are found in Figures 3H (line 212), Figures S2 (line 122), S5I (line 197), and S6I (line209). Figure S6H is not referred to anywhere. There is no description for the numbers at the top. Are they mean values? Do red bars represent S.D.?

Figure 1D

There is no description of R* to the right of gels.

Figure S2

A 4 hour nocodazole treatment is too short to drive all cells into mitosis. Is the data taken from mitotic cells only?

Significance

The interaction of FACT with kinetochore components has been known for several years. However how FACT contributes to architecture or function of kinetochore is not very well understood. How the FACT complex, which is known for its established role as a histone chaperone, is involved in kinetochore assembly/architecture will attract interest in several fields of basic research including epigenetics, mitosis, structural biology.

Identification of CCAN subunits that interact with FACT is important for future analysis to understand the kinetochore function of FACT. The authors identified OPQRU and CHIKM subcomplex in addition to TW as FACT-interacting domains. These subcomplexes are geographically scattered in a 3D model of CCAN holocomplex. Stoichiometry of CCAN and FACT might be informative whether a single or multiple FACT binds to the multiple sites of CCAN. The authors do not address whether these multiple sites are occupied simultaneously, separately or sequentially.

The statement at the end of Abstract (lines 23-25) is a speculative hypothesis without evidence for "a pool of CCAN that is not stably integrated into chromatin", "chaperoning CCAN", and "stabilisation of CCAN".

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Reply to the Reviewers

I thank the Referees for their...

Referee #1

1. The authors should provide more information when...

Responses + The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A). + Though this is not stated in the MS 2. Figure 6: Why has only...

Response: We expanded the comparison

Minor comments:

1. The text contains several...

Response: We added...

Referee #2

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

In the manuscript from Sogues et al, the authors investigate the S-layer of Corynebacterium glutamicum, a bacterium extensively used in biotechnological applications, using single-particle cryoEM of purified PS2 S-layer, advanced light microscopy, and bioinformatics. They convincingly demonstrate that the C. glutamicum S-layer consists of hexagonal PS2 arrays and provide the underlying structural basis of this assembly. Furthermore, they nicely analyze the conserved and divergent elements of PS2 across Corynebacteria. Engineering SP2 for its use with the SpyTag-SpyCatcher technology revealed, that SP2 is incorporated in the S-layer at the poles.

Minor comments:

• At first it was unclear to me why the authors decided to heterologously express PS2 in C. glutamicum ATCC 13032 if there are other C. glutamicum strains available that naturally harbor an S-layer (e.g. ATCC 13058). It became clear while reading the manuscript but it would help the reader if the authors would clarify and reason their choice of model strain at the beginning of the results section.
• Figure 3: The font size as well as the panels are very small - please increase the size. In panel d, a schematic showing the location of the funnel would aid in an easy understanding of the figure.
• Figure 5: Font sizes are very small. Can the authors make it a full-page figure?
• As this is a back-to-back submission, the manuscript from Isbilir et al. should be cited.
• Typo: Supplementary Figure 5 is labeled as Supplementary Figure 4 in its title.
• Typo in several figure legends: um/nm instead uM/nM (micro/nanometer vs. micro/nanomolar).

Significance

This is a well-written manuscript, scientifically sound, and the conclusions are convincing. Furthermore, I appreciate that the authors are not overselling their findings.

The findings in this manuscript are exciting for a specialized audience interested in bacterial cell surfaces/surface appendages and S-layers. On top, as C. glutamicum is widely used in biotechnological applications, the results have clear significance within this field.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Corynebacterium glutamicum is an important organism with industrial applications, and it constitutes a model organism for the study of other Corynebacteriales, which include important pathogens such as Mycobacterium tuberculosis and Corynebacterium diphtheriae. This work provides with a thorough structural and functional characterization of the S-layer structure of C. glutamicum based on solid data acquired through protein engineering, structural biology, and cell microscopy/imaging studies, and phylogenetic analysis. The authors have determined an atomic structural model of the S-layer from C. glutamicum formed by the protein PS2 exhibiting a different degree of conservation between external and mycomembrane facing surfaces; and they show evidence in vivo of how the S-layer assemble at the cell poles in this organism in line with the actinobacterial elongasome. The authors also show that the presence of the S-layer provides resistance to lysozyme, elaborating several hypotheses that may explain this observation, and demonstrate PS2 S-layer as a feasible platform for covalent surface display both in vitro and in vivo.

The conclusions are well supported by the data provided. When required, experiments have been performed with an adequate number of replicates and their statistical analysis is properly provided. The information provided in the data and methods´ section are sufficient for experimental reproducibility.

No major comments

Minor comments. Text and figures are clear but the following aspects/questions should be addressed/clarified:

• While the authors indicate that "S-layers are two-dimensional monolayered crystals typically composed of a single (glyco)protein ..." (lines 23-24), I haven´t found a reference to whether PS2 is glycosylated or not in the text. If PS2 is glycosylated and its glycosylation sites are known, where would they locate in the glycosylated structure? Would glycosylation affect the size of the pores observed with the recombinant protein?
• Related to the permeability of lysozyme through the S-layer. Have the authors considered the IP of the lysozyme, which (assuming it is hen white egg lysozyme) it´s > 9. Could the negatively charged PS2 nonspecifically capture/retain at the outward-facing surface? Could glycosylation have something to do with it too?
• Clarify which AF version was used for predicting the structural model of PS2, AF2 (as described in the main text, lines 160 and 656) or AF3 (supplementary Fig. 2). If it was AF3, the corresponding reference should be updated.
• Line 205. Replace "Analysis of its surface electrostatics reveals that PS2..." by "Analysis of the electrostatic potential surface of PS2 reveals that..."
• Figure 2 - panels (e), (g), (i), (j). Cartoons and specially ball-and-stick representations colored in white are very hard to visualize or not visible. Please use a darker color or darken the edges to improve visibility. Labels in panel (g) are very small and difficult to see, please increase their size (panels (i) and (j) seem okay).
• Line 215. "vivo and recombinant PS2AD" remove "and".
• Line 1011-12. Replace "...positive in blue to negative in red" by "...positive and negative charges are colored in blue and red, respectively"
• Supplementary figure 3. Reduce the label size in the why axis (probability)
• Supplementary figure 5. It is labeled as "4" instead of "5". The view captured in the figure does not allow to visualize the interface clearly. Please consider another orientation or an alternative representation such an open-book view.
• Supplementary table 1. Replace "BL21(DH3)" by "BL21 (DE3)"
• Review abbreviations, italics, spaces between number and units... (page 517, C. glutamicum in italic; choose either cryoEM or cryo-EM abbreviation for consistency...)

Significance

From my point of view as structural biologist, the present work uncovers key aspects of PS2 S-layer architecture and assemble over the OM of C. glutamicum, together with evidences in vivo of how the S-layer incorporated at cell poles alongside with the bacterial elongasome, and data supporting an implication of the PS2 S-layer in cell envelop stability. These findings constitute an important advance in the structural and functional understanding of S-layer in corynebacteriales, at the time it opens new questions regarding the role of the S-layer in cell integrity and as an interaction interface with external factors. Moreover, the authors present data supporting the feasibility of the PS2 S-layer of C. glutamicum as a protein-based platform to anchor with potential application in bioengineering materials and synthetic biology, and which has the potential to expand the biotechnological/industrial applications of C. glutamicum. Thus, this work has a significant relevance for the scientific community investigating the structure, function and biogenesis of the S-layer and the cell envelop, in particular. But also in a more general outlook, for the scientific community working in the fields of host-pathogen interactions and bioengineering materials.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, the authors investigate the structure of the surface layer, or S-layer, in the Corynebacteriales organism Corynebacterium glutamicum. Studies of the S-layer in Corynebacteriales are lacking and both the function and assembly of the S-layer is unclear in the context of the unique cell envelope of these microbes. In other bacterial systems, the S-layer has been implicated in many critical biological processes. The authors report the ex vivo cryo-EM structure of the S-layer protein PS2 from C. glutamicum, which shows hexameric symmetry with additional trimeric interfaces. The authors show that the C-terminal membrane anchor domain, which is not resolved in the reported structure, is important for lipid binding based on heterologous expression experiments in E. coli. Used the Spytag/Spycatcher tagging system and fluorescence microscopy, the authors determine that S-layer assembly occurs at the cell poles and is likely coordinated the polar growth mechanism of C. glutamicum.

Major comments:

1. The description of the different types of symmetry within the PS2 structure was confusing and difficult to correlate with the structure as depicted in Fig. 2. Authors should clarify labeling and coloring in Fig. 2e, g-j.
2. Investigation of the function of the S-layer as a permeability barrier (Fig. 3e) would be strengthened by testing susceptibility of cells +/- S-layer to different classes of antibiotics or osmotic shock (optional).
3. Due to the probable importance of the membrane-anchoring domain on S-layer function, can the authors comment on potential predicted structure of the regions of the membrane anchoring domain that was not resolved in their structure? How does this region differ between different Corynebacteriales species (or in S-layer proteins in mycobacterial species) that have different mycomembrane dimensions?
4. The authors need to clarify if the version of PS2 used in the live cell imaging experiments detailed in Fig. 4d-f are PS2AD or PS2FL. While they show that PS2AD-Spytag is able to self-assemble, it is possible that the dynamics of PS2AD assembly in vivo are very different from PS2FL due to the absence of the membrane-anchoring domain. Comparison of dynamics between these two constructs would also be a nice addition to the paper.
5. The pulse labeling experiments using Spycatcher would be strengthened by including fluorescent D-amino acids within the same cells to show true co-localization of S-layer assembly and PG synthesis. This could also shed light on the timescale of S-layer assembly in relation to biogenesis of other layers of the cell envelope.

Minor comments:

1. line 71: authors should elaborate on terminology "P6 symmetry"
2. In Fig. 1g, it is not immediately clear that there is lattice formation. Authors should consider including an inset zoomed in box to make this clearer.
3. line 165, 171, 194: do the authors mean "protomers"? If not, use of the word "promoter" is confusing
4. citation on line 374 is incorrect. The cited paper focuses on inner membrane proteins that transport mycolic acid. Also, many of the mycomembrane porins, especially in C. glutamicum do not have a beta-barrel structure (see Ziegler et al, JMC, 2008)
5. Citations detailing polar assembly of other envelope layers would provide additional support for generalized polar assembly of Corynebacteriales cell envelope (arabinogalactan- Marando et al, JACS, 2022) (mycolic acid biosynthesis proteins- Thouvenel et al, Sci Reports, 2023)
6. Some of the supplementary figures are not referenced in the text

Significance

This study is of broad interest to both the Corynebacteriales and S-layer fields. The study is thorough and detailed but could be strengthened by some clarification in how the structure is presented and further discussion of the biological implications of the membrane anchoring domain. There is a long-held interest in understanding how the unique Corynebacteriales cell envelope is assembled, and the work contributes substantially to the field.

Reviewer expertise: bacterial genetics, bacterial cell envelope, protein transport

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a response at this time.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In this manuscript, Anne Schreuder et al studied the genetic vulnerabilities of two previously described hypomorphic BRCA1 missense mutations- I26A and R1699Q, and compare these to a BRCA1-depleted setting to identify novel vulnerabilities of the two hypomorphic BRCA1 alleles. The authors showed that BRCA1I26A mutated cells have very similar vulnerabilities to BRCA1 wildtype cells, while the BRCA1R1699Q mutation induced a more similar phenotype to BRCA1-deficient cells. Then the authors unveiled a unique vulnerability to the loss of NDE1 with increased genomic instability specifically in BRCA1R1699Q mutated cells, but not BRCA1-proficient or -deficient cells. While the experiment design strategy is quite reasonable and the data are quite solid, some of the interpretations look not that convincing.

Major concerns:

1. According to your data, RAD51 IRIF were reduced to similar levels in BRCA1 depleted cells reconstituted with either BRCA1R1699Q or BRCA1I26A mutants，suggesting that both the two mutants have defects in HR (Line 110-117). And when you tested the Olaparib sensitivity, your results showed that unlike wildtype BRCA1, re-expression of BRCA1I26A only partially rescued the sensitivity, suggesting that BRCA1I26A still have the capacity to perform HR (Line 120-125). Since the function of BRCA1I26A is quite controversial in the field, the authors should explain in your experiment why RAD51 IRIF of BRCA1I26A is not correlated with its HR level, these two data should be consistent.

Moreover, in line 194-195, you mentioned that this finding correlates with research showing that the I26A mutation does not affect tumour suppression and HR by BRCA1. It is hard to tell whether BRCA1I26A is defective or functional in HR, what's your opinion about it? If you agree that BRCA1I26A is functional in HR, then why it affects RAD51 IRIF. <br /> 2. In line 175, the authors validated the synthetic lethal interaction between BRCA1 and CSA in BRCA1-depleted RPE1 cells and BRCA1-mutated HCC1937 cells (Figure 2D, Supplemental figure 2A, B, C). Actually, HCC1937 is a both BRCA1 and FAM35A-mutated cell line (DOI: 10.15252/embj.201899543), it is a HR functional cell line that does not response to PARPi. According to your CRSIPR data in Table1 and others publications, loss of 53BP1 or its downstream factors such as C20ORF196, FAM35A are synthetic survival with BRCA1 loss. If CSA is synthetic lethal with BRCA1 loss in HCC1937, suggesting that CSA is not simply synthetic lethal with BRCA1 loss of function, at least not only synthetic lethal with HR deficiency. CSA maybe a promising drug target for treating with the PARPi resistant or the PARPi non-response patients. The authors should mention it in the manuscript. 3. RPE1 hTERT P53-/- BRCA1-/- cells have very severe cell growth defects compared with RPE1 hTERT P53-/- BRCA1+/+ cells. Did you see a growth defect or a certain cell death when you induce acute BRCA1 depletion? In Figure 1C, you only showed the survival rate compared with PARPi non-treatment group. Can you also show the growth curve of all these cell lines? 4. Based on your CRISPR screen results from Table 1,2,3, you made the conclusion that BRCA1I26A exhibits vulnerabilities similar to BRCA1-proficient cells and BRCA1R1699Q exhibits vulnerabilities similar to BRCA1-deficient cells. However, when looked at the data carefully, XRCC1 and several FA genes were all found as synthetic lethality hits with BRCA1-deficient, BRCA1I26A, BRCA1R1699Q. And the known genes such as TP53BP1 and ATMIN were found beneficial for survival in the all three screens. If BRCA1I26A exhibits vulnerabilities similar to BRCA1-proficient cells, then why the known hits in the screen are same with BRCA1-deficient cells. Loss of NDE1 is specifically toxic to cells expressing BRCA1R1699Q. Did you find any target that specifically toxic to cells expressing BRCA1I26A?

It is hard to tell whether your conclusion is correct. Of course, the three cells have some same and also different genetic background, you may consider how to separate the difference. Separate the difference will benefit the treatment for patients with different BRCA1 mutation background.

Minor concerns:

1. RPE1 hTERT P53-/- BRCA1-/- cell line has very clear BRCA1 depletion background. Why at the beginning, you did not choose to use RPE1 hTERT P53-/- BRCA1-/- cells reconstituted with BRCA1 wildtype, BRCA1R1699Q or BRCA1I26A mutants to perform the CRISPR screens? What are the advantages of your strategy by first depletion of BRCA1 with auxin and then inducible express BRCA1 constructs? It looks much more complicated.
2. In Supplemental Figure 2C, a blot to detect BRCA1 should be included.

Significance

If the conclusions are correct, the new findings will tell the importance to differentiate between patient-derived mutations when assessing novel treatment targets.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

Exploiting synthetic lethality based on functional correlations has the potential to significantly improve the survival of cancer patients by reducing resistance to targeted therapies and increasing anti-tumour efficacy when combined with other treatment modalities. Schreuder et al., aim to identifying novel vulnerabilities of patient-derived mutations that could improve patient stratification based on a specific genetic background. Precisely, they established a model system to perform a genome-wide CRISPR-Cas9 KO screen to identify genomic vulnerabilities of BRCA1 variants with reported hypomorphic phenotypes, namely BRCA1 R1699Q and BRCA1 I26A in engineered RPE1 hTERT cells with AID tag. Using this system the authors were able to confirm known synthetic lethal genes reported in literature (e.g. APEX2, PARP1, POLQ) comparing cells with acute BRCA loss and BRCA1 deficiency. Moreover, the screen identified two genes, CSA and GPX4 that were not previously described as synthetic lethal with BRCA1 loss. What is potentially interesting, but marginally explored, is the identification of a unique synthetic vulnerability of cells expressing BRCA1 R1699Q mutant and NDE1 gene encoding for a dynamic scaffold protein essential in neocortical neurogenesis and heterochromatin patterning by H4K20me3, whose loss of function results in nuclear architecture aberrations and DNA double-strand breaks (Chomiak et al., iScience 2022). Accordingly, cells ablated of NDE1 and expressing BRCA1 R1699Q mutant show less proliferation of cells expressing either BRCA1 WT or BRCA1-depleted. Furthermore, cells lacking NDE1 show increased genomic instability by means of increased micronuclei and anaphase bridges compared to BRCA1 proficient and BRCA1 R1699Q mutant.

Major comments:

1. The authors claim that cells expressing BRCA1-I26A are largely HR-proficient, based on a milder effect on Olaparib sensitivity compared to cells expressing BRCA1-R1699A (Fig. 1C). However, I26A mutant cells are defective in RAD51 IRIF (Fig. 1B), indicative of an HR defect. Recently it has been shown that BRCA1 RING mutations that do not impact BARD1 binding, including I26A, render BRCA1 unable to accumulate to DNA damage sites and unable to form RAD51 foci when such mutation is combined with mutations that disable RAP80-BRCA1 interaction (Sherker et al., 2021). How do the authors explain this discrepancy with the literature?
2. The reduction in survival following CSA depletion in BRCA1-proficient vs. -deficient cells is only 20% (Figure 2 and S2B). In my opinion, such a minor difference is not supporting the notion of a SL interaction between BRCA1 and CSA. To substantiate CSA as synthetic lethal hit, I would recommend the authors comparing the effect of CSA loss to that of EXO1 or BLM loss, both genes recently identified by the same group as SL partners of BRCA1 using the same experimental screening set up (van de Kooij et al, 2024). Moreover, validation data for GPX4 is missing.
3. Similar to the minor effect observed for CSA, DOT1L and OTUD5 depletions caused rather mild and/or divergent phenotypes between the two sgRNAs used (Figure 4B), rather arguing against robust SL interactions between those genes and BRCA1 deficiency that could be therapeutically exploited.
4. To strengthen their conclusion in Figure 4C the authors should perform complementation experiments with NDE1 WT and, ideally, with NDE1 mutant(s). On a related note, are NDE1 knock-out cells expressing BRCA1-R1699A more sensitive to PARPi?
5. Graphs shown in Fig. 1A-C, Fig. 4B, S2D, S3B, S3E and S3F are lacking proper statistical analysis of the differences. Some experiments have only been repeated twice (e.g. Figure 1C), precluding running statistical tests.

Minor comments:

1. The authors should include representative images for results shown in Fig.1 A-C
2. The authors should add immunoblots for BRCA1 in Fig. S2C to indicate successful BRCA1 cDNA complementation in HCC1937 cells.
3. Most numbers in the Venn diagram shown in Figure 3A cannot be read when printed.
4. In the western blots shown in Supplemental Figure 1A, the electrophoretic mobility of BRCA1 variants expressed in RPE1 is quite variable. Could the authors indicate in the Figure (e.g. with arrowheads) which bands represent endogenous and which transgenic BRCA1. Moreover, in BRCA-wt complemented cells there are two bands following auxin/DOX addition, whereas there is one band observed in cells expressing BRCA1 hypomorphic variants
5. Line 229 please correct "BRCA1-proficient" to "BRCA1-depleted".

Significance

General assessment:

This manuscript starts with an attractive hypothesis, which is the generation of a cellular system to study patient-derived hypomorphic BRCA1 missense mutations rather than using BRCA1 knockout cells. Performing CRISPR/Cas9-mediated genome-wide synthetic lethal screens in this system allowed uncovering genetic vulnerabilities of cells expressing BRCA1-R1699A, a pathogenic mutant identified in several cancer patients. The data are of good quality and the manuscript is coherent and generally well written (few typos). However, some data describe mainly negative results (e.g. BRCA1-I26A mutant) or weak phenotypes while other more interesting aspects are not rigorously exploited (e.g. NDE1 SL) and therefore need to be interpreted with more caution and extended by additional experiments.

Advance:

BRCA1-R1699Q is classified as a pathogenic variant despite its low penetrance and intermediate cancer risk in breast and ovarian cancer compared to other variants. A recent case report highlighted the unique clinical outcome of a patient with the BRCA1 R1699Q variant, suggesting that this variant may differ from others in terms of cancer risk and drug response (Saito et al., Cancer Treatment and Research Communications 2022). These findings underscore the need for further studies to confirm these observations and to elucidate the specific mechanisms underlying the response to platinum agents and PARP inhibitors in patients with the BRCA1 R1699Q variant. The manuscript proposed by the authors has the potential to help understanding how BRCA1 missense mutations can contribute to determine treatment sensitivity and pave the way to patient stratification.

Audience:

This manuscript is suitable for a specialized, basic research audience.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

1. Point-by-point description of the revisions

• *Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The authors present the use of previously identified biosensors in a single-molecule concentration regime to address lipid effector recruitment. Using controlled and careful single-cell based analysis, the study investigates how expression of the commonly used PIP3 sensor based on Akt-PH domain interferes with the native detection of PIP3. Predominantly live-cell fluorescence microscopy coupled to image analysis drives their studies.

Conceptually, this manuscript carefully and quantitatively describes the influence of lipid biosensor overexpression and presents a means to overcome the inherent and long-recognized problems therein. This solution, namely employing low expression of the lipid biosensor, should be generally applicable. The work is of general interest to cell biologists focused on answering questions at membranes and organelles, including especially those interested in lipid-mediated signaling transductions.

Reviewer 1 Major:

#1.1 The terminology "single molecule biosensor" is not really appropriate. A protein is not "single-molecule". An enzyme does not "single molecule". Better is biosensors at single-molecule expression levels. In most cases, this should be changed. Single-molecule vs single-cell vs. bulk measurements are often poorly defined in quantifications and conflating these does not help the case, which is already supported by generally clear data.

We appreciate the reviewer’s thoughtful critique of our grammatically incorrect use of jargon; we saw this as soon as they mentioned it! We have amended the manuscript where appropriate as detailed:

• Title is now changed to “Lipid Biosensors Expressed at Single Molecule Levels Mitigates Inhibition of Endogenous Effector Proteins”
• Last paragraph of the introduction on __ 2__ now reads “As well as alleviating inhibition of PI3K signaling, biosensors expressed at these low levels show improved dynamic range and report more accurate kinetics than their over-expressed counterparts."
• The title of the results section on __ 6__ is now: Mitigating PIP3 competition using biosensors expressed at single molecule levels
• Last paragraph of the results section on 6 now reads: “this showed that when expressed at single molecule levels, the biosensor has substantially better dynamic range”. #1.2 Figure 1D-F, images not as clearly describing quantitation as one would hope. Untransfected cells in 1E should demonstrate more translocated Akt-pS473 than transfected, but it is difficult for this reviewer to find. Consider inset images in addition to the wider field. Consider also moving the "negative" data of Fig 1B-C to Supplement.

We regret not making this figure easier to interpret; we have substantially updated the figure, as comprehensively detailed in our point-by-point response to reviewer 2’s point 2.3. To specifically address this reviewer’s concerns:

The older figure used non-confocal, low-resolution images that were used for quantification. Such an approach was employed to enable fluorescence from the entire cellular volume to be captured, which produces more robust quantification. However, to the reviewer’s point, it is not possible to see the translocation of PH-AKT1 nor translocated AKT-pS473 in these images. Fortunately, we had in parallel captured high resolution confocal images for some experiments. These are now shown in Fig 1D-E, which clearly shows translocated AKT-pS473 and PH-AKT-EGFP

#1.3 The cell line being used is not clearly specified after the initial development of the NG1 followed by CRISPRed NG2 onto Akt. For example, for the Figure 3C experiments, the text states "complete ablation of endogenous AKT1-NG2" but this information is not apparent from the figure legend or figure. Throughout the cell line used and the aspects transfected need to be made explicitly clear.

We are grateful to the reviewer for highlighting this ambiguity. We have now defined the gene-edited cells used throughout as “AKT1-NG2 cells” and expressly used this term when referring to experiments in figures 2-5.

#1.4 Fig. 5 shows single cells. It is therefore unclear if broken promoters have resulted in decreased expression. This point is important because the expression plasmids should be made publicly available, and for their use to be understood properly, this must be clarified. The details of the plasmids are unclear. Perhaps listed in the table? - unclear. This aspect would be important for the field to effectively use the reagents.

Thank you for drawing our attention to the lack of adequate detail here. We have now updated the results text to expressly reference Morita et al., 2022 where the origins of the truncated CMV promoters are detailed. We have also updated the plasmids table 1 to add pertinent details for these constructs: *pCMVd3 plasmids are based on the pEGFP-C1 backbone, with the CMV promoter truncated to remove 18 of the 26 putative transcription factor binding sites in the human Cytomegalovirus Major Intermediate Enhancer/Promoter (pCMV∆3 as described in Morita et al., 2012). The full sequences will be deposited with the plasmids on Addgene.

We did not perform a formal comparison of full vs truncated promoters. Our only observation is that the truncated promoters greatly help in increasing the number of expressing cells presenting single-molecule resolvable expression levels (though the approach can still work with full promoters).

#1.5 This manuscript speculates several times that with more abundant PIs like PI45P2, the observed saturation effect is probably not happening. This should be removed. While the back of envelope calculations may reflect an ideal scenario, the heterogeneity of distribution and multiple key cellular structures involved would seem to corral increased PI45P2 levels in certain regions. These factors amid multivalency and electrostatic mechanisms of lipid effector recruitment (e.g. MARCKS) suggest that speculation may be too strong. Moreover, Maib et al JCB 2024 demonstrated PI4P probe overexpression could directly mask the ability to detect PI4P post-fixation - not fully, but partially. Repeating the titration experiments of this manuscript for multiple PIs is entirely beyond the scope of reasonable, and hence, such experiments are not requested, in favor of adopting more conscientious speculation.

The reviewer’s point is well taken. Whilst we still believe the overall argument for lipids is sounds (for example, PS or cholesterol are far too abundant for any expressed, stoichiometric binding protein to bind the majority of the population) even abundant phosphoinositides like PI4P and PI(4,5)P2 are an edge case. We have therefore undated the first paragraph of the introduction on __p. 1 __to be less explicit: One of the most prominent is the fact that lipid engagement by a biosensor occludes the lipid’s headgroup, blocking its interaction with proteins that mediate biological function. It follows that large fractions of lipid may be effectively outcompeted by the biosensor, inhibiting the associated physiology. We have argued that, in most cases, this is unlikely because the total number of lipid molecules outnumbers expressed biosensors by one to two orders of magnitude (Wills et al., 2018). However, for less abundant lipids, total molecule copy numbers may be in the order of tens to hundreds of thousands, making competition by biosensors a real possibility.

We also removed the explicit discussion of PI(4,5)P2 from the introduction, and focus now solely on the PI3K lipids.

Reviewer 1 Minor:

1.6 Schematics throughout need simplification, enabling their enlargement.

We have now enlarged the size of all schematics

#1.7 Numerous spelling (Fig. 4 schemas) and capitalizations need fixing.

Thank you for drawing our attention to these. We have thoroughly proof-read the figure panels and corrected errors.

#1.8 Pg 1 Famous is not appropriate wording

We respectfully beg to differ with the reviewer here. We believe it is perfectly accurate to state that PIP3 is a second messenger molecule that is known about by many people; we see this as the dictionary definition of the word “famous”.

#1.9 Fig. 1A statistical testing of microscopy quantifications absent (generally, throughout) and should be included.

This was indeed an oversight on our part. We have now added appropriate multiple comparisons tests to the data presented in figures 1F, 3F, 4C, 4F and 5C.

#1.10 Fig.1. In a transient transfection, the protein expression is not uniform. Please explain how you normalized the quantification.

We hope this is now clarified by the expanded “Image Analysis” part of the methods section on pp. 10-11 (relevant sentence is underlined): For immunofluorescence, we identified individual cells by auto thresholding the DAPI channel using the “Huang” method, followed by the Watershed function to segment bunched cells that appeared to touch. We then used the Voronoi function to generate boundary lines for the segmentation of the cells. To identify cytoplasm, auto thresholding of the CellMask channel using the “Huang” function was employed, with the cells segmented by adding the nuclear Voronoi boundaries. The “analyze particles” function was then used to identify individual cellular ROIs that were greater than 10 µm2 and were not touching the image periphery. These ROIs were used to measure the raw 12-bit intensity of the EGFP and AKT-pS473 channels. A cutoff of EGFP > 100 was used to define EGFP-positive cells, since this value was greater than the mean ± 3 standard deviations of the non-transfected cells’ EGFP intensity. Background intensity of AKT-pS473 was estimated from control cells subject to immunofluorescence in the absence of AKT-pS473 antibody; this value was subtracted from the measured values of all other conditions.

#1.11 Fig. 1D. EGFP expression levels increased with EGF stimulation. How is this possible?

There appeared to be a difference due to the presence of 5 strongly expressing cells in the chosen field in the original field for the EGF stimulated, EGFP cells. However, this arose just by chance. The new set of high-resolution images in the new figure 1 were selected to be more representative.

#1.12 Fig. 1D. The images have pS473 whereas the y-axis label on box plots has p473. Can these box plots be labelled separately for consistency?

Thank you. This has now been corrected in the revised Figure 1.

#1.13 Fig.1. T308 phosphorylation is mentioned in Figure 1, but only pS473 data is shown.

Both T308 and S473 phosphorylation are indicative of AKT activation. However, antibodies suitable for immunofluorescence are only available for pS473, hence why our experiments are restricted to this moiety.

#1.14 Fig.1 legend. 'Over-expression of PH-AKT is hypothesised to outcompete the endogenous AKT's PH domain'. Why do you need to state a hypothesis in the legend?

We included this statement for the benefit of the casual reader – i.e. one who looks at the pictures, but doesn’t read the main text!

#1.15 Fig.1E You stated that the PH-AKT R25C-EGFP is stimulated by EGF addition. However, the GFP signal looks the same in both unstimulated and stimulated. Could you please clarify? Are you sure that the stimulation worked?

We have clarified the second paragraph of the results section “Inhibition of AKT activation by PIP3 biosensor”__on __p. 4 as follows: In the non PIP3 binding PH-AKT1R25C-EGFP positive cells, we still observed an increase in pS473 intensity.

The revised figure 1 images also show that PH-AKT1R25C does not translocate to the membrane with EGF stimulation.

#1.16 You mention...that the AKT enzyme is activated by PDK1 and TORC2, which phosphorylate at residues T308 and S473, respectively. Phosphorylation is also known to occur on T450 at c-tail. Does this phosphorylation also contribute to its activation?

Yes and no. Threonine 450 phosphorylation is thought to occur co-translationally and is important for AKT stability (see Truebestein et al as cited in the manuscript). It is not really relevant in the context for T308 and S473, which are phosphorylated acutely to activate the protein.

#1.17 Fig. 1 scale bar in all images equivalent?

We have now added scale bars to panels in both figure 1D and E to clarify.

__#1.18 __Pg. 1 paragraph 1 "we have argued..." vs. paragraph 3"...consider that an..." feels like arguing with themselves.

We believe the re-write we have done in response to major point #1.5 clarifies this point also.

#1.19 Pg. 1 para 3 what is RFC score - must explain

We have now defined this more clearly in third __paragraph of the __introduction on p. 1: PH domain containing PIP3effector proteins can be predicted based on sequence comparison to known PIP3 effectors vs non effectors using a recursive functional classification matrix for each amino acid (Park et al., 2008).

#1.20 Discussion of numbers of PIP3 vs. effectors etc may not be appropriate for the introduction, as the points made by these calculations are already made in the previous paragraphs. May fit better in pg 6 Mitigating PIP3 titration... with an accompanying schematic.

Respectfully, we prefer to keep this discussion of molecular concentrations, as this adds details and specifics to the pathway that is core to the paper.

#1.21 Pg 2 "a neonGreen" not well defined, needs accurate description.

We have clarified this in the sentence in the first paragraph of the results section “Genomic tagging of AKT1…” __on __p. 4, which includes the citation to the full description of the tag: To that end, we used gene editing to incorporate a bright, photostable neonGreen fluorescent protein to the C-terminus of AKT1 via gene editing using a split fluorescent protein approach (Kamiyama et al., 2016).

#1.22 Fig 2C should give a unstimulated trajectory of puncta/100 um2 to compare with the stimulated

Unfortunately, we did not record a full 5.5-minute video-rate time-lapse with unstimulated cells. However, we do not believe this control is essential for this experiment, since this example data is included to illustrate (1) the problem of photobleaching, which is clear in the 30-s pre-stimulus and (2) the variability in the raw molecule counts.

#1.23 Fig 2C and F and G should be systematized for easier comparison. E.g. min vs seconds, 0 timepoint of EGF/rapa addition

We have made the adjustment to figure 2C to be consistent with 2F and G:

#1.24 Pg 5 "...and calibrated them..." unclear what is being calibrated, as the text later states that the histograms are fit to monomer/dimer/multimer model resulting in 98.1% in monomer. Minor point.

We have clarified this point in the second paragraph of the results section “__Genomic tagging of AKT1…” __on __p. 4 __as follows: We analyzed the intensity of these spots and compared them to intensity distributions from a known monomeric protein localized to the plasma membrane (PM) and expressed at single molecule levels

#1.25 Explain why baselines in Fig2CFG are different

We did not comment on figure 2C; it is a single cell measurement, as opposed to the mean of 20 cells reported in F. However, we do now clarify the difference between figure 2F and G as the very end of the “Genomic tagging of AKT1…” results section on p 4: Notably, baseline AKT-NG2 localization increased from ~5 to ~15 per 100 µm2 in iSH2 cells, perhaps because the iSH2 construct does not contain the inhibitory SH2 domains of p85 regulatory subunits, producing higher basal PI3K activity.

#1.26 Fig. 2 has quantification with images; Fig. 3 has it separate. Make consistent.

We sometimes combine images with quantification, and other times separate the panel containing graphs. This is done deliberately, depending on whether the reader is directed to both together, or whether we consider the data separately in the results section.

#1.27 Fig. 3B comes before images? Where are the images? Also, y-axis = Intensity (a.u.). Is intensity just full image field? Or per cell? All very unclear.

We have modified both the graph y-axis label and the figure legend to clarify: (C) TIRF imaging of AKT1-NG2 cells from (B) stimulated with 10 ng/ml EGF

#1.28 Fig. 3C missing images

We believe the reviewer is referring to the mCherry channel for the “0 ng cDNA” condition. These images are missing because they do not exist. Since these cells were transfected with pUC19, there was no mCherry fluorescence to image.

#1.29 Fig 3 C needs brightness/contrast adjusted as images are nearly entirely black (zero values).

We believe the addition of insets addresses this concern. To the reviewer’s specific suggestion, we found that further increases in the brightness and contrast will bring up the camera noise, but this then occludes the signal from single molecules, such as those found after EGF stimulation of the 0 ng condition.

#1.30 Fig 3C needs scale bar systemization

We believe that the incorporation of scaled 6 µm insets addresses this point.

#1.31 Fig 4 needs 4 panels A-D

We have now added these individual panel labels to figure 4.

#1.32 Pg 6 5-OH phosphatases needs reference

We have added a citation to Trésaugues at the very end of the “Sequestration of PIP3 by lipid biosensors” results section on p. 6, which describes the activity of the whole 5-OH phosphatase activity against PIP3, not just the SHIP phosphatases.

#1.33 Fig 5B, make images bigger

Again, we trust that the addition of insets to all single molecule images has addressed this point.

Reviewer 1 Referees cross-commenting**

I have read the other reviews and find them entirely reasonable. My impression is we landed on similar general content that needs work, none of which is out of line. The importance and care taken in the author's work is uniformly lauded.

We agree. At the risk of restoring to alliteration, we have been delighted to receive a trio of clear, concise and consistent comments on the manuscript! We believe it is now much improved.

Reviewer #1 (Significance (Required)):

This manuscript clearly and reasonably demonstrates that the commonly used PIP3 sensor can be titrated to low concentrations, at which it does not interfere with Akt translocation and activation. This work is a good technical reference for the field. Signal transduction and membrane biologists should be especially interested in the data. The reviewer/s have core expertise in phosphoinositides, protein biochemistry, cell biology, and membrane biophysics.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

The authors characterize the inhibition of lipid second messenger mediated cell signaling through lipid biosensors that outcompete endogenous effector proteins. This is a very important study that as it quantitatively assesses an issue that many people suspected to exit, yet never properly characterized. This paper is therefore as much a service to the community as a research study in its own right and should be published without undue delay. I am glad that the authors decided to carry out this study & really appreciate their work.

I do however, have a number of suggestions that I think will make the manuscript stronger and can be readily implemented, mostly by reformulating and/or re-analysis of exiting datasets. I've structured my comments by the datasets in the respective figures to follow the logic of the paper.

Reviewer 2 Major:

#2.1 Throughout the manuscript, statistical tests are missing, e.g. in figures 1C-F. This must be amended in the revised version. The authors are making a very quantitative point about buffering, data should be treated accordingly.

We have now added appropriate multiple comparisons tests to figures 1F, 3F, 4C, 4F and 5C.

#2.2 I do not think that "PIP3 titration" is the best term to describe the observed effect. "Titration" usually implies the controlled modulation of a concentration, e. g. in analytical chemistry. I think either "competitive binding of PIP3" or "buffering of free PIP3" are more adequate.

This point is well taken. We have now replaced the word “titration” throughout, replacing it with either “competitive binding” or “sequestration”.

#2.3 Specific comments: Figure 1

#2.3a Why are data in 1D-Ff shown as median, with interquartile ranges and 10-90 percentile distance when everything else in the paper is mean +/- se? There might be a good reason for it, but I did not find it mentioned everywhere

For consistency’s sake, we have changed figure 1F to show a bar graph, though as noted in the figure legend: Graphs show medians ± 95% confidence interval of the median from 82-160 cells pooled from three experiments (medians are reported since the data are not normally distributed).

#2.3b The authors should test, whether the difference between the +EGF conditions in 1D (EGFP) and 1F (PH-AktR25C-EGFP) is indeed statistically significant. If this observation holds up, what does it mean? Is the mutant still competing with endogenous Akt despite the much-reduced binding affinity? The authors should discuss.

We have re-analyzed the data in figure 1, with the quantitative data presented in figure 1F combined with statistical analysis. The new data shows no significant effect of the PH-AKT1R25C mutant in either resting or EGF stimulated condition

There results are also described in the__ second paragraph__ of the first results section on pp. 3-4: This analysis showed that the R25C mutant had no substantial effect on pS473 levels, whereas wild-type PH-AKT greatly inhibited pS473 staining in EGF-stimulated cells as well as reducing basal levels in serum starved cells (Fig. 1F).

#2.3c How were biosensor/GFP positive cells chosen? Did the authors choose a defined fluorescence intensity cut-off? I think that a pure manual selection is problematic from a methodological point of view as this may introduce biases. Since the authors use Fiji, they can also simply use the "Analyze particles" function, which allows to automatically segment cells from a thresholded image. By choosing the same threshold for all images, it would be ensured that all images are treated exactly the same way.

We had initially opted for manual outlining of cells since automatic segmentation of irregularly-shaped HEK293a cells is imperfect. However, we agree with André that this opens the possibility of bias. We have therefore re-run the analysis with an automated segmentation and thresholding approach, as suggested. This is detailed in the__ second paragraph__ of the first results section on pp. 3-4: In parallel, we imaged cells with a low resolution 0.75 NA air objective to capture fluorescence from the cells’ entire volume, then quantified these images using an automatically determined threshold for GFP-positive cells (see Materials and Methods). This analysis showed that the R25C mutant had no substantial effect on pS473 levels, whereas wild-type PH-AKT greatly inhibited pS473 staining in EGF-stimulated cells as well as reducing basal levels in serum starved cells (Fig. 1F).

Further detail is provided in the first paragraph of the “Image analysis” subsection of the methods on pp. 10-11: For immunofluorescence, we identified individual cells by auto thresholding the DAPI channel using the “Huang” method, followed by the Watershed function to segment bunched cells that appeared to touch. We then used the Voronoi function to generate boundary lines for the segmentation of the cells’ cytoplasm. To identify cytoplasm, auto thresholding of the CellMask channel using the “Huang” function was employed, with the images segmented by adding the nuclear Voronoi boundaries. The “analyze particles” function was then used to identify individual cellular ROIs that were greater than 10 µm2 and were not touching the image periphery. These ROIs were used to measure the raw 12-bit intensity of the EGFP and AKT-pS473 channels. A cutoff of EGFP > 100 was used to define EGFP-positive cells, since this value was greater than the mean ± 3 standard deviations of the untransfected cells’ EGFP intensity. Background intensity of AKT-pS473 was estimated from control cells subject to immunofluorescence with the AKT-pS473 antibody omitted; this value was subtracted from the measured values of all other conditions.

#2.3d I am missing a statement in the methods section that all images were acquired using the same settings.

This was indeed an important oversight on our part – thanks for spotting the omission of this crucial detail. This is now included at the end of the “Immunofluorescence” section of the Methods on pp. 9-10: Identical laser excitation power, scan speeds and photomultiplier gains were used across experiments to enable direct comparison.

#2.3e I recommend that the authors include a single cell correlation plot of EGFP fluorescence intensity vs AktpS473 intensity in Figure 1 D-F. This should be rather informative & make the concentration dependence clear.

We did not observe a strong correlation between PH-AKT1-EGFP intensity and pS473 staining, likely driven by both the imprecision of the cell segmentation and the fact that very low concentrations of PH domain effectively inhibit endogenous AKT1 (as we show in the later figures with the more precise, live cell AKT-NG2 recruitment experiments: see response to #2.5).

#2.3f I further recommend that the authors look at alterations of baseline Akt activity in the presence of the biosensor. In the images it looks like there might be an effect, but this is then lost in the analysis due to the normalization.

As covered in our response to #2.3b, there is indeed an inhibition of baseline pS473 in PH-AKT1-EGFP expressing cells, now explicitly quantified and documented in results.

#2.3g Please include zoomed image insets in Fig. 1D-F, in the current magnification one needs to zoom in quite a bit to see the effect in the raw data. It is a clear effect, but having a zoomed version would make for much easier reading.

We now include high-resolution confocal images instead of low power, low NA volumes as shown in the last version of the manuscript, which we believe addresses this point and also reviewer #1.2.

2.3h Up to the authors: I wonder whether it is possible to extract an IC50 value for the competitive inhibition of Akt by the respective biosensors. The transient expression gives the authors access to a wide range of expression levels at the single cell level, which could be quantified by counterstaining with a EGFP-nanobody at a different color (since the EGFP fluorophore went through the fixation process, it is likely unsuitable for quantification) and microscope calibration. Activity could be quantified as the ratio of observed and expected Akt-pS473 fluorescence (derived from the mean FI per cell from the EGFP control). This is not strictly necessary, but would be a beautiful quantitative experiment, give an easy-to-understand number & make the paper much stronger.

This is a great suggestion, but does not produce precise enough data to work out, as we detail in response to #2.3e. From our data in new figure 3F and figure 5, it seems we have not explored the appropriate expression range to see intermediate levels of inhibition necessary to estimate IC50. This would be a cool experiment though!

__#2.4 __Specific comments: Figure 2. Overall, compelling data. However, 25 molecules/100 um^2 at maximal recruitment feels low. Assuming a total cell surface area of appr. 2000 um^2 per cell and taking a baseline of 5 molecules/100 um^2 into account, this would mean that only about 400 copies of Akt are recruited in response to a pretty robust stimulus. Is it possible that the association reaction of the split GFP is not complete under these conditions? I think that a direct measurement of intracellular endogenous Akt concentration is required to put these numbers into context.

This is an excellent point that we had missed. We now specifically address this point in the third paragraph of the “Genomic tagging of AKT…” section on p. 4: __Accumulation of AKT-NG2 was ~25 molecules per 100 µm2, which assuming a surface area of ~1,500 µm2 per cell corresponds to ~375 molecules total. It should be noted that tagging likely only occurred at a single allele in each cell, and the population still exhibited expression of non-edited AKT1 (__Fig. 2B). Given that HEK293 are known to be pseudotriploid (Bylund et al., 2004), the true number of AKT1 molecules would be at least 1,125. However, given an estimated total copy number of 23,000 AKT1 in these cells (Cho et al., 2022), this is still only about 5%. However, we do not interpret these raw numbers due to uncertainties in the efficiency of NG2 complementation under these conditions, as well as potential for reduced expression from the edited allele.

We also removed the specific comment on molecule density from the abstract.

#2.5 Specific comments: Figure 3 I think that the classification by plasmid dose does not make a lot of sense, as the resulting expression levels are rather similar. I suggest to pool all traces and calculate mean curves by actual expression levels using a binning approach (e.g. 0-50 au, 50-100 au and so on in raw intensity from Figure 3b). If there is an effect in the realized concentration regime, this should pick it up.

This is an excellent suggestion, and we have done just that: thank you! The data is now included as a new panel Fig. 3F. The result is described in the results section, “Sequestration of PIP3 by lipid biosensors”, end of the first paragraph on pp. 4-6: To observe the concentration-dependence of AKT1-PH-mCherry inhibition, we pooled the single cell data from these experiments and split transfected cells into cohorts based on raw expression level (excitation and gain were consistent between experiments, allowing direct comparison). This analysis showed profound inhibition of AKT1-NG2 recruitment at all expression levels, with a slightly reduced effect only visible in the lowest expressing cohort (Fig. 2F).

#2.6 Specific comments: Figure 5 These are very interesting data, in particular with regard to the underlying PIP3 dynamics. I agree with the conclusion of the authors that shielding of PIP3 from degradation is the likely culprit. What I would like to see here is actual kinetic fits - and different terms. On- and off-rate imply biosensor binding, but these are likely rather fast and not on the minute-timescale. The detected processes are much more likely to reflect production and degradation of PIP3 and that should be reflected in the terminology. For the fit: I think that a simple rate law for subsequent reactions ([PIP3]=C(e^-k1t-e^k2t)) will give good results and yield effective rate constants for PIP3 generation and degradation. This implies the quasi-steady state assumption for biosensor binding and implies that [PIP3] is proportional to the biosensor bound [PIP3], but these are reasonable assumptions to make.

The is an excellent suggestion, which we have added. Specifically, fits are now present on Figs. 5G and 5I; we describe these in the last paragraph of results on p. 8: Normalizing data from both expression modes to their maximum response (Fig. 5G) and fitting kinetic profiles for cooperative synthesis and degradation reactionsrevealed the rate of synthesis is remarkably similar: 1.09 min–1 (95% C.I. 1.02-1.17) for single molecule expression vs 1.02 min-1 (95% C.I. 0.98-1.06) for over-expression. On the other hand, degradation slowed with over expression from 0.34 min–1 (95% C.I. 0.24-0.58) to 0.13 min–1 (95% C.I. 0.12-0.15). This is expected, since synthesis of PIP3molecules would not be prevented by biosensor. On the other hand, PIP3 degradation could be slowed by the over-expressed biosensor competing with PTEN and 5-OH phosphatases that degrade PIP3. An even more exaggerated result is achieved with the cPHx1 PI(3,4)P2 biosensor; this shows an increase in fold-change over baseline of 600% for single molecule expression levels, compared to only 100% in over-expressed cells (Fig. 5H). Again, the degradation rate of the signal is substantially slowed by the over-expressed sensor, reducing from 0.27 min–1 (95% C.I. 0.22-0.39) to 0.16 min–1 (95% C.I. 0.14-0.19), whereas synthesis remains only minorly impacted, changing from 0.61 min–1 (95% C.I. 0.57-0.64) to 0.54 min–1 (95% C.I. 0.52-0.56) with over-expression (Fig. 5I). Collectively, these data show that single molecule based PI3K biosensors show improved dynamic range and kinetic fidelity compared to the same sensors over-expressed.

Details of the fits are given in a new methods section on p. 11:

Fitting of reaction kinetics

Curve fitting was performed in Graphpad Prism 9 or later. For the data presented in Figs. 5G and 5I, both synthesis and degradation phases displayed clear “s” shaped profiles not well fit by simple first order kinetics. Since activation of the PI3K pathway involves many multiplicative interactions between adapters and allosteric activation of the enzymes themselves, we assumed cooperativity and fit reactions with the two phase reaction as follows:

Where Ft denotes ∆Ft/∆FMAX, nsyn and ndeg are the Hill coefficients of the respective synthesis and degradation reactions, and the rate constants for the reactions are derived from ksyn = 1/τsyn and kdeg = 1/τdeg.

André Nadler

Reviewer #2 (Significance (Required)):

This is an important paper, analyses the effects of over-expressed lipid biosensors on cell signalling in some detail and will be of significant interest to a broad readership.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

This is essentially a methods paper in which the authors provide a detailed and highly quantitative analysis of the potentially deleterious effects of expressing phosphoinositide-binding domains as biosensors. Specifically, they study the effects on PIP3 signalling, using biosensors that are widely used in the field.

They show that the most-commonly used method of expressing PIP3 biosensors using transient transfection with viral promotors has clear deleterious effects on downstream signalling due to out-competing the endogenous effectors. Importantly, they also describe a new approach to overcome this by developing new plasmids and methodology to express these reporters at low levels.

Reviewer 3 Major comments:

The work in this paper is thorough and very nicely done. I particularly appreciate the efforts to quantitate or estimate actual numbers and densities of molecules, which significantly strengthen their arguments. The data are excellent and strongly support all their conclusions. I would therefore be happy to see this work published in its current form.

Reviewer 3 Minor comments:

I only have some minor and optional suggestions for improvement.

#3.1 In figure 1D-F they show that PH-Atk-EGFP expression can suppress downstream Akt activation by quantifying P-Akt signal my microscopy. In these panels they say tgey selectively measure this in GFP-expressing cells, but it is not clear how they define which cells are expressing GFP - was a threshold used? Also, it would be nice to also measure both PH-Akt-GFP and P-Akt staining by flow cytometry to look for a correlation. Is there a threshold of biosensor expression that blocks downstream signalling, or is there a linear relationship? This might help specifically measure how much biosensor is too much.

This is an important comment, also raised by reviewer 2. We provide a detailed explanation and outline revisions that address this in our response to reviewer #2.3c; essentially, we replaced the analysis with an automated segmentation and quantification, estimating GFP-positive cells from a fraction of non transfected cells. We have not performed a FACS analysis, but as we note in our response to #2.3e __and #2.3h, the correlation between EGFP and pAKT staining is imprecise in these experiments. The new __Fig. 3C does address this point for AKT1-NG2 recruitment, as described in our response to #2.5.

#3.2 Some of their microscopy images (e.g. Fig 1D-F, Fig 5) are very small and would benefit from a zoom box - especially when they are trying to demonstrate single molecule detection.

This is a fair point raised by all of the reviewers in one form or another. We have added zoomed insets to all of the single molecule images in Figs 2-5, and added higher magnification, confocal section images to Fig. 1.

Reviewer #3 (Significance (Required)):

This is both a methods paper and cautionary tale for cell biologists working in this field. Whilst everyone who uses these probes should be aware of the potential risk of biosensors titrating our effectors, this is often not sufficiently acknowledged. This paper is a very nice and clear demonstration of these risks, exemplified with probably the most highly-used biosensor and key downstream signalling pathway.

Whilst the concepts presented are not especially novel, this paper nonetheless makes an important contribution to the community and hopefully will make others more cautious in how they use these biosensors.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

This is essentially a methods paper in which the authors provide a detailed and highly quantitative analysis of the potentially deleterious effects of expressing phosphoinositide-binding domains as biosensors. Specifically, they study the effects on PIP3 signalling, using biosensors that are widely used in the field.

They show that the most-commonly used method of expressing PIP3 biosensors using transient transfection with viral promotors has clear deleterious effects on downstream signalling due to out-competing the endogenous effectors. Importantly, they also describe a new approach to overcome this by developing new plasmids and methodology to express these reporters at low levels.

Major comments:

The work in this paper is thorough and very nicely done. I particularly appreciate the efforts to quantitate or estimate actual numbers and densities of molecules, which significantly strengthen their arguments. The data are excellent and strongly support all their conclusions. I would therefore be happy to see this work published in its current form.

Minor comments:

I only have some minor and optional suggestions for improvement.

In figure 1D-F they show that PH-Atk-EGFP expression can suppress downstream Akt activation by quantifying P-Akt signal my microscopy. In these panels they say tgey selectively measure this in GFP-expressing cells, but it is not clear how they define which cells are expressing GFP - was a threshold used? Also, it would be nice to also measure both PH-Akt-GFP and P-Akt staining by flow cytometry to look for a correlation. Is there a threshold of biosensor expression that blocks downstream signalling, or is there a linear relationship? This might help specifically measure how much biosensor is too much.

Some of their microscopy images (e.g. Fig 1D-F, Fig 5) are very small and would benefit from a zoom box - especially when they are trying to demonstrate single molecule detection.

Significance

This is both a methods paper and cautionary tale for cell biologists working in this field. Whilst everyone who uses these probes should be aware of the potential risk of biosensors titrating our effectors, this is often not sufficiently acknowledged. This paper is a very nice and clear demonstration of these risks, exemplified with probably the most highly-used biosensor and key downstream signalling pathway.

Whilst the concepts presented are not especially novel, this paper nonetheless makes an important contribution to the community and hopefully will make others more cautious in how they use these biosensors.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors characterize the inhibition of lipid second messenger mediated cell signaling through lipid biosensors that outcompete endogenous effector proteins. This is a very important study that as it quantitatively assesses an issue that many people suspected to exit, yet never properly characterized. This paper is therefore as much a service to the community as a research study in its own right and should be published without undue delay. I am glad that the authors decided to carry out this study & really appreciate their work.

I do however, have a number of suggestions that I think will make the manuscript stronger and can be readily implemented, mostly by reformulating and/or re-analysis of exiting datasets. I've structured my comments by the datasets in the respective figures to follow the logic of the paper.

• Throughout the manuscript, statistical tests are missing, e.g. in figures 1C-F. This must be amended in the revised version. The authors are making a very quantitative point about buffering, data should be treated accordingly.
• I do not think that "PIP3 titration" is the best term to describe the observed effect. "Titration" usually implies the controlled modulation of a concentration, e. g. in analytical chemistry. I think either "competitive binding of PIP3" or "buffering of free PIP3" are more adequate.

Specific comments:Figure 1

• Why are data in 1D-Ff shown as median, with interquartile ranges and 10-90 percentile distance when everything else in the paper is mean +/- se? There might be a good reason for it, but I did not find it mentioned everywhere
• The authors should test, whether the difference between the +EGF conditions in 1D (EGFP) and 1F (PH-AktR25C-EGFP) is indeed statistically significant. If this observation holds up, what does it mean? Is the mutant still competing with endogenous Akt despite the much-reduced binding affinity? The authors should discuss.
• How were biosensor/GFP positive cells chosen? Did the authors choose a defined fluorescence intensity cut-off? I think that a pure manual selection is problematic from a methodological point of view as this may introduce biases. Since the authors use Fiji, they can also simply use the "Analyze particles" function, which allows to automatically segment cells from a thresholded image. By choosing the same threshold for all images, it would be ensured that all images are treated exactly the same way.
• I am missing a statement in the methods section that all images were acquired using the same settings.
• I recommend that the authors include a single cell correlation plot of EGFP fluorescence intensity vs AktpS473 intensity in Figure 1 D-F. This should be rather informative & make the concentration dependence clear.
• I further recommend that the authors look at alterations of baseline Akt activity in the presence of the biosensor. In the images it looks like there might be an effect, but this is then lost in the analysis due to the normalization.
• Please include zoomed image insets in Fig. 1D-F, in the current magnification one needs to zoom in quite a bit to see the effect in the raw data. It is a clear effect, but having a zoomed version would make for much easier reading.
• Up to the authors: I wonder whether it is possible to extract an IC50 value for the competitive inhibition of Akt by the respective biosensors. The transient expression gives the authors access to a wide range of expression levels at the single cell level, which could be quantified by counterstaining with a EGFP-nanobody at a different color (since the EGFP fluorophore went through the fixation process, it is likely unsuitable for quantification) and microscope calibration. Activity could be quantified as the ratio of observed and expected Akt-pS473 fluorescence (derived from the mean FI per cell from the EGFP control). This is not strictly necessary, but would be a beautiful quantitative experiment, give an easy-to-understand number & make the paper much stronger.

Specific comments:Figure 2

• Overall, compelling data. However, 25 molecules/100 um^2 at maximal recruitment feels low. Assuming a total cell surface area of appr. 2000 um^2 per cell and taking a baseline of 5 molecules/100 um^2 into account, this would mean that only about 400 copies of Akt are recruited in response to a pretty robust stimulus. Is it possible that the association reaction of the split GFP is not complete under these conditions? I think that a direct measurement of intracellular endogenous Akt concentration is required to put these numbers into context.

Specific comments:Figure 3

• I think that the classification by plasmid dose does not make a lot of sense, as the resulting expression levels are rather similar. I suggest to pool all traces and calculate mean curves by actual expression levels using a binning approach (e.g. 0-50 au, 50-100 au and so on in raw intensity from Figure 3b). If there is an effect in the realized concentration regime, this should pick it up.

Specific comments:Figure 5

• These are very interesting data, in particular with regard to the underlying PIP3 dynamics. I agree with the conclusion of the authors that shielding of PIP3 from degradation is the likely culprit. What I would like to see here is actual kinetic fits - and different terms. On- and off-rate imply biosensor binding, but these are likely rather fast and not on the minute-timescale. The detected processes are much more likely to reflect production and degradation of PIP3 and that should be reflected in the terminology. For the fit: I think that a simple rate law for subsequent reactions ([PIP3]=C(e^-k1t-e^k2t)) will give good results and yield effective rate constants for PIP3 generation and degradation. This implies the quasi-steady state assumption for biosensor binding and implies that [PIP3] is proportional to the biosensor bound [PIP3], but these are reasonable assumptions to make.

André Nadler

Significance

This is an important paper, analyses the effects of over-expressed lipid biosensors on cell signalling in some detail and will be of significant interest to a broad readership.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The authors present the use of previously identified biosensors in a single-molecule concentration regime to address lipid effector recruitment. Using controlled and careful single-cell based analysis, the study investigates how expression of the commonly used PIP3 sensor based on Akt-PH domain interferes with the native detection of PIP3. Predominantly live-cell fluorescence microscopy coupled to image analysis drives their studies.

Conceptually, this manuscript carefully and quantitatively describes the influence of lipid biosensor overexpression and presents a means to overcome the inherent and long-recognized problems therein. This solution, namely employing low expression of the lipid biosensor, should be generally applicable. The work is of general interest to cell biologists focused on answering questions at membranes and organelles, including especially those interested in lipid-mediated signaling transductions.

Major:

1. The terminology "single molecule biosensor" is not really appropriate. A protein is not "single-molecule". An enzyme does not "single molecule". Better is biosensors at single-molecule expression levels. In most cases, this should be changed. Single-molecule vs single-cell vs. bulk measurements are often poorly defined in quantifications and conflating these does not help the case, which is already supported by generally clear data.
2. Figure 1D-F, images not as clearly describing quantitation as one would hope. Untransfected cells in 1E should demonstrate more translocated Akt-pS473 than transfected, but it is difficult for this reviewer to find. Consider inset images in addition to the wider field. Consider also moving the "negative" data of Fig 1B-C to Supplement.
3. The cell line being used is not clearly specified after the initial development of the NG1 followed by CRISPRed NG2 onto Akt. For example, for the Figure 3C experiments, the text states "complete ablation of endogenous AKT1-NG2" but this information is not apparent from the figure legend or figure. Throughout the cell line used and the aspects transfected need to be made explicitly clear.
4. Fig. 5 shows single cells. It is therefore unclear if broken promoters have resulted in decreased expression. This point is important because the expression plasmids should be made publicly available, and for their use to be understood properly, this must be clarified. The details of the plasmids are unclear. Perhaps listed in the table? - unclear. This aspect would be important for the field to effectively use the reagents.
5. This manuscript speculates several times that with more abundant PIs like PI45P2, the observed saturation effect is probably not happening. This should be removed. While the back of envelope calculations may reflect an ideal scenario, the heterogeneity of distribution and multiple key cellular structures involved would seem to corral increased PI45P2 levels in certain regions. These factors amid multivalency and electrostatic mechanisms of lipid effector recruitment (e.g. MARCKS) suggest that speculation may be too strong. Moreover, Maib et al JCB 2024 demonstrated PI4P probe overexpression could directly mask the ability to detect PI4P post-fixation - not fully, but partially. Repeating the titration experiments of this manuscript for multiple PIs is entirely beyond the scope of reasonable, and hence, such experiments are not requested, in favor of adopting more conscientious speculation.

Minor:

1. Schematics throughout need simplification, enabling their enlargement.
2. Numerous spelling (Fig. 4 schemas) and capitalizations need fixing.
3. Pg 1 Famous is not appropriate wording
4. Fig. 1A statistical testing of microscopy quantifications absent (generally, throughout) and should be included.
5. Fig.1. In a transient transfection, the protein expression is not uniform. Please explain how you normalized the quantification.
6. Fig. 1D. EGFP expression levels increased with EGF stimulation. How is this possible?
7. Fig. 1D. The images have pS473 whereas the y-axis label on box plots has p473. Can these box plots be labelled separately for consistency?
8. Fig.1. T308 phosphorylation is mentioned in Figure 1, but only pS473 data is shown.
9. Fig.1 legend. 'Over-expression of PH-AKT is hypothesised to outcompete the endogenous AKT's PH domain'. Why do you need to state a hypothesis in the legend?
10. Fig.1E You stated that the PH-AKT R25C-EGFP is stimulated by EGF addition. However, the GFP signal looks the same in both unstimulated and stimulated. Could you please clarify? Are you sure that the stimulation worked?
11. You mention...that the AKT enzyme is activated by PDK1 and TORC2, which phosphorylate at residues T308 and S473, respectively. Phosphorylation is also known to occur on T450 at c-tail. Does this phosphorylation also contribute to its activation?
12. Fig. 1 scale bar in all images equivalent?
13. Pg. 1 paragraph 1 "we have argued..." vs. paragraph 3"...consider that an..." feels like arguing with themselves.
14. Pg. 1 para 3 what is RFC score - must explain
15. Discussion of numbers of PIP3 vs. effectors etc may not be appropriate for the introduction, as the points made by these calculations are already made in the previous paragraphs. May fit better in pg 6 Mitigating PIP3 titration... with an accompanying schematic.
16. Pg 2 "a neonGreen" not well defined, needs accurate description.
17. Fig 2C should give a unstimulated trajectory of puncta/100 um2 to compare with the stimulated
18. Fig 2C and F and G should be systematized for easier comparison. E.g. min vs seconds, 0 timepoint of EGF/rapa addition
19. Pg 5 "...and calibrated them..." unclear what is being calibrated, as the text later states that the histograms are fit to monomer/dimer/multimer model resulting in 98.1% in monomer. Minor point.
20. Explain why baselines in Fig2CFG are different
21. Fig. 2 has quantification with images; Fig. 3 has it separate. Make consistent.
22. Fig. 3B comes before images? Where are the images? Also, y-axis = Intensity (a.u.). Is intensity just full image field? Or per cell? All very unclear.
23. Fig. 3C missing images
24. Fig 3 C needs brightness/contrast adjusted as images are nearly entirely black (zero values).
25. Fig 3C needs scale bar systemization
26. Fig 4 needs 4 panels A-D
27. Pg 6 5-OH phosphatases needs reference
28. Fig 5B, make images bigger

Referees cross-commenting

I have read the other reviews and find them entirely reasonable. My impression is we landed on similar general content that needs work, none of which is out of line. The importance and care taken in the author's work is uniformly lauded.

Significance

This manuscript clearly and reasonably demonstrates that the commonly used PIP3 sensor can be titrated to low concentrations, at which it does not interfere with Akt translocation and activation. This work is a good technical reference for the field. Signal transduction and membrane biologists should be especially interested in the data. The reviewer/s have core expertise in phosphoinositides, protein biochemistry, cell biology, and membrane biophysics.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2024-02546

Corresponding author: Woo Jae, Kim

1. General Statements

This is the second version of revision.

After thoroughly reviewing the comments provided by the EMBO Journal reviewers, we found their feedback to be highly constructive and valuable for enhancing our manuscript without the need for additional experiments. For example, Reviewer 1 acknowledged that our "data are intriguing and some of the experiments are quite convincing," but suggested that the manuscript contained excessive data that required simplification. This sentiment was echoed by Reviewer 2. In response, we have completely reformatted our manuscript to eliminate unnecessary imaging quantification data and CrzR-related screening data. The reviewers noted the density of our experimental data, which has led us to focus on the SIFa to Crz-CrzR circuit mechanisms related to heart function and interval timing in future projects.

Reviewer 2's comments were generally more moderate, and we successfully addressed all five of their points with detailed explanations and modifications to our manuscript. They positively remarked that "Overall, this highly interesting study advances our knowledge about the behavioral roles of SIFamide and contributes to an understanding of how motivated behavior such as mating is orchestrated by modulatory peptides." Additionally, Reviewer 3 accepted our manuscript without any further comments.

In summary, we believe we have effectively addressed all concerns raised by Reviewers 1 and 2, resulting in a clearer manuscript that is more accessible to a broader audience.

2. Point-by-point description of the revisions

Reviewer #1

General Comments: In this revision of their manuscript, Zhang et al have attempted to address most of the points raised by the reviewers, however, they have not assuaged my most important concerns. The manuscript contains a ton of information, but at times this is to the detriment of the narrative flow. I had a lot of trouble following the rationale of each experiment, and the throughline from one experiment to the next is not always obvious. The data are intriguing, and some of the experiments are quite convincing, but other experiments are either superfluous or have methodological issues. I will summarize the most acute issues below.

• *Answer: Thank you for your thoughtful feedback and for acknowledging our efforts to address your previous comments. We appreciate your recognition of the intriguing nature of our data and the convincing aspects of our experiments. In this second revision, we have taken your concerns regarding the narrative flow and data overload to heart. We have completely reshaped our manuscript, significantly reducing unnecessary data, including the NP5270 data and overlapping quantification results that did not contribute meaningfully to the storytelling. Our goal was to streamline the presentation of our findings to enhance clarity and coherence, ensuring that each experiment clearly supports the overarching narrative. We believe these revisions will not only improve the readability of our manuscript but also allow readers to follow the rationale behind each experiment more easily. We are confident that this refined approach will make our contributions clearer and more impactful. Thank you once again for your constructive insights, which have been invaluable in guiding us toward a more focused and compelling presentation of our work.

Comment 1. *The authors argue that genetic controls are unnecessary because they have been conducted in previously published papers. I am concerned with this argument, as it is good practice to repeat controls with each experiment. However, I am overall convinced by the basic phenotype indicating that panneuronal SIFaR knockdown eliminates the changes in mating duration associated with previous experience. As for the more restricted 24F06-GAL4, the phenotype is odd-the flies do actually change their mating duration, just in the opposite direction of controls. Doesn't this imply that these flies are still capable of "interval timing", and of changing their mating strategy following exposure to rivals or following sexual experience? *

• *

__ Answer:__ We appreciate the reviewer's critical comments regarding genetic control and the intriguing phenotypes we observed in specific genetic combinations. We fully agree with the reviewer and have repeated all genetic control experiments for this revision, confirming that our genetic controls consistently demonstrate intact LMD and SMD behaviors, as previously reported. These genetic control experiments have been included in Supplementary Information 1-2. We are grateful to the reviewer for the opportunity to reaffirm that LMD and SMD represent stable behavioral phenotypes suitable for genetically studying interval timing, supported by reproducible data.

• *

We acknowledge the reviewer's insightful comments about the exciting phenotype observed when SIFaR is knockdown which shows both singly reared and sexually experienced male show lengthened mating duration in contrast to normal LMD and SMD behaviors. Actually, we have observed such phenotype when specific neural circuits are disrupted such as when sNPF peptidergic signaling is disrupted in restricted neuronal population [4]. We are now investigating such phenotype as hypothesis as disinhibition. We explained this phenotype and about disinhibition in main text as below.

In the spatial, the targeted reduction of SIFaR expression in the GAL424F06 neuronal subset resulted in a notable alteration of mating behavior. Both singly reared and sexually experienced flies exhibited an extended mating duration relative to naïve flies, contrary to the expected reduction. This observation indicates a deficit in the neural mechanism responsible for modulating mating duration, suggesting a disinhibition-like effect within the neural circuitry governing mating behavior. We have also previously observed a similar phenotype when sNPF peptidergic signaling is inhibited in specific neuronal circuits [62]. Disinhibition, characterized by the alleviation of inhibitory constraints, permits the activation of neural circuits that are ordinarily repressed. This process is instrumental in sculpting behavioral patterns and facilitating the sequential progression of behaviors. Through the orchestrated promotion of select neuronal activation and concurrent inhibition of competing neural routes, disinhibition empowers the brain with the ability to dynamically ascertain and preserve the requisite behavioral state, concurrently smoothing the transition to ensuing behavioral phases [63]. It is known that Drosophila neural circuits also exhibit disinhibition phenotypes in light preference and ethanol sensitization [64,65]. Further investigation is needed to uncover the underlying mechanisms of this disinhibition-like phenotype observed in LMD and SMD behaviors.

This reversed phenotype strongly suggests a disruption in interval timing, as one would expect that if interval timing were normal and intact, male flies would decrease their mating duration in response to appropriate environmental changes. For instance, research has shown that patients with Parkinson's disease exhibit heterogeneity in temporal processing, leading to disrupted interval timing phenotypes [5]. Therefore, if male flies subjected to social isolation or sexual experience do not show a reduction in mating duration compared to control conditions, it indicates a potential disruption in their interval timing mechanisms. We appreciate the reviewer's encouragement to further explore this intriguing disinhibition-like phenotype, and we plan to investigate this aspect in our future projects.

Comment 2. *I am glad the see the addition of data assessing the extent of SIFaR and CrzR RNAi knockdown; however, this has not completely addressed my concerns about interpretation of behavioral phenotypes. In both cases, the knockdown was assessed by qPCR using the very strong tub-GAL4 driver. mRNA levels are decreased but not nearly eliminated. Thus, when in line 177-178 the authors assert: "Consequently, we infer that the knockdown of SIFaR using the HMS00299 line nearly completely diminishes the levels of the SIFaR protein," the statement is not supported by the data. The qPCR results showed a knockdown at the mRNA level of ~50%. No assays were conducted to measure protein levels. The conclusions should be tempered to align with the data. Furthermore, it is not clear that knockdown is as successful with other drivers, which means that negative behavioral data must be interpreted with caution. For example, the lack of phenotype with repo-GAL4 driving SIFaR RNAi or elav-GAL4 driving CrzR RNAi could be due to a lack of efficient knockdown. This should be acknowledged. *

   __Answer:__ We appreciate the reviewer's critical observation regarding the efficiency of SIFaR knockdown. We fully agree that it is essential to confirm both for ourselves and our readers that the SIFaR knockdown phenotype is robust and convincing. At the outset of this project, we tested all available SIFaR-RNAi strains following established protocols within the fly community to ensure consistency in our findings. When we employed strong drivers such as tub-GAL4 and nSyb-GAL4 for SIFaR-RNAi knockdown, we observed that the flies failed to eclose and exhibited a lethal phenotype during the larval stage, which closely resembles the homozygous lethal phenotype seen in SIFaR mutants. This suggests that, in most cases, the effects of SIFaR knockdown can effectively mimic those of SIFaR mutations. To share our methodology and reinforce our findings, we have added clarifying statements in the main text as follows:

"Employment of broad drivers, including the tub-GAL4 and the strong neuronal driver nSyb-GAL4, with HMS00299 line consistently results in 100% embryonic lethality (data not shown). This phenotype mirrors the homozygous lethality observed in the SIFaRB322 mutant."

• *

Due to the significant lethality phenotype observed, we conducted PCR analyses using a combination of tub-GAL80ts and SIFaR-RNAi. As detailed in Fig. 1E, we reared the flies at 22{degree sign}C to suppress RNAi expression and then shifted the temperature to 29{degree sign}C for just three days prior to performing PCR. While our PCR results indicate a 50% reduction in SIFaR levels, we believe that experiments conducted without the tub-GAL80ts system would likely demonstrate an even greater reduction in SIFaR expression. To clarify this point and provide additional context, we have included the following description in the main text:

"The silencing of SIFaR mRNA was achieved at approximately 50% using the HMS00299 knockdown line in combination with tub-GAL80ts, with RNAi induction lasting for three days (bottom diagram in Fig. 1E). Notably, the same tub-GAL4 driver, when used without the tub-GAL80ts combination, resulted in embryonic lethality while still reducing SIFaR mRNA levels by 50% after three days of RNAi induction. This finding suggests that SIFaR knockdown using the HMS00299 line with GAL4 drivers is likely sufficient to elicit the observed LMD and SMD behaviors. This rationale underscores the effectiveness of our experimental approach and its potential implications for understanding the role of SIFaR in mating behaviors."

We also concur with the reviewer that the absence of a behavioral phenotype associated with CrzR-RNAi may be due to inefficient RNAi knockdown. Consequently, we have included a description of this issue in the main text as follows:

• *

"It is important to consider that the 50% knockdown of SIFaR and CrzR may be sufficient to disrupt LMD and/or SMD behavior. However, the lack of phenotype with repo-GAL4 or elav-GAL4 could be due to a less efficient knockdown. This possibility highlights the need for cautious interpretation of negative behavioral data."

Comment 3. *Regarding the issue of outcrossing, I am confused by the authors' statement: "To reduce the variation from genetic background, all flies were backcrossed for at least 3 generations to CS strain. For the generation of outcrosses, all GAL4, UAS, and RNAi lines employed as the virgin female stock were backcrossed to the CS genetic background for a minimum of ten generations. Notably, the majority of these lines, which were utilized for LMD assays, have been maintained in a CS backcrossed state for long-term generations subsequent to the initial outcrossing process, exceeding ten backcrosses." It's not clear what this means. Perhaps the authors could definitively state how many times each line was outcrossed. The genetic background is important because of 1) the lack of all controls, and 2) the variability of the behavioral phenotype. Often, the presence or absence of LMD or SMD appears to depend on the behavior of the control flies. When these flies show low mating duration, there is typically not a reduction following sexual experience or group raising. Could these differences derive from genetic background or transgenic insertion effects? *

Answer: We appreciate the reviewer's concern regarding the potential for confusion stemming from our descriptions of the genetic background. As the reviewer noted, we have published multiple papers on LMD and SMD behaviors, and we have conducted our experiments with careful attention to controlling the genetic background [1-3,6-8]. In response to the reviewer's comments about the importance of genetic control and background, we have completed all necessary genetic control experiments and confirmed that all our flies have been backcrossed for more than ten generations to the Canton-S (CS) strain. We believe that we have adequately addressed the reviewer's concerns regarding potential differences arising from genetic background or transgenic insertion effects. To provide readers with more detailed information about our genetic background, we have added a paragraph in the MATERIALS AND METHODS section as follows:

"The CS background was selected as the experimental background due to its well-characterized and consistent LMD and SMD behaviors. To ensure that genetic variation did not confound our results, all GAL4, UAS, and RNAi lines employed in our assays were rigorously backcrossed into the CS strain, often exceeding ten generations of backcrossing. This approach was undertaken to isolate the effects of our genetic manipulations from those of genetic background. We assert that the extensive backcrossing to the CS background, in concert with the internal control in LMD and SMD, provides a stable platform for the accurate interpretation of the LMD and SMD phenotypes observed in our experiments."

Comment 4. *I continue to have substantial concerns about the thresholding method used across many experiments to quantify overlap, and then to claim that this indicates that synaptic connections are being made between different neuronal populations. The degree of overlap will depend on factors including the settings during imaging (was care taken to prevent pixel saturation?). It is also not clear to me from the methods whether analysis was done on single confocal images or on projections. The images shown in the figures look like maximum projections of a confocal stack. Overlap would have to be assessed on individual confocal sections-it is possible that this is what was done for analysis but not clear from the description in the methods. Furthermore, a lot of figure space is dedicated to superfluous information. For example, in Figure 1F-J, there is a massive amount of space dedicated to assessing the agree of overlap between red stinger and CD4GFP, each driven from the same SIFaR2A driver, and further assessing what percentage of the CD4GFP signal overlaps with nc82, with the apparent goal of showing that a lot of the SIFaR signal is at active zones. This information does little to drive the narrative forward, and is quite confusing to read. Finally, the confocal images are generally too small to actually assess. *

   __Answer:__ We appreciate the reviewer's concerns regarding our imaging quantification methods. We recognize the importance of providing a clear and transparent methodology for both readers and the broader scientific community. Instead of using maximum projection of confocal images, we employed a projection method that incorporates the standard deviation function available in ImageJ. Based on our experience, this approach yields more reliable quantification results, allowing for a more accurate assessment of our data. To ensure clarity and reproducibility, we have detailed our methods in the MATERIALS AND METHODS section as follows:

• *

"The quantification of the overlap was performed using confocal images with projection by standard deviation function provided by ImageJ to ensure precise measurements and avoid pixel saturation artifacts."

We appreciate the reviewer's suggestion regarding the inclusion of image quantification data for overlapping regions, which may not be essential to the logical flow of our narrative and could lead to confusion for readers. In response, we have removed nearly all of the quantification data related to overlapping regions, retaining only those that we consider critical for the paper. Currently, only Fig. S3B-E remains, as it is important for illustrating how SIFa neuronal arborization interacts with SIFaR neurons in the central nervous system.

Additionally, we fully agree with the reviewer that the overall size of the confocal images was too small for effective assessment. To address this concern, we have enlarged all confocal images and increased the spacing in the figures. We believe these improvements will enhance the clarity of our manuscript and facilitate a better understanding of our findings.

• *

Comment 5. *In general, the figures are still very cluttered, with panels too close together, and the labels are hard to read. *

Answer: We thank the reviewer for their valuable feedback regarding the clarity of our figures. In response to their concern, we have enlarged the figures to enhance readability and ensure that the panels are more distinct. We believe these adjustments will significantly improve the viewer's ability to interpret the data. We appreciate the reviewer's attention to detail, which has helped us to refine the presentation of our findings.

Comment 6. *There are no methodological details on how the VFB was used. The authors have not addressed my concern that they are showing only the neuronal skeleton (rather than the actual site of synapses). They are simply identifying all locations where the neuronal skeleton overlaps an entire brain region, and suggesting that these represent synapses. Many papers use the VFB to denote the actual location of synapses, which should be done in Figures 3B and S4A. *

Answer: We appreciate the reviewer's constructive comments regarding the methodological details of using VFB data. We fully agree that we cannot draw definitive conclusions about SIFa projections to specific regions based solely on neuronal skeleton data, which do not indicate the actual locations of synapses. To address this concern, we have made it clear to readers that the VFB skeleton data serves only as a preliminary indication of potential SIFa projections to GA, FB, and AL.

To confirm the presence of actual synapses from SIFa neurons, we conducted a thorough analysis using FlyWire data, which validated our findings from VFB. By integrating insights from VFB with the detailed synaptic mapping provided by FlyWire, we can confidently assert the functional relevance of these connections within the context of SIFa neuronal activity. This comprehensive approach not only bolsters our conclusions but also enhances our understanding of how SIFa neurons interact within the broader neural circuitry. We believe this rationale highlights the significance of our work in elucidating the complex relationships among these neuronal populations. We have detailed our findings in the main text as follows:

"We utilized the "Virtual Fly Brain (VFB)" platform, an interactive tool designed for exploring neuronal connectivity, to gain insights into the connectivity of SIFa neurons with four other neurons, specifically GA, FB, and AL (Fig. 3B and Fig. S4B) [74]. While VFB provides valuable information, it does not offer precise locations of synapses originating from SIFa neurons. To address this limitation, we incorporated data from the FlyWire connectome, which allowed us to confirm that SIFa projections indeed form actual synapses with GA, AL, FB, and SMP (Fig. S3F and S3G) [75]. This multi-faceted approach enhances the robustness of our findings by integrating different data sources to validate neuronal connections."

• *

Comment 7. *The changes in GRASP and CaLexA with experience are very interesting, and suggest a substantial rearrangement of synaptic connectivity associated with changes in mating duration following group rearing or female exposure. I am still concerned, however, that the nsyb and tGRASP images look so different. I wouldn't expect them to be identical, but it is puzzling that the nsyb-GRASP data show connections in a few discrete brain areas, while the tGRASP data show connections in a much larger overall brain area, but curiously not in the major regions seen with nsyb-GRASP (ie PI, FB and GA). Shouldn't the tGRASP signal appear in all the places that the nsyb-GRASP does? For CaLexA and GRASP data, the methods should indicate the timing of the dissections and staining relative to the group/sexual experience. *

Answer: We appreciate the reviewer's constructive comments regarding our GRASP data, which indeed reveal an intriguing neural plasticity phenotype, as the reviewer noted. In our previous response, we suggested that the observed differences may be attributed to the distinct SIFa-GAL4 strains utilized, as described in another manuscript focused on SIFa inputs [9]. In that manuscript, we classified the four SIFa neurons into two groups: SIFaDA (dorsal-lateral) and SIFaVP (ventral-posterior). The SIFa2A-GAL4 specifically labels only the SIFaVP neurons, while the SIFa-PT driver labels all four neurons. We acknowledge that we did not clearly communicate this distinction to the reviewer or our readers, and we apologize for any confusion this may have caused. To rectify this oversight, we have added a detailed explanation of these differences in the main text as follows:

"The subtle differences in GRASP signals observed in Fig. 3A may stem from the distinct expression patterns of the SIFa2A-lexA and GAL4SIFa.PT drivers. We would like to emphasize that the SIFa2A driver labels only a subset of SIFa neurons in other regions (Kim 2024)."

We recognize that a clear and transparent methodology is essential for generating reproducible data. In response to the reviewer's suggestion, we have revised our MATERIALS AND METHODS section to include more detailed descriptions of the dissection conditions. This enhancement aims to provide readers with the necessary information to replicate our experiments effectively.

"To ascertain calcium levels and synaptic intensity from microscopic images, we dissected and imaged five-day-old flies of various social conditions and genotypes under uniform conditions. For group reared (naïve) flies, the flies were reared in group condition and dissect right after 5 days of rearing without any further action. For single reared flies, the flies were reared in single condition and dissect at the same time as group reared flies right after 5 days of rearing without any further action. For sexual experienced flies, the flies were reared in group condition after 4 days of rearing and will be given virgins to give them sexual experience for one day, those flies will also be dissected at the same time as group and single reared flies after one day."

• *

Comment 8. *The calcium imaging data are odd. In most cases, the experimental flies don't actually show an increase in calcium levels but rather a lack of a decrease that is present in the ATR- controls. Also, in the cases where they argue for an excitatory affect of SIF neuron stimulation, the baseline signal intensity appears higher in ATR- controls compared to ATR+ experimental flies (eg Fig 5L, 6O), while it is significantly higher in ATR+ flies compared to ATR- controls when the activation results in decreased calcium signals. Perhaps more details on how these experiments were conducted and whether data were normalized in some way would help to clarify this. *

Answer: Thank you for your valuable feedback. We appreciate your careful analysis of our calcium imaging data and have addressed your concerns below:

In our experiments, we observed that ATR+ flies maintained relatively stable calcium levels, whereas ATR- controls exhibited a gradual decrease. Under confocal imaging, GFP signals typically decrease over time, which we observed in ATR- controls. However, ATR+ flies did not exhibit this decline. To better convey this observation, we have refined the language in the manuscript. Specifically, we now describe this as a tendency to sustain the activity of Crz neurons in the OL and AG regions (Fig. 6K-M, Fig. S6G-I). This is supported by the sustained intracellular calcium activity in ATR+ flies compared to the gradual decline to baseline levels observed in ATR- controls (Fig. 6K-M).

Baseline signal intensity differences: You correctly noted that in some cases, the baseline signal intensity appears higher in ATR- controls compared to ATR+ flies. These differences are likely due to technical factors, such as variations in the distance between the imaged brain and the objective lens. Even minor positional shifts in the brain (forward or backward) can affect the observed signal intensity.

Our analyses focus on relative changes in fluorescence intensity within the same sample, which we present as line graphs to highlight trends rather than absolute values. However, we acknowledge that showing the magnitude of relative values instead of absolute values may have caused some confusion. We have revised the images to better align with our conclusions, ensuring that the adjustments do not affect the observed relative changes.

Normalization and experimental details: The calcium imaging data were normalized to ΔF/F to account for differences in baseline fluorescence intensity. However, we recognize that further clarification of the normalization process and experimental setup is essential. We have expanded the methods section to include detailed descriptions of data acquisition, normalization steps, and statistical analyses.

As the reviewer correctly noted, calcium signals in ATR+ flies are generally higher than those in ATR- flies. However, it appears that the calcium levels exhibit a maintained response rather than a dramatic increase compared to the control ATR- condition, particularly in the case shown in Fig. 6K, which illustrates SIFa-to-Crz signaling. We believe this observation may reflect the actual physiological conditions under which SIFa influences SIFaR neurons to sustain activity during activation. We have included our interpretation of these findings in the main text as follows:

"Upon optogenetic stimulation of SIFa neurons, we observed a tendency to maintain the activity of Crz neurons in OL and AG regions (Fig. 6K-M, Fig. S6H-J), evidenced by a sustained activity in intracellular Ca2+ levels that persisted in a high level compared to control ATR- condition which shows gradual declining to baseline levels (Fig. 6K-M). In contrast to the OL and AG regions, the cells in the upper region of the SIP consistently show a decrease in Ca2+ levels following stimulation of the SIFa neurons (Fig. 6N-P)."

To enhance readers' understanding of our calcium imaging results, we have reformatted our GCaMP data for improved clarity and included additional details in the MATERIALS AND METHODS section regarding the quantification of GCaMP imaging methods. Furthermore, as the reviewer correctly noted, discrepancies in baseline activity were due to our error in presenting the baseline data. We have now corrected this oversight accordingly.

• *

Comment 9. *The models in Fig 4 J and T show data from Song et al, though I could not find a citation for this. I would omit this part of the model since these data are not discussed at all in the manuscript. *

Answer: We appreciate the reviewer for correctly identifying our oversight in failing to properly cite Song et al.'s paper. This error occurred partly because the preprint was not available at the time we submitted our manuscript. We now have a preprint for Song et al.'s paper, which discusses the contributions of SIFa neurons to various energy balance behaviors, and we plan to submit this paper back-to-back with our current submission to PLOS Biology. We have briefly cited Song et al.'s work in the manuscript; however, we have removed references to it from Fig. 4J and T to avoid any potential confusion for readers.

Comment 10. *The graphs for the SCOPE data (eg Figure 8I-L) are still too small to make sense of. *

Answer: We enlarged the tSNE plot generated from the SCOPE data.

• *

Comment 11. The rationale behind including the data in Figure 9 is not well explained. I would omit this data to help streamline and focus the manuscript.

Answer: We fully understand and agree with the reviewer's concerns, and we have removed all previous versions of Figure 9 from the manuscript to prevent any confusion regarding the storyline.

• *

Comment 12. *The single control group is still being duplicated in two different graphs but with different names in each graph. The authors updated figure caption hints at this but does not make it explicit. At the very least, these should be given the same name across all graphs, as is done, for example, in the CaLexA experiments in Figure 4B-C. *

Answer: We concur with the reviewer and have changed the label for all "group" conditions to "naïve" in all figures.

• *

Comment 13. *Lines 640-641: Moreover, the pacemaker function is essential for the generation of interval timing capabilities (Meck et al, 2012; Matell, 2014; Buhusi & Meck, 2005), with the heart being recognized as the primary pacemaker organ within the animal body". This is an intriguing idea, however, I attempted to look at the cited references and don't see any claim about the heart being involved in interval timing. I could not find a paper matching the citation of Matell 2014. Meck et al 2012 is an introduction to a Frontiers in Integrative Neuroscience Research Topic and does not mention the heart, nor does the Buhusi and Meck 2005 paper. Perhaps there is a more suitable reference to make the assertion that the fly's interval timer would be affected by changes in heart rate. My suggestion would be to simplify the manuscript, focusing on the most robust findings-the behavioral effect of SIFaR knockdown, the GRASP and CaLexA data showing differences following group rearing or female exposure, and the effect of Crz knockdown in SIFaR neurons. Other details could be included but would have to be verified with more rigorous experiments. *

__ Answer:__ We appreciate the reviewer's interest in our exploration of the role of heart function in interval timing. While we found that knocking down CrzR in the heart specifically disrupts LMD behavior, we agree that our manuscript needs to be streamlined for clarity. As a result, we have eliminated all CrzR-RNAi knockdown data except for the oenocyte, neuronal and glial knockdown data presented in Fig. S8C-H. This decision was made to ensure a more focused comparison with the SIFaR knockdown experiments shown in Fig. 1. We are dedicated to further investigating the role of Crz-CrzR in heart function and its influence on interval timing in a future project. This approach allows us to maintain clarity in our current manuscript while laying the groundwork for more comprehensive studies ahead.

In line with the reviewer's suggestions, we have simplified our manuscript by eliminating unnecessary data, such as overlapping image quantification and CrzR-RNAi screening, allowing us to focus on SIFaR knockdown and GRASP, as well as CaLexA with GCaMP imaging. We are grateful to the reviewer for providing us with the opportunity to delineate the role of CrzR in heart function related to LMD as a significant future project. We believe that our manuscript has been greatly improved by the reviewer's constructive feedback.

• *

__ __

---

Reviewer #2

General Comments:* The authors investigate mating behavior in male fruit flies, Drosophila melanogaster, and test for a role of the SIFamide receptor (SIFaR) in this type of behavior, in particular mating duration in dependence of social isolation and prior mating experience. The anatomy of SIFamide-releasing neurons in comparison with SIFamide receptor-expressing neurons is characterized in a detail-rich manner. Isolating males or exposing them to mating experience modifies the anatomical organization of SIFamidergic axon termini projecting onto SIFamide receptor-expressing neurons. This structural synaptic plasticity is accompanied by changes in calcium influx. Lastly, it is reported that corazonin-releasing neurons are modulated by SIFamide releasing neurons and impact the duration of mating behavior.

Overall, this highly interesting study advances our knowledge about the behavioral roles of SIFamide, and contributes to an understanding how motivated behavior such as mating is orchestrated by modulatory peptides. The manuscript has some points that are less convincing.*

__ Answer:__ We appreciate the reviewer's positive feedback regarding our investigation into the role of the SIFamide receptor (SIFaR) in mating behavior in male Drosophila melanogaster. We are pleased that the detailed characterization of SIFamide-releasing neurons and their anatomical changes in response to social isolation and mating experience has been recognized as a valuable contribution to the understanding of synaptic plasticity and its impact on behavior. We are also grateful that the reviewer described our manuscript as a "highly interesting study" that advances knowledge about the behavioral roles of SIFamide and contributes to the understanding of how motivated behaviors, such as mating, are orchestrated by modulatory peptides. We sincerely thank the reviewer for these encouraging comments about our work.

We acknowledge the reviewer's concerns about certain aspects of our manuscript that may be less convincing. We are committed to addressing these points thoroughly to strengthen our arguments and enhance the clarity of our findings. In response to the feedback, we have made several revisions throughout the manuscript, including clarifying our methodology, enhancing the presentation of our data, and providing additional context where needed. We believe these changes will improve the overall quality of the manuscript and make our conclusions more compelling. Thank you for your thoughtful review, and we look forward to your further insights.

Comment 1. *It remains unclear why the authors link the differentially motivated duration of mating behavior with the psychological concept of interval timing. This distracts from the actually interesting neurobiology and is not necessary to make the study interesting. The study deals with the modulation of mating behavior by SIFamide. The abstraction that SIFamide plays a role in the neuronal calculation of time intervals for the perception of time sequenc es is not convincing in itself. *

• Answer: We appreciate the reviewer's thoughtful comments regarding our conclusion that links SIFamide to interval timing in mating behavior. We recognize that our data primarily indicate that SIFamide is essential for normal mating duration and influences the motivation-dependent aspects of this behavior. We also acknowledge the need for more robust evidence to establish a clearer connection between these findings and interval timing. Recent research by Crickmore et al. has provided valuable insights into how mating duration in Drosophila *serves as an effective model for examining changes in motivation over time as behavioral goals are achieved. For example, around six minutes into mating, sperm transfer occurs, resulting in a significant shift in the male's nervous system, where he no longer prioritizes continuing the mating at the expense of his own survival. This pivotal change is mediated by four male-specific neurons that release the neuropeptide Corazonin (Crz). When these Crz neurons are inhibited, sperm transfer does not take place, and as a result, the male fails to reduce his motivation, leading to matings that can extend for hours instead of the typical duration of approximately 23 minutes [10].

Recent research conducted by Crickmore et al. has secured NIH R01 funding (Mechanisms of Interval Timing, 1R01GM134222-01) to investigate mating duration and sperm transfer timing in Drosophila as a genetic model for understanding interval timing. Their study emphasizes how fluctuations in motivation over time can affect mating behavior, particularly noting that significant behavioral changes occur during mating. For instance, around six minutes into the mating process, sperm transfer takes place, which corresponds with a notable decrease in the male's motivation to continue mating [10]. These findings indicate that mating duration serves not only as an endpoint for behavior but may also reflect fundamental mechanisms associated with interval timing.

   We believe that by leveraging the robustness and experimental tractability of these findings, along with our own work on SIFamide's role in mating behavior, we can gain deeper insights into the molecular and circuit mechanisms underlying interval timing. We will revise our manuscript to clarify this relationship and emphasize how SIFamide may interact with other neuropeptides and neuronal circuits involved in motivation and timing.

   In addition to the efforts of Crickmore's group to connect mating duration with a straightforward genetic model for interval timing, we have previously published several papers demonstrating that LMD and SMD can serve as effective genetic models for interval timing within the fly research community. For instance, we have successfully connected SMD to an interval timing model in a recently published paper [3], as detailed below:

"We hypothesize that SMD can serve as a straightforward genetic model system through which we can investigate "interval timing," the capacity of animals to distinguish between periods ranging from minutes to hours in duration.....

In summary, we report a novel sensory pathway that controls mating investment related to sexual experiences in Drosophila. Since both LMD and SMD behaviors are involved in controlling male investment by varying the interval of mating, these two behavioral paradigms will provide a new avenue to study how the brain computes the 'interval timing' that allows an animal to subjectively experience the passage of physical time [11-16]."

   Lee, S. G., Sun, D., Miao, H., Wu, Z., Kang, C., Saad, B., ... & Kim, W. J. (2023). Taste and pheromonal inputs govern the regulation of time investment for mating by sexual experience in male Drosophila melanogaster. *PLoS Genetics*, *19*(5), e1010753.

   We have also successfully linked LMD behavior to an interval timing model and have published several papers on this topic recently [6-8].

   Sun, Y., Zhang, X., Wu, Z., Li, W., & Kim, W. J. (2024). Genetic Screening Reveals Cone Cell-Specific Factors as Common Genetic Targets Modulating Rival-Induced Prolonged Mating in male Drosophila melanogaster. *G3: Genes, Genomes, Genetics*, jkae255.

   Zhang, T., Zhang, X., Sun, D., & Kim, W. J. (2024). Exploring the Asymmetric Body's Influence on Interval Timing Behaviors of Drosophila melanogaster. *Behavior Genetics*, *54*(5), 416-425.

   Huang, Y., Kwan, A., & Kim, W. J. (2024). Y chromosome genes interplay with interval timing in regulating mating duration of male Drosophila melanogaster. *Gene Reports*, *36*, 101999.

   Finally, in this context, we have outlined in our INTRODUCTION section below how our LMD and SMD models are related to interval timing, aiming to persuade readers of their relevance. We hope that the reviewer and readers are convinced that mating duration and its associated motivational changes such as LMD and SMD provide a compelling model for studying the genetic basis of interval timing in *Drosophila*.

"The dimension of time is the fundamental basis for an animal's survival. Being able to estimate and control the time between events is crucial for all everyday activities [25]. The perception of time in the seconds-to-hours range, referred to as 'interval timing', is involved in foraging, decision making, and learning via activation of cortico-striatal circuits in mammals [26]. Interval timing requires entirely different neural mechanisms from millisecond or circadian timing [27-29]. There is abundant psychological research on time perception because it is a universal cognitive dimension of experience and behavioral plasticity. Despite decades of research, the genetic and neural substrates of temporal information processing have not been well established except for the molecular bases of circadian timing [30,31]. Thus, a simple genetic model system to study interval timing is required. Considering that the mating duration in fruit flies, which averages approximately 20 minutes, is well within the range addressed by interval timing mechanisms, this behavioral parameter provides a relevant context for examining the neural circuits that modulate the Drosophila's perception of time intervals. Such an investigation necessitates an understanding of the extensive neural and behavioral plasticity underlying interval timing [32-37]."

We would like to highlight that many researchers are currently working to bridge the gap between interval timing as a purely psychological concept and its neurobiological underpinnings, as illustrated in the following articles [15,17-20]. We appreciate the reviewer's concerns regarding the relationship between mating duration and interval timing. However, we believe that our LMD and SMD model can effectively bridge the gap between psychological concepts and neurobiological mechanisms using a straightforward genetic model organism. By employing Drosophila as our model, we aim to elucidate the underlying neural circuits that govern these behaviors, thereby contributing to a deeper understanding of how interval timing is represented in both psychological and biological contexts.

Matell, M. S. Neurobiology of Interval Timing. Adv. Exp. Med. Biol. 209-234 (2014) doi:10.1007/978-1-4939-1782-2_12.

Matell, M. S. & Meck, W. H. Cortico-striatal circuits and interval timing: coincidence detection of oscillatory processes. Cogn. Brain Res. 21, 139-170 (2004).

Merchant, H. & Lafuente, V. de. Introduction to the neurobiology of interval timing. Adv Exp Med Biol 829, 1-13 (2014).

Golombek, D. A., Bussi, I. L. & Agostino, P. V. Minutes, days and years: molecular interactions among different scales of biological timing. Philosophical Transactions Royal Soc B Biological Sci 369, 20120465 (2014).

Balcı, F. & Toda, K. Editorial: Psychological and neurobiological mechanisms of time perception and temporal information processing: insight from novel technical approaches. Front. Behav. Neurosci. 17, 1208794 (2023).

Comment 2. *For all behavioral experiments, genetic controls should always be conducted. That is, both the heterozygous Gal4-line as well as the heterozygous UAS-line should be used as controls. This is laborious, but important and common standard. The authors often report data only for offspring from genetc crosses in which UAS-lines and Gal4-lines are combined (e.g. figure S1). This is not sufficient. *

• *Answer: We are grateful for the reviewer's constructive suggestions regarding the genetic control experiments. In response to similar concerns raised by another reviewer, we have conducted all necessary genetic control experiments and included the results in Supplementary Information 1-2. We hope that this thorough effort will demonstrate to both the reviewer and readers that the LMD and SMD behaviors represent stable and reproducible phenotypes for investigating the genetic components of interval timing.

Comment 3. *There are quite a lot of citations of preprints, including preprints from the authors's own lab. It seems inappropriate to cite non-peer reviewed preprints in order to present the basic principles of the study (interval timing in flies) as recognized knowledge. In general, it is unclear whether the information presented in these multiple preprints will turn out to be credible and acceptable. *

• *Answer: We concur with the reviewer and have removed most of the preprint material, retaining only one preprint that discusses SIFa function, which has been co-submitted with this manuscript.

Comment 4. *Anatomical images are often very small and not informative. For example, figure S1 O, R, S and U shows small images of fly brains and ventral nerve chords that do not convincingly describe the expression of fluorescent proteins. The choice of a threshold to quantify fluorescence seems arbitrary. It is also not clear what the quantification "83% of brain and 71% of VNC SIFaR+ neurons" actually tells us. This quantification does not rely on counting neurons (such as 83% of neurons), but only shows how fluorescence in these neurons overlaps with an immunostaining of an ubiquitous active zone protein. The same is true for figure S2 or S3: overlapping brain areas do not inform you about numbers of cells, as stated in the text. *

Answer: We appreciate the reviewer's concerns regarding our imaging quantification methods. In response to similar questions raised by another reviewer, we have thoroughly reformatted our methods section and eliminated much of the overlapping data that appeared unnecessary for this paper. We recognize the importance of providing a clear and transparent methodology for both readers and the broader scientific community. Instead of using maximum projection of confocal images, we employed a projection method that incorporates the standard deviation function available in ImageJ. Based on our experience, this approach yields more reliable quantification results, allowing for a more accurate assessment of our data. To ensure clarity and reproducibility, we have detailed our methods in the MATERIALS AND METHODS section as follows:

• *

"The quantification of the overlap was performed using confocal images with projection by standard deviation function provided by ImageJ to ensure precise measurements and avoid pixel saturation artifacts."

We appreciate the reviewer's suggestion regarding the inclusion of image quantification data for overlapping regions, which may not be essential to the logical flow of our narrative and could lead to confusion for readers. In response, we have removed nearly all of the quantification data related to overlapping regions, retaining only those that we consider critical for the paper. Currently, only Fig. S3B-E remains, as it is important for illustrating how SIFa neuronal arborization interacts with SIFaR neurons in the central nervous system.

Additionally, we fully agree with the reviewer that the overall size of the confocal images was too small for effective assessment. To address this concern, we have enlarged all confocal images and increased the spacing in the figures. We believe these improvements will enhance the clarity of our manuscript and facilitate a better understanding of our findings.

Comment 5. *The authors have consistently confused the extensive overlap of neuronal processes (dendrites and presynaptic regions) across large brain areas with synaptic connections. One cannot infer functional synaptic connectivity from the overlap of these fluorescent signals. *

Answer: We appreciate the reviewer's feedback and, in light of similar comments from another reviewer, we have removed most of the DenMark and syt.eGFP data, retaining only Fig. 3A. We are grateful for the constructive suggestions, which have significantly enhanced our manuscript. We believe that these revisions have clarified the narrative for readers, allowing for a more focused exploration of SIFaR's role in synaptic plasticity and neuronal orchestration.

Reviewer #3

General Comments: In this revised manuscript, the authors have fully and satisfactorily addressed my comments on the previous version. I recommend publication of this manuscript.

__ Answer:__ We would like to extend our heartfelt thanks for the careful consideration and positive assessment of our revised manuscript. Your insightful feedback has been instrumental in shaping the final version of our work, and we are delighted to hear that our revisions have met your expectations.

Your dedication to ensuring the quality and rigor of the scientific literature is truly commendable, and we are immensely grateful for the time and effort you have devoted to reviewing our paper. Your support for publication is a significant encouragement to us and validates the hard work we have put into addressing the issues you raised.

Please accept our sincere appreciation for your professional and constructive approach throughout the review process. We look forward to the possibility of contributing to the scientific community through the dissemination of our research.

REFERENCES

1. Kim WJ, Jan LY, Jan YN. Contribution of visual and circadian neural circuits to memory for prolonged mating induced by rivals. Nat Neurosci. 2012;15: 876-883. doi:10.1038/nn.3104
2. Kim WJ, Jan LY, Jan YN. A PDF/NPF Neuropeptide Signaling Circuitry of Male Drosophila melanogaster Controls Rival-Induced Prolonged Mating. Neuron. 2013;80: 1190-1205. doi:10.1016/j.neuron.2013.09.034
3. Lee SG, Sun D, Miao H, Wu Z, Kang C, Saad B, et al. Taste and pheromonal inputs govern the regulation of time investment for mating by sexual experience in male Drosophila melanogaster. PLOS Genet. 2023;19: e1010753. doi:10.1371/journal.pgen.1010753
4. Zhang X, Miao H, Kang D, Sun D, Kim WJ. Male-specific sNPF peptidergic circuits control energy balance for mating duration through neuron-glia interactions. bioRxiv. 2024; 2024.10.17.618859. doi:10.1101/2024.10.17.618859
5. Merchant H, Luciana M, Hooper C, Majestic S, Tuite P. Interval timing and Parkinson's disease: heterogeneity in temporal performance. Exp Brain Res. 2008;184: 233-248. doi:10.1007/s00221-007-1097-7
6. Sun Y, Zhang X, Wu Z, Li W, Kim WJ. Genetic Screening Reveals Cone Cell-Specific Factors as Common Genetic Targets Modulating Rival-Induced Prolonged Mating in male Drosophila melanogaster. G3: Genes, Genomes, Genet. 2024; jkae255. doi:10.1093/g3journal/jkae255
7. Zhang T, Zhang X, Sun D, Kim WJ. Exploring the Asymmetric Body's Influence on Interval Timing Behaviors of Drosophila melanogaster. Behav Genet. 2024; 1-10. doi:10.1007/s10519-024-10193-y
8. Huang Y, Kwan A, Kim WJ. Y chromosome genes interplay with interval timing in regulating mating duration of male Drosophila melanogaster. Gene Rep. 2024; 101999. doi:10.1016/j.genrep.2024.101999
9. Kim WJ, Song Y, Zhang T, Zhang X, Ryu TH, Wong KC, et al. Peptidergic neurons with extensive branching orchestrate the internal states and energy balance of male Drosophila melanogaster. bioRxiv. 2024; 2024.06.04.597277. doi:10.1101/2024.06.04.597277
10. Thornquist SC, Langer K, Zhang SX, Rogulja D, Crickmore MA. CaMKII Measures the Passage of Time to Coordinate Behavior and Motivational State. Neuron. 2020;105: 334-345.e9. doi:10.1016/j.neuron.2019.10.018
11. Buhusi CV, Meck WH. What makes us tick? Functional and neural mechanisms of interval timing. Nat Rev Neurosci. 2005;6: 755-765. doi:10.1038/nrn1764
12. Merchant H, Harrington DL, Meck WH. Neural Basis of the Perception and Estimation of Time. Annu Rev Neurosci. 2012;36: 313-336. doi:10.1146/annurev-neuro-062012-170349
13. Allman MJ, Teki S, Griffiths TD, Meck WH. Properties of the Internal Clock: First- and Second-Order Principles of Subjective Time. Annu Rev Psychol. 2013;65: 743-771. doi:10.1146/annurev-psych-010213-115117
14. Rammsayer TH, Troche SJ. Neurobiology of Interval Timing. Adv Exp Med Biol. 2014; 33-47. doi:10.1007/978-1-4939-1782-2_3
15. Golombek DA, Bussi IL, Agostino PV. Minutes, days and years: molecular interactions among different scales of biological timing. Philosophical Transactions Royal Soc B Biological Sci. 2014;369: 20120465. doi:10.1098/rstb.2012.0465
16. Jazayeri M, Shadlen MN. A Neural Mechanism for Sensing and Reproducing a Time Interval. Curr Biol. 2015;25: 2599-2609. doi:10.1016/j.cub.2015.08.038
17. Balcı F, Toda K. Editorial: Psychological and neurobiological mechanisms of time perception and temporal information processing: insight from novel technical approaches. Front Behav Neurosci. 2023;17: 1208794. doi:10.3389/fnbeh.2023.1208794
18. Gür E, Duyan YA, Arkan S, Karson A, Balcı F. Interval timing deficits and their neurobiological correlates in aging mice. Neurobiol Aging. 2020;90: 33-42. doi:10.1016/j.neurobiolaging.2020.02.021
19. Merchant H, Lafuente V de. Introduction to the neurobiology of interval timing. Adv Exp Med Biol. 2014;829: 1-13. doi:10.1007/978-1-4939-1782-2_1
20. Matell MS. Neurobiology of Interval Timing. Adv Exp Med Biol. 2014; 209-234. doi:10.1007/978-1-4939-1782-2_12

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary

The article investigates the role of the neuropeptide SIFa and its receptor SIFaR in regulating two distinct mating duration behaviors in male Drosophila melanogaster, Longer-Mating-Duration (LMD) and Shorter-Mating-Duration (SMD). The study reveals that SIFaR expression in specific neurons is required for both behaviors. It shows that social context and sexual experience lead to synaptic reorganization between SIFa and SIFaR neurons, altering internal brain states. The SIFa-SIFaR/Crz-CrzR neuropeptide relay pathway is essential for generating these behaviors, with Crz neurons responding to SIFa neuron activity. Furthermore, CrzR expression in non-neuronal cells is critical for regulating LMD and SMD behaviors. The study utilizes neuropeptide RNAi screening, chemoconnectome (CCT) knock-in, and genetic intersectional methods to elucidate these findings.

Major Comments

• Are the key conclusions convincing? The key conclusions are intriguing but require more robust data to be fully convincing. While the study presents compelling evidence for the involvement of SIFa and SIFaR in mating behaviors, additional experiments are needed to firmly establish the proposed mechanisms.
• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? The authors should qualify certain claims as preliminary or speculative. Specifically, the proposed SIFa-SIFaR/Crz-CrzR neuropeptide relay pathway is only investigated via imaging approach. More experiments using behavioral tests are needed to confirm that Crz relays the SIFa signaling pathway. For example, Crz-Gal4>UAS-SIFaR RNAi should be done to show that SIFaR+ Crz+ cells are necessary for LMD and SMD.
• Would additional experiments be essential to support the claims of the paper? Yes, additional experiments are essential. Detailed molecular and imaging studies are needed to support claims about synaptic reorganization. For example:
  • More controls are needed for RNAi and Gal80ts experiments, such as Gal4-only control, RNAi-only control, etc.
  • Using synaptic markers and high-resolution imaging to observe synaptic changes directly.
  • Electrophysiological recordings from neurons expressing SIFa and SIFaR to analyze their functional connectivity and activity patterns.
• Are the suggested experiments realistic in terms of time and resources? The suggested experiments are realistic but will require considerable time and resources. Detailed molecular interaction studies, imaging synaptic plasticity, and electrophysiological recordings could take several months to over a year, depending on the complexity and availability of necessary equipment and expertise. The cost would be moderate to high, involving expenses for reagents, imaging equipment, and animal husbandry for maintaining Drosophila stocks.
• Are the data and the methods presented in such a way that they can be reproduced? The methods are generally described in detail, allowing for potential reproducibility. However, more precise documentation of certain experimental conditions, such as the timing and conditions of RNAi induction and temperature controls, is necessary. The methods about imaging analysis are too detailed. The exact steps about how to use ImageJ should be removed.
• Are the experiments adequately replicated and statistical analysis adequate? Most figures in the manuscript need to be re-plotted. The right y-axis "Difference between means" is not necessary, if not confusing. The image panels are too small to see, while the quantification of overlapping cells are unnecessarily large. The figures are too crowded with labels and texts, which makes it extremely difficult to comprehend the data.

Minor Comments

• Specific experimental issues that are easily addressable. Clarify the timing of RNAi induction and provide more detailed figure legends for better understanding and reproducibility.
• Are prior studies referenced appropriately? Yes.
• Are the text and figures clear and accurate? The text is generally clear, but the figures need re-work. See comment above.
• Suggestions to improve the presentation of data and conclusions. Use smaller fonts in the bar plots and make the plots smaller. Enlarge the imaging panels and let the pictures tell the story.

Significance

Nature and Significance of the Advance

This study aims to advance understanding of how neuropeptides modulate context-dependent behaviors in Drosophila. It provides novel insights into the role of SIFa and SIFaR in interval timing behaviors, contributing to the broader field of neuropeptide research and behavioral neuroscience. However, the significance of the findings is limited by the preliminary nature of some claims and the need for additional supporting data.

Context in Existing Literature

The work builds on previous studies that identified various roles of neuropeptides in behavior modulation but lacked detailed mechanistic insights. By elucidating the SIFa-SIFaR/Crz-CrzR pathway, this study attempts to fill a gap in the literature, but more robust evidence is required to solidify its contributions.

Interested Audience

The findings will interest neuroscientists, behavioral biologists, and researchers studying neuropeptides and their roles in behavior and neural circuitry. Additionally, this research may have implications for understanding neuropeptidergic systems in other organisms, making it relevant to a broader audience in the fields of neurobiology and physiology.

Field of Expertise

Keywords: Neuropeptides, Drosophila melanogaster, Behavioral Neuroscience. Areas without sufficient expertise: courtship behavior.

Recommendation

I recommend a major revision of this manuscript. The study presents intriguing findings, but several key claims are preliminary and require additional experiments for support. The data is poorly presented and the figures can be significantly improved. Detailed molecular and imaging studies, as well as more rigorous statistical analyses, are necessary to strengthen the conclusions. Addressing these concerns will significantly improve the robustness and impact of the paper.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Zhang et al., "Long-range neuropeptide relay as a central-peripheral communication mechanism for the context-dependent modulation of interval timing behaviors".

The authors investigate mating behavior in male fruit flies, Drosophila melanogaster, and test for a role of the SIFamide receptor (SIFaR) in this type of behavior, in particular mating duration in dependence of social isolation and prior mating experience. The anatomy of SIFamide-releasing neurons in comparison with SIFamide receptor-expressing neurons is characterized in a detail-rich manner. Isolating males or exposing them to mating experience modifies the anatomical organization of SIFamidergic axon termini projecting onto SIFamide receptor-expressing neurons. This structural synaptic plasticity is accompanied by changes in calcium influx. Lastly, it is shown that corazonin-releasing neurons are modulated by SIFamide releasing neurons and impact the duration of mating behavior.

Overall, this highly interesting study advances our knowledge about the behavioral roles of SIFamide, and contributes to an understanding how motivated behavior such as mating is orchestrated by modulatory peptides. The approach to take the entire organism, including peripheral tissue, into consideration, is very good and a rather unique point. The manuscript has only some points that are less convincing, and these should be addressed.

Major concerns:

• It is highly interesting that the duration of mating behavior is dependent on external and motivational factors. In fact, that provides an elegant way to study which neuronal mechanisms orchestrate these factors. However, it remains elusive why the authors link the differentially motivated durations of mating behavior to the psychological concept of interval timing. This distracts from the actually interesting neurobiology, and is not necessary to make the study interesting.
• In figure 4 A and 4K, fluorescence microscopy images of brains and ventral nerve chords are shown, one illustrating GRASP experiments, and one showing CaLexA experiments. The extreme difference between the differentially treated flies (bright fluorescence versus almost no fluorescence) is - in its drastic form- surprising. Online access to the original confocal microscopy images (raw data) might help to convince the reader that these illustrations do not reflect the most drastic "representative" examples out of a series of brain stainings.
• In particular for behavioral experiments, genetic controls should always be conducted. That is, both the heterozygous Gal4-line as well as the heterozygous UAS-line should be used as controls. This is laborious, but important.

Minor comments:

• Line 75: word missing ("...including FEEDING-RELATED BEHAVIOR, courtship, ...").
• Line 120: word missing ("SIFaR expression in adult neurons BUT not glia...").
• I find the figures often to be quite overloaded, and anatomical details often very small (e.g., figure 7A).

Significance

Overall, this highly interesting study advances our knowledge about the behavioral roles of SIFamide, and contributes to an understanding how motivated behavior is orchestrated by modulatory peptides. The approach to take the entire organism, including peripheral tissue, into consideration, is very good and a rather unique point.

Since decades it has been investigated how sensory stimuli are processed and encoded by the brain, and how behavioral actions are executed. Likewise, principles underlying learning and memory, sleep, orentation, circadian rhythms, etc. are subject to intense investigation. However, how motivational factors (sleep pressure, hunger, sexual drive) are actually "encoded", signaled and finally used to orchstrate behavior and guide decision-making is, to a very large degree, unknown - in any species. The model use here (Drosophila and its peptidergic system wit SIFamide as a central hub) represents actually a ideal entry point to study just this question. In this sense, the manuscript is at the forefront of modern, state-of-the-art neurobiology.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

This manuscript from Zhang et al. primarily investigates the contribution of the SIFa neuropeptide receptor (SIFaR) to mating duration in male fruit flies. Through RNAi-mediated downregulation, they show that SIFaR receptor is necessary for previous experience to alter mating duration. Using cell-specific knockdown and rescue of the SIFaR receptor, they identify a population of ~400 neurons that could underlie this effect. This is still a large number of cells but is narrowed from the ~1,200 total SIFaR-expressing neurons. They then use the GRASP synaptic labeling technique to show that SIFa+ neurons form synapses onto the relevant SIFaR-expressing population, and that the area of synaptic contact is systematically altered depending on the fly's past mating history. Finally, they provide evidence to argue that SIFa neurons act through SIFaR neurons that release the neuropeptide corazonin to regulate mating duration. Overall, the authors have used an impressive array of techniques in their attempt to define the neural circuits and molecules involved in changing internal state to modify the duration of mating.

Major Comments:

1. The authors are to be commended for the sheer quantity of data they have generated, but I was often overwhelmed by the figures, which try to pack too much into the space provided. As a result, it is often unclear what components belong to each panel. Providing more space between each panel would really help.
2. The use of three independent RNAi lines to knock down SIFaR expression is experimentally solid, as the common phenotype observed with all 3 lines supports the conclusion that the SIFaR is important for mating duration choice. However, the authors have not tested whether these lines effectively reduce SIFaR expression, nor whether the GAL80 constructs used to delimit knockdown are able to effectively do so. This makes it hard to make definitive conclusions with these manipulations, especially in the face of negative results. A lack of complete knockdown is suggested by the fact that the F24F06 driver rescues lethality when used to express SIFaR in the B322 mutant background, but does not itself produce lethality when used to express SIFaR RNAi. The authors should either conduct experiments to determine knockdown efficiency or explicitly acknowledge this limitation in drawing conclusions from their experiments. A similar concern relates to the CrzR knockdown experiments (eg Figure 7).
3. Most of the behavioral experiments lack traditional controls, for example flies that contain either the GAL4 or UAS elements alone. The authors should explain their decision to omit these control experiments and provide an argument for why they are not necessary to correctly interpret the data. In this vein, the authors have stated in the methods that stocks were outcrossed at least 3x to Canton-S background, but 3 outcrosses is insufficient to fully control for genetic background.
4. Throughout the manuscript, the authors appear to use a single control condition (sexually naïve flies raised in groups) to compare to both males raised singly and males with previous sexual experience. These control conditions are duplicated in two separate graphs, one for long mating duration and one for short mating duration, but they are given different names (group vs naïve) depending on the graph. If these are actually the same flies, then this should be made clear, and they should be given a consistent name across the different "experiments".
5. The authors have consistently conflated overlap of neuronal processes with synaptic connections. Claims of synaptic connectivity deriving solely from overlap of processes should be tempered and qualified.
   • For example, they say (Lines 201-202) "These findings suggest that SIFa neurons and GAL424F06-positive neurons form more synapses in the VNC than in the brain." This is misleading. Overlap of24F06-LexA>CD8GFP and SIFa-GAL4>CD8RFP tells us nothing about synapse number, or even whether actual synapses are being formed.
   • Lines 210-211: "The overlap of DenMark and syt.EGFP signals was highly enriched in both SOG and ProNm regions, indicating that these regions are where GAL424F06 neurons form interconnected networks". This is misleading. Overlap of DenMark and syt.EGFP does not indicate synapses (especially since these molecules can be expressed outside the expected neuronal compartment if driven at high enough levels).
   • Lines 320-322: "Neurons expressing Crz exhibit robust synaptic connections with SIFaR24F06 neurons located in the PRW region of the SOG in the brain (panels of Brain and SOG in Fig. 5A)". This is again misleading. They are not actually measuring synapses here, but instead looking at area of overlap between neuronal processes of Crz and SIFaR cells.
   • In Figs 3B and S4A, they are claiming that all neuronal processes within a given delineated brain area are synapses. The virtual fly brain and hemibrain resource have a way to actually identify synapses. This should be used in addition to the neuron skeleton. Otherwise, it is misleading to label these as synapses.
   • Furthermore, measuring the area of GRASP signal is not the same as quantifying synapses. We don't know if synapse number changes (eg in lines 240-242).
6. In general, the first part of the manuscript (implicating SIFaR in mating duration) is much stronger than the second part, which attempts to demonstrate that SIFa acts through Crz-expressing neurons to induce its effects. The proof that SIFa acts through Crz-expressing neurons to modify mating duration is tenuous. The most direct evidence of this, achieved via knockdown on Crz in SIFaR-expressing cells, is relegated to supplemental figures. The calcium response of the Crz neurons to SIFa neuron activation (Fig. 6) is more of a lack of a decrease that is observed in controls. Also, this is only done in the VNC. Why not look in the brain, because the authors previously stated a hypothesis that the "transmission of signals through SIFaR in Crz-expressing neurons is limited to the brain" (lines 381-382)?

Furthermore, the authors suggest that Crz acts on cells in the heart to regulate mating duration. It would be useful to add a discussion/speculation as to possible mechanisms for heart cells to regulate mating decisions. Is there evidence of CrzR in the heart? The SCope data presented in Fig. 7I-L and S7G-H is hard to read. 7. In several cases, the effects of being raised single are opposite the effects of sexual experience. For example, in Fig. 4T, calcium activity is increased in the AG following sexual experience, but decreased in flies raised singly. Likewise, Crz-neurons in the OL have increased CaLexA signal in singly-raised flies but reduced signals in flies with previous sexual experience. In some cases, manipulations selectively affect LMD or SMD. It would be useful to discuss these differences and consider the mechanistic implications of these differential changes, when they all result in decreased mating duration. This could help to clarify the big picture of the manuscript.

Minor Comments:

1. For CaLexA experiments (eg Fig 7A-D), signal intensity should be quantified in addition to area covered. Increased intensity would indicate greater calcium activity within a particular set of neurons.
2. In Figure 5K: quantification of cell overlap is missing. In the text they state that there are ~100 neurons that co-express SIFaR24F06 and Crz. How was this determined? Is there a graph or numerical summary of this assertion?
3. In lines 709-711: "Our experience suggests that the relative mating duration differences between naïve and experienced condition and singly reared are always consistent; however, both absolute values and the magnitude of the difference in each strain can vary. So, we always include internal controls for each treatment as suggested by previous studies." I had trouble understanding this section of methods. What is done with the data from the internal controls?
4. Could the authors comment on why the brain GRASP signal is so different in Figures 3A and 4A? I realize that different versions of GRASP were used in these experiments, but I would expect broad agreement between the different approaches.

Significance

This study will be most relevant to researchers interested in understanding neuronal control of behavior. The manuscript offers a conceptual advance in identifying cell types and molecules that influence mating duration decisions. The strength of the manuscript is the number of different assays used; however, there is a sense that this has occurred at the cost of providing a cohesive narrative. The first part of the manuscript (detailing the role of SIFaR in LMD and SMD) is relatively stronger and more conclusive.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

We want to thank both reviewers for their thorough and constructive review of our manuscript. Below, we have re-iterated their comments followed by an explanation of how we have revised the manuscript to address this.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

This manuscript presented by Segeren et al. applied an interesting HRASG12V inducible cell model to study the mechanism of cellular resistance to replication stress inducing agents. They also employed a novel reversible fixation technique which allows them to FAC sort cells according to their replication stress levels before applying single cell sequencing analysis to the same cell populations. By comparing cells with low levels of replication stress to cells with high levels of replication stress, they found that reduction in gene expression of FOXM1 target genes potentially protects cells against replication stress induced by CHK1i plus gemcitabine combination. Overall, this is a very interesting study. However, the following points should be addressed prior to publication:

Major: 1. Figure 3E and 3F showed two lists of differentially expressed genes in γH2Ax low cells. However, instead of arbitrarily extracting the FOXM1 target genes and TP53 targeted genes, it would be appreciated if the author could perform an unbiased and unsupervised gene set enrichment analysis such as Enrichr.

As recommended, we performed an enrichment analysis using Enrichr to identify transcriptional programs associated with the we used the genes that were downregulated in the γH2AX-low cells. FOXM1 appeared as a prominent hit in different databases (both experimental and computational). We have included the lists of differentially expressed genes as an additional supplemental table (Table S1) and have included the Enrichr results as Table S3 (i.e. CHEA and ENCODE). We have described our results in lines 198-200 of the revised manuscript.

1. At the experiment design stage, the authors also included HRASG12V status as a test condition because they previously found that HRASG12V mutation induces basal level replication stress and they would like to include this condition to study the adaptation to replication stress (line 110). However, the difference in HRASG12V negative and HRASG12V positive cells was not followed up in the later part of the paper. Can they show lists of differentially expressed genes identified under HRASG12V negative conditions as well (in the same format of Figure 3E and 3F) and comment on the differences as well?

In the original manuscript, we included heatmaps of differentially expressed genes in the control cells in Figure S2. For improved clarity, we have modified this figure so that the heatmaps are labeled "Control cells". In the revised manuscript, we have also included Table S2, which lists the differentially expressed genes between yH2AX low and yH2AX high control cells, and Table S3, which lists the Enrichr results obtained based on these gene lists.

We observed FOXM1 target genes in both the control and HRASG12V cells. Thus, the mechanism we identify does not appear to be specific to oncogenic Ras expression. We discuss this in lines 221-225. Because there were no other notable differences between the gene sets, we do not focus on this in the manuscript.

1. In line 194 and in Figure S2B, the authors claimed that ANLN, HMGB2, CENPE, MKI67, and UBE2C demonstrated co-expression, but other genes displaying similar correlation scores were not commented (such as F3, CYR61, CTGF, etc). To avoid being biased at the analysis stage, the authors should define clearly what the cut-off of correlation score is and why only co-expression of ANLN, HMGB2, CENPE, MKI67, and UBE2C were mentioned.

As suggested, we explain now in the revised manuscript that we focused on gene clusters consisting of at least 3 genes, that had a correlation coefficient greater than or equal to 0.4 with at least one other gene within the clusters. This cutoff is typically defined as representing a "moderate to good" correlation in biological data (Overholser, Sowinski, 2008). To make clear which clusters correlating gene sets passed these criteria, we have also highlighted these genes in Figure S3B. This returned the cluster we had already identified as FOXM1 targets, and as well spotted by the reviewer, a larger cluster which included F3, CYR61, CTGF, SERPINE1, ANKRD1, KRTAP2-3, UGCG, and AMOTL. Our Enrichr analysis did not identify any putative transcription factors linking the genes in this larger cluster. We are still interested to identify the putative transcription regulation mechanism linking these genes in future studies, but this is beyond the scope of the current manuscript. We have described these observations in lines 211-218.

1. In line 215, instead of validating CENPE, UBE2C, HMGB2, ANLN, and MKI67 individually, the authors decided to validate FOXM1 instead, because they believe all the aforementioned genes are targets of FOXM1, therefore, validating FOXM1 alone would suffice. Again, this makes the validation process also biased. CENPE, UBE2C, HMGB2, ANLN, and MKI67 should be validated individually because they might sensitize cells to replication stress via different mechanisms. Besides, if all these genes were identified together because they are FOXM1 target genes, why did the authors not identify FOXM1 itself as a differentially expressed gene from the single cell sequencing? The sequencing only analyzed the S/G2/M cells, expression of FOXM1 should be detected easily.

We agree with the reviewer that the omission of individual FOXM1 target genes in the validation process makes a biased impression. Therefore we ordered siRNAs against CENPE, UBE2C, HMGB2, ANLN, and MKI67. Similar to the other DE genes in the original mini-screen we first knocked down these genes using the siRNA Smartpools (pools of 4 individual siRNAs against each genes). Here, we observed a decrease in γH2AX signal compared to drug-treated cells transfected with all 5 Smartpools compared to drug-treated cells transfected with control siRNA. We next moved on to the deconvolution step of the screen, where we transfected cells with 4 individual siRNA against each gene. Here, we observed inconsistent effects of ANLN, CENPE, and HMGB2 when comparing the individual siRNAs, which all produce efficient knockdown of their target genes. But interestingly, for both MKI67 and UBE2C, each of the 4 individual siRNAs similar decreased yH2AX signal, though it was not as strong as the decrease observed when FOXM1 is knocked out. Understanding the exact mechanism of how MKI67 and UBE2C reduce replication stress is beyond the scope of this paper, but we hypothesize that, as with FOXM1, it is likely linked to their role in promoting progression through the cell cycle. These results are shown in Figures S5, and we mention these remarkable findings in the revised abstract and discuss these in the light of the recent literature in the Discussion section (lines 275-286).

Then, we also addressed the comment about FOXM1 not being changed in the single cell RNA-seq analysis. We could indeed readily detect FOXM1 expression our single-cell RNA sequencing data. The difference in expression did not change significantly in cells sorted according to γH2AX level (Figure 4C). Because FOXM1 is highly regulated post-translationally, we hypothesized that an increase in the (active) protein is correlated to increased replication stress rather than transcript levels. This was indeed the case and we further explain our experiment to test this hypothesis in response to Point #6 (results are displayed in Figure 4D and described in lines 201-209).

1. As pointed out by the author in the Discussion, single cell sequencing is not good at differentiating the causes from the consequences. The author tried to validate many of the differentially expressed genes in γH2Ax low cells. However, the fact that only FOXM1 knockdown passed the validation and deconvolution pointed out that the great majority of the identified genes are not the cause of the sensitivity change to replication stress inducing agents but likely the consequences. Therefore, in Figure S2C and S2D, it would be better that the authors could just name the genes as 'downregulated genes' in Figure S2C and 'upregulated genes' in Figure S2D. Taking into consideration that the expression change in the great majority of these genes are just consequences of sensitivity change to replication stress, defining them as 'potentially sensitizing' genes and 'potentially conferring resistance' genes is rather misleading.

We agree that the way we originally labeled these plots may have been misleading. We have renamed then to "Downregulated in yH2AXlow" and "Upregulated in yH2AXlow", as recommended by the reviewer.

1. To better prove that FOXM1 is the leading cause of the sensitivity to CHK1i+Gemcitabine induced replication stress, can the authors show the FOXM1 expression status in the tolerant cell population identified in Figure 1B (lowest panel)? Alternatively, can they plot FOXM1 expression level in the same tSNE plots shown in Figure 3B to 3D to see whether some of the γH2Ax low populations also show reduced FOXM1 expression?

FOXM1 expression levels were not increased with gH2AXhigh versus gH2AXlow HRASG12V cells in the single cell RNA-sequencing data (Figure 4C in revised manuscript). However, as mentioned in our answer to point #4 we performed an additional experiment, which showed a strong positive correlation between phospho-FOXM1 and γH2AX (as measured by flow cytometry) in S-phase cells (Figure 4D). This indicates that the active form of the FOXM1 indeed increases as yH2AX levels increase, consistent with the observed increase in FOXM1 target genes. These results are described in lines 201-209.

1. Clonogenic survival assay in Figure 4D was not quantified properly in Figure 4E. To rule out the siFOXM1 mediated growth/survival defects and to only focus on the siFOXM1 mediated resistance to CHK1i+Gemcitabine, the survival rate (intensity percent in this case) of CHK1i+Gemcitabine treated condition should be normalized against the survival rate of the Vehicle condition. E.g., the intensity percent of the siSCRAMBLE after treatment should be divided by the intensity percent of the untreated siSCRAMBLE; the intensity percent of the si#1 after treatment should be divided by the intensity percent of the untreated si#1, and so on. If the authors would like to show siFOXM1 induced growth/survival defects, they can still present the left part of the Figure 4E (the Vehicle group).

Originally, we chose to show the absolute IntensityPercent for all groups, without normalizing to the untreated group, because we wanted to also highlight the FOXM1-mediated changes in growth. We agree that normalizing the IntensityPercent of the drug-treated group to the vehicle group better highlights the siFOXM1-mediated resistance. We have therefore re-analyzed the data and presented it this way in Figure 5E (described in lines 293-295). We moved our original Figure 4E to a new supplemental figure (Figure S4B) to still point out the effects of siFOXM1 on cell growth in untreated cells.

Minor:

1. In line 176, the author claimed that 'Interestingly, rare cells treated with CHK1i + gemcitabine are located within the untreated cell cluster (Fig. 3C)'. However, it is not as obvious where these cells are in the plot, especially to people who are new to tSNE plots. It would be appreciated if the authors could label these cells by circling them with red lines and make the point stronger.

Rather than circling these points (we thought this would make the plot too "busy"), we have created an inset that zooms in on the region where we see the untreated cells within the untreated cell cluster. Within the inset, we use arrows to point out the cells we are referring to. This can be seen in our updated Figure 3C.

1. In Figure S2B, it will be ideal to label clearly which genes are upregulated genes and which are downregulate.

On the x-axis of the heatmap, we have drawn lines to separate the downregulated and upregulated genes.

1. In line 50, the word 'multifaced' needs to be corrected to 'multifaceted'.

Thank you for catching this, we have fixed it.

1. It is unclear what 'underly drug resistance' means in line 150.

We have reworded this sentence so that is more clear. It is now written as follows: "we aimed to identify gene-expression programs that mediate the low level of RS in a subset of cells, which could potentially mediate drug resistance". This change is in lines 155.

1. It is advised that the phrase 'cell cycle position' could be changed to 'cell cycle phase' or 'cell cycle stage'.

We purposefully used the phrase "cell cycle position" because we wanted to emphasis gradient-like progress through the cell cycle rather than a discrete distinction from one-phase to the next. We have reworded the text slightly to now say "position within S-phase" (lines 163, 187, 191, 208), since all the cells we are interested in are in S phase, but some are further through S phase than others.

1. In line 185, the word 'in' after 'within' can be removed.

Thank you for catching this, we have fixed it.

1. In line 194, 'Among genes downregulated in γH2AXlow cells, the expression of ANLN, HMGB2, CENPE, MKI67 and UBE2C correlated' is missing an 'are' in front of the word 'correlated'.

Thank you for catching this, we have fixed it.

1. In line 239, Fig.SC3 should be Fig. S3C.

Thank you for catching this, we have fixed it.

1. FOXM1 is known as a crucial gene for G2/M transition. Therefore, FOXM1 knockdown cells are expected to be mostly arrested at the G2/M interface. Therefore, in line 244, it is incorrect to say stronger FOXM1 knockdown induced a 'lower proportion of cells in G2 phase'. In fact, as shown in Figure 4C, cells are accumulating in G2 phase (peaking around 11M on the DAPI axis) and depleted from G1 phase (peaking around 7M).

We have reworded this to say that there is "a higher proportion of cells in S-phase and a less distinct G2 peak" (lines 270-271). The DAPI profiles of the scrambled, siFOXM1 #1, and siFOXM1 #2 conditions all show an S-phase "valley" between a G1 and G2 peak (the valley sits at about 8M-9M). In the siFOXM1 #3 and siFOXM1 #4 conditions, we no longer see this valley, therefore we interpret this as cells still in S-phase. If they had progressed from S-phase into G2 phase, we expect that we would again see this "valley" to the left of a clear G2 peak. In the figure below, we overlayed DNA content histograms of the different FOXM1 targeting siRNAs with the scrambled siRNA to demonstrate this point more clearly.

Reviewer #1 (Significance (Required)):

Advance: The study reported a novel reversible fixation technique which can lead to potentially good citations. However, the findings from the single cell sequencing alone fell short in novelty to reach high impact because FOXM1 has been reported to impact on cellular sensitivity to CHK1 inhibition mediated replication stress (PMC7970065). Moreover, the study did not provide mechanistic explanation to the observed phenotype but only validated the finding from the sequencing, and the gene of focus (FOXM1) was not originally identified from the sequencing, slightly undermining the paper's foundation. To make it a better paper. the authors need to be less biased when it comes to data analysis and interpretation.

Audience: People who are interested in basic research in cell cycle, DNA damage, cancer, chemotherapy would be interested.

My expertise: Cancer, DNA damage, cell cycle

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary:

Replication stress activates ATR and CHEK1 kinases as part of the inter S phase DNA damage response. CHEK1 kinase inhibitors (CHK1i) have been shown to induce an accumulation of unresolved replication stress and widespread DNA damage and cell death caused by replication catastrophe, and are therefore under clinical evaluation. At the same time, CHEK1 inhibition results in the activation of CDK1 and FOXM1 and premature expression of G2/M genes (Saldivar et al., 2018 Science). FOXM1-drivent premature mitosis has been shown to be required for the replication catastrophe and CHK1i sensitivity (Branigan et al., 2021 Cell Rep.). In this study, Segeren and colleagues set out to investigate the mechanisms of replication stress tolerance. They used CHK1i inhibitors in combination with the DNA-damaging chemotherapeutic agent Gemcitabine and oncogenic HRASG12V expression to increase replication stress. The authors utilized an intriguing setup of combined immunofluorescence staining followed by single cell RNA-seq analysis to overcome limitations of bulk cell analyses. In particular, the authors sought to identify genes that are differentially regulated in replication stress-tolerant cells compared to sensitive cells. However, even single cell analyses can be confounded by differences in cell cycle distribution. To mitigate this, the authors selected mid S-phase cells for their analysis. While this may not have completely eliminated minor differences in cell cycle progression, the authors identified FOXM1-regulated G2/M cell cycle genes, among others, that were down-regulated in the tolerant cells. When the authors followed up on the effect of these genes on replication stress tolerance, they identified FOXM1 knockdown as the only robust mediator of replication stress tolerance.

Major comments:

The authors observed that cell cycle distribution could be a major confounding factor in their single cell analysis and attempted to reduce this variation by selecting mid S-phase cells based on the DAPI signal. The authors then chose to compare gH2AXlow and gH2AXhigh subpopulations of RPE-HRASG12V cells because their "DAPI signal was comparable" (line 181-184). However, their data show that these subpopulations also show differences in their DAPI signal distribution, with gH2AXlow cells tending to have lower DAPI signals than gH2AXhigh cells (Supplementary Figure 2A). Thus, the major confounding factor that the authors sought to remove seems to have prevailed and it remains possible that the difference in cell cycle gene expression is merely due to differences in cell cycle progression of the individual cells. Given that DAPI information seem to be readily available for the individual cells, the authors should normalize their analysis to the DAPI signal to remove this potential confounding effect or clearly state this potential limitation.

We agree that indeed it is very challenging to fully disentangle the influence of cell cycle distribution on our analysis. And indeed, the γH2AXlow HRASG12V cells have slightly reduced median DNA content compared to γH2AXmid and γH2AXhigh. However, this was not the case in the RPE control cells, and we still found that FOXM1 target genes were strongly enriched in the γH2AXhigh cells (Fig S2C and Table S4). Therefore, it is highly unlikely that bias in S-phase position distributions does not explain our results. Nevertheless, to be transparent about this write in the Results on lines 192-193 the following: "The other groups all showed similar DAPI intensities, although gH2AXlow RPE-HRASG12V cells showed a slight but statistically significant reduction compared to their gH2AXhigh counterparts (Fig. S2A)".

In our subsequent experiments to assess the relationship between phospho-FOXM1 (representing the transcriptionally active protein) and γH2AX, we observed that though there was a strong correlation between pFOXM1 and γH2AX, there was no correlation between phospho-FOXM1 and DAPI (Figure 4D-E). We therefore would like to point out that although our readout for replication stress inevitably increases as cells progress through DNA replication, heterogeneity in phospho-FOXM1 levels cannot be explained by position in S-phase. These results are described in lines 203-209.

Finally, we do not think it would be statistically appropriate to use the DAPI signal (generated by fluorescence intensity as measured by the flow cytometer) as a normalization factor for our gene expression data.

Minor comments:

The findings of Saldivar et al., 2018 Science and Branigan et al., 2021 Cell Rep. should be mentioned in the introduction.

As recommended, we mentioned both these papers in the introduction. In line 62, we cite the Branigan paper as showing that modulation of cell cycle regulators is a strategy used by cancer cells to resist replication stress. In lines 63-65, we reference them as follows: "The RS response is tightly linked with cell cycle progression, as multiple intra S-phase checkpoint kinases play a role in curtailing proteins involved in the S-G2 transition (Branigan et al., 2021, Saldivar et al., 2018)."

The authors conclude that "cell cycle position can be a major confounding factor when evaluating the transcriptomic response to RS." It should be noted that stochastic differences in the cell cycle distribution of bulk cells are perhaps the best-known confounder in single cell analyses (see, for example, Buettner et al., 2015 Nat. Biotechnol.).

We chose to reference the Buettner paper to justify our decision to select only cycling cells in our scRNA seq approach. Our reference to the paper, and to the fact that cell cycle distribution is a major confounder in single cell analysis, is in lines 138-140.

Supplementary Figure 2A: The median should be added to the violin plots.

As suggested, we have added medians to the violin plots. In addition, we added details on statistical analysis.

The statement "Differential expression analysis revealed 19 genes that were significantly downregulated in gH2AXlow RPE-HRASG12V cells, suggesting that elevated levels of these genes are correlated with sensitivity to RS-inducing drugs" refers to Figure 3E and Table S1. However, Table S1 lists the "key resources" and does not seem to be related to this statement. A table showing log2fold-changes and FDR values should be added and referenced here.

We have generated tables with the fold change values of differentially expressed genes between the yH2AX low and yH2AX high cells. These are found in Table S1 (for HRAS G12V cells) and Table S2 (for Control cells) in the supplementary file of the revised manuscript. The "key resources" has been moved to Table S5.

The statement "Remarkably, Braningan and co-workers observed no effect of full FOXM1 deletion on cell cycle progression" seems somewhat inconsistent with what has been stated and assessed in that study. The authors may want to replace "progression" with "distribution". A reduction in proliferation is commonly observed when FOXM1 levels are reduced.

In addition, the authors may want to consider that their addition of HRASG12V and Gemcitabine may contribute to a more substantial S phase checkpoint response.

We agree with the reviewer that a reduction in proliferation is commonly observed when FOXM1 levels are reduced (Barger et al., 2021, Cheng et al., 2022, Yang et al., 2015, Wu et al., 2010), but in Branigan et al., they see no decrease in proliferation with knockout of FOXM1. They state "There were no apparent differences in the growth rate of the LIN54 and FOXM1 KO versus EV cells over 10 days (Figure 1G)". Though they do not elaborate on why they see this unexpected response, we suspect a permanent full knockout of FOXM1 could cause compensatory adaptation in their cell lines. In our experiments, we perform transient knockdowns, so cells may not have the time to adapt to the loss of FOXM1 and obtain compensatory mechanisms that would allow them to continue cycling as rapidly as control cells treated with non-targeting siRNA.

However, we decided to remove this from the Discussion section, as it seemed to interrupt the discussion about the potential mechanisms underlying protection against DNA damage by FOXM1 depletion.

The statement that "the mechanism by which high FOXM1 activity is a prerequisite to accumulate DNA damage in S-phase during CHK1 inhibition remains to be uncovered" seems to neglect that premature mitosis has been suggested as a mechanistic cause (Branigan et al., 2021 Cell Rep.). It would be helpful if the authors could elaborate on this.

In our discussion, we do already emphasize the described role of FOXM1 in promoting premature mitosis (lines 330-337), but we argue that in our experimental conditions we are observing another - previously undescribed- role for FOXM1 in promoting replication stress during S phase. We previously observed with live cell imaging that CHK1i + gemcitabine does not cause premature mitosis in RPE-HRASG12V cells (published in Segeren et al. Oncogene 2022, Figure 5). Instead, these cells typically showed a cell cycle exit from G2. This makes it highly unlikely that premature mitosis is the reason why these cells would accumulate excessive DNA damage. We realize now that it was an important omission not to elaborate on this and have added this clarification to the Discussion (lines 341-345 in revised manuscript). In addition, we have removed a few lines of less important text (about the lack of direct effect of FOXM1 KO in the Branigan paper; see answer to previous point) to improve clarity and readability.

Reviewer #2 (Significance (Required)):

General assessment: The strength of the study is the intriguing methodology of combined immunofluorescence followed by single cell RNA-seq. The limitations are that this methodology does not seem to fully solve the stated problems. In addition, the study is essentially limited to confirming previous findings.

Advance: The study strengthens current knowledge but provides essentially no advance. The authors confirm existing knowledge with an additional approach. While this is not an advance in itself, it is important to the community.

Audience: I felt that the study would appeal to a basic science audience. In particular, the CHK1i and intra S-phase checkpoint areas, with limited interest beyond that.

My relevant expertise lies in transcriptomics, gene regulation and the cell cycle.

Reference list

Barger, C.J., Chee, L., Albahrani, M., Munoz-Trujillo, C., Boghean, L., Branick, C., Odunsi, K., Drapkin, R., Zou, L. & Karpf, A.R. 2021, "Co-regulation and function of FOXM1/RHNO1 bidirectional genes in cancer", eLife, vol. 10, pp. 10.7554/eLife.55070.

Branigan, T.B., Kozono, D., Schade, A.E., Deraska, P., Rivas, H.G., Sambel, L., Reavis, H.D., Shapiro, G.I., D'Andrea, A.D. & DeCaprio, J.A. 2021, "MMB-FOXM1-driven premature mitosis is required for CHK1 inhibitor sensitivity", Cell reports, vol. 34, no. 9, pp. 108808.

Cheng, Y., Sun, F., Thornton, K., Jing, X., Dong, J., Yun, G., Pisano, M., Zhan, F., Kim, S.H., Katzenellenbogen, J.A., Katzenellenbogen, B.S., Hari, P. & Janz, S. 2022, "FOXM1 regulates glycolysis and energy production in multiple myeloma", Oncogene, vol. 41, no. 32, pp. 3899-3911.

Overholser, B.R. & Sowinski, K.M. 2008, "Biostatistics primer: part 2", Nutrition in clinical practice : official publication of the American Society for Parenteral and Enteral Nutrition, vol. 23, no. 1, pp. 76-84.

Saldivar, J.C., Hamperl, S., Bocek, M.J., Chung, M., Bass, T.E., Cisneros-Soberanis, F., Samejima, K., Xie, L., Paulson, J.R., Earnshaw, W.C., Cortez, D., Meyer, T. & Cimprich, K.A. 2018, "An intrinsic S/G(2) checkpoint enforced by ATR", Science (New York, N.Y.), vol. 361, no. 6404, pp. 806-810.

Segeren, H.A., van Liere, E.A., Riemers, F.M., de Bruin, A. & Westendorp, B. 2022, "Oncogenic RAS sensitizes cells to drug-induced replication stress via transcriptional silencing of P53", Oncogene, vol. 41, no. 19, pp. 2719-2733.

Wu, Q., Liu, C., Tai, M., Liu, D., Lei, L., Wang, R., Tian, M. & Lu, Y. 2010, "Knockdown of FoxM1 by siRNA interference decreases cell proliferation, induces cell cycle arrest and inhibits cell invasion in MHCC-97H cells in vitro", Acta Pharmacologica Sinica, vol. 31, no. 3, pp. 361-366.

Yang, K., Jiang, L., Hu, Y., Yu, J., Chen, H., Yao, Y. & Zhu, X. 2015, "Short hairpin RNA- mediated gene knockdown of FOXM1 inhibits the proliferation and metastasis of human colon cancer cells through reversal of epithelial-to-mesenchymal transformation", Journal of experimental & clinical cancer research : CR, vol. 34, no. 1, pp. 40-1.

We want to thank both reviewers for their thorough and constructive review of our manuscript. Below, we have re-iterated their comments followed by an explanation of how we have revised the manuscript to address this.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

Replication stress activates ATR and CHEK1 kinases as part of the inter S phase DNA damage response. CHEK1 kinase inhibitors (CHK1i) have been shown to induce an accumulation of unresolved replication stress and widespread DNA damage and cell death caused by replication catastrophe, and are therefore under clinical evaluation. At the same time, CHEK1 inhibition results in the activation of CDK1 and FOXM1 and premature expression of G2/M genes (Saldivar et al., 2018 Science). FOXM1-drivent premature mitosis has been shown to be required for the replication catastrophe and CHK1i sensitivity (Branigan et al., 2021 Cell Rep.). In this study, Segeren and colleagues set out to investigate the mechanisms of replication stress tolerance. They used CHK1i inhibitors in combination with the DNA-damaging chemotherapeutic agent Gemcitabine and oncogenic HRASG12V expression to increase replication stress. The authors utilized an intriguing setup of combined immunofluorescence staining followed by single cell RNA-seq analysis to overcome limitations of bulk cell analyses. In particular, the authors sought to identify genes that are differentially regulated in replication replication stress-tolerant cells compared to sensitive cells. However, even single cell analyses can be confounded by differences in cell cycle distribution. To mitigate this, the authors selected mid S-phase cells for their analysis. While this may not have completely eliminated minor differences in cell cycle progression, the authors identified FOXM1-regulated G2/M cell cycle genes, among others, that were down-regulated in the tolerant cells. When the authors followed up on the effect of these genes on replication stress tolerance, they identified FOXM1 knockdown as the only robust mediator of replication stress tolerance.

Major comments:

The authors observed that cell cycle distribution could be a major confounding factor in their single cell analysis and attempted to reduce this variation by selecting mid S-phase cells based on the DAPI signal. The authors then chose to compare gH2AXlow and gH2AXhigh subpopulations of RPE-HRASG12V cells because their "DAPI signal was comparable" (line 181-184). However, their data show that these subpopulations also show differences in their DAPI signal distribution, with gH2AXlow cells tending to have lower DAPI signals than gH2AXhigh cells (Supplementary Figure 2A). Thus, the major confounding factor that the authors sought to remove seems to have prevailed and it remains possible that the difference in cell cycle gene expression is merely due to differences in cell cycle progression of the individual cells. Given that DAPI information seem to be readily available for the individual cells, the authors should normalize their analysis to the DAPI signal to remove this potential confounding effect or clearly state this potential limitation.

Minor comments:

The findings of Saldivar et al., 2018 Science and Branigan et al., 2021 Cell Rep. should be mentioned in the introduction.

The authors conclude that "cell cycle position can be a major confounding factor when evaluating the transcriptomic response to RS." It should be noted that stochastic differences in the cell cycle distribution of bulk cells are perhaps the best-known confounder in single cell analyses (see, for example, Buettner et al., 2015 Nat. Biotechnol.).

Supplementary Figure 2A: The median should be added to the violin plots.

The statement "Differential expression analysis revealed 19 genes that were significantly downregulated in gH2AXlow RPE-HRASG12V cells, suggesting that elevated levels of these genes are correlated with sensitivity to RS-inducing drugs" refers to Figure 3E and Table S1. However, Table S1 lists the "key resources" and does not seem to be related to this statement. A table showing log2fold-changes and FDR values should be added and referenced here.

The statement "Remarkably, Braningan and co-workers observed no effect of full FOXM1 deletion on cell cycle progression" seems somewhat inconsistent with what has been stated and assessed in that study. The authors may want to replace "progression" with "distribution". A reduction in proliferation is commonly observed when FOXM1 levels are reduced. In addition, the authors may want to consider that their addition of HRASG12V and Gemcitabine may contribute to a more substantial S phase checkpoint response.

The statement that "the mechanism by which high FOXM1 activity is a prerequisite to accumulate DNA damage in S-phase during CHK1 inhibition remains to be uncovered" seems to neglect that premature mitosis has been suggested as a mechanistic cause (Branigan et al., 2021 Cell Rep.). It would be helpful if the authors could elaborate on this.

Significance

General assessment: The strength of the study is the intriguing methodology of combined immunofluorescence followed by single cell RNA-seq. The limitations are that this methodology does not seem to fully solve the stated problems. In addition, the study is essentially limited to confirming previous findings.

Advance: The study strengthens current knowledge but provides essentially no advance. The authors confirm existing knowledge with an additional approach. While this is not an advance in itself, it is important to the community.

Audience: I felt that the study would appeal to a basic science audience. In particular, the CHK1i and intra S-phase checkpoint areas, with limited interest beyond that.

My relevant expertise lies in transcriptomics, gene regulation and the cell cycle.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

This manuscript presented by Segeren et al. applied an interesting HRASG12V inducible cell model to study the mechanism of cellular resistance to replication stress inducing agents. They also employed a novel reversible fixation technique which allows them to FAC sort cells according to their replication stress levels before applying single cell sequencing analysis to the same cell populations. By comparing cells with low levels of replication stress to cells with high levels of replication stress, they found that reduction in gene expression of FOXM1 target genes potentially protects cells against replication stress induced by CHK1i plus gemcitabine combination.

Overall, this is a very interesting study. However, the following points should be addressed prior to publication:

Major:

1. Figure 3E and 3F showed two lists of differentially expressed genes in γH2Ax low cells. However, instead of arbitrarily extracting the FOXM1 target genes and TP53 targeted genes, it would be appreciated if the author could perform an unbiased and unsupervised gene set enrichment analysis such as Enrichr.
2. At the experiment design stage, the authors also included HRASG12V status as a test condition because they previously found that HRASG12V mutation induces basal level replication stress and they would like to include this condition to study the adaptation to replication stress (line 110). However, the difference in HRASG12V negative and HRASG12V positive cells was not followed up in the later part of the paper. Can they show lists of differentially expressed genes identified under HRASG12V negative conditions as well (in the same format of Figure 3E and 3F) and comment on the differences as well?
3. In line 194 and in Figure S2B, the authors claimed that ANLN, HMGB2, CENPE, MKI67, and UBE2C demonstrated co-expression, but other genes displaying similar correlation scores were not commented (such as F3, CYR61, CTGF, etc). To avoid being biased at the analysis stage, the authors should define clearly what the cut-off of correlation score is and why only co-expression of ANLN, HMGB2, CENPE, MKI67, and UBE2C were mentioned.
4. In line 215, instead of validating CENPE, UBE2C, HMGB2, ANLN, and MKI67 individually, the authors decided to validate FOXM1 instead, because they believe all the aforementioned genes are targets of FOXM1, therefore, validating FOXM1 alone would suffice. Again, this makes the validation process also biased. CENPE, UBE2C, HMGB2, ANLN, and MKI67 should be validated individually because they might sensitize cells to replication stress via different mechanisms. Besides, if all these genes were identified together because they are FOXM1 target genes, why did the authors not identify FOXM1 itself as a differentially expressed gene from the single cell sequencing? The sequencing only analyzed the S/G2/M cells, expression of FOXM1 should be detected easily.
5. As pointed out by the author in the Discussion, single cell sequencing is not good at differentiating the causes from the consequences. The author tried to validate many of the differentially expressed genes in γH2Ax low cells. However, the fact that only FOXM1 knockdown passed the validation and deconvolution pointed out that the great majority of the identified genes are not the cause of the sensitivity change to replication stress inducing agents but likely the consequences. Therefore, in Figure S2C and S2D, it would be better that the authors could just name the genes as 'downregulated genes' in Figure S2C and 'upregulated genes' in Figure S2D. Taking into consideration that the expression change in the great majority of these genes are just consequences of sensitivity change to replication stress, defining them as 'potentially sensitizing' genes and 'potentially conferring resistance' genes is rather misleading.
6. To better prove that FOXM1 is the leading cause of the sensitivity to CHK1i+Gemcitabine induced replication stress, can the authors show the FOXM1 expression status in the tolerant cell population identified in Figure 1B (lowest panel)? Alternatively, can they plot FOXM1 expression level in the same tSNE plots shown in Figure 3B to 3D to see whether some of the γH2Ax low populations also show reduced FOXM1 expression?
7. clonogenic survival assay in Figure 4D was not quantified properly in Figure 4E. To rule out the siFOXM1 mediated growth/survival defects and to only focus on the siFOXM1 mediated resistance to CHK1i+Gemcitabine, the survival rate (intensity percent in this case) of CHK1i+Gemcitabine treated condition should be normalized against the survival rate of the Vehicle condition. E.g., the intensity percent of the siSCRAMBLE after treatment should be divided by the intensity percent of the untreated siSCRAMBLE; the intensity percent of the si#1 after treatment should be divided by the intensity percent of the untreated si#1, and so on. If the authors would like to show siFOXM1 induced growth/survival defects, they can still present the left part of the Figure 4E (the Vehicle group).

Minor:

1. In line 176, the author claimed that 'Interestingly, rare cells treated with CHK1i + gemcitabine are located within the untreated cell cluster (Fig. 3C)'. However, it is not as obvious where these cells are in the plot, especially to people who are new to tSNE plots. It would be appreciated if the authors could label these cells by circling them with red lines and make the point stronger.
2. In Figure S2B, it will be ideal to label clearly which genes are upregulated genes and which are downregulate.
3. In line 50, the word 'multifaced' needs to be corrected to 'multifaceted'.
4. It is unclear what 'underly drug resistance' means in line 150.
5. It is advised that the phrase 'cell cycle position' could be changed to 'cell cycle phase' or 'cell cycle stage'.
6. In line 185, the word 'in' after 'within' can be removed.
7. In line 194, 'Among genes downregulated in γH2AXlow cells, the expression of ANLN, HMGB2, CENPE, MKI67 and UBE2C correlated' is missing an 'are' in front of the word 'correlated'.
8. In line 239, Fig.SC3 should be Fig. S3C.
9. FOXM1 is known as a crucial gene for G2/M transition. Therefore, FOXM1 knockdown cells are expected to be mostly arrested at the G2/M interface. Therefore, in line 244, it is incorrect to say stronger FOXM1 knockdown induced a 'lower proportion of cells in G2 phase'. In fact, as shown in Figure 4C, cells are accumulating in G2 phase (peaking around 11M on the DAPI axis) and depleted from G1 phase (peaking around 7M).

Significance

Advance:

The study reported a novel reversible fixation technique which can lead to potentially good citations. However, the findings from the single cell sequencing alone fell short in novelty to reach high impact because FOXM1 has been reported to impact on cellular sensitivity to CHK1 inhibition mediated replication stress (PMC7970065). Moreover, the study did not provide mechanistic explanation to the observed phenotype but only validated the finding from the sequencing, and the gene of focus (FOXM1) was not originally identified from the sequencing, slightly undermining the paper's foundation. To make it a better paper. the authors need to be less biased when it comes to data analysis and interpretation.

Audience:

People who are interested in basic research in cell cycle, DNA damage, cancer, chemotherapy would be interested.

My expertise:

Cancer, DNA damage, cell cycle

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2024-02545

Corresponding author(s): Woo Jae, Kim

1. General Statements

We sincerely appreciate the positive and constructive feedback provided by all three reviewers. Their insightful comments have been invaluable in guiding our revisions. In response, we have made every effort to address their suggestions through additional experiments and by restructuring our manuscript to improve clarity and coherence.

In this revision, we have streamlined the presentation of our data to enhance the narrative flow, ensuring that it is more accessible to a general readership. We believe that these changes not only strengthen our manuscript but also align with the reviewers' recommendations for improvement.

We are hopeful that the revisions we have implemented meet the expectations of the reviewers and contribute to a clearer understanding of our findings. Thank you once again for your thoughtful critiques, which have greatly aided us in refining our work.

---

2. Point-by-point description of the revisions

Reviewer #1

General comment: This manuscript by Song et al. investigates the molecular mechanisms underlying changes in mating duration in Drosophila induced by previous experience. As they have shown previously, they find that male flies reared in isolation have shorter mating duration than those reared in groups, and also that male flies with previous mating experience have shorter mating duration than sexually naïve males. They have conducted a myriad of experiments to demonstrate that the neuropeptide SIFa is required for these changes in mating duration. They have further provided evidence that SIFa-expressing neurons undergo changes in synaptic connectivity and neuronal firing as a result of previous mating experience. Finally, they argue that SIFa neurons form reciprocal connections with sNPF-expressing neurons, and that communication within the SIFa-sNPF circuit is required for experience-dependent changes in mating duration. These results are used to assert that SIFa neurons track the internal state of the flies to modulate behavioral choice.

   __Answer:__ We appreciate the reviewer's thoughtful comments and commendations regarding our manuscript. The recognition of our investigation into the molecular mechanisms influencing mating duration in *Drosophila* is greatly valued. In particular, we are grateful for the reviewer's positive remarks about our comprehensive experimental approach to demonstrate the role of the neuropeptide SIFa in these changes. The evidence we provided indicating that SIFa-expressing neurons undergo alterations in synaptic connectivity and neuronal firing due to previous social experiences is crucial for elucidating the underlying neural circuitry involved in experience-dependent behaviors. Finally, we are thankful for the recognition of our assertion that SIFa neurons form reciprocal connections with sNPF-expressing neurons, emphasizing the importance of this circuit in modulating behavioral choices based on internal states. To provide stronger evidence for the interactions between SIFa and sNPF, we conducted detailed GCaMP experiments, which revealed intriguing neural connections between these two neuropeptides. We have included this new data in our main figure. We believe these insights contribute significantly to the existing literature on neuropeptidergic signaling and its implications for understanding complex behaviors in *Drosophila*. We look forward to addressing any further comments and enhancing our manuscript based on your invaluable feedback. Thank you once again for your constructive critique and support.

Major concerns:

Comment 1. The authors are to be commended for the sheer quantity of data they have generated, but I was often overwhelmed by the figures, which try to pack too much into the space provided. As a result, it is often unclear what components belong to each panel. Providing more space between each panel would really help.

   __Answer:__ We sincerely appreciate the reviewer’s commendation regarding the extensive data we have generated in our study. It is gratifying to know that our efforts to provide a comprehensive analysis of the molecular mechanisms underlying changes in mating duration have been recognized. We understand the concern regarding the density of information presented in our figures. We aimed to convey a wealth of data to support our findings, but we acknowledge that this may have led to some confusion regarding the organization and clarity of the panels. We are grateful for your constructive feedback on this matter. In response, we have significantly reduced the density of the main figures and decreased the size of the graphs to improve clarity. We have also increased the spacing between panels to ensure that each component is more easily distinguishable. Further details will be provided in our responses to each comment below.

• *

Comment 2. This is a rare instance where I would recommend paring down the paper to focus on the more novel, clear and relevant results. For example, all of Figure 2 shows the projection pattern of SIFa+ neuron dendrites and axons, which have been reported by multiple previous papers. Figure 7G and J show trans-tango data and SIFaR-GAL4 expression patterns, which were previously reported by Dreyer et al., 2019. These parts could be removed to supplemental figures. Figure 5 details experiments that knock down expression of different neurotransmitter receptors within the SIFa-expressing cells. The results here are less definitive than the SIFa knockdown results, and the SCope data supporting the idea that these receptors are expressed in SIFa-expressing neurons is equivocal. I would recommend removing these data (perhaps they could serve as the basis for another manuscript) or focusing solely on the CCHa1R results, which is the only manipulation that affects both LMD and SMD.

   __Answer:__ We sincerely appreciate the reviewer’s positive feedback regarding the extensive data generated in our study. We also fully agree with the reviewer that the sheer volume of our data made it challenging to support our hypothesis that SIFa neurons serve as a hub for integrating multiple neuropeptide inputs and orchestrating various behaviors related to energy balance, as highlighted in our new Figure 5N.

   In response to the reviewer's suggestions, we have streamlined our manuscript by removing excessive and redundant data to enhance clarity and simplicity. First, we have moved Figure 2 to the supplementary materials as the reviewer noted that the branching patterns of SIFa neurons are well-documented in previous literature. Second, we relocated the trans-tango data from Figure 7G to Figure S7, since this information is also well-established. We retained this data in the supplementary section to illustrate the connection of SIFa to our recent findings regarding SIFaR24F06 neuron connections. Additionally, we have completely removed the neuropeptide receptor input screening data previously included in Figure 5, as well as Figure S8, which presented fly SCope tSNE data. As suggested by the reviewer, we plan to utilize these data for a future paper focused on investigating the underlying mechanisms of SIFa inputs that modulate SIFa activity. Thanks to the reviewer’s constructive suggestions, we believe our manuscript is now more convincing and clearer for readers.

Comment 3. Finally, I would like the authors to spend more time explaining how they think the results tie together. For example, how do the authors think the changes in branching and activity in SIFa-expressing neurons tie to the change in mating duration provoked by previous experience? It would benefit the manuscript to simplify and clarify the message about what the authors think is happening at the mechanistic level. The various schematics (eg. Fig 7N) describe the results but the different parts feel like separate findings rather than a single narrative. (MECHANISMS diagram and explanation)

   __Answer:__ We appreciate the reviewer’s constructive comments, which have significantly improved our manuscript and conclusions for our readers. As the reviewer will see, we have made substantial revisions in line with the suggestions provided. We dedicated additional time to clarify the electrical activities and synaptic plasticity of SIFa neurons in relation to internal states that orchestrate various behaviors. We have summarized our hypothesis regarding the mechanistic role of SIFa neurons in Figure 5N. In brief, we propose that SIFa neurons function as a hub that receives diverse neuropeptidergic signals, which subsequently alters their electrical activity and synaptic branching. This, in turn, leads to different internal states. The internal states of SIFa neurons can then be interpreted by SIFaR-expressing cells, which help orchestrate various behaviors and physiological responses. We aim to address these aspects further in another manuscript that has been co-submitted alongside this one [1].

Comment 4. Most of the experiments lack traditional controls. For example, in experiments in Fig 1C-K, one would typically include genetic controls that contain either the GAL4 or UAS elements alone. The authors should explain their decision to omit these control experiments and provide an argument for why they are not necessary to correctly interpret the data. In this vein, the authors have stated in the methods that stocks were outcrossed at least 3x to Canton-S background, but 3 outcrosses is insufficient to fully control for genetic background.

   __Answer:__ We sincerely thank the reviewer for insightful comments regarding the absence of traditional genetic controls in our study of LMD and SMD behaviors. We acknowledge the importance of such controls and wish to clarify our rationale for not including them in the current investigation. The primary reason for not incorporating all genetic control lines is that we have previously assessed the LMD and SMD behaviors of GAL4/+ and UAS/+ strains in our earlier studies. Our past experiences have consistently shown that 100% of the genetic control flies for both GAL4 and UAS exhibit normal LMD and SMD behaviors. Given these findings, we deemed the inclusion of additional genetic controls to be non-essential for the present study, particularly in the context of extensive screening efforts. We understand the value of providing a clear rationale for our methodology choices. To this end, we have added a detailed explanation in the "MATERIALS AND METHODS" section and the figure legends of Figure 1. This clarification aims to assist readers in understanding our decision to omit traditional controls, as outlined below.

"Mating Duration Assays for Successful Copulation

The mating duration assay in this study has been reported[33,73,93]. To enhance the efficiency of the mating duration assay, we utilized the Df (1)Exel6234 (DF here after) genetic modified fly line in this study, which harbors a deletion of a specific genomic region that includes the sex peptide receptor (SPR)[94,95]. Previous studies have demonstrated that virgin females of this line exhibit increased receptivity to males[95]. We conducted a comparative analysis between the virgin females of this line and the CS virgin females and found that both groups induced SMD. Consequently, we have elected to employ virgin females from this modified line in all subsequent studies. For naïve males, 40 males from the same strain were placed into a vial with food for 5 days. For single reared males, males of the same strain were collected individually and placed into vials with food for 5 days. For experienced males, 40 males from the same strain were placed into a vial with food for 4 days then 80 DF virgin females were introduced into vials for last 1 day before assay. 40 DF virgin females were collected from bottles and placed into a vial for 5 days. These females provide both sexually experienced partners and mating partners for mating duration assays. At the fifth day after eclosion, males of the appropriate strain and DF virgin females were mildly anaesthetized by CO2. After placing a single female in to the mating chamber, we inserted a transparent film then placed a single male to the other side of the film in each chamber. After allowing for 1 h of recovery in the mating chamber in 25℃ incubators, we removed the transparent film and recorded the mating activities. Only those males that succeeded to mate within 1 h were included for analyses. Initiation and completion of copulation were recorded with an accuracy of 10 sec, and total mating duration was calculated for each couple. All assays were performed from noon to 4pm. Genetic controls with GAL4/+ or UAS/+ lines were omitted from supplementary figures, as prior data confirm their consistent exhibition of normal LMD and SMD behaviors [33,73,93,96,97]. Hence, genetic controls for LMD and SMD behaviors were incorporated exclusively when assessing novel fly strains that had not previously been examined. In essence, internal controls were predominantly employed in the experiments, as LMD and SMD behaviors exhibit enhanced statistical significance when internally controlled. Within the LMD assay, both group and single conditions function reciprocally as internal controls. A significant distinction between the naïve and single conditions implies that the experimental manipulation does not affect LMD. Conversely, the lack of a significant discrepancy suggests that the manipulation does influence LMD. In the context of SMD experiments, the naïve condition (equivalent to the group condition in the LMD assay) and sexually experienced males act as mutual internal controls for one another. A statistically significant divergence between naïve and experienced males indicates that the experimental procedure does not alter SMD. Conversely, the absence of a statistically significant difference suggests that the manipulation does impact SMD. Hence, we incorporated supplementary genetic control experiments solely if they deemed indispensable for testing. All assays were performed from noon to 4 PM. We conducted blinded studies for every test[98,99] .

   While we have previously addressed this type of reviewer feedback in our published manuscript [2–7], we appreciate the reviewer’s suggestion to include traditional genetic control experiments. In response, we conducted all feasible combinations of genetic control experiments for LMD/SMD during the revision period. The results are presented in the supplementary figures and are described in the main text.

   We appreciate the reviewer's inquiry regarding the genetic background of our experimental lines. In response to the comments, we would like to clarify the following. All of our GAL4, UAS, or RNAi lines, which were utilized as the virgin female stock for outcrosses, have been backcrossed to the Canton-S (CS) genetic background for over ten generations. The majority of these lines, particularly those employed in LMD assays, have been maintained in a CS backcrossed status for several years, ensuring a consistent genetic background across multiple generations. Our experience has indicated that the genetic background, particularly that of the X chromosome inherited from the female parent, plays a pivotal role in the expression of certain behavioral traits. Therefore, we have consistently employed these fully outcrossed females as virgins for conducting experiments related to LMD and SMD behaviors. It is noteworthy that, in contrast to the significance of genetic background for LMD behaviors, we have previously established in our work [6] that the genetic background does not significantly influence SMD behaviors. This distinction is important for the interpretation of our findings. To provide a comprehensive understanding of our experimental design, we have detailed the genetic background considerations in the __"Materials and Methods"__ section, specifically in the subsection __"Fly Stocks and Husbandry"__ as outlined below.

"To reduce the variation from genetic background, all flies were backcrossed for at least 3 generations to CS strain. For the generation of outcrosses, all GAL4, UAS, and RNAi lines employed as the virgin female stock were backcrossed to the CS genetic background for a minimum of ten generations. Notably, the majority of these lines, which were utilized for LMD assays, have been maintained in a CS backcrossed state for long-term generations subsequent to the initial outcrossing process, exceeding ten backcrosses. Based on our experimental observations, the genetic background of primary significance is that of the X chromosome inherited from the female parent. Consequently, we consistently utilized these fully outcrossed females as virgins for the execution of experiments pertaining to LMD and SMD behaviors. Contrary to the influence on LMD behaviors, we have previously demonstrated that the genetic background exerts negligible influence on SMD behaviors, as reported in our prior publication [6]. All mutants and transgenic lines used here have been described previously."

Comment 5. Throughout the manuscript, the authors appear to use a single control condition (sexually naïve flies raised in groups) to compare to both males raised singly and males with previous sexual experience. These control conditions are duplicated in two separate graphs, one for long mating duration and one for short mating duration, but they are given different names (group vs naïve) depending on the graph. If these are actually the same flies, then this should be made clear, and they should be given a consistent name across the different "experiments".

   __Answer:__ We are grateful to the reviewer for highlighting the potential for confusion among readers regarding the visualization methods used in our figures. In response to this valuable feedback, we have now included a more detailed explanation of the graph visualization techniques in the legends of Figure 1, as detailed below. This additional information should enhance the clarity and understanding of the figure for all readers.

In the mating duration (MD) assays, light grey data points denote males that were group-reared (or sexually naïve), whereas blue (or pink) data points signify males that were singly reared (or sexually experienced). The dot plots represent the MD of each male fly. The mean value and standard error are labeled within the dot plot (black lines). Asterisks represent significant differences, as revealed by the unpaired Student’s t test, and ns represents non-significant differences M.D represent mating duration. DBMs represent the 'difference between means' for the evaluation of estimation statistics (See MATERIALS AND METHODS). Asterisks represent significant differences, as revealed by the Student’s t test (* p

Comment 6. The authors use SCope data to provide evidence for co-expression of SIFa and other neurotransmitters or neuropeptide receptors. The graphs they show are hard to read and it is not clear to what extent the gene expression is actually overlapping. It would be more definitive to show graphs that indicate which percentage of SIFa-expressing cells co-express other neurotransmitter components, and what the actual level of expression of the genes is. The authors should also provide more information on how they identified the SIFa+ cells in the fly atlas dataset. These are important pieces of information to be able to interpret the effects of manipulation of these other neurotransmitter systems within SIFa-expressing cells on mating duration.

__ Answer: We appreciate the reviewer for pointing out the potential for confusion among readers regarding the visualization methods used in our figures, particularly concerning the tSNE plots of scRNA-seq data. As mentioned in our previous response, we have removed most of the tSNE plots related to co-expression data with SIFa and NPRs, which we believe will reduce any confusion for readers interpreting these plots. However, we have retained a few tSNE plots, specifically Figures 2N-O, to confirm the potential co-expression of the ple and Vglut genes in SIFa cells. We understand the reviewer’s concerns about the clarity of the presented data and the necessity for more detailed information regarding the extent of co-expression and the identification of SIFa-expressing cells. To address these concerns, we have included a comprehensive description of our methods in the __MATERIALS AND METHODS section below.

"Single-nucleus RNA-sequencing analyses

The snRNAseq dataset analyzed in this paper is published in [112] and available at the Nextflow pipelines (VSN, https://github.com/vib-singlecell-nf), the availability of raw and processed datasets for users to explore, and the development of a crowd-annotation platform with voting, comments, and references through SCope (https://flycellatlas.org/scope), linked to an online analysis platform in ASAP (https://asap.epfl.ch/fca). For the generation of the tSNE plots, we utilized the Fly SCope website (https://scope.aertslab.org/#/FlyCellAtlas/*/welcome). Within the session interface, we selected the appropriate tissues and configured the parameters as follows: 'Log transform' enabled, 'CPM normalize' enabled, 'Expression-based plotting' enabled, 'Show labels' enabled, 'Dissociate viewers' enabled, and both 'Point size' and 'Point alpha level' set to maximum. For all tissues, we referred to the individual tissue sessions within the '10X Cross-tissue' RNAseq dataset. Each tSNE visualization depicts the coexpression patterns of genes, with each color corresponding to the genes listed on the left, right, and bottom of the plot. The tissue name, as referenced on the Fly SCope website is indicated in the upper left corner of the tSNE plot. Dashed lines denote the significant overlap of cell populations annotated by the respective genes. Coexpression between genes or annotated tissues is visually represented by differentially colored cell populations. For instance, yellow cells indicate the coexpression of a gene (or annotated tissue) with red color and another gene (or annotated tissue) with green color. Cyan cells signify coexpression between green and blue, purple cells for red and blue, and white cells for the coexpression of all three colors (red, green, and blue). Consistency in the tSNE plot visualization is preserved across all figures.

Single-cell RNA sequencing (scRNA-seq) data from the Drosophila melanogaster were obtained from the Fly Cell Atlas website (https://doi.org/10.1126/science.abk2432). Oenocytes gene expression analysis employed UMI (Unique Molecular Identifier) data extracted from the 10x VSN oenocyte (Stringent) loom and h5ad file, encompassing a total of 506,660 cells. The Seurat (v4.2.2) package (https://doi.org/10.1016/j.cell.2021.04.048) was utilized for data analysis. Violin plots were generated using the “Vlnplot” function, the cell types are split by FCA.

   We have also included detailed descriptions in the figure legends for the initial tSNE plot presented below to help readers clearly understand the significance of this visualization.

"Each tSNE visualization depicts the coexpression patterns of genes, with each color corresponding to the genes listed on the left, right, and/or bottom of the plot. The tissue name, as referenced on the Fly SCope website is indicated in the upper left corner of the tSNE plot. Consistency in the tSNE plot visualization is preserved across all figures."

Comment 7. I would like to see more information on how the thresholding and normalization was done for immunohistochemistry experiments. Was thresholding applied equally across all datasets? Furthermore, "overlap" of Denmark and Syt-eGFP is taken as evidence for synaptic connectivity, but the latter requires more than just overlap in the location of the axon terminal and dendrite regions of the neuron.

__ Answer: Thank you for your continued engagement with our manuscript and for highlighting the need for further clarification on our methods. Your attention to the details of our immunohistochemistry experiments is commendable, and we agree that providing a clear explanation of our thresholding and normalization procedures is essential for the transparency and reproducibility of our results. We concur that the intensity of these signals is indeed correlated with the area measurements, which is a critical factor to consider. In response to the reviewer's valuable suggestion, we have revised our approach and now present our data based on intensity measurements. Additionally, we have updated the labeling of our Y-axis to "Norm. GFP Int.", which stands for "normalized GFP intensity". This change ensures clarity and consistency in the presentation of our data. We primarily adhered to the established methods outlined by Kayser et al. [8]. To address your first point, we have now included a more detailed description of our thresholding and normalization procedures in the __MATERIALS AND METHODS section as below.

"Quantitative analysis of fluorescence intensity

To ascertain calcium levels and synaptic intensity from microscopic images, we dissected and imaged five-day-old flies of various social conditions and genotypes under uniform conditions. The GFP signal in the brains and VNCs was amplified through immunostaining with chicken anti-GFP primary antibody. Image analysis was conducted using ImageJ software. For the quantification of fluorescence intensities, an investigator, blinded to the fly's genotype, thresholded the sum of all pixel intensities within a sub-stack to optimize the signal-to-noise ratio, following established methods [93]. The total fluorescent area or region of interest (ROI) was then quantified using ImageJ, as previously reported. For CaLexA or TRIC signal quantification, we adhered to protocols detailed by Kayser et al. [94], which involve measuring the ROI's GFP-labeled area by summing pixel values across the image stack. This method assumes that changes in the GFP-labeled area and intensity are indicative of alterations in the CaLexA and TRIC signal, reflecting synaptic activity. ROI intensities were background-corrected by measuring and subtracting the fluorescent intensity from a non-specific adjacent area, as per Kayser et al. [94]. For normalization, nc82 fluorescence is utilized for CaLexA, while RFP signal is employed for TRIC experiments, as the RFP signal from the TRIC reporter is independent of calcium signaling [76]. For the analysis of GRASP or tGRASP signals, a sub-stack encompassing all synaptic puncta was thresholded by a genotype-blinded investigator to achieve the optimal signal-to-noise ratio. The fluorescence area or ROI for each region was quantified using ImageJ, employing a similar approach to that used for CaLexA or TRIC quantification [93]. 'Norm. GFP Int.' refers to the normalized GFP intensity relative to the RFP signal."

Comment 8. None of the RNAi experiments have been validated to demonstrate effective knockdown. In many cases, this would be difficult to do because of a lack of an antibody to quantify in a cell-specific manner; however, this fact should be acknowledged, especially in cases where there was found to be a lack of phenotype, which could result from lack of knockdown. The authors could also look for evidence in the literature of cases where RNAi lines they have used have been previously validated. For SIFa, knockdown can be easily confirmed with the SIFa antibody the authors have used elsewhere in the manuscript.

__ Answer:__ We appreciate the reviewer’s constructive and critical comments regarding the validation of our RNAi experiments through effective knockdown. We understand the reviewer’s concerns about achieving effective knockdown with RNAi; however, we have demonstrated in our unpublished preprint that the neuronal knockdown using independent SIFa-RNAi lines aligns with the SIFa mutant phenotype, which is consistent with our current findings on SIFa knockdown (Wong 2019). In most cases involving RNAi experiments, we have utilized independent RNAi strains to confirm consistent phenotypes and have compared these results with those from mutant phenotypes [1,9]. Therefore, we are confident that our observed SIFa phenotype results from effective RNAi knockdown. Nevertheless, we respect the reviewer’s comments and have conducted additional SIFa knockdown experiments using various GAL4 drivers, followed by immunostaining with SIFa antibodies. As shown in Figure S1B, both neuronal GAL4 drivers and SIFa-GAL4 effectively reduced SIFa immunoreactivity. We believe this indicates that our SIFa knockdown efficiently phenocopies the SIFa mutant phenotype. We also described this result in manuscript as below:

"Using the GAL4SIFa.PT driver and the elavc155 driver, we observed a significant decrease in SIFa immunoreactivity following SIFa-RNAi treatment, thereby confirming the effective knockdown of SIFa in these cells. In contrast, when SIFa-RNAi was expressed under the control of the repo-GAL4 driver, no significant change in SIFa immunoreactivity was detected (Fig. S1B). This control experiment highlights the specificity of the SIFa-RNAi effect and supports the conclusion that the behavioral changes observed in SMD and LMD are likely attributable to the targeted reduction of SIFa in the intended neuronal populations."

Minor comments:

Comment 1. There are quite a lot of citations to preprints, including preprints of the manuscripts under review. It seems inappropriate to cite a preprint of the manuscript you are submitting because it gives a false sense of strengthening the assertions being made in the manuscript.

   __Answer:__ We agree with the reviewer and have omitted all preprints that are currently under review, except for those that are deemed necessary, such as the Zhang et al. 2024 preprint, which is being submitted alongside this manuscript.

Comment 2. It seems that labels are incorrect on a number of the immunohistochemistry figures. For example, in Fig 2N, it labels dendrites as green, but this is sytEGFP, which is the presynaptic terminal.

__ Answer:__ We thoroughly reviewed and corrected the errors in the labels.

Comment ____3. Fig 4N shows grasp between SIFa-LexA and sNPF-R-GAL4, but the authors have argued that these two components should both be expressed in SIFa-expressing cells. This would make grasp signal misleading, because it would appear in the SIFa-expressing cells even without synaptic contacts due to both split GFP molecules being expressed in these cells.

   __Answer:__ We appreciate the reviewer’s critical comments regarding the interpretation of our GRASP experiments. As the reviewer noted, we acknowledge that the GRASP results also indicate synaptic contacts between SIFa cells. We have elaborated on these results in the following sections.

"This indicates that the synapses between SIFa cells expressing sNPF-R become stronger (S5K to S5M Fig)."

   However, we understand that readers may find the interpretation of this GRASP data confusing, so we have included additional explanations below to clarify.

This indicates that the synapses between SIFa cells expressing sNPF-R become stronger (S5K to S5M Fig) since we have found that SIFa cells express sNPF-R (Fig 3M, S5E and S5G)

Comment 4. For quantifying TRIC and CaLexA experiments (eg. Figure 6A-E), intensity of signal should be measured in addition to the area covered by the signal.

__ Answer:__ We concur with the reviewer. Since all of our analyses indicated that the area covered by the signal correlates with the signal intensity, we opted to use normalized intensity rather than area coverage.

Conclusive Comments: This study will be most relevant to researchers interested in understanding neuronal control of behavior. It has provided novel information about the mechanisms underlying mating duration in flies, which is used to delineate how internal state influences behavioral outcomes. This represents a conceptual advance, particularly in identifying a cell type and molecule that influences mating duration decisions. The strength of the manuscript is the number of different assays used to investigate the central question from a number of angles. The limitation is that there is a lack of a big picture tying the different components of the manuscript together. Too much data is presented without providing a framework to understand how the data points fit together.

• Answer: We sincerely appreciate the reviewer’s positive feedback regarding our study and the recognition of its relevance to researchers interested in understanding the neuronal control of behavior. We are grateful for the acknowledgment of our novel insights into the mechanisms underlying mating duration in Drosophila*, particularly in how internal states influence behavioral outcomes. The identification of specific cell types and molecules that affect mating duration decisions indeed represents a significant conceptual advance. We also appreciate the reviewer’s commendation of the diverse array of assays employed in our investigation, which allowed us to approach our central question from multiple perspectives.

  In response to the reviewer’s constructive criticism regarding the lack of a cohesive framework tying the various components of our manuscript together, we have completely restructured our manuscript. We removed redundant data and incorporated additional convincing experiments, such as GCaMP analyses, to enhance clarity and coherence. Furthermore, we have provided a simplified yet comprehensive overview that describes the role of SIFa as a hub for neuropeptidergic signaling. This framework illustrates how SIFa orchestrates multiple behaviors related to energy balance through calcium signaling and synaptic plasticity via SIFaR-expressing cells.

  We believe these revisions address the reviewer’s concerns and provide a clearer understanding of how the different elements of our study fit together, ultimately strengthening the overall impact of our manuscript. Thank you for your valuable feedback, which has guided us in improving our work.

Reviewer #2

General Comments:* In the present study, the authors employ mating behavior in male fruit flies, Drosophila melanogaster, to investigate the behavioral roles of the neuropeptide SIFamide. The duration of mating behavior in these animals varies depending on context, previous experience, and internal metabolic state. The authors use this variability to explore the neuronal mechanisms that control these influences. In an abstraction step, they compare the different mating durations to concepts of neuronal interval timing.

The behavioral functions of the neuropeptide SIFamide have been thoroughly characterized in several studies, particularly in the contexts of circadian rhythm and sleep, courtship behavior, and food uptake. This study adds new data, demonstrating that SIFamide is essential for the proper control of mating behavior, highlighting the interconnection of various state- and motivation-dependent behaviors at the neuronal level. However, the hypothesis that mating behavior is related to interval timing is not convincingly supported.

Experimentally, the authors show that RNAi-mediated downregulation of SIFamide affects mating duration in male flies. They use combinations of RNAi lines under the control of various Gal4 lines to identify additional neurotransmitters, neuropeptides, and receptors involved in this process. This approach is complemented by neuroanatomical staining and single-cell RNA sequencing.*

* Overall, the study advances our knowledge about the behavioral roles of SIFamide, which is certainly important, interesting, and worthy of being reported. However, the manuscript also raises several serious caveats and includes points that remain speculative, are less convincing, or are simply incorrect.*

• Answer: We would like to thank the reviewer for their thoughtful and constructive comments regarding our study. We appreciate the recognition of our investigation into the behavioral roles of the neuropeptide SIFamide in male Drosophila melanogaster*, particularly how we explored the variability in mating duration influenced by context, previous experience, and internal metabolic state. We are grateful for the acknowledgment that our study adds valuable data demonstrating the essential role of SIFamide in regulating mating behavior, highlighting the interconnectedness of various state- and motivation-dependent behaviors at the neuronal level.

  We also appreciate the reviewer's recognition of our experimental approach, which includes RNAi-mediated downregulation of SIFamide, the use of various Gal4 lines to identify additional neurotransmitters, neuropeptides, and receptors involved in this process, as well as our incorporation of neuroanatomical staining and single-cell RNA sequencing.

  In response to the reviewer’s concerns regarding the hypothesis that mating behavior is related to interval timing, we acknowledge that this aspect requires further clarification and support. We have revisited this hypothesis in our manuscript to strengthen its foundation and address any speculative elements. We aim to provide more robust evidence and clearer connections between mating behavior and neuronal interval timing.

  Furthermore, we have taken care to address any points that may have been perceived as less convincing or incorrect. We are committed to refining our manuscript to ensure that all claims are well-supported by our data. Thank you once again for your valuable feedback. We believe that these revisions will enhance the clarity and impact of our study while addressing the concerns raised.

Major concerns:

Comment 1. The authors conclude from their mating experiments that SIFamide controls interval timing. This conclusion is not supported by the data, which only indicate that SIFamide is required for normal mating duration and modulates the motivation-dependent component of this behavior. There is no clear evidence linking this to interval timing.

__ Answer: __We appreciate the reviewer’s insightful comments regarding our conclusion linking SIFamide to interval timing in mating behavior. We acknowledge that our data primarily demonstrate that SIFamide is required for normal mating duration and modulates the motivation-dependent aspects of this behavior, and we recognize the need for clearer evidence connecting these observations to interval timing. Current research by Crickmore et al. has shed light on how mating duration in Drosophila serves as a powerful model for exploring changes in motivation over time as behavioral goals are achieved. For instance, at approximately six minutes into mating, sperm transfer occurs, leading to a significant shift in the male's nervous system: he no longer prioritizes sustaining the mating at the expense of his own survival. This change is driven by the output of four male-specific neurons that produce the neuropeptide Corazonin (Crz). When these Crz neurons are inhibited, sperm transfer does not occur, and the male fails to downregulate his motivation, resulting in matings that can last for hours instead of the typical ~23 minutes [10].

   Recent research by Crickmore et al. has received NIH R01 funding (Mechanisms of Interval Timing, 1R01GM134222-01) to explore mating duration in *Drosophila* as a genetic model for interval timing. Their work highlights how changes in motivation over time can influence mating behavior, particularly noting that significant behavioral shifts occur during mating, such as the transfer of sperm at approximately six minutes, which correlates with a decrease in the male's motivation to continue mating [10]. These findings suggest that mating duration is not only a behavioral endpoint but may also reflect underlying mechanisms related to interval timing.

   We believe that by leveraging the robustness and experimental tractability of these findings, along with our own work on SIFamide's role in mating behavior, we can gain deeper insights into the molecular and circuit mechanisms underlying interval timing. We will revise our manuscript to clarify this relationship and emphasize how SIFamide may interact with other neuropeptides and neuronal circuits involved in motivation and timing.

   In addition to the efforts of Crickmore's group to connect mating duration with a straightforward genetic model for interval timing, we have previously published several papers demonstrating that LMD and SMD can serve as effective genetic models for interval timing within the fly research community. For instance, we have successfully connected SMD to an interval timing model in a recently published paper [6], as detailed below:

"We hypothesize that SMD can serve as a straightforward genetic model system through which we can investigate "interval timing," the capacity of animals to distinguish between periods ranging from minutes to hours in duration.....

In summary, we report a novel sensory pathway that controls mating investment related to sexual experiences in Drosophila. Since both LMD and SMD behaviors are involved in controlling male investment by varying the interval of mating, these two behavioral paradigms will provide a new avenue to study how the brain computes the ‘interval timing’ that allows an animal to subjectively experience the passage of physical time [11–16]."

   Lee, S. G., Sun, D., Miao, H., Wu, Z., Kang, C., Saad, B., ... & Kim, W. J. (2023). Taste and pheromonal inputs govern the regulation of time investment for mating by sexual experience in male Drosophila melanogaster. *PLoS Genetics*, *19*(5), e1010753.

   We have also successfully linked LMD behavior to an interval timing model and have published several papers on this topic recently [4,5,7].

   Sun, Y., Zhang, X., Wu, Z., Li, W., & Kim, W. J. (2024). Genetic Screening Reveals Cone Cell-Specific Factors as Common Genetic Targets Modulating Rival-Induced Prolonged Mating in male Drosophila melanogaster. *G3: Genes, Genomes, Genetics*, jkae255.

   Zhang, T., Zhang, X., Sun, D., & Kim, W. J. (2024). Exploring the Asymmetric Body’s Influence on Interval Timing Behaviors of Drosophila melanogaster. *Behavior Genetics*, *54*(5), 416-425.

   Huang, Y., Kwan, A., & Kim, W. J. (2024). Y chromosome genes interplay with interval timing in regulating mating duration of male Drosophila melanogaster. *Gene Reports*, *36*, 101999.

   Finally, in this context, we have outlined in our INTRODUCTION section below how our LMD and SMD models are related to interval timing, aiming to persuade readers of their relevance. We hope that the reviewer and readers are convinced that mating duration and its associated motivational changes such as LMD and SMD provide a compelling model for studying the genetic basis of interval timing in *Drosophila*.

"The mating duration of male fruit flies is a suitable model for studying interval timing and it could change based on internal states and environmental context. Previous studies by our group[27–30] and others[31,32] have established several frameworks for investigating the mating duration using sophisticated genetic techniques that can analyze and uncover the neural circuits’ principles governing interval timing. In particular, males exhibit LMD behavior when they are exposed to an environment with rivals, which means they prolong their mating duration. Conversely, they display SMD behavior when they are in a sexually saturated condition, meaning they reduce their mating duration[33,34]."

Comment 2. On line 160, the authors state, "The connection between the dendrites and axons of the SIFamide neuronal processes is unknown." This is not entirely correct. State-of-the-art connectome analyses can determine synaptic connectivities between SIFamidergic neurons and pre-/postsynaptic neurons. The authors also overlook the thorough connectivity analysis by Martelli et al. (2017), which includes functional analyses and detailed anatomical descriptions that the current study confirms.

__ Answer:__ We appreciate the reviewer for acknowledging the efforts of Martelli et al. in elucidating the neuronal architecture of SIFa neurons. We recognize that it was an oversight on our part to state that "the connection between the dendrites and axons of SIFa neurons is unknown." This error arose because our manuscript has been in preparation for over ten years, predating the publication of Martelli et al.'s work. That statement likely reflects an outdated section of the manuscript.

We fully acknowledge the findings from previous publications and have removed that sentence entirely from our manuscript. In its place, we have added the following statement:

"The established connections and architecture of SIFa neurons has been described by Martelli et al., which enhances our understanding of their functional roles within the neuronal circuitry [51]. To identify the dendritic and axonal components of SIFa-neuronal processes, we employed a similar approach to that reported by Martelli [51]."

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

Comment 3. The mating experiments are overall okay, with sufficiently high sample sizes and appropriate statistical tests. However, many experiments lack genetic controls for the heterozygous parental strains, such as Gal4-ines AND UAS-lines. This is of course of importance and common standard.

__ Answer: __While we have previously addressed this type of reviewer feedback in our published manuscript [2–7] as well as this manuscript by Reviewer #1, we appreciate the reviewer’s suggestion to include traditional genetic control experiments. In response, we conducted all feasible combinations of genetic control experiments for LMD/SMD during the revision period. The results are presented in the supplementary figures and are described in the main text.

Comment 4. *Using a battery of RNAi lines, the authors aim to uncover which neurotransmitters might be co-released from SIFamide neurons to influence mating behavior. However, a behavioral effect of an RNAi construct expressed in SIFamidergic neurons does not demonstrate that the respective transmitter is actually released from these neurons. Alternative methods are needed to show whether glutamate, dopamine, serotonin, octopamine, etc., are present and released from SIFamide neurons. It is particularly challenging to prove that a certain substance acts as a transmitter released by a specific neuron. For example, anti-Tdc2 staining does not actually cover SIFamide neurons, and dopamine has not been described as present in SIFamide neurons. *

__ Answer:__ We appreciate the reviewer’s constructive comments regarding the need to demonstrate the presence of the responsible neurotransmitters in SIFa neurons. While many studies utilize neurotransmitter-synthesizing enzymes such as TH, VGlut, Gad1, and Trhn to assess neurotransmitter effects, we recognize the importance of conclusively establishing that glutamate and dopamine play significant roles in modulating energy balance within SIFa neurons.

   First, the enrichment of tyramine (TA), octopamine (OA), and dopamine (DA) in SIFa neurons was suggested in the study by Croset et al. (2018) [17]. Although we tested Tdc2-RNAi and observed interesting phenotypes, we chose not to publish these findings, as our data on glutamate and dopamine provide a more compelling explanation for how SIFa cotransmission with these neurotransmitters can independently influence various behaviors, including sleep and mating duration.

   To confirm the expression of DA in SIFa neurons, we employed a well-established genetic toolkit for dissecting dopamine circuit function in *Drosophila* [18]. Our findings indicate that TH-C-GAL4 specifically labels SIFa neurons, which have been confirmed as dopaminergic (S4M Fig). Our genetic intersection data, along with Xie et al.'s findings from 2018, confirm that a subset of SIFa neurons is indeed dopaminergic. We have described these new results in the main text as follows:

To further verify the presence of DA neurons within the SIFa neuron population, we utilized a well-established genetic toolkit for dissecting DA circuits and confirmed part of SIFa neurons are dopaminergic (S4M Fig) [58].

    To confirm the glutamatergic characteristics of SIFa neurons, we conducted several experiments that established glutamate as the most critical neurotransmitter for generating interval timing in both SIFa and SIFaR neurons. First, to demonstrate the presence of glutamatergic synaptic vesicles in SIFa neurons, we utilized a conditional glutamatergic synaptic vesicle marker for *Drosophila*, developed by Certel et al. [19]. Our results confirmed that SIFa neurons exhibit strong expression of glutamatergic synaptic vesicles (Fig. 2P and Fig. S4N as a genetic control). We have described these new results in the main text as follows:

“To further verify the presence of DA neurons within the SIFa neuron population, we utilized a well-established genetic toolkit for dissecting DA circuits and confirmed part of SIFa neurons are dopaminergic (S4M Fig) [58]. We also employed a conditional glutamatergic synaptic vesicle marker to confirm the presence of glutamatergic SIFa neurons (Fig 2P and Fig S4N) [59].”

   To further confirm that glutamate release from SIFa neurons influences the function of SIFaR neurons, we tested several RNAi strains targeting glutamate receptors. Our results showed that the knockdown of glutamate receptors in SIFaR-expressing neurons produced phenotypes similar to those observed with VGlut-RNAi knockdown in SIFa neurons (Fig. G-L). We believe that this series of experiments demonstrates that glutamate and dopamine work in conjunction with SIFa to modulate interval timing and other behaviors related to energy balance. We have described these new results in the main text as follows:

"To further substantiate the role of glutamate in SIFa-mediated behaviors. we targeted knockdown of VGlut receptors in SIFaR-expressing neurons. Strikingly, the knockdown of VGlut receptors in these neurons also disrupted SMD behavior, mirroring the phenotype observed upon direct suppression of glutamatergic signaling in SIFa neurons (S4G to S4L Fig). This suggests that glutamate is an essential neurotransmitter for modulating interval timing in SIFa neurons.”

Comment 5. Single-cell RNA sequencing data alone is insufficient to claim multiple transmitter co-release from SIFamide neurons. Figures illustrating single-cell RNA sequencing, such as Figure 3P-R, are not intuitively understandable, and the figure legends lack sufficient information to clarify these panels. As a side note, Tdc2 is not only present in octopaminergic neurons, but also in tyraminergic neurons.

__ Answer:__ We agree with the reviewer that scRNA-seq data alone is insufficient to support claims of multiple transmitter co-release in SIFa neurons. We also appreciate the reviewer for highlighting the potential for confusion among readers regarding the visualization methods used in our figures, particularly the tSNE plots of the scRNA-seq data. As noted in our previous response to Reviewer #1, we have removed most of the tSNE plots related to co-expression data involving SIFa and NPRs, which we believe will help clarify the interpretation for readers. However, we have retained a few tSNE plots, specifically Figures 2N-O, to illustrate the potential co-expression of the ple and Vglut genes in SIFa cells.

   We understand the reviewer’s concerns regarding the clarity of the presented data and the need for more detailed information about the extent of co-expression and the identification of SIFa-expressing cells. To address these concerns, we have provided a comprehensive description of our methods in the __MATERIALS AND METHODS__ section below.

"Single-nucleus RNA-sequencing analyses

The snRNAseq dataset analyzed in this paper is published in [20]and available at the Nextflow pipelines (VSN, https://github.com/vib-singlecell-nf), the availability of raw and processed datasets for users to explore, and the development of a crowd-annotation platform with voting, comments, and references through SCope (https://flycellatlas.org/scope), linked to an online analysis platform in ASAP (https://asap.epfl.ch/fca). For the generation of the tSNE plots, we utilized the Fly SCope website (https://scope.aertslab.org/#/FlyCellAtlas/*/welcome). Within the session interface, we selected the appropriate tissues and configured the parameters as follows: 'Log transform' enabled, 'CPM normalize' enabled, 'Expression-based plotting' enabled, 'Show labels' enabled, 'Dissociate viewers' enabled, and both 'Point size' and 'Point alpha level' set to maximum. For all tissues, we referred to the individual tissue sessions within the '10X Cross-tissue' RNAseq dataset. Each tSNE visualization depicts the coexpression patterns of genes, with each color corresponding to the genes listed on the left, right, and bottom of the plot. The tissue name, as referenced on the Fly SCope website is indicated in the upper left corner of the tSNE plot. Dashed lines denote the significant overlap of cell populations annotated by the respective genes. Coexpression between genes or annotated tissues is visually represented by differentially colored cell populations. For instance, yellow cells indicate the coexpression of a gene (or annotated tissue) with red color and another gene (or annotated tissue) with green color. Cyan cells signify coexpression between green and blue, purple cells for red and blue, and white cells for the coexpression of all three colors (red, green, and blue). Consistency in the tSNE plot visualization is preserved across all figures.

Single-cell RNA sequencing (scRNA-seq) data from the Drosophila melanogaster were obtained from the Fly Cell Atlas website (https://doi.org/10.1126/science.abk2432). Oenocytes gene expression analysis employed UMI (Unique Molecular Identifier) data extracted from the 10x VSN oenocyte (Stringent) loom and h5ad file, encompassing a total of 506,660 cells. The Seurat (v4.2.2) package (https://doi.org/10.1016/j.cell.2021.04.048) was utilized for data analysis. Violin plots were generated using the “Vlnplot” function, the cell types are split by FCA."

   We have also included detailed descriptions in the figure legends for the initial tSNE plot presented below to help readers clearly understand the significance of this visualization.

"Each tSNE visualization depicts the coexpression patterns of genes, with each color corresponding to the genes listed on the left, right, and/or bottom of the plot. The tissue name, as referenced on the Fly SCope website is indicated in the upper left corner of the tSNE plot. Consistency in the tSNE plot visualization is preserved across all figures."

   We appreciate the reviewer for acknowledging that Tdc2 is present in both TA and OA neurons. As we mentioned earlier, we have completely removed the Tdc2-related results from this manuscript, as we believe that more detailed experiments are necessary to confirm the roles of TA and OA in SIFa neurons.

Comment 6. The same argument applies to the expression of sNPF receptors in SIFamide neurons. The rather small anatomical stainings shown in figure 4M do not convincingly and unambiguously show that actually sNPF receptors are located on SIFamide neurons.

__ Answer:__ We appreciate the reviewer for pointing out that the co-expression of sNPF-R and SIFa needs further verification, and we agree with this assessment. To confirm the co-expression of SIFa with sNPF-R, we conducted a mini-screen of various sNPF-R driver lines and found that the chemoconnectome (CCT) sNPF-R2A driver which represent the physiological expression patterns of sNPF-R, consistently labels SIFa neurons [21].

   To further establish the functional connection between the SIFa and sNPF systems, we performed GCaMP experiments using SIFa-driven GCaMP in conjunction with sNPF-R neurons expressing P2X2, which can be activated by ATP treatment. As shown in Figures 3N-P, we demonstrated that activation of sNPF-R neurons by ATP significantly increases calcium levels in SIFa neurons. Our results strongly suggest that the sNPF-sNPF-R/SIFa system is functionally present and plays a role in modulating interval timing behaviors.

Comment 7. The authors use the GRASP technique (figure 4N) to determine whether synaptic connections are subject to modulation as a result from the animals' individual experience. The overall extremely bright fluorescence at the dorsal areas of both brain hemispheres (figure 4 N, middle panel) raises doubts whether this signal is actually a specific GRASP fluorescence between two small populations of neurons.

Answer: We appreciate the reviewer for critically highlighting the inadequacies in our presentation of the GRASP data. We agree that one of our previous panels contained excessive background noise, making it difficult for reviewers and readers to discern the different neuronal connections. To address this issue, we have replaced it with a more representative image that clearly illustrates the strengthening of synaptic connections from SIF to sNPF-R in several neurons, including SIFa cells (Fig. S5J). We hope that this updated image will help convince both the reviewer and readers of the validity of our GRASP data.

Comment 8. The authors cite Martelli et al. (2017) with the hypothesis that sNPF-releasing neurons provide input signals to SIFamide neurons to modulate feeding behavior. However, the cited manuscript does not contain such a hypothesis. The authors should review the reference in more detail.

__ Answer:__ We appreciate reviewer to correctly point our misunderstanding of references. We agree with reviewer that Martelli et al.'s paper didn't mention about sNPF signaling transmits hunger and satiety information to SIFa neurons. We removed this sentence and replaced it as below correctly mentioning that sNPF signaling is related to feeding behavior however it's connection to SIFa neurons are not known. We greatly appreciate the reviewer for acknowledging our efforts to accurately cite previous articles that support our rationale and ideas.

" Short neuropeptide F (sNPF) signaling plays a crucial role in regulating feeding behavior in Drosophila melanogaster, influencing food intake and body size [60,66,67]. However, there is currently no direct evidence reported linking sNPF signaling to SIFa neurons."

Comment ____9. In lines 281 ff., the authors state that SIFamide neurons receive inputs from peptidergic neurons but simultaneously claim that "this speculation is based on morphological observations." This is incorrect. The functional co-activation/imaging analyses provided in Martelli et al. (2017) should not be ignored.

* Answer: We fully agree with the reviewer that we misinterpreted Martelli et al.'s analysis. We have removed "this speculation is based on morphological observations." from* the following sentence and finalize as below:

"The SIFa neurons receive inputs from many peptidergic pathways including Crz, dilp2, Dsk, sNPF, MIP, and hugin"

Comment 10. Figure 6: A transcriptional calcium sensor (TRIC) was used to quantify the accumulation GFP induced by calcium influx in SIFamide neurons. However, I could not find any description of the method in the materials and methods section, nor any explanation how the data were acquired or analyzed. What is the RFP expression good for? How exactly are thresholds determined, and why are areas rather than fluorescence intensities quantified? Overall, this part of the manuscript is rather confusing and needs more explanation.

__ Answer: Thank you for your continued engagement with our manuscript and for highlighting the need for further clarification on our methods. Your attention to the details of our immunohistochemistry experiments is commendable, and we agree that providing a clear explanation of our thresholding and normalization procedures is essential for the transparency and reproducibility of our results. We primarily adhered to the established methods outlined by Kayser et al. [8]. To address your first point, we have now included a more detailed description of our thresholding and normalization procedures in the __MATERIALS AND METHODS section as below.

"Quantitative analysis of fluorescence intensity

To ascertain calcium levels and synaptic intensity from microscopic images, we dissected and imaged five-day-old flies of various social conditions and genotypes under uniform conditions. The GFP signal in the brains and VNCs was amplified through immunostaining with chicken anti-GFP, rabbit anti-DsRed, and mouse anti-nc82 primary antibodies. Image analysis was conducted using ImageJ software. For the quantification of fluorescence intensities, an investigator, blinded to the fly's genotype, thresholded the sum of all pixel intensities within a sub-stack to optimize the signal-to-noise ratio, following established methods [100]. The total fluorescent area or region of interest (ROI) was then quantified using ImageJ, as previously reported. For CaLexA or TRIC signal quantification, we adhered to protocols detailed by Kayser et al. [101], which involve measuring the ROI's GFP-labeled area by summing pixel values across the image stack. This method assumes that changes in the GFP-labeled area and intensity are indicative of alterations in the CaLexA and TRIC signal, reflecting synaptic activity. ROI intensities were background-corrected by measuring and subtracting the fluorescent intensity from a non-specific adjacent area, as per Kayser et al. [101]. For normalization, nc82 fluorescence is utilized for CaLexA, while RFP signal is employed for TRIC experiments, as the RFP signal from the TRIC reporter is independent of calcium signaling [72] . For the analysis of GRASP or tGRASP signals, a sub-stack encompassing all synaptic puncta was thresholded by a genotype-blinded investigator to achieve the optimal signal-to-noise ratio. The fluorescence area or ROI for each region was quantified using ImageJ, employing a similar approach to that used for CaLexA or TRIC quantification [100]. 'Norm. GFP Int.' refers to the normalized GFP intensity relative to the RFP signal.

• *

__Comment 11. __Similarly, it remains unclear how exactly syteGFP fluorescence and DenMark fluorescence were quantified. Why are areas indicated and not fluorescence intensity values? In fact, it appears worrisome that isolation of males should lead to a drastic decline in synaptic terminals (as measure through a vesicle-associated protein) by ~ 30%, or, conversely, keeping animals in groups lead to an respective increase (figure 7D). The technical information how exactly this was quantified is not sufficient.

__ Answer: __Thank you for your ongoing engagement with our manuscript and for emphasizing the need for clarification on our methods. We appreciate your attention to the details of our immunohistochemistry experiments and agree that a clear explanation of our thresholding and normalization procedures is vital for transparency and reproducibility. We acknowledge that signal intensity correlates with area measurements, which is an important consideration. In response to your valuable suggestion, we have revised our approach to present data based on intensity measurements and updated the Y-axis labeling to "Norm. GFP Int." (normalized GFP intensity) for clarity. We primarily followed the established methods from Kayser et al. (2014) [8]. Additionally, we have included a more detailed description of our thresholding and normalization procedures in the "Quantitative analysis of fluorescence intensity" in __MATERIALS AND METHODS __section as we quoted above.

• *

Minor concerns:

Comment 1. Reference 29 and reference 33 are the same.

   __Answer:__ We removed reference 29.

Comment 2. In figure legends, abbreviations should be explained when used first (e.g., figure 1 A "MD", is explained below for panel C-F), or "CS males". __ __

__Answer: __We have ensured that abbreviations are explained only when they are first used in the figure legends.

Comment 3. Indications for statistical significance must be shown in all figure legends at the end of each figure legend, not only in figure 1. __ __

__ Answer:__ We appreciate the reviewer’s advice. However, we have published all our other manuscripts using the same format for mating duration, stating, "The same notations for statistical significance are used in other figures," in the first figure where we describe our statistical significances. We intend to continue with this approach initially and will then adhere to the journal's policy.

Comment 4. The figures appear overloaded. For example why do you need two different axis designations (mating duration and differences between means)? __ __

__ Answer: __We appreciate the reviewer's suggestion to refine our figures, and we have indeed reformatted them to provide clearer presentation and improved readability. Our decision is based on the fact that our analysis encompasses not only traditional t-tests but also incorporates estimation statistics, which have been demonstrated to be effective for biological data analysis [22]. The inclusion of DBMs is essential for the accurate interpretation of these estimation statistics, ensuring a comprehensive representation of our findings. This is the primary area where we present two different axis designations.

Comment 5. Line: 1154: Typo: gluttaminergic should be glutamatergic.

   __Answer:__ We fixed all.

Comment 6. The authors frequently write "system" when referring to transmitter types, e.g., "glutaminergic system", "octopaminergic system", etc. It I not clear what the term "system" actually refers to. If the authors claim that SIFamide neurons release these transmitters in addition to SIFamide, they should state that precisely and then add experiments to show that this is the case.

   __Answer:__ We agree with reviewer and removed the word 'system' after the name of neurotransmitter's name.

Comment 7. Figure S6: It is not explained in the figure legend what fly strain "UAS-ctrl" actually is. Does "ctrl" mean control? And what genotype is hat control? __ __

__Answer: __It was wild-type strain. We fixed it as "+".

Comment 8. Figure legend S6, line 1371: The authors indicate experiments using UAS-OrkDeltaC. I could not find these data in the figure. __ __

__Answer: __It's now in Fig.S6U-W.

Comment 9. Line 470: "...reduced branching of SIFa axons at the postsynaptic level" should perhaps be "presynaptic level"?

Answer: Reviewer is correct. We fixed it.

Conclusive Comments:* Overall, the study advances our knowledge about the behavioral roles of SIFamide, which is certainly important, interesting, and worthy of being reported. However, the manuscript also raises several serious caveats and includes points that remain speculative and are less convincing.

Overall, the neuronal basis of action selection based on motivational factors (metabolic state, mating experience, sleep/wake status, etc.) is not well understood. The analysis of SIFamide function in insects might provide a way to address the question how different motivational signals are integrated to orchestrate behavior.*

• *Answer: Thank you for your thoughtful review and for recognizing the significance of our study in advancing knowledge about the behavioral roles of SIFamide. We appreciate your acknowledgment that our work is important, interesting, and worthy of publication.

We understand your concerns regarding the caveats and speculative points raised in the manuscript. We agree that the neuronal basis of action selection influenced by motivational factors—such as metabolic state, mating experience, and sleep/wake status—remains poorly understood. We believe that our analysis of SIFamide function in insects offers valuable insights into how various motivational signals are integrated to orchestrate behavior.

In response to your comments, we have made revisions to clarify our findings and address the concerns raised. We aim to strengthen the arguments presented in the manuscript and provide a more robust discussion of the implications of our results. Thank you once again for your constructive feedback, which has been instrumental in improving the clarity and impact of our work.

• *

* *

Reviewer #3

General Comments:* The Manuscript Peptidergic neurons with extensive branching orchestrate the internal states and energy balance of male Drosophila melanogaster by Yuton Song and colleagues addresses the question how SIFamidergic neurons coordinate behavioral responses in a context-dependent manner. In this context the authors investigate how SIFa neurons receive information about the physiological state of the animal and integrate this information into the processing of external stimuli. The authors show that SIFamidergic neurons and sNPPF expressing neurons form a feedback loop in the ventral nerve cord that modulate long mating (LMD) and shorter mating duration (SMD).

The manuscript is well written and very detailed and provides an enormous amount of data corroborating the claims of the authors. However, before publication the authors may want to address some points of concern that warrant some deeper explanation.*

• *__Answer: __Thank you for your positive feedback on our manuscript. We appreciate your recognition of the importance of our study in investigating how SIFa neurons integrate information about the physiological state of the animal with external stimuli, as well as your acknowledgment of the substantial data we provide to support our claims. We understand your concerns regarding certain points that require deeper explanation, and we are committed to addressing these issues to enhance the clarity and robustness of our findings. Your insights into the neuronal basis of action selection influenced by motivational factors are invaluable, and we believe that our exploration of SIFamide function in insects contributes significantly to understanding how various motivational signals orchestrate behavior. Thank you once again for your constructive comments, which will help us improve our manuscript before publication.

Major concerns:

Comment 1. On page 6 line 110 the authors describe that knocking-down SIFamide in glia cell does not change LMD or SMD and say that SIFa expression in glia does not contribute to interval timing behavior. However, the authors do not provide any information why they investigate the role of SIFa expression in glia. Is there any SIFa-expression in glia? The authors should somehow demonstrate using antibody labelling against SIFamide whether any glia specific expression of this peptide is to be expected. If they cannot provide this data - the take home message of the experiment cannot be that glia knockdown of SIFamide does not affect the behavior because you cannot knockdown anything that is not there.

• *

• In the latter case the experiment could be considered as a nice negative control for the elav-Gal4 pan-neuronal knockdown of SIFamide. The authors provide some Figure supplement where they use repo-Gal80 to partially answer this question. However, the authors should keep in mind that Gal4-drivers are not always complete in the expression pattern. Accordingly, the result should be corroborated with immune-labelling against SIFamide directly.*

__ Answer: __We appreciate the reviewer's constructive and critical comments regarding the use of our glial cell drivers. As the reviewer rightly pointed out, we believe that glial control is not essential for our manuscript, given that the expression of SIFa is well established in only four neurons. Therefore, we have removed the data related to glial drivers from this manuscript.

Comment 2. At this point I would like to directly comment on the figure quality. The figures are so crowded that the described anatomical details are hardly visible. In my opinion the manuscript would profit from less data in the main part and more stringent description of the core of the biological problem the authors want to address. The authors may want to reduce data from the main text and provide additional data that are not directly related to the main story as supplementary information.

__ Answer: __We agree with the reviewer. As another reviewer also suggested that we streamline our figures and data, we have completely restructured our figures and their presentation. In response, we have significantly reduced the density of the main figures and decreased the size of the graphs to enhance clarity. Additionally, we have increased the spacing between panels to ensure that each component is more easily distinguishable. Further details will be provided in our responses to each comment below.

• *

Comment 3. On page 8 starting with line 140 the authors describe the architecture of SIFamidergic neurons using several anatomical markers e.g., Denmark and further state that they have discovered that the dendrites of SIFa neurons span just the central brain area. Seeing that these data have been published in Martelli et al., 2017 the authors should tune down the claim that this was discovered in their work but rather corroborated earlier results.

__ Answer: __We acknowledge this error, as another reviewer also raised this issue. We have corrected our manuscript as follows:

"The established connections and architecture of SIFa neurons has been described by Martelli et al., which enhances our understanding of their functional roles within the neuronal circuitry [51]. To identify the dendritic and axonal components of SIFa-neuronal processes, we employed a similar approach to that reported by Martelli [51]."

Comment 4. In the next chapter, the authors aim at identifying the presynaptic inputs from SIFa positive neurons that may influence interval timing behavior and make a broad RNAi knock-down screen targeting a majority of neuromodulators. The authors claim that glutaminergic and dopaminergic signaling is necessary for interval timing behavior. I guess the authors mean "glutamatergic" instead of "glutaminergic" as glutamine is the precursor but not the neurotransmitter.

__ Answer: __The reviewer is correct. We have corrected this error and changed all instances to "glutamatergic."

Comment 5____. Furthermore, the authors show that the knock down of Tdc2 with RNAi has comparable effects on SMD than Glutamate and dopamine but appear to not further discuss this in the main text. To me it is not clear why the authors exclude Tdc2 from their resume. The authors should explain this in detail.

   __Answer:__ We appreciate the reviewer’s constructive comments regarding the need for a more detailed demonstration of the role of Tdc2 data. While we did test Tdc2-RNAi and observed interesting phenotypes, we decided not to include these findings in our publication, as our data on glutamate and dopamine offer a more compelling explanation for how SIFa cotransmission with these neurotransmitters can independently influence various behaviors, such as sleep and mating duration. Consequently, we have removed all data related to Tdc2. We believe that further evaluation is necessary to better understand the roles of the tyramine and octopamine systems in SIFa neurons.

Comment 6. The authors base their assumptions that the tested neurotransmitters are expressed in SIFamidergic neurons on Scope database analysis. But a transcript does not necessarily mean that it will be translated too. To my knowledge there is no available data in the literature showing that tyrosine hydroxylase is expressed in SIFamidergic neurons (see e.g., Mao and Davis, 2010). To show that ple or Tdc2 are indeed expressed and translated into functional enzymes in SIFamidergic neurons the authors should provide the according antibody labelling corroborating the result from the transcriptome analysis.

__ Answer:__ We appreciate the reviewer’s constructive comments regarding the role of neurotransmitters in conjunction with SIFa in modulating interval timing behaviors. To confirm the expression of dopamine (DA) in SIFa neurons, we utilized a well-established genetic toolkit for dissecting dopamine circuit function in Drosophila [18]. Our findings demonstrate that TH-C-GAL4 specifically labels SIFa neurons, which have been confirmed to be dopaminergic (Fig. S4M). This aligns with the genetic intersection data and the findings from Xie et al. (2018), confirming that a subset of SIFa neurons is indeed dopaminergic. We have included these new results in the main text as follows:

" To further verify the presence of DA neurons within the SIFa neuron population, we utilized a well-established genetic toolkit for dissecting DA circuits and confirmed part of SIFa neurons are dopaminergic (S4M Fig) [58]."

   To confirm the glutamatergic characteristics of SIFa neurons, we conducted several experiments that established glutamate as the most critical neurotransmitter for generating interval timing in both SIFa and SIFaR neurons. First, to demonstrate the presence of glutamatergic synaptic vesicles in SIFa neurons, we utilized a conditional glutamatergic synaptic vesicle marker for *Drosophila*, developed by Certel et al. [19]. Our results confirmed that SIFa neurons exhibit strong expression of glutamatergic synaptic vesicles (Fig. 2P and Fig. S4N as a genetic control). We have described these new results in the main text as follows:

"To further substantiate the role of glutamate in SIFa-mediated behaviors. we targeted the expression of VGlut receptor in neurons that carry the SIFaR. Strikingly, the knockdown of VGlut receptor in these neurons also disrupted SMD behavior, mirroring the phenotype observed upon direct suppression of glutamatergic signaling in SIFa neurons (S4O-L Fig)."

   To further confirm that glutamate release from SIFa neurons influences the function of SIFaR neurons, we tested several RNAi strains targeting glutamate receptors. Our results showed that the knockdown of glutamate receptors in SIFaR-expressing neurons produced phenotypes similar to those observed with VGlut-RNAi knockdown in SIFa neurons (Fig. S4I-N). We believe that this series of experiments demonstrates that glutamate and dopamine work in conjunction with SIFa to modulate interval timing and other behaviors related to energy balance. We have described these new results in the main text as follows:

"We also further verified that the knockdown of glutamate receptors in SIFaR-expressing neurons produces phenotypes similar to those resulting from VGlut knockdown in SIFa neurons (S4G to S4L Fig). This suggests that glutamate is an essential neurotransmitter for modulating interval timing in SIFa neurons."

Comment 7. The authors compare the LMD and SMD behavior of the animals with reduced expression with "heterozygous control animals" the authors should describe in detail what these are - are these controls the driver lines or the effector lines or a mix of both? The authors should provide the data for heterozygous driver line controls as well as heterozygous effector line controls to exclude any genetic background influence on the measured behavior. Accordingly, the authors should provide the data for the same controls for the sleep experiment in figure 3O and all the other behavioral experiments in the following parts of the manuscript.

__ Answer: __We sincerely thank the reviewer for insightful comments regarding the absence of traditional genetic controls in our study of LMD and SMD behaviors. We acknowledge the importance of such controls and wish to clarify our rationale for not including them in the current investigation. The primary reason for not incorporating all genetic control lines is that we have previously assessed the LMD and SMD behaviors of GAL4/+ and UAS/+ strains in our earlier studies. Our past experiences have consistently shown that 100% of the genetic control flies for both GAL4 and UAS exhibit normal LMD and SMD behaviors. Given these findings, we deemed the inclusion of additional genetic controls to be non-essential for the present study, particularly in the context of extensive screening efforts. We understand the value of providing a clear rationale for our methodology choices. To this end, we have added a detailed explanation in the "MATERIALS AND METHODS" section and the figure legends of Figure 1. This clarification aims to assist readers in understanding our decision to omit traditional controls, as outlined below.

"Mating Duration Assays for Successful Copulation

The mating duration assay in this study has been reported [33,73,93]. To enhance the efficiency of the mating duration assay, we utilized the Df (1) Exel6234 (DF here after) genetic modified fly line in this study, which harbors a deletion of a specific genomic region that includes the sex peptide receptor (SPR)[94,95]. Previous studies have demonstrated that virgin females of this line exhibit increased receptivity to males [95]. We conducted a comparative analysis between the virgin females of this line and the CS virgin females and found that both groups induced SMD. Consequently, we have elected to employ virgin females from this modified line in all subsequent studies. For naïve males, 40 males from the same strain were placed into a vial with food for 5 days. For single reared males, males of the same strain were collected individually and placed into vials with food for 5 days. For experienced males, 40 males from the same strain were placed into a vial with food for 4 days then 80 DF virgin females were introduced into vials for last 1 day before assay. 40 DF virgin females were collected from bottles and placed into a vial for 5 days. These females provide both sexually experienced partners and mating partners for mating duration assays. At the fifth day after eclosion, males of the appropriate strain and DF virgin females were mildly anaesthetized by CO2. After placing a single female in to the mating chamber, we inserted a transparent film then placed a single male to the other side of the film in each chamber. After allowing for 1 h of recovery in the mating chamber in 25℃ incubators, we removed the transparent film and recorded the mating activities. Only those males that succeeded to mate within 1 h were included for analyses. Initiation and completion of copulation were recorded with an accuracy of 10 sec, and total mating duration was calculated for each couple. All assays were performed from noon to 4pm. Genetic controls with GAL4/+ or UAS/+ lines were omitted from supplementary figures, as prior data confirm their consistent exhibition of normal LMD and SMD behaviors [33,73,93,96,97]. Hence, genetic controls for LMD and SMD behaviors were incorporated exclusively when assessing novel fly strains that had not previously been examined. In essence, internal controls were predominantly employed in the experiments, as LMD and SMD behaviors exhibit enhanced statistical significance when internally controlled. Within the LMD assay, both group and single conditions function reciprocally as internal controls. A significant distinction between the naïve and single conditions implies that the experimental manipulation does not affect LMD. Conversely, the lack of a significant discrepancy suggests that the manipulation does influence LMD. In the context of SMD experiments, the naïve condition (equivalent to the group condition in the LMD assay) and sexually experienced males act as mutual internal controls for one another. A statistically significant divergence between naïve and experienced males indicates that the experimental procedure does not alter SMD. Conversely, the absence of a statistically significant difference suggests that the manipulation does impact SMD. Hence, we incorporated supplementary genetic control experiments solely if they deemed indispensable for testing. All assays were performed from noon to 4 PM. We conducted blinded studies for every test[98,99] .

   While we have previously addressed this type of reviewer feedback in our published manuscript [2–7], we appreciate the reviewer’s suggestion to include traditional genetic control experiments. In response, we conducted all feasible combinations of genetic control experiments for LMD/SMD during the revision period. The results are presented in the supplementary figures and are described in the main text.

__Comment 8. __On page 11 line 231 to page 12 line 233 the authors claim that "sNPF signaling transmits hunger and satiety information to SIFa neurons in order to control food search and feeding" and cite Martelli et al., 2017. Could the authors explain more in detail how the Martelli paper somehow proposes this idea? I do not find the link between sNPF signaling hunger and SIFamide in this precise paper.

__ Answer:__ We appreciate the reviewer for accurately pointing out our misunderstanding of the references. We agree that Martelli et al.'s paper does not mention that sNPF signaling transmits hunger and satiety information to SIFa neurons. Consequently, we have removed the relevant sentence and replaced it with a statement correctly indicating that while sNPF signaling is related to feeding behavior, its connection to SIFa neurons remains unknown. We are grateful to the reviewer for acknowledging our efforts to accurately cite previous articles that support our rationale and ideas.

" Short neuropeptide F (sNPF) signaling plays a crucial role in regulating feeding behavior in Drosophila melanogaster, influencing food intake and body size [60,66,67] . However, there is currently no direct evidence reported linking sNPF signaling to SIFa neurons."

---

Comment 9. On page 15 line 302 - 303 the authors write that "except for PK2-R2, all other genes coexpress with SIFa in SCope data, indicating that hugin inputs to SIFa may not be transmitted through peptidergic signaling" - if SIFamidergic neurons do not express hugin-receptors how do the authors explain the inverted effect of PK2-R2-RNAi on single housed male courtship index when compared to heterozygous SIFaPT Gal4 control that show a reduction under comparable conditions.

__ Answer:__ We appreciate the reviewer’s constructive comments. In line with another reviewer’s suggestion, we have completely removed results of other neuropeptidergic inputs, focusing instead on how sNPF inputs modulate SIFa-mediated behavioral modulation using more advanced techniques such as GCaMP (Fig 3N). Consequently, the phenotypes resulting from various knockdowns of neuropeptide receptors are currently under investigation for a separate manuscript that we are preparing. We hope to successfully address how different neuropeptidergic inputs regulate SIFa neuron activity through various strategies.

Comment 10. On page 17 line 350 - 351 the authors write that "Stimulation of SIFa neurons resulted in an elevation in food consumption. Further, the authors write that "deactivation of SIFa neurons leads to a decrease in food consumption in male flies". From the way this is formulated it is not visible that the role of SIFamide in feeding control was published by Martelli and colleagues before. As the authors do not discuss the finding further in their discussion but cite the concerned paper in other aspects it appears as the authors intentionally want to omit this information to the reader. The authors may add a note that this has been shown before for female flies by Martelli and colleagues.

__ Answer:__ We appreciate reviewer's concern for properly mention previous Martelli et al.'s results about female feeding behavior modulated by SIFa neurons' activity. We agree with reviewer and added sentence as below in main text.

"Nevertheless, the temporary deactivation of SIFa neurons leads to a decrease in food consumption in male flies (Fig 4N and S6F to S6H) as previously described by Martelli et al.'s report in female flies [43]."

Comment 11. SIFamide receptor and GnIHR are discussed as descendants from a common ancestor and the authors nicely demonstrate that SIFamide does not only control homeostatic behavior as shown by Martelli and colleagues but also controls reproductive behavior. The evolution of such behavior control mechanisms may be integrated in the discussion too.

Answer: We appreciate the reviewer’s constructive comments, which enhance the evolutionary significance of our study. We agree with the reviewer and have added the following paragraph to the DISCUSSION section:

"The relationship between SIFamide receptors (SIFaR) and gonadotropin inhibitory hormone receptors (GnIHR) [89] highlights an intriguing evolutionary connection, as both are believed to have descended from a common ancestor [90,91]. This study expands on previous findings by Martelli et al., demonstrating that SIFamide not only regulates homeostatic behaviors but also plays a significant role in reproductive behavior [43]. GnIHR regulates food intake and reproductive behavior in opposing directions, thereby prioritizing feeding behavior over other behavioral tasks during times of metabolic need [92]. The evolution of these behavioral control mechanisms suggests a complex interplay between neuropeptides that modulate both physiological states and reproductive strategies. As SIFamide influences various behaviors, including feeding and sexual activity, it may be integral to understanding how organisms adapt their reproductive strategies in response to environmental and internal cues. This integration of behavioral modulation underscores the evolutionary significance of SIFamide signaling in coordinating essential life functions in Drosophila melanogaster and potentially other species, revealing pathways through which neuropeptides can shape behavior across different contexts."

Conclusive Comments: The manuscript by Song and colleagues is very interesting and may attract a broad readership. However, the authors miss to make clear what was already known and published on the role of SIFamide in homeostatic behavior control before their own study. Seen that the receptors for SIFamide and GnRHI derive from a common ancestor and apparently both GnRHI and SIFamide share similar roles in behavioral control this might indeed suggests that the basic function of this SIFaR/GnIHR-signaling pathway is conserved. This more broad evolutionary aspect is missing in the discussion of the manuscript.

• *Answer: We wholeheartedly agree with the reviewer regarding the evolutionary significance of SIFaR's function in relation to GnIHR, and we have expanded the DISCUSSION section to emphasize this important aspect.

---

"The relationship between SIFamide receptors (SIFaR) and gonadotropin inhibitory hormone receptors (GnIHR) [89] highlights an intriguing evolutionary connection, as both are believed to have descended from a common ancestor [90,91]. This study expands on previous findings by Martelli et al., demonstrating that SIFamide not only regulates homeostatic behaviors but also plays a significant role in reproductive behavior [43]. GnIHR regulates food intake and reproductive behavior in opposing directions, thereby prioritizing feeding behavior over other behavioral tasks during times of metabolic need [92]. The evolution of these behavioral control mechanisms suggests a complex interplay between neuropeptides that modulate both physiological states and reproductive strategies. As SIFamide influences various behaviors, including feeding and sexual activity, it may be integral to understanding how organisms adapt their reproductive strategies in response to environmental and internal cues. This integration of behavioral modulation underscores the evolutionary significance of SIFamide signaling in coordinating essential life functions in Drosophila melanogaster and potentially other species, revealing pathways through which neuropeptides can shape behavior across different contexts."

---

---

---

---

Reference

1. Zhang T, Wu Z, Song Y, Li W, Sun Y, Zhang X, et al. Long-range neuropeptide relay as a central-peripheral communication mechanism for the context-dependent modulation of interval timing behaviors. bioRxiv. 2024; 2024.06.03.597273. doi:10.1101/2024.06.03.597273
2. Kim WJ, Jan LY, Jan YN. A PDF/NPF Neuropeptide Signaling Circuitry of Male Drosophila melanogaster Controls Rival-Induced Prolonged Mating. Neuron. 2013;80: 1190–1205. doi:10.1016/j.neuron.2013.09.034
3. Kim WJ, Jan LY, Jan YN. Contribution of visual and circadian neural circuits to memory for prolonged mating induced by rivals. Nat Neurosci. 2012;15: 876–883. doi:10.1038/nn.3104
4. Zhang T, Zhang X, Sun D, Kim WJ. Exploring the Asymmetric Body’s Influence on Interval Timing Behaviors of Drosophila melanogaster. Behav Genet. 2024; 1–10. doi:10.1007/s10519-024-10193-y
5. Sun Y, Zhang X, Wu Z, Li W, Kim WJ. Genetic Screening Reveals Cone Cell-Specific Factors as Common Genetic Targets Modulating Rival-Induced Prolonged Mating in male Drosophila melanogaster. G3: Genes, Genomes, Genet. 2024; jkae255. doi:10.1093/g3journal/jkae255
6. Lee SG, Sun D, Miao H, Wu Z, Kang C, Saad B, et al. Taste and pheromonal inputs govern the regulation of time investment for mating by sexual experience in male Drosophila melanogaster. PLOS Genet. 2023;19: e1010753. doi:10.1371/journal.pgen.1010753
7. Huang Y, Kwan A, Kim WJ. Y chromosome genes interplay with interval timing in regulating mating duration of male Drosophila melanogaster. Gene Rep. 2024; 101999. doi:10.1016/j.genrep.2024.101999
8. Kayser MS, Yue Z, Sehgal A. A Critical Period of Sleep for Development of Courtship Circuitry and Behavior in Drosophila. Science. 2014;344: 269–274. doi:10.1126/science.1250553
9. Wong K, Schweizer J, Nguyen K-NH, Atieh S, Kim WJ. Neuropeptide relay between SIFa signaling controls the experience-dependent mating duration of male Drosophila. Biorxiv. 2019; 819045. doi:10.1101/819045
10. Thornquist SC, Langer K, Zhang SX, Rogulja D, Crickmore MA. CaMKII Measures the Passage of Time to Coordinate Behavior and Motivational State. Neuron. 2020;105: 334-345.e9. doi:10.1016/j.neuron.2019.10.018
11. Buhusi CV, Meck WH. What makes us tick? Functional and neural mechanisms of interval timing. Nat Rev Neurosci. 2005;6: 755–765. doi:10.1038/nrn1764
12. Merchant H, Harrington DL, Meck WH. Neural Basis of the Perception and Estimation of Time. Annu Rev Neurosci. 2012;36: 313–336. doi:10.1146/annurev-neuro-062012-170349
13. Allman MJ, Teki S, Griffiths TD, Meck WH. Properties of the Internal Clock: First- and Second-Order Principles of Subjective Time. Annu Rev Psychol. 2013;65: 743–771. doi:10.1146/annurev-psych-010213-115117
14. Rammsayer TH, Troche SJ. Neurobiology of Interval Timing. Adv Exp Med Biol. 2014; 33–47. doi:10.1007/978-1-4939-1782-2_3
15. Golombek DA, Bussi IL, Agostino PV. Minutes, days and years: molecular interactions among different scales of biological timing. Philosophical Transactions Royal Soc B Biological Sci. 2014;369: 20120465. doi:10.1098/rstb.2012.0465
16. Jazayeri M, Shadlen MN. A Neural Mechanism for Sensing and Reproducing a Time Interval. Curr Biol. 2015;25: 2599–2609. doi:10.1016/j.cub.2015.08.038
17. Croset V, Treiber CD, Waddell S. Cellular diversity in the Drosophila midbrain revealed by single-cell transcriptomics. eLife. 2018;7: e34550. doi:10.7554/elife.34550
18. Xie T, Ho MCW, Liu Q, Horiuchi W, Lin C-C, Task D, et al. A Genetic Toolkit for Dissecting Dopamine Circuit Function in Drosophila. Cell Reports. 2018;23: 652–665. doi:10.1016/j.celrep.2018.03.068
19. Certel SJ, Ruchti E, McCabe BD, Stowers RS. A conditional glutamatergic synaptic vesicle marker for Drosophila. G3. 2022;12: jkab453. doi:10.1093/g3journal/jkab453
20. Li H, Janssens J, Waegeneer MD, Kolluru SS, Davie K, Gardeux V, et al. Fly Cell Atlas: A single-nucleus transcriptomic atlas of the adult fruit fly. Science. 2022;375: eabk2432. doi:10.1126/science.abk2432
21. Deng B, Li Q, Liu X, Cao Y, Li B, Qian Y, et al. Chemoconnectomics: Mapping Chemical Transmission in Drosophila. Neuron. 2019;101: 876-893.e4. doi:10.1016/j.neuron.2019.01.045
22. Claridge-Chang A, Assam PN. Estimation statistics should replace significance testing. Nat Methods. 2016;13: 108–109. doi:10.1038/nmeth.3729

---

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Review on the manscurpit "Peptidergic neurons with extensive branching orchestrate the internal states and energy balance of male Drosophila melanogaster." By Yuton Song and colleagues.

The Manuscript Peptidergic neurons with extensive branching orchestrate the internal states and energy balance of male Drosophila melanogaster by Yuton Song and colleagues addresses the question how SIFamidergic neurons coordinate behavioral responses in a context-dependent manner. In this context the authors investigate how SIFa neurons receive information about the physiological state of the animal and integrate this information into the processing of external stimuli. The authors show that SIFamidergic neurons and sNPPF expressing neurons form a feedback loop in the ventral nerve cord that modulate long mating (LMD) and shorter mating duration (SMD).

The manuscript is well written and very detailed and provides an enormous amount of data corroborating the claims of the authors. However, before publication the authors may want to address some points of concern that warrant some deeper explanation.

On page 6 line 110 the authors describe that knocking-down SIFamide in glia cell does not change LMD or SMD and say that SIFa expression in glia does not contribute to interval timing behavior. However, the authors do not provide any information why they investigate the role of SIFa expression in glia. Is there any SIFa-expression in glia? The authors should somehow demonstrate using antibody labelling against SIFamide whether any glia specific expression of this peptide is to be expected. If they cannot provide this data - the take home message of the experiment cannot be that glia knockdown of SIFamide does not affect the behavior because you cannot knockdown anything that is not there. In the latter case the experiment could be considered as a nice negative control for the elav-Gal4 pan-neuronal knockdown of SIFamide. The authors provide some Figure supplement where they use repo-Gal80 to partially answer this question. However, the authors should keep in mind that Gal4-drivers are not always complete in the expression pattern. Accordingly, the result should be corroborated with immune-labelling against SIFamide directly.

At this point I would like to directly comment on the figure quality. The figures are so crowded that the described anatomical details are hardly visible. In my opinion the manuscript would profit from less data in the main part and more stringent description of the core of the biological problem the authors want to address. The authors may want to reduce data from the main text and provide additional data that are not directly related to the main story as supplementary information. On page 8 starting with line 140 the authors describe the architecture of SIFamidergic neurons using several anatomical markers e.g., Denmark and further state that they have discovered that the dendrites of SIFa neurons span just the central brain area. Seeing that these data have been published in Martelli et al., 2017 the authors should tune down the claim that this was discovered in their work but rather corroborated earlier results.

In the next chapter, the authors aim at identifying the presynaptic inputs from SIFa positive neurons that may influence interval timing behavior and make a broad RNAi knock-down screen targeting a majority of neuromodulators. The authors claim that glutaminergic and dopaminergic signaling is necessary for interval timing behavior. I guess the authors mean "glutamatergic" instead of "glutaminergic" as glutamine is the precursor but not the neurotransmitter. Furthermore, the authors show that the knock down of Tdc2 with RNAi has comparable effects on SMD than Glutamate and dopamine but appear to not further discuss this in the main text. To me it is not clear why the authors exclude Tdc2 from their resume. The authors should explain this in detail. The authors base their assumptions that the tested neurotransmitters are expressed in SIFamidergic neurons on Scope database analysis. But a transcript does not necessarily mean that it will be translated too. To my knowledge there is no available data in the literature showing that tyrosine hydroxylase is expressed in SIFamidergic neurons (see e.g., Mao and Davis, 2010). To show that ple or Tdc2 are indeed expressed and translated into functional enzymes in SIFamidergic neurons the authors should provide the according antibody labelling corroborating the result from the transcriptome analysis. The authors compare the LMD and SMD behavior of the animals with reduced expression with "heterozygous control animals" the authors should describe in detail what these are - are these controls the driver lines or the effector lines or a mix of both? The authors should provide the data for heterozygous driver line controls as well as heterozygous effector line controls to exclude any genetic background influence on the measured behavior. Accordingly, the authors should provide the data for the same controls for the sleep experiment in figure 3O and all the other behavioral experiments in the following parts of the manuscript.

On page 11 line 231 to page 12 line 233 the authors claim that "sNPF signaling transmits hunger and satiety information to SIFa neurons in order to control food search and feeding" and cite Martelli et al., 2017. Could the authors explain more in detail how the Martelli paper somehow proposes this idea? I do not find the link between sNPF signaling hunger and SIFamide in this precise paper. On page 15 line 302 - 303 the authors write that "except for PK2-R2, all other genes coexpress with SIFa in SCope data, indicating that hugin inputs to SIFa may not be transmitted through peptidergic signaling" - if SIFamidergic neurons do not express hugin-receptors how do the authors explain the inverted effect of PK2-R2-RNAi on single housed male courtship index when compared to heterozygous SIFaPT Gal4 control that show a reduction under comparable conditions.

On page 17 line 350 - 351 the authors write that "Stimulation of SIFa neurons resulted in an elevation in food consumption. Further, the authors write that "deactivation of SIFa neurons leads to a decrease in food consumption in male flies". From the way this is formulated it is not visible that the role of SIFamide in feeding control was published by Martelli and colleagues before. As the authors do not discuss the finding further in their discussion but cite the concerned paper in other aspects it appears as the authors intentionally want to omit this information to the reader. The authors may add a note that this has been shown before for female flies by Martelli and colleagues. SIFamide receptor and GnIHR are discussed as descendants from a common ancestor and the authors nicely demonstrate that SIFamide does not only control homeostatic behavior as shown by Martelli and colleagues but also controls reproductive behavior. The evolution of such behavior control mechanisms may be integrated in the discussion too.

Significance

The manuscript by Song and colleagues is very interesting and may attract a broad readership. However, the authors miss to make clear what was already known and published on the role of SIFamide in homeostatic behavior control before their own study. Seen that the receptors for SIFamide and GnRHI derive from a common ancestor and apparently both GnRHI and SIFamide share similar roles in behavioral control this might indeed suggests that the basic function of this SIFaR/GnIHR-signaling pathway is conserved. This more broad evolutionary aspect is missing in the discussion of the manuscript.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In the present study, the authors employ mating behavior in male fruit flies, Drosophila melanogaster, to investigate the behavioral roles of the neuropeptide SIFamide. The duration of mating behavior in these animals varies depending on context, previous experience, and internal metabolic state. The authors use this variability to explore the neuronal mechanisms that control these influences. In an abstraction step, they compare the different mating durations to concepts of neuronal interval timing.

The behavioral functions of the neuropeptide SIFamide have been thoroughly characterized in several studies, particularly in the contexts of circadian rhythm and sleep, courtship behavior, and food uptake. This study adds new data, demonstrating that SIFamide is essential for the proper control of mating behavior, highlighting the interconnection of various state- and motivation-dependent behaviors at the neuronal level. However, the hypothesis that mating behavior is related to interval timing is not convincingly supported.

Experimentally, the authors show that RNAi-mediated downregulation of SIFamide affects mating duration in male flies. They use combinations of RNAi lines under the control of various Gal4 lines to identify additional neurotransmitters, neuropeptides, and receptors involved in this process. This approach is complemented by neuroanatomical staining and single-cell RNA sequencing. Overall, the study advances our knowledge about the behavioral roles of SIFamide, which is certainly important, interesting, and worthy of being reported. However, the manuscript also raises several serious caveats and includes points that remain speculative, are less convincing, or are simply incorrect.

Major concerns:

• The authors conclude from their mating experiments that SIFamide controls interval timing. This conclusion is not supported by the data, which only indicate that SIFamide is required for normal mating duration and modulates the motivation-dependent component of this behavior. There is no clear evidence linking this to interval timing.
• On line 160, the authors state, "The connection between the dendrites and axons of the SIFamide neuronal processes is unknown." This is not entirely correct. State-of-the-art connectome analyses can determine synaptic connectivities between SIFamidergic neurons and pre-/postsynaptic neurons. The authors also overlook the thorough connectivity analysis by Martelli et al. (2017), which includes functional analyses and detailed anatomical descriptions that the current study confirms.
• The mating experiments are overall okay, with sufficiently high sample sizes and appropriate statistical tests. However, many experiments lack genetic controls for the heterozygous parental strains, such as Gal4-ines AND UAS-lines. This is of course of importance and common standard.
• Using a battery of RNAi lines, the authors aim to uncover which neurotransmitters might be co-released from SIFamide neurons to influence mating behavior. However, a behavioral effect of an RNAi construct expressed in SIFamidergic neurons does not demonstrate that the respective transmitter is actually released from these neurons. Alternative methods are needed to show whether glutamate, dopamine, serotonin, octopamine, etc., are present and released from SIFamide neurons. It is particularly challenging to prove that a certain substance acts as a transmitter released by a specific neuron. For example, anti-Tdc2 staining does not actually cover SIFamide neurons, and dopamine has not been described as present in SIFamide neurons. Single-cell RNA sequencing data alone is insufficient to claim multiple transmitter co-release from SIFamide neurons. Figures illustrating single-cell RNA sequencing, such as Figure 3P-R, are not intuitively understandable, and the figure legends lack sufficient information to clarify these panels. As a side note, Tdc2 is not only present in octopaminergic neurons, but also in tyraminergic neurons.
• The same argument applies to the expression of sNPF receptors in SIFamide neurons. The rather small anatomical stainings shown in figure 4M do not convincingly and unambiguously show that actually sNPF receptors are located on SIFamide neurons.
• The authors use the GRASP technique (figure 4N) to determine whether synaptic connections are subject to modulation as a result from the animals' individual experience. The overall extremely bright fluorescence at the dorsal areas of both brain hemispheres (figure 4 N, middle panel) raises doubts whether this signal is actually a specific GRASP fluorescence between two small populations of neurons.
• The authors cite Martelli et al. (2017) with the hypothesis that sNPF-releasing neurons provide input signals to SIFamide neurons to modulate feeding behavior. However, the cited manuscript does not contain such a hypothesis. The authors should review the reference in more detail.
• In lines 281 ff., the authors state that SIFamide neurons receive inputs from peptidergic neurons but simultaneously claim that "this speculation is based on morphological observations." This is incorrect. The functional co-activation/imaging analyses provided in Martelli et al. (2017) should not be ignored.
• Figure 6: A transcriptional calcium sensor (TRIC) was used to quantify the accumulation GFP induced by calcium influx in SIFamide neurons. However, I could not find any description of the method in the materials and methods section, nor any explanation how the data were acquired or analyzed. What is the RFP expression good for? How exactly are thresholds determined, and why are areas rather than fluorescence intensities quantified? Overall, this part of the manuscript is rather confusing and needs more explanation.
• Similarly, it remains unclear how exactly syteGFP fluorescence and DenMark fluorescence were quantified. Why are areas indicated and not fluorescence intensity values? In fact, it appears worrisome that isolation of males should lead to a drastic decline in synaptic terminals (as measure through a vesicle-associated protein) by ~ 30%, or, conversely, keeping animals in groups lead to an respective increase (figure 7D). The technical information how exactly this was quantified is not sufficient.

Minor comments:

• Reference 29 and reference 33 are the same.
• In figure legends, abbreviations should be explained when used first (e.g., figure 1 A "MD", is explained below for panel C-F), or "CS males".
• Indications for statistical significance must be shown in all figure legends at the end of each figure legend, not only in figure 1.
• The figures appear overloaded. For example why do you need two different axis designations (mating duration and differences between means)?
• Line: 1154: Typo: gluttaminergic should be glutamatergic.
• The authors frequently write "system" when referring to transmitter types, e.g., "glutaminergic system", "octopaminergic system", etc. It I not clear what the term "system" actually refers to. If the authors claim that SIFamide neurons release these transmitters in addition to SIFamide, they should state that precisely and then add experiments to show that this is the case.
• Figure S6: It is not explained I the figure legend what fly strain "UAS-ctrl" actually is. Does "ctrl" mean control? And what genotype is hat control?
• Figure legend S6, line 1371: The authors indicate experiments using UAS-OrkDeltaC. I could not find these data in the figure.
• Line 470: "...reduced branching of SIFa axons at the postsynaptic level" should perhaps be "presynaptic level"?

Significance

Overall, the study advances our knowledge about the behavioral roles of SIFamide, which is certainly important, interesting, and worthy of being reported. However, the manuscript also raises several serious caveats and includes points that remain speculative and are less convincing.

Overall, the neuronal basis of action selection based on motivational factors (metabolic state, mating experience, sleep/wake status, etc.) is not well understood. The analysis of SIFamide function in insects might provide a way to address the question how different motivational signals are integrated to orchestrate behavior.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

This manuscript by Song et al. investigates the molecular mechanisms underlying changes in mating duration in Drosophila induced by previous experience. As they have shown previously, they find that male flies reared in isolation have shorter mating duration than those reared in groups, and also that male flies with previous mating experience have shorter mating duration than sexually naïve males. They have conducted a myriad of experiments to demonstrate that the neuropeptide SIFa is required for these changes in mating duration. They have further provided evidence that SIFa-expressing neurons undergo changes in synaptic connectivity and neuronal firing as a result of previous mating experience. Finally, they argue that SIFa neurons form reciprocal connections with sNPF-expressing neurons, and that communication within the SIFa-sNPF circuit is required for experience-dependent changes in mating duration. These results are used to assert that SIFa neurons track the internal state of the flies to modulate behavioral choice.

Major Comments:

1. The authors are to be commended for the sheer quantity of data they have generated, but I was often overwhelmed by the figures, which try to pack too much into the space provided. As a result, it is often unclear what components belong to each panel. Providing more space between each panel would really help.

This is a rare instance where I would recommend paring down the paper to focus on the more novel, clear and relevant results. For example, all of Figure 2 shows the projection pattern of SIFa+ neuron dendrites and axons, which have been reported by multiple previous papers. Figure 7G and J show trans-tango data and SIFaR-GAL4 expression patterns, which were previously reported by Dreyer et al., 2019. These parts could be removed to supplemental figures. Figure 5 details experiments that knock down expression of different neurotransmitter receptors within the SIFa-expressing cells. The results here are less definitive than the SIFa knockdown results, and the SCope data supporting the idea that these receptors are expressed in SIFa-expressing neurons is equivocal. I would recommend removing these data (perhaps they could serve as the basis for another manuscript) or focusing solely on the CCHa1R results, which is the only manipulation that affects both LMD and SMD.

Finally, I would like the authors to spend more time explaining how they think the results tie together. For example, how do the authors think the changes in branching and activity in SIFa-expressing neurons tie to the change in mating duration provoked by previous experience? It would benefit the manuscript to simplify and clarify the message about what the authors think is happening at the mechanistic level. The various schematics (eg Fig 7N) describe the results but the different parts feel like separate findings rather than a single narrative. 2. Most of the experiments lack traditional controls. For example, in experiments in Fig 1C-K, one would typically include genetic controls that contain either the GAL4 or UAS elements alone. The authors should explain their decision to omit these control experiments and provide an argument for why they are not necessary to correctly interpret the data. In this vein, the authors have stated in the methods that stocks were outcrossed at least 3x to Canton-S background, but 3 outcrosses is insufficient to fully control for genetic background. 3. Throughout the manuscript, the authors appear to use a single control condition (sexually naïve flies raised in groups) to compare to both males raised singly and males with previous sexual experience. These control conditions are duplicated in two separate graphs, one for long mating duration and one for short mating duration, but they are given different names (group vs naïve) depending on the graph. If these are actually the same flies, then this should be made clear, and they should be given a consistent name across the different "experiments". 4. The authors use SCope data to provide evidence for co-expression of SIFa and other neurotransmitters or neuropeptide receptors. The graphs they show are hard to read and it is not clear to what extent the gene expression is actually overlapping. It would be more definitive to show graphs that indicate which percentage of SIFa-expressing cells co-express other neurotransmitter components, and what the actual level of expression of the genes is. The authors should also provide more information on how they identified the SIFa+ cells in the fly atlas dataset. These are important pieces of information to be able to interpret the effects of manipulation of these other neurotransmitter systems within SIFa-expressing cells on mating duration. 5. I would like to see more information on how the thresholding and normalization was done for immunohistochemistry experiments. Was thresholding applied equally across all datasets? Furthermore, "overlap" of Denmark and Syt-eGFP is taken as evidence for synaptic connectivity, but the latter requires more than just overlap in the location of the axon terminal and dendrite regions of the neuron. 6. None of the RNAi experiments have been validated to demonstrate effective knockdown. In many cases, this would be difficult to do because of a lack of an antibody to quantify in a cell-specific manner; however, this fact should be acknowledged, especially in cases where there was found to be a lack of phenotype, which could result from lack of knockdown. The authors could also look for evidence in the literature of cases where RNAi lines they have used have been previously validated. For SIFa, knockdown can be easily confirmed with the SIFa antibody the authors have used elsewhere in the manuscript.

Minor Comments:

1. There are quite a lot of citations to preprints, including preprints of the manuscripts under review. It seems inappropriate to cite a preprint of the manuscript you are submitting because it gives a false sense of strengthening the assertions being made in the manuscript.
2. It seems that labels are incorrect on a number of the immunohistochemistry figures. For example, in Fig 2N, it labels dendrites as green, but this is sytEGFP, which is the presynaptic terminal.
3. Fig 4N shows grasp between SIFa-LexA and sNPF-R-GAL4, but the authors have argued that these two components should both be expressed in SIFa-expressing cells. This would make grasp signal misleading, because it would appear in the SIFa-expressing cells even without synaptic contacts due to both split GFP molecules being expressed in these cells.
4. For quantifying TRIC and CaLexA experiments (eg Figure 6A-E), intensity of signal should be measured in addition to the area covered by the signal.

Significance

This study will be most relevant to researchers interested in understanding neuronal control of behavior. It has provided novel information about the mechanisms underlying mating duration in flies, which is used to delineate how internal state influences behavioral outcomes. This represents a conceptual advance, particularly in identifying a cell type and molecule that influences mating duration decisions. The strength of the manuscript is the number of different assays used to investigate the central question from a number of angles. The limitation is that there is a lack of a big picture tying the different components of the manuscript together. Too much data is presented without providing a framework to understand how the data points fit together.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2024-02648

Corresponding author(s): Kevin Berthenet (kevin.berthenet@lyon.unicancer.fr) and Gabriel Ichim (gabriel.ichim@lyon.unicancer.fr)

1. General Statements

We thank all the reviewers for their time and their constructive criticism, based on which we propose the revision plan detailed bellow. All our responses are indicated in italics font. When is the case, the figures for the reviewers are included just below the answer. Only where indicated they have been included in the manuscript. The line numbers indicated here refer to those in original manuscript.

The two reviews are listed in full at the end of the document.

2. Description of the planned revisions

Reviewer #1

In this manuscript, the authors report a non-apoptotic role for caspase 3 in promoting cell migration. RNA sequencing revealed a "gene signature" associated with caspase 3 knockdown in a melanoma cell line, although there is no investigation of the connection between caspase 3 expression and the regulation of gene expression. Mass spectrometry-based experiments (AP-MS and BioID) identified numerous interacting proteins, with coronin 1B being the most extensively characterized. Data provided indicates that there is a direct interaction between caspase 3 and coronin 1B, and that caspase 3 influences coronin 1B phosphorylation basally and following ligand stimulation. Both proteins are required for efficient cell migration in scratch wound assays. Data is provided indicating that the actions of caspase 3 are independent of proteolytic activity, although the pharmacological inhibition of caspase activity is not complete, nor is the knockdown of BAX/BAK, making these conclusions poorly substantiated. Evaluation of pathways regulating caspase 3 expression implicates the SP1 transcription factor.

Response: We thank the reviewer for their supportive comment. Regarding specific pharmacological inhibition of caspase-3, work is under way to complement the results obtained with a pan-caspase inhibitor (qVD-OPh). We will use specific effector caspases inhibitors, complemented by several other approaches: complete KO of BAX and BAK proteins to prevent all eventual mitochondrial permeabilization and low-level effector caspase activation, overexpression (OE) of the anti-apoptotic protein BCL-xL to also prevent residual mitochondrial permeabilization, while also OE XIAP, a potent caspase inhibitor. The promising preliminary data using two effector caspases specific inhibitors (Ac-DEVD-CHO and Ac-DNLD-CHO) in two different melanoma cells, during wound healing migration, is shown below, with no effect on melanoma cell migration.

Line 129 - The data in Sup. Fig. 1H-L are technical, but where are the mass spectrometry results from the BioID2 experiments? These technical figures are really only relevant if the BioID2 system has been used for protein pull-downs, not for the IF analysis in Fig. 2B.

Response: We apologize for lack of precision in the article logical flow, we will now incorporate the MS data based on the BioID2 experiment earlier in the manuscript.

Line 143 - Figure 2C - it is not entirely convincing that caspase 7 is not associated with the cytoskeleton, there is a visible band in lysates from both cell lines, in contrast with GAPDH which is convincingly cytoplasmic. This is particularly true in the WM852 cell lines, in which the Caspase 3 band is almost the same as Caspase 7. These results would also be more convincing if there was IF of Caspase 7 and actin to show whether it is or is not enriched in regions of higher F-actin levels.

Response: Indeed, our data points towards an enrichment of caspase-3 at the cell cortex. Since generally caspase-7 protein levels are lower, we detected it less in the cytosolic fraction. As suggested, now we performed more sensitive IF colocalization confocal imaging between caspase-7 and F-actin and find it also partially localized to the cortical cytoskeleton (see below). However, this effector caspase is not involved in melanoma cell migration (see wound healing assay below, with two different siRNAs for CASP7 and the positive control of siRNA CASP3).

Figure 2D - knockdowns with only a single siRNA are insufficient, this should be replicated with additional siRNAs. In addition to the effect on actin anisotropy, it appears as though cells are smaller, is this and any other morphological changes reproducible?

Response: We plan to strengthen the data shown in Fig.2D with additional siRNAs, as shown below. In addition, high-content screening (HCS) microscopy will provide several other cell morphology descriptors.

Figure 2D-E. Is it cytochalasin B or D used in these experiments? The text and figures don't agree with each other. 5. Figure 2F-G, same comments above for 2D-E (i.e. comments 3 & 4).

Response: The experimental conditions will be better detailed in the revised manuscript.

Figure 2F-G, it appears as though the fewer focal adhesions in the Caspase 3 knockdown cells are bigger per focal adhesion, is this a consistent result? If so, what is the explanation?

Response: In addition to number, we also plan to quantify the size of focal adhesions.

Figure 2H - it's not clear how this RNAseq data is relevant to the manuscript. There are some genes in the heat map, but it's not clear which ones are changed in their expression in the caspase 3 knockdown cells, nor is it clear how this is relevant to the proposed mechanisms of Caspase 3 interacting with and influencing the phosphorylation of coronin 1B. If there is no connection, then these data can be removed.* *

Response: As suggested by the reviewer, the RNAseq data presented in Figure 2H will be removed from the revised manuscript since it is not very relevant.

Supp. Figure 3 - given that there is data from multiple siRNAs for the incucyte migration data, it should be in the primary figures. And since there are multiple siRNAs and CRISPR/Cas9 KO cells, there should be nothing limiting the replication of the other data presented from only a single siRNA.

Response: Several siRNA are now used for replicating key results as shown above.

Figure 3A - how was cell adhesion measured? The methods section says "cell adhesion was determined through cell shape analysis and scoring" But this is very vague.

Response: We thank the reviewer for spotting out this ambiguity, in the revised manuscript we will be more precise in Material and Methods section.

Figure 3L - was the Casp7 knockdown experiments done with multiple siRNAs? Both melanoma cell lines? Why is this figure only shown out to 24 hours, whereas the other Incucyte experiment run out to 48 hours? Where is the western blot confirming the caspase 7 knockdown? This is important to establish a clear lack of effect.

Response*: We apologize for lacking more details, we now provide several siRNA for caspase-7, all showing no or minimal effect of melanoma cell migration (see answer to point 2). *

Line 190 - it is not true to say that in the presence of QVD there is no longer any caspase activity induced by actinomycin D/ABT263 in supplemental Figures 3J-K. The way that the Y axis has been broken diminishes the difference between untreated and treated cells. In fact, there is apparently over 3-4 times more caspase activity in the actinomycin D/ABT263 treated cells in the presence of QVD relative to basal caspase activity. As a result, it cannot be concluded that there is no residual caspase activity.

Response: We were not precise enough in describing the data in S3J-K. In the revised manuscript we will clearly say that since treatment with a pan-caspase inhibitor does not have the effect of lowering any basal caspase activity (column 1 versus 2), we conclude that in melanoma cells (WM793 and WM852) there is no basal caspase activation that could drive cell motility. The ActD/ABT263 treatment was used as positive control for bona fide induction of effector caspase activation. These results will be complemented by BAX/BAK DKO and BCLxL OE.

Line 192 - Does the knockout of BAX/BAK (which apparently reduced but did not eliminate BAX/BAK protein levels in Supp. Fig. 3L) actually "completely block" caspase activity via the mitochondrial pathway? This has not been demonstrated.

Response: We now provide a fluorometric effector caspases assay showing abrogation of caspase activity in BAX/BAK DKO cells (see below, caspase activating treatment is ActinomycinD plus ABT263). In addition, we will improve the DKO efficacy.

Line 217 - coronin 1B was a hit from which assays? IP-MS and/or BioID2? I see that this is shown in Figure 5A but not referenced in this sentence.

Line 218 - the reference to Figure 5A should be in the previous sentence. Line 220 - Can it really be said that the interaction is specific since there is a coronin 1B band in the GFP "negative" control?__ __

Response*: The revised manuscript will address these inadequacies. *

Line 222 - it is a good control to show that siRNA-knockdown of Caspase 3 reduced the PLA signal in Figure 5C, but the reciprocal experiment of looking at what happens with Coronin 1B knockdown should be included. How does the PLA signal relate to phalloidin-stained F-actin?

Response: The proximity ligation assay (PLA) is now complemented by KD of Coronin 1B (see below) and we will try to also add the phalloidin staining for F-actin, if compatible with the PLA protocol.

Line 224 - looking at the line scans, is the lack of recruitment of coronin 1B to the F-actin at the edge of the protrusion in the Caspase 3 knockdown cells reproducible? Is the point that caspase 3 recruits Coronin 1B? There is an obvious difference in the F-actin at the cell edge, but if the F-actin were as dense in the Caspase 3 knockdown cells as they are for the control, would the same lack of coronin 1B be apparent?

Response: This aspect will be better addressed/discussed in the revised manuscript.

Line 227 - where is the western blot showing the effectiveness of the coronin 1B knockdown to accompany Figure 5F.

Response: The efficacy of coronin 1B KD will be added in the revised manuscript.

Figure 5G - the blots indicate that there is no change in phospho-PKCalpha in the caspase 3 knockdown cells, although phospho-coronin 1B does decrease. This has not been commented upon in the text. Is the implication that there is a non-PKCalpha mediated mechanism for coronin 1B phosphorylation that is dependent on caspase 3?

Figure 5H - following from the previous point, there is no phospho-PKCalpha blot that would be a positive control for the effect of PDGF stimulation on PKC activation, in control and caspase 3 knockdown cells, to evaluate whether the effect on coronin 1B phosphorylation was upstream or downstream of PKCalpha. This is also true for Supp. Fig. 4H.

Response*: Since there are several PKC isoforms that might be co-expressed in melanoma cells, it is possible that PKCalpha is not the one responsible for phosphorylating Coronin 1B. We will be more precise in our investigations by using a pan-phospho-PKC antibody. *

Does phosphorylation of coronin 1B affect its interaction with caspase 3?

Response: We will assess by Co-IP the interaction of caspase-3 with both non-phosphorylated and phosphorylated Coronin 1B.

Figure 6 - as before, only a single siRNA to knockdown SP1 is insufficient to robustly support the conclusions.

Response: As shown below, we addressed this helpful comment by using several siRNAs to assess the role of SP1 in melanoma cell motility, in two different melanoma cell lines.

• *

Reviewer #2

In this manuscript, the authors provide substantial amounts of experimental evidence that caspase-3, more precisely pro-caspase-3, might be involved in promoting melanoma cell migration and invasion. As such, this function, which might stem from scaffolding roles independent of proteolytic activity (yet not shown entirely convincingly), could possibly be similar to those attributed to other caspases, yet the latter omitted experiments testing for the necessity of enzyme activity. The data are novel and interesting and obviously deserve publication. Yet, a number of criticisms need to be listed.

Response*: We thank the reviewer for upholding the novelty of our study. As also rightfully pointed by R1, we will strive in a revised manuscript to definitely show that caspase-3 participate to melanoma cell motility independently of its pro-apoptotic protease role: we will use two effector caspases specific inhibitors (Ac-DEVD-CHO and Ac-DNLD-CHO, as shown above) complemented by several other approaches: complete KO of BAX and BAK protein to prevent all eventual mitochondrial permeabilization and low-level effector caspase activation, OE of the anti-apoptotic protein BCL-xL to also prevent residual mitochondrial permeabilization, while also OE XIAP, a potent caspase inhibitor. *

• *

• First and foremost, I don't seem to find ethical approval information on the animal experiments. While I do not work with zebrafish myself, I am also somewhat concerned by the size of tumours seen in some of the depicted fish. It is highly important that appropriate information in this direction, including possible endpoints, is provided. Response*: We completely agree with the reviewer, yet the ethical approval is already provided in the manuscript (line 588) and will be complemented by adding the endpoints. *

The second major issue lies in figure 1. The figure as a whole seems to be very much forced to support or motivate later experimental findings. The authors lack sufficient clarity on some of the approaches and seem to judge on the data to a good bit as they see fit. (…)

I´d suggest to largely take out Fig1 in its current form, spend time on properly describing any analysis of public data, carefully interpret these and move them probably to the end of the results. Currently, it just leaves the impression that the data were pushed as hard as possible to promote the good work that follows.

Response*: We will carefully consider the reviewer’s comments and rework the bioinformatics analysis presented in Figure 1 (and associated supplementary figure), making sure we will present certain data as correlation (and not causality) and go into more details on the physio-pathological features of melanoma patients with low/high caspase-3 expression. *

• *

The text on line 129ff seems to have omitted any outcomes from the Suppl. Fig1H-L. What was found and what are we supposed to learn from this?

Response: We apologize for lack of precision in the article logical flow, we will now incorporate the MS data based on the BioID2 experiment earlier in the manuscript.* *

Lines 146/147 state similar effects upon CASP3 depletion and cytochalasin D. I cannot make that out from Fig.2D. Can you be more specific or visualize this better?

Response: We will fix this by including zoomed and detailed images of individual cells.

• Is it possible to state whether effects such as in Fig.3B are general rather than showing just 1 cell?

Response: The defects in cell adhesion for caspase-3-depleted cells are quantified in Figure 3A. Moreover, we will add representative images.

• *

It is unclear how the genes in Fig.2H were defined and why would all of these differ (unless this was an inclusion criterion for the panel). Are these considered to be downstream of CASP3 somehow? I don't fully get the message here. Is this panel even required here?

Response: As it brings little information, panel 2H will be excluded from the revised manuscript.

To fully prove independence of caspase-3 activity, it would be appropriate to k/o caspase-3 to then reconstitute the cells with inactive caspase-3.

• *

Response: We will try our best of addressing this comment in the revised manuscript.

Fig.4C and associated text: Statements on changes in tumor size cannot be made from data on tumor free survival.

Response: We apologize for the misleading data interpretation; this will be tuned down in a revised manuscript.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors provide substantial amounts of experimental evidence that caspase-3, more precisely pro-caspase-3, might be involved in promoting melanoma cell migration and invasion. As such, this function, which might stem from scaffolding roles independent of proteolytic activity (yet not shown entirely convincingly), could possibly be similar to those attributed to other caspases, yet the latter omitted experiments testing for the necessity of enzyme activity. The data are novel and interesting and obviously deserve publication. Yet, a number of criticisms need to be listed.

Major comments

• First and foremost, I don't seem to find ethical approval information on the animal experiments. While I do not work with zebrafish myself, I am also somewhat concerned by the size of tumours seen in some of the depicted fish. It is highly important that appropriate information in this direction, including possible endpoints, is provided.
• The second major issue lies in figure 1. The figure as a whole seems to be very much forced to support or motivate later experimental findings. The authors lack sufficient clarity on some of the approaches and seem to judge on the data to a good bit as they see fit. For example
  • The authors claim CASP3 expression is high in skin, yet the data in Fig.1A proofs this to be wrong, since it is rather medium across the range of available tissues.
  • The authors state that CASP3 stood out to be highly expressed in primary and metastatic melanoma cells, but don't state against what they compared. Other caspases or non-melanoma cell lines? The latter would be relevant comparison, I suppose. Also, names of cell lines were omitted in the figure as were information on whether they were from primary or metastatic tissue.
  • The authors state that CASP3 expression is "clinically relevant" since it differed between primary and metastatic classified TCGA cases. Why would that have clinical relevance at all? It simply correlates with staging. Clinical relevance for example could be found in data where e.g. CASP3 expression in primary melanoma associates with higher risk for recurrence or progression to metastasis.
  • The associated supplemental fig. 1 needs to be criticised as well. Panel S1D shows a Kaplan Meyer plot of high UP vs low UP signatures. Looking at the survival times plotted (less than one year), one wonders how this plot was generated. What stages were included and why, were these balanced in size, what are the group sizes, and why was a cutoff of 300 days chosen (I can only guess this might have been limited to late stage disease, but what would be the point?). There doesn´t seem to be any useful information included in this to make this somewhat interpretable from the disease or clinical side, let alone usefulness when taking into account other confounding variables. Please also note that the TCGA data need to be looked at with great care, since dates of diagnosis often are not the dates when the analysed samples were taken (e.g. diagnosis might be been primary melanoma at the time the initial lesion was removed by a dermatologist, yet the associated TCGA sample was taken much later when the disease had recurred and could already be metastatic).
  • Combining the problems mentioned above with the descriptive rest of the figure leads into a vastly exaggerated but probably wished for claim that "CASP3 expression must confer melanoma cells with certain advantages, likely unrelated to the role of caspase-3 in apoptosis). I´d suggest to largely take out Fig1 in its current form, spend time on properly describing any analysis of public data, carefully interpret these and move them probably to the end of the results. Currently, it just leaves the impression that the data were pushed as hard as possible to promote the good work that follows.
• The text on line 129ff seems to have omitted any outcomes from the Suppl. Fig1H-L. What was found and what are we supposed to learn from this?
• Lines 146/147 state similar effects upon CASP3 depletion and cytochalasin D. I cannot make that out from Fig.2D. Can you be more specific or visualize this better?
• Is it possible to state whether effects such as in Fig.3B are general rather than showing just 1 cell?
• The micrographs, especially those that were quantitatively analysed, in print display seem largely overexposed. It wouldn't make sense to measure correlations across areas that seemingly are just saturated. If the analyses were done on non-saturated raw images with higher dynamic range, please state so clearly and maybe adjust the settings more appropriately for display items.
• It is unclear how the genes in Fig.2H were defined and why would all of these differ (unless this was an inclusion criterion for the panel). Are these considered to be downstream of CASP3 somehow? I don't fully get the message here. Is this panel even required here?
• To fully prove independence of caspase-3 activity, it would be appropriate to k/o caspase-3 to then reconstitute the cells with inactive caspase-3.
• Fig.4C and associated text: Statements on changes in tumor size cannot be made from data on tumor free survival.

Minor comments:

• Please check the sentence on line 43. Obviously this applies to living, not dead organisms, and obviously dead cells don´t migrate. Maybe simply delete.
• Please add mol. weight markers to all panels.
• Please check the entire manuscript to ensure, also for interpretability, that procaspase-3 and processed or active caspase-3 variants are appropriately referred to

Significance

Significance

Provide contextual information to readers (editors and researchers) about the novelty of the study, its value for the field and the communities that might be interested.

The following aspects are important: General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

The main finding is of high significance and already supported very well by experimental evidence. The authors discuss the limitations of their study appropriately, e.g. the possibility that more advanced in vivo settings might provide additional evidence for a pro-migratory role of caspase-3. However, I would clearly NOT suggest to include e.g. mouse models in the study; in my opinions very little would be learned from that in addition to what the authors already show in a well established melanoma zebrafish model. As stated in the previous section, I am clearly very unconvinced about the first figure centering on public data repositories and their analysis. This indeed is the weakest part of the paper.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

Non-death roles of proteins classically linked to cell death processes are now slowly becoming appreciated more widely. As such, the contribution of the authors is very timely and noteworthy. No other convincing studies exist that would ascribe a non-proteolytic role of caspase-3 to migration or invasion. The novelty thus is high. The advance is primarily seen in the idenfication of this role and the mechanistic and functional basis of it.

Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

Primarily, basic researchers with links to cell death /survival regulation will appreciate these results very highly. This could be a fairly large audience. Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. Cell death regulation, cancer, systems biology, cellular imaging

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this manuscript, the authors report a non-apoptotic role for caspase 3 in promoting cell migration. RNA sequencing revealed a "gene signature" associated with caspase 3 knockdown in a melanoma cell line, although there is no investigation of the connection between caspase 3 expression and the regulation of gene expression. Mass spectrometry-based experiments (AP-MS and BioID) identified numerous interacting proteins, with coronin 1B being the most extensively characterized. Data provided indicates that there is a direct interaction between caspase 3 and coronin 1B, and that caspase 3 influences coronin 1B phosphorylation basally and following ligand stimulation. Both proteins are required for efficient cell migration in scratch wound assays. Data is provided indicating that the actions of caspase 3 are independent of proteolytic activity, although the pharmacological inhibition of caspase activity is not complete, nor is the knockdown of BAX/BAK, making these conclusions poorly substantiated. Evaluation of pathways regulating caspase 3 expression implicates the SP1 transcription factor.

Major comments:

1. Line 129 - The data in Sup. Fig. 1H-L are technical, but where are the mass spectrometry results from the BioID2 experiments? These technical figures are really only relevant if the BioID2 system has been used for protein pull-downs, not for the IF analysis in Fig. 2B.
2. Line 143 - Figure 2C - it is not entirely convincing that caspase 7 is not associated with the cytoskeleton, there is a visible band in lysates from both cell lines, in contrast with GAPDH which is convincingly cytoplasmic. This is particularly true in the WM852 cell lines, in which the Caspase 3 band is almost the same as Caspase 7. These results would also be more convincing if there was IF of Caspase 7 and actin to show whether it is or is not enriched in regions of higher F-actin levels.
3. Figure 2D - knockdowns with only a single siRNA are insufficient, this should be replicated with additional siRNAs. In addition to the effect on actin anisotropy, it appears as though cells are smaller, is this and any other morphological changes reproducible?
4. Figure 2D-E. Is it cytochalasin B or D used in these experiments? The text and figures don't agree with each other.
5. Figure 2F-G, same comments above for 2D-E (i.e. comments 3 & 4).
6. Figure 2F-G, it appears as though the fewer focal adhesions in the Caspase 3 knockdown cells are bigger per focal adhesion, is this a consistent result? If so, what is the explanation?
7. Figure 2H - it's not clear how this RNAseq data is relevant to the manuscript. There are some genes in the heat map, but it's not clear which ones are changed in their expression in the caspase 3 knockdown cells, nor is it clear how this is relevant to the proposed mechanisms of Caspase 3 interacting with and influencing the phosphorylation of coronin 1B. If there is no connection, then these data can be removed.
8. Supp. Figure 3 - given that there is data from multiple siRNAs for the incucyte migration data, it should be in the primary figures. And since there are multiple siRNAs and CRISPR/Cas9 KO cells, there should be nothing limiting the replication of the other data presented from only a single siRNA.
9. Figure 3A - how was cell adhesion measured? The methods section says "cell adhesion was determined through cell shape analysis and scoring" But this is very vague.
10. Figure 3L - was the Casp7 knockdown experiments done with multiple siRNAs? Both melanoma cell lines? Why is this figure only shown out to 24 hours, whereas the other Incucyte experiment run out to 48 hours? Where is the western blot confirming the caspase 7 knockdown? This is important to establish a clear lack of effect.
11. Line 190 - it is not true to say that in the presence of QVD there is no longer any caspase activity induced by actinomycin D/ABT263 in supplemental Figures 3J-K. The way that the Y axis has been broken diminishes the difference between untreated and treated cells. In fact, there is apparently over 3-4 times more caspase activity in the actinomycin D/ABT263 treated cells in the presence of QVD relative to basal caspase activity. As a result, it cannot be concluded that there is no residual caspase activity.
12. Line 192 - Does the knockout of BAX/BAK (which apparently reduced but did not eliminate BAX/BAK protein levels in Supp. Fig. 3L) actually "completely block" caspase activity via the mitochondrial pathway? This has not been demonstrated.
13. Line 217 - coronin 1B was a hit from which assays? IP-MS and/or BioID2? I see that this is shown in Figure 5A but not referenced in this sentence.
14. Line 218 - the reference to Figure 5A should be in the previous sentence.
15. Line 220 - Can it really be said that the interaction is specific since there is a coronin 1B band in the GFP "negative" control?
16. Line 222 - it is a good control to show that siRNA-knockdown of Caspase 3 reduced the PLA signal in Figure 5C, but the reciprocal experiment of looking at what happens with Coronin 1B knockdown should be included. How does the PLA signal relate to phalloidin-stained F-actin?
17. Line 224 - looking at the line scans, is the lack of recruitment of coronin 1B to the F-actin at the edge of the protrusion in the Caspase 3 knockdown cells reproducible? Is the point that caspase 3 recruits Coronin 1B? There is an obvious difference in the F-actin at the cell edge, but if the F-actin were as dense in the Caspase 3 knockdown cells as they are for the control, would the same lack of coronin 1B be apparent?
18. Line 227 - where is the western blot showing the effectiveness of the coronin 1B knockdown to accompany Figure 5F?
19. Figure 5G - the blots indicate that there is no change in phospho-PKCalpha in the caspase 3 knockdown cells, although phospho-coronin 1B does decrease. This has not been commented upon in the text. Is the implication that there is a non-PKCalpha mediated mechanism for coronin 1B phosphorylation that is dependent on caspase 3?
20. Figure 5H - following from the previous point, there is no phospho-PKCalpha blot that would be a positive control for the effect of PDGF stimulation on PKC activation, in control and caspase 3 knockdown cells, to evaluate whether the effect on coronin 1B phosphorylation was upstream or downstream of PKCalpha. This is also true for Supp. Fig. 4H.
21. Does phosphorylation of coronin 1B affect its interaction with caspase 3?
22. Figure 6 - as before, only a single siRNA to knockdown SP1 is insufficient to robustly support the conclusions.

Minor comments:

1. Figure 2C - all caps for CASP7
2. Figures 2D,F - Cytochalsin
3. Figure 2H, the labelling of gene names is too small to read.
4. Supplemental Fig 1A - why is A375 here? Why plot a graph and not just write a percentage protein remaining under the figure? There are no errors indicated, so presumably this is N = 1.
5. Line 127 - smal

Significance

The manuscript is interesting and novel, making it relevant for a broad basic research audience. The role of caspase 3 in non-apoptotic biological processes is not extensively characterized, making this study an advance in the field. The methods are appropriate and well-executed. The statistical methods are mostly appropriate, although some assays (e.g. wound healing assays) do not have associated statistical analysis. Most of the conclusions are adequately substantiated by the results, but as indicated above and in the points below, this is not entirely consistent. There is an issue with only a single siRNA being used in several experiments that should be addressed.

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Reviewer #1

Drawbacks: -While the population-specific approach is a strength, it also limits the direct applicability of findings to other populations.

We thank the Reviewer for highlighting this important question. While we acknowledge the mentioned limitation, we would like to emphasize the benefits of adopting a population-specific approach, especially given that human gut microbiome diversity remains underexplored in many populations worldwide. Researching the Estonian population microbiome, we contribute to the broader global collection of gut microbial species, helping to address this gap.

Moreover, new microbial species and strains identified in the Estonian population may be relevant for populations with similar environmental and lifestyle factors, such as the Finnish, Baltic, and Nordic populations. These findings can enhance understanding of regionally relevant microbiome characteristics and may serve as a useful reference for studies in these related populations. As more population-based microbiome research is published, it will build a valuable resource for cross-population comparative studies, shedding light on global microbiome diversity and its implications for health.

Lastly, as part of the Estonian Biobank, our primary objective is to advance personalized medicine for the Estonian population. This requires a highly accurate reference for our specific population. We believe our approach not only benefits Estonian healthcare but also provides insights and methodologies that other population biobanks may find valuable as they embark on similar paths toward personalized medicine.

-The study primarily focuses on taxonomic composition at the genus or species level, but a more in-depth functional analysis of the novel species could provide additional insights.

We thank the Reviewer for this valuable addition. Functional analysis plays a crucial role in understanding the mechanisms that link the microbiome to human health, making it an essential. This becomes even more critical when studying newly discovered species. However, before embarking on functional analysis, we believe it is important to emphasize that, while high-quality metagenome-assembled genomes (MAGs) provide valuable insights, they do not fully represent the genomic completeness and accuracy of genomes reconstructed from pure bacterial cultures. Acknowledging this distinction was one of the reasons we decided not to include functional analysis in the original article. With these considerations in mind, we research a strain structure of four known species of Butyricimonas genus. While the primary interest lies in species associated with diseases, this particular species lacks a substantial number of high-quality MAGs. To gain deeper insights, we prioritized including a new species within the analyzed genus to perform a comparative analysis between the new species and a well-defined strain of a known species, creating a more comprehensive understanding. Among the 758 different genera present in our MAG collection, we selected the Butyricimonas genus for the following reasons: (1) it is a well-described genus of gut bacteria, represented by 300 high-quality MAGs in our dataset (2) it contains four known species along with two newly identified species clusters, and (3) the newly discovered species were shown to be prevalent in the human gut microbiome, being detected in more than 50% of samples through mapping.

The following section was integrated in the new paragraph “Genome level analysis of species of interest” on page 6 in the revised version of the manuscript:

“Species-level association studies can help identify candidates for genome-level analysis by exploring strain structure and functional differences. However, such analyses require a large number of high-quality MAGs from the same species, which is only feasible within large cohorts with deep sequencing data. While we currently need more samples to obtain sufficient MAGs for the new disease-associated species, we perform an analysis with the Butyricimonas genus species as an example. We show that the assembled MAGs of Butyricimonas species such as B. faeciominis, B. virosa, B. paravirosa and B. faecalis make up different strains (Figure 4a, Figure 4b, Supplementary results, Supplementary Table S5). After selecting a strain representative, we conducted a pan-genome analysis of species and strain-representative MAGs, including the two new species. The analysis revealed unique gene clusters consistently present in the new species but absent in all other analyzed species and strains (Figure 4c, Supplementary results, Supplementary Table S6).

Figure 4. Strain-level structure of the Butyricimonas genus and comparative functional analysis of new species and known species strain. a. The strain structure of known Butyricimonas species assembled in the Estonian population - B. paravirosa, B. faecalis, B. virosa, and B. faecihominis (based on ANI index comparison). __b. __Butyricimonas genus structure. Comparisons include all known species from Butyricimonas genus (species assembled in Estonian population and publically available species) and all 4 newly assembled MAGs belonged to a new species. Publicly available Butyricimonas species - B. synergistica, "Candidatus B. faecavium", "Candidatus B. hominis", "Candidatus B. phoceensis", and "Candidatus B. vaginalis"—are each represented by a single genome of the type strain (the strain defining the species according to ISCP). Species assembled from our data are represented by both the type strain and all strain-representative MAGs. ANI values less than 95% (represent that MAGs belonged to different species) are not coloured, 95–100% ANI colored in different colors with 1% step. c. Pan-genome analysis of Butyricimonas genus. The analysis included the same genomes and MAGs as the analysis of the Butyricimonas genus structure and showed a core gene, as well as specific gene, set for the species. The two new species clusters (highlighted in green) also exhibit unique species-specific gene sets.

We have also added Supplementary Results to our paper, providing a more detailed description of the strain structure analysis of Butyricimonas species and the functional analysis of both known and new species. We chose not to include this in the main text to avoid shifting the focus of the paper.

Supplementary results

Butyricimonas genus species strain-level and functional analysis

Beyond taxonomic characterisation, it is crucial to understand the functional differences of newly detected species, as this insight is key to fully understanding the mechanisms that link the microbiome to human health. Reconstructing MAGs from a large cohort provides multiple genomes of the same species, particularly for prevalent species. During our study, we assembled MAGs from 758 different genera, including 358 genera with more than 10 extracted MAGs. Conducting a detailed in-depth strain-level and functional analysis of all these genera requires substantial effort. Therefore, we conduct an in-depth strain-level and functional analysis using the genus Butyricimonas as an example, because. The genus Butyricimonas was chosen for the following reasons: (1) it is a well-characterized genus of gut bacteria, represented by 300 high-quality MAGs in our dataset (2) it included four known species and two newly identified species clusters, and (3) the new discovered species have been shown to be prevalent in the human gut microbiome.

*Known Butyricimonas species exhibit a clear strain-level structure based on pairwise ANI comparisons (ANI > 99.0), as calculated using ANIclustermap19 (Figure 4a). From a total of 300 high-quality MAGs selected for strain and functional analysis within the Butyricimonas genus, the species Butyricimonas paravirosa is represented by 23 MAGs and forms 5 distinct strain clusters. While one big cluster (cluster_id: B30) includes 7 highly similar genomes with ANI values close to 100%, other clusters (B31, B32, B34) exhibit more genomic diversity, with genomes showing ANI values greater between 99.0% and 99.6%. The final cluster (B33) contains a single MAG, suggesting unique genomic variation. Butyricimonas faecihominis is represented by 65 MAGs and forms 8 distinct strain clusters, exhibiting high genome similarity within each cluster. Butyricimonas virosa is represented by 67 MAGs and forms 14 distinct strain clusters. These strain clusters can be divided into two strain cluster groups, with low similarity between the groups (ANI values between strain cluster groups ranging from 95.0% to 96% and approaching the species boundary). Within each group, the strain clusters also exhibit genomic diversity, indicating a substantial level of variation even within closely related strains. Finally, Butyricimonas faecalis has the highest number of MAGs within its species 141 MAGs and shows a clean picture of 5 strain clusters with high similarity within the strain cluster (Figure SR1). *

Figure SR1. The strain structure of known Butyricimonas species assembled in the Estonian population - B. paravirosa, B. faecalis, B. virosa, and B. faecihominis (ANI index comparison histogram).

In addition to the four known species, we assembled two new species within the Butyricimonas genus. The first new species cluster (id: Bn1) is represented by a single MAG (H0366_Butyricimonas_undS), which serves as the representative genome for this species. The second new species cluster (id: Bn2) comprises three MAGs, with H1068_Butyricimonas_undS designated as the representative genome, selected using dRep. To determine the placement of these new species within the genus, we conducted genome pairwise comparisons based on the Average Nucleotide Identity (ANI) index between the MAGs of the new species and other species within the Butyricimonas genus. For the known species identified in our population, we selected representative genomes for each strain. These comparisons were made between the all new species MAGs, strain-level representative MAGs of four known species, and type strain genomes (the strain that defines the species according to ISCP) from other species of the Butyricimonas genus that were not present in our cohort,, such as Butyricimonas synergistica, "Candidatus Butyricimonas faecavium", "Candidatus Butyricimonas hominis", "Candidatus Butyricimonas phoceensis", and "Candidatus Butyricimonas vaginalis" (Figure 4b). The MAGs from the second new species cluster (Bn2) form a distinct and cohesive group, showing a closer relationship to Butyricimonas paravirosa and Butyricimonas faecihominis. In contrast, the first new species (Bn1), represented by a single MAG, is positioned closer to Butyricimonas virosa. Interestingly, while the ANI index between the type strain of Butyricimonas virosa and the Bn1 MAG is less than 95%, certain strains of B. virosa (e.g., strains 3, 6, 7, 9, 10, and 12) show ANI values slightly above 95%, which technically classifies them as the same species.

To explore functional differences between new species clusters and other known species we perform pangenomic analysis using the analysis and visualization platform for ‘omics data (Anvi’o) workflow for microbial pangenomics20__. As the first new species cluster (id:Bn1) is represented by a single MAG, despite it containing unique genes not found in any other analyzed genomes, it is challenging to draw definitive conclusions. Another new species cluster (id:Bn2) consisting of three MAGs provides clearer insights. All three MAGs within this new species cluster share 183 unique genes that are consistently present across the species cluster but absent in all other analyzed species and strains. (Figure 4c). The majority of these genes (142 genes, 73.96%) have unknown functions. Among the genes with defined functions, the functions are distributed across various COG categories (__Suppl. Table S5,____Suppl. Figure SR2), with the top three categories being “Cell wall/membrane/envelope biogenesis”, “General function prediction only”, and “Posttranslational modification, protein turnover, and chaperones”.

Figure SR2. COG categories for 183 unique genes that are consistently present across the new species MAGs from Butyricimonas genus (cluster id:Bn2) but absent in all other analyzed species and strains.

Undoubtedly, further research is needed to understand the role of newly identified species in the human microbiome and to determine whether strain-level differences influence bacterial interactions with the gut and their overall impact. However, our current analysis has already significantly expanded our knowledge of the diversity within this genus. It has added two new species to the ten previously described and revealed the strain structure of known species within the Estonian population.

-Is it possible for this large dataset to distill information and have plots for strain diversity of abundant and prevalent species, including low abundance species per donor or between donors? Can authors add such a plot or discuss this?

We thank the Reviewer for this insightful question. Strain-level analysis holds significant potential and is one of the key reasons to use the genome assembly approach, rather than relying on microbiome community profiling using existing human gut species databases. To demonstrate how this can be applied in large datasets like ours, we focused on the same Butyricimonas genus selected for functional analysis. We believe that combining both strain-level and functional analyses provides a more comprehensive understanding when used together.

The following section has been incorporated into a new paragraph, “Genome-Level Analysis of Species of Interest,” on page 6 of the revised manuscript, and in-depth analysis has been included in the Supplementary Results. As this section has already been cited in a previous response (due to its logical connection with the functional analysis of the new species), we will not cite it again here. Please refer to the previous answer for further details.

-While associations between microbes and diseases were found, the study design cannot establish causal relationships. Are the authors planning to test some of the associations experimentally and see whether these observations work in vitro or in vivo?

We agree that elaboration of causal relationships is crucial. However, this was beyond the scope of the current study, which is intended as a foundational step for future investigations. However, the samples are stored in the Estonian Biobank in a way that allows culturomic studies and follow-up experiments as done by Krigul et al [1].

Krigul KL, Feeney RH, Wongkuna S, Aasmets O, Holmberg SM, Andreson R, Puértolas-Balint F, Pantiukh K, Sootak L, Org T, Tenson T, Org E, Schroeder BO. A history of repeated antibiotic usage leads to microbiota-dependent mucus defects. Gut Microbes. 2024 Jan-Dec;16(1):2377570. doi: 10.1080/19490976.2024.2377570.

Minor comments:

• The authors could provide more context on how their findings compare to similar studies in other populations. What are the differences and similarities, and how does this work at the next level and set new directions?

We thank the Reviewer for this suggestion. We provided a summary of other population cohorts in the Introduction (Lines 79–90). Since MAG recovery from large cohorts is a relatively new approach, there are limited opportunities for direct comparison. However, we did note a decreasing number of newly recovered species in our study compared to previous studies (Lines 274–290).

• Figures' quality and readability can be improved easily; all of them are low resolution, and the axes are hardly visible, particularly Figure 2, which could benefit from additional labeling or explanations in the legend to improve clarity.

We apologize for the quality issues with the figures. We completely revised Figure 2 to improve clarity and placed a new higher-resolution version of Figure 2 to improve readability, ensuring that axes and details are clearly visible.

Summary of performed changes: (1) we introduced a new Figure 2a to showcase the phylogenetic diversity of the recovered species and highlight the position of the newly assembled species identified for the first time in this study (2) We have updated Figure 2b. In the initial figure, a single line was presented. However, to enhance the visualization and emphasize the trend, five lines were subsequently plotted by altering the order of the samples. Since the order of the samples is not significant, this modification allows for a clearer representation of the overall trend of accumulation of the new species (3) we added new Figure 2c, to address the question about the range of diversity of detected species (4) we moved Figure 2a and 2d to Supplementary Figures to enhance clarity and relevance (Figure S4 and Figure S6 respectively).

“Figure 2. Overview of species from the EstMB MAG collection a. Phylogenetic tree of the Estonian species representative MAGs. The inner circle displays a phylogenetic tree of species cluster representative MAGs, with branches colored according to their assigned phylum in the Genome Taxonomy Database (GTDB) (see color text). The surrounding ring highlights MAGs that represent novel species assembled in the current study, using the same colors as in the inner circle to indicate the phylum to which each new species belongs (see color text). b. The relationship between the number of samples analyzed and the cumulative number of new species identified c. Distribution of number of species detected by mapping per sample “species hits” (yellow color violinplot) and number of recovered MAGs per sample (blue color violinplot) from Estonian representative MAGs number. d. Number of recovered species (blue color dots) and species detected by mapping the reads against the EstMB MAG collection (yellow color dots) for each sample. Samples are sorted from those with the highest to the lowest number of recovered MAGs e. __The prevalence and number of recovered MAGs per species. The top 10 species with the highest number of recovered MAGs are shown. Blue bars represent the number of samples where MAG of the species were recovered, while gray bars show the species prevalence in EstMB __f. The prevalence and number of recovered MAGs per new species. The top 10 new species with the highest number of recovered MAGs are shown. Green bars represent the number of samples where MAG of the new species were recovered, while gray bars show the new species prevalence.”

-A brief discussion on the potential clinical implications of the new species-disease associations would enhance the relevance. Why discovering new species are in testing and relevant for the microbiome field? Can authors add this somewhere, discussion?

We thank the Reviewer for this suggestion. As such, the following section was integrated in the Discussion on page 8 in the revised version of the manuscript:

“Reconstruction of a new species and new strain is critical for many aspects of personal medicine. We can identify three primary applications of the microbiome in personalized medicine: disease risk assessment and prevention, disease diagnosis, and disease treatment. The latter includes approaches such as microbial supplementation, suppression, or metabolite modulation [Karina Ratiner, 2024]. Both disease prevention and diagnosis rely on identifying bacterial biomarkers associated with prevalent or incident disease cases. In our study, an average of 4% of reads belonged to the newly identified species, with a maximum of 34.76%, demonstrating that excluding this species would lead to a significant loss of community diversity. This omission could potentially exclude biomarkers critical for disease prediction and diagnosis. Notably, one-third of the associations between bacterial species and diseases in our analysis involved the newly identified species, further emphasizing its potential importance as a biomarker. For disease treatment, it is crucial to understand the complete microbial diversity to distinguish between beneficial and harmful species. Equally important is knowing the genomic structure of species and strains to develop effective strategies for microbiome modulation. Without genome assembly, we are limited to assumptions based on previously described genomes of related bacteria. However, given the substantial genomic diversity within species, such assumptions may be highly inaccurate, underscoring the importance of genome assembly in advancing microbiome-based interventions.”

• In lines 265-266, the authors discuss detected species per sample, on average, 389 species. Can the authors guide which plot is linked to it and whether it is possible to show the disturbing median number of species per sample to get an overall idea about the range of diversity this type of analysis can capture now? Maybe this will improve in the future; it is worth mentioning here.

We thank the Reviewer for highlighting the need for the clarification. Original Figure 2c displayed the number of species detected through mapping (species hits) and the number of assembled MAGs for each individual sample. To provide a broader characterization of the distribution, we calculated the minimum, mean, median, and maximum values across all samples. As such, the __new Figure 2c __and the following section was integrated in the paragraph “Estimation of species prevalence using population-specific reference” on page 5 in the revised version of the manuscript:

“Distribution of the number of species detected by mapping per sample exhibits a wide range of values, with a maximum of 842 and a minimum of 7, while the mean and median are 399 and 405, respectively. The distribution of numbers of recovered MAGs per sample shows a narrower range, with a maximum of 155 and a minimum of 1, alongside a mean of 45 and a median of 41 (Figure 2c).”

Figure 2c.* Distribution of number of species detected by mapping per sample “species hits” (yellow color violinplot) and number of recovered MAGs per sample (blue color violinplot). *

Other comments:

-The key conclusions are generally convincing. The authors have successfully assembled a large number of MAGs from the Estonian population, identified potentially novel species, and established associations between microbial abundance and diseases.

We appreciate the Reviewer's positive feedback on our findings. We are pleased that the significance of our MAG assembly, novel species identification, and disease associations is well-received.

-The data presented appear to support the claims well. However, the authors should emphasize and clarify that the disease associations are correlational, not causal, and further validation is required.

We agree that this is an important point to emphasize. We revised the manuscript to clarify that the disease associations are correlational and emphasize the need for further validation by adding the following section in Discussion on page 8 in the revised version of the manuscript:

“While association does not imply causation, analyzing the association between bacterial species and diseases is a crucial first step in identifying potential biomarkers. This can be followed by meta-analyses across different cohorts and laboratory experiments to validate and confirm the observed effects.”

-Even though I am not an expert in metagenomics analysis, the current experimental design and analysis are sound to support the main claims.

We thank the Reviewer for recognizing the robustness of our experimental design and analysis.

-The methods section can be improved by providing more details about how samples were collected and stored and how long after storage gDNA was extracted and processed for sequencing, allowing for reproducibility. The authors provide information on the bioinformatics pipelines, including software versions and parameters, but this can again be improved by adding details about the steps between sample processing and raw data processing.

We thank the Reviewer for this suggestion and we agree that this is important information. All these details were thoroughly described in our previous paper, which focuses on our cohort description (Aasmets, O., Krigul, K.L., Lüll, K., Metspalu, A., and Org, E. (2022). Gut metagenome associations with extensive digital health data in a volunteer-based Estonian microbiome cohort. Nat. Commun. 13, 869.

https://doi.org/10.1038/s41467-022-28464-9).

However, to improve accessibility of this information, the following paragraph was integrated in the Methods on page 17 in the revised version of the manuscript:

“Microbiome sample collection and DNA extraction

The participants collected a fresh stool sample immediately after defecation with a sterile Pasteur pipette and placed it inside a polypropylene conical 15 mL tube. The participants were instructed to time their sample collection as close as possible to the visiting time in the study centre The samples were stored at −80 °C until DNA extraction. The median time between sampling and arrival at the freezer in the core facility was 3 h 25 min (mean 4 h 34 min) and the transport time wasn’t significantly associated with alpha (Spearman correlation, p-value 0.949 for observed richness and 0.464 for Shannon index) nor beta diversity (p-value 0.061, R-squared 0.0005). Microbial DNA extraction was performed after all samples were collected using a QIAamp DNA Stool Mini Kit (Qiagen, Germany). For the extraction, approximately 200 mg of stool was used as a starting material for the DNA extraction kit, according to the manufacturer’s instructions. DNA was quantified from all samples using a Qubit 2.0 Fluorometer with a dsDNA Assay Kit (Thermo Fisher Scientific).”

-The study includes a large cohort (1,878 samples), which provides statistical power. The statistical analyses, including linear regression models adjusted for BMI, gender, and age, seem appropriate for the type of data presented. I suggest adding a separate paragraph about how the data is processed and statistically analyzed.

Authors should include:

• Appropriateness of the statistical tests used for the data types and experimental designs

• Adequate description and justification of the statistical models and test and assumptions

• Proper handling of replicates, controls, and data normalization

• Reporting of effect sizes, sample size, confidence intervals, and statistical power

• Data processing and analysis workflows.

We thank the Reviewer for this recommendation. To highlight the statistical analysis carried out, we have made a separate paragraph for statistical analysis under the Methods section (lines 617-628). We note that we have previously described data processing and normalization. This study has an exploratory nature. Hence, the power calculations are not applicable, but this study can be an input for the power calculations of future studies testing statistical hypotheses. However, we agree that the sample sizes for each phenotype and beta estimation would support our results. We have now added them to __Table 1_. _ __

Reviewer #1 (Significance (Required)):

---

-This study represents an advance in the context of population-specific studies. Creating a comprehensive Estonian population-specific MAG reference and identifying new species contribute to our understanding of microbiome diversity.

-The work builds upon previous large-scale microbiome projects, such as those that established the Unified Human Gastrointestinal Genome (UHGG) collection but focuses on a specific population.

-The associations between microbial species (including novel ones) and common diseases provide potential avenues for future research into microbiome-based diagnostics or therapeutics.

-The findings would interest microbiome researchers, bioinformaticians, and clinicians interested in the role of the gut microbiome in health and disease.

We thank the Reviewer for the thoughtful feedback and recognition of our study's contributions to microbiome research. By creating an Estonian population-specific MAG reference and identifying new species, we advance population-specific studies and enhance global microbiome diversity. Building on projects like UHGG, we integrate local data into the global context and highlight potential applications in microbiome-based diagnostics and therapeutics. To address your suggestions, we expanded the results section with an example from the Butyricimonas genus. We hope our publicly available data will support future research and further advance understanding of the gut microbiome in health and disease.

__ Reviewer #2 (Evidence, reproducibility and clarity (Required)):__

---

The manuscript by Pantiukh et al. presents the collection of MAGs assembled from the Estonian Biobank, with a specific focus on the novel species clusters the authors defined and found associations with some of the diseases as collected among the samples available in their biobank. The manuscript is well organized. However, it lacks a bit in terms of novelty and also some statements that can mislead the readers to overinterpret some parts.

Majors

• The last paragraph of the introduction (lines 91-98) anticipates some results but lacks some methodological details. Please consider whether to move it to the results section or add very brief specifications, like (1) "sequence with deep coverage" is vague, how deep is deep? (2) "84,762 MAGs representing 2,257 species" are the 84k MAGs already quality-controlled? (3) "353 MAGs (15,6%) of the EstMB MAGs collection to represent potentially novel species." 353 are MAGs or species? As species clusters are defined later at 95% ANI, are all these 353 defining their own species clusters?

We thank the Reviewer for insightful questions and suggestions. To address these points, we have added the following clarifications to the text:

We specified the depth of coverage for sequences, providing an average reads number per sample - 56 mln reads. (Lines 92). We clarified that among 84,762 assembled MAGs, 42,049 MAGs (49.60 %) were high-quality (HQ) MAGs. (Lines 93-94). We revised the statement about the 353 MAGs, explicitly noting that they represent potentially novel species. Additionally, we clarified that all 2,257 representative MAGs, including these 353 new species MAGs represent separate species clusters based on the 95% ANI threshold mentioned later in the text. (Lines 94-98).

In the paper, we included only the figure showing the quality group distribution for species cluster representative MAGs to avoid potential confusion between two similar figures: one for all assembled MAGs (n=84,762) and another for cluster representative MAGs (n=2,257). However, in response to this query, we have added a new __Supplementary Figure S1__that illustrates the quality group distribution for all assembled MAGs to provide a more comprehensive view.

Figure S1. Quality estimation for the assembled MAGs (n=84,762). High-quality MAGs (HQ) – 42,049; Medium-quality MAGs (MQ) – 26,806; Low-quality MAGs (LQ) – 15,907.

• lines 109 and 265, "11.73 +/- 3.9 Gb data per sample and 56.13 +/- 19.37 million reads per sample", numbers don't match... 11.73 Gbp is about 78M reads at 150nt read length, plus later the average depth is not 56.13 but 53.04, please double check these numbers

We apologize for any misunderstanding. The numbers mentioned in the paper refer to the number of reads and the file size of each compressed *.fasta.gz file. This file size does not directly represent the total base pairs (Gb) for the current metagenome. Instead, it reflects the disk space occupied by the compressed sequencing data, including additional information such as sequence headers. We selected this parameter to provide an easy point of comparison with file sizes from other metagenome sequencing datasets, as *.fasta.gz is a commonly used format for storing sequence data. To clarify further, here is an example of the relationship between these parameters for one sample:

Sample XX

Value

Meaning

Program

Compressed file size

4.2 GB

Represents disk space occupied by the compressed sequencing data. This applies to forward reads only; for a rough estimation of the disk space for both forward and reverse reads, it should be multiplied by 2 or calculated separately for both files.

du -sh V00HXZ.fq1.gz

The total number of reads

41,062,933 reads

(avg. read len = 147.7 bp)

Represents number of forward reads. This applies to forward reads only; for a rough estimation of both forward and reverse reads, it should be multiplied by 2 or calculated separately for both files.

seqkit stats V00HXZ.fq1.gz -a -T

Total base pairs (Gb)

6,066,493,002 bp (6.07 Gb)

Represents total base pairs (Gb) for the current sample. This applies to forward reads only; for a rough estimation of both forward and reverse reads, it should be multiplied by 2 or calculated separately for both files.

seqkit stats V00HXZ.fq1.gz -a -T

We now realize this may have caused confusion. To address this, we have calculated the total base pairs (Gb) parameter for both forward and reverse reads and exchanged the __Compressed file size __number to __Total base pairs__with following section in the paragraph “Cohort overview and study design” on page 3 in the revised version of the manuscript:

“The EstMB-deep samples were resequenced at deep coverage, generating an average of 16.49 ± 6.2 Gb of total base pairs per sample, or 56.13 ± 19.37 million paired reads per sample, with an average forward read length of 146.85 bp and an average reverse read length of 147.01 bp.”

• line 118, "completeness > 90% and contamination We thank Reviewer for this comment, we use CheckM v2 for evaluation MAG completeness and contamination. We have incorporated the requested information into the manuscript. (Lines 128).

• line 120, "84,762 MAGs were clustered at the species level with an average nucleotide identity (ANI) threshold of 95%.", as for my previous comment, either specify the Methods or quickly mention the tool used for the ANI analysis.

We use dRep with default parameters for clustering. We have incorporated the requested information into the manuscript. (Lines 130).

• lines 135-138, "The bacterial species most represented in our MAGs collection were Odoribacter splanchnicus (MAG recovered from 70.93% samples), Barnesiella intestinihominis (62.83%), Parabacteroides distasonis (60,38%), Alistipes putredinis (54,53%) and Agathobacter rectalis (51.92%) (Figure S2, Table S2).", it will be interesting to compare (some of) these speceis with other populations, to see if these species are globally prevalent in the human gut microbiome or specific to the Estonian population.

We thank the Reviewer for this question. As highlighted in Figures 4e and 2d, the number of MAGs recovered for a given species often differs significantly from its prevalence in the population. Due to the complexities of MAG assembly, species prevalence is generally much higher, and these values do not correlate linearly, as shown in Supplementary Figure S5. Keeping in mind that species with the higher number of assembled MAGs are not the same as species with the higher prevalence, we compared our top assembled species with the most comprehensive up to date USGG collection of gut bacteria and integrated the following section in the paragraph “Population-specific Metagenome-Assembled Genomes (MAGs) reference” on page 4 in the revised version of the manuscript:

“... All these species are also well-represented in other cohorts. For example, Parabacteroides distasonis, Alistipes putredinis, and Agathobacter rectalis rank among the top 6 species in the USGG by the number of genomes. Additionally, Barnesiella intestinihominis and Odoribacter splanchnicus rank among the top 40 species out of a total of 4,644 species in the USGG database.”

• lines 143-144, "MAGs, 353 MAGs (15,64%) represent a new species according to the GTDB criteria.", these 353 MAGs might define fewer species clusters, I think the 'species' word in this sentence is misleading and can lead to an overinterpretation of the diversity, it will be more correct to report how many species clusters these MAGs defined.

We apologize for not providing sufficient clarification. In our case each cluster represented a new distinct species. We added clarification in lines 152-153.

• lines 163-168, the paragraph could be an overinterpretation, as it is unlikely that there is 'infinite' diversity, so it could be that by doubling the samples, there is already a plateau in terms of novel species clusters identified. I think this paragraph should be reconsidered.

We thank the Reviewer for this question. We have updated Figure 2b. Instead of presenting a single version of the cumulative sum of new species discoveries, we reordered the samples five times to provide a more accurate approximation of new species accumulation as the number of samples increases. Additionally, we integrated the following section in the paragraph “Novel species and comparison of the population-specific reference with global reference UHGG” on page 4 in the revised version of the manuscript:

“Our analysis so far shows a clear linear trend without indication of a plateau (although we can not exclude that plateau had been reached exactly at current sample size, which may not yet be evident).”

__Figure 4b. __The relationship between the number of samples analyzed and the cumulative number of new species identified.

• lines 182-184, "Even species which have been recovered from a large number of samples can be found in significantly more samples after mapping (Figure 2e, Table S2).", this is not novel as assembly requires higher coverage than calling a species present via mapping, please, rephrase this part.

We thank the Reviewer for this thoughtful suggestion. We included this point in the article not because of its novelty but to emphasize that even a small number of recovered MAGs per sample can still hold significant value. This is because despite a small number of assembled genomes, the same species prevalence, as detected through mapping, can still be substantial which makes it possible to use them for, for example, association study. We added this perspective based on our personal experience of initial disappointment with the small number of MAGs recovered for many new species clusters. Our intention is to prevent similar discouragement among other researchers who may begin recovering MAGs from their large population cohorts.

• lines 185-188, "which are usually extracted from a small number of samples, 185 show a prevalence exceeding 80% for some species. For example, Bacteroides faecalis has a prevalence of 97.23%, although only 1 MAG was assembled, and Bacteroides intestinigallinarum has a prevalence of 95.85% although only 2 MAGs were assembled.", this should be much better contextualized and discussed in terms of relative abundance and not only on the ability to reconstruct (which is highly impacted by coverage, which is a proxy for abundance) with its prevalence, it is known in the field that there are very highly prevalent species at very low abundance values, which are not that often reconstructed via metagenomic assembly.

We agree that understanding the causes of assembly complications is important in the field, with abundance playing a key role. Moreover, other factors such as the presence of closely related species with similar genomes or multiple strains of the same species within a sample can significantly impact assembly, even for species with high abundance. However, since this paper focuses on the potential applications of MAG assembly in large population cohorts rather than the technical aspects of assembly, our main goal was to emphasize that MAGs assembled from the samples should not be used to estimate species prevalence.

• Data availability, it appears that the provided accession number does not exist, please double-check this.

We apologies about that issue, data now available with provided accession number PRJEB76860:

Minors

• line 106, "includes 1,308 women (69.64 %) and 570 men (30.35 %)", these sums up to 99.99%, the ratio for women is 1308/1878=0.69648, so can be rounded up to 69.65%.

We thank the Reviewer for this correction. We correct numbers from 69.64% to 69.65% (Lines 114).

• line 293, "ones[Philip Hugenholtz, 2008].", citation to fix.

Thank you for the correction. We corrected the links. (Lines 414).

• Fig. 1g, why completeness is up to 25%, from the text it seemed the MAGs were screened for completeness We apologize for not providing sufficient clarification. Indeed, as noted in Lines 124-126, *"We successfully reconstructed 84,762 metagenome-assembled genomes (MAGs), an average of 45 MAGs per sample. Among these, 42,048 according to CheckM, MAGs (49.6%) have completeness > 90% and contamination 90% and contamination 50% and contamination (Lines 131-132).

• Fig. 2f says "Blue bars represent", but I believe it should be green instead of blue.

Thank you for the correction. We corrected the color.

(Lines 520).

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The manuscript by Pantiukh et al. presents the collection of MAGs assembled from the Estonian Biobank, with a specific focus on the novel species clusters the authors defined and found associations with some of the diseases as collected among the samples available in their biobank. The manuscript is well organized. However, it lacks a bit in terms of novelty and also some statements that can mislead the readers to overinterpret some parts.

Majors

• The last paragraph of the introduction (lines 91-98) anticipates some results but lacks some methodological details. Please consider whether to move it to the results section or add very brief specifications, like (1) "sequence with deep coverage" is vague, how deep is deep? (2) "84,762 MAGs representing 2,257 species" are the 84k MAGs already quality-controlled? (3) "353 MAGs (15,6%) of the EstMB MAGs collection to represent potentially novel species." 353 are MAGs or species? As species clusters are defined later at 95% ANI, are all these 353 defining their own species clusters?
• lines 109 and 265, "11.73 +/- 3.9 Gb data per sample and 56.13 +/- 19.37 million reads per sample", numbers don't match... 11.73 Gbp is about 78M reads at 150nt read length, plus later the average depth is not 56.13 but 53.04, please double check these numbers
• line 118, "completeness > 90% and contamination < 5%", please specify either the Methods section or briefly which tool was used to estimate quality.
• line 120, "84,762 MAGs were clustered at the species level with an average nucleotide identity (ANI) threshold of 95%.", as for my previous comment, either specify the Methods or quickly mention the tool used for the ANI analysis.
• lines 135-138, "The bacterial species most represented in our MAGs collection were Odoribacter splanchnicus (MAG recovered from 70.93% samples), Barnesiella intestinihominis (62.83%), Parabacteroides distasonis (60,38%), Alistipes putredinis (54,53%) and Agathobacter rectalis (51.92%) (Figure S2, Table S2).", it will be interesting to compare (some of) these speceis with other populations, to see if these species are globally prevalent in the human gut microbiome or specific to the Estonian population.
• lines 143-144, "MAGs, 353 MAGs (15,64%) represent a new species according to the GTDB criteria.", these 353 MAGs might define fewer species clusters, I think the 'species' word in this sentence is misleading and can lead to an overinterpretation of the diversity, it will be more correct to report how many species clusters these MAGs defined.
• lines 163-168, the paragraph could be an overinterpretation, as it is unlikely that there is 'infinite' diversity, so it could be that by doubling the samples, there is already a plateau in terms of novel species clusters identified. I think this paragraph should be reconsidered.
• lines 182-184, "Even species which have been recovered from a large number of samples can be found in significantly more samples after mapping (Figure 2e, Table S2).", this is not novel as assembly requires higher coverage than calling a species present via mapping, please, rephrase this part.
• lines 185-188, "which are usually extracted from a small number of samples, 185 show a prevalence exceeding 80% for some species. For example, Bacteroides faecalis has a prevalence of 97.23%, although only 1 MAG was assembled, and Bacteroides intestinigallinarum has a prevalence of 95.85% although only 2 MAGs were assembled.", this should be much better contextualized and discussed in terms of relative abundance and not only on the ability to reconstruct (which is highly impacted by coverage, which is a proxy for abundance) with its prevalence, it is known in the field that there are very highly prevalent species at very low abundance values, which are not that often reconstructed via metagenomic assembly.
• Data availability, it appears that the the provided accession number does not exist, please double-check this.

Minors

• line 106, "includes 1,308 women (69.64 %) and 570 men (30.35 %)", these sums up to 99.99%, the ratio for women is 1308/1878=0.69648, so can be rounded up to 69.65%.
• line 293, "ones[Philip Hugenholtz, 2008].", citation to fix.
• Fig. 1g, why completeness is up to 25%, from the text it seemed the MAGs were screened for completeness <5%. Like in panel f for contamination that is never below 50%.
• Fig. 2f says "Blue bars represent", but I believe it should be green instead of blue.

Significance

General assessment: the manuscript presents a large-scale effort to reconstruct microbial genomes from metagenomes present in the Estonian biobank. This can be very useful in future analyses, as the knowledge of novel and population-specific species can improve future studies linking diseases with the microbiome data. However, the analyses presented are quite limited and also do not provide the perspective of how these newly reconstructed genomes will be integrated into public databases that can improve future microbiome profiling (both at the taxonomic and functional levels).

Advance: the manuscript presents an incremental advancement in the field, and with the limited data made available (the provided accession number was not found in the mentioned database, and only representative MAGs were deposited), it is difficult to assess how much this data can be a resource for the research community.

Audience: the audience targeted at the moment is specialized people in microbiome analysis and in particular those that are focusing on the analysis tools development (like UGG and GTDB)

Microbiome expert.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

In this paper "Metagenome-assembled genomes of Estonian Microbiome cohort reveal novel species and their links with prevalent diseases", the authors present a comprehensive analysis of metagenome-assembled genomes (MAGs) from the Estonian Microbiome cohort, offering several key insights and contributions to microbiome research. The authors assembled 84,762 MAGs from stool samples of 1,878 individuals in the Estonian Microbiome Cohort, representing 2,257 species. Notably, they identified 353 potentially novel species (15.6%) and 607 species (26.9%) not present in the global Unified Human Gastrointestinal Genome (UHGG) reference database.

Work is timely and important for several reasons:

• It aligns with the growing trend of population-specific microbiome studies, which are crucial for understanding regional variations in gut microbiota.
• Finding new bacterial species and population-specific microbes contributes to the expanding catalog of human-associated microorganisms.
• The associations between microbial species and common diseases provide potential avenues for future research to test those ideas into microbiome-based diagnostics or therapeutics.

Strengths:

• The study provides a valuable population-specific reference for the Estonian gut microbiome, which can enhance the accuracy of future microbiome studies in this population.
• Identifying potentially new bacterial species contributes to our understanding of microbial diversity.
• This work uncovered associations between bacterial abundance and 15 common diseases, including links with potentially new species.
• The study combined deep metagenomic sequencing with extensive phenotypic data, allowing for a more rounded analysis. The paper's focus on an Estonian population and the creation of a population-specific reference set it apart from global microbiome studies. This approach allows for detecting microbial species that need to be included in more general studies.

Drawbacks:

• While the population-specific approach is a strength, it also limits the direct applicability of findings to other populations.
• The study primarily focuses on taxonomic composition at the genus or species level, but a more in-depth functional analysis of the novel species could provide additional insights.
• Is it possible for this large dataset to distill information and have plots for strain diversity of abundant and prevalent species, including low abundance species per donor or between donors? Can authors add such a plot or discuss this? While associations between microbes and diseases were found, the study design cannot establish causal relationships. Are the authors planning to test some of the associations experimentally and see whether these observations work in in vitro or in vivo?

Minor comments:

• The authors could provide more context on how their findings compare to similar studies in other populations. What are the differences and similarities, and how does this work at the next level and set new directions?
• Figures' quality and readability can be improved easily; all of them are low resolution, and the axes are hardly visible, particularly Figure 2, which could benefit from additional labeling or explanations in the legend to improve clarity.
• A brief discussion on the potential clinical implications of the new species-disease associations would enhance the relevance. Why discovering new species are in testing and relevant for the microbiome field? Can authors add this somewhere, discussion? In lines 265-266, the authors discuss detected species per sample, on average, 389 species. Can the authors guide which plot is linked to it and whether it is possible to show the disturbing median number of species per sample to get an overall idea about the range of diversity this type of analysis can capture now? Maybe this will improve in the future; it is worth mentioning here.

Other comments:

• The key conclusions are generally convincing. The authors have successfully assembled a large number of MAGs from the Estonian population, identified potentially novel species, and established associations between microbial abundance and diseases.
• The data presented appear to support the claims well. However, the authors should emphasize and clarify that the disease associations are correlational, not causal, and further validation is required.
• Even though I am not an expert in metagenomics analysis, the current experimental design and analysis are sound to support the main claims.
• The methods section can be improved by providing more details about how samples were collected and stored and how long after storage gDNA was extracted and processed for sequencing, allowing for reproducibility. The authors provide information on the bioinformatics pipelines, including software versions and parameters, but this can again be improved by adding details about the steps between sample processing and raw data processing.
• The study includes a large cohort (1,878 samples), which provides statistical power. The statistical analyses, including linear regression models adjusted for BMI, gender, and age, seem appropriate for the type of data presented. I suggest adding a separate paragraph about how the data is processed and statistically analyzed. Authors should include:
• Appropriateness of the statistical tests used for the data types and experimental designs
• Adequate description and justification of the statistical models and test and assumptions
• Proper handling of replicates, controls, and data normalization
• Reporting of effect sizes, sample size, confidence intervals, and statistical power
• Data processing and analysis workflows

Significance

• This study represents an advance in the context of population-specific studies. Creating a comprehensive Estonian population-specific MAG reference and identifying new species contribute to our understanding of microbiome diversity.
• The work builds upon previous large-scale microbiome projects, such as those that established the Unified Human Gastrointestinal Genome (UHGG) collection but focuses on a specific population.
• The associations between microbial species (including novel ones) and common diseases provide potential avenues for future research into microbiome-based diagnostics or therapeutics.
• The findings would interest microbiome researchers, bioinformaticians, and clinicians interested in the role of the gut microbiome in health and disease.

My Expertise:

Gut microbiome, gut microbiota resilience, ecology, and evolution in microbial communities, antimicrobial resistance, high-throughput drug-bacteria interactions

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Manuscript number: RC-2024-02535

Corresponding author(s): Modica, Maria Vittoria

1. General Statements [optional]

We are grateful to the reviewers for their detailed evaluation and insightful comments on our manuscript, which has led us to introduce several clarifications, expand a few issues initially underscored, and amend some incongruencies.

We have been able to incorporate changes to reflect most of the suggestions provided by the reviewers, as highlighted in the main text. Most of the additional analyses proposed by the reviewers were carried out, in some cases providing interesting insights that were included in the manuscript, while in others revealed not conclusive, as detailed below.

We believe that the congruence and readability of the manuscript has been overall improved, and we are confident that our responses align with the level of detail required by the reviewers

• *

2. Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

* Summary: The manuscript by Modica et al reports characterisation of the venom system in the white sea fan Eunicella singularis, a species of an octocorallian coral. E. singularis is common in the north-western Mediterranean sea. The authors used a proteo-transcriptomic approach followed by extensive bioinformatics analysis. Specifically, they generated a new E. singularis *transcriptome and characterised extracts from nematocysyts (venom-bearing structures) and whole body using tandem mass spectrometry. Toxins were identified by HMMER using Tox-prot and VenomZone databases as queries as well as ClanTox web server.

Major comments:

As far as I am aware, venom production by ectodermal gland cells has been reported only in sea anemones (Moran et al, 2011), therefore it is unclear whether it is the case in the octocorallian sea fan as well. Additionally, cnidarian toxin-like proteins might be produced by neurons (Sachkova et al, 2020) or involved in development (Surm et al 2024). Thus, it is probable that in E. singularis not all the toxin-like proteins found in the whole body proteome and missing from the nematocyst proteome are venom components. Thus, additional experiments would be required to localise those proteins to ectodermal gland cells. I suggest to mention this limitation and refer to such proteins as "toxin-like" or "putative toxins".

• *

We thank the Reviewer for this observation, which is indeed correct. We have modified the text according to this suggestion and we have added a cautionary statement to the analysis section.

In addition to submitting proteomics data to PRIDE, it would be helpful for readers/reviewers to provide a supplementary excel file with all the peptides and proteins identified by PEAKS Studio. I could not access the data on PRIDE as I think they still have not been assigned a PXD dataset identifier.

Excel files with both proteomes have now been provided as supplementary material (Suppl tab. 2 and 3).

* *Minor comments:

It would be helpful for readers to split the Results and Discussions into smaller subsections with headings, perhaps according to the identified toxin families. It would be also helpful to provide a summary figure with all the toxins identified and perhaps toxin expression levels. Especially showing cysteine patterns for new toxins would be very useful.

Wherever possible, Results and Discussions were split into subsections according to toxin families, following reviewer’s suggestion.

Figure 2.C summarizes the identified toxin families along with the number of validated sequences for each of them. We provided an excel file with the sequences and expression levels of the identified toxins as supplementary table 2. We have now added a column with cysteine patterns to better define and characterize these toxins

It is unclear why the Toxin annotation pipeline is hidden in the supplementary material. It would be also helpful to show it as a schematic pipeline in the main text.

We have prepared a figure describing the annotation pipeline that is now provided as Fig.1 in the main text.

The identification of proteolytic cleavage sites is not really described. It would be also helpful to mark them at the Figure 2.

We have adjusted the Methods section in the Supplementary Material to give a clearer explanation of the methods applied to identify putative cleavage sites. The figure (now Fig. 3) has been adjusted to include the protease recognition site.

"Other peptides present in E. singularis nematocysts and displaying protease inhibitory domains, but likely lacking a toxin function (Kazal-type, cystatines, antistasins, and macins)..." - why do they likely lack a toxin function? what is the rational behind this statement?

• *While we were referring to a strictly neurotoxic function, the statement is indeed misleading and was removed from the amended text and modified as follows “Other peptides present in E. singularis nematocysts displaying protease inhibitory domains (Kazal-type, cystatines, antistasins, and macins) were detected but did not present novelty elements. Their sequences are described in supplementary data.”

"cell- or tissue-specific differential maturation patterns" - I think the differential maturation needs to be confirmed by additional experiments to exclude a possibility of being an artifact due to low mass spectrometry sensitivity.

This is indeed true. Nonetheless, our proteomic analyses provided quite convincing evidence of this phenomenon. Figure 3 in the manuscript summarizes the output of our PEAKS studio analyses, but for clarity we reported as Suppl. Fig. 1 the original output for the identification of U-GRTX-Esi2a/b.In the figure, each blue line below the precursor sequence denotes a peptide that was confidently identified by LC-MS/MS. As visible, several peptides were identified for this protein in either proteome, but there is a clear pattern pointing toward the complete absence of the first domain in the NEM-P. The Reviewers have rightfully raised concerns that, given the ethanol extraction protocol employed, our NEM-P may be partial and/or contaminated by other extracted proteins. This is true, and in fact we have added cautionary statements throughout the text. It is reasonable to assume, though, that proteins with similar sequence and physicochemical features, like U-GRTX-ESI-2a and 2b, will respond similarly to the ethanol extraction procedure. If present, we believe the first domain (U-GRTX-ESI-2a) should have produced some detectable peptide also in the NEM-P. This seems even more reasonable if we consider that the WB-P contained a much higher number of proteins, which could have led to the loss of detection of some peptides due to instrument settings. With the due caution, we believe it is reasonable to leave our claim in the manuscript, supporting it by adding the Suppl. Fig.1.

"three consecutive ShK domains with peculiar characteristics (Suppl. Fig. 2)" - what are these characteristics?* *

This has been better clarified in the text which now reads “Only the C-terminal domain has the typical ShKT cysteine pattern, whereas the first two domains present an unusual shift of the C-terminal cysteine. None of the domains of U-GRTX-Esi4 presents the key Lys residue necessary for binding KV1.2 and KV1.3, while the subsequent Tyr residue, also important for binding KV1, is extremely conserved”. The reference figure is now Suppl. Fig. 3.

Fig. S1 legend: "Octocorallia (cyano bar) and Hexacorallia (blue bar)" - the bars look pink and cyan.* *

*The figure (now Suppl. Fig. 2) was modified in order to fix this issue. *

* *Referee cross-commenting

I agree with both reviewers that additional validation of the ethanol extraction method would be required to confirm its specificity and efficiency. Since ethanol is widely used for tissue fixation, I would guess that it is improbable that it leads to disruption of other coral cell types in addition to discharging nematocytes. However, to be 100% sure that would need to be confirmed experimentally. I think the suggestion to use Xenia single cell dataset to validate the nematocyst proteome reported in this paper is really worth trying. However, toxin-like genes in cnidarians might be recruited to non-venom cell types (Sachkova et al, 2020; Surm et al 2024) therefore if a gene is nematocyte-specific in one species it does not mean it would the same in another one, especially if they are distantly related. Thus, the best would be to run some additional experiments in Eunicella singularis, if the tissue is available.

We have received this concern and addressed it by rephrasing the text. We have also performed the requested check with Xenia nematocysts single cell data set. In detail, we recovered 243 high-confidence single-copy orthologs conserved between Xenia and E. singularis, which were described as belonging to cluster 11, associated to nematocytes by Hu and colleagues in their 2020 Nature article. We comparatively evaluated the abundance of the peptide fragments that could be mapped to the corresponding de novo assembled contigs in E. singularis whole-body and nematocyst proteomes, finding very little overlap, both with the whole-body, and with the nematocyst proteome. In detail, we found none of the sequences shared with Xenia cluster 11 in the NEM-P, while 16 sequences were retrieved in the WB-P. None of the latter corresponded to toxins, but rather possessed PFAM domains indicative of housekeeping functions.

We believe that these observations are not surprising, due to the following reasons:

(i) as we show in Figure 6, Xenia appears to display a highly divergent venom arsenal not just from Eunicella singularis, but also from all other Octocorallia. Consequently, we can hardly expect any of the main molecular components of the venom to display a 1:1 orthology between the two species. In addition, Xenia is a zooxanthellate species, obtaining most of its energy autotrophically and complementing with the absorption of particulated organic matter. Due to its trophic ecology, we do not expect this species to produce predatory venom.

(ii) although Xenia cluster 11 includes genes specifically expressed in the nematocysts, these do not necessarily encode venom components but also other cellular components from the nematocytes. In contrast, if successful, our approach would yield a fraction enriched in secretory products while other intracellular or membrane-bound proteins that are specifically expressed by nematocytes, are not expected to be particularly enriched in the NEM-P.

In addition, due to the remarkable divergence between these two species, not all Xenia nematocyte-specific transcripts are expected to retain the same specificity also in Eunicella.

Reviewer #1 (Significance (Required)):

This study reports venom composition of an octocoral for the first time. These data are very important for understanding biology and ecology of these animals as they rely on venom for feeding and deterring predators. This study is a significant advancement of the cnidarian venomics as most of the literature is limited to sea anemone and jellyfish venoms. This study will be interesting to the broad audience: venomics and coral ecology communities, evolutionary biologists and marine scientists. The main strength of this work is that it provides a comprehensive overview of the venom system in a widespread octocoral species with important ecological roles. The limitations of this study is that the toxicity and biological function of the identified venom components have not been confirmed experimentally. However, the localisation of the proteins to nematocysts is a very strong indication of being a venom component. My expertise: cnidarian venom (biochemistry, ecology and evolution).

*

*Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary: The authors of this work explore the venom repertoire of octocoral, a group of cnidarians whose venom has largely been ignored in the literature. As a first step into characterizing the venom of octocorals, the authors use a proteo-transcriptomic approach for Eunicella singularis, Specifically, they generated the transcriptome and proteome from whole-body as well as a more specific proteome of the nematocyst, a specialized sub-cellular structure found only in cnidarians and used to inject venom. The nematocyst proteome is a crucial dataset of the manuscript as it allows the authors to discriminate what is most likely a bona fide toxin compared to general physiological proteins.

* Major: However, I have some skepticism regarding the legitimacy of this nematocyst proteome. Specifically, the proteins from this are nematocyst-specific. The authors used an approach to soak the animal in ethanol, which theoretically should cause the nematocyst to fire, releasing the venom housed inside. This is a technique previously used in box jellyfish where they show that indeed the nematocyst have fired using histological approaches. However, this was not validated for Eunicella singularis*. I am hesitant to fully accept that the data from the nematocyst-proteome is specific. Other approaches, such as isolating nematocyst using a percoll gradient, will likely generate a more specific nematocyst proteome. This percoll gradient approach has been used to isolate nematocysts from different species of cnidarians ranging from hydra to sea anemones, however, I recognize that although this approach is robust for different cnidarians, acquiring enough material is challenging and maybe beyond the capacity for this octocoral. I would argue this would be the best approach, but if not feasible I can understand. However, other potential validation could be used to help improve the confidence that this is, at least mostly, nematocyst-specific. Furthermore, one could argue that this ethanol approach used in box jellyfish also specifically used tentacle, a tissue significantly enriched in nematocyst likely greatly improving the specificity in isolating nematocyst-specific proteins. whereas in this study they use a collection of whole polyps, therefore, anything that is extracted from the ethanol would precipitate. This is a much more complex collection of tissues which I would assume could interfere with isolating nematocyst-specific proteins

We thank the Reviewer for these comments. It is indeed true that there are cleaner procedures to extract venom from nematocysts. Preliminary attempts with electrical stimulation of colonies to milk the venom were also performed, but did not yield satisfactory peptide amounts for further analysis. We then decided to attempt ethanol extraction. As also noted by Reviewer #1, ethanol is routinely used for tissue fixation, and we think that it could have only limited effect on other cell types, therefore we assumed that most proteins in this extract had to come from nematocysts firing. While we cannot be sure that we fired all kind of nematocysts from E. singularis, the enrichment of the NEM-P in proteins with typical toxin features (i.e. signal peptide, small size, elaborate cysteines patterns), represented an indirect proof of this hypothesis. We believe this NEM-P may represent a good snapshot of venom components from E. singularis. On the other hand, it is true that the ethanol procedure may introduce some contamination. Indeed, we adopted a conservative approach and discussed in detail only the proteins with toxin-like features. At any rate, we have clearly stated the methodological limitations of our approach in the text and added cautionary statements through the manuscript.

* *A computational approach, that I think is essential, is to use the Xenia single-cell atlas. Xenia is also an octocoral with a nice single-cell atlas in which the cnidocytes form a distinct cluster. The authors can perform a reciprocal best-blast hit with the xenia genome and Eunicella singularis transcriptome and then see if gene-encoding proteins found in Eunicella nematocyst proteome have orthologs with genes found in the Xenia cnidocyte cluster. A statistical test could then be performed to show that there is a significant overlap between the nematocyst proteins from Eunicella and their orthologs in the Xenia cnidocyte cluster. This is still quite indirect but can give some insights. A better approach would be to perform proteomics from Xenia using the ethanol approach and mapping to see where the proteins captured are found in the atlas. This would massively elevate this work and provide proof that indeed this approach using ethanol is capable of precipitating nematocyst-specific proteins. I would strongly recommend trying to provide some evidence that this is indeed a nematocyst-specific protein, or at the least, is significantly enriched. Because this is unknown, many of the interpretations presented downstream are not well supported.

As previously stated in response to Reviewer #1, we have performed the requested check on Xenia nematocyte single cell data set. In detail, we followed the advice provided by the reviewer, extracting the protein sequences of the 432 Xenia genes included in cluster 11 from the work by Hu and colleagues, and recovered the nucleotide sequence of the assembled transcripts of 243 high-confidence 1:1 orthologs from E. singularis. In this process, we paid particular attention to excluding ambiguous matches, such as genes subjected to lineage-specific duplications, and therefore we exploited the availability of the annotated genome of the congeneric species E. verrucosa for the first step of orthology detection (performed through a reciprocal BLASTp approach). In the second step of the analysis, the corresponding assembled transcripts from E. singularis were identified with tBLASTn, assuming an inter-specific divergence This subset of putative nematocyst-specific sequences was subjected to an in-depth analysis, which comparatively evaluated the relative abundance of mapped peptide fragments in the whole-body and nematocyst proteomes. This process led to the identification of very little overlap between Xenia and E. singularis. We believe that these observations are not surprising, due to the following reasons:

(i) as we show in Figure 6, Xenia appears to display a highly divergent venom arsenal not just from Eunicella singularis, but also from all other Octocorallia. Consequently, we can hardly expect any of the main molecular components of the venom to display a 1:1 orthology between the two species. In addition, Xenia is a zooxanthellate species, obtaining most of its energy autotrophically and complementing with the absorption of particulated organic matter. Due to its trophic ecology, we do not expect this species to produce predatory venom.

(ii) although Xenia cluster 11 includes genes specifically expressed in the nematocysts, these do not necessarily encode venom components but also other cellular components from the nematocytes. In contrast, if successful, our approach would yield a fraction enriched in secretory products while other intracellular or membrane-bound proteins that are specifically expressed by nematocytes, are not expected to be particularly enriched in the NEM-P.

In addition, due to the remarkable divergence between these two species, not all Xenia nematocyte-specific transcripts are expected to retain the same specificity also in Eunicella.

Another major issue with the manuscript is the section referring to SCRiPs. First, the authors do not cite Jouiaei, Sunagar et al. (2015) which was the first publication to functionally characterize SCRiPs as toxins. Additionally, the majority of SCRiPs identified in this study and those found in Eunicella have a different cysteine framework. The authors acknowledge this online 245 but claim that, given the alphafold structure is similar, they are from the same gene family. First, I think this is very weak support as typically sharing a conserved cysteine framework is the bare minimum to categorize these toxins in a gene family. Although some cysteine frameworks are somewhat hard to resolve as the space between the cysteines can be variable, in this case, SCRiPs have a very distinct triple repeat of cysteines near the C terminal that is missing in these octocoral SCRiPs. These make me suspicious that these are indeed from the same gene family. Then relying on alphafold to predict the structure and claiming it's similar to Tau-AnmTx Ueq 12-1 from Urticina eques is also fairly weak support. Although I am not an expert in protein structures, I cannot tell from the images comparing the 2 structures in the supplementary figure s1 that these are similar. Perhaps you could align or overlap them, or give some readout of the similarity of these structures. Currently, I am skeptical of any of the SCRiPs described in this manuscript. Additionally, if the authors can show that indeed these are SCRiPs, again I would strongly advise the authors to check the Xenia scRNA-seq to see if these Xenia SCRiP-like sequences are expressed in cnidocytes.

Given the concerns raised by the Reviewer, throughout the text we now referred to octocoral SCRiPs as SCRIP-like proteins or octo-SCRiPs. Reference to Jouiaei, Sunagar et al. (2015) was added. However, we would like to point out that we do not associate them to hexacoral SCRiPs based on their predicted structure similarity: the Suppl. Fig. 2 presents the alignment of the sequences of these proteins with representative sequences from Hexacorallia, highlighting a sequence similarity up to 68%. Considering the high level of sequence divergence generally recognized within toxin families, this high similarity value contributes to support our claims. Despite the relevance of the cys framework in defining toxin families, a single amino acid shift is not necessarily indicative of a new structural family.

Concerning the structural comparison between SCRiPs and octo-SCRiPs, Suppl. Figure 2.B has been replaced with a superposition of the structure of AnmTx Ueq 12-1 with the model of U-GRTX-Esi1a. The structures were aligned with TM-align, resulting in a Cα RMSD for the aligned region of 1.86 Å, which confirms the strict similarity of the two proteins.

Unfortunately, we need to rely on available genome annotations for the evaluation of the Xenia scRNA-seq data. The only currently annotated Xenia gene showing significant homology with the SCRiP-like of E. singularis (Xe_002907) has a highly different organization, as it shows five consecutive cysteine-rich domains, and is therefore not orthologous to any of the three sequences we report in the present work. In the paper by Hu and colleagues, Xe_002907 is associated to cluster 2, which was unrelated with nematocysts.

* Minor:

*The ShK protein, U-GRTX-Esi4, strikes me as similar to NEP3 gene family identified in Nematostella, which also has 3 ShK domains (Columbus-Shenkar et al. 2018).

We have added reference to the NEP3 family in the text and discussed the similarities of U-GRTX-Esi4 with its members, highlighting that while in NEP3 the mature toxin corresponds only to the first ShK domain, U-GRTX-Esi4 is supported as a multidomain protein by our proteomic analyses.

Interestingly U-GRTX-Esi20 and 21 were found to be structurally similar to acrorhagin 1a but do not share a conserved cysteine framework ( 6 cysteines vs 8). One thing that the authors should be careful of, and perhaps point out that this is indeed not nematocyst-specific, is that an ortholog acrorhagin 1a was found to be expressed in the neurons in Nematostella (Sachkova et al. 2020). Perhaps ancestral acrorhagin 1 was found in the last common ancestor of Anthozoa but was a neuropeptide that got recruited to the venom in Actinia.

Because of the methodology employed, we expected the NEM-P to be a toxin-enriched subset of the WB-P. Indeed, some of the toxin-like proteins detected in the NEM-P were not observed in the WB-P, where they might have been below the LOD during proteomic analysis. On the other hand, being a whole-body proteome, we expect the WB-P to contain ALSO nematocyst specific proteins. At present, the detection of U-GRTX-Esi20 and 21 in the WB-P does not rule out that these may be nematocyst specific, whereas their presence in the NEM-P, in our view, confirms their occurrence in the venom. At any rate, given the current level of evidence, this Reviewer is right in considering all possibilities, such as their neuropeptide nature. These considerations have been added to the text.

* Also in general the authors refer to a lot of phylogenetics that I cannot see in the paper. For example, on line 339: "Our genomic survey indicates that these two toxins belong to two distinct monophyletic orthogroups within a very large superfamily of cysteine-rich peptides, encoded by ancestrally duplicated paralogous genes with intronless structures, that also include other members in E. singularis, not detected in the NEM-P." *What genomic survey are you referring to (where is this data)? What do you mean by "belong to two distinct monophyletic orthogroups".

In the attempt to keep the manuscript more concise, we concentrated comparative genomic analyses in the supplementary material. We now provide in the main text a detailed phylogenetic tree that displays the complex evolutionary relationships between U-GRTX-Esi20 and 21 and a number of other related sequences sharing significant sequence homology and predicted structural organization (Figure 6). In detail, the two Eunicella toxins belong to two groups of sequences, labeled as “type I” and “type VI” which are highly supported by robust bootstrap values (94 and 95, respectively) as monophyletic within Malacalcyonacea. Notably, we could identify four additional monophyletic groups, characterized by similar support values, that included sequences from both Eunicella and other Malacalcyonacea species (type II, III, IV and V). Nevertheless, these sequences were not identified as venom components by our proteomic analyses. Related proteins were also identified in species belonging to Scleralcyonacea, even though their precise relationships with those of Malacalcyonacea were often unclear.

Also, there is no visualization of the results when the authors refer to the genomic surveys, especially when referring to intron-exon boundaries. Please include which genomes include which sequences and their given intron-exon boundaries for a given gene family. I do not understand how the authors resolved figure 4. How do you know there was a loss not a gain of f exon 2 in the gene encoding for U-GRTX-Esi17. Providing the genomic loci for the toxin gene families would help. Maybe something like figure 5 from Koludarov et al. (2024) would be useful, but ideally including intron-exon boundaries.

The scenario we propose is far more parsimonious than the alternative hypothesis involving an intron gain, since this would have required an extremely complex combination of far less likely events, i.e. the independent acquisition of two partial colipase-like arrays in positions compatible with the generation of a complete colipase-like cysteine array. Despite being theoretically possible, we believe this scenario to be highly unlikely, also considering the well-established differences between the rates of intron gain and intron loss in eukaryotes, with the latter exceeding the former by several orders of magnitude (see Roy and Gilbert, 2005, https://doi.org/10.1073/pnas.0500383102).

We present a supplementary figure which schematically displays the architecture of the genes encoding novel putative venom components described in this manuscript. We need to remark the fact that, as mentioned in the main text, no genome assembly is presently available for E. singularis, and therefore such gene architectures have been inferred from the congeneric species E. verrucosa. Despite being certainly interesting, the approach proposed by the reviewer referring to figure 5 from Koludarov et al., which would basically involve a microsynteny analysis for all loci, would go far beyond the aims and scopes of the present work and require an unreasonable workload, with a very marginal increase in the quality of the data we report. First and foremost, no genome assembly is available for our target species. Moreover, just a very few genomes of Octocorallia are associated with publicly available gene annotations (in detail, no gene annotation tracks are available for R. reniformis, P. caledonicum, V. gustaviana, P. papillata, Chrysogorgia sp., H. coerulea, P. subtilis, Trachytela sp. and M. muricata). The lack of existing annotations does de facto prevent the possibility of retrieving flanking genes and providing evolutionary insights at the level requested by the reviewer. We believe that the manual annotation of the target genes of interest in all analyzed species fully meets the objectives of this study.

In the methods the author's mention:

"Whenever needed (i.e., U-GRTX-Esi20 and 21), a fine-scale classification of orthologous sequences was aided by Maximum Likelihood phylogenetic inference analyses, carried out with IQ-Tree [49] with 1000 ultrafast bootstrap replicates based on the best-fitting model of molecular evolution detected by ModelFinder [50]."

So please include this data as supplementary figures. The authors did plenty of analysis they refer to but do not include this in the paper. This lack of data makes it very hard to follow many of the phylogenetic and genomic insights from this manuscript.

The phylogenetic tree which concerns U-GRTX-Esi20 and 21 has been added in the main text as Figure 6. In pretty much all other cases where we referred to comparative genomics analyses, our inferences were simply based on the detection (or lack thereof) of orthologous genes. Considering the narrow taxonomic distribution of most target sequences, which prevents the possibility of identifying suitable outgroups for tree rooting purposes, and their usual presence as single-copy genes in E. singularis, we don’t think that adding phylogenetic trees would add useful information to the manuscript. Nevertheless, we have added the multiple sequence alignments of all relevant groups of orthologous sequences as supplementary figures.

• *Reviewer #2 (Significance (Required)):

* *This work is very can be very useful in extending our knowledge of venom in cnidarians and can help build better resolution of the evolutionary history of the ecologically essential proteins

* *Reviewer #3 (Evidence, reproducibility and clarity (Required)):

*

*SECTION A - Evidence, reproducibility and clarity

* =================================================

Summary: *Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

* This manuscript describes the proteotranscriptomic analysis of samples from the coral Eunicella singularis. A number of putative venom toxins are identified. In silico structural analyses are performed for select putative toxins and inferred activity/function is discussed. In my opinion the subject of the study is important. However, I have some important questions about the methodology (regarding "venom collection" and assignment of "venom components"), and given the preliminary nature of the study I found some of the conclusions (regarding activity) somewhat overstated. *Major comments:

• Are the key conclusions convincing?

* While some conclusions were justified, I felt unconvinced by others. Some of my pessimism stems from the technique used to extract the venom i.e. ethanol immersion. I'm not familiar with the use of this technique, however it strikes me as likely to be associated with some limitations. For example, while the nematocysts may indeed discharge their contents I would expect some contents e.g. larger proteins to be insoluble. Was this considered? This would have some major impacts on the conclusions drawn e.g. *(L418: "absence, in the NEM-P of E. singularis, of the common cnidarian cytolytic proteins." AND (L492): "conventional pore forming toxins (PFTs) of Cnidaria, including the aerolysin-like Δ-GRTX-Esi29 and the two actinoporins Δ-GRTX-Esi30 and 31 were not retrieved in the nematocysts' proteome."

Because of this observation, the authors concluded that these were not venom components in this species and speculated on other functions. However, I can't help wondering if these were simply excluded from analysis as a result of the ethanol extraction i.e. a false negative.

As anticipated in our response to Reviewer #1, we opted for ethanol extraction due to sample limitation and unsuccessful attempts with other venom collection protocols. The procedure we employed was first described by Jouiaei et al., 2015, to extract venom from the tentacles of Chironex fleckeri. Proteins and peptides extracted from the nematocysts were indeed precipitated from ethanol and subsequently resuspended for proteomic analysis. The original protocol by Jouiaei et al. used precipitation at -80°C to recover the proteins from ethanol. Albeit denaturing, this protocol should not imply sample losses. Large proteins that did precipitate were still resuspended and analyzed. We have introduced an evaporation/lyophilization step, which should not alter the outcome. In fact, we did detect higher molecular weight proteins in the NEM-P (mostly structural and enzymes). While denaturation and precipitation may functionally inactivate these proteins, these should all be detected by proteomics. The authors of the original paper presented a comparison between the venom obtained from ethanol extracted tentacles and the proteome of pressure disrupted purified nematocysts. In both cases, additional “non venom” and “structural” proteins were also detected (e.g. histones, filamin, ribosomal proteins, myosin, actin, collagen…). Given the prevalence of toxins or toxin-like proteins in our extract, we were reasonably convinced of the success of the extraction protocol. For sure, the method may present limitations: as also observed by Reviewer #1 and #3, contamination with non-nematocyst proteins is possible. This has also been considered. In fact, we adopted a conservative approach, choosing to discuss in detail only proteins with structural similarities with known toxins and/or typical toxin-like features. On the other hand, as noted by this Reviewer, our results may be partial, but, in our opinion, this would be most likely due to incomplete nematocysts firing rather than to sample loss. All these possibilities have now been better discussed and addressed in the text. At any rate, we are convinced that the protein diversification detected in the NEM-P is indicative of the presence of several venom components and provides a first indication of the existence of novel, octocoral-specific, venom protein families.

Comparisons were made to other tissue samples (whole bodies). Were these samples prepared in the same way i.e. ethanol extraction? If not, the power of any comparisons would be limited.

Following the described experimental approach, we expected the NEM-P to be a subset of the WB-P, for which no purification/enrichment of sort was performed. In fact, we reported both proteomes to confirm the enrichment of the NEM-P in venom components, highlighting the presence of putative toxins that might have been below the instrumental limit of detection in the more crowded whole body protein extract. At any rate, we have now modified the text, adding cautionary statements that may also explain our results.

• *It was unclear to me exactly how "venom components" (Fig. 1A) were defined. Why are "enzymes" , "structural" and "unknow" NOT considered venom components when they were identified in the "venom" extract?

The “structural” and “enzymes” categories were used to analyze the hits in the NEM-P. We decided to discuss only putative neurotoxins or cytolytic toxins based on the limited selectivity of the extraction protocol employed and on the lack of histological control. As structural components and enzymes, in the absence of a crude venom extract, may derive from other tissues, we preferred not to discuss them. We hope this is clearer in the amended version of the manuscript.

Furthermore, a large proportion of proteins detected are "structural" - doesn't this suggest that the "venom" extract included a large proportion of false positives i.e. non-toxin proteins? Is it possible that some of the proteins which are considered as "venom components" are also false positives?

• *As also noted by Reviewer #1, aside from contamination from other tissues, some of the toxin-like proteins we identified may have different functions (e.g, neuronal, developmental) and their toxin function is presumed on the basis of structural features. This issue is clearly addressed in the manuscript. Nonetheless, putative toxins are definitely enriched in the NEM-P compared to the WB-P, which leads us to believe that the NEM-P is a fraction enriched in nematocysts content. This is now more evident also in the PEAKS output files, provided as Supplementary Tables 2 and 3.

The nematocyst ethanol extract is referred to throughout the manuscript as "venom". Similarly, what I would consider putative toxins are referred to throughout the manuscript as "toxins". Given the preliminary nature of the study I suggest the authors consider rewording these.

This has been changed throughout the text.

In short, the evidence presented left me unconvinced that the nematocyst ethanol extract that was analysed represented the genuine "venom" of this species and that the "toxins" identified represent the genuine toxin repertoire. The authors should at least discuss potential limitations, defend my claims in this context and adjust conclusions accordingly.

We hope that the additional clarifications provided in the Results and Discussion section, and the amendments we made throughout the manuscript made our statements more convincing

Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? See comment above regarding venom collection and conclusions drawn.

We have introduced cautionary statements throughout the text.

* *Also, despite the absence of any experimental activity/functional data, there was a lot of inference about activity and function.

A few examples: L299 - "might have acquired peculiar biological activity."

L301 - "support their relevance for the predatory and/or defensive strategies…"

L326 - "abundance of this protein suggests a strong functional relevance…"

L358 - "the structure presented a SCRiP-like W-shaped fold, indicative of a potential neurotoxic function."

L427 - "suggestive of a peculiar chemical selectivity towards different lipids"

L506 - "the cytolytic activity seems to be ascribable mostly to the six saposins"

* *I suggest some removal or rewording throughout the Results/Discussion section to reflect the fact that most of this is purely speculative.

This has been modified according to the reviewer’s suggestions.

Regarding the following statement on L300 - "Notably, the transcripts for all these toxins had exceptionally high TPM values (1806, 569, 826 and 429, respectively for the U-GRTX-Esi14 to 17/18), which support their relevance for the predatory and/or defensive strategies of Eunicella singularis." These TPM values don't seem high to me e.g. 1806 TPM = 0.0018% of transcripts. How do these numbers compare to other "non-venom" components of the transcriptome? A graph illustrating this would be helpful.

We thank the Reviewer for this suggestion. The expression values we report in this work were calculated based on an RNA-seq library generated from a whole body sample. Consequently, considering the low relative abundance of nematocysts to total body weight, we expect that the contribution of this cell type to the total extracted RNA to be rather low. We exploited the available information from a previously published single-cell RNA-seq dataset obtained from another octocoral species (i.e. Xenia, see Hu et al., 2020, Nature) to identify the most likely candidate nematocyst-specific mRNAs venom components having a 1:1 orthology relationship with E. singularis. In detail, we were able to detect high-confidence 1:1 orthologs for 242 out of the 432 Xenia genes included in cluster 11 in the study by Hu and colleagues (i.e. the cluster associated with nematocysts). This allowed us to assess the expression of the orthologous sequences, expected to share a similar cell-specificity, in E. singularis. The 242 putative nematocyst-specific mRNAs displayed an average expression level of 16.65 TPM (median = 4.85 TPM) in the whole body sample, and just 8 out of these (i.e. about 3% of the total) had an expression level higher than 100 TPM. Based on these observations, we believe that our statement that “all these toxins had exceptionally high TPM values” holds true. Supplementary table 2 reports the sequences of the toxins identified in the NEM-P together with the TPM of the corresponding transcripts.

Regarding the following statement on L463 - "Our investigation unequivocally demonstrated that Octocorallia do produce venom" Was it not already known that Octocorallia have nematocysts and therefore are venomous (in which case this should be cited)? If this wasn't known, I don't think this study was really designed to test this hypothesis. Regardless, I don't think this is a meaningful claim to make here.

This observation is correct. We have rephrased the text accordingly.

Table S2: on what basis are the sequences highlighted in red considered "proteomics validated" e.g. confidence, coverage? Could a protein abundance column be included in this table (for NEM and WB tissues)?* *

Residues highlighted in red in Table S2 (now Suppl tab. 4) correspond to the tryptic peptides identified with good confidence by the LC-MS analysis. We have added supplementary files, as per request of Reviewer #1, with the summary of the PEAKS Studio outputs for the two proteomes, highlighting the confidence and coverage scores. In Suppl. Tab. 4, coverage has been recalculated considering the sequence of the predicted mature peptide (not the precursor identified by PEAKS Studio). Finally, as PEAKS Studio does not provide a quantitative measure of the identified peptides (i.e., counts), we have calculated and added to said tables the exponentially modified Protein Abundance Index (emPAI), which provides an approximate label free measure of each protein’s abundance. We have also added the relative emPAI, which normalizes each protein's emPAI value relative to the total emPAI of all proteins in the sample, providing a percentage abundance. It is noteworthy that all the proteins that have been identified as putative toxins have higher relative emPAI values in the NEM-P, thus providing yet an additional indirect proof of the validity of the ethanol extraction protocol (see Suppl. Tab. 2 and 3).

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. *Additional experiments e.g. synthesis and activity assays would go a long way towards bolstering some of the conclusions. However, if some of the conclusions can be toned down a little (see comments above), I don't consider these to be essential.

In my opinion, the study would benefit from some additional analyses (described in the comments above).

See our answers to the specific comments above.

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

N/A* * Are the data and the methods presented in such a way that they can be reproduced?

Yes. * Are the experiments adequately replicated and statistical analysis adequate? *No - I may be wrong, but as far as I can tell from the text, replicates were not collected. Three cDNA libraries were generated but were these replicates (please clarify this in the Methods)? It could be reasonably argued (and I would mostly agree) that replicates are not necessary for a general analysis of the composition of the samples. However in a couple of instances conclusions are drawn based on "differential expression". I suggest that in the absence of expression level replicates these conclusions should be withdrawn.

The statements about differential expression (more correctly differential maturation) are based on proteomics results and not on DEG analysis in the transcriptome (see also reply to reviewer #1). All the claims have been rephrased and the supplementary figure 1 has been added to support our statements.

Concerning the cDNA libraries, however, they were prepared as technical replicates to account for variations in venom expression among samples, and the resulting assemblies were pooled before assembly, as explained in the Methods section.

• *"Abundance" of proteins or toxins was mentioned on occasion, but no data on quantification or abundance of proteins is mentioned anywhere (although this is something that could be done with the LC-MS/MS data). In my opinion these data would be very useful and should be included, especially if mentioned in the text.

• *As previously discussed, we have calculated and added to the PEAKS output file the emPAI and the relative emPAI values. These data are now provided in the supplementary Tables 2 and 3.

Minor comments:

* *Specific experimental issues that are easily addressable.

Are there limitations to the ethanol extraction procedure (please add a paragraph in the Discussion)? Are there any previous studies using this procedure?

This has been done: the potential drawbacks of the ethanol extraction procedure are now addressed in the Results and Discussion section.

* *Are prior studies referenced appropriately?

Yes, for the most part (but see comment above).

* *Are the text and figures clear and accurate?

In general yes, although I found myself looking for actual data. Most of the current figures are summaries or cartoons. I would have liked to have seen pictures of the species in question (including a picture/diagram of the tissue from which the cDNA libraries and proteomes were derived); a picture of the nematocysts; the total ion chromatogram of the "venom"; Some type of figure to place the "toxin" expression level in the context of all transcripts; some more of the actual sequences identified including alignments (in the main text rather than the SI);

Various figures in the manuscript have been modified in accordance to the Reviewers’ suggestions. We have included a workflow of the extraction with a picture of E. singularis and modified Fig1 (now Fig 2) to include the TIC of the NEM-P.

Figure 4: could the motifs and termini for each be labelled please.

This has been done.

Do you have suggestions that would help the authors improve the presentation of their data and conclusions? See comments above. In my opinion, the work done was quite preliminary (i.e. analysis of a single species and does not include any activity/functional data) but still significant and useful to the field. I felt that some of the conclusions were unnecessarily over-reaching and could be toned down without detracting from the importance of the manuscript.

Several instances of hyperbole could be toned down e.g. use of the words: remarkable (L27); rich (L28); intricate (L38); significant (L189); peculiar (L299, 427); only (L191); exceptionally (L300); extremely (L316); strong (L326). Similarly, some wording is subjective e.g. "worthy of" (L33); "interestingly" (L220, 382, 426, 492, 535). Please amend.

We have toned down our statements through the manuscript.

"Homology" is used throughout when referring to similarity. Please change.

This has been done

Minor typos and similar:

2.5 cm (L97) - use 25 mm (cm is not a standard scientific measure).

30" (L97) - 30 min?

ml (L97) - mL is technically correct although some journals use ml, regardless should be consistent throughout. Reverse-phase (L127) – reversed-phase

30,000 (L141) – units?

Typos were corrected.

*

*Reviewer #3 (Significance (Required)):

*

*SECTION B – Significance

* ========================

*- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

* *Cnidarian venoms and toxins have been the subject of extensive study over the past several decades. However there has been very little work performed on corals. In this respect, this subject of this manuscript is significant.

* *- Place the work in the context of the existing literature (provide references, where appropriate).

* *The subject of this manuscript i.e. the characterisation of the venom composition of a coral is an interesting topic. The work is rather preliminary, but still represents an important addition to the literature (without requiring overinterpretation of the results-see comments above).

* *- State what audience might be interested in and influenced by the reported findings.

* *I would expect the manuscript to be of interest to others working in the toxinology field, particularly those working on Cnidarian venoms or toxins.

* *- Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

* *Venom; Toxins; Pep

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

This manuscript describes the proteotranscriptomic analysis of samples from the coral Eunicella singularis. A number of putative venom toxins are identified. In silico structural analyses are performed for select putative toxins and inferred activity/function is discussed. In my opinion the subject of the study is important. However, I have some important questions about the methodology (regarding "venom collection" and assignment of "venom components"), and given the preliminary nature of the study I found some of the conclusions (regarding activity) somewhat overstated.

Major comments:

• Are the key conclusions convincing?

While some conclusions were justified, I felt unconvinced by others. Some of my pessimism stems from the technique used to extract the venom i.e. ethanol immersion. I'm not familiar with the use of this technique, however it strikes me as likely to be associated with some limitations. For example, while the nematocysts may indeed discharge their contents I would expect some contents e.g. larger proteins to be insoluble. Was this considered? This would have some major impacts on the conclusions drawn e.g. (L418: "absence, in the NEM-P of E. singularis, of the common cnidarian cytolytic proteins." AND (L492): "conventional pore forming toxins (PFTs) of Cnidaria, including the aerolysin-like Δ-GRTX-Esi29 and the two actinoporins Δ-GRTX-Esi30 and 31 were not retrieved in the nematocysts' proteome." Because of this observation, the authors concluded that these were not venom components in this species and speculated on other functions. However, I can't help wondering if these were simply excluded from analysis as a result of the ethanol extraction i.e. a false negative.

Comparisons were made to other tissue samples (whole bodies). Were these samples prepared in the same way i.e. ethanol extraction? If not, the power of any comparisons would be limited.

It was unclear to me exactly how "venom components" (Fig. 1A) were defined. Why are "enzymes" , "structural" and "unknow" NOT considered venom components when they were identified in the "venom" extract? Furthermore, a large proportion of proteins detected are "structural" - doesn't this suggest that the "venom" extract included a large proportion of false positives i.e. non-toxin proteins? Is it possible that some of the proteins which are considered as "venom components" are also false positives?

The nematocyst ethanol extract is referred to throughout the manuscript as "venom". Similarly, what I would consider putative toxins are referred to throughout the manuscript as "toxins". Given the preliminary nature of the study I suggest the authors consider rewording these.

In short, the evidence presented left me unconvinced that the nematocyst ethanol extract that was analysed represented the genuine "venom" of this species and that the "toxins" identified represent the genuine toxin repertoire. The authors should at least discuss potential limitations, defend my claims in this context and adjust conclusions accordingly. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

See comment above regarding venom collection and conclusions drawn.

Also, despite the absence of any experimental activity/functional data, there was a lot of inference about activity and function. A few examples: L299 - "might have acquired peculiar biological activity." L301 ¬- "support their relevance for the predatory and/or defensive strategies..." L326 - "abundance of this protein suggests a strong functional relevance..." L358 - "the structure presented a SCRiP-like W-shaped fold, indicative of a potential neurotoxic function." L427 - "suggestive of a peculiar chemical selectivity towards different lipids" L506 - "the cytolytic activity seems to be ascribable mostly to the six saposins" I suggest some removal or rewording throughout the Results/Discussion section to reflect the fact that most of this is purely speculative.

Regarding the following statement on L300 - "Notably, the transcripts for all these toxins had exceptionally high TPM values (1806, 569, 826 and 429, respectively for the U-GRTX-Esi14 to 17/18), which support their relevance for the predatory and/or defensive strategies of Eunicella singularis." These TPM values don't seem high to me e.g. 1806 TPM = 0.0018% of transcripts. How do these numbers compare to other "non-venom" components of the transcriptome? A graph illustrating this would be helpful.

Regarding the following statement on L463 - "Our investigation unequivocally demonstrated that Octocorallia do produce venom" Was it not already known that Octocorallia have nematocysts and therefore are venomous (in which case this should be cited)? If this wasn't known, I don't think this study was really designed to test this hypothesis. Regardless, I don't think this is a meaningful claim to make here.

Table S2: on what basis are the sequences highlighted in red considered "proteomics validated" e.g. confidence, coverage? Could a protein abundance column be included in this table (for NEM and WB tissues)? - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Additional experiments e.g. synthesis and activity assays would go a long way towards bolstering some of the conclusions. However, if some of the conclusions can be toned down a little (see comments above), I don't consider these to be essential.

In my opinion, the study would benefit from some additional analyses (described in the comments above). - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

N/A - Are the data and the methods presented in such a way that they can be reproduced?

Yes. - Are the experiments adequately replicated and statistical analysis adequate?

No - I may be wrong, but as far as I can tell from the text, replicates were not collected. Three cDNA libraries were generated but were these replicates (please clarify this in the Methods)? It could be reasonably argued (and I would mostly agree) that replicates are not necessary for a general analysis of the composition of the samples. However in a couple of instances conclusions are drawn based on "differential expression". I suggest that in the absence of expression level replicates these conclusions should be withdrawn.

"Abundance" of proteins or toxins was mentioned on occasion, but no data on quantification or abundance of proteins is mentioned anywhere (although this is something that could be done with the LC-MS/MS data). In my opinion these data would be very useful and should be included, especially if mentioned in the text.

Minor comments:

• Specific experimental issues that are easily addressable.

Are there limitations to the ethanol extraction procedure (please add a paragraph in the Discussion)? Are there any previous studies using this procedure? - Are prior studies referenced appropriately?

Yes, for the most part (but see comment above). - Are the text and figures clear and accurate?

In general yes, although I found myself looking for actual data. Most of the current figures are summaries or cartoons. I would have liked to have seen pictures of the species in question (including a picture/diagram of the tissue from which the cDNA libraries and proteomes were derived); a picture of the nematocysts; the total ion chromatogram of the "venom"; Some type of figure to place the "toxin" expression level in the context of all transcripts; some more of the actual sequences identified including alignments (in the main text rather than the SI);

Figure 4: could the motifs and termini for each be labelled please. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

See comments above. In my opinion, the work done was quite preliminary (i.e. analysis of a single species and does not include any activity/functional data) but still significant and useful to the field. I felt that some of the conclusions were unnecessarily over-reaching and could be toned down without detracting from the importance of the manuscript.

Several instances of hyperbole could be toned down e.g. use of the words: remarkable (L27); rich (L28); intricate (L38); significant (L189); peculiar (L299, 427); only (L191); exceptionally (L300); extremely (L316); strong (L326). Similarly, some wording is subjective e.g. "worthy of" (L33); "interestingly" (L220, 382, 426, 492, 535). Please amend.

"Homology" is used throughout when referring to similarity. Please change.

Minor typos and similar:

2.5 cm (L97) - use 25 mm (cm is not a standard scientific measure). 30" (L97) - 30 min? ml (L97) - mL is technically correct although some journals use ml, regardless should be consistent throughout. Reverse-phase (L127) - reversed-phase 30,000 (L141) - units?

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Cnidarian venoms and toxins have been the subject of extensive study over the past several decades. However there has been very little work performed on corals. In this respect, this subject of this manuscript is significant. - Place the work in the context of the existing literature (provide references, where appropriate).

The subject of this manuscript i.e. the characterisation of the venom composition of a coral is an interesting topic. The work is rather preliminary, but still represents an important addition to the literature (without requiring overinterpretation of the results-see comments above). - State what audience might be interested in and influenced by the reported findings.

I would expect the manuscript to be of interest to others working in the toxinology field, particularly those working on Cnidarian venoms or toxins. - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Venom; Toxins; Peptides

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

Summary:

The authors of this work explore the venom repertoire of octocoral, a group of cnidarians whose venom has largely been ignored in the literature. As a first step into characterizing the venom of octocorals, the authors use a proteo-transcriptomic approach for Eunicella singularis, Specifically, they generated the transcriptome and proteome from whole-body as well as a more specific proteome of the nematocyst, a specialized sub-cellular structure found only in cnidarians and used to inject venom. The nematocyst proteome is a crucial dataset of the manuscript as it allows the authors to discriminate what is most likely a bona fide toxin compared to general physiological proteins.

Major:

However, I have some skepticism regarding the legitimacy of this nematocyst proteome. Specifically, the proteins from this are nematocyst-specific. The authors used an approach to soak the animal in ethanol, which theoretically should cause the nematocyst to fire, releasing the venom housed inside. This is a technique previously used in box jellyfish where they show that indeed the nematocyst have fired using histological approaches. However, this was not validated for Eunicella singularis. I am hesitant to fully accept that the data from the nematocyst-proteome is specific. Other approaches, such as isolating nematocyst using a percoll gradient, will likely generate a more specific nematocyst proteome. This percoll gradient approach has been used to isolate nematocysts from different species of cnidarians ranging from hydra to sea anemones, however, I recognize that although this approach is robust for different cnidarians, acquiring enough material is challenging and maybe beyond the capacity for this octocoral. I would argue this would be the best approach, but if not feasible I can understand. However, other potential validation could be used to help improve the confidence that this is, at least mostly, nematocyst-specific. Furthermore, one could argue that this ethanol approach used in box jellyfish also specifically used tentacle, a tissue significantly enriched in nematocyst likely greatly improving the specificity in isolating nematocyst-specific proteins. whereas in this study they use a collection of whole polyps, therefore, anything that is extracted from the ethanol would precipitate. This is a much more complex collection of tissues which I would assume could interfere with isolating nematocyst-specific proteins

A computational approach, that I think is essential, is to use the Xenia single-cell atlas. Xenia is also an octocoral with a nice single-cell atlas in which the cnidocytes form a distinct cluster. The authors can perform a reciprocal best-blast hit with the xenia genome and Eunicella singularis transcriptome and then see if gene-encoding proteins found in Eunicella nematocyst proteome have orthologs with genes found in the Xenia cnidocyte cluster. A statistical test could then be performed to show that there is a significant overlap between the nematocyst proteins from Eunicella and their orthologs in the Xenia cnidocyte cluster. This is still quite indirect but can give some insights. A better approach would be to perform proteomics from Xenia using the ethanol approach and mapping to see where the proteins captured are found in the atlas. This would massively elevate this work and provide proof that indeed this approach using ethanol is capable of precipitating nematocyst-specific proteins. I would strongly recommend trying to provide some evidence that this is indeed a nematocyst-specific protein, or at the least, is significantly enriched. Because this is unknown, many of the interpretations presented downstream are not well supported.

Another major issue with the manuscript is the section referring to SCRiPs. First, the authors do not cite Jouiaei, Sunagar et al. (2015) which was the first publication to functionally characterize SCRiPs as toxins. Additionally, the majority of SCRiPs identified in this study and those found in Eunicella have a different cysteine framework. The authors acknowledge this online 245 but claim that, given the alphafold structure is similar, they are from the same gene family. First, I think this is very weak support as typically sharing a conserved cysteine framework is the bare minimum to categorize these toxins in a gene family. Although some cysteine frameworks are somewhat hard to resolve as the space between the cysteines can be variable, in this case, SCRiPs have a very distinct triple repeat of cysteines near the C terminal that is missing in these octocoral SCRiPs. These make me suspicious that these are indeed from the same gene family. Then relying on alphafold to predict the structure and claiming it's similar to Tau-AnmTx Ueq 12-1 from Urticina eques is also fairly weak support. Although I am not an expert in protein structures, I cannot tell from the images comparing the 2 structures in the supplementary figure s1 that these are similar. Perhaps you could align or overlap them, or give some readout of the similarity of these structures. Currently, I am skeptical of any of the SCRiPs described in this manuscript. Additionally, if the authors can show that indeed these are SCRiPs, again I would strongly advise the authors to check the Xenia scRNA-seq to see if these Xenia SCRiP-like sequences are expressed in cnidocytes.

Minor:

The ShK protein, U-GRTX-Esi4, strikes me as similar to NEP3 gene family identified in Nematostella, which also has 3 ShK domains (Columbus-Shenkar et al. 2018).

Interestingly U-GRTX-Esi20 and 21 were found to be structurally similar to acrorhagin 1a but do not share a conserved cysteine framework ( 6 cysteines vs 8). One thing that the authors should be careful of, and perhaps point out that this is indeed not nematocyst-specific, is that an ortholog acrorhagin 1a was found to be expressed in the neurons in Nematostella (Sachkova et al. 2020). Perhaps ancestral acrorhagin 1 was found in the last common ancestor of Anthozoa but was a neuropeptide that got recruited to the venom in Actinia.

Also in general the authors refer to a lot of phylogenetics that I cannot see in the paper. For example, on line 339:

"Our genomic survey indicates that these two toxins belong to two distinct monophyletic orthogroups within a very large superfamily of cysteine-rich peptides, encoded by ancestrally duplicated paralogous genes with intronless structures, that also include other members in E. singularis, not detected in the NEM-P."

What genomic survey are you referring to (where is this data)? What do you mean by "belong to two distinct monophyletic orthogroups".

Also, there is no visualization of the results when the authors refer to the genomic surveys, especially when referring to intron-exon boundaries. Please include which genomes include which sequences and their given intron-exon boundaries for a given gene family. I do not understand how the authors resolved figure 4. How do you know there was a loss not a gain of f exon 2 in the gene encoding for U-GRTX-Esi17. Providing the genomic loci for the toxin gene families would help. Maybe something like figure 5 from Koludarov et al. (2024) would be useful, but ideally including intron-exon boundaries.

In the methods the author's mention:

"Whenever needed (i.e., U-GRTX-Esi20 and 21), a fine-scale classification of orthologous sequences was aided by Maximum Likelihood phylogenetic inference analyses, carried out with IQ-Tree [49] with 1000 ultrafast bootstrap replicates based on the best-fitting model of molecular evolution detected by ModelFinder [50]."

So please include this data as supplementary figures. The authors did plenty of analysis they refer to but do not include this in the paper. This lack of data makes it very hard to follow many of the phylogenetic and genomic insights from this manuscript

Significance

This work is very can be very useful in extending our knowledge of venom in cnidarians and can help build better resolution of the evolutionary history of the ecologically essential proteins

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript by Modica et al reports characterisation of the venom system in the white sea fan Eunicella singularis, a species of an octocorallian coral. E. singularis is common in the north-western Mediterranean sea. The authors used a proteo-transcriptomic approach followed by extensive bioinformatics analysis. Specifically, they generated a new E. singularis transcriptome and characterised extracts from nematocysyts (venom-bearing structures) and whole body using tandem mass spectrometry. Toxins were identified by HMMER using Tox-prot and VenomZone databases as queries as well as ClanTox web server.

Major comments:

1. As far as I am aware, venom production by ectodermal gland cells has been reported only in sea anemones (Moran et al, 2011), therefore it is unclear whether it is the case in the octocorallian sea fan as well. Additionally, cnidarian toxin-like proteins might be produced by neurons (Sachkova et al, 2020) or involved in development (Surm et al 2024). Thus, it is probable that in E. singularis not all the toxin-like proteins found in the whole body proteome and missing from the nematocyst proteome are venom components. Thus, additional experiments would be required to localise those proteins to ectodermal gland cells. I suggest to mention this limitation and refer to such proteins as "toxin-like" or "putative toxins".
2. In addition to submitting proteomics data to PRIDE, it would be helpful for readers/reviewers to provide a supplementary excel file with all the peptides and proteins identified by PEAKS Studio. I could not access the data on PRIDE as I think they still have not been assigned a PXD dataset identifier.

Minor comments:

1. It would be helpful for readers to split the Results and Discussions into smaller subsections with headings, perhaps according to the identified toxin families. It would be also helpful to provide a summary figure with all the toxins identified and perhaps toxin expression levels. Especially showing cysteine patterns for new toxins would be very useful.
2. It is unclear why the Toxin annotation pipeline is hidden in the supplementary material. It would be also helpful to show it as a schematic pipeline in the main text.
3. The identification of proteolytic cleavage sites is not really described. It would be also helpful to mark them at the Figure 2.
4. "Other peptides present in E. singularis nematocysts and displaying protease inhibitory domains, but likely lacking a toxin function (Kazal-type, cystatines, antistasins, and macins)..." - why do they likely lack a toxin function? what is the rational behind this statement?
5. "cell- or tissue-specific differential maturation patterns" - I think the differential maturation needs to be confirmed by additional experiments to exclude a possibility of being an artifact due to low mass spectrometry sensitivity.
6. "three consecutive ShK domains with peculiar characteristics (Suppl. Fig. 2)" - what are these characteristics?
7. Fig. S1 legend: "Octocorallia (cyano bar) and Hexacorallia (blue bar)" - the bars look pink and cyan.

Referee cross-commenting

I agree with both reviewers that additional validation of the ethanol extraction method would be required to confirm its specificity and efficiency. Since ethanol is widely used for tissue fixation, I would guess that it is improbable that it leads to disruption of other coral cell types in addition to discharging nematocytes. However, to be 100% sure that would need to be confirmed experimentally. I think the suggestion to use Xenia single cell dataset to validate the nematocyst proteome reported in this paper is really worth trying. However, toxin-like genes in cnidarians might be recruited to non-venom cell types (Sachkova et al, 2020; Surm et al 2024) therefore if a gene is nematocyte-specific in one species it does not mean it would the same in another one, especially if they are distantly related. Thus, the best would be to run some additional experiments in Eunicella singularis, if the tissue is available.

Significance

This study reports venom composition of an octocoral for the first time. These data are very important for understanding biology and ecology of these animals as they rely on venom for feeding and deterring predators. This study is a significant advancement of the cnidarian venomics as most of the literature is limited to sea anemone and jellyfish venoms. This study will be interesting to the broad audience: venomics and coral ecology communities, evolutionary biologists and marine scientists. The main strength of this work is that it provides a comprehensive overview of the venom system in a widespread octocoral species with important ecological roles. The limitations of this study is that the toxicity and biological function of the identified venom components have not been confirmed experimentally. However, the localisation of the proteins to nematocysts is a very strong indication of being a venom component.

My expertise: cnidarian venom (biochemistry, ecology and evolution).

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Transparent Peer Review

---

Download the complete Review Process [PDF] including:

• reviews
• authors' reply
• editorial decisions

</br>

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

The authors do not wish to provide a response at this time.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #4

Evidence, reproducibility and clarity

Summary

This study analyses the shugoshin gene (SGO1) of the single-celled basidiomycete Cryptococcus neoformans. The function of Sgo proteins has been studied in various organisms, including yeasts (budding and fission yeast, C. albicans), flies, frog eggs, mammals, and plants. In general, Sgo proteins function as adapter proteins that recruit activities, such as the PP2A phosphatase, the chromosomal passenger complex (CPC), kinesins, or condensin to the pericentromeric region and kinetochores. This is required for proper biorientation of sister kinetochores at metaphase, correction of erroneous microtubule-kinetochore attachments, signaling by the spindle-assembly checkpoint (SAC), and protection of centromeric cohesin from removal by separase at meiosis and a non-proteolytic pathway in mammalian mitosis. These processes are interconnected, which has made distinguishing different functions of Sgo proteins a challenging and ongoing task.

The authors use plate assay to show that proliferation of the sgo1 mutant is sensitive to microtubule-depolymerizing drugs. Double mutants with a deletion of the SAC component MAD2 or a non-essential kinetochore subunit are even more sensitive. The sgo1 mutant fails to halt cell division, re-budding, and DNA replication in the presence of a MT drug, suggesting that it is defective in inducing or maintaining SAC activity.

Live-cell imaging is used to analyze the kinetochores recruitment of several proteins involved in error correction and/or SAC activity in the presence of a MT drug. They conclude that sgo1 mutants fail to maintain the SAC kinase Bub1 at kinetochores. Furthermore, sgo1 mutants fail to maintain at kinetochores the Aurora B kinase, which is required for error correction and SAC activity. Conversely, sgo1 mutants recruit higher levels of the PP1 phosphatase, which is known to oppose Aurora B in several processes. The authors suggest that the sgo1 mutant is defective in SAC function because it shifts the balance between Aurora B and PP1 towards the latter.

While the kinase activity of Bub1 promotes the SAC, it is not essential. However, kinase activity is required for recruitment of Sgo1 to centromeres/kinetochores. Bub1 phosphorylates histone H2A to which Sgo1 is thought to bind via its conserved SGO domain. The authors analyzed a BUB1 kinase-dead mutant and find it to be defective in SAC activity, while a mutation in Sgo1's SGO domain is SAC proficient. The authors conclude that Sgo1 recruitment in Cryptococcus differs from the conventional, Bub1-dependent mechanism.

Finally, the author present experiments suggesting that Sgo1 localizes to spindle pole bodies (SPBs) and the spindle, whereas it accumulates at the pericentromere in other organisms.

Major comments

This work might be seen against the background of a large body of work on Sgo proteins in various organisms, including detailed and mechanistic studies in yeast and animals. The author should better explain what we might learn from a less-commonly studied microorganism in which detailed mechanistic studies are much harder. They briefly mention that Cryptococcus has an unconventional kinetochore but do not elaborate. Studying Sgo in such a context is certainly interesting and would give this work a unique angle.

One of the challenges of working on Sgo function is to distinguish its functions in the interconnected processes of biorientation, error correction, and SAC activity. For instance, the authors show that sgo1 mutants fail to arrest at metaphase in response to microtubule depolymerization. Does this failure lead to the loss of Bub1/Aurora from kinetochores or is this loss the reason for the inability to arrest? Furthermore, error correction leads to SAC activation, which in turn leads to accumulation of proteins relevant to error correction. The authors should discuss these issues.

The authors might want to refrain from making detailed claims about the mechanism of Sgo recruitment to subcellular structures, while the experiments presented are not detailed enough to reject more conventional models. The authors detect Sgo on SPBs and the spindle, which does not mean that it is absent from kinetochores or the pericentromere. I note that vertebrate Sgo1 has originally been identified as a microtubule-binding protein.

Recruitment of Sgo to the pericentromere is more complex than implied by the authors. Bub1's kinase activity is important but not essential for SAC function. It is required for Sgo recruitment even in cells containing a phosphomimic version of histone H2A, and Sgo proteins have additional binding partners at the pericentromere, including cohesin and HP1.

Minor comments

The time course experiments are difficult to interpret. It would be preferably to show separate curves for large-budded cells and e.g. Bub1 or Aurora B at kinetochores. It is difficult to see what fraction of cells arrested at metaphase and what fraction recruited Bub1/Aurora B.

I cannot judge the live imaging experiments. Materials and Methods mentions the removal of outliers and the bridging of gaps in the imaging but lacks information on how these procedures might affect the data presented. Furthermore, the graphs showing statistics are unconventional. They present the means of three experiments (open circles) and all the individual data points (colored circles), while the (very small) error bars refer to the means (that is what I assume). It would be preferable to separately show the individual data points and their respective means and then use an ANOVA to compare them.

The live -cell imaging experiments could be presented as montages (or, indeed, movies) to capture changes over time. Also, the quantification might be presented as percentages or intensities over time - not just a single timepoint. After all, the authors claim that the relevant proteins are first recruited to but then lost from kinetochores in the sgo1 mutant.

Referee Cross-Commenting

I agree with the comments made by the other reviewers. In particular, all reviewers indicate that claims about a new mechanism (Bub1-independent role of Sgo1) should be toned down or backed-up by new experiments. Same for the relevance of the localization of Sgo1 to spindles and SPBs. In agreement with reviewer #2, I would strongly recommend describing and discussing the use of C. neoformans. I still feel that presentation, analysis, and statistics of the live-imaging experiments should be improved.

Significance

This study is interesting to researchers working on mechanisms of chromosome segregation in microorganisms and the functions of Sgo proteins. As stated above, the author could make their study more appealing if they explained the unique features of Cryptococcus with regards to chromosome segregation. This reviewer works on mechanisms controlling chromosome segregation including Sgo proteins but is not familiar with the Cryptococcus system.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

This study investigates the spindle assembly checkpoint (SAC) in a budding yeast Cryptococcus neoformans. The authors propose that Sgo1, the shugoshin homolog in the above species, maintains the SAC activity independently of the Bub1 kinase activity, which is usually critical for the full SAC activity in other species.

Major comments:

The main conclusion of the manuscript may not appear convincing because of the following reasons (1) The spotting assay in Fig. 5B can be interpreted as Sgo1 depends on the Bub1 kinase activity as in other species, but Sgo1 also has additional roles in chromosome segregation, which leads to the stronger sensitivity to TBZ in sgo1∆ compared to bub1-kd. (2) Both bub1-kd and sgo1∆ show defects in maintaining SAC arrest (Fig. 2D). If Sgo1 does not depend on the Bub1 kinase activity to maintain SAC arrest, Bub1 is maintaining the arrest through other pathways. Therefore, if the authors repeated this experiment with sgo1∆ bub1-kd double mutants, there would be an additive effect and the cells would arrest less efficient compared to single mutants. On the other hand, if Sgo1 depends on Bub1, the double mutant will behave similarly to single mutants. I strongly recommend the authors to perform this experiment. (3) Along the same line; if it is not through Sgo1, how does the Bub1 kinase activity support the SAC arrest? (4) The authors conclude that the SPB localization is critical for Sgo1 functions. However, there are some dotty Sgo1 signals between the SPBs in metaphase (Fig. 6A) that could be centromeric localization. I would recommend the authors to repeat this experiment in bub1-kd mutant to see if they detect similar centromeric enrichment of Sgo1. If not, this indicate that there is a Sgo1 pool at the centromere that depends on Bub1, similar to other species. (5) The only convincing supporting evidence is the Sgo1-K382A mutant showing no TBZ sensitivity, but this data is not sufficient to draw the conclusion (and having this conclusion as their tile) because the SGO motif is not so conserved and this mutation may not be completely abolishing the interaction with H2ApT120.

Minor comments:

Line 180-181: Mad2 is the master regulator of SAC, and mad2 mutants cancel the SAC completely in other systems. However, it appears that sgo1∆mad2∆ has slightly "stronger" SAC compared to mad2∆. This is an interesting observation, and I recommend the authors to speculate why deleting sgo1 made the SAC stronger in mad2∆ cells. Also, this contradicts with the TBZ sensitivity that sgo1∆mad2∆ shows higher sensitivity compared to mad2∆. This would also be a nice discussion point.

Line 210: The evidence presented to make this point is flawed. Fig. 2D shows that the sgo1 mutant starts with a percent large-budded cells with signal below the other two (see 40 min). It would make sense then that the peak for sgo1∆ cells is lower at the inflection point the authors are referring to around 160min. A better argument is that bub1-kd and sgo1∆ act like each other, not that there is a particular difference. This again points out the possibility that Sgo1 and the Bub1 kinase activity is in the same pathway for the SAC signaling.

Line 330: Is the centromeric localization actually killed in Sgo1-K382A mutant? Tagging the mutant protein with GFP would be informative (also see comments above regarding Sgo1 localization experiment in bub1-kd background).

Line 385: The resolution used in this microscopy is not enough to tell whether or not Sgo1 localizes to centromeres in this species. Perhaps the kinetochore pool of Sgo1 is buried in the spindle signal the authors see. I understand the technical difficulty but an experimental system to completely dissociate kinetochores from SPB (like nda3-cs mutant in pombe) is required to make this conclusion.

Line 418: Again, this conclusion is supported by weak evidence. Perhaps Sgo1 localization is more diffuse than expected along the spindle and concentrated at SPBs, but it is premature to conclude that there is not a pool of Sgo1 that does not localize in the proximity of centromeres in this particular species.

• There are no error bars in the Figure 3F and Supp Figure 4B. Are these experiments repeated?
• The quantification of the intensity of the fluorescent signals is performed on the maximum intensity Z-projected images, and it is recommended to use sum-projected images for accurate measurement.

Significance

The authors investigate fundamental mechanisms that support faithful chromosome segregation, using a non-typical model organism. It is very important to study diverse model systems to comprehensively understand what the conserved mechanisms are in each lineage.

our expertise: mitosis and meiosis, mouse oocytes, spindle, chromosome segregation, centromere, confocal microscopy, genetics, cell biology

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors characterized the mitotic function of Shugoshin SGO1 in a basidiomycete budding yeast Cryptococcus neoformans. Sgo1 is well conserved protein, which ensures the maintenance of spindle assembly checkpoint signals in response to unattached kinetochore. Based on their results the authors propose that Shugoshin monitors the kinetochore-MT attachments by maintaining higher Aurora B and lower PP1 levels at kinetochores. Shugoshin localizes to centromeres/kinetochores during mitosis in most species, however Shugoshin in C. neoformans specifically localizes to SPBs and along the mitotic spindle. Two of the distinctive findings are the unique localization of Sgo1 and the Bub1 kinase independent checkpoint maintenance function of Sgo1.

The experiments are performed thoroughly with appropriate controls. suitable statistical measures, and results are presented in a manner that is logical and easy to understand. Although results are interesting for the centromere and chromosome biology communities, mechanistic studies for localization of Sgo1 and how the unique Bub1 independent kinase function of Sgo1 mediates its function has not been adequately addressed. Also, I was not very clear of the unique advantage of pursuing studies with this yeast? How are these studies advancing our understanding of chromosome segregation in human health and disease? Are there other differences between findings from C. neoformans and budding/fission yeast wrt to chromosome segregation?

Major Comments:

1. Localization of Sgo1 to CEN or not? Authors report that Sgo1 is recruited to SPBs and along the mitotic spindle (lines 332-362). They have also observed Sgo1 signal at the periphery of the kinetochore. In other systems, Sgo1 has been associated with CEN and peri-CEN chromatin (Deng and Kuo 2018 G3 8:2901-2911; Garcia-Nieto et al. 2023 NSMB 30: 853-859). Cell biology is not most definitive to rule out kinetochore localization, ChIP experiments are most definitive can these be done?
2. Localization of Sgo1 to SPB. As highlighted in summary of the review, recruitment of Sgo1 to the SPBs is an interesting observation for C. neoformans, however, the molecular mechanisms involved in this novel function of Sgo1 remains unknown. Which factors mediate the localization of Sgo1 to the SPBs during the cell cycle? The recruitment of Sgo1 to SPBs could be influenced or mediated by the geometric changes in the mitotic spindle that occur during the mitosis. It is possible that orientation of mitotic spindle relative to the kinetochore during the mitotic cell cycle may dictate the recruitment of Sgo1 to the SPBs. There is precedent from S. cerevisiae where kinetochore protein Ndc10 was found to be associated with SPBs and along mitotic spindle (Bouck and Bloom, 2005 PNAS 102: 5408-5413). It is likely that similar mechanisms might be involved for Sgo1. One of the candidate genes mediating localization of Sgo1 to the SPBs could be the components of CPCs (Abad et al. 2022 JCB 221:e202108156). Authors should at least examine one of them that will help provide a mechanistic insight into the novel role of Sgo1 at the SPBs.
3. Bub1 independent function of Sgo1. It would be useful to provide the evolutionarily timescale for the gain or loss of Bub1-independent SAC function of Sgo1. An evolutionary comparison between basidiomycetes and ascomycetes would help readers understand the biological reasoning and significance of Bub1-independent SAC function of Sgo1.
4. Bub1 independent function of Sgo1. What is the localization of Sgo1 in bub1-kd strain?
5. Authors have established a relationship between Sgo1, Bub1 and Aurora B (lines 247-248). However, such observations could also be mediated by other molecular factors.. It will improve their manuscript and conclusions if they provide further evidence for in vivo interaction of Sgo1 with Bub1 or Aurora B in C. neoformans using Co-IP.

Minor Comments:

1. Figure 1D: The figure is very crowded and difficult to understand. Authors should use letters to show the statistical significance instead of drawing multiple lines.
2. Figures 1B and 5D: The sgo1null strain is not sensitive to 3 ug of thiabendazole in Figure 1B but it is in figure 5D. Please explain.
3. Figures 1 and 2: Authors have used 1 ug of nocodazole in figure 1 and it is 2.5 ug in figure 2. Please explain.
4. Figure 2C-2E: Is GFP-Bub1 signals in sgo1∆ similar to GFP-bub1-kd signals? To clarify the GFP-bub1-kd signals in Figure 2, the authors should show pictures of GFP-bub1-kd signals in Figure 2C, as well as GFP-bub1-kd intensity in Figure 2E. They need to explain how they score the diffused GFP-Bub1 signals in the whole cells of 280 min post-nocodazole treatment.
5. In line 253-256, the authors incubated the Aurora B-overexpressed cells (galactose medium) at permissive temperature, but Aurora B-depleted cells (glucose medium) at non-permissive temperature. What is the purpose for incubations at different temperatures? Do the Aurora B-overexpressed cells show a ts phenotype?
6. Reproducibility of localization pattern of GFP-Sgo1 in Figure 6. Can the signals be quantified?
7. Figure 5: Since Sgo1 in C. neoformans has unique localization pattern, it is possible that the target of phosphorylation by Bub1 is different, rather than binding to phosphorylated H2A. The authors should at least discuss the possibility.
8. Authors have used a linker protein Bgi1 as a control (lines 148-150). However, there are other controls, which are more suitable than Bgi1. Perhaps authors should use a protein that interacts with microtubules. One of the candidates in this experiment would be evolutionarily conserved Ndc80.
9. Bub1 independent function of Sgo1. It is unclear which factors are involved in Bub1-independent function of Sgo1.. It is possible that histone H3 or its variant CENP-A might have some role in Sgo1 recruitment as has been shown for S. cerevisiae and other systems (Luo et al. 2016 Genetics 204:1029-1043; Wu et al. 2023 JMCB, mjad061; Mishra et al. 2018 Cell Cycle 17:11-23). Authors can try to deplete CENP-A and examine the localization of Sgo1 at the kinetochore and at the SPBs in Bub1 and its mutant strains.

Referee Cross-Commenting

Summary: The data supporting an unusual role of Sgo1 as indicated in the title is not supported by the data. Two main conclusions of the paper are the unique localization of Sgo1 and the Bub1 kinase independent role of Sgo1. With respect to localization: Molecular evidence to rule out lack of Sgo1 at centromeric and pericentromeric regions is needed (ChIP, FRET) is needed. Same is true for SPB association is this affected in spb mutants?

Bub1 kinase independent role of Sgo1 needs further experimentation.

Discussion about the significance of studying C. neoformans needs to be included.

Significance

The experiments are performed thoroughly with appropriate controls. suitable statistical measures, and results are presented in a manner that is logical and easy to understand. Although results are interesting for the centromere and chromosome biology communities, mechanistic studies for localization of Sgo1 and how the unique Bub1 independent kinase function of Sgo1 mediates its function has not been adequately addressed. Also, I was not very clear of the unique advantage of pursuing studies with this yeast? How are these studies advancing our understanding of chromosome segregation in human health and disease? Are there other differences between findings from C. neoformans and budding/fission yeast wrt to chromosome segregation?

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The authors present a thorough characterization of the mitotic protein Shugoshin (Sgo1) in the context of Cryptococcus neoformans, an interesting and medically important fungal species. Sgo1 function in chromosome segregation has been well-studied in other eukaryotic species: it recruits the error correction kinase Aurora B and Protein Phosphatase 2 to the centromere and promotes the loading of cohesion at the centromeric locus. The primary function of these proteins is to enable the bipolar attachment of sister chromatids to the spindle apparatus. In this manuscript, Polysetty et al mainly investigate the "secondary" function of Sgo1 in Spindle Assembly Checkpoint (SAC) signaling. They show that: (1) sgo1Δ cells fail to maintain a prolonged SAC response to spindle poisons, because they cannot achieve or maintain normal Bub1 recruitment at unattached kinetochores. (2) The lower Bub1 recruitment is mainly due to the loss of centromeric Aurora B recruitment and increased PP1 recruitment to the kinetochore. There are some interesting departures from the behavior Sgo1 known in other eukaryotes. (3) Sgo1 localizes to the spindle poles in C neoformans with smaller amounts dispersed along the spindle. (4) Furthermore, Sgo1 localization at the centromeres does not require Bub1 kinase activity. Based on these and other observations, the authors advance a model for how Sgo1 is recruited to the centromeres and how it promotes strong SAC response to spindle poisons.

Main comments:

1. In interpreting the effects of thiabendazole on colony growth, the authors should also consider the role of Sgo1 in promoting bipolar attachments by establishing centromeric cohesion and proper geometry (Indjeian and Murray Current Biology 2007, Verzijlbergen et al. eLife 2014). In the absence of Sgo1, cells are more likely to divide with wrongly attached chromosomes and become highly aneuploid, which may promote mortality. The relative importance of Sgo1 function in biorientation and SAC signaling will have to be established using known separation of function mutations in Sgo1.
2. Unless I am missing something, the phenotypes of Sgo1 related to the SAC are completely consistent with the established model of Aurora B and PP1 roles in regulating SAC signaling. Sgo1 promotes Aurora B activity at the kinetochore, and the increased Aurora B activity can promote SAC signaling by: (1) delaying SAC silencing by creating unattached kinetochores during error correction, (2) suppressing PP1 recruitment to the kinetochore, and (3) potentially phosphorylating MELT motif-proximal residues to promote Bub1 recruitment as has been observed in Drosophila (Audette et al MBoC 2021). Conversely, Sgo1 deletion will result in hyperstabilization of even wrong kinetochore-microtubule attachments, higher PP1 recruitment and, therefore, weaker SAC signaling. These points should be discussed when interpreting the results in this study.
3. Phenotypes related to the sgo1-K382A mutations are interesting, and they suggest that Sgo1 recruitment may be independent of Bub1 kinase activity. However, the data need to be strengthened to fully support this conclusion. First, the multiple sequence alignment for Sgo1 shows lysine residues at position 381 and 382 in Cryptococcus. This makes me wonder if the point mutation is sufficient to abolish the Sgo1-pH2A interaction. Second, the expression levels of the mutant should be compared with the wild type to confirm that the phenotype is not due to over-expression/stabilization of the mutant protein. I understand that the thiabendazole resistance of Bub1-kd is quite interesting, but Haspin kinases are also involved in loading Sgo1 at the centromere. The authors could investigate their role in Crypotcoccus to define the alternative mechanism of centromere specific Sgo1 loading.
4. In Figure 6, the authors find strong Sgo1 colocalization at the spindle poles and what they describe as "spindle-like location along the pole-to-pole axis" (lines 358-360). The authors should consider the possibility that this is the pool of centromere associated Sgo1 because it colocalizes reasonably well with CENPA. This interpretation obviates the necessity of the complex model in Figure 6E explaining Sgo1 loading at the centromeres. Given that there must be Sgo1 at the centromeres, the null hypothesis has to be that this Sgo1 is associated with centromeres rather than microtubules. The authors could use biochemical methods to test the hypothesis. Alternatively, BiFC ro FRET based assays may be useful if the authors want to persist with cell biology experiments.

Minor points:

1. The authors use gene repression and over-expression using the Gal1 promoter, but do not assay protein levels for the degree of over-expression. This is fine in many cases because the phenotypes are consistent with over-expression/repression. However, it needs to be confirmed when interpreting the effects of point mutations, e.g., Bub1-kd, Sgo1-K382, etc.
2. I found the model in 5A confusing because the arrows are used to indicate both protein recruitment and promotion/expression of downstream proteins/events. Adding to the confusion is the inverted sgo1 → Aur B direction. The authors should simplify this important panel.
3. The model in Figure 6E is missing some information: gradients in Sgo1 and Ipl1 pools are shown, but they don't line up with the spindle direction and are not otherwise indicated on the spindle. Importantly, this model is necessary only if the authors can conclusively show that the Sgo1 along the spindle axis is associated with microtubule and not the centromere.
4. The authors examine Sgo1's role in loading cohesin at the centromere in Figure S6. An interesting experiment would be to test the thiabendazole sensitivity of Scc1 over-expressing cells to understand whether it can suppress the effects of sgo1Δ.

Referee Cross-Commenting

I think Reviewer #2's comment above summarizes the all the comments effectively. I don't have anything else to add.

Significance

This is a well-constructed and well-executed study. However, the interpretation of many of the results and how strongly these results depart from what's already known in other systems is debatable. Almost all the results describing CnSgo1 involvement in SAC signaling reinforce the established model that Sgo1 recruits Aurora B, which suppresses the recruitment of PP1, the main antagonist for Bub1 recruitment. Thus, Δsgo1 cells are unable to mount a strong SAC response because increased PP1 recruitment antagonizes SAC signaling. In my view, the novel findings are the Bub1 kinase activity-independent loading of Sgo1 at the centromere and the surprising Sgo1 localization at the spindle poles. The manuscript will generate wider interest if the authors dissected the molecular basis of these unexpected observations rather than its established functions. Doing so will require a functional and molecular dissection of Sgo1.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

---

Reply to the reviewers

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Reply to the Reviewers

I thank the Referees for their...

Referee #1

1. The authors should provide more information when...

Responses + The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A). + Though this is not stated in the MS 2. Figure 6: Why has only...

Response: We expanded the comparison

Minor comments:

1. The text contains several...

Response: We added...

Referee #2

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Dr. Ancheta et al. designed several parameters to assess different velocity algorithms, including local consistency, method agreement, overlap of derived genes, and robustness to sequencing depth. Generally, this helps scientists understand the performance of each software. However, I don't think this is enough to help scientists judge which one is better. The biggest problem in the manuscript is the lack of a ground truth. I suggest the authors choose tissues with reliable ground truth, such as spermiogenesis, which has a single lineage direction. You would see a clear streamline from pachytene spermatocytes to sperm, or embryonic cells with different culture days, where the direction should go from earlier to later stages. I strongly suggest the authors use clear lineage samples like spermiogenesis. After that, I think it will be a very helpful paper for scientists.

1. Local consistency is a useful parameter that helps scientists determine which one has more uniform directions.

2. Method agreement is problematic because I don't know which one is ground truth. If you cannot get ground truth, you could use the average direction or angle as the ground truth to see which one is significantly biased from the averages.

3. The overlap of the driver genes also lacks ground truth. Fig4C is good; we could use the overlap of all methods' genes as ground truth to see which one is too biased. I suggest you perform a GO term analysis to see the driver gene distribution and count how many genes are related to the expected GO term. That would also provide evidence to support the ground truth.

4. Robustness to sequencing depth is a good parameter. No comment.

5. The discussion could include more about other methods, such as nascent RNA single-cell sequencing methods and full-length single-cell sequencing methods, which improve the estimation of alpha, beta, and gamma. This could help delve deeper into enhancing the velocity program.

Significance

The biggest problem in the manuscript is the lack of a ground truth. I suggest the authors choose tissues with reliable ground truth, such as spermiogenesis, which has a single lineage direction. You would see a clear streamline from pachytene spermatocytes to sperm, or embryonic cells with different culture days, where the direction should go from earlier to later stages. I strongly suggest the authors use clear lineage samples like spermiogenesis. After that, I think it will be a very helpful paper for scientists.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The authors present a comparative statistical analysis of five RNA velocity methods using two datasets and a single performance metric. Using the selected statistical metric, they describe the variable performance of RNA velocity methods, their variable robustness across different cell states, and the discrepancy of sets of identified lineage-specific driver genes.

At this point, the scientific community extensively documented limitations and lack of stability of RNA velocity performance across methods and datasets. In that context, the manuscript lacks clear theoretical and practical conclusions that would be beneficial to the scientific community.

The choice to focus on only a subset of RNA velocity methods is not discussed. Recent and important extensions, such as VeloVAE, VeloVI, LatentVelo, and Pyro-Velocity, are omitted, which limits the generality of the analysis. The statistical properties of the chosen consistency metric are not explored. The authors do not provide a justification for why this metric is appropriate for comparative analysis. Additionally, the authors do not present how the consistency score can be utilized to evaluate RNA velocity performance on user datasets. Overall, a discussion of the pressing issue of choosing statistical metrics to interpret RNA velocity results is lacking. The pros and cons of different RNA velocity methods, especially in light of the various statistical metrics, are not discussed. The manuscript does not present conclusions from the sampling analysis of sequencing depth. For instance, formalizing these findings with code that users can employ for their datasets would enhance the manuscript's practical utility. Overall, the manuscript would benefit from a thorough benchmark of the methodological approaches in the RNA velocity field, and testing various methods to evaluate RNA veloicty performance.

Significance

At this point, the scientific community extensively documented limitations and lack of stability of RNA velocity performance across methods and datasets. In that context, the manuscript lacks clear theoretical and practical conclusions that would be beneficial to the scientific community.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The authors present a survey of RNA velocity methods, evaluate them on a variety of model datasets, and introduce metrics to determine the local consistency of each individual method. They investigate differences between the methods with a separate metric that identifies consistency across methods, and using this, comment on applicability of each method to novel datasets. The effect of these differences on a downstream driver-gene identification task is also evaluated, and further conclusions are drawn related to this, particularly related to variability as a function of sequencing depth.

Major comments:

• There are a few changes that could be made to improve future applicability. One assumption seems to be that consistency between methods will indicate the most likely trajectory, however without a number of ground truth trajectories it seems that this is difficult to justify. In fact, there are probably good reasons why this would not be the case and that some methods might well be expected to underperform in certain cases. A deep comparison of the mechanics of the methods, or validating a robust set of novel ground truth trajectories, is probably beyond the scope of this paper, but it would be good to make some reference to the fact that these methods do differ in ways that might lead one to expect that some outperform others for good reasons.

• Related to this, it's still tricky to identify a clear path between the underlying approaches of the methods, the empirical observations in Fig 6, and how a reader coming cold to the field could match these aspects to the aims for the analysis of their own dataset. Though, I think that this might well be solved by rephrasing Fig 6 to include statements on the dataset itself - e.g., if you have large transcriptional diversity and a smaller dataset, then probably you would disfavour DeepVelo.

• One other suggestion relates to the uncertainties in the trajectories. This is touched upon in the case of the 'DeepVelo' method, where, for example, it's mentioned that these have a large number of parameters and could be prone to overfitting. However, the paper doesn't go as far to suggest that this could result in the trajectories having a much higher variance, which is is potentially evident in the sequencing depth study. This is perhaps a confounding issue in the comparisons in, for example, Fig 1a, where it seems that there is much more dynamical structure in the DeepVelo plot, but in reality this may be due to a higher degree of variance in the predictions. In this case, it may be that, in fact, all of the trajectories are perfectly consistent between the methods, within their uncertainties, despite the 'mean' values displayed in the plot looking quite different.

• Likely a full accounting of the uncertainties on all of the outputs of these models is also beyond the scope of the paper, however some indication of what the variance of these trajectories looks like (or the average value of this across the UMAMP plot, etc), although optional, would also be another valuable point of comparison between the methods. Bootstrap resampling of the data and re-running the methods, for example, would likely give a good indication of the consequences of the behaviour seen in the sequencing depth studies.

Minor comments on specific sections:

Intro:

It would be good to define exactly what you mean by 'state' with respect to the expression (or expression programs, etc) up front here.

• lineages between states' sounds a little awkward to me, I would suggest something like 'state lineages' instead.
• During cellular transitions' - suggest removing and starting with 'scRNASeq data...'
• Also would be good to define concretely what you mean by 'trajectory' with respect to expression
• inconsistent or incorrect directionalities' - suggest 'inconsistent or incorrect trajectories'?

Perhaps move 'RNA velocity has been applied...' after the description of RNA velocity

• Given these limitations...' - it would perhaps be nice to give some vignettes of how the methods differ before discussing their limitations
• As the mRNA matures...' - perhaps mention the key piece of information is the splicing out of introns, and this permits identification of the mature and immature mRNA (otherwise it seems a bit vague), and/or define splicing in the text
• The method yields...' - redundant?
• ...linear differential equations with constant slope...' - unclear what 'constant slope' means here
• steady state solution' - not clear whether 'steady state' here is synonymous with 'equilibrium', so it would be good to define (e.g., whether this means alpha = gamma, or whether this is a statement on beta, etc).
• ..the directionality in the cell-cell graph,...' - not clear how this becomes a graph, so it would be good to expand on how this is obtained
• the results depend heavily on chosen hyperparameters' - not clear that the other methods don't have this issue. I would guess that this is a matter of degree, but it would be good to indicate whether there are specific reasons why some models are expected to be less sensitive by construction.
• treating them as probabilistic events and resulting in a Markov process' -> 'treating them as probabilistic events in a Markov process
• a dynamic model (scv-Dyn) to address many of the original issues' - not clear from this description how the methods fixes these issues. Perhaps also talk a bit more about this 'latent time' parameter, if it's useful to contextualise the results later.
• deriving gene-specific splicing parameters in a single step,' - not clear what doing this in a 'single step' is, or why it might be advantageous.
• graph convolution' -> graph convolutional
• ...but also its neighbors...' - neighbours in what space?
• the mouse pancreas, a well studied lineage' - phrasing sounds a bit weird, maybe 'with a well studied lineage'?
• RNA velocity streams' -> trajectories? (if defined before)
• Therefore, a general benchmark that compares RNA velocity methods...' It might be nice here also to explain what exactly one might expect to be the ground truth in this case, as it's not particularly clear that something like VeloCyto that apparently predicts basically nothing is a 'bad' result compared to something like scv-Sto which predicts much more complicated dynamics where there may not be any.
• Disparate or contradictory results from various RNA velocity methods undermine our confidence in the predicted trajectories.' -

As mentioned before, I think it is important here to add that these methods were each individually developed for a specific purpose, and likely with an aim to improve upon previous techniques in the literature. So I think this kind of statement would have to be motivated a bit better, if claiming this without specific reference to the designs of each of the techniques on their own merit. For example, one could imagine in future an 'oracle' method that somehow predicts all trajectories with 100% accuracy, but its results are rejected because they don't align with the earlier and more primitive methods in the field. Equivalently, it could be such that one model is designed specifically for a specific type of dataset, or in the low data size regime, so a comparison using other datasets is more unfair (I don't think that is necessarily the case here, but without surveying the rest of the literature, a reader would not know that).

Results:

• 30 nearest neighbors' - With a fixed number of neighbours rather than a fixed similarity, it seems like you might end up getting results that are hard to compare if this is calculated in a sparse region (or the datasets have significantly different sizes)?
• Cell types from well-defined lineages...', '...those with more complex cellular heterogeneity...' - it would be good to indicate how these are considered 'well defined' and what 'more complex cellular heterogeneity' refers to (whether this is just from the UMAP, or whether these are statements that include prior biological assumptions that are used to evaluate the method).
• ...their differentiation process is more complex..' ... '..lineages with complex diversity...' - is this a statement based purely on the variation in expression? If so, it would be good to be clear here.
• ...the landscape's smoothness varies depending on cell type.' - it's been a while since you mentioned 'landscape', so it would be good to remind the reader that this is the distribution of expression in your high dimensional space.
• correlated with cell diversity' -> cell type diversity? Although 'notochord, endoderm and hindbrain' have already been indicated as 'cell types' here, so this is a little confusing
• ...can indicate overtraining or over smoothing...' - this seems a little contradictory, where I would assume that overtraining would result in higher variance, and oversmoothing would give the opposite effect?
• Altogether, the variation in agreement...' - it would be nice to go a little further here and make specific recommendations, even if it's something very vague, as there will be cases where there are no clear biological clues.

Downstream:

• ..overlap in macrostates...' - even if macrostates is a term defined in CellRank, it would be good to redefine it here for the reader
• ..scv-Dyn and UniTVelo both utilize a shared latent time variable..' - is it possible to give any indication why this might lead to a difference? Or even which might be more plausible?
• RNA Velocity' -> RNA velocity

Robustness to sequencing depth:

• DeepVelo, scv-Dyn, and UniTVelo maintained low levels of correlation with the magnitudes from the full reads... - this seems like quite a startling effect. It seems like this indicates the models are really quite unstable, if the removal of 2% of the dataset gives such a considerable difference.

Discussion:

• Our research emphasizes the importance of implementing a method that best fits the dataset...' - You don't indicate any goodness of fit metrics prior to this, so it's not really clear what this means in practice.

• Because the pancreas dataset is often used as a benchmark dataset for RNA velocity methods...' - presumably also this could mean that methods are developed to overfit to this dataset?

• Capturing the full splicing dynamics..' - not clear what 'full splicing dynamics' means here

Fig 1c. (and elsewhere):

Often it's hard to see the trajectory arrows in the rasterised plots. If this isn't just an issue with the review PDF, in Matplotlib it's possible to rasterise the points without rasterising the annotations and axes (https://matplotlib.org/stable/gallery/misc/rasterization_demo.html), which makes things a lot easier to read, but also doesn't leave you with giant file sizes.

Fig 2a.: The equation is a bit confusing, as k seems to be the size of the set of neighbours and the set itself, where in the text k is only ever the number of neighbours. Perhaps it would be better to have something like a set K of neighbours k (where k ∈ K), and then the sum is normalised by |K| and the sum is over k (or alternatively have k = |K| to be consistent with the text).

Fig 2d. (and others) A label on the z axis would be good here

Significance

This is a commendable effort, and will be of use to practitioners navigating the properties of current and future RNA velocity methods, particularly those without a background in the more advanced mathematical formulations of the newer methods. It also is the first time, to my knowledge, that a systematic comparison has been performed using a number of real datasets and with a novel metric.

However, the paper does not go as far as to link specific approaches or assumptions within the methods directly to their empirical observations, which could limit the applicability of the conclusions to only datasets and methods similar to those studied.